Unstructured and Semistructured Interviewing - H. Russell Bernard

节选出处：H. Russell Bernard, Research Methods in Anthropology: Qualitative and Quantitative Approaches (5th Edition, AltaMira Press, 2011), Chapter 8 (pp. 156-186).

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Interviewing I: Unstructured and Semistructured 156 9 Interviewing II: Questionnaires 187 10 Interviewing III: Cultural Domains 223 11 Scales and Scaling 238 12 Participant Observation 256 13 Field Notes and Database Management 291 14 Direct and Indirect Observation 306 15 Introduction to Qualitative and Quantitative Analysis 337 16 Cognitive Anthropology I: Analyzing Cultural Domains 346 17 Cognitive Anthropology II: Decision Modeling, Taxonomies, and Componential Analysis 386 18 Text Analysis I: Interpretive Analysis, Narrative Analysis, Performance Analysis, and Conversation Analysis 407 19 Text Analysis II: Schema Analysis, Grounded Theory, Content Analysis, and Analytic Induction 429 20 Univariate Analysis 458 21 Bivariate Analysis: Testing Relations 492

22 Multivariate Analysis 533 Appendix A: Table of Areas under a Normal Curve 559 Appendix B: Student's t Distribution 561 Appendix C: Chi-Square Distribution Table 562 Appendix D: F Table for the .05 Level of Significance 564 Appendix E: Resources for Fieldworkers 566 References 571 Subject Index 638 Author Index 649 About the Author 666

Preface to the Fifth Edition

Since 1988, when I wrote the first edition of this book, I’ve heard from many colleagues that their departments are offering courses in research methods. This is wonderful. Anthropologists of my generation, trained in the 1950s and 1960s, were hard-pressed to find courses we could take on how to do research. There was something rather mystical about the how-to of fieldwork; it seemed inappropriate to make the experience too methodical.

The mystique is still there. Anthropological fieldwork is fascinating and dangerous. Seriously, read Nancy Howell’s (1990) book on the physical hazards of fieldwork if you think this is a joke. But many anthropologists have found that participant observation loses none of its allure when they collect data systematically and according to a research design. Instead, they learn that having lots of reliable data when they return from fieldwork makes the experience all the more magical.

I wrote this book to make it easier for students to collect and analyze reliable data beginning with their first fieldwork experience. We properly challenge one another’s explanations for why Hindus don’t eat their cattle and why, in some cultures, mothers are more likely than fathers are to abuse their children. That’s how knowledge grows. Whatever our theories, though, all of us need data on which to test those theories. The methods for collecting and analyzing data belong to all of us.

WHAT’S IN THIS BOOK

The book begins with a chapter about where I think anthropology fits in the social sciences. With one foot planted squarely in the humanities and the other in the sciences, there has always been a certain tension in the discipline between those who would make anthropology a quantitative science and those whose goal it is to produce documents that convey the richness—indeed, the uniqueness—of human thought and experience.

Students of cultural anthropology and archeology may be asked early in their training to take a stand for qualitative or quantitative research. Readers of this textbook will find no support for this pernicious distinction. I lay out my support for positivism in chapter 1, but I also make clear that positivism is not a synonym for quantitative. As you read chapter 1, think about your own position. You don’t have to agree with my ideas on epistemological issues to profit from the later chapters on how to select informants, how to choose a sample, how to do questionnaire surveys, how to write and manage field notes, and so on.

Chapter 2 introduces the vocabulary of social research. There’s a lot of jargon, but it’s the good kind. Important concepts deserve words of their own, and chapter 2 is full of important concepts like reliability, validity, levels of measurement, operationism, and covariation.

Whenever I introduce a new term, like positivism, hermeneutics, or whatever, I put it in boldface type. If you aren’t sure what a factorial design is (while you’re reading about focus groups in chapter 8, on unstructured and semistructured interviewing), the index will tell you that there are other examples of that piece of jargon in chapter 4 (on experiments), in chapter 9 (on questionnaires), and in chapter 19 (on analytic induction).

Chapter 3 is about preparing for research: choosing research topics and showing how your research question contributes to theory. We always want our research to be theoretically important, but what does that mean? After you study this chapter, you should know what theory is and how to tell if your research is likely to contribute to theory or not. It may seem incongruous to spend a lot of time talking about theory in a textbook about methods, but it isn’t. Theory is about answering research questions . . . and so is method. I don’t like the bogus distinction between method and theory any more than I like the one between qualitative and quantitative.

Part of preparing for research is covering the literature. In the old days, before the Internet, you could get away with starting a research paper or a grant proposal with the phrase ‘‘little is known about . . .’’ and filling in the blank. Now, with online databases, you simply can’t do that. Chapter 3 is also one of several places in the book where I deal with ethics. I don’t have a separate chapter on ethics. The topic is important in every phase of research, even in the beginning phase of choosing a problem to study.

Chapter 4 is about research design and the experimental method. You should come away from chapter 4 with a tendency to see the world as a series of natural experiments waiting for your evaluation.

Chapters 5, 6, and 7 are about sampling. Chapter 5 is an introduction to the basics: why we need samples and how samples of individual data and cultural data are different. Chapter 6 is about sampling theory—where we deal with the question: ‘‘How big should my sample be?’’ If you’ve had a course in statistics, the concepts in chapter 6 will be familiar to you. If you haven’t had any stats before, read the chapter anyway. Trust me. There is almost no math in chapter 6. The formula for calculating the standard error of the mean has a square root sign. That’s as hard as it gets. If you don’t understand what the standard error is, you have two choices. You can ignore it and concentrate on the concepts that underlie good sampling or you can study chapter 20 on univariate statistics and return to chapter 6 later. Chapter 7 is about nonprobability sampling and about choosing informants.

I’ve placed the sampling chapters early in the book because the concepts in these chapters are so important. The validity of research findings depends crucially on measurement, but your ability to generalize from valid findings depends crucially on sampling.

Chapters 8–14 are about methods for collecting data. Chapter 8 is on unstructured and semistructured interviewing. All data gathering in fieldwork boils down to two broad kinds of activities: watching and listening. You can observe people and the environment and you can talk to people and get them to tell you things. Most data collection in anthropology is done by just talking to people. This chapter is about how to do that effectively.

Chapter 9 is devoted entirely to questionnaires—how to write good questions, how to train interviewers, the merits of face-to-face interviews versus self-administered and telephone interviews, minimizing response effects, and so on.

Chapter 10 is about structured interviewing for cultural domain analysis: pile sorts, triad tests, free listing, frame eliciting, ratings, rankings, and paired comparisons.

Chapter 11 is about how to build and use scales to measure concepts. This chapter has a long section on Likert-like scales, the most common scaling device in social research, but it also covers Guttman scaling, semantic differential scaling, and other methods.

Chapter 12 is about participant observation, the core method in cultural anthropology. Participant observation is what produces rapport, and rapport is what makes it possible for anthropologists to do all kinds of otherwise unthinkably intrusive things—watch people bury their dead, accompany fishermen for weeks at a time at sea, ask women how long they breast-feed, go into people’s homes at random times and weigh their food, watch people apply poultices to open sores. . . .

Lone fieldworkers don’t have time—even in a year—to interview hundreds and hundreds of people, so our work tends to be less reliable than that of our colleagues in some other disciplines. But participant observation lends validity to our work, and this is a very precious commodity. (More about the difference between reliability and validity in chapter 2.)

Participant observation fieldwork produces field notes—lots of them. Chapter 13 describes how to write and manage field notes.

Chapter 14 is about watching. There are two kinds of watching: the direct, obtrusive kind (standing around with a stopwatch and a note pad) and the indirect, unobtrusive kind (lurking out of sight). Direct observation includes continuous monitoring and spot sampling, and the latter is the method used in time allocation research. Unobtrusive observation poses serious ethical problems, which I treat in some detail in this chapter. One kind of unobtrusive observation poses hardly any ethical problems: research on the physical traces of behavior. You may be surprised at how much you can learn from studying phone bills, marriage contracts, office memos, and other traces of behavior. Your credit rating, after all, is based on other people’s evaluation of the traces of your behavior.

Chapters 15–22 are about data analysis. Chapter 15 is a general introduction to the fundamentals of analysis. Data do not ‘‘speak for themselves.’’ You have to process data, pore over them, sort them out, and produce an analysis. The canons of science that govern data analysis and the development of explanations apply equally to qualitative and quantitative data.

Chapters 16 and 17 are about analyzing data in cognitive anthropology. Chapter 16 focuses on analyzing the data from methods on interviewing introduced in chapter 10: free lists, pile sorts, and so on. This involves multidimensional scaling, cluster analysis, and cultural consensus analysis, so these methods of analysis are explained here, rather than in the chapter on multivariate statistics, as in previous editions. Chapter 17 is about ethnographic decision tree modeling, taxonomies, and componential analysis.

Chapters 18 and 19 cover text analysis. Chapter 18 is about methods that treat whole texts as the unit of interest, while chapter 19 is about methods that involve coding for themes, either inductively or a priori.

Finally, chapters 20, 21, and 22 are an introduction to the basics of statistical reasoning and data analysis—methods that are used across the social sciences. Chapter 20 deals with univariate statistics—that is, statistics that describe a single variable, without making any comparisons among variables. Chapters 21 and 22 are discussions of bivariate and multivariate statistics—statistics that describe relationships among variables and let you test hypotheses about what causes what.

If you want to become comfortable with statistical analysis, you need more than a basic course; you need a course in regression and applied multivariate analysis and a course (or a lot of hands-on practice) in the use of one of the major statistical packages, like SPSS^, SAS^, STATA^, and SYSTAT^. Neither the material in this book nor a course in the use of statistical packages is a replacement for taking statistics from professional instructors of that subject. Nevertheless, after working through the materials in chapters 20–22, you will be able to use basic statistics to describe your data and be able to take your data to a professional statistical consultant and understand what she or he suggests.

I don’t provide exercises at the end of chapters. Instead, throughout the book, you’ll find dozens of examples of real research that you can replicate. One of the best ways to learn about research is to repeat someone else’s successful project. The best thing about replicating previous research is that whatever you find out has to be significant. Whether you corroborate or falsify someone else’s findings, you’ve made a serious contribution to the store of knowledge. If you repeat any of the research projects described in this book, write and tell me about what you found.

WHAT’S NEW IN THIS EDITION?

There is now a section labeled Further Reading at the end of each chapter and pointers within the chapters to chunks of that further reading. The result is that the bibliography is about 40% larger than in the last edition. People ask me why there are so many references to really, really old stuff. The reason is that I want students to know that the literature on research methods is very rich and I want them to know about many of the classics. Many examples have been updated, including, when available, new information about classics.

The separate chapter on searching the literature is gone from this edition because students are universally aware of the databases. I’ve retained the information, however, about the databases that I think are most important for students to control and instructions on how to use the databases effectively.

Sampling takes up three chapters in this edition, up from two in the last one. In earlier editions, I treated consensus analysis in the chapter on nonprobability sampling and choosing informants. Consensus analysis has been moved to chapter 16, on cultural domain analysis.

Interviewing takes up three chapters in this edition. In chapter 8, on unstructured and semistructured interviewing, the sections on recording equipment and on voice recognition software (VRS) have been updated, and examples have been added or updated. Chapters 9 and 10 are on two very different kinds of structured interviewing. Chapter 9 focuses on questionnaires and surveys. I’ve updated the material on computer-based methods and on Internet-based surveys and added material on the list experiment. Chapter 10 introduces methods used in cognitive anthropology, including free lists, pile sorts, triad tests, and paired comparisons. Methods for analyzing these data are in chapter 16. In chapter 11, on scaling, I’ve added material on an instrument called the happiness stick. In chapter 12, on participant observation, I’ve updated several examples and added bibliography. In chapter 13, on taking and managing field notes, I’ve updated or added examples, and added information on using word processors as text managers. In chapter 14, the bibliography has been updated.

Chapter 15 is essentially unchanged. Chapter 16 contains new material on analyzing data from the systematic ethnographic methods described in chapter 10: free lists, pile sorts, and so on. Multidimensional scaling and cluster analysis are described in chapter 16, as is cultural consensus analysis and cultural consonance analysis. Chapter 17 continues with other methods associated with cognitive anthropology. The chapter on text analysis in the previous edition is now two chapters. The work in these two chapters owes much to my work with Gery Ryan (Bernard and Ryan 2010; Ryan and Bernard 2000, 2003). Chapter 18 focuses on methods for analyzing whole texts; chapter 19 deals with methods that involve finding themes in texts and analyzing the distribution of themes.

Chapters 20, 21, and 22 have been updated, but are essentially the same as chapters 19, 20, and 21 in the 4th edition.

A word about some things that are not in this book. Visual anthropology is developing quickly with the advent of easy-to-carry, easy-to-use cameras that produce high-quality still and moving images and synchronized sound as well as software for analyzing video as text (see appendix E). For more on visual anthropology, see El Guindi (2004).

Those interested in geospatial analysis should consult De Smith et al. (2007) and various online tutorials (e.g., http://www.spatialanalysisonline.com).

For methods in the study of online communities, see Hine (2000) and Kozinets (2010).

And finally, network analysis. Anthropologists contributed in the 1950s and ’60s to the development of this field but, with a few exceptions, abandoned it after the 1970s. Interest by anthropologists has picked up recently with the development of software for collecting and analyzing network data (Borgatti et al. 2002) and especially personal network data (McCarty et al. 2010). Key work on analyzing personal, or egocentric, networks is by McCarty (2002) and Wellman (2007) (and see the entire May 2007 issue of Field Methods). For an introduction to the field of network analysis, see the online text by Hanneman and Riddle (2005): http://faculty.ucr.edu/hanneman.

ACKNOWLEDGMENTS

My debt to colleagues, students, and friends is enormous. Colleagues and students who use this book continue to share their ideas with me on the teaching of research methods or to point out errors. My thanks to Susan Andreatta, Michael Chibnik, Bonnie Dixson, Kerry Feldman, Penn Handwerker, Margo-Lea Hurwicz, Paul James, Robert Van Kemper, Carmella Moore, John Poggie (and his student, Timothy Campbell), Paula Sabloff (and her student, Shimul Melwani), and David Zeitlyn. I’m grateful—and very pleased to know that the book is read so carefully and that students are learning from my mistakes.

I can not thank my students enough for the help I’ve received from them over the years, particularly Clarence Gravlee, Christopher McCarty, and Gery Ryan. Continuing discussions with Gravlee and McCarty have sharpened my focus on the methods for analyzing relational data. Ryan’s influence will be evident in chapters 17, 18, and 19 in the discussions about ethnographic decision models, conversation analysis, and coding themes. He is also the coauthor with me of a book on analyzing qualitative data (Bernard and Ryan 2010).

Students at the University of Florida have been keen critics of my writing over the years. Domenick Dellino, Michael Evans, Camilla Harshbarger, Fred Hay, Shepherd Iverson, Christopher McCarty, and David Price were very helpful as I wrote the first edition. Holly Williams, Gery Ryan, Gene Ann Shelley, Barbara Marriott, Kenneth Adams, Susan Stans, Bryan Byrne, and Louis Forline gave me the benefit of their advice for the second edition. Discussions with Nanette Barkey, Clarence Gravlee, Harold Green, Scott Hill, David Kennedy, George Mbeh, Isaac Nyamongo, Jorge Rocha, Amanda Stronza, and Kenneth Sturrock helped me with the third edition, as did discussions with Oliver Kortendick, Julia Pauli, and Michael Schnegg at the University of Cologne during 1994–95. For the fourth and fifth editions, I have benefited from the continuing input of many former students, as well as from discussions with Aryeh Jacobsohn, Stacey Giroux, Mark House, Adam Kisˇ, Mason Mathews, Chad Maxwell, Rosalyn Negron, Fatma Soud, Eri Sugita, Tracy Van Holt, and Amber Wutich. All gave freely of their time to talk to me about research methods and about how to teach research methods.

Over 45 years of teaching research methods, I have benefited from the many textbooks on the subject in psychology (e.g., Kerlinger 1973; Murphy et al. 1937), sociology (e.g.,

Babbie 1983; Goode and Hatt 1952; Lundberg 1964; Nachmias and Nachmias 1976), and anthropology (e.g., Brim and Spain 1974; A. Johnson 1978; Pelto and Pelto 1978). The scholars whose works most influenced my thinking about research methods were Paul Lazarsfeld (1954, 1982; Lazarsfeld and Rosenberg 1955; Lazarsfeld et al. 1972) and Donald Campbell (1957, 1974, 1975; Campbell and Stanley 1966; Cook and Campbell 1979).

Over those same 45 years, I’ve profited from discussions about research methods with Michael Agar, Stephen Borgatti, James Boster, Devon Brewer, Michael Burton, Joel Cohen, Ronald Cohen, Roy D’Andrade, Don Dillman, William Dressler, Carol Ember, the late Melvin Ember, Michael Fischer, Linton Freeman, Sue Freeman, John Gatewood, Christina Gladwin, Ricardo Godoy, Raymond Hames, the late Marvin Harris, Penn Handwerker, Jeffrey Johnson, Hartmut Lang, Gary Martin, Michael Paolisso, Pertti Pelto, the late Jack Roberts, A. Kimball Romney, Lee Sailer, the late Thomas Schweizer, J. Richard Stepp, Susan Weller, Douglas White, and Oswald Werner. Other colleagues who have influenced on my thinking about research methods include Ronald Burt, Patrick Doreian, Linda Garro, Theodore Graves, Eugene Hammel, Allen Johnson, Charles Kadushin, Conrad Kottak, Maxine Margolis, Stuart Plattner, Ronald Rice, the late Peter Rossi, James Short, Harry Triandis, the late Charles Wagley, Eben Weitzman, Harry Wolcott, and Alvin Wolfe. Most of them knew that they were helping me talk and think through the issues presented in this book, but some may not have, so I take this opportunity to thank them all.

Time is a gift we all cherish. The first edition of this book was written in 1985–86 during a year of research leave from the University of Florida, for which I thank Charles Sidman, then dean of the College of Liberal Arts and Sciences. I had the opportunity to read widely about research methods and to begin writing the second edition when I was a guest professor at the Museum of Ethnology in Osaka, Japan, from March to June, 1991. My deep appreciation to Kazuko Matsuzawa for that opportunity. A year at the University of Cologne, in 1994–95, as a von Humboldt scholar, gave me the time to continue reading about research methods, across the social and behavioral sciences. Alas, my colleague and host for that year, Thomas Schweizer, died in 1999. The University of Florida granted me a sabbatical to bring out the fourth edition. Since 2007, I’ve been on a permanent sabbatical—that is, retired from full-time teaching.

In 1987, Pertti Pelto, Lee Sailer, and I taught the first National Science Foundation Summer Institute on Research Methods in Cultural Anthropology. Stephen Borgatti joined the team in 1988 (when Sailer left), and the three of us taught together for 8 years, from 1988 to 1995. My intellectual debt to those two colleagues is profound. Pelto, wrote the pioneering methods text in cultural anthropology (1970), and I’ve long been influenced by his sensible combination of ethnographic and numerical data in field research. Borgatti’s influence is evident in my discussion of domain analysis. He is the author of ANTHROPAC, an antique DOS program that is still the only software I know that supports the collection and analysis of free lists, triad tests, pile sorts, and paired comparisons. The manual that Borgatti wrote for ANTHROPAC is an underground treasure (see appendix E). Teachers of these methods will want to consult that manual as well as Borgatti’s web pages and his chapter in the Ethnographer’s Tool Kit (Borgatti 1999).

When the original methods camp ended in 1995, Jeffrey Johnson initiated a new, NSFsupported program, the Summer Institute on Research Design in Cultural Anthropology (the SIRD)—this one for Ph.D. students. Johnson invited Susan Weller and me to join him in that program and I’ve benefited every year since then from long discussions with these colleagues—and the more than 200 students who have participated—about the pedagogy of research methods.

In 2005, we initiated another program, the Short Courses on Research Methods in Cultural Anthropology (the SCRM)—again, supported by NSF. These 5-day courses run in parallel to the SIRD at the Duke University Marine Laboratories, in Beaufort, North Carolina. And here again I have benefited from the wisdom of the faculty who teach in this program, including Christopher McCarty, Amber Wutich, Clarence Gravlee, Jeffrey Johnson, J. Richard Stepp, Gary Martin, Raymond Hames, Michael Paolisso, Elizabeth Cartwright, and Jerome Crowder.

My closest colleague, and the one to whom I am most intellectually indebted, was Peter Killworth, with whom I worked from 1972 until his death in 2008. Peter was a geophysicist at the University of Southampton and was accustomed to working with data that had been collected by deep-sea current meters, satellite weather scanners, and the like. He shared my vision of an effective science of humanity and he showed an appreciation for the difficulties a naturalist like me encounters in collecting real-life data, in the field, about human behavior and thought. Most importantly, he helped me see the possibilities for overcoming those difficulties through the application of scientific research practices. The results are never perfect, but the process of trying is always exhilarating. That’s the central lesson of this book, and I hope it comes through.

Mitch Allen commissioned the first four editions of this book and is a treasured friend and critic. My editors for this edition, Jack Meinhardt and Marissa Parks, have continued this tradition of support. I thank the production staff at Rowman & Littlefield for their thoroughly professional work. It’s so important to have really good production people on your side.

Finally, my enduring thanks to Carole Bernard for editing my work and for all her support over the years. Every writer needs an editor. Few are blessed with an editor who is a life partner.

H. R. B.

March 15, 2010

Gainesville, Florida

Anthropology and the Social Sciences

THE CRAFT OF RESEARCH

This book is about research methods in anthropology—methods for designing research, methods for sampling, methods for collecting data, and methods for analyzing data. And in anthropology, this all has to be done twice—once for qualitative data and once for quantitative data.

No one is expert in all the methods for research. But by the time you get through this book, you’ll know about the range of methods used in anthropology and you’ll know which kinds of research problems are best addressed by which methods.

Research is a craft. I’m not talking analogy here. Research isn’t like a craft. It is a craft. If you know what people have to go through to become skilled carpenters or makers of clothes, you have some idea of what it takes to learn the skills for doing research. It takes practice, practice, and more practice.

Have you ever known a professional seamstress? My wife and I were doing fieldwork in Ixmiquilpan, a small town in the state of Hidalgo, Mexico, in 1962 when we met Florencia. She made dresses for little girls—Communion dresses, mostly. Mothers would bring their girls to Florencia’s house. Florencia would look at the girls and say ‘‘turn around . . . turn again . . . OK,’’ and that was that. The mother and daughter would leave, and Florencia would start making a dress. No pattern, no elaborate measurement. There would be one fitting to make some adjustments, and that was it.

We were amazed at Florencia’s ability to pick up a scissors and start cutting fabric without a pattern. Then, 2 years later, in 1964, we went to Greece and met Irini. She made dresses for women on the island of Kalymnos where I did my doctoral fieldwork. Women would bring Irini a catalog or a picture—from Sears or from some Paris fashion show— and Irini would make the dresses. Irini was more cautious than Florencia was. She made lots of measurements and took notes. But there were no patterns. She just looked at her clients, made the measurements, and started cutting fabric.

How do people learn that much? With lots of practice. And that’s the way it is with research. Don’t expect to do perfect research the first time out. In fact, don’t ever expect to do perfect research. Just expect that each time you do a research project, you will bring more and more experience to the effort and that your abilities to gather and analyze data and write up the results will get better and better.

METHODS BELONG TO ALL OF US

As you go through this book, you’ll learn about methods that were developed in other fields as well as methods that were developed in anthropology. In my view, there are no anthropological or sociological or psychological methods. The questions we ask about the human condition may differ across the social sciences, but methods belong to all of us.

Truth is, from the earliest days of the discipline, right up to the present, anthropologists have been prodigious inventors, consumers, and adapters of research methods. Anthropologists developed some of the widely used methods for finding patterns in text, for studying how people use their time, and for learning how people make decisions. Those methods are up for grabs by everyone. The questionnaire survey has been developed mostly by sociologists, but that method is now everyone’s. Psychologists make the most consistent use of the experiment, and historians of archives, but anthropologists use and contribute to the improvement of those methods, too.

Anthropologists make the most consistent use of participant observation, but that method turns up in political science, nursing, criminology, and education. The boundaries between the social science disciplines remain strong, but those boundaries are less and less about methods and even less and less about content. These days, anthropologists are just as likely as sociologists are to study the values of working-class Americans in Pennsylvania and New York (Durrenberger and Doukas 2008), or environmental degradation in Arizona (West and Va´ squez-Leo´ n 2008), or how women are socialized to become modern mothers in Greece (Paxon 2004).

In fact, the differences within anthropology and sociology with regard to methods are more important than the differences between those disciplines. There is an irreducible difference, for example, between those of us in any of the social sciences for whom the first principle of inquiry is that reality is constructed uniquely by each person (the constructivist view) and those of us who start from the principle that external reality awaits our discovery through a series of increasingly good approximations to the truth (the positivist view). There is also an important (but not incompatible) difference between those of us who seek to understand people’s beliefs—the grand interpretivist tradition in the social sciences—and those of us who seek to explain what causes those beliefs and action and what those beliefs and actions cause—the equally grand scientific tradition.

Whatever our epistemological differences, though, the actual methods for collecting and analyzing data belong to everyone (Bernard 1993).

EPISTEMOLOGY: WAYS OF KNOWING

The problem with trying to write a book about research methods (besides the fact that there are so many of them) is that the word ‘‘method’’ has at least three meanings. At the most general level, it means epistemology, or the study of how we know things. At a stillpretty-general level, it’s about strategic choices, like whether to do participant observation fieldwork, dig up information from libraries and archives, do a survey, or run an experiment. These are strategic methods, which means that they comprise lots of methods at once. (For a review of epistemological issues in anthropology, see Schweizer 1998.)

At the specific level, method is about choice of technique—whether to stratify a sample or not, whether to do face-to-face interviews or use the telephone or the Internet, whether to use a Solomon four-group design or a static-group comparison design in running an experiment, and so on. (We’ll get to all these things as we go along—experimental designs in chapter 4, sampling in chapters 5, 6, and 7, personal and telephone interview formats in chapters 8 and 9).

When it comes to epistemology, there are several key questions. One is whether you subscribe to the philosophical principles of rationalism or empiricism. Another is whether you buy the assumptions of the scientific method, often called positivism in the social sciences, or favor the competing method, often called humanism or interpretivism. These are tough questions, with no easy answers. I discuss them in turn.

RATIONALISM, EMPIRICISM, AND KANT

The virtues and dangers of rationalism versus empiricism have been debated for centuries. Rationalism is the idea that human beings achieve knowledge because of their capacity to reason. From the rationalist perspective, there are a priori truths, which, if we just prepare our minds adequately, will become evident to us. From this perspective, progress of the human intellect over the centuries has resulted from reason. Many great thinkers, from Plato (428–327 bce) to Leibnitz (Gottfried Wilhelm Baron von Leibniz, 1646–1716) subscribed to the rationalist principle of knowledge. ‘‘We hold these truths to be self-evident’’ is an example of assuming a priori truths.

The competing epistemology is empiricism. For empiricists, like John Locke (1632– 1704), human beings are born tabula rasa—with a ‘‘clean slate.’’ What we come to know is the result of our experience written on that slate. David Hume (1711–1776) elaborated the empiricist philosophy of knowledge: We see and hear and taste things, and, as we accumulate experience, we make generalizations. We come, in other words, to understand what is true from what we are exposed to.

This means, Hume held, that we can never be absolutely sure that what we know is true. (By contrast, if we reason our way to a priori truths, we can be certain of whatever knowledge we have gained.) Hume’s brand of skepticism is a fundamental principle of modern science. The scientific method, as it’s understood today, involves making incremental improvements in what we know, edging toward truth but never quite getting there—and always being ready to have yesterday’s truths overturned by today’s empirical findings.

Immanuel Kant (1724–1804) proposed a way out, an alternative to either rationalism or empiricism. A priori truths exist, he said, but if we see those truths it’s because of the way our brains are structured. The human mind, said Kant, has a built-in capacity for ordering and organizing sensory experience. This was a powerful idea that led many scholars to look to the human mind itself for clues about how human behavior is ordered.

Noam Chomsky, for example, proposed that any human can learn any language because we have a universal grammar already built into our minds. This would account, he said, for the fact that material from one language can be translated into any other language. A competing theory was proposed by B. F. Skinner, a radical behaviorist. Humans learn their language, Skinner said, the way all animals learn everything, by operant conditioning, or reinforced learning. Babies learn the sounds of their language, for example, because people who speak the language reward babies for making the ‘‘right’ sounds. A famous debate between Chomsky (1957, 1959) and Skinner (1957) that began over 50 years ago has been a hot topic for partisans on both sides ever since (Further Reading: the Chomsky-Skinner debate).

RATIONALISM, EMPIRICISM, AND MORALITY

The intellectual clash between empiricism and rationalism creates a dilemma for all social scientists. Empiricism holds that people learn their values and that values are therefore relative. I consider myself an empiricist, but I accept the rationalist idea that there are universal truths about right and wrong.

I’m not in the least interested, for example, in transcending my disgust with, or taking a value-neutral stance about genocide in Germany of the 1940s, or in Cambodia of the

1970s, or in Bosnia and Rwanda of the 1990s, or in Sudan in 2010. I can never say that the Aztec practice of sacrificing thousands of captured prisoners was just another religious practice that one has to tolerate to be a good cultural relativist. No one has ever found a satisfactory way out of this rationalist-empiricist dilemma. As a practical matter, I recognize that both rationalism and empiricism have contributed to our current understanding of the diversity of human behavior.

Modern social science has its roots in the empiricists of the French and Scottish Enlightenment. The early empiricists of the period, like David Hume, looked outside the human mind, to human behavior and experience, for answers to questions about human differences. They made the idea of a mechanistic science of humanity as plausible as the idea of a mechanistic science of other natural phenomena.

In the rest of this chapter, I outline the assumptions of the scientific method and how they apply to the study of human thought and behavior in the social sciences today.

THE NORMS OF SCIENCE

The norms of science are clear. Science is ‘‘an objective, logical, and systematic method of analysis of phenomena, devised to permit the accumulation of reliable knowledge’’ (Lastrucci 1963:6). Three words in Lastrucci’s definition—‘‘objective,’’ ‘‘method,’’ and ‘‘reliable’’—are especially important.

1. Objective. The idea of truly objective inquiry has long been understood to be a delusion. Scientists do hold, however, that striving for objectivity is useful. In practice, this means being explicit about our measurements (whether we make them in words or in numbers), so that others can more easily find the errors we make. We constantly try to improve measurement, to make it more precise and more accurate, and we submit our findings to peer review—what Robert Merton called the ‘‘organized skepticism’ of our colleagues (1938:334–36).

2. Method. Each scientific discipline has developed a set of techniques for gathering and handling data, but there is, in general, a single scientific method. The method is based on three assumptions: (1) that reality is ‘‘out there’’ to be discovered; (2) that direct observation is the way to discover it; and (3) that material explanations for observable phenomena are always sufficient and metaphysical explanations are never needed. Direct observation can be done with the naked eye or enhanced with various instruments (like microscopes); and human beings can be improved by training as instruments of observation. (I’ll say more about that in chapters 12 and 14 on participant observation and direct observation.)

Metaphysics refers to explanations of phenomena by any nonmaterial force, such as the mind or spirit or a deity—things that, by definition, cannot be investigated by the methods of science. This does not deny the existence of metaphysical knowledge, but scientific and metaphysical knowledge are quite different. There are time-honored traditions of metaphysical knowledge—knowledge that comes from introspection, self-denial, and spiritual revelation—in cultures across the world.

In fact, science does not reject metaphysical knowledge—though individual scientists may do so—only the use of metaphysics to explain natural phenomena. The great insights about the nature of existence, expressed throughout the ages by poets, theologians, philosophers, historians, and other humanists may one day be understood as biophysical phenomena, but so far, they remain tantalizingly metaphysical.

3. Reliable. Something that is true in Detroit is just as true in Vladivostok and Nairobi. Knowledge can be kept secret by nations, but there can never be such a thing as ‘‘Venezuelan physics,’’ ‘‘American chemistry,’’ or ‘‘Kenyan geology.’’

Not that it hasn’t been tried. From around 1935–1965, T. D. Lysenko, with the early help of Josef Stalin, succeeded in gaining absolute power over biology in what was then the Soviet Union. Lysenko developed a Lamarckian theory of genetics, in which humaninduced changes in seeds would, he claimed, become inherited. Despite public rebuke from the entire non-Soviet scientific world, Lysenko’s ‘‘Russian genetics’’ became official Soviet policy—a policy that nearly ruined agriculture in the Soviet Union and its European satellites well into the 1960s (Joravsky 1970; Soifer 1994) (Further Reading: the norms of science).

THE DEVELOPMENT OF SCIENCE: FROM DEMOCRITUS TO NEWTON

The scientific method is barely 400 years old, and its systematic application to human thought and behavior is less than half that. Aristotle insisted that knowledge should be based on experience and that conclusions about general cases should be based on the observation of more limited ones. But Aristotle did not advocate disinterested, objective accumulation of reliable knowledge. Moreover, like Aristotle, all scholars until the 17th century relied on metaphysical concepts, like the soul, to explain observable phenomena. Even in the 19th century, biologists still talked about ‘‘vital forces’’ as a way of explaining the existence of life.

Early Greek philosophers, like Democritus (460–370 bce), who developed the atomic theory of matter, were certainly materialists, but one ancient scholar stands out for the kind of thinking that would eventually divorce science from studies of mystical phenomena. In his single surviving work, a poem entitled On the Nature of the Universe (1998), Titus Lucretius Carus (98–55 bce) suggested that everything that existed in the world had to be made of some material substance. Consequently, if the soul and the gods were real, they had to be material, too (see Minadeo 1969). Lucretius’ work did not have much impact on the way knowledge was pursued, and his work is little appreciated in the social sciences (but see Harris [1968] for an exception).

EXPLORATION, PRINTING, AND MODERN SCIENCE

Skip to around 1400, when a series of revolutionary changes began in Europe—some of which are still going on—that transformed Western society and other societies around the world. In 1413, the first Spanish ships began raiding the coast of West Africa, hijacking cargo and capturing slaves from local traders. New tools of navigation (the compass and the sextant) made it possible for adventurous plunderers to go farther and farther from European shores in search of booty.

These breakthroughs were like those in architecture and astronomy by the ancient Mayans and Egyptians. They were based on systematic observation of the natural world, but they were not generated by the social and philosophical enterprise we call science. That required several other revolutions.

Johannes Gutenberg (1397–1468) completed the first edition of the Bible on his newly invented printing press in 1455. (Printing presses had been used earlier in China, Japan, and Korea, but lacked movable type.) By the end of the 15th century, every major city in Europe had a press. Printed books provided a means for the accumulation and distribution of knowledge. Eventually, printing would make organized science possible, but it did not by itself guarantee the objective pursuit of reliable knowledge, any more than the invention of writing had done four millennia before (N. Z. Davis 1981; Eisenstein 1979).

Martin Luther (1483–1546) was born just 15 years after Gutenberg died. No historical figure is more associated with the Protestant Reformation, which began in 1517, and the Reformation added much to the history of modern science. It challenged the authority of the Roman Catholic Church to be the sole interpreter and disseminator of theological doctrine.

The Protestant affirmation of every person’s right to interpret scripture required literacy on the part of everyone, not just the clergy. The printing press made it possible for every family of some means to own and read its own Bible. This promoted widespread literacy, in Europe and later in the United States, and this, in turn, helped make possible the development of science as an organized activity.

Galileo

The direct philosophical antecedents of modern science came at the end of the 16th century. If I had to pick one single figure on whom to bestow the honor of founding modern science, it would have to be Galileo Galilei (1564–1642). His best-known achievement was his thorough refutation of the Ptolemaic geocentric (Earth-centered) theory of the heavens. But he did more than just insist that scholars observe things rather than rely on metaphysical dogma to explain them. He developed the idea of the experiment by causing things to happen (rolling balls down differently inclined planes, for example, to see how fast they go) and measuring the results.

Galileo became professor of mathematics at the University of Padua in 1592 when he was just 28. He developed a new method for making lenses and used the new technology to study the motions of the planets. He concluded that the sun (as Copernicus claimed), not the Earth (as the ancient scholar Ptolemy had claimed) was at the center of the solar system.

This was one more threat to their authority that Roman church leaders didn’t need at the time. They already had their hands full, what with breakaway factions in the Reformation and other political problems. The church reaffirmed its official support for the Ptolemaic theory, and in 1616 Galileo was ordered not to espouse either his refutation of it or his support for the Copernican heliocentric (sun-centered) theory of the heavens.

Galileo waited 16 years and published the book that established science as an effective method for seeking knowledge. The book’s title was Dialogue Concerning the Two Chief World Systems, Ptolemaic and Copernican, and it still makes fascinating reading (Galilei 1967 [1632], 1997 [1632]). Between the direct observational evidence that he had gathered with his telescopes and the mathematical analyses that he developed for making sense of his data, Galileo hardly had to espouse anything. The Ptolemaic theory was simply rendered obsolete.

In 1633, Galileo was convicted by the Inquisition for heresy and disobedience. He was ordered to recant his sinful teachings and was confined to house arrest until his death in 1642. He nearly published and perished. For the record, in 1992, Pope John Paul II reversed the Roman Catholic Church’s 1616 ban on teaching the Copernican theory and apologized for its condemnation of Galileo.

Bacon and Descartes

Two other figures are often cited as founders of modern scientific thinking: Francis Bacon (1561–1626) and Rene´ Descartes (1596–1650). Bacon is known for his emphasis on induction, the use of direct observation to confirm ideas and the linking together of observed facts to form theories or explanations of how natural phenomena work. Bacon correctly never told us how to get ideas or how to accomplish the linkage of empirical facts. Those activities remain essentially humanistic—you think hard (box 1.1).

BOX 1.1

O N I N D U C T I O N A N D D E D U C T I O N

There are two great epistemological approaches in all research: induction and deduction. In its idealized form, inductive research involves the search for pattern from observation and the development of explanations—theories—for those patterns through a series of hypotheses. The hypotheses are tested against new cases, modified, retested against yet more cases, and so on, until saturation occurs—that is, new cases stop requiring more testing. In its idealized form, deductive research starts with theories (derived from common sense, from observation, or from the literature) and hypotheses derived from theories, and then moves on to observations—which either confirm or falsify the hypotheses.

Real research is never purely inductive or purely deductive. In general, the less we know about a research problem, the more inductive we’ll be—the more we let observation be our guide—and the more we know about a problem, the more deductive we’ll be. Exploratory research is, therefore, likely to be pretty inductive, while confirmatory research is likely to be deductive.

When I started working with the N^˜ a¨ hn˜ u of central Mexico, for example, I wondered why so many parents wanted their children not to learn how to read and write N^˜ a¨ hn˜ u in school. As I became aware of the issue, I started asking everyone I talked to about it. With each new interview, pieces of the puzzle fell into place. This was a really, really inductive approach. After a while, as I came to understand the problem (it’s a long, sad story, repeated across the world by indigenous people who have learned to devalue their own cultures) I started right off by asking people about my hunches. In other words, I switched to a really, really deductive approach.

It’s messy, but this paradigm for building knowledge—the continual combination of inductive and deductive research—is used by scholars across the humanities and the sciences alike and has proved itself, over thousands of years. If we know anything about how and why stars explode or about how HIV is transmitted or about why women lower their fertility when they enter the labor market, it’s because of this combination of effort. Human experience—the way real people experience real events—is endlessly interesting because it is endlessly unique, and so, in a way, the study of human experience is always exploratory, and is best done inductively. On the other hand, we also know that human experience is patterned. A migrant from Mexico who crosses the U.S. border one step ahead of the authorities lives through a unique experience and has a unique story to tell, but 20 such stories will almost certainly reveal similarities.

To Bacon goes the dubious honor of being the first ‘‘martyr of empiricism.’’ In March 1626, at the age of 65, Bacon was driving through a rural area north of London. He had noticed earlier that both cold and fire impeded putrefaction (Bacon 1902 [1620]:137). To test his observation, he stopped his carriage, bought a hen from a local resident, killed the hen, and stuffed it with snow. Bacon was right—the cold snow did keep the bird from rotting—but he himself caught bronchitis and died a month later (Lea 1980).

Descartes didn’t make any systematic, direct observations—he did neither fieldwork nor experiments—but in his Discourse on Method (1960 [1637]) and particularly in his monumental Meditations (1993 [1641]), he distinguished between the mind and all external material phenomena—matter—and argued for what is called dualism in philosophy, or the independent existence of the physical and the mental world. Descartes also outlined clearly his vision of a universal science of nature based on direct experience and the application of reason—that is, observation and theory.

Newton

Isaac Newton (1643–1727) pressed the scientific revolution at Cambridge University. He invented calculus and used it to develop celestial mechanics and other areas of physics. Just as important, he devised the hypothetico-deductive model of science that combines both induction (empirical observation) and deduction (reason) into a single, unified method (Toulmin 1980).

In this model, which more accurately reflects how scientists actually conduct their work, it makes no difference where you get an idea: from data, from a conversation with your brother-in-law, or from just plain, hard, reflexive thinking. What matters is whether you can test your idea against data in the real world. This model seems rudimentary to us now, but it is of fundamental importance and was quite revolutionary in the late 17th century (Further Reading: history of science).

SCIENCE, MONEY, AND WAR

The scientific approach to knowledge was established just as Europe began to experience the growth of industry and the development of large cities. Those cities were filled with uneducated factory laborers. This created a need for increased productivity in agriculture among those not engaged in industrial work.

Optimism for science ran high, as it became obvious that the new method for acquiring knowledge about natural phenomena promised bigger crops, more productive industry, and more successful military campaigns. The Royal Society in England has its roots in meetings among a group of philosophers in London in 1644 who did experiments (much like a club . . . they paid dues for the experiments).

One of the leaders of that group was John Wilkins. In 1648, he published Mathematicall Magick, a book about the benefit of science in developing new technology, ‘‘particularly for such Gentlemen as employ their Estates in those chargeable Adventures of Draining Mines, Coalpits, etc.’’ The organizing mandate for the French Academy of Science in 1666 included a modest proposal to study ‘‘the explosive force of gunpowder enclosed (in small amounts) in an iron or very thick copper box’’ (Easlea 1980:207, 216).

As the potential benefits of science became evident, political support increased across Europe. More scientists were produced; more university posts were created for them to work in. More laboratories were established at academic centers. Journals and learned societies developed as scientists sought more outlets for publishing their work. Sharing knowledge through journals made it easier for scientists to do their own work and to advance through the university ranks. Publishing and sharing knowledge became a material benefit, and the behaviors were soon supported by a value, a norm.

The norm was so strong that European nations at war allowed enemy scientists to cross their borders freely in pursuit of knowledge. In 1780, Reverend Samuel Williams of Harvard University applied for and received a grant from the Massachusetts legislature to observe a total eclipse of the sun predicted for October 27. The perfect spot, he said, was an island off the coast of Massachusetts.

Unfortunately, Williams and his party would have to cross Penobscot Bay. The American Revolutionary War was still on, and the bay was controlled by the British. The speaker of the Massachusetts House of Representatives, John Hancock, wrote a letter to the commander of the British forces, saying ‘‘Though we are politically enemies, yet with regard to Science it is presumable we shall not dissent from the practice of civilized people in promoting it’’ (Rothschild 1981, quoted in Bermant 1982:126). The appeal of one ‘‘civilized’’ person to another worked. Williams got his free passage (box 1.2).

BOX 1.2

C A P T A I N S T A N L E Y G E T S I N S T R U C T I O N S

In 1846, the great naturalist Thomas Huxley set sail from Plymouth, England, to Australia on Her Majesty’s ship, Rattlesnake. The expedition, to map the Torres Straits and to report on discoveries of scientific interest, would be gone for 4 years. The Admiralty Commission gave the captain of the ship, Owen Stanley, strict instructions to:

refrain from any act of aggression towards the vessels or settlements of any nation with which we may be at war, as expeditions employed on behalf of discovery and science have always been considered by all civilised communities as acting under a general safeguard. [quoted in Mitchell 1913:14]

THE DEVELOPMENT OF SOCIAL SCIENCE: FROM NEWTON TO ROUSSEAU

It is fashionable these days to say that social science should not imitate physics. As it turns out, physics and social science were developed at about the same time, and on the same philosophical basis, by two friends, Isaac Newton and John Locke (1632–1704). It would not be until the 19th century that a formal program of applying the scientific method to the study of humanity would be proposed by Auguste Comte, Claude-Henri de Saint-Simon, Adolphe Que´telet, and John Stuart Mill (more about them in a bit). But Locke understood that the rules of science applied equally to the study of celestial bodies (what Newton was interested in) and to human behavior (what Locke was interested in).

In his An Essay Concerning Human Understanding (1996 [1690]), Locke reasoned that because we cannot see everything and because we cannot even record perfectly what we do see, some knowledge will be closer to the truth than will other knowledge. Prediction of the behavior of planets might be more accurate than prediction of human behavior, but both predictions should be based on better and better observation, measurement, and reason (see Nisbet 1980; Woolhouse 1996).

Voltaire, Condorcet, and Rousseau

The legacy of Descartes, Galileo, and Locke was crucial to the 18th-century Enlightenment and to the development of social science. Voltaire (Franc¸ois Marie Arouet, 1694– 1778) was an outspoken proponent of Newton’s nonreligious approach to the study of all natural phenomena, including human behavior (Voltaire 1967 [1738]). In several essays, Voltaire introduced the idea of a science to uncover the laws of history. This was to be a science that could be applied to human affairs and enlightened those who governed so that they might govern better.

Other Enlightenment figures had quite specific ideas about the progress of humanity. Marie Jean de Condorcet (1743–1794) described all of human history in 10 stages, beginning with hunting and gathering, and moving up through pastoralism, agriculture, and several stages of Western states. The ninth stage, he reckoned, began with Descartes and ended with the French Revolution and the founding of the republic. The last stage was the future, reckoned as beginning with the French Revolution.

Jean-Jacques Rousseau (1712–1778), by contrast, believed that humanity had started out in a state of grace, characterized by equality of relations, but that civilization, with its agriculture and commerce, had corrupted humanity and led to slavery, taxation, and other inequalities. Rousseau was not, however, a raving romantic, as is sometimes supposed. He did not advocate that modern people abandon civilization and return to hunt their food in the forests. Rousseau held that the state embodied humanity’s efforts, through a social contract, to control the evils brought about by civilization. In his classic work On the Social Contract, Rousseau (1988 [1762]) laid out a plan for a state-level society based on equality and agreement between the governed and those who govern.

The Enlightenment philosophers, from Bacon to Rousseau, produced a philosophy that focused on the use of knowledge in service to the improvement of humanity, or, if that weren’t possible, at least to the amelioration of its pain. The idea that science and reason could lead humanity toward perfection may seem naive to some people these days, but the ideas of John Locke, Jean Jacques Rousseau, and other Enlightenment figures were built into the writings of Thomas Paine (1737–1809) and Thomas Jefferson (1743–1826), and were incorporated into the rhetoric surrounding rather sophisticated events—like the American and French Revolutions (Further Reading: history of social science).

EARLY POSITIVISM: QUE^´ TELET, SAINT-SIMON, COMTE

The person most responsible for laying out a program of mechanistic social science was Auguste Comte (1798–1857). In 1824, he wrote: ‘‘I believe that I shall succeed in having it recognized . . . that there are laws as well defined for the development of the human species as for the fall of a stone’’ (quoted in Sarton 1935:10).

Comte could not be bothered with the empirical research required to uncover the Newtonian laws of social evolution that he believed existed. He was content to deduce the social laws and to leave ‘‘the verification and development of them to the public’’ (1875–1877, III:xi; quoted in Harris 1968).

Not so Adolphe Que´telet (1796–1874), a Belgian astronomer who turned his skills to both fundamental and applied social research. He developed life expectancy tables for insurance companies and, in his book A Treatise on Man (1969 [1842]), he presented statistics on crime and mortality in Europe. The first edition of that book (1835) carried the audacious subtitle ‘‘Social Physics,’’ and, indeed, Que´telet extracted some very strong generalizations from his data. He showed that, for the Paris of his day, it was easier to predict the proportion of men of a given age who would be in prison than the proportion of those same men who would die in a given year. ‘‘Each age [cohort]’’ said Que´telet, ‘‘paid a more uniform and constant tribute to the jail than to the tomb’’ (1969 [1842]:viii).

Despite Que´telet’s superior empirical efforts, he did not succeed in building a following around his ideas for social science. But Claude-Henri de Saint-Simon (1760–1825) did, and he was apparently quite a figure. He fought in the American Revolution, became wealthy in land speculation in France, was imprisoned by Robespierre during the French Revolution, studied science after his release, and went bankrupt living flamboyantly.

Saint-Simon’s arrogance must have been something. He proposed that scientists become priests of a new religion that would further the emerging industrial society and would distribute wealth equitably. Saint-Simon’s narcissistic ideas were taken up by industrialists after his death in 1825, but the movement broke up in the early 1830s, partly because its treasury was impoverished by paying for some monumental parties (see Durkheim 1958).

Saint-Simon may have been the originator of the positivist school of social science, but it was Comte who developed the idea in a series of major books. Comte tried to forge a synthesis of the great ideas of the Enlightenment—the ideas of Kant, Hume, and Voltaire—and he hoped that the new science he envisioned would help to alleviate human suffering. Between 1830 and 1842, Comte published a six-volume work on what he called positive philosophy, in which he proposed his famous ‘‘law of three stages’’ through which knowledge developed (see Comte 1877, 1974).

In the first stage of human knowledge, said Comte, phenomena are explained by invoking the existence of capricious gods whose whims can’t be predicted by human beings. Comte and his contemporaries proposed that religion itself evolved, beginning with the worship of inanimate objects (fetishism) and moving up through polytheism to monotheism. But any reliance on supernatural forces as explanations for phenomena, said Comte, even a modern belief in a single deity, represented a primitive and ineffectual stage of human knowledge.

Next came the metaphysical stage, in which explanations for observed phenomena are given in terms of ‘‘essences,’’ like the ‘‘vital forces’’ commonly invoked by biologists of the time. The so-called positive stage of human knowledge is reached when people come to rely on empirical data, reason, and the development of scientific laws to explain phenomena. Comte’s program of positivism, and his development of a new science he called ‘‘sociology,’’ is contained in his four-volume work System of Positive Polity (1875–1877).

I share many of the sentiments expressed by the word ‘‘positivism,’’ but I’ve never liked the word itself. I suppose we’re stuck with it. Here is John Stuart Mill (1866) explaining the sentiments of the word to an English-speaking audience: ‘‘Whoever regards all events as parts of a constant order, each one being the invariable consequent of some antecedent condition, or combination of conditions, accepts fully the Positive mode of thought’’ (p. 15) and ‘‘All theories in which the ultimate standard of institutions and rules of actions was the happiness of mankind, and observation and experience the guides . . . are entitled to the name Positive’’ (p. 69).

Mill thought that the word ‘‘positive’’ was not really suited to English and would have preferred to use ‘‘phenomenal’’ or ‘‘experiential’’ in his translation of Comte. I wish Mill had trusted his gut on that one.

Comte’s Excesses

Comte wanted to call the new positivistic science of humanity ‘‘social physiology,’’ but Saint-Simon had used that term. Comte tried out the term ‘‘social physics,’’ but apparently dropped it when he found that Que´telet was using it, too. The term ‘‘sociology’ became somewhat controversial; language puritans tried for a time to expunge it from the literature on the grounds that it was a bastardization—a mixture of both Latin (societas) and Greek (logo) roots. Despite the dispute over the name, Comte’s vision of a scientific discipline that both focused on and served society found wide support.

Unfortunately, Comte, like Saint-Simon, had more in mind than just the pursuit of knowledge for the betterment of humankind. Comte envisioned a class of philosophers who, with support from the state, would direct all education. They would advise the government, which would be composed of capitalists ‘‘whose dignity and authority,’ explained John Stuart Mill, ‘‘are to be in the ratio of the degree of generality of their conceptions and operations—bankers at the summit, merchants next, then manufacturers, and agriculturalists at the bottom’’ (1866:122).

It got worse. Comte proposed his own religion; condemned the study of planets that were not visible to the naked eye; and advocated burning most books except for a hundred or so of the ones that people needed to become best educated. ‘‘As his thoughts grew more extravagant,’’ Mill tells us, Comte’s ‘‘self-confidence grew more outrageous. The height it ultimately attained,’’ Mill continued, ‘‘must be seen, in his writings, to be believed’’ (p. 130).

Comte attracted a coterie of admirers who wanted to implement the master’s plans. Mercifully, they are gone (we hope), but for many scholars, the word ‘‘positivism’’ still carries the taint of Comte’s outrageous ego.

The Activist Legacy of Comte’s Positivism

Despite Comte’s excesses, there were three fundamental ideas in his brand of positivism that captured the imagination of many scholars in the 19th century and continue to motivate many social scientists, including me. The first is the idea that the scientific method is the surest way to produce knowledge about the natural world. The second is that scientifically produced knowledge is effective—it lets us control nature, whether we’re talking about the weather, or disease, or our own fears, or buying habits. And the third is that effective knowledge can be used to improve human lives. As far as I’m concerned, those ideas haven’t lost any of their luster.

Some people are very uncomfortable with this ‘‘mastery over nature’’ metaphor. When all is said and done, though, few people—not even the most outspoken critics of science— would give up the material benefits of science. For example, one of science’s great triumphs over nature is antibiotics. We know that overprescription of those drugs eventually sets the stage for new strains of drug-resistant bacteria, but we also know perfectly well that we’re not going to stop using antibiotics. We’ll rely (we hope) on more science to come up with better bacteria fighters.

Air conditioning is another of science’s triumphs over nature. In Florida, where I live, there is constant criticism of overdevelopment. But try getting middle-class people in my state to give up air conditioning for even a day in the summer and you’ll find out in a hurry about the weakness of ideology compared to the power of creature comforts. If running air conditioners pollutes the air or uses up fossil fuel, we’ll rely (we hope) on more science to solve those problems, too.

TECHNOLOGY AND SCIENCE

We are accustomed to thinking about the success of the physical and biological sciences, but not about the success of the social sciences. Ask 500 people, as I did in a telephone survey, to list ‘‘the major contributions that science has made to humanity’’ and there is strong consensus: Cures for diseases, space exploration, computers, nuclear power, satellite telecommunications, television, automobiles, artificial limbs, and transplant surgery head the list. Not one person—not one—mentioned the discovery of the dual helix structure of DNA or Einstein’s theory of relativity.

In other words, the contributions of science are, in the public imagination, technologies—the things that provide the mastery over nature I mentioned.

Ask those same people to list ‘‘the major contributions that the social and behavioral sciences have made to humanity’’ and you get a long silence on the phone, followed by a raggedy list, with no consensus.

I want you to know, right off the bat, that social science is serious business and that it has been a roaring success, contributing mightily to humanity’s global effort to control nature. Everyone in science today, from astronomy to zoology, uses probability theory and the array of statistical tools that have developed from that theory. It is all but forgotten that probability theory was applied social science from the start. It was developed in the 17th century by mathematicians Pierre Fermat (1601–1665) and Blaise Pascal (1623– 1662) to help people do better in games of chance, and it was well established a century later when two other mathematicians, Daniel Bernoulli (1700–1782) and Jean D’Alambert (1717–1783), debated publicly the pros and cons of large-scale inoculations in Paris against smallpox.

In those days (before Edward Jenner’s breakthrough in 1798), inoculations against smallpox involved injecting small doses of the live disease. There was a substantial risk of death from the inoculation (about 1-in-200), but the disease was ravaging cities in Europe and killing people by the thousands. The problem was to assess the probability of dying from smallpox versus dying from the vaccine.

This is one of the earliest uses of I have found of social science and probability theory in the making of state policy, but there were soon to be many more. One of them is state lotteries—taxes on people who are bad at math. Another is social security.

In 1889, Otto von Bismarck came up with a pension plan for retired German workers. Based on sound social science data, Bismarck’s minister suggested that 70 would be just the right age for retirement. At that time, the average life expectancy in Germany was closer to 50, and just 30% of children born then could expect to live to 70. Germany lowered the retirement age to 65 in 1916, by which time, life expectancy had edged up a bit—to around 55 (Max-Planck Institute 2002). In 1935, when the Social Security system was signed into law in the United States, Germany’s magic number 65 was adopted as the age of retirement. White children born that year in the United States had an average life expectancy of about 63; for black children it was about 51 (SAUS 1947:table 88).

Today, life expectancy in the highly industrialized nations is close to 80—fully 30 years longer than it was 100 years ago—and social science data are being used more than ever in the development of public policy. How much leisure time should we have? What kinds of tax structures are needed to support a medical system that caters to the needs of 80- somethings, when birthrates are low and there are fewer working adults to support the retirement of the elderly?

The success of social science is not all about probability theory and risk assessment. Fundamental breakthroughs by psychologists in understanding the stimulus-response mechanism in humans have made possible the treatment and management of phobias, bringing comfort to untold millions of people. Unfortunately, the same breakthroughs have brought us wildly successful attack ads in politics and millions of adolescents becoming hooked on cigarettes. I never said you’d like all the successes of social science.

And speaking of great successes that are easy not to like. . . . In 1895, Frederick Winslow Taylor read a paper before the American Society of Mechanical Engineers, entitled ‘‘A piece-rate system.’’ This was the start of scientific management, which brought spectacular gains in productivity and profits—and spectacular gains in worker alienation as well. In 1911, F. B. Gilbreth studied bricklayers. He looked at things like where masons set up their pile of bricks and how far they had to reach to retrieve each brick. From these studies, he made recommendations on how to lessen worker fatigue, increase morale, and raise productivity through conservation of motion.

The method was an instant hit—at least among people who hired bricklayers. Before Gilbreth, the standard in the trade was 120 bricks per hour. After Gilbreth published, the standard reached 350 bricks per hour (Niebel 1982:24). Bricklayers, of course, were less enthusiastic about the new standards.

Just as in the physical and biological sciences, the application of social science knowledge can result in great benefits or great damage to humankind.

SOCIAL SCIENCE FAILURES

If the list of successes in the social sciences is long, so is the list of failures. School busing to achieve racial integration was based on scientific findings in a report by James Coleman (1966). Those findings were achieved in the best tradition of careful scholarship. They just happened to be wrong because the scientists involved in the study couldn’t anticipate ‘‘white flight’’—a phenomenon in which Whites abandoned cities for suburbs, taking much of the urban tax base with them and driving the inner cities further into poverty.

On the other hand, the list of failures in the physical and biological sciences is impressive. In the Middle Ages, alchemists tried everything they could to turn lead into gold. They had lots of people investing in them, but it just didn’t work. Cold fusion is still a dream that attracts a few hardy souls. And no one who saw the explosion of the space shuttle Challenger on live television in January 1986 will ever forget it.

There are some really important lessons from all this. (1) Science isn’t perfect but it isn’t going away because it’s just too successful at doing what people everywhere want it to do. (2) The sciences of human thought and human behavior are much, much more powerful than most people understand them to be. (3) The power of social science, like that of the physical and biological sciences, comes from the same source: the scientific method in which ideas, based on hunches or on formal theories, are put forward, tested publicly, and replaced by ideas that produce better results. (4) Social science knowledge, like that of any science, can be used to enhance our lives or to degrade them.

THE VARIETIES OF POSITIVISM

These days, positivism is often linked to support for whatever power relations happen to be in place. It’s an astonishing turnabout, because historically, positivism was linked to social activism. In The Subjection of Women (1869), John Stuart Mill advocated full equality for women, and Adolphe Que´telet, the Belgian astronomer whose study of demography and criminology carried the audacious title Social Physics (1969 [1835]), was a committed social reformer.

The legacy of positivism as a vehicle for social activism is clear in Jane Addams’s work with destitute immigrants at Chicago’s Hull House (1926), in Sidney and Beatrice Webb’s attack on the abuses of the British medical system (1910), in Charles Booth’s account of the living conditions of the poor in London (1902), and in Florence Nightingale’s (1871) assessment of death rates in maternity hospitals. (See McDonald [1993] for an extended account of Nightingale’s long-ignored research.)

The central position of positivism is that experience is the foundation of knowledge. We record what we experience—what we see others do, what we hear others say, what we feel others feel. The quality of the recording, then, becomes the key to knowledge. Can we, in fact, record what others do, say, and feel? Yes, of course we can. Are there pitfalls in doing so? Yes, of course there are. To some social researchers, these pitfalls are evidence of natural limits to a science of humanity; to others, like me, they are a challenge to extend the current limits by improving measurement. The fact that knowledge is tentative is something we all learn to live with.

LATER POSITIVISM: THE VIENNA CIRCLE

Positivism has taken some interesting turns. Ernst Mach (1838–1916), an Austrian physicist, took an arch-empiricist stance further than even Hume might have done himself: If you could not verify something, Mach insisted, you should question its existence. If you can’t see it, it isn’t there. This stance led Mach to reject the atomic theory of physics because, at the time, atoms could not be seen.

Discussion of Mach’s ideas was the basis of a seminar group that met in Vienna and Berlin during the 1920s and 1930s. The group, composed of mathematicians, philosophers, and physicists, came to be known as the Vienna Circle of logical positivists. They were also known as logical empiricists, and when social scientists today discuss positivism, it is often this particular brand that they have in mind (see Mach 1976).

The term logical empiricism better reflects the philosophy of knowledge of the members of the Vienna Circle than does logical positivism. Unfortunately, Herbert Feigl and Albert Blumberg used ‘‘logical positivism’’ in the title of their 1931 article in the Journal ofPhilosophy in which they laid out the program of their movement, and the name ‘‘positivism’’ stuck—again (L. D. Smith 1986).

The fundamental principles of the Vienna Circle were that knowledge is based on experience and that metaphysical explanations of phenomena were incompatible with science. Science and philosophy, they said, should attempt to answer only scientifically answerable questions. A question like ‘‘Was Mozart or Brahms the better composer?’’ can only be addressed by metaphysics and should be left to artists.

In fact, the logical positivists of the Vienna Circle did not see art—painting, sculpture, poetry, music, literature, and literary criticism—as being in conflict with science. The arts, they said, allow people to express personal visions and emotions and are legitimate unto themselves. Because poets do not claim that their ideas are testable expressions of reality, their ideas can be judged on their own merits as either evocative and insightful, or not. Therefore, any source of wisdom (like poetry) that generates ideas, and science, which tests ideas, are mutually supportive and compatible (Feigl 1980).

I find this eminently sensible. Sometimes, when I read a really great line of poetry, like Robert Frost’s line from The Mending Wall, ‘‘Good fences make good neighbors,’’ I think ‘‘How could I test that? Do good fences always make good neighbors?’’ When sheepherders fenced off grazing lands across the western United States in the 19th century, keeping cattle out of certain regions, it started range wars.

Listen to what Frost had to say about this in the same poem: ‘‘Before I built a wall I’d ask to know / What I was walling in or walling out, / And to whom I was like to give offence.’’ The way I see it, the search for understanding is a human activity, no matter who does it and no matter what epistemological assumptions they follow.

Understanding begins with questions and with ideas about how things work. When do fences make good neighbors? Why do women earn less, on average, for the same work as men in most industrialized countries? Why is Barbados’s birthrate falling faster than Saudi

Arabia’s? Why is there such a high rate of alcoholism on Native American reservations? Why do nation states, from Italy to Kenya, almost universally discourage people from maintaining minority languages? Why do public housing programs often wind up as slums? If advertising can get children hooked on cigarettes, why is public service advertising so ineffective in lowering the incidence of high-risk sex among adolescents?

INSTRUMENTAL POSITIVISM

The practice that many researchers today love to hate, however, is neither the positivism of Auguste Comte nor that of the Vienna Circle. It is, instead, what Christopher Bryant (1985:137) called instrumental positivism.

In his 1929 presidential address to the American Sociological Society, William F. Ogburn laid out the rules. In turning sociology into a science, he said, ‘‘it will be necessary to crush out emotion.’’ Further, ‘‘it will be desirable to taboo ethics and values (except in choosing problems); and it will be inevitable that we shall have to spend most of our time doing hard, dull, tedious, and routine tasks’’ (Ogburn 1930:10). Eventually, he said, there would be no need for a separate field of statistics because ‘‘all sociologists will be statisticians’’ (p. 6).

THE REACTION AGAINST POSITIVISM

That kind of rhetoric just begged to be reviled. In The Counter-Revolution of Science, Friedrich von Hayek (1952) laid out the case against the possibility of what Ogburn imagined would be a science of humanity. In the social sciences, Hayek said, we deal with mental phenomena, not with material facts. The data of the social sciences, Hayek insisted, are not susceptible to treatment as if they were data from the natural world. To pretend that they are is what he called ‘‘scientism.’’

Furthermore, said Hayek, scientism is more than just foolish. It is evil. The ideas of Comte and of Marx, said Hayek, gave people the false idea that governments and economies could be managed scientifically and this, he concluded, had encouraged the development of the communism and totalitarianism that seemed to be sweeping the world when he was writing in the 1950s (Hayek 1952:110, 206).

I have long appreciated Hayek’s impassioned and articulate caution about the need to protect liberty, but he was wrong about positivism, and even about scientism. Science did not cause Nazi or Soviet tyranny any more than religion caused the tyranny of the Crusades or the burning of witches in 17th-century Salem, Massachusetts. Tyrants of every generation have used any means, including any convenient epistemology or cosmology, to justify and further their despicable behavior. Whether tyrants seek to justify their power by claiming that they speak to the gods or to scientists, the awful result is the same. But the explanation for tyranny is surely neither religion nor science.

It is also apparent that an effective science of human behavior exists, no matter whether it’s called positivism or scientism or human engineering or anything else. However distasteful it may be to some, John Stuart Mill’s simple formula for a science applied to the study of human phenomena has been very successful in helping us understand (and control) human thought and behavior. Whether we like the outcomes is a matter of conscience, but no amount of moralizing diminishes the fact of success.

Today’s truths are tomorrow’s rubbish, in anthropology just as in physics, and no epistemological tradition has a patent on interesting questions or on good ideas about the answers to such questions. Several competing traditions offer alternatives to positivism in the social sciences. These include humanism, hermeneutics, and phenomenology (Further Reading: positivism).

Humanism

Humanism is an intellectual tradition that traces its roots to Protagoras’ (485–410 bc) famous dictum that ‘‘Man is the measure of all things,’’ which means that truth is not absolute but is decided by individual human judgment. Humanism has been historically at odds with the philosophy of knowledge represented by science.

Ferdinand C. S. Schiller (1864–1937), for example, was a leader of the European humanist revolt against positivism. He argued that as the method and contents of science are the products of human thought, reality and truth could not be ‘‘out there’’ to be found, as positivists assume, but must be made up by human beings (Schiller 1969 [1903]).

Wilhelm Dilthey (1833–1911) was another leader of the revolt against positivism in the social sciences. He argued that the methods of the physical sciences, although undeniably effective for the study of inanimate objects, were inappropriate for the study of human beings. There were, he insisted, two distinct kinds of sciences: the Geisteswissenschaften and the Naturwissenschaften—that is, the human sciences and the natural sciences. Human beings live in a web of meanings that they spin themselves. To study humans, he argued, we need to understand those meanings (Dilthey 1989 [1883]) (Further Reading: Dilthey).

Humanists, then, do not deny the effectiveness of science for the study of nonhuman objects, but emphasize the uniqueness of humanity and the need for a different (that is, nonscientific) method for studying human beings. Similarly, scientists do not deny the inherent value of humanistic knowledge. To explore whether King Lear is to be pitied as a pathetic leader or admired as a successful one is an exercise in seeking humanistic knowledge. The answer to the question cannot possibly be achieved by the scientific method.

In any event, finding the answer to the question is not important. Carefully examining the question of Lear, however, and producing many possible answers, leads to insight about the human condition. And that is important (box 1.3).

Hermeneutics

The ancient Greek god, Hermes (known as Mercury in the Roman pantheon—he of the winged hat), had the job of delivering and interpreting for humans the messages of the other gods. From this came the Greek word hermeneus, or interpreter, and from that comes our word hermeneutics, the continual interpretation and reinterpretation of texts.

Modern hermeneutics in social science is an outgrowth of the Western tradition of biblical exegesis. In that tradition, the Old and New Testaments are assumed to contain eternal truths, put there by an omnipotent creator through some emissaries—prophets, writers of the gospels, and the like. The idea is to continually interpret the words of those texts to understand their original meaning and their directives for living in the present (box 1.4).

The hermeneutic tradition has come into the social sciences with the close and careful study of all free-flowing texts. In anthropology, the texts may be myths or folk tales. The hermeneutic approach would stress that: (1) The myths contain some underlying meaning, at least for the people who tell the myths; and (2) It is our job to discover that meaning, knowing that the meaning can change over time and can also be different for subgroups within a society. Think, for example, of the stories taught in U.S. schools about Columbus’s voyages. The meaning of those stories may be quite different for Navajos, urban African Americans, Chicanos, and Americans of northern and central European descent.

BOX 1.3

T H E M A N Y K I N D S O F H U M A N I S M

Just as there are many competing definitions of positivism, so there are for humanism as well. Humanism is often used as a synonym for humanitarian or compassionate values and a commitment to the amelioration of suffering. The problem is that died-in-the-wool positivists can also be committed to humanitarian values. Counting the dead accurately in Darfur is a really good way to preserve outrage. We need more, not less, science, lots and lots more, and more humanistically informed science, to contribute more to the amelioration of suffering and the weakening of false ideologies—racism, sexism, ethnic nationalism—in the world.

Humanism sometimes means a commitment to subjectivity—that is, to using our own feelings, values, and beliefs to achieve insight into the nature of human experience. In fact, trained subjectivity is the foundation of clinical disciplines, like psychology, as well as the foundation of participant observation ethnography. It isn’t something apart from social science. (See Berg and Smith [1988] for a review of clinical methods in social research.)

Humanism sometimes means an appreciation of the unique in human experience. Writing a story about the thrill or the pain of giving birth, about surviving hand-to-hand combat, about living with AIDS, about winning or losing a long struggle with illness—or writing someone else’s story for them, as ethnographers often do—are not activities opposed to a natural science of experience. They are the activities of a natural science of experience.

The hermeneutic approach—the discovery of the meaning of texts through constant interpretation and reinterpretation—is easily extended to the study of any body of texts: sets of political speeches, letters from soldiers in battle to their families at home, transcriptions of doctor-patient interactions. The idea that culture is ‘‘an assemblage of texts’’ is the basis for the interpretive anthropology of Clifford Geertz (1973). And Paul Ricoeur, arguing that action, like the written word, has meaning to actors, extended the hermeneutic approach even to free-flowing behavior itself (1981, 2007). In fact, portable camcorders make it easy to capture the natural behavior of people dancing, singing, interacting over meals, telling stories, and participating in events. In chapter 18, we’ll look at how anthropologists apply the hermeneutic model to the study of culture (Further Reading: hermeneutics).

Phenomenology

Phenomenology is a branch of philosophy that emphasizes the direct experience of phenomena to determine their essences, the things that make them what they are. Gold, for example, has been a universal currency for centuries, but variations in its price are accidents of history, and do not reflect its essence. This distinction between essential and accidental properties of things was first made by Aristotle in his Metaphysics (especially Book VII) and has influenced philosophy ever since.

The philosophical foundations of phenomenology were developed by Edmund Husserl

BOX 1.4

B I B L I C A L H E R M E N E U T I C S

Rules for reconciling contradictions in scripture were developed by early Talmudic scholars, about a hundred years after the death of Jesus of Nazareth. For example, one of the rules was that ‘‘the meaning of a passage can be derived either from its context or from a statement later on in the same passage’’ (Jacobs 1995:236). Another was that ‘‘when two verses appear to contradict one another, a third verse can be discovered which reconciles them’’ (Jacobs 1995:236). Today, the 13 Talmudic rules for interpreting scripture remain part of the morning service among Orthodox Jews.

Scholars of the New Testament have used hermeneutic reasoning since the time of Augustine (354–430) to determine the order in which the three synoptic gospels (Mark, Mathew, and Luke) were written. They are called synoptic gospels because they are all synopses of the same events and can be lined up and compared for details. Whenever there is a discrepancy about the order of events, Mark and Mathew agree or Mark and Luke agree, but Mathew and Luke almost never agree against Mark. There are many theories about what caused this—including some that involve one or more of the gospels being derived from an undiscovered source. Research on this problem continues to this day (for a review, see Stein 1987).

Today, in the United States, constitutional law is a form of biblical hermeneutics. Jurists take it as their task to consider what the writers of each phrase in the U.S. Constitution meant when they wrote the phrase, and to interpret that meaning in light of current circumstances. It is exegesis on the U.S. Constitution that has produced entirely different interpretations across time about the legality of slavery, abortion, women’s right to vote, the government’s ability to tax income, and so on.

Although they have not influenced Western social science, there are long exegetical traditions in Islam (Abdul-Rahman 2003; Calder 1993), Hinduism (Sherma and Sharma 2008; Timm 1992), and other religions.

(1859–1938), who argued that the scientific method, appropriate for the study of physical phenomena, was inappropriate for the study of human thought and action (see Husserl 1964 [1907], 1999). Husserl was no antipositivist. What was needed, he said, was an approach that, like positivism, respects the data that we acquire through our senses but that is appropriate for understanding how human beings experience the world (Spiegelberg 1980:210). To do this requires putting aside—or bracketing—our biases so that we don’t filter other people’s experiences through our own cultural lens and can understand experiences as others experience them (Giorgi 1986; McNamara 2005:697; Moustakas 1994).

Husserl’s ideas were elaborated by Alfred Schutz, and Schutz’s version of phenomenology has had a major impact in social science, particularly in psychology but also in anthropology. When you study molecules, Schutz said, you don’t have to worry about what the world ‘‘means’’ to the molecules (1962:59). But when you try to understand the reality of a human being, it’s a different matter entirely. The only way to understand social reality, said Schutz, was through the meanings that people give to that reality. In a phenomenological study, the researcher tries to see reality through another person’s eyes.

Phenomenologists try to produce convincing descriptions of what they experience rather than explanations and causes. Good ethnography—a narrative that describes a culture or a part of a culture—is usually good phenomenology, and there is still no substitute for a good story, well told, especially if you’re trying to make people understand how the people you’ve studied think and feel about their lives (Further Reading: phenomenology).

ABOUT NUMBERS AND WORDS: THE QUALITATIVE/ QUANTITATIVE SPLIT

The split between the positivistic approach and the interpretive-phenomenological approach pervades the human sciences. In psychology and social psychology, most research is in the positivistic tradition, but much clinical work is in the interpretivist tradition because, as its practitioners cogently point out, it works. In sociology, there is a growing tradition of interpretive research, but most sociology is done from the positivist perspective.

In anthropology, the situation is a bit more complicated. Most anthropological data collection is done by fieldworkers who go out and stay out, watch and listen, take notes, and bring it all home. This makes anthropology a thoroughly empirical enterprise. But much of anthropological data analysis is done in the interpretivist tradition; some empirical anthropologists reject the positivist epistemological tradition, and other empirical anthropologists (like me) identify with that tradition.

Notice in the last two paragraphs the use of words like ‘‘approach,’’ ‘‘perspective,’’ ‘‘tradition,’’ and ‘‘epistemology.’’ Not once did I say that ‘‘research in X is mostly quantitative’’ or that ‘‘research in Y is mostly qualitative.’’ That’s because a commitment to an interpretivist or a positivist epistemology is independent of any commitment to, or skill for, quantification. Searching the Bible for statistical evidence to support the subjugation of women doesn’t turn the enterprise into science.

By the same token, at the early stages of its development, any science relies primarily on qualitative data. Long before the application of mathematics to describe the dynamics of avian flight, qualitative, fieldworking ornithologists did systematic observation and recorded (in words) data about such things as wing movements, perching stance, hovering patterns, and so on. Qualitative description is a kind of measurement, an integral part of the complex whole that comprises scientific research.

As sciences mature, they come inevitably to depend more and more on quantitative data and on quantitative tests of qualitatively described relations. But this never, ever lessens the need for or the importance of qualitative research in any science.

For example, qualitative research might lead us to say that ‘‘most of the land in Popotla´n is controlled by a minority.’’ Later, quantitative research might result in our saying ‘‘76% of the land in Popotla´n is controlled by 14% of the inhabitants.’’ The first statement is not wrong, but its sentiment is confirmed and made stronger by the second statement. If it turned out that ‘‘54% of the land is controlled by 41% of the inhabitants,’’ then the first part of the qualitative statement would still be true—more than 50% of the land is owned by less than 50% of the people, so most of the land is, indeed controlled by a minority—but the sentiment of the qualitative assertion would be rendered weak by the quantitative observations.

For anthropologists whose work is in the humanistic, phenomenological tradition, quantification is inappropriate. And for those whose work is in the positivist tradition, it is important to remember that numbers do not automatically make any inquiry scientific. In chapters 18 and 19, I’ll discuss how texts—words and pictures—can be collected and analyzed by scholars who identify with either the positivist or the interpretivist tradition.

In the rest of this book, you’ll read about methods for describing individuals and groups of people. Some of those methods involve library work, some involve controlled experiments, and some involve fieldwork. Some methods result in words, others in numbers. Never use the distinction between quantitative and qualitative as cover for talking about the difference between science and humanism. Lots of scientists do their work without numbers, and many scientists whose work is highly quantitative consider themselves humanists.

ETHICS AND SOCIAL SCIENCE

The biggest problem in conducting a science of human behavior is not selecting the right sample size or making the right measurement. It’s doing those things ethically, so you can live with the consequences of your actions. I’m not exaggerating about this. Ethics is part of method in science, just as it is in medicine, business, or any other part of life. For although philosophers discuss the fine points of whether a true science of human behavior is really possible, effective social science is being done all the time, and with rather spectacular, if sometimes disturbing, success.

In the mid-19th century, when Que´telet and Comte were laying down the program for a science of human affairs, no one could predict the outcome of elections, or help people through crippling phobias with behavior modification, or engineer the increased consumption of a particular brand of cigarettes. We may question the wisdom of engineering cigarette purchases in the first place, but the fact remains, we can do these things, we are doing these things, and we’re getting better and better at it all the time.

It hardly needs to be pointed out that the increasing effectiveness of science over the past few centuries has also given human beings the ability to cause greater environmental degradation, to spread tyranny, and even to cause the ultimate, planetary catastrophe through nuclear war. This makes a science of humanity even more important now than it has ever been before.

Consider this: Marketers in a midwestern city, using the latest supercomputers, found that if someone bought disposable diapers at 5 p.m., the next thing he or she was likely to buy was a six-pack of beer. So they set up a display of chips next to the disposable diapers and increased snack sales by 17% (Wilke 1992). At the time, 20 years ago, that was a breakthrough in the monitoring of consumer behavior. Today, every time you buy something on the Internet or download a computer program or a piece of music, you leave a trail of information about yourself and your consumer preferences. By tracking your purchases over time, and by sharing information about your buying behavior across websites, market researchers develop ads that are targeted just for you.

We need to turn our skills in the production of such effective knowledge to solving the problems of hunger, disease, poverty, war, environmental pollution, family and ethnic violence, and racism, among others. Social scientists, including anthropologists, can play an important role in social change by predicting the consequences of ethically mandated programs and by refuting false notions (such as various forms of racism) that are inherent in most popular ethical systems. This has been a hallmark of anthropology since Franz Boas’s devastating critique, a century ago, of racial theories about why some ethnic minorities in the United States were taller and healthier than others (Boas 1910b; Gravlee et al. 2003a, 2003b).

Don’t get me wrong. The people who discovered that fact about the six-packs and the diapers were good scientists, as are the people who design all those automated datacollection mechanisms for monitoring your behavior on the Internet. I’m not calling for rules to make all those scientists work on problems that I think are important. Scientists choose to study the things that industry and government pay for, and those things change from country to country and from time to time in the same country. Science has to earn its support by producing useful knowledge. What ‘‘useful’’ means, however, changes from time to time even in the same society, depending on all sorts of historical circumstances.

Suppose we agreed that ‘‘useful’’ means to save lives. AIDS is a terrible disease, but over three times as many people died in motor vehicle accidents in the United States in 2005 as died of AIDS—about 45,000 and 13,000 respectively (SAUS 2009:table 118). Should we spend three times more money teaching safe driving than we do teaching safe sex?

I think the answer is pretty clear. In a democracy, researchers and activists want the freedom to put their skills and energies to work on what they think is important. Fortunately, that’s just how it is, and, personally, I hope it stays just that way.

FURTHER READING

The Chomsky-Skinner debate: Chomsky (1969, 1972, 1977); MacCorquodale (1970); Palmer (2006); Stemmer (1990, 2004); Virue´s-Ortega (2006).

The norms of sciences: Ben-David and Sullivan (1975); Jasanoff et al. (1995); Merton (1970, 1973); Resnik (2007); Storer (1966).

The history of science: Porter (2003–2006). For the early history of science, see Sarton (1952–1959). See Drake (1978) and Finocchiaro (2005) for more on Galileo; see Cottingham (1999), Hausman and Hausman (1997), Markie (1986), Schuster (1977), and M. D. Wilson (1991) on Descartes.

The history of social science: S. Gordon (1991); McDonald (1994); Olson (1993); R. Smith (1997); Wagner (2001); Znaniecki (1963 [1952]).

Positivism: Bryant (1985). See Goldman (2002) on social science and policy in 19th-century Britain and see O’Connor (2001) on social science and poverty in the United States. See Turner (1986) on the history of methods in the social sciences.

Dilthey: Hodges (1952); Makkreel (1975).

Hermeneutics: Hoffman et al. (2005); Sherratt (2006); Zigon (2009).

Phenomenology: Elliott (2005); Moran (2000); Sokolowski (2000); Zahavi (2003).

The Foundations of Social Research

THE LANGUAGE OF SOCIAL RESEARCH

This chapter is about the fundamental concepts of social research: variables, measurement, validity, reliability, cause and effect, and theory. When you finish this chapter, you should understand the crucial role of measurement in science and the mutually supportive roles of data and ideas in the development of theory.

You should also have a new skill: You should be able to operationalize any complex human phenomenon, like ‘‘machismo’’ or ‘‘anomie’’ or ‘‘alienation’’ or ‘‘acculturation.’’ You should, in other words, be able to reduce any complex variable to a set of measurable traits.

By the end of this chapter, though, you should also become very critical of your new ability at operationalizing. Just because you can make up measurements doesn’t guarantee that they’ll be useful or meaningful. The better you get at concocting clever measurements for complex things, the more critical you’ll become of your own concoctions and those of others.

VARIABLES

A variable is something that can take more than one value. The values can be words or numbers. If you ask a woman how old she was at her first pregnancy, the answer will be a number (16 or 40, or whatever), but if you ask her about her religion, the answer will be a word (‘‘Muslim’’ or ‘‘Methodist’’).

Social research is based on defining variables, looking for associations among them, and trying to understand whether—and how—variation in one thing causes variation in another. Some common variables that you’ll find in social research are age, sex, ethnicity, race, education, income, marital status, and occupation.

A few of the hundreds of variables you’ll see in anthropological research include number of children by each of several wives in a polygynous household, distance from a clinic or a market or a source of clean water, blood pressure, and level of support for various causes (the distribution of clean needles to drug addicts, the new farmer’s co-op, rebels fighting in Eritrea, etc.).

Variables Have Dimensions

Variables can be unidimensional or multidimensional. The distance from Chicago to Albuquerque can be expressed in driving time or in miles, but no matter how you measure it, distance is expressed as a straight line and straight lines are one dimensional. You can see this in figure 2.1.

Boston Denver

Three days' driving

Boston Denver

1,863 miles

FIGURE 2.1.

Two ways to measure distance.

If we add Miami, we have three distances: Chicago-Miami, Chicago-Albuquerque, Albuquerque-Miami. One dimension isn’t enough to express the relation among three cities. We have to use two dimensions. Look at figure 2.2.

FIGURE 2.2.

Three points create two dimensions.

The two dimensions in figure 2.2 are up-down and right-left, or North-South and East-West. If we add Nairobi to the exercise, we’d either have to add a third dimension (straight through the paper at a slight downward angle from Albuquerque), or do what Gerardus Mercator (1512–1594) did to force a three-dimensional object (the Earth) into a two-dimensional picture. Mercator was able to project a sphere in two dimensions, but at the cost of distortion at the edges. This is why, on a map of the world, Greenland (an island of 840,000 square miles), looks the same size as China (a land mass of about 3.7 million square miles).

Height, weight, birth order, age, and marital status are unidimensional variables and are relatively easy to measure. By contrast, political orientation (being conservative or liberal) is multidimensional and is, therefore, a lot more difficult to measure. We often talk about political orientation as if it were unidimensional, with people lying somewhere along a line between strictly conservative and strictly liberal. But if you think about it, people can be liberal about some dimensions of life and conservative about others. For example, you might agree strongly with the statement that ‘‘men and women should get equal pay for equal work’’ and also with the statement that ‘‘a strong military is necessary to defend freedom in America.’’ These statements test political orientation about domestic economic policy and foreign policy—two of the many dimensions of political orientation.

Even something as seemingly straightforward as income is multidimensional. To measure the annual income of retired Americans in Florida, for example, you have to account for social security benefits, private pension funds, gifts from children and other kin, gambling winnings, tax credits, interest on savings, wages paid entirely in cash (including tips), food stamps. . . .

And don’t think it’s easier in out-of-the-way communities around the world. If you think it’s tough assessing the amount that a waitress earns from tips, try assessing the amount a family in Haiti gets from people who are working in Miami and sending money home.

In chapter 11, I’ll discuss the building of scales and how to test for the unidimensionality of variables.

Simplifying Variables: Race and Gender

In the United States, at least, race is treated (by academics as well as by people in general) as a dichotomous variable, with two values: black and white. This makes race easy to measure and, in fact, we’ve learned a lot by making the measurement simple. For example, any man in the United States who is labeled ‘‘black’’ is about seven times more likely to be the victim of homicide than is any man labeled ‘‘white.’’ Black babies are about two-and-a-half times more likely to die in infancy than are white babies, and people labeled ‘‘black’’ are two-and-a-half times more likely as people labeled ‘‘white’’ to be poor (which meant $20,614 for a family of four in 2006) (SAUS 2009: tables 100, 111, 689).

Still, we know that there are gradations of skin color besides black and white, so it’s reasonable to ask whether people who are more black are more likely to be a victim of homicide, to die in infancy, to be poor, etc. Around 1970, medical researchers began to find a relation in the United States between darkness of skin color and blood pressure among people labeled ‘‘Blacks’’ (see Boyle 1970; Harburg et al. 1978). The darker the skin, the higher the blood pressure was likely to be.

Later, researchers began to find that education and social class were more important predictors of high blood pressure among Blacks than was darkness of skin color (see Keil, Sandifer et al. 1981; Keil, Tyroler et al. 1977). This meant that darker-skinned people were more likely to be the victims of discrimination and, as a consequence, uneducated and poor. Poverty causes stress and poor diet, both of which are direct causes of high blood pressure.

But suppose we treated skin color as the continuous variable it really is rather than as a dichotomous variable? Clarence Gravlee (2002b; Gravelee et al. 2005) did this in his study of race and blood pressure in Puerto Rico. He measured skin color in two ways. First, he showed people a line with nine numbers on it and asked them to rate themselves from light to dark by telling him which number best described their skin color. Then he measured the color of people’s inner arm with a photospectrometer. The first measure is emic (what people think, themselves, about their color) and the second is etic (an objective, external measurement that doesn’t depend on what people think).

Now, etic skin color—the amount of melanin that people have in their skin, as measured by a photospectrometer—by itself doesn’t account for variation in blood pressure. But the difference between etic skin color and what people say their color is strongly associated with people’s blood pressure (Gravlee 2002b:182). The relationship between these variables is anything but simple. Poor people who rate themselves as having darker skin than they really have are likely to have higher blood pressure. For middle-class people, it’s the other way around: They are likely to have lower blood pressure when they rate their skin color as darker than it really is. The puzzle requires a lot more work, but this much is clear: Variation in blood pressure is not caused by melanin (Gravlee and Dressler 2005) (box 2.1).

Gender is another dichotomous variable (male and female) that is more complex than it seems. We usually measure gender according to the presence of male or female sexual characteristics. Then we look at the relation between the presence of those characteristics and things like income, level of education, amount of labor migration, attitudes to various social issues, aptitude for math, success in certain jobs, and so on. But if you think about it, we’re not interested in whether differences in human anatomy predict any of these things. What we really want to know is how being more male or more female (socially and

BOX 2.1

E V E R Y R E S E A R C H Q U E S T I O N H A S A N E T H I C A L C O M P O N E N T

It may not be possible for everyone who uses skin color as an independent variable to measure it with a photospectrometer (the gadgets are very expensive), but if we did this, we could assess whether white schoolteachers react more negatively to darker-skinned black children than they do to lighter-skinned black children, and if so, by how much. This would help us account for some of the variation in black children’s school scores as a function of teacher reaction to skin color. This, in turn, would show how skin color leads to discrimination in education, how discrimination in education leads to poverty, and how all this leads to lowered life expectancy.

We already know that Whites live longer than Blacks do. Making skin color a continuous variable would help us learn how racism actually works, not just its consequences. If the benefits of such research are attractive, though, consider the risks. Racists might claim that our findings support their despicable ideas about the genetic inferiority of African Americans. Life insurance companies might start charging premiums based on amount of skin pigmentation. Even if the Supreme Court ruled against this practice, how many people would be hurt before the matter was adjudicated? As you can see, every research question has an ethical component.

psychologically) predicts attitudes about social issues, success in various jobs, and many other things—like the ability to secure agricultural credit, the ability to cope with widowhood, or health status in old age.

Sandra Bem (1974, 1979) developed a scale called the BSRI (Bem Sex Role Inventory) to measure sex-role identity. The scale consists of 60 words or phrases: 20 that represent what Americans in the early 1970s generally thought of as masculine traits (like independent and assertive); 20 that represented generally accepted feminine traits (like affectionate and sympathetic); and 20 that represented generally accepted gender-neutral traits (like tactful and happy). Respondents rate themselves on a scale of 1 to 7 on how much they think each trait applies to them. Depending on your score, you are either ‘‘sex typed’’ (displaying stereotyped feminine traits or masculine traits) or androgynous (getting a high score on both feminine and masculine traits) or undifferentiated (getting a low score on both feminine and masculine traits).

The BSRI has been used in hundreds of studies across many societies and, although ideas about typically masculine or feminine traits have changed in four decades, the work has produced many interesting results. In Finland, Sundvik and Lindeman (1993) applied the BSRI to 257 managers (159 men and 98 women) of a government-controlled transportation company. Each manager had rated a subordinate on 30 dimensions—things like the ability to get along with others, independence in getting the job done, willingness to implement innovations, and so on. The sex-typed female managers (the women who scored high on femaleness, according to the BSRI) rated their male subordinates more favorably than they rated their female subordinates. Similarly, the sex-typed male managers rated their female subordinates more favorably than they rated their male subordinates.

The bottom line, according to Sundvik and Lindeman: ‘‘Among persons whose selfconcepts are formed on the basis of gender, both the queen bee and the king ape syndromes are alive and well’’ (1993:8). Sex-typed managers discriminate against subordinates of the same sex.

Of course, traits thought to be masculine in one culture might be thought of as feminine in another. Aggressiveness is a trait widely viewed across many cultures to be desirable for men and boys and undesirable for women and girls. In Zimbabwe, however, 488 schoolteachers, half of whom were men, gave this trait their lowest desirability rating of the 20 masculine items in the BSRI (Wilson et al. 1990).

In Japan, Katsurada and Sugihara (1999) found that all 20 masculine traits in the BSRI were culturally appropriate, but that three of the classically 20 feminine traits in the scale (‘‘sensitive to the needs of others,’’ ‘‘understanding,’’ and ‘‘loyal’’) were inappropriate. (Loyalty, for example, is seen as a highly desirable trait for everyone in Japan, so it can’t be used in a test to distinguish between men and women.) Based on tests with 300 college students, Katsurada and Sugihara recommend substituting ‘‘conscientious,’’ ‘‘tactful,’’ and ‘‘happy’’ in the list of feminine adjectives when the BSRI is used in Japan. After nearly 40 years of research with the BSRI, we’ve learned a lot about the differences between men and women.

One thing we’ve learned is that those differences are much more complex than a biological dichotomy would make them appear to be. We’ve also learned that gender role differences are even more complex than Bem imagined. Choi and Fuqua (2003) looked at 23 validation studies of the BSRI and found that Bem’s inventory doesn’t fully capture the complexity of masculinity and femininity. But that just means that we’re learning more with each generation of researchers—exactly what we expect from a cumulative science (Further Reading: measuring gender across cultures).

Dependent and Independent Variables

Beginning in the 1840s, breakthroughs in sociology and anthropology produced insights into the impact of economic and political forces on demography. One practical result of all this work was life insurance. The way life insurance works is that you bet the company that you’ll die within 365 days. You answer a few questions (How old are you? Do you smoke? What do you do for a living? Do you fly a small plane?), and the company sets the odds—say, your $235 against the company’s promise to pay your heirs $100,000 if you win the bet and die within 365 days. But if you lose the bet and stay alive, they keep your $235, and next year you go through all this again, except that now the odds are raised against you to, say, your $300 against the company’s promise to pay your heirs a lot of money.

For insurance companies to turn a profit, they have to win more bets than they lose. They can make mistakes at the individual level, but in the aggregate (that is, averaging over all people) they have to predict longevity from things they can measure.

Longevity, then, is the dependent variable, because it depends on sex, education, occupation, etc. These latter are called independent variables because they are logically prior to, and therefore independent of, the dependent variable of longevity. How long you live doesn’t have any effect on your sex. In our earlier example, blood pressure was the dependent variable. There is no way skin color depends on a person’s blood pressure.

It’s not always easy to tell whether a variable is independent or dependent. Does high female infant mortality among Amazonian tribal people depend on high levels of warfare, or is it the other way around? Does high income depend on having a lot of land, or vice versa? Do inner-city adolescent girls get pregnant because they are poor, or . . .? Does the need for litigation stimulate the production of attorneys, or . . . ?

Failure to understand which of two variables depends on the other is the source of endless shenanigans. One of my teachers, Oscar Lewis (1961, 1965), described what he called a ‘‘culture of poverty’’ among slum dwellers in cities around the world. People who live in a culture of poverty, said Lewis, are not very future oriented. This plays out, he said, in their shopping for food every day and in never buying large economy sizes of anything. Lewis’s point was that truly poor people can’t invest in soap futures by buying large boxes of it. He saw a low level of expressed orientation toward the future, then, as the dependent variable and poverty as the independent variable.

Many people interpreted Lewis’s work as meaning exactly the opposite: that poverty is caused by a low level of future orientation. According to this topsy-turvy, victim-blaming reasoning, if poor people everywhere would just learn to save their money and invest in the future, then they could break the poverty cycle. Such reasoning may serve to create pointless programs to teach poor people how to save money they don’t have, but it doesn’t do much else.

In rural West Virginia, for example, there is a lot of teen pregnancy and many adolescents drop out of high school. Since the 1960s, according to Bickel et al. (1997), state policymakers in West Virginia have blamed these behaviors on the culture of poverty. The behaviors that state policymakers want so much to change, however, are caused by the continuing deterioration of economic and social conditions in rural communities. No amount of ‘‘educating’’ poor people about their bad habits will change the material circumstances that cause the so-called culture of poverty (box 2.2).

MEASUREMENT AND CONCEPTS

Variables are measured by their indicators, and indicators are defined by their values. Some variables, and their indicators, are easily observed and measured. Others are more conceptual. The difference is important.

Consider the variables race and gender again. If skin color can take one of two values (black or white), then to measure race you simply look at a person and decide which value to record. If you use secondary sexual characteristics as an indicator of gender, then to measure gender you look at a person and decide whether they are female or male.

In other words, measurement is deciding which value to record. That decision is prone to error. Some people whom you classify as white or black might be classified as black or white by another observer. And gender is even worse. Many people, both men and women, have ambiguous secondary sexual characteristics and many women wear what were once considered to be men’s clothes. Is Pat a man’s name or a woman’s? What about Chris? Leslie? Any of these indicators may lead you into making the wrong measurement—marking down a man or boy as a woman or girl, or vice versa.

Improving measurement in science means lowering the probability of and the amount of error. Light-skinned African Americans who cease to identify themselves ethnically as black persons count on those errors for what they hope will be upward economic mobility. Dark-skinned ‘‘Whites,’’ like some Americans of Mediterranean descent, sometimes complain that they are being ‘‘mistaken for’’ Blacks and discriminated against.

Race and gender are concepts or constructs. We have to make them up to study them. All variables are concepts, but some concepts, like height and weight, are easy to measure; other concepts like religious intensity, jealousy, compassion, willingness to accept new

BOX 2.2

T H E E D U C A T I O N A L M O D E L O F S O C I A L C H A N G E

This educational model of social change is a lesson in confusion about dependent and independent variables. The model is based on the attractive idea that, because the last thing that happens before an action is a thought, if you want to create better actions then you need to create better thoughts. In other words, if you want to change people’s behavior, you have to change how they think: Teach women in India the value of small families so they’ll use birth control to prevent unwanted pregnancies; teach Kenyans why it’s important to use bed nets to prevent malaria; teach farmers across the world the importance of washing their hands after handling manure and before preparing or eating food.

The educational model is the basis for one of the world’s biggest industries— social change and development—but the model is mostly ineffective because behavioral change (the supposed dependent variable) doesn’t usually depend on education (the supposed independent variable). In fact, across the developing world, when women have access to well-paying jobs outside the home, they tend to lower their fertility. Once that happens, they encourage their daughters to stay in school longer (Handwerker 1989). Education doesn’t just cause jobs to happen. Instead, jobs for women in one generation cause education in the next. (I’ll have more to say on fertility control and the educational model of behavioral change in chapter 3, when I discuss the role of theory in the development of research questions.)

agricultural technologies, and tolerance for foreign fieldwork are complex and difficult to measure.

We are led to defining constructs by our experience: Some people just seem more religiously intense than others, more jealous than others, more tolerant of foreign fieldwork than others, etc. We verify our intuition about conceptual variables by measuring them, or by measuring their results.

Suppose you put an ad in the paper that says: ‘‘Roommate wanted. Easy-going, nonsmoker preferred.’’ When people answer the ad you can look at their fingers and smell their clothes to see if they smoke. But you have to ask people a series of indicator questions to gauge their easy-goingness.

Similarly, if you are doing fieldwork in a Peruvian highland village and you want to predict who among the villagers is predisposed to migrate to the coast in search of work, you will want to measure that predisposition with a series of indicators. In this case, the indicators can be answers to questions (‘‘Have you ever thought about migrating?’’). Or they might be observable facts (Does a person have a close relative who has already migrated?). Or they might be a combination of these.

It may be easier to measure some concepts than others, but all measurement is difficult. People have worked for centuries to develop good instruments for measuring things like temperature. And if it’s difficult to measure temperature (a concept, after all, backed up by time-tested theories), how do you measure future orientation or machismo? Measuring variables like these is one of our biggest challenges because these variables are mostly what we’re interested in.

One of the most famous variables in all of social science is ‘‘socioeconomic status’’ (SES). Measuring it is no easy task. You can use income as one indicator, but there are many wealthy people who have low SES (the so-called nouveau riche), and many relatively low-income people who have high SES (think of those down-at-the-heels nobles in England who have to open their castles to tourists to make ends meet).

You can add ‘‘level of education’’ to income as an indicator, but that still won’t be enough in most societies of the world to get at something as multidimensional as SES. You can add occupation, father’s occupation, number of generations in a community, and so on, depending on the group you are studying, and you still might wind up dissatisfied with the result if your measure fails to predict some dependent variable of interest.

And, as you saw with the Bem androgyny scale earlier, indicators of any concept may vary from culture to culture. This doesn’t mean that measurement is impossible. It means that you have to test (and, if necessary, adapt) every measure of every variable in every new culture where you want to use it.

CONCEPTUAL AND OPERATIONAL DEFINITIONS

Although most of the interesting variables in social science are concepts, some of our most important concepts are not variables. The concept of ‘‘positivism’’ is not a variable, but the concept of ‘‘philosophies of science’’ is a variable, and positivism is one member of the list of those philosophies. The concept of ‘‘love’’ is not a variable, but the concept of ‘‘being in love or not’’ is one. The concept of ‘‘culture’’ is not a variable, but the concept of ‘‘intensity of feeling of belonging to a particular culture’’ is one. The concept of ‘‘attitude’’ is not a variable, but the concept of ‘‘attitude toward clitoridectomy as a violation of human rights’’ implies a variable with at least two attributes, support and nonsupport.

CONCEPTUAL DEFINITIONS

There are two ways to define variables—conceptually and operationally. Conceptual definitions are abstractions, articulated in words, that facilitate understanding. They are the sort of definitions we see in dictionaries, and we use them in everyday conversation to tell people what we mean by some term or phrase. Operational definitions consist of a set of instructions on how to measure a variable that has been conceptually defined.

Suppose I tell you that ‘‘Alice and Fred just moved to a spacious house.’’ Nice concept. You ask: ‘‘What do you mean by ‘spacious’?’’ and I say: ‘‘You know, big rooms, high ceilings.’’

If that isn’t enough for you, we’ll have to move from a conceptual definition of ‘‘spacious’’ to an operational one. We’ll have to agree on what to measure: Do we count the screened-in porch and the garage or just the interior living space? Do we count the square footage or the cubic footage? That is, do we get a measure of the living surface, or some measure of the ‘‘feeling of spaciousness’’ that comes from high ceilings? Do we measure the square footage of open space before or after the furniture and appliances go in? If we had to agree on things like this for every concept, ordinary human discourse would come to a grinding halt.

Science is not ordinary human discourse, however, and this, in my view, is the most important difference between the humanistic and the scientific (positivistic) approaches to social science. Humanistic researchers seek to maintain the essential feel of human discourse. Positivists focus more on specific measurement. I do not see these two styles as inimical to one another, but as complementary.

To get a feel for how complementary the two styles can be, ask some 50 year olds and some 20 year olds—men and women of both ages—to tell you how old you have to be in order to be middle aged. You’ll see immediately how volatile the conceptual definition of ‘‘middle age’’ is. If you ask people about what it means to ‘‘be middle aged,’’ you’ll get plenty of material for an interesting paper on the subject. If you want to measure the differences between men and women and between older and younger people on this variable, you’ll have to do more than just ask them. Figure 2.3 shows an instrument for measuring this variable.

Here is a line that represents age. Obviously, a person 1 year of age is a baby, and a person 100 years of age is old. Put a mark on the line where you think middle age begins and another mark where you think middle age ends.

FIGURE 2.3.

An instrument for measuring what people think ‘‘middle age’’ means.

Many concepts that we use in anthropology have volatile definitions: ‘‘power,’’ ‘‘social class,’’ ‘‘machismo,’’ ‘‘alienation,’’ ‘‘willingness to change,’’ and ‘‘fear of retribution.’’ If we are to talk sensibly about such things, we need clear, intersubjective definitions of them. In other words, although there can be no objective definition of middle age, we can at least agree on what we mean by ‘‘middle age’’ for a particular study and on how to measure the concept.

Complex variables are conceptually defined by reducing them to a series of simpler variables. Saying that ‘‘the people in this village are highly acculturated’’ can be interpreted in many ways. But if you state clearly that you include ‘‘being bilingual,’’ ‘‘working in the national economy,’’ and ‘‘going to school’’ in your conceptual definition of acculturation, then at least others will understand what you’re talking about when you say that people are ‘‘highly acculturated.’

Similarly, ‘‘machismo’’ might be characterized by ‘‘a general feeling of male superiority,’’ accompanied by ‘‘insecure behavior in relationships with women.’’ Intelligence might be conceptually defined as ‘‘the ability to think in abstractions and to generalize from cases.’’ These definitions have something important in common: They have no external reality against which to test their truth value.

Conceptual definitions are at their most powerful when they are linked together to build theories that explain research results. When the United Nations was founded in 1945, the hope was that trade between industrialized and nonindustrialized countries of the world would result in economic development for everyone. The economies of the developed countries would expand and the benefits of an expanding economy would be seen in the underdeveloped countries. A decade later, it was obvious that this wasn’t what was happening. The rich countries were getting richer and the poor countries were getting poorer.

Raul Prebisch, an Argentinian economist who worked at the UN, argued that under colonialism, rich countries were importing raw materials from poor countries to produce manufactured goods and that poor countries had come to depend economically on the rich countries. Prebisch’s ‘‘dependency theory’’ links the concept of ‘‘control of capital’ with those of ‘‘mutual security’’ and ‘‘economic dependency,’’ and the linkage helps explain why economic development often results in some groups winding up with less access to capital than they had before a development program (Prebisch 1984, 1994).

Conceptual definitions are at their weakest in the conduct of research itself, because concepts are abstractions—we have to make them up to study them.

There is nothing wrong with this. There are three things one wants to do in any science: (1) describe a phenomenon of interest; (2) explain what causes it; and (3) predict what it causes. The existence of a conceptual variable is inferred from what it predicts—how well it makes theoretical sense out of a lot of data.

The Concept of Intelligence

The classic example of a conceptual variable is intelligence. Intelligence is anything we say it is. There is no way to tell whether it is: (1) the ability to think in abstractions and to generalize from cases; (2) the ability to remember long strings of unconnected facts; or (3) the ability to recite all of Shakespeare from memory. In the last analysis, the value of the concept of intelligence is that it allows us to predict, with varying success, things like job success, grade-point average, likelihood of having healthy children, and likelihood of being arrested for a felony.

The key to understanding the last statement is the phrase ‘‘with varying success.’’ It is by now well known that measures of intelligence are culture bound; the standard U.S. intelligence tests are biased in favor of Whites and against African Americans because of differences in access to education and differences in life experiences. Further afield, intelligence tests that are designed for Americans may not have any meaning at all to people in radically different cultures.

There is an apocryphal story about some American researchers who were determined to develop a culture-free intelligence test based on manipulating and matching shapes and colors. With an interpreter along for guidance, they administered the test to a group of Bushmen in the Kalahari Desert of South Africa. The first Bushman they tested listened politely to the instructions about matching the colors and shapes and then excused himself.

He returned in a few minutes with half a dozen others, and they began an animated discussion about the test. The researchers asked the interpreter to explain that each man had to take the test himself. The Bushmen responded by saying how silly that was; they solve problems together, and they would solve this one, too. So, although the content of the test might have been culture free, the testing procedure itself was not.

This critique of intelligence testing in no way lessens the importance or usefulness of the concept of intelligence. The concept is useful, in certain contexts, because its measurement allows us to predict other things we want to know. And it is to actual measurement that we now turn.

OPERATIONAL DEFINITIONS

Conceptual definitions are limited because, although they point us toward measurement, they don’t really give us any recipe for measurement. Without measurement, we cannot make useful comparisons. We cannot tell whether Spaniards are more flamboyant than the British, or whether Catholicism is more authoritarian than Buddhism. We cannot evaluate the level of anger in an urban community over perceived abuses by the police of their authority, or compare the level of that anger to the anger found in another community in another city.

Operational definitions specify exactly what you have to do to measure something that has been defined conceptually. Here are four examples of operational definitions:

1. Intelligence: Take the Wechsler Adults Intelligence Scale (WAIS) and administer it to a person. Count up the score. Whatever score the person gets is his or her intelligence.

2. Machismo: Ask a man if he approves of women working outside the home, assuming the family doesn’t need the money; if he says ‘‘no,’’ then give him a score of 1, and if he says ‘‘yes,’’ score him 0. Ask him if he thinks women and men should have the same sexual freedom before marriage; if he says ‘‘no,’’ score 1 and score 0 for ‘‘yes.’’ Ask him if a man should be punished for killing his wife and her lover; if he says ‘‘no,’ score 1; score 0 for ‘‘yes.’’ Add the scores. A man who scores 3 has more machismo than a man who scores 2, and a man who scores 2 has more machismo than a man who scores 1.

3. Tribal identity: Ask American Indians if they speak the language of their ancestors fluently. If ‘‘yes,’’ score 1. If ‘‘no,’’ score 0. Ask them if they attend at least one tribal pow-wow each year. Score 1 for ‘‘yes,’’ and 0 for ‘‘no.’’ Ask them eight other questions of this type, and give them a score of 1 for each answer that signifies self-identification with their tribal heritage. Anyone who scores at least 6 out of 10 is an ‘‘identifier.’’ Five or less is a ‘‘rejecter’’ of tribal heritage or identity.

4. Support for trade barriers against China: Ask workers in a textile factory to complete the Support of Trade Barriers against China Scale. Add the four parts of the scale together to produce a single score. Record that score.

These definitions sound pretty boring, but think about this: If you and I use the same definitions for variables, and if we stick to those definitions in making measurements, then our data are strictly comparable:

We can tell if children in city A have higher intelligence scores than do children in city B.

We can tell if older men in Huehuetenango have higher machismo scores than do younger men in that same village.

We can tell if people in tribe A have higher cultural identity scores than do people in tribe B.

We can tell whether the average scores indicating level of support for trade barriers against China is greater among workers in the factory you studied than among workers in the factory I studied.

I find the ability to make such comparisons exciting and not at all boring. But did you notice that I never said anything in those comparisons about ethnic identity per se, or intelligence per se, or machismo per se, or support for trade barriers per se. In each case, all I said was that we could tell if the scores were bigger or smaller.

What’s So Good about Operationism?

Operational definitions are strictly limited to the content of the operations specified. That’s why I also didn’t say anything about whether it was a good idea or a bad one to make any of these measurements or comparisons. Ifthe content ofan operational definition is bad, then so are all conclusions you draw from using it to measure something.

This is not an argument against operationism in science. Just the opposite. Operationism is the best way to expose bad measurement. By defining measurements operationally, we can tell if one measurement is better than another. If the operational measurement of, say, machismo, seems silly or offensive, it may be because the concept is not very useful to begin with. No amount of measurement or operationism bails out bad concepts. The act of trying, though, usually exposes bad concepts and helps you jettison them.

Adhering to bad measurements is bad science and can have some bad consequences for people. In the 1960s, I was a consultant on a project that was supposed to help Chicano high schoolers develop good career aspirations. Studies had been conducted in which Chicano and Anglo high schoolers were asked what they wanted to be when they reached 30 years of age. Chicanos expressed, on average, a lower occupational aspiration than did Anglos. This led some social scientists to advise policymakers that Chicano youth needed reinforcement of career aspirations at home. (There’s that educational model again.)

Contrary to survey findings, ethnographic research showed that Chicano parents had very high aspirations for their children. The parents were frustrated by two things: (1) despair over the cost of sending their children to college; and (2) high school counselors who systematically encouraged Chicana girls to become housewives and Chicano boys to learn a trade or go into the armed services.

The presumed relation between the dependent variable (level of career aspiration among adolescents) and the independent variable (level of aspiration by parents for the careers of their children) was backward. The parents’ level of career aspiration for their children didn’t cause the children to have low aspirations. The children were driven to low aspirations by structural features of their environment. The parents of those children reflected this reality in order—they said explicitly to interviewers who bothered to ask— not to give their children false hopes.

The operational definition of the variable ‘‘parents’ career aspirations for their children’’ was useless. Here’s the operational definition that should have been used in the study of Chicano parents’ aspirations for their children’s careers:

Go to the homes of the respondents. Using the native language of the respondents (Spanish or English as the case may be), talk to parents about what they want their high school-age children to be doing in 10 years. Explore each answer in depth and find out why parents give each answer.

Ask specifically if the parents are telling you what they think their children will be doing or what they want their children to be doing. If parents hesitate, say: ‘‘Suppose nothing stood in the way of your [son] [daughter] becoming anything they wanted to be. What would you like them to be doing 10 years from now?’’

Write down what the parents say and code it for the following possible scores: 1  unambivalently in favor of children going into high-status occupations; 2  ambivalent about children going into high-status occupations; 3  unambivalently in favor of children going into low- or middle-status occupations.

Use the Nam-Powers-Boyd occupation scale (Nam and Boyd 2004) to decide whether the occupations selected by parents as fitting for their children are high, middle, or low status. Be sure to take and keep notes on what parents say are the reasons for their selections of occupations.

Notice that taking an ethnographic—a so-called qualitative—approach did not stop us from being operational.

Operationism is often crude, but that, too, can be a strength. Robert Wuthnow (1976) operationalized the concept of religiosity in 43 countries using UNESCO data on the number of books published in those countries and the fraction of those books classified as religious literature. Now that’s crude. Still, Wuthnow’s measure of ‘‘average religiosity’ correlates with seven out of eight indicators of modernity. For example, the higher the literacy rate in 1952, the lower the religiosity in 1972.

I have no idea what that means, but I think following up Wuthnow’s work with more refined measurements—to test hypotheses about the societal conditions that support or weaken religiosity—is a lot more exciting than dismissing it because it was so audaciously crude.

The Problem with Operationism

Strict operationism creates a knotty philosophical problem. We make up concepts and measurement turns these abstractions into reality. Because there are many ways to measure the same abstraction, the reality of any concept hinges on the device you use to measure it. So, sea temperature is different if you measure it from a satellite (you get an answer based on radiation) or with a thermometer (you get an answer based on a column of mercury). Intelligence is different if you measure it with a Stanford-Binet test or the Wechsler scales. If you ask a person in any of the industrialized nations ‘‘How old are you?’’ or ‘‘How many birthdays have you had?’’ you will probably retrieve the same number. But the very concept of age in the two cases is different because different ‘‘instruments’’ (queries are instruments) were used to measure it.

This principle was articulated in 1927 by Percy Bridgman in The Logic of Modern Physics and has become the source of an enduring controversy. The bottom line on strict operational definitions is this: No matter how much you insist that intelligence is really more than what is measured by an intelligence test, that’s all it can ever be. Whatever you think intelligence is, it is exactly and only what you measure with an intelligence test and nothing more.

If you don’t like the results of your measurement, then build a better test, where ‘‘better’’ means that the outcomes are more useful in building theory, in making predictions, and in engineering behavior.

I see no reason to waffle about this, or to look for philosophically palatable ways to soften the principle here. The science that emerges from a strict operational approach to understanding variables is much too powerful to water down with backpedaling. It is obvious that ‘‘future orientation’’ is more than my asking someone ‘‘Do you buy large or small boxes of soap?’’ The problem is, you might not include that question in your interview of the same respondent unless I specify that I asked that question in that particular way (box 2.3).

LEVELS OF MEASUREMENT

Whenever you define a variable operationally, you do so at some level of measurement. Most social scientists recognize the following four levels of measurement, in ascending order: nominal, ordinal, interval, and ratio. The general principle in research is: Always use the highest level of measurement that you can. (This principle will be clear by the time you get through the next couple of pages.)

Nominal Variables

A variable is something that can take more than one value. The values of a nominal variable comprise a list of names (from the Latin nomen for name). You can list religions, occupations, and ethnic groups; and you can list fruits, emotions, body parts, things to do on the weekend, baseball teams, rock stars . . . the list of things you can list is endless.

All of the following questions produce nominal data: In what country were you born? Are you healthy? On the whole, do you think the economy is in good shape? Is Bangladesh a poor country? Is Switzerland a rich country? What is your sex?

For sex, you can assign the numeral 1 to men and 2 to women, but gender will still be a qualitative, nominal variable. The number 2 happens to be twice as big as the number 1,

BOX 2.3

O P E R A T I O N A L D E F I N I T I O N S P E R M I T S C I E N T I S T S T O T A L K T O O N E A N O T H E R U S I N G T H E S A M E L A N G U A G E

Operational definitions permit replication of research and the accumulation of knowledge. The Attitudes Toward Women Scale (AWS), for example, was developed by Janet Spence and Robert Helmreich in 1972 (Spence and Helmreich 1972, 1978) and has been used in about 400 studies since then, including some 70 dissertations. Many of those studies involved American college students and, as you’d guess, attitudes toward women have became more liberal/feminist over the years.

By 1990, men’s average score on the AWS was about the same as women’s average score in 1975 (Twenge 1997). In other words, men’s attitudes changed but lagged those of women by 15 years. (These data, remember, reflect the attitudes of college students—the quarter of the population whom we expect to be at the vanguard of social change.)

Some of the items on the AWS seem pretty old-fashioned today. For example, in one item, people are asked how much they agree or disagree with the idea that ‘‘women should worry less about their rights and more about becoming good wives and mothers.’’ You probably wouldn’t use that item if you were building an attitudes-toward-women scale today, but keeping the original, 1972 AWS intact over all this time lets us track attitudes toward women over time. (For an assessment of the AWS, see Loo and Thorpe 1998, 2005.)

but this fact is meaningless with nominal variables. You can’t add up all the 1s and 2s and calculate the ‘‘average sex’’ any more than you can add up all the telephone numbers in the Chicago phone book and get the average phone number.

Assigning numbers to things does make it easier to do certain kinds of statistical analysis on qualitative data—more on this in chapters 19 (on coding text) and 21 (on regression).

The following survey item is an operationalization of the nominal variable called ‘‘religious affiliation’’:

26a. Do you identify with any religion? (check one)

□ Yes

□ No

If you checked ‘‘yes,’’ then please answer question 26b.

26b. What is your religion (check one):

□ Protestant

□ Catholic

□ Jewish

□ Moslem

□ Other religion

This operationalization of the variable ‘‘religious affiliation’’ has two important characteristics: It is exhaustive and mutually exclusive. The famous ‘‘other’’ category in nominal variables makes the list exhaustive—that is, all possible categories have been named in the list—and the instruction to ‘‘check one’’ makes the list mutually exclusive. (More on this in chapter 9 when we discuss questionnaire design.)

‘‘Mutually exclusive’’ means that things can’t belong to more than one category of a nominal variable at a time. We assume, for example, that people who say they are Catholic generally don’t say they are Moslem. I say ‘‘generally’’ because life is complicated and variables that seem mutually exclusive may not be. Some citizens of Lebanon have one Catholic and one Moslem parent and may think of themselves as both Moslem and Catholic.

Most people think of themselves as either male or female, but not everyone does. The prevalence of transsexuals in human populations is not known precisely, but worldwide, it is likely to be between one in ten thousand and one in a hundred thousand for maleto-female transsexuals (biological males whose gender identity is female) and between one in a hundred thousand and one in four hundred thousand for female-to-male transsexuals (Cohen-Kettenis and Gooren 1999).

Most people think of themselves as a member of one so-called race or another, but more and more people think of themselves as belonging to two or more races. In 2000, the U.S. Census offered people the opportunity to check off more than one so-called race from six choices: White, Black or African American, American Indian or Alaska Native, Asian, Native Hawaiian and other Pacific islander, and Other. Nearly seven million people (2.4% of the 281 million in the United States in 2000) checked more than one of the six options (Grieco and Cassidy 2001).

And when it comes to ethnicity, the requirement for mutual exclusivity is just hopeless. There are Chicano African Americans, Chinese Cuban Americans, Filipino Cherokees, and so on. This just reflects the complexity of real life, but it does make analyzing data more complicated because each combination of attributes has to be treated as a separate category of the variable ‘‘ethnicity’’ or collapsed into one of the larger categories. More about this in chapters 20 and 21 when we get to data analysis.

Occupation is a nominal variable, but lots of people have more than one occupation. People can be peasant farmers and makers of fireworks displays for festivals; they can be herbalists and jewelers; or they can be pediatric oncology nurses and antique car salespeople at the same time. A list of occupations is a measuring instrument at the nominal level: You hold each person up against the list and see which occupation(s) he or she has (have).

Ordinal Variables

Like nominal-level variables, ordinal variables are generally exhaustive and mutually exclusive, but they have one additional property: Their values can be rank ordered. Any variable measured as high, medium, or low, like socioeconomic class, is ordinal. The three classes are, in theory, mutually exclusive and exhaustive. In addition, a person who is labeled ‘‘middle class’’ is lower in the social class hierarchy than someone labeled ‘‘high class’’ and higher in the same hierarchy than someone labeled ‘‘lower class.’’ What ordinal variables do not tell us is how much more.

Scales of opinion—like the familiar ‘‘strongly agree,’’ ‘‘agree,’’ ‘‘neutral,’’ ‘‘disagree,’ ‘‘strongly disagree’’ found on so many surveys—are ordinal measures. They measure an internal state, agreement, in terms of less and more, but not in terms of how much more.

This is the most important characteristic of ordinal measures: There is no way to tell how far apart the attributes are from one another. A person who is middle class might be twice as wealthy and three times as educated as a person who is lower class. Or he or she might be three times as wealthy and four times as educated. A person who ‘‘agrees strongly’’ with a statement may agree twice as much as someone who says they ‘‘agree’’—or eight times as much, or half again as much. There is no way to tell.

Interval and Ratio Variables

Interval variables have all the properties of nominal and ordinal variables. They are an exhaustive and mutually exclusive list of attributes, and the attributes have a rankorder structure. They have one additional property as well: The distances between the attributes are meaningful. Interval variables, then, involve true quantitative measurement.

The difference between 30 and 40 Celsius is the same 10 as the difference between 70 and 80, and the difference between an IQ score of 90 and 100 is (assumed to be) the same as the difference between one of 130 and 140. On the other hand, 80 Fahrenheit is not twice as hot as 40, and a person who has an IQ of 150 is not 50% smarter than a person who has an IQ of 100.

Ratio variables are interval variables that have a true zero point—that is, a 0 that measures the absence of the phenomenon being measured. The Kelvin scale of temperature has a true zero: It identifies the absence of molecular movement, or heat.

The consequence of a true zero point is that measures have ratio properties. A person who is 40 years old is 10 years older than a person who is 30, and a person who is 20 is 10 years older than a person who is 10. The 10-year intervals between the attributes (years are the attributes of age) are identical. That much is true of an interval variable. In addition, however, a person who is 20 is twice as old as a person who is 10; and a person who is 40 is twice as old as a person who is 20. These, then, are true ratios.

Although temperature (in Fahrenheit or Celsius) and IQ are nonratio interval variables, most interval-level variables in the social sciences are also ratio variables. In fact, it has become common practice in the social sciences to refer to ratio-level variables as interval variables and vice versa. This is not technically pure, but the confusion of the terms ‘‘interval’’ and ‘‘ratio’’ doesn’t cause much real damage.

Some examples of ratio variables include: age, number of times a person has changed residence, income in dollars or other currency, years married, years spent migrating, population size, distance in meters from a house to a well, number of hospital beds per hundred thousand population, number of months since last employment, number of kilograms of fish caught per week, number of hours per week spent in food preparation activities. Number of years of education is usually treated as a ratio variable, even though a year of grade school is hardly worth the same as a year of graduate school.

In general, concepts (like alienation, political orientation, level of assimilation) are measured at the ordinal level. People get a high score for being ‘‘very assimilated,’’ a low score for being ‘‘unassimilated,’’ and a medium score for being ‘‘somewhat assimilated.’ When a concept variable like intelligence is measured at the interval level, it is likely to be the focus of a lot of controversy regarding the validity of the measuring instrument.

Concrete observables—things you can actually see—are often measured at the interval level. But not always. Observing whether a woman has a job outside her home is nominal, qualitative measurement based on direct observation.

A Rule about Measurement

Remember this rule: Always measure things at the highest level of measurement possible. Don’t measure things at the ordinal level if you can measure them as ratio variables.

If you really want to know the price that people paid for their homes, then ask the price. Don’t ask them whether they paid ‘‘less than a million pesos, between a million and five million, or more than five million.’’ If you really want to know how much education people have had, ask them how many years they went to school. Don’t ask: ‘‘Have you completed grade school, high school, some college, four years of college?’’

This kind of packaging just throws away information by turning interval-level variables into ordinal ones. As we’ll see in chapter 9, survey questions are pretested before going into a questionnaire. If people won’t give you straight answers to straight questions, you can back off and try an ordinal scale. But why start out crippling a perfectly good intervalscale question by making it ordinal when you don’t know that you have to?

During data analysis you can lump interval-level data together into ordinal or nominal categories. If you know the ages of your respondents on a survey, you can divide them into ‘‘old’’ and ‘‘young’’; if you know the number of calories consumed per week for each family in a study, you can divide the data into low, medium, and high. But you cannot do this the other way around. If you collect data on income by asking people whether they earn ‘‘up to a million pesos per year’’ or ‘‘more than a million per year,’’ you cannot go back and assign actual numbers of pesos to each informant.

Notice that ‘‘up to a million’’ and ‘‘more than a million’’ is an ordinal variable that looks like a nominal variable because there are only two attributes. If the attributes are rankable, then the variable is ordinal. ‘‘A lot of fish’’ is more than ‘‘a small amount of fish,’’ and ‘‘highly educated’’ is greater than ‘‘poorly educated.’’ Ordinal variables can have any number of ranks. For purposes of statistical analysis, though, ordinal scales with five or more ranks are often treated as if they were interval-level variables. More about this in chapter 21 on bivariate data analysis.

UNITS OF ANALYSIS

One of the very first things to do in any research project is decide on the unit of analysis. In a case study, there is exactly one unit of analysis—the village, the school, the hospital, the organization. Research designed to test hypotheses requires a sample of units of analysis from a population. How many? That depends on several things, which we’ll get to in chapter 6 on sampling theory and in chapter 16 on cultural domain analysis. Here’s a hint, though: Good research samples can be much smaller than you might think (peek at table 16.13).

Although most research in social science is about populations of people, many other things can be the units of analysis. You can focus on farms instead of farmers, or on unions instead of union members, or on wars instead of warriors. You can study marriage contracts; folk tales, songs, and myths; and countries, cultures, and cities.

Paul Doughty (1979), for example, surveyed demographic data on 134 countries to make a list of ‘‘primate cities.’’ Geographers say that a country has a primate city if its most populous city is at least twice the size of its second-most populous city (Jefferson 1939). Doughty, an anthropologist who had worked in Peru, looked at the population of the three largest cities in each country and coded whether the largest city was at least three times greater than the second and third cities combined. He discovered that this extreme form of population concentration was associated with Latin America more than with any other region of the world at the time.

Holly Mathews (1987, 1992) did a study of how men and women in a Mexican village tell a famous folk tale differently. The tale is called La Llorona (The Weeping Woman) and is known all over Mexico. Mathews’s research has to do with the problem of intracultural variation—different people telling the same story in different ways. She studied a sample of the population of La Llorona stories in a community where she was working. Each story, as told by a different person, had characteristics that could be compared across the sample of stories. One of the characteristics was whether the story was told by a man or by a woman, and this turned out to be the most important variable associated with the stories, which were the units of analysis. (See the section on schema analysis in chapter 19 for more about Mathews’s study of the La Llorona tales.)

You can have more than one unit of analysis in a study. When Mathews looked for similarities and differences in tellings of the story, then the stories were the units of analysis. But when she looked at patterns in the tellers of the stories, then people were her units of analysis.

Robert Aunger (2004:145–62) asked 424 people in four ethnic groups (Sudanic, Efe, Bantu, and Tswa) in the Ituri Forest (Democratic Republic of Congo) about food taboos. For each of 145 animals, Aunger asked each informant if it was edible, and, if so, if there were any times when it should not be eaten. For example, some animals were said to be off limits to pregnant women or to children; some animals required permission from an elder to eat; some animals should not be eaten by members of this or that clan; and so on. When Aunger analyzes looks at which animals have similar patterns of avoidance, the 145 animals are the units of analysis. But when he looks at differences in food taboos across people—like patterns of food taboos in the four ethnic groups—then people are the units of analysis.

A Rule about Units of Analysis

Remember this rule: No matter what you are studying, always collect data on the lowest level unit of analysis possible.

Household economics can only be understood by studying . . . households (Wilk 1990). Collect data, though, on individuals within households. You can always package your data about individuals into data about households during analysis, but if you want to examine the association between female income and child spacing and you collect income data on households in the first place, then you are locked out. You can always aggregate data collected on individuals, but you can never disaggregate data collected on groups.

This rule applies whether you’re studying people or countries. If you are studying relations among trading blocs in major world regions, then collect trade data on countries and pairs of countries, not on regions of the world.

Sometimes, though, the smallest unit of analysis is a collective, like a household or a region. For example, each person in a household consumes a certain number of grams of protein per week. But you can’t just add up what individuals consume and get the number of grams of protein that comes into a household. Some grams are lost to waste, some to pets, some to fertilizer, some to fuel. After you add up all the grams, you get a single number for the household. If you are testing whether this number predicts the number of days per year that people in the household are sick, then the household is your unit of analysis.

The Ecological Fallacy

Once you select your unit of analysis, remember it as you go through data analysis, or you’re likely to commit the dreaded ‘‘ecological fallacy.’’ This fallacy (also known as the Nosnibor effect, after W. S. Robinson [1950], who described it) comes from drawing conclusions about the wrong units of analysis—making generalizations about people, for example, from data about groups or places. For example, in 1930, 11% of foreign-born people in the United States were illiterate, compared with 3% of those born in the United States. The correlation between these two variables was .118. In other words, across 97 million people (the population of the United States at the time), being foreign born was a moderately strong predictor of being illiterate. But when Robinson looked at the data for the (then) 48 states in the United States, he got an entirely different result. The correlation between the percent illiterate and the percent of foreign-born people was .526. That minus sign means that the more foreign born, the less illiteracy.

What’s going on? Well, as Jargowsky (2005) observes, immigrants went mostly to the big industrial states where they were more likely to find jobs. Those northern and midwestern states had better schools and, of course, higher literacy—along with a lot of immigrants, many of whom were illiterate. And that was Robinson’s point: If you only looked at the state-by-state averages (the aggregated units of analysis) instead of at the individual data, you’d draw the wrong conclusion about the relationship between the two variables (Further Reading: the ecological inference problem).

This is an important issue for anthropologists. Suppose you do a survey of villages in a region of southern India. For each village, you have data on such things as the number of people, the average age of men and women, and the monetary value of a list of various consumer goods in each village. That is, when you went through each village, you noted how many refrigerators and kerosene lanterns and radios there were, but you do not have these data for each person or household in the village because you were not interested in that when you designed your study. (You were interested in characteristics of villages as units of analysis.)

In your analysis, you notice that the villages with the population having the lowest average age also have the highest average dollar value of modern consumer goods. You are tempted to conclude that young people are more interested in (and purchase) modern consumer goods more frequently than do older people.

But you might be wrong. Villages with greater employment resources (land and industry) will have lower levels of labor migration by young people. Because more young people stay there, this will lower the average age of wealthier villages. Though everyone wants household consumer goods, only older people can afford them, having had more time to accumulate the funds.

It might turn out that the wealthy villages with low average age simply have wealthier older people than villages with higher average age. It is not valid to take data gathered about villages and draw conclusions about villagers, and this brings us to the crucial issue of validity.

VALIDITY, RELIABILITY, ACCURACY, AND PRECISION

Validity refers to the accuracy and trustworthiness of instruments, data, and findings in research. Nothing in research is more important than validity.

The Validity of Instruments and Data

Are the instruments that were used to measure something valid? Are SAT and GRE scores, for example, valid instruments for measuring the ability of students to get good grades? If they are, then are grades a valid measure of how smart students are? Is the question ‘‘Do you practice polytheistic fetishism?’’ a valid instrument for measuring religious practices? No, it isn’t, because the concept of ‘‘polytheistic fetishism’’ is something that is meaningful only to specialists in the comparative study of religion.

Asking people that question is asking them to think in categories that are alien to their culture. Is the instrument ‘‘How long does it take you to drive to work each day?’’ a valid one for measuring the amount of time it takes people to drive to work each day? That depends on how accurate you want the data to be. If you want the data to be accurate to within, say, 20 minutes on, say 70% of occasions, then the instrument is probably valid. If you want the data to be accurate to, say, within 5 minutes on, say, 90% of occasions, then the instrument is probably not valid because people just can’t dredge up the information you want at that level of accuracy.

The validity of data is tied to the validity of instruments. If questions asking people to recall their behavior are not valid instruments for tapping into informants’ past behavior, then the data retrieved by those instruments are not valid either.

The Validity of Findings

Assuming, however, that the instruments and data are valid, we can ask whether the findings and conclusions derived from the data are valid. Asian Americans get higher average scores on the math part of the SATs (scholastic aptitude tests) than do other ethnic groups in the United States—581 versus 515 for all ethnic groups combined (College Board 2008). Suppose that the SAT math test is a valid instrument for measuring the general math ability of 18 year olds in the United States. Is it valid to conclude that ‘‘Asians are better at math’’ than other people are? No, it isn’t. That conclusion can only be reached by invoking an unfounded, racist assumption about the influence of certain genes—particularly genes responsible for epicanthic eye folds—on the ability of people to do math.

Reliability

Reliability refers to whether or not you get the same answer by using an instrument to measure something more than once. If you insert a thermometer into boiling water at sea level, it should register 212 Fahrenheit each and every time. ‘‘Instruments’’ can be things like thermometers and scales, or they can be questions that you ask people.

Like all other kinds of instruments, some questions are more reliable for retrieving information than others. If you ask 10 people ‘‘Do the ancestors take revenge on people who don’t worship them?’’ don’t expect to get the same answer from everyone. ‘‘How many brothers and sisters do you have?’’ is a pretty reliable instrument (you almost always get the same response when you ask a person that question a second time as you get the first time), but ‘‘How much is your parents’ house worth?’’ is much less reliable. And ‘‘How old were you when you were toilet trained?’’ is just futile.

Precision

Precision is about the number of decimal points in a measurement. When you stand on an old-fashioned scale, the spring is compressed. As the spring compresses, it moves a pointer to a number that signifies how much weight is being put on the scale. Let’s say that you really, truly weigh 156.625 pounds, to the nearest thousandth of a pound.

If you have a predigital bathroom scale like mine, there are five little marks between each pound reading; that is, the scale registers weight in fifths of a pound. In terms of precision, then, your scale is somewhat limited. The best it could possibly do would be to announce that you weigh ‘‘somewhere between 156.6 and 156.8 pounds, and closer to the former figure than to the latter.’’ In this case, you might not be too concerned about the error introduced by lack of precision.

Whether you care or not depends on the needs you have for the data. If you are concerned about losing weight, then you’re probably not going to worry too much about the fact that your scale is only precise to the nearest fifth of a pound. But if you’re measuring the weights of pharmaceuticals, and someone’s life depends on your getting the precise amounts into a compound, that’s another matter.

Accuracy

Finally, accuracy. Assume that you are satisfied with the level of precision of the scale. What if the spring was not calibrated correctly (there was an error at the factory where the scale was built, or last week your overweight house guest bent the spring a little too much) and the scale was off? Now we have the following interesting situation: The data from this instrument are valid (it has already been determined that the scale is measuring weight—exactly what you think it’s measuring); they are reliable (you get the same answer every time you step on it); and they are precise enough for your purposes. But they are not accurate. What next?

You could see if the scale were always inaccurate in the same way. You could stand on it 10 times in a row, without eating or doing exercise in between. That way, you’d be measuring the same thing 10 different times with the same instrument. If the reading was always the same, then the instrument would at least be reliable, even though it wasn’t accurate. Suppose it turned out that your scale was always incorrectly lower by 5 pounds. This is called systematic bias. Then, a simple correction formula would be all you’d need to feel confident that the data from the instrument were pretty close to the truth. The formula would be:

$$ \text { true weight } = \text { your scale weight } + 5 \text { pounds } $$

The scale might be off in more complicated ways, however. It might be that for every 10 pounds of weight put on the scale, an additional half-pound correction has to be made. Then the recalibration formula would be

$$ \text { true weight } = (\text { your scale weight }) + (\text { scale weight } / 1 0) (. 5) $$

or

(your scale weight)(1.05)

That is, take the scale weight, divide by 10, multiply by half a pound, and add the result to the reading on your scale.

If an instrument is not precise enough for what you want to do with the data, then you simply have to build a more precise one. There is no way out. If it is precise enough for your research and reliable, but inaccurate in known ways, then a formula can be applied to correct for the inaccuracy.

The real problem is when instruments are inaccurate in unknown ways. The bad news is that this happens a lot. If you ask people how long it takes them to drive to work, they’ll tell you. If you ask people what they ate for breakfast, they’ll tell you that, too. Answers to both questions may be dead on target, or they may bear no useful resemblance to the truth. The good news is that informant accuracy is one of the methodological questions that social scientists have been investigating for years and on which real progress continues to be made (Further Reading: informant accuracy).

DETERMINING VALIDITY

You may have noticed a few paragraphs back that I casually slipped in the statement that some scale had already been determined to be a valid instrument. How do we know that the scale is measuring weight? Maybe it’s measuring something else. How can we be sure? We have to make concepts up to study them, so there is no direct way to evaluate the validity of an instrument for measuring a concept. Ultimately, we are left to decide, on the basis of our best judgment, whether an instrument is valid or not.

We are helped in making that judgment by some tests for face validity, content validity, construct validity, and criterion validity.

Face Validity

Establishing face validity involves simply looking at the operational indicators of a concept and deciding whether or not, on the face of it, the indicators make sense. On the face of it, asking people ‘‘How old were you when you were toilet trained?’’ is not a valid way to get at this kind of information. A paper-and-pencil test about the rules of the road is not, on the face of it, a valid indicator of whether someone knows how to drive a car. But the paper-and-pencil test is probably a valid test for determining if an applicant for a driver’s license can read road signs. These different instruments—the road test and the paper-and-pencil test—have face validity for measuring different things.

Boster (1985) studied how well the women of the Aguaruna Jı´varo in Peru understood the differences among manioc plants. He planted some fields with different varieties of manioc and asked women to identify the varieties. This technique, or instrument, for measuring cultural competence has great face validity; most researchers would agree that being able to identify more varieties of manioc is a valid indicator of cultural competence in this domain.

Boster might have simply asked women to list as many varieties of manioc as they could. This instrument would not have been as valid, on the face of it, as having them identify actual plants that were growing in the field. There are just too many things that could interfere with a person’s memory of manioc names, even if they were really competent about planting roots, harvesting them, cooking them, trading them, and so on.

Face validity is based on consensus among researchers: If everyone agrees that asking people ‘‘How old are you’’ is a valid instrument for measuring age, then, until proven otherwise, that question is a valid instrument for measuring age.

Content Validity

Content validity is achieved when an instrument has appropriate content for measuring a complex concept, or construct. If you walk out of a test and feel that it was unfair because it tapped too narrow a band of knowledge, your complaint is that the test lacked content validity.

Content validity is very, very tough to achieve, particularly for complex, multidimensional constructs. Consider, for example, what’s involved in measuring a concept like strength of ethnic identity among, say, second-generation Mexican Americans. Any scale to assess this has to have components that deal with religion, language, socioeconomic status, sense of history, and gastronomy.

Religion: Mexican Americans tend to be mostly Roman Catholic, but a growing number of Mexicans are now Protestants. The migration of a few million of these converts to the United States over the next decade will have an impact on ethnic politics—and ethnic identity—within the Mexican American population.

Language: Some second-generation Mexican Americans speak almost no Spanish; others are completely bilingual. Some use Spanish only in the home; others use it with their friends and business associates.

Socioeconomic status: Many Mexican Americans are poor (about 31% of Hispanic households in the United States have incomes below $25,000 a year), but many others are well off (about 20% have incomes above $75,000 a year) (SAUS 2010:table 674). People with radically different incomes tend to have different political and economic values.

Sense of history: Some so-called Mexican Americans have roots that go back to before the British Pilgrims landed at Plymouth Rock. The Hispanos (as they are known) of New Mexico were Spaniards who came north from the Spanish colony of Mexico. Their selfdescribed ethnic identity is quite different from recent immigrants from Mexico.

Gastronomy: The last refuge of ethnicity is food. When language is gone (Spanish, Yiddish, Polish, Gaelic, Greek, Chinese . . .), and when ties to the ‘‘old country’’ are gone, burritos, bagels, pirogis, corned beef, mousaka, and lo mein remain. For some secondgeneration Mexican Americans, cuisine is practically synonymous with identity; for others it’s just part of a much larger complex of traits.

A valid measure of ethnic identity, then, has to get at all these areas. People’s use of Spanish inside and outside the home and their preference for Mexican or Mexican American foods are good measures of some of the content of Mexican American ethnicity. But if these are the only questions you ask, then your measure of ethnicity has low content validity. (See Cabassa [2003] and Cruz et al. [2008] on acculturation scales for Hispanics in the United States.)

‘‘Life satisfaction’’ is another very complex variable, composed of several concepts— like ‘‘having sufficient income,’’ ‘‘a general feeling of well-being,’’ and ‘‘satisfaction with level of personal control over one’s life.’’ In fact, most of the really interesting things that social scientists study are complex constructs, things like ‘‘quality of life,’’ ‘‘socioeconomic class,’’ ‘‘ability of teenagers to resist peer pressure to smoke,’’ and so on.

Construct Validity

An instrument has high construct validity if there is a close fit between the construct it supposedly measures and actual observations made with the instrument. An instrument has high construct validity, in other words, if it allows you to infer that a unit of analysis (a person, a country, whatever) has a particular complex trait and if it supports predictions that are made from theory.

Scholars have offered various definitions of the construct of ethnicity, based on different theoretical perspectives. Does a particular measure of Mexican American ethnicity have construct validity? Does it somehow ‘‘get at,’’ or measure, the components of this complex idea?

Asking people ‘‘How old are you?’’ has so much face validity that you hardly need to ask whether the instrument gets at the construct of chronological age. Giving people an IQ test, by contrast, is controversial because there is so much disagreement about what the construct of intelligence is. In fact, lots of constructs in which we’re interested— intelligence, ethnicity, machismo, alienation, acculturation—are controversial and so are the measures for them. Getting people to agree that a particular measure has high construct validity requires that they agree that the construct is valid in the first place.

Criterion Validity—The Gold Standard

An instrument has high criterion validity if there is a close fit between the measures it produces and the measures produced by some other instrument that is known to be valid. This is the gold standard test.

A tape measure, for example, is known to be an excellent instrument for measuring height. If you knew that a man in the United States wore shirts with 35 sleeves, and pants with 34 cuffs, you could bet that he was over 6- tall and be right more than 95% of the time. On the other hand, you might ask: ‘‘Why should I measure his cuff length and sleeve length in order to know most of the time, in general, how tall he is, when I could use a tape measure and know all of the time, precisely how tall he is?’

Indeed. If you want to measure someone’s height, use a tape measure. Don’t substitute a lot of fuzzy proxy variables for something that’s directly measurable by known, valid indicators. But if you want to measure things like acculturation or quality of life or socioeconomic class—things that don’t have universally accepted, valid indicators—then a complex measure will just have to do until something simpler comes along (box 2.4).

BOX 2.4

T H E P R I N C I P L E O F O C K H A M ’ S R A Z O R

The preference in science for simpler explanations and measures over more complicated ones is called the principle of parsimony. It is also known as Ockham’s razor, after William of Ockham (1285–1349), a medieval philosopher who argued Pluralitas non est ponenda sine necessitate, or ‘‘Don’t make things more complicated than they need to be.’’

You can tap the power of criterion validity for complex constructs with the known group comparison technique. If you develop a scale to measure political ideology, you might try it out on members of the American Civil Liberties Union and on members of the Christian Coalition of America. Members of the ACLU should get high ‘‘left’’ scores, and members of the CCA should get high ‘‘right’’ scores. If they don’t, there’s probably something wrong with the scale. In other words, the known-group scores are the criteria for the validity of your instrument.

A particularly strong form of criterion validity is predictive validity—whether an instrument lets you predict accurately something else you’re interested in. ‘‘Stress’’ is a complex construct. It occurs when people interpret events as threatening to their lives. Some people interpret a bad grade on an exam as a threat to their whole life, and others just blow it off. Now, stress is widely thought to produce a lowered immune response and increase the chances of getting sick. A really good measure of stress, then, ought to predict the likelihood of getting sick.

Remember the life insurance problem? You want to predict whether someone is likely to die in the next 365 days to know how much to charge them in premiums. Age and sex tell you a lot. But if you know their weight, whether they smoke, whether they exercise regularly, what their blood pressure is, whether they have ever had any one of a list of diseases, and whether they test-fly experimental aircraft for a living, then you can predict—with a higher and higher degree of accuracy—whether they will die within the next 365 days. Each piece of data—each component of a construct you might call ‘‘lifestyle’’—adds to your ability to predict something of interest.

The Bottom Line

The bottom line on all this is that although various forms of validity can be demonstrated, Truth, with a capital T, is never final. We are never dead sure of anything in science. We try to get closer and closer to the truth by better and better measurement. All of science relies on concepts whose existence must ultimately be demonstrated by their effects. You can ram a car against a cement wall at 50 miles an hour and account for the amount of crumpling done to the radiator by referring to a concept called ‘‘force.’’ You can’t see force, but you can sure see its effects. The greater the force, the more crumpled the radiator. You demonstrate the existence of intelligence by showing how it predicts school achievement or monetary success (Further Reading: validity).

The Problem with Validity

If you suspect that there is something deeply, desperately wrong with all this, you’re right. The whole argument for the validity (indeed, the very existence) of something like intelligence is, frankly, circular: How do you know that intelligence exists? Because you see its effects in achievement. And how do you account for achievement? By saying that someone has achieved highly because they’re intelligent. How do you know machismo exists? Because men dominate women in some societies. And how do you account for dominance behavior, like wife beating? By saying that wife beaters are acting out their machismo.

In the hierarchy of construct reality, then, force ranks way up there (after all, it’s got several hundred years of theory and experimentation behind it), and things like intelligence and machismo are pretty weak by comparison. And yet, as I made clear in chapter 1, the social and behavioral sciences are roaring successes, on a par with the physical sciences in terms of the effects they have on our lives every day. This is possible because social scientists have refined and tested many useful concepts and measurements for those concepts.

Ultimately, the validity of any concept—force in physics, the self in psychology, modernization in sociology and political science, acculturation in anthropology—depends on two things: (1) the utility of the device that measures it; and (2) the collective judgment of the scientific community that a concept and its measure are valid. In the end, we are left to deal with the effects of our judgments, which is just as it should be. Valid measurement makes valid data, but validity itself depends on the collective opinion of researchers.

CAUSE AND EFFECT

Cause and effect is among the most highly debated issues in the philosophy of knowledge. (See Hollis [1996] for a review.) We can never be absolutely certain that variation in one thing causes variation in another. Still, if measurements of two variables are valid, you can be reasonably confident that one variable causes another if four conditions are met.

1. The two variables co-vary—that is, as scores for one variable increase or decrease, scores for the other variable increase of decrease as well.

2. The covariation between the two variables is not spurious.

3. There is a logical time order to the variables. The presumed causal variable must always precede the other in time.

4. A mechanism is available that explains how an independent variable causes a dependent variable. There must, in other words, be a theory.

Condition 1: Covariation

When two variables are related they are said to co-vary. Covariation is also called correlation or, simply, association.

Association is a necessary but insufficient condition for claiming a causal relation between two variables. Whatever else is needed to establish cause and effect, you can’t claim that one thing causes another if they aren’t related in the first place.

Here are a few interesting covariations:

1. Sexual freedom for women tends to increase with the amount that women contribute to subsistence (Schlegel and Barry 1986).

2. Ground-floor, corner apartments occupied by students at big universities have a much higher chance of being burglarized than other units in the same apartment bloc (M. B. Robinson and C. E. Robinson 1997).

3. When married men and women are both employed full time, they spend the same amount of time in the various rooms of their house—except for the kitchen (Ahrentzen et al. 1989).

You might think that to establish cause, independent variables would have to be strongly related to the dependent variable. Not always. People all over the world make decisions about whether or not to use (or demand the use of) a condom as a part of sexual relations. These decisions are based on many factors, all of which may be weakly but causally related to the ultimate decision. These factors include: the education level of one or both partners; the level of income of one or both partners; the availability and cost of condoms; the amount of time that partners have been together; the amount of previous sexual experience of one or both partners; whether either or both partners know anyone personally who has died of AIDS; and so on.

Each independent variable may contribute only a little to the outcome of the dependent variable (the decision that is finally made), but the contribution may be quite direct and causal.

Condition 2: Lack of Spuriousness

Just as weak correlations can be causal, strong correlations can turn out not to be. When this happens, the original correlation is said to be spurious. There is a correlation between the number of firefighters at a fire and the amount of damage done: the more firefighters, the higher the insurance claim. You could easily conclude that firefighters cause fire damage.

We know better: Both the amount of damage and the number of firefighters is caused by the size of the blaze. We need to control for this third variable—the size of the blaze—to understand what’s really going on.

Dellino (1984) found an inverse relation between perceived quality of life and involvement with the tourism industry on the island of Exuma in the Bahamas. When he controlled for the size of the community (he studied several on the island), the original correlation disappeared. People in the more congested areas were more likely to score low on the perceived-quality-of-life index whether or not they were involved with tourism, and those in the small, outlying communities were more likely to score high on the index. People in the congested areas were also more likely to be involved in tourism-related activities, because that’s where the tourists go.

Mwango (1986) found that illiterates in Malawi were much more likely than literates to brew beer for sale from part of their maize crop. The covariation vanished when he controlled for wealth, which causes both greater education (hence, literacy) and the purchase, rather than the brewing, of maize beer.

The list of spurious relations is endless, and it is not always easy to detect them for the frauds that they are. A higher percentage of men than women get lung cancer, but when you control for the length of time that people have smoked, the gender difference in lung cancer vanishes. Pretty consistently, young people accept new technologies more readily than older people, but in many societies, the relation between age and readiness to adopt innovations disappears when you control for level of education. Urban migrants from tribal groups often give up polygyny in Africa and Asia, but both migration and abandonment of polygyny are likely to be caused by a third factor: lack of wealth.

Your only defense against spurious covariations is vigilance. No matter how obvious a covariation may appear, discuss it with disinterested colleagues—people who have no stake at all in telling you what you want to hear. Present your initial findings in class seminars at your university or where you work. Beg people to find potentially spurious relations in your work. You’ll thank them for it if they do.

Condition 3: Precedence, or Time Order

Besides a nonspurious association, something else is required to establish a causeand-effect relation between two variables: a logical time order. Firefighters don’t cause fires—they show up after the blaze starts. African Americans have higher blood pressure, on average, than Whites do, but high blood pressure does not cause people to be African American.

Unfortunately, things are not always clear-cut. Does adoption of new technologies cause wealth, or is it the other way around? Does urban migration cause dissatisfaction with rural life, or the reverse? Does consumer demand cause new products to appear, or vice versa? Does the growth in the number of lawsuits cause more people to study law so that they can cash in, or does overproduction of lawyers cause more lawsuits?

What about the increase in elective surgery in the United States? Does the increased supply of surgeons cause an increase in elective surgery, or does the demand for surgery create a surfeit of surgeons? Or are both caused by external variables, like an increase in discretionary income in the upper middle class or the fact that insurance companies pay more and more of Americans’ medical bills?

Figure 2.4 shows three kinds of time order between two variables. Read figure 2.4a as $^ { \mathfrak { a } }$ is antecedent to $b . ^ { \dag }$ Read figure 2.4b as ‘‘a and b are antecedent to $c _ { \cdot } ^ { \mathrm { ~ \tiny ~ > ~ } }$ And read figure 2.4c as $^ { \mathfrak { a } }$ is antecedent to $b ,$ which is an intervening variable antecedent to $c _ { \cdot } ^ { \mathrm { ~ \tiny ~ \mathfrak ~ { ~ p ~ } ~ } }$ A lot of data analysis is about understanding and controlling for antecedent and intervening variables—about which much more in chapter 21.

$$ \begin{array}{c c c} A \to B & \stackrel { {A} } { {\searrow} } C & A \to B \to C \ & B \end{array} $$

FIGURE 2.4.

Time order between two or three variables.

Condition 4: Theory

Finally, even when you have established nonspurious, consistent, strong covariation, as well as a logical time sequence for two or more variables, you need a theory—a mechanism—that explains the association. Theories are ideas about how things work. Good theories are good ideas about how things work—that is, ideas that have held up against challenges and that explain new cases of things as they come up.

One of my favorites is called cognitive dissonance theory (Festinger 1957). It’s based on the insight that: (1) People can tell when their beliefs about what ought to be don’t match their perception of how things really are; and (2) This causes an uncomfortable feeling. The feeling is called cognitive dissonance. People then have a choice: They can live with the dissonance (be uncomfortable); change the external reality (fight city hall); or change their beliefs (usually the path of least resistance, but not necessarily the easy way out).

Cognitive dissonance theory helps explain why some people accept new technologies that they initially reject out of fear for their jobs: Once a technology is entrenched, and there is no chance of getting rid of it, it’s easier to change your ideas about what’s good and what’s bad than it is to live with dissonance (Bernard and Pelto 1987). Dissonance theory helps explain why men in countries across the world are increasingly accepting of women working outside the home: When economic necessity drives women into the workforce, it’s painful to hold on to the idea that that’s the wrong thing for women to do.

On the other hand, some people do actually quit their jobs rather than accept new technologies, and some men continue to argue against women working outside the home, even when those men depend on their wives’ income to make ends meet. This is an example of a general theory that fails to predict local phenomena. It leads us to seek more data and more understanding to predict when cognitive dissonance theory is insufficient as an explanation.

Many theories are developed to explain a purely local phenomenon and then turn out to have wider applicability. Many observers have noticed, for example, that when men from polygynous African societies move to cities, they often give up polygyny (Clignet 1970; Dorjahn 1977, 1988; Jacoby 1995). This consistent covariation is explained by the fact that men who move away from tribal territories in search of wage labor must abandon their land, their houses, and the shared labor of their kinsmen. Under those conditions, they simply cannot afford to provide for more than one wife, much less the children that multiple wives produce. The relation between urbanization and changes in marriage customs is explained by antecedent and intervening variables.

If you read the literature across the social sciences, you’ll see references to something called ‘‘contagion theory.’’ This one invokes a copycat mechanism to explain why suicides are more likely to come in batches when one of them is widely publicized in the press (Jamieson et al. 2003) and why more women candidates stand for election in districts that already have women legislators in office (Matland and Studlar 1996).

‘‘Relative deprivation theory’’ is based on the insight that people compare themselves to specific peer groups, not to the world at large (Martin 1981; Stouffer et al. 1949). It explains why anthropology professors don’t feel all that badly about engineering professors earning a lot of money, but hate it if sociologists in their university get significantly higher salaries than they do.

Theories start with one or two primitive axioms—things that are simply defined and that you have to take at face value. The definition of cognitive dissonance is an example: When people have inconsistent beliefs, or when they perceive things in the real world to be out of whack with their ideas of how things should be, they feel discomfort. This discomfort leads people to strive naturally toward cognitive consonance. Neither the fact of dissonance, nor the discomfort it produces, nor the desire for consonance are ever explained. They are primitive axioms. How people deal with dissonance and how they try to achieve consonance are areas for empirical research. As empirical research accumulates, the theory is tested and refined (box 2.5).

BOX 2.5

C U L T U R A L C O N S O N A N C E T H E O R Y

William Dressler developed his theory of cultural consonance based on cognitive dissonance theory. Cultural consonance is the degree to which people’s lives mirror a widely shared set of beliefs about what lives should look like. What’s a successful life? This differs from culture to culture, but in many cultures, the list of things that indicate success is widely shared. Dressler and his colleagues have found that people who have more of these things (whose lives are in consonance with the cultural model) have lower stress and fewer blood pressure problems than do people whose lives lack cultural consonance (Dressler et al. 1997, 2002, 2007; Dressler, Ribeiro et al. 2004, and see chapter 16 on measuring cultural consensus).

In relative deprivation theory, the fact that people have reference groups to which they compare themselves doesn’t get explained, either. It, too, is a primitive axiom, an assumption, from which you deduce some results. The results are predictions, or hypotheses, that you then go out and test. The ideal in science is to deduce a prediction from theory and to test the prediction. That’s the culture of science. The way social science really works much of the time is that you don’t predict results, you postdict them. You analyze your data, come up with findings, and explain the findings after the fact.

There is nothing wrong with this. Knowledge and understanding can come from good ideas before you collect data or after collect data. You must admit, though, there’s a certain panache in making a prediction, sealing it in an envelope, and testing it. Later, when you take the prediction out of the envelope and it matches your empirical findings, you get a lot of points (Further Reading: causal analysis in the social sciences).

THE KALYMNIAN CASE

Here’s an example of explaining findings after the fact. In my experience, it’s pretty typical of how social scientists develop, refine, and change their minds about theories.

In my fieldwork in 1964–1965 on the island of Kalymnos, Greece, I noticed that young sponge divers (in their 20s) were more likely to get the bends than were older divers (those over 30). (The bends is a crippling malady that affects divers who come up too quickly after a long time in deep water.) I also noticed that younger divers were more productive than very old divers (those over 45), but not more productive than those in their middle years (30–40).

As it turned out, younger divers were subject to much greater social stress to demonstrate their daring and to take risks with their lives—risks that men over 30 had already put behind them. The younger divers worked longer under water (gathering more sponges), but they came up faster and were consequently at higher risk of bends. The middle group of divers made up in experience for the shortened time they spent in the water, so they maintained their high productivity at lower risk of bends. The older divers were feeling the effects of infirmity brought on by years of deep diving, hence their productivity was lowered, along with their risk of death or injury from bends.

The real question was: What caused the young Kalymnian divers to engage in acts that placed them at greater risk?

My first attempt at explaining all this was pretty lame. I noticed that the men who took the most chances with their lives had a certain rhetoric and swagger. They were called leve´dhis (Greek for a brave young man) by other divers and by their captains. I concluded that somehow these men had more levedhia´ (the quality of being brave and young) and that this made them higher risk takers. In fact, this is what many of my informants told me. Young men, they said, feel the need to show their manhood, and that’s why they take risks by staying down too long and coming up too fast.

The problem with this cultural explanation was that it just didn’t explain anything. Yes, the high risk takers swaggered and exhibited something we could label machismo or levedhia´. But what good did it do to say that lots of machismo caused people to dive deep and come up quickly? Where did young men get this feeling, I asked? ‘‘That’s just how young men are,’’ my informants told me. I reckoned that there might be something to this testosterone-poisoning theory, but it didn’t seem adequate.

Eventually, I saw that the swaggering behavior and the values voiced about manliness were cultural ways to ratify, not explain, the high-risk diving behavior. Both the diving behavior and the ratifying behavior were the product of a third factor, an economic distribution system called pla´tika.

Divers traditionally took their entire season’s expected earnings in advance, before shipping out in April for the 6-month sponge fishing expedition in North Africa. By taking their money (pla´tika) in advance, they placed themselves in debt to the boat captains. Just before they shipped out, the divers would pay off the debts that their families had accumulated during the preceding year. By the time they went to sea, the divers were nearly broke and their families started going into debt again for food and other necessities.

In the late 1950s, synthetic sponges began to take over the world markets, and young men on Kalymnos left for overseas jobs rather than go into sponge fishing. As divers left the island, the remaining divers demanded higher and higher pla´tika. They said that it was to compensate them for increases in the cost of living, but their demand for more money was a pure response by the divers to the increasing scarcity of their labor. The price of sponges, however, was dropping over the long term, due to competition with synthetics, so the higher pla´tika for the divers meant that the boat captains were losing profits. The captains put more and more pressure on the divers to produce more sponges, to stay down longer, and to take greater risks. This resulted in more accidents on the job (Bernard 1967, 1987).

Note that in all the examples of theory I’ve just given, the predictions and the post hoc explanations, I didn’t have to quote a single statistic—not even a percentage score. That’s because theories are qualitative. Ideas about cause and effect are based on insight; they are derived from either qualitative or quantitative observations and are initially expressed in words. Testing causal statements—finding out how much they explain rather than whether they seem to be plausible explanations—requires quantitative observations. But theory construction—explanation itself—is the quintessential qualitative act.

FURTHER READING

Measuring gender across cultures: Auster and Ohm (2000); Isaac and Shah (2004); Norvilitis and Reid (2002); O^¨ ngen (2007); O^¨ zkan and Lajunen (2006); Peng (2006); Sugihara and Katsurada

(2000); Sugihara and Warner (1999); Zhang et al. (2001). For a version of the BSRI tested for use in Mexico, see Lara-Cantu´ and Navarro-Arias (1987). For a version of the BSRI for use in China, see Qin and Yianjie (2003).

The ecological inference problem: Freedman (2001); Jargowsky (2005); King (1997).

Informant accuracy: Adams and Moody (2007); Bernard, Killworth et al. (1984); Calahan (1968); Dressler, Borges et al. (2005); Freeman et al. (1987); Godoy et al. (2008); Lapham et al. (2004); McPhee et al. (2002); Patten et al. (2002); Pescosolido and Wright (2003); Rocha (2005); Romney et al. (1986); Schwarz (1999); Sudman et al. (1996); Vadez et al. (2003); Woodside and Wilson (2002); Zimmerman et al. (2002).

Validity: Adams (1950); Hardesty and Bearden (2004); McKenzie et al. (1999); Mosier (1947); Nevo (1985); Sireci (1998).

Causal analysis in the social sciences: Blalock (1964, 1971); Lagnado et al. (2007); Marini and Singer (1988); Maxwell (2004); Rafferty (1998).

Preparing for Research

SETTING THINGS UP

This chapter is about the things that go on before data are collected and analyzed. I’ll take you through the ideal research process and compare that to how research really gets done. Then I’ll discuss the problem of choosing problems—how do I know what to study?—and I’ll give you some pointers on how to scour the literature so you can benefit from the work of others when you start a research project.

I’ll have a lot more to say about the ethics of social research in this chapter—choosing a research problem involves decisions that can have serious ethical consequences—and a lot more about theory, too. Method and theory, it turns out, are closely related.

THE IDEAL RESEARCH PROCESS

Despite all the myths about how research is done, it’s actually a messy process that’s cleaned up in the reporting of results. Figure 3.1 shows how the research process is supposed to work in the ideal world:

FIGURE 3.1. How research is supposed to work.

1. First, a theoretical problem is formulated;

2. Next, an appropriate site and method are selected;

3. Then, data are collected and analyzed;

4. Finally, the theoretical proposition with which the research was launched is either challenged or supported.

In fact, all kinds of practical and intellectual issues get in the way of this neat scheme. In the end, research papers are written so that the chaotic aspects of research are not emphasized, and the orderly inputs and outcomes are.

I see nothing wrong with this. It would be a monumental waste of precious space in books and journals to describe the real research process for every project that’s reported. Besides, every seasoned researcher knows just how messy it all is, anyway. You shouldn’t have to become a highly experienced researcher before you’re let into the secret of how it’s really done.

A REALISTIC APPROACH

There are five questions to ask yourself about every research question you are thinking about pursuing. Most of these can also be asked about potential research sites and research methods. If you answer these questions honestly (at least to yourself), chances are you’ll do good research every time. If you cheat on this test, even a teeny bit, chances are you’ll regret it. Here are the five questions:

1. Does this topic (or research site, or data collection method) really interest me?

2. Is this a problem that is amenable to scientific inquiry?

3. Are adequate resources available to investigate this topic? To study this population at this particular research site? To use this particular data collection method?

4. Will my research question, or the methods I want to use, lead to unresolvable ethical problems?

5. Is the topic of theoretical and/or practical interest?

Personal Interest

The first thing to ask about any research question is: Am I really excited about this? Researchers do their best work when they are genuinely having fun, so don’t do boring research when you can choose any topic you like.

Of course, you can’t always choose any topic you like. In contract research, you sometimes have to take on a research question that a client finds interesting but that you find deadly dull. The most boring research I’ve ever done was on a contract where my coworkers and I combined ethnographic and survey research of rural homeowners’ knowledge of fire prevention and their attitudes toward volunteer fire departments. This was in 1973. I had young children at home and the research contract paid me a summer salary. It was honest work and I delivered a solid product to the agency that supported the project. But I never wrote up the results for publication.

By comparison, that same year I did some contract research on the effects of co-ed prisons on homosexuality among male and female inmates. I was very interested in that study and it was much easier to spend the extra time and effort polishing the contract reports for publication (Killworth and Bernard 1974).

I’ve seen many students doing research for term projects, M.A. theses, and even doctoral dissertations simply out of convenience and with no enthusiasm for the topic. If you are not interested in a research question, then no matter how important other people tell you it is, don’t bother with it. If others are so sure that it’s a dynamite topic of great theoretical significance, let them study it.

The same goes for people and places. Agricultural credit unions and brokerage houses are both complex organizations. But they are very different kinds of places to spend time in, so if you are going to study a complex organization, check your gut first and make sure you’re excited about where you’re going. It’s really hard to conduct penetrating, indepth interviews over a period of a several weeks to a year if you aren’t interested in the lives of the people you’re studying.

You don’t need any justification for your interest in studying a particular group of people or a particular topic. Personal interest is . . . personal. So ask yourself: Will my interest be sustained there? If the answer is ‘‘no,’’ then reconsider. Accessibility of a research site or the availability of funds for the conduct of a survey are pluses, but by themselves they’re not enough to make good research happen.

Science Versus Nonscience

The next question is: Is this a topic that can be studied by the methods of science? If the answer is ‘‘no,’’ then no matter how much fun it is, and no matter how important it seems, don’t even try to make a scientific study of it. Either let someone else do it, or use a different approach.

Consider this empirical question: How often do derogatory references to women occur in the Old Testament? If you can come up with a good, operational definition of ‘‘derogatory,’’ then you can answer this question by looking through the corpus of data and counting the instances that turn up. Pretty straightforward, descriptive science.

But consider this question: Does the Old Testament offer support for unequal pay for women today? This is simply not answerable by the scientific method. It is no more answerable than the question: Is Rachmaninoff’s music better than Tchaikovsky’s? Or this: Should the remaining hunting-and-gathering bands of the world be preserved just the way they are and kept from being spoiled by modern civilization? Whether or not a study is a scientific one depends first on the nature of the question being asked and then on the methods used.

I can’t stress too often or too strongly that when I talk about using the scientific method I’m not talking about numbers. In science, whenever a research problem can be investigated with quantitative measurement, numbers are more than just desirable; they’re required. On the other hand, there are many intellectual problems for which quantitative measures are not yet available. Those problems require qualitative measurement.

Descriptions of processes (skinning a goat, building a fireworks tower, putting on makeup, setting the table for Thanksgiving), or of events (funerals, Little League games, parades), or of systems of nomenclature (kinship terms, disease terms, ways to avoid getting AIDS) require words, not numbers. Dorothy Holland and Debra Skinner (1987) asked some university women to list the kinds of guys there are. They got a list of words like ‘‘creep,’’ ‘‘hunk,’’ ‘‘nerd,’’ ‘‘jerk,’’ ‘‘sweetie pie,’’ and so on. Then they asked some women, for each kind: ‘‘Is this someone you’d like to date?’’ The yes-no answers are nominal—that is, qualitative—measurement.

We’ll get back to this kind of systematic, qualitative data collection in chapters 16 and 17 on cultural domain analysis.

Resources

The next question to ask is whether adequate resources are available for you to conduct your study. There are three major kinds of resources: time, money, and people. What may be adequate for some projects may be inadequate for others. Be totally honest with yourself about this issue.

Time

Some research projects take a few weeks or months; others take years. It takes a year or more to do an ethnographic study of a culture that is very different from your own, but a lot of focused ethnography can be done much more quickly. Gwendolyn Dordick (1996) spent 3 months studying a homeless shelter for 700 men in New York City. She visited the shelter four times a week for 3 hours or more each time, and spent 4 days at the shelter from morning until lights-out at 10 p.m. This was enough time for her to understand a great deal about life in the shelter, including how a group of just 15 men had coalesced into a ruling elite and how some men had formed faux marriages (that could, but did not necessarily, involve sex) to protect themselves and their few possessions from violence and thievery.

Much of today’s applied anthropological research is done in weeks or months, using rapid assessment methods. Rapid assessment methods are the same ones that everyone else uses but they are done quickly. (I’ll lay out some rapid assessment methods in chapter 12 on participant observation.) If you are doing research for a term project, the topic has to be something you can look at in a matter of a few months—and squeezing the research into a schedule of other classes, at that. It makes no sense to choose a topic that demands two semesters’ work when you have one semester in which to do the research. The effort to cram 10 gallons of water into a 5-gallon can is futile and quite common. Don’t do it.

Money

Many things come under the umbrella of money. Equipment is essentially a money issue, as is salary or subsistence for you and other people involved in the research. Funds for assistants, supplies, and travel have to be calculated before you can actually conduct a major research project. No matter how interesting it is to you, and no matter how important it may seem theoretically, if you haven’t got the resources to use the right methods, skip it for now.

Naturally, most people do not have the money it takes to mount a major research effort. That’s why there are granting agencies. Writing proposals is a special craft. It pays to learn it early. Research grants for M.A. research are typically between $1,000 and $5,000. Grants for doctoral research are typically between $10,000 and $30,000. If you spend 100 hours working on a grant proposal that brings you $10,000 to do your research, that’s $100 an hour for your time. If you get turned down and spend another 100 hours rewriting the proposal, that’s still $50 an hour for your time if you’re successful. Pretty good pay for interesting work.

If your research requires comparison of two groups over a period of 12 months, and you only have money for 6 months of research, can you accomplish your research goal by studying one group? Can you accomplish it by studying two groups for 3 months each? Ask yourself whether it’s worthwhile pursuing your research if it has to be scaled down to fit available resources. If the answer is ‘‘no,’’ then consider other topics.

Does the research require access to a particular village? Can you gain access to that village? Will the research require that you interview elite members of the society you are studying—like village elders, shamans, medical malpractice lawyers, Lutheran priests? Will you be able to gain their cooperation? Or will they tell you to get lost or, even worse, lead you on with a lot of cliche´s about their culture? It’s better not to do the study in the first place than to wind up with useless data.

People

‘‘People’’ includes you and others involved in the research as well as those whom you are studying. Does the research require that you speak Papiamento? If so, are you willing to put in the time and effort to learn that language? Can the research be done effectively with interpreters? If so, are such people available at a cost that you can handle? Does the research require that you personally do multiple regression? If it does, are you prepared to acquire that skill?

ETHICS

I wish I could give you a list of criteria against which you could measure the ‘‘ethicalness’’ of every research idea you ever come up with. Unfortunately, it’s not so simple. What’s popularly ethical today may become popularly unethical tomorrow, and vice versa. (This does not mean that all ethics are relative. But more on that later.) During World War II, lots of anthropologists worked for what would today be called the Department of Defense, and they were applauded as patriots for lending their expertise to the war effort (Mead 1979). In the 1960s, anthropologists took part in Project Camelot, a project by the U.S. Army to study counterinsurgency in Latin America (Horowitz 1965). This caused a huge outpouring of criticism, and the American Anthropological Association (AAA) produced its first statement on ethics—not a formal code, but a statement—in 1967, rejecting quite specifically the use of the word ‘‘anthropology’’ as a disguise for spying (Fluehr-Lobban 1998:175).

During the Vietnam War, some anthropologists did clandestine work for the Department of Defense. There was a strong reaction against this behavior, and in 1971 the AAA promulgated a formal code of ethics, titled Principles of Professional Responsibility (American Anthropological Association 1991). That document specifically forbade anthropologists from doing any secret research and asserted the AAA’s right to investigate allegations of behavior by anthropologists that hurts people who are studied, students, or colleagues (Fluehr-Lobban 1998:177). More recently, anthropologists have participated in U.S. military programs for studying local culture in battle zones and this, too, has produced intense debate within the discipline about the proper role, if any, of anthropologists in military and intelligence operations (Rohde 2007) (Further Reading: anthropology in the military and in intelligence).

Despite the rhetoric, though, no anthropologists have been expelled from the AAA because of unethical conduct. One reason is that, when push comes to shove, everyone recognizes that there are conflicting, legitimate interests. In applied anthropology, for example, you have a serious obligation to those who pay for research. This obligation may conflict with your obligation to those whom you are studying. And when this happens, where do you stand? The Society for Applied Anthropology has maintained that the first obligation is to those whom we study. But the National Association of Practicing Anthropologists has promulgated a statement of professional responsibilities that recognizes how complex this issue can be (http://practicinganthropology.org/ethical -guidelines).

We are a long, long way from finding the answers to these questions (Caplan 2003; Fluehr-Lobban 2002). Today, anthropologists are once again working for the Department of Defense. Is this simply because that’s where the jobs are? (box 3.1).

Perhaps. Times and popular ethics change. Whether you are subject to those changes is a matter for your own conscience, but it’s because popular ethics change that Stanley Milgram was able to conduct his famous experiment on obedience in the 1960s.

Milgram’s Obedience Experiment

Milgram (1963, 1965) duped people into thinking that they were taking part in an experiment on how well human beings learn under conditions of punishment. The subjects in the experiment were ‘‘teachers.’’ The ‘‘learners’’ were Milgram’s accomplices. The idea was to see how obedient people would be—how much electrical shock they would administer to a ‘‘learner’’ when told to do so by someone in authority, like an experimenter in a lab coat.

Milgram varied the conditions in his experiments to test for gender differences, for differences in locale (the Yale University campus vs. a run-down building in downtown Bridgeport, Connecticut), and for differences the proximity of the experimenter and the victim to the subject (in the same room, in different rooms), but in all the experiments, the basics were the same. The subjects sat at a panel of 30 switches, labeled from 15 volts

BOX 3.1

W H E R E T H E J O B S A R E

In 1961, when I entered graduate school, there were 39 departments of anthropology in the United States and fewer than 100 Ph.D. degrees awarded—in all four fields of anthropology. Today, there are 105 Ph.D.-granting departments of anthropology in the United States awarding about 500 Ph.D.s per year (Rudd et al. 2008:3). As of 2005, about 22% of Ph.D. anthropologists went into nonacademic jobs (Rudd et al. 2008:4). This is only a part of the story, though. Counting all anthropologists, including those without the Ph.D., there were more working outside academe in 1986 than in it (Fluehr-Lobban 2002:xii). The growth in nonacademic jobs for anthropologists has increased steadily since then. In 2009, there were over 1,500 registered members of the anthrodesign listerv (devoted to an anthropological approach to product design and marketing) on Yahoo.com.

to 450 volts. Each switch supposedly delivered 15 more volts than the last, and the panel had labels every four switches (that is, every 60 volts), from ‘‘Slight Shock’’ (15 volts) all the way up to ‘‘Danger: Severe Shock’’ (375 volts) and ‘‘XXX’’ (435 volts and 450 volts). Each time the learner made a mistake on a word-recall test, the subject was told to give the learner a bigger shock.

Milgram paid each participant $4.50 up front (about $32 in 2010 dollars) to make them feel obligated to go through with the experiment. He also gave them a little test shock—45 volts (the second lever on the 30-lever panel)—to make them believe that the punishment they’d be delivering to the so-called learners was for real.

In many of the experiments, the learner grunted at 75 volts. The reaction escalated as the putative voltage increased. At 150 volts, learners began pleading to be let out of the experiment. And at 285 volts, the learner’s response, as Milgram reported it, could ‘‘only be described as an agonizing scream’’ (1974:4). All those reactions by the learners were actually played back from tape so that subjects would hear exactly the same things. The experimenter, in a gray lab coat, kept telling the subject to administer the shocks—saying things like: ‘‘You have no choice. You must go on.’’ In the original experiment (where, by the way, the learner didn’t complain until the subject supposedly gave him a 300-volt shock, and then pounded on the wall of the room separating him from the subject), 65% of Milgrams’s subjects obeyed orders and administered what they thought were shocks beyond the XXX level. Many subjects protested but were convinced by the researchers that it was all right to follow orders.

Until Milgram did his experiments, it had been easy to scoff at Nazi war criminals whose defense was that they were ‘‘just following orders.’’ In 1979, Milgram was asked on CBS’s show, Sixty Minutes, if that sort of thing could happen again. His answer: ‘‘Having observed a thousand people in the experiment . . . if a system of death camps were set up in the United States of the sort we had seen in Nazi Germany, one would be able to find sufficient personnel for those camps in any medium-sized American town’’ (quoted in Blass 1999:955) (box 3.2).

BOX 3.2

S O M E Q U E S T I O N S A B O U T M I L G R A M ’ S E X P E R I M E N T S O N O B E D I E N C E

Are Milgram’s findings still important? When people hear about Milgram’s study they typically say that they wouldn’t be as blindly obedient to authority as Milgram’s subjects were. Most of those who dropped out of Milgram’s experiments did so after administering 150-volt shocks. Milgram’s full experiment wouldn’t get by any Human Subjects Review Board now, but Jerry Burger (2009) was able to replicate Milgram’s original experiment up to that crucial 150-volt limit. The bottom line: Twenty-eight of Burger’s 40 subjects agreed to continue after the 150-volt limit.

Were Milgram’s experiments unethical? Did Milgram cause his subjects emotional harm when they thought about what they’d done? If you were among Milgram’s subjects who obeyed to the end, would you be haunted by this? The literature on this is mixed (see Murray [1980] and Herrera [2001] for contrasting views), but we do know this: Milgram’s make-believe experiment was less costly, and more ethical, than the natural experiments carried out at My Lai, or Chatila, or Srebenica—the Vietnamese village (in 1968) and the Lebanese refugee camp (in 1982), and the Bosnian village (1995)—whose civilian inhabitants were wiped out by American and Lebanese and Serbian soldiers, respectively, ‘‘under orders.’’ Those experiments, too, showed what ordinary people are capable of doing—except that in those cases, real people really got killed.

What Does It All Mean?

Just because times, and ethics, seem to change, does not mean that anything goes. Everyone agrees that scholars have ethical responsibilities, but not everyone agrees on what those responsibilities are. All the major scholarly societies have published their own code of ethics—all variations on the same theme, but all variations nonetheless. I’ve listed the Internet addresses for several of these codes of ethics in appendix E.

These documents are not perfect, but they cover a lot of ground and are based on the accumulated experience of thousands of researchers who have grappled with ethical dilemmas over the past 60 years. Look at those codes of ethics regularly during the course of any research project, both to get some of the wisdom that has gone into them and to develop your own ideas about how the documents might be improved.

Don’t get trapped into nihilistic relativism. Cultural relativism (the unassailable fact that people’s ideas about what is good and beautiful are shaped by their culture) is a great antidote for overdeveloped ethnocentrism. But, as Merrilee Salmon makes clear (1997), ethical relativism (that all ethical systems are equally good since they are all cultural products) is something else entirely.

Can you imagine defending the human rights violations of Nazi Germany as just another expression of the richness of culture? Would you feel comfortable defending, on the basis of cultural relativism, the so-called ethnic cleansing in the 1990s of Bosnians and Kosovar Albanians by Serbs in the former Yugoslavia? Or the slaughter of Tutsis by Hutus in Rwanda? Or of American Indians by immigrant Europeans in the 19th century?

There is no value-free science. Everything that interests you as a potential research focus comes fully equipped with risks to you and to the people you study. Should anthropologists do social marketing for a state lottery, knowing that poor people will be squandering their meager resources on false hopes of sudden riches? Or is social marketing only for getting people to use condoms and to wash their hands before preparing food? Should anthropologists work on projects that raise worker productivity in developing nations if that means some workers will become redundant? In each case, all you can do (and must do) is assess the potential human costs and the potential benefits. And when I say ‘‘potential benefits,’’ I mean not just to humanity in the abstract, but also to you personally.

Don’t hide from the fact that you are interested in your own glory, your own career, your own advancement. It’s a safe bet that your colleagues are interested in their career advancement, too. We have all heard of cases in which a scientist put her or his career above the health and well-being of others. This is devastating to science, and to scientists, but it happens when otherwise good, ethical people (1) convince themselves that they are doing something noble for humanity, rather than for themselves, and (2) consequently fool themselves into thinking that that justifies their hurting others. (See Hudson [2004] for more on fraud in science.) When you make these assessments of costs and benefits, be prepared to come to decisions that may not be shared by all your colleagues. Remember the problem of the relation between darkness of skin color and measures of life success, like wealth and longevity? Would you, personally, be willing to participate in a study of this problem?

Suppose the study was likely to show that a statistically significant percentage of the variation in earning power in the United States is predictable from (not caused by) darkness of skin color. Some would argue that this would be useful evidence in the fight against racism and would jump at the chance to do the investigation. Others would argue that the evidence would be used by racists to do further damage in our society, so the study should simply not be done lest the information it produces fall into the wrong hands.

There is no answer to this dilemma. Above all, be honest with yourself. Ask yourself: Is this ethical? If the answer is ‘‘no,’’ then skip it; find another topic. Once again, there are plenty of interesting research questions that won’t put you into a moral bind (Further Reading: ethical issues in anthropology).

THEORY—EXPLANATION AND PREDICTION

All research is specific. Whether you conduct ethnographic or questionnaire research, the first thing you do is describe a process or investigate a relation among some variables in a population. Description is essential, but to get from description to theory is a big leap. It involves asking: ‘‘What causes the phenomenon to exist in the first place?’’ and ‘‘What does this phenomenon cause?’’ Theory, then, is about explaining and predicting things.

It may seem odd to talk about theory in a book about methods, but you can’t design research until you choose a research question, and research questions depend crucially on theory. A good way to understand what theory is about is to pick something that begs to be explained and to look at competing explanations for it. See which explanation you like best. Do that for a few phenomena and you’ll quickly discover which paradigm you identify with. That will make it easier to pick research problems and to develop hypotheses that you can go off and test.

Here is an example of something that begs to be explained: Everywhere in the world, there is a very small chance that children will be killed or maimed by their parents. However, the chance that a child is killed by a parent is much higher if a child has one or more nonbiological parents than if the child has two biological parents (Daly and Wilson 1988, 1998; Lightcap et al. 1982). This ‘‘Cinderella effect,’’ as it’s known, means that those evil-step-parent folk tales are based on more than fantasy. Or are they? A lot depends on the paradigm you start with.

Alternative Paradigms for Building Theories

One explanation is that this is all biological—in the genes. After all, male gorillas are known to kill off the offspring of new females they bring into their harem. Humans, the reasoning goes, have a bit of that instinct in them, too. They mostly fight and overcome the impulse, but over millions of cases, it’s bound to come out once in a while. Culture usually trumps biology, but sometimes, biology is just stronger. This is an explanation based on assumptions from sociobiology or evolutionary psychology or evolutionary anthropology.

Another explanation is that it’s cultural. Yes, it seems like it’s more common for children to be killed by nonbiological than by biological parents, but this kind of mayhem is more common in some cultures than in others. Also, the deaths of some children at the hand of their biological parents may go unnoticed and unreported simply because we don’t expect that, while the deaths of children at the hands of nonbiological parents get more notice simply because we’re on the lookout for it (Crume et al. 2002). And, although killing children is rare everywhere, in some cultures mothers are more likely to kill their children; in other cultures, fathers are more likely to be the culprits. This is because women and men learn different gender roles in different societies. So, the reasoning goes, we have to look at cultural differences for a true explanation of the phenomenon. This is called an idealist, or a cultural, theory because it is based on what people think—on their ideas.

Yet another explanation is that when adult men and women bring children to a second marriage, they know that their assets are going to be diluted by the claims the spouse’s children have on those assets—immediate claims and later claims of inheritance. This leads some of those people to harm their spouse’s children from the former marriage. In a few cases, this causes death. This is a materialist theory, as is the idea that women who have children from a previous marriage may, on average, be forced to marry men who carry a higher risk of being abusive.

Sociobiology, idealism, and materialism are not theories. They are paradigms or theoretical perspectives. They contain a few basic rules for finding theories that explain observed events. Sociobiology stresses the primacy of evolutionary, biological features of humans as the basis for human behavior. Idealism stresses the importance of internal states—attitudes, preferences, ideas, beliefs, values—as the basis for human behavior. And materialism stresses structural and infrastructural forces—like the economy, the technology of production and reproduction, demography, and environmental conditions—as causes of human behavior.

When you want to explain a specific phenomenon, you apply the principles of your favorite paradigm and come up with a specific explanation—a theory.

Why do women everywhere in the world tend to have nurturing roles? If you think that biology rules here, then you’ll be inclined to support evolutionary theories about other phenomena as well. If you think economic and political forces cause values and behavior, then you’ll be inclined to apply the materialist perspective in your search for explanations in general. If you think that culture—people’s values—is of paramount importance, then you’ll tend to apply the idealist perspective to come up with explanations. The different paradigms are not so much in competition as they are complementary, for different levels of analysis. The evolutionary explanation for the battering of nonbiological children is appealing for aggregate, evolutionary phenomena—the big, big picture. An evolutionary explanation addresses the question: What is the reproductive advantage of this behavior happening at all?

But we know that the behavior of hurting or killing step-children is not inevitable, so an evolutionary explanation can’t account for why some step-parents hurt their children and others don’t. A materialist explanation is more productive for addressing this question. Some step-parents who bring a lot of resources to a second marriage become personally frustrated by the possibility of having their wealth raided and diluted by their new spouse’s children. The reaction would be strongest for step-parents who have competing obligations to support their biological children who are living with yet another family. These frustrations will cause some people to become violent, but not others.

But even this doesn’t explain why a particular step-parent is supportive or unsupportive of his or her nonbiological children. At this level of analysis, we need a processual and psychological explanation, one that takes into account the particular historical facts of the case. Whatever paradigm they follow, all empirical anthropologists rely on ethnography to test their theories.

Handwerker (1996b), for example, found that step-parents in Barbados were, overall, no more likely to treat children violently than were biological parents. But the presence of a step-father increased the likelihood that women battered their daughters and decreased the likelihood that women battered their sons. In homes with step-parents, women saw their daughters as potential competitors for resources available from their partner and they saw sons as potential sources of physical protection and income.

And there was more. Powerful women (those who had their own sources of income) protected their children from violence, treated them affectionately, and elicited affection for them from their man. The probability that a son experienced an affectionate relationship with a biological father rose with the length of time the two lived together, but only for sons who had powerful mothers. Men battered powerless women and the children of powerless women, and powerless women battered their own children.

Is there any evolutionary basis for powerful spouses to batter powerless ones? Or is this all something that gets stimulated by material conditions, like poverty? A lot of research is being done on this now but this much is clear: Different paradigms produce different, interesting answers to the same question.

Idiographic and Nomothetic Theory

Theory comes in two basic sizes: elemental, or idiographic theory and generalizing or nomothetic theory. An idiographic theory accounts for the facts in a single case. A nomothetic theory accounts for the facts in many cases. The more cases that a theory accounts for, the more nomothetic it is.

The distinction was first made by Wilhelm Windelband, a philosopher of science, in 1894. By the late 1800s, Wilhelm Dilthey’s distinction between the Naturwissenschaften and Geisteswissenschaften—the sciences of nature and the sciences of the mind—had become quite popular. The problem with Dilthey’s distinction, said Windelband, was that it couldn’t accommodate the then brand-new science of psychology. The subject matter made psychology a Geisteswissenchaft, but the discipline relied on the experimental method, and this made it a Naturwissenschaft.

What to do? Yes, said Windelband, the search for reliable knowledge is, indeed, of two kinds: the sciences of law and the sciences of events, or, in a memorable turn of phrase, ‘‘the study of what always is and the study of what once was.’’ Windelband coined the terms idiographic and nomothetic to replace Dilthey’s Natur- and Geisteswissenschaften.

Organic evolution is governed by laws, Windelband observed, but the sequence of organisms on this planet is an event that is not likely to be repeated on any other planet. Languages are governed by laws, but any given language at any one time is an event in human linguistic life. The goal of the idiographic, or historical sciences, then, is to deliver ‘‘portraits of humans and human life with all the richness of their unique forms’’ (Windelband 1998 [1894]:16).

Windelband went further. Every causal explanation of an event—every idiographic analysis, in other words—requires some idea of how things happen at all. No matter how vague the idea, there must be nomothetic principles guiding idiographic analysis.

Windelband’s formulation is a perfect description of what all natural scientists— vulcanologists, ornithologists, astronomers, ethnographers—do all the time. They describe things; they develop deep understanding of the cases they study; and they produce explanations for individual cases based on nomothetic rules. The study of a volcanic eruption, of a species’ nesting habits, of a star’s death is no more likely to produce new nomothetic knowledge than is the study of a culture’s adaptation to new circumstances. But the idiographic effort, based on the application of nomothetic rules, is required equally across all the sciences if induction is to be applied and greater nomothetic knowledge achieved.

Those efforts in psychology are well known: Sigmund Freud based his theory of psychosexual development on just a few cases. Jean Piaget did the same in developing his universal theory of cognitive development, as did B. F. Skinner in developing the theory of operant conditioning.

In anthropology, Lewis Henry Morgan (1877) and others made a brave, if ill-fated effort in the 19th century to create nomothetic theories about the evolution of culture from the study of cases at hand. The unilineal evolutionary theories they advanced were wrong, but the effort to produce nomothetic theory was not wrong. Franz Boas and his students made clear the importance of paying careful attention to the particulars of each culture, but Leslie White (1959) and Julian Steward (1949, 1955) did not reject the idea that cultures evolve. Instead, they advanced more nuanced theories about how the process works.

Steward (1955) chose just a handful of cases when he developed his theory of cultural evolution. Over time, data from Tehuaca´n, Mexico, and Ali Kosh, Iran—6,000 miles and several thousand years apart—support Steward’s nomothetic formulation about the multistage transition from hunting and gathering to agriculture. (The sequences appear to be similar responses to the retreat of the last glacier of the Paleolithic.) As we get more comparisons, the big picture will either become more and more nomothetic or it will be challenged.

And the effort goes on. Wittfogel (1957) developed his so-called hydraulic theory of cultural evolution—that complex civilizations, in Mexico, India, China, Egypt, and Mesopotamia developed out of the need to organize the distribution of water for irrigation— based on idiographic knowledge of a handful of cases. David Price (1995) studied a modern, bureaucratically organized water supply system in the Fayoum area of Egypt. The further downstream a farmer’s plot is from an irrigation pump, the less water he is likely to get because farmers upstream divert more water than the system allows them legally to have. Price’s in-depth, idiographic analysis of the Fayoum irrigation system lends support to Wittfogel’s long neglected theory because, says Price, it shows ‘‘how farmers try to optimize the disadvantaged position in which the state has placed them’ (1995:107–108). Susan Lees (1986) showed how farmers in Israel, Kenya, and Sudan got around bureaucratic limitations on the water they were allotted. We need much more idiographic analysis, more explanations of cases, to test the limitations of Wittfogel’s theory. (See Harrower [2009] for recent archeological work in southern Arabia on the role of irrigation systems in state formation.)

Idiographic Theory

As in all sciences, most theory in anthropology is idiographic. Here are three examples:

1. In 1977, the New Delhi police reported 311 deaths by kitchen fires of women, mostly young brides who were killed because their families had not delivered a promised dowry to the groom’s family (Claiborne 1984). By 1987, the government of India reported 1,912 such ‘‘dowry deaths’’ of young women, and by 1997 the number was 6,975—over 19 per day (Dugger 2000; and see Shenk 2007; Srinivasan 2005; Van Willigen and Chana 1991). How to explain this?

Gross (1992) theorized that the phenomenon is a consequence of female hypergamy (marrying up) and dowry. Families that can raise a large dowry in India can marry off their daughter to someone of a higher caste and greater means. This has created a bidding war, as the families of wealthier sons demand more and more for the privilege of marrying those sons (and see S. Anderson 2003).

Apparently, many families of daughters in India have gone into debt to accumulate the dowries. When they can’t pay off the debt, some of the families of grooms have murdered the brides in faked ‘‘kitchen accidents,’’ where kerosene stoves purportedly blow up. This gives the grooms’ families a chance to get another bride whose families can deliver.

2. Next, consider the case of fraternal polyandry, where two or more brothers marry one woman. This phenomenon has been the subject of investigation by anthropologists for generations (Petros 1963). In 1971, Goldstein observed that the custom was practiced in Tibet only among a class of serfs, known as tre-ba, who held title to their land but who also had major tax and corve´e obligations to their lord. In order not to break up the land, Goldstein concluded, brothers would take a single bride into one household.

3. Finally, consider an idiographic theory derived entirely from ethnography. When Anthony Paredes began his study of the Poarch Band of Creek Indians in Alabama the group was a remnant of an earlier group. They had lost the use of the Creek language, were not recognized by the U.S. government as a tribe, and had little contact with other Indians for decades. Yet, the Poarch Creek Indians had somehow maintained their identity.

Paredes wanted to know how the Indians had managed this. He did what he called ‘‘old-fashioned ethnography,’’ including key-informant interviewing and learned about a cultural revitalization movement that had been going on since the 1940s. That movement was led by some key people whose efforts over the years had made a difference. Paredes’s description of how the Poarch Creek Indians held their cultural identity in the face of such odds is an excellent example of elemental, idiographic theory. As you read his account you feel you understand how it worked (see Paredes 1974, 1992).

So What’s Wrong?

Nothing’s wrong. Gross’s explanation for the kitchen fires in India rings true, but it doesn’t explain why other societies that have escalating dowry don’t have kitchen fires. Nor does it tell us why dowry persists in India despite being outlawed since 1961, or why dowry—which, after all, only occurs in 7.5% of the world’s societies—exists in the first place. But Gross’s theory is a first-class example of theory at the local level—where research begins.

Goldstein’s theory is attractive for understanding the Tibetan case of fraternal polyandry, but it doesn’t say anything about other cases of polyandry, like the one studied by Hiatt in Sri Lanka (1980). Over the years, other case studies of polyandry, in Tibet and elswhere, have either supported or not supported Goldstein’s theory (Levine 1988; Levine and Silk 1997). As the idiographic studies build, we’ll gain better and better understanding of the nomothetic principles, if any, at work. In the meantime, E. A. Smith (1998) and others have applied an an evolutionary perspective to understanding polyandry and other scholars have tested the effects of structural changes on polyandry.

Paredes’s theory helps us understand how the Poarch Creeks maintained their cultural identity, but it doesn’t tell us how other Native American groups managed to do this or why some groups did not manage it. Nor does it tell us anything about why other ethnic groups maintain or fail to maintain their identity in the United States or why ethnicity persists at all in the face of pressure from states on ethnic groups to assimilate. Others can try to make the theory more nomothetic.

In any science, much of the best work is at the idiographic level of theory making.

Nomothetic Theory

Nomothetic theories address questions like ‘‘So, what does account for the existence of dowry?’’

Several theorists have tried to answer this question. Esther Boserup (1970) hypothesized that dowry should occur in societies where a woman’s role in subsistence production is low. She was right, but many societies where women’s productive effort is of low value do not have dowry.

Gaulin and Boster (1990) offered a sociobiological theory that predicts dowry in stratified societies that have monogamous or polyandrous marriage. They tested their theory on Murdock and White’s (1969) Standard Cross-Cultural Sample of 186 societies. The Gaulin-Boster theory works better than Boserup’s—it misclassifies fewer societies. That’s how nomothetic theory grows, though the Gaulin-Boster theory still makes some mistakes. Fully 77% of dowry societies are, in fact, stratified and have monogamous marriage, but 63% of all monogamous, stratified societies do not have dowry. We need more good ideas and more tests to make the theory more inclusive—more nomothetic (box 3.3).

One More: The Second Demographic Transition

Let’s do one more—the second demographic transition. The first demographic transition happened at the end of the Paleolithic when people swapped agriculture for hunting and gathering as the main means of production. During the Paleolithic, population growth was very, very slow. But across the world, as people switched from hunting and gathering to agriculture, as they settled down and accumulated surplus, their populations exploded.

The second demographic transition began in the late 18th century in Europe with industrialization and has been spreading around the world ever since. Today, Japan, Germany, Italy, and other highly industrialized countries have total fertility rates (the aver-

BOX 3.3

C O M P A R A T I V E R E S E A R C H A N D T E S T I N G T H E O R Y

If an idiographic theory accounts for some data in say, India, Japan, or England, then an obvious next step is to see how far the theory extends. Alice Schlegel and Herbert Barry (1986), for example, looked at the consequences of female contribution to subsistence. Their nomothetic theory predicts that women will be more respected in societies where they contribute a lot to subsistence than in societies where their contribution is low.

Whether their theory is supported depends crucially on how Schlegel and Barry operationalize the concept of respect. In societies where women contribute a lot to subsistence, say Schlegel and Barry, women will be spared some of the burden of pregnancy ‘‘through the attempt to space children’’ more evenly (Schlegel and Barry 1986:146). In such societies, women will be subjected to rape less often; they will have greater sexual freedom; they will be worth more in bride wealth; and they will have greater choice in selection of a spouse. Schlegel and Barry coded the 186 societies in the Standard Cross-Cultural Sample for each of those indicators of respect—and their predictions were supported.

age number of children born to women during their reproductive years), or TFRs, in the neighborhood of 1.5 to 1.2—that’s 29% to 43% below the 2.1 TFR needed in those countries just to replace the current population. In the past 40 years, some previously high TFR countries, like Barbados, Mauritius, and Mexico, have been through a major demographic transition.

Explaining why women in Barbados are having fewer children is idiographic; predicting the conditions under which women in any underdeveloped country will start lowering their fertility rate is nomothetic. Handwerker’s theory (1989) is that women in low-wage jobs encourage their daughters to get more education. And when women get sufficiently educated, their participation in the labor market becomes more effective (they earn more), freeing them from dependency on men (sons and husbands). As this dependency diminishes, women lower their fertility.

Handwerker’s theory is nomothetic and materialist. It relies on material conditions forces to explain how preferences develop for fewer children and it does not rely on preferences (culture, ideas, values) to explain the level of a country’s TFR.

The Consequences of Paradigm

Differences in theoretical paradigms have profound consequences. If you think that beliefs and attitudes are what make people behave as they do, then if you want to change people’s behavior, the obvious thing to do is change their attitudes. This is the basis of the educational model of social change I mentioned in chapter 2—the runaway bestseller model for change in our society.

Want to get women in developing nations to have fewer children? Educate them about the importance of small families. Want to lower the rate of infectious disease in developing countries? Educate people about the importance of good hygiene. Want to get adolescents in Boston or Seattle or wherever to stop having high-risk sex? Educate them about the importance of abstinence or, if that fails, about how to take protective measures against sexually transmitted disease. Want to get people in the United States to use their cars less? Educate them about car pooling.

These kinds of programs rarely work—but they do work sometimes. You can educate people (through commercial advertising) about why they should switch from, say, a Honda to a Toyota, or from a Toyota to a Ford, but you can’t get people to give up their cars. You can educate people (through social advertising) to use the pill rather than lesseffective methods of birth control, once they have decided to lower their fertility, but educational rhetoric doesn’t influence the number of children that people want in the first place.

The closer a behavior is to the culture (or superstructure) of society, the easier it is to intervene culturally. Brand preferences are often superstructural, so advertising works to get people to switch brands—to change their behavior. But if people’s behavior is rooted in the structure or infrastructure of society, then forget about changing their behavior by educating them to have better attitudes.

Eri Sugita (2006) studied 50 women in rural Uganda who had children under 5 years of age in their care. Over 14 months of fieldwork, Sugita found that the number of liters of water available per person in each household did a better job of predicting whether the women washed their hands before preparing or serving food than did the women’s education or knowledge of hygiene. Women and children fetched all the water, so those who lived near a well were able to make more trips and get more water—unless they had a bicycle. Men, however, monopolized the bicycle in families that could afford one. Teaching people more about hygiene wouldn’t do nearly as much for public health in that village as giving women bicycles would.

In poor countries, having many children may be the only security people have in their old age. Under those circumstances, no amount of rhetoric about the advantages of small families is going to change anyone’s mind about the number of children they want to have. If you need a car because the only affordable housing is 30 miles from your job, no amount of rhetoric will convince you to take the bus. Demographic transition theory is highly nomothetic. It accounts for why Japan, a fully industrialized nation, has such a low TFR. But it doesn’t predict what the consequences of that low TFR will be. For the time being, at least (until even bigger nomothetic theories are developed), we still need an idiographic theory for this.

Japan has about 126 million people—about 40% of the population of the United States—living in an area the size of Montana. Japan has the world’s second largest economy and the Japanese enjoy a per capita income of about $34,000 in 2008 (IMF 2009). This is based on manufacturing products for export. The oil to run the factories that produce all those exports has to be imported. So does a lot of food to feed all those people who are working in the factories. The TFR of 1.3 in Japan makes it easy to predict that Japan’s industries need to find lots of new workers to maintain productivity—and the lifestyle supported by that productivity.

Belgium and Italy—two other countries with low TFRs—solved this problem by opening their borders to people from the formerly communist countries of eastern Europe and by increasing female participation in the labor force. In 1991, there was strong resistance to these solutions. By 2000, there were over 700,000 foreign workers in Japan (about 1% of the labor force), including about 230,000 illegals (Ducanes and Abella 2008:18).

How will lower TFR in the developed countries of the world affect world migration? This is one of my current favorite topics to think about because it illustrates how important theory is in developing research questions and it showcases the contributions of idealist and materialist perspectives as well as the importance of idiographic and nomothetic theory.

There is no list of research questions. You have to use your imagination and your curiosity about how things work, and follow your hunches. Above all, never take anything at face value. Every time you read an article, ask yourself: ‘‘What would a study look like that would test whether the major assertions and conclusions of this article were really correct?’’ If someone says: ‘‘The only things students care about are sex, drugs, and twitter,’’ the proper response is: ‘‘We can test that.’’

A GUIDE TO RESEARCH TOPICS, ANYWAY

There may not be a list of research topics, but there are some useful guidelines. First of all, there are very few big-theory issues—I call them research arenas—in all of social science. Here are four of them: (1) the nature-nurture problem, (2) the evolution problem, (3) the internal-external problem, and (4) the social facts or emergent properties problem.

1. The nature-nurture problem. This is an age-old question: How much of our personality and behavior is determined by our genes and how much by our exposure to different environments? Many diseases (cystic fibrosis, Tay-Sachs, sickle-cell anemia) are highly determined by our genes, but others (heart disease, diabetes, asthma) are at least partly the result of our cultural and physical environment.

Schizophrenia is a genetically inherited disease, but its expression is heavily influenced by our cultural environment. Hallucinations are commonly associated with schizophrenia, but when Robert Edgerton (1966) asked over 500 people in four East African tribes to list the behavior of people who are severely mentally ill, less than 1% of them mentioned hallucinations (see also Edgerton and Cohen 1994; Jenkins and Barrett 2004).

Research on the extent to which differences in cognitive functions of men and women are the consequence of environmental factors (nurture) or genetic factors (nature) or the interaction between those factors is part of this research arena (Caplan et al. 1997). So are studies of human response to signs of illness across cultures (Hielscher and Sommerfeld 1985; Kleinman 1980).

2. The evolution problem. Studies of how groups change through time from one kind of thing to another kind of thing are in this arena. Societies change very slowly through time, but at some point we say that a village has changed into a town or a town into a city or that a society has changed from a feudal to an industrial economy. All studies of the differences between small societies—Gemeinschaften—and big societies— Gesellschaften—are in this arena. So are studies of inexorable bureaucratization as organizations grow.

3. The internal-external problem. Studies of the way in which behavior is influenced by values and by environmental conditions are in this arena. Studies of response effects (how people respond differently to the same question asked by a woman or by a man, for example) are in this arena, too. So are studies of the difference between what people say they do and what they actually do.

4. The social facts, or emergent properties problem. The name for this problem comes from Emile Durkheim’s (1933 [1893]) argument that social facts exist outside of individuals and are not reducible to psychological facts. A great deal of social research is based on the assumption that people are influenced by social forces that emerge from the interaction of humans but that transcend individuals. Many studies of social networks and social support, for example, are in this arena, as are studies that test the influence of organizational forms on human thought and behavior.

Generating of Types of Studies

Now look at table 3.1. I have divided research topics (not arenas) into classes, based on the relation among kinds of variables.

Table 3.1 Types of Studies

	Internal States	External States	Reported Behavior	Observed Behavior	Artifacts	Environment
Internal states	I	II	IIIa	IIIb	IV	V
External states		VI	VIIa	VIIb	VIII	IX
Reported behavior			Xa	Xb	XIa	XIIa
Observed behavior				Xc	XIb	XIIb
Artifacts					XIII	XIV
Environment						XV

The five major kinds of variables are:

1. Internal states. These include attitudes, beliefs, values, and perceptions. Cognition is an internal state.

2. External states. These include characteristics of people, such as age, wealth, health status, height, weight, gender, and so on.

3. Behavior. This covers what people eat, who they communicate with, how much they work and play—in short, everything that people do and much of what social scientists are interested in understanding.

4. Artifacts. This includes all physical residue from human behavior—radioactive waste, tomato slices, sneakers, arrowheads, computer disks, Viagra, skyscrapers—everything.

5. Environment. This includes physical and social environmental characteristics. The amount of rainfall, the amount of biomass per square kilometer, location on a river or ocean front—these are physical features that influence human thought and behavior. Humans also live in a social environment. Living under a democratic versus an authoritarian re´gime or working in an organization that tolerates or does not tolerate sexual harassment are examples of social environments that have consequences for what people think and how they behave.

Keep in mind that category (3) includes both reported behavior and actual behavior. A great deal of research has shown that about a third to a half of everything people report about their behavior is not true (Bernard, Killworth et al. 1984). If you want to know what people eat, for example, asking them is not a good way to find out (Basiotis et al. 1987; R. K. Johnson et al. 1996). If you ask people how many times a year they go to church, you’re likely to get highly exaggerated data (Hadaway et al. 1993, 1998).

Some of the difference between what people say they do and what they actually do is the result of out-and-out lying. Most of the difference, though, is the result of the fact that people can’t hang on to the level of detail about their behavior that is called for when they are confronted by social scientists asking them how many times they did this or that in the last month. What people think about their behavior may be what you’re interested in, but that’s a different matter.

Most social research focuses on internal states and on reported behavior. But the study of humanity can be much richer, once you get the hang of putting together these five kinds of variables and conjuring up potential relations. Here are some examples of studies for each of the cells in table 3.1.

Cell I:

The interaction of internal states, like perceptions, attitudes, beliefs, values, and moods.

Religious beliefs, authoritarianism, and prejudice against homosexuals (Tsang and Rowatt 2007).

Perceived gender role and attitudes about rape in Turkey (Go¨lge et al. 2003).

American Indians’ beliefs about ethnic identity and their perceptions about the beliefs their parents hold regarding education (Okaqaki et al. 2009).

This cell is also filled with studies that compare internal states across groups. For example, Cooke’s (2004) study of attitudes toward gun control among American, British, and Australian youth and Yarrow et al.’s (2006) study comparing the early development of implicit racial prejudice in rural Japan and urban United States.

Cell II:

The interaction of internal states (perceptions, beliefs, moods, etc.) and external states (completed education, health status, organizational conditions).

Health status and hopefulness about the future (Vieth et al. 1997).

The relation between racial attitudes and the political context in different cities (Glaser and Gilens 1997).

Cell IIIa:

The interaction between reported behavior and internal states.

The relation, among adolescent girls in New Hampshire, between feeling that it’s important to contribute to their community and self-reports of taking up smoking (Dinapoli 2009).

Attitudes toward the environment and reported environment-friendly behavior (Minton and Rose 1997).

Cell IIIb:

The interaction between observed behavior and internal states.

Attitudes and beliefs about resources and actual behavior in the control of a household thermostat (Kempton 1987).

Mexicans report being less talkative (feeling less sociable) than Americans but are behaviorally more social (more talkative) than Americans (Ramı´rez-Esparza et al. 2009).

Cell IV:

The interaction of material artifacts and internal states.

The effects on Holocaust Museum staff in Washington, DC, of working with the physical reminders of the Holocaust (McCarroll et al. 1995).

The ideas and values that brides and grooms in the United States share (or don’t share) about the kinds of ritual artifacts that are supposed to be used in a wedding (Lowrey and Otnes 1994).

How children learn that domestic artifacts are considered feminine and artifacts associated with nondomestic production are considered masculine (Crabb and Bielawski 1994).

Cell V:

The interaction of social and physical environmental factors and internal states.

How culture influences the course of schizophrenia (Edgerton and Cohen 1994).

The extent to which adopted children and biological children raised in the same household develop similar personalities (Loehlin et al. 2009).

Cell VI:

How the interaction among external states relates to outcomes, like longevity or financial success.

The effects of age, sex, race, marital status, education, income, employment status, and health status on the risk of dying from the abuse of illegal drugs (Kallan 1998).

The impact of a person’s race, age, and gender, along with community crime rate, unemployment rate, and voting patterns on the length of received prison sentences (Helms and Jacobs 2002).

The effect of skin color on acculturation among Mexican Americans (Montalvo and Codina 2001; Vasquez et al. 1997).

Cell VIIa:

The relation between external states and reported behavior.

The likelihood that baby-boomers will report attending church as they get older (Miller and Nakamura 1996).

The effect of age, income, and season on how much leisure time Tawahka Indian spouses spend with each other (Godoy 2002).

Gender differences in self-reported marijuana use (Warner et al. 1999) and suicidal behavior (Vannatta 1996) among adolescents.

Cell VIIb:

The relation between external states and observed behavior.

The relation between the importance of gender-specific subsistence activities and the amount of time in childhood allocated to playing (and and learning) those activities (Bock and Johnson 2004).

Observed recycling behavior among Mexican housewives is better predicted by their observed competencies than by their beliefs about recycling (Corral-Verdugo 1997).

Cell VIII:

The relation of physical artifacts and external states.

How age and gender differences relate to cherished possessions among children and adolescents from 6 to 18 years of age (Dyl and Wapner 1996).

How engineering drawings and machines delineate boundaries and facilitate interaction among engineers, technicians, and assemblers in a firm that manufactures computer chips (Bechky 2003).

Cell IX:

The relation of external states and environmental conditions.

How the work environment contributes to heart disease (Kasl 1996).

The different effects, for older men and women in the United States, of neighborhood characteristics on the likelihood of obesity (Grafova et al. 2008).

How proximity to a supermarket affects the nutrition of pregnant women (Laraia et al. 2004).

Cell Xa:

The relation between behaviors, as reported by people to researchers.

The relation of self-reported level of church attendance and self-reported level of environmental activism among African Americans in Louisiana (Arp and Boeckelman 1997).

The relation of reported changes in fertility practices to reported changes in actions to avoid HIV infection among women in rural Zimbabwe (Gregson et al. 1998).

Cell Xb:

The relation between reported and observed behavior.

Assessing the accuracy of reports by Tsimane Indians in Bolivia about the size of forest plots they’ve cleared in the past year by comparing those reports to a direct physical measure of the plots (Vadez et al. 2003).

The relation of reports about recycling behavior and actual recyling behavior (Corral-Verdugo 1997).

Cell Xc

The relation between observed behaviors

Slower eating reduces the amount of food that men actually eat, but not on how much women eat (C. Martin et al. 2007).

Cell XIa:

The relation of observed behavior to specific physical artifacts.

The number of incidents of smoking in movies was the same in 2002 as it was in 1950, even though the incidence of smoking had declined by half in that time (Glantz et al. 2004).

Cell XIb:

The relation of reported behavior to specific physical artifacts.

People who are employed view prized possessions as symbols of their own personal history, whereas people who are unemployed see prized possessions as having utilitarian value (Ditmar 1991).

Cell XIIa:

The relation of reported behavior to factors in the social or physical environment.

The relation of compulsive consumer behavior in young adults and whether they were raised in intact or disrupted families (Rindfleisch et al. 1997).

The relation of social support and independent daily functioning (bathing, eating, etc.) in elder Navajos (Fitzpatrick et al. 2008).

Cell XIIb:

The relation of observed behavior to factors in the social or physical environment.

People are willing to wait longer when music is playing than when there is silence (North and Hargreaves 1999).

How environmental features of gay bathhouses facilitate sexual activity (Tewksbury 2002).

Cell XIII:

The association of physical artifacts to one another and what this predicts about human thought or behavior.

The research on how to arrange products in stores to maximize sales is in this cell. Comparing the favorite possessions of urban Indians (in India) and Indian immigrants to the United States to see whether certain sets of possessions remain meaningful among immigrants (Mehta and Belk 1991). This is also an example of Cell IV. Note the difference between expressed preferences across artifacts and the coexistence of artifacts across places or times.

Cell XIV:

The probability that certain artifacts (relating, for example, to subsistence) will be found in certain physical or social environments (rain forests, deserts, shoreline communities). In anthropology, this area of research is mostly the province of archeology.

Cell XV:

How features of the social and physical environment interact and affect human behavioral and cognitive outcomes.

Social and physical environmental features of retail stores interact to affect the buying behavior of consumers (Baker et al. 1992).

Social and physical environmental features of communities interact to affect people’s physical activity (Transportation Research Board and Institute of Medicine 2005).

The above list is only meant to give you an idea of how to think about potential covariations and, consequently, about potential research topics. Always keep in mind that covariation does not mean cause. Covariation can be the result of an antecedent or an intervening variable, or even just an accident. (Refer to chapter 2 for a discussion of causality, spurious relations, and antecedent variables.)

And keep in mind that many of the examples in the list above are statements about possible bivariate correlations—that is, about possible covariation between two things. Social phenomena being the complex sorts of things they are, a lot of research involves multivariate relations—that is, covariation among three or more things at the same time.

For example, it’s well known that people who call themselves religious conservatives in the United States are likely to support the National Rifle Association’s policy on gun control (Cell I). But the association between the two variables (religious beliefs and attitudes toward gun control) is by no means perfect and is affected by many intervening variables.

I’ll tell you about testing for bivariate relations in chapter 21 and about testing for multivariate relations in chapter 22. As in so many other things, you crawl before you run and you run before you fly.

THE LITERATURE SEARCH

The first thing to do after you get an idea for a piece of research is to find out what has already been done on it. Don’t neglect this part of the research process. You need to make a heroic effort to uncover sources. People will know it if you don’t, and without that effort you risk wasting a lot of time going over already-covered ground. Even worse, you risk having your colleagues ignore your work because you didn’t do your homework. Fortunately, heroic efforts are pretty easy, what with all the resources available for scouring the literature.

Begin by looking through volumes of the Annual Review. There are Annual Review volumes for psychology (every year since 1950), anthropology (every 2 years from 1959– 1971 and every year since 1972), sociology (since 1975), public health (since 1997), and political science (since 1998). Authors who are invited to publish in these volumes are experts in their fields; they have digested a lot of information and have packaged it in a way that gets you right into the middle of a topic in a hurry.

Also contact people on listservs and networking groups that deal with your research topic. If there are central figures in the field, contact them by e-mail and request a time when you can call them on the phone. Yes, by phone. E-mail may be convenient for you, but most scholars are just too busy to respond to requests for lists of articles and books. On the other hand, many scholars will talk to you on the phone if they think they can really help.

All you need is a few key references to get started. Don’t worry about the key references being out of date. The ISI Web of Knowledge eliminates the problem of obsolescence in bibliographies.

The ISI Web ofKnowledge

The Thompson Reuters corporation produces the ISI Web of Knowledge, which contains the Science Citation Index Expanded, the Social Sciences Citation Index, and the Arts and Humanities Citation Index. These indexes are available online at most university libraries, and in many small college libraries. I used the paper versions of these indexes for 30 years before they went online. If the online versions vanished, I’d go back to the paper ones in a minute. They’re that good.

At the ISI Web of Knowledge headquarters in Philadelphia, hundreds of people pore over thousands of journals each year—about 8,000 in the sciences, about 2,700 in the social sciences, and about 1,500 in the arts and humanities. (Some journals are indexed in more than one database, but that still means about 10,000 journals every year.) The staff at ISI enter the title, author, journal, year, page numbers for each article and, where available, the e-mail address of the corresponding author—that is, the author to whom you would write if you had a question about something in an article.

The most important part though is this: The staff enters all the references cited by each author of each article in each journal surveyed. Some articles have a handful of references, but review articles, like the ones in the Annual Review series, can have hundreds of citations. All those citations go into the Web of Knowledge databases. So, if you know the name of just one author whose work should be cited by anyone working in a particular field, you can find out, for any given year, who cited that author, and where. In other words, you can search the literature forward in time, and this means that older bibliographies, like those in the Annual Review series, are never out of date.

Suppose you are interested in the sociolinguistics of African American Vernacular English, also known as Black English. If you ask anyone who has worked on this topic (a sociolinguist in your department, for example) you’ll run right into William Labov’s Language in the Inner City: Studies in the Black English Vernacular, published in 1972. Look up the subject heading of Black English in your library’s catalog and you’ll also find Spoken Soul: The Story of Black English, by John and Russell Rickford (2000) and Black Street Speech by John Baugh (1983). You’ll find Labov’s book mentioned prominently in both of the latter books, so right away, you know that Labov’s book is a pioneering work and is going to be mentioned by scholars who come later to the topic.

If you are starting a search today of the literature about Black English, you’d want to know who has cited Labov’s work, as well as the works of Baugh and the Rickfords. That’s where the Web of Knowledge comes in. The Social Science Citation Index alone indexes about 150,000 articles a year. Okay, so 150,000 sources is only a good-sized fraction of the social science papers published in the world each year, but the authors of those articles read—and cited—about 3 million citations to references to the literature (Web of Science Databases. http://tinyurl.com/nltbhy). That’s 3 million citations every year, for decades and decades. Now that’s a database.

That classic book by Labov on Black English? As of January 2009, some 1,500 researcher articles had cited the book across the sciences and the humanities. Of those, the Web of Knowledge shows you the full citation for about 1,100 (that is, articles that are in its own database). You can take any of those citations and clip it into another search window and keep the search going. And going and going.

Don’t get overwhelmed by this. You’ll be surprised at how quickly you can scan through a thousand hits and pick out things you really need to take a closer look at. As you read some articles and books, you’ll find yourself running into the same key literature again and again. That’s when you know you’re getting to the edges of the world on a particular topic. That’s what you want when you’re doing research—you want to be working at the edges so as to push the frontiers of knowledge back a bit (box 3.4).

BOX 3.4

G E T T I N G A R T I C L E T I T L E S R I G H T

A word of caution to new scholars who are writing for publication: Online literature searches make it easy for people to find articles only if the articles (or their abstracts) contain descriptive words. Cute titles on scientific articles hide them from people who want to find them in the indexing tools. If you write an article about illegal Mexican labor migration to the United States and call it something like ‘‘Whither Juan? Mexicans on the Road,’’ it’s a sure bet to get lost immediately, unless (1) you happen to publish it in one of the most widely read journals and (2) it happens to be a blockbuster piece of work that everyone talks about and is cited in articles that do have descriptive titles.

Because most scientific writing is not of the blockbuster variety, you’re better off putting words into the titles of your articles that describe what the articles are about. It may seem awfully dull, but descriptive, unimaginative titles are terrific for helping your colleagues find and cite your work.

I use the Web of Knowledge regularly to keep current with the literature on several topics. I’ve studied bilingualism in Mexico, for example, particularly the development of bilingual education among the N^˜ a¨hn˜u of the Mezquital Valley. The N^˜ a¨hn˜u are widely known in the literature as the Otomı´, so I scan the Web of Knowledge and look for everything with the word ‘‘Otomı´’’ in the title or abstract. Doing this even once a year makes a big difference in your ability to keep up with the expanding literature in every field.

ANTHROPOLOGY DATABASES

Besides the Web of Knowledge, important resources for anthropologists include Anthro-Source, JSTOR, and Anthropology Plus.

AnthroSource and JSTOR

AnthroSource is a service of the American Anthropological Association and is available to all members of the association. The database covers 32 journals in anthropology. JSTOR is a full-text database that covers over 1,000 journals in humanities, social sciences, and sciences. Journals available through JSTOR, including many covered by AnthroSource, have a 3 to 5 year lag. Members of the AAA, however, can access all years of the journals covered by AnthroSource.

Anthropology Plus

Anthropology Plus combines two databases, Anthropological Index Online (which is free) and Anthropological Literature (by subscription). AIO is published by the Royal Anthropological Institute in London and indexes the periodicals in Museum of Mankind library of the British Museum. Besides the major journals for cultural anthropology and archeology, AIO covers small journals from developing nations and Eastern Europe. You’ll find articles in AIO from journals like the Annals ofthe Na´prstek Museum in Prague, the Quarterly Journal of the Mythic Society, in Bangalore, and the Hong Kong Anthropology Bulletin. Anthropological Literature is the index for the books and articles at the Tozzer Library at Harvard University. The Tozzer is the largest collection of anthropological literature in the world, and Anthropological Literature grows by about 10,000 citations every year. It is particularly good for finding older materials on North American, Middle American, and South American archeology and ethnology.

If your library doesn’t subscribe to Anthropology Plus, you can use Anthropological Index Online free, here: http://aio.anthropology.org.uk/aio.

FREE DATABASES OF RELEVANCE TO ANTHROPOLOGY

ERIC

The Educational Resources Information Center, or ERIC, indexes nearly 1,000 journals of interest to researchers in education. ERIC is free at http://www.eric.ed.gov. With over a million citations, it’s a treasure, but the unique advantage of ERIC is the access it gives you to the gray literature—over 200,000, full-text research reports on research funded by government agencies and by private foundations. (The database is updated weekly and grows by about 34,000 documents every year.)

For example, I follow the efforts of indigenous peoples around the world to keep their languages alive. I found a report in ERIC by Marion Blue Arm, published in a conference proceeding, on attitudes by Indians, Whites, and mixed families toward the teaching of Lakota in the schools on the Cheyenne River Sioux Reservation in South Dakota. ERIC is filled with useful material like that.

NTIS

NTIS, the National Technical Information Service, indexes and abstracts federally funded research reports in all areas of science. Many technical reports eventually get published as articles, which means you can find them through all the other databases. But many research reports just get filed and shelved—and lost. A major reason that technical reports don’t get published is that they contain data—huge tables of the stuff—which journals don’t have room for.

The NTIS has technical reports from archeological digs, from focus groups on attitudes about unprotected sex, from development projects on giant clam mariculture in the Solomon Islands, from natural experiments to test how long people can stay in a submerged submarine without going crazy—if the federal government has funded it under contract, there’s probably a technical report of it. The NTIS is available free at http://www.gov.

MEDLINE

MEDLINE is a product of the National Library of Medicine and the National Institutes of Health. It covers over 5,200 journals in the life sciences—including the medical social sciences—going back to 1949. MEDLINE is free through PUBMED at http://www.ncbi .nlm.nih.gov/pubmed. If you are working on anything that has to do with health care, MEDLINE, with its 16 million citations (and growing at around 700,000 citations a year) is a must.

OTHER DATABASES

There are dozens of subscription databases that are useful for work in anthropology. Here are just a few, to give you an idea of what’s out there.

PsycINFO, from the American Psychological Association, is a Jurassic database, covering some 2,500 journals in the behavioral and social sciences back to the 1800s. Cambridge Scientific Abstracts (CSA) is portal to databases in science, social science, and the humanities. CSA’s Sociological Abstracts covers about 1,800 journals, with nearly a million records going back to 1952. PsycINFO and Sociological Abstracts have excellent coverage of research methods, the sociology of language, occupations and professions, health, family violence, poverty, and social control. They cover the sociology of knowledge and the sociology of science, as well as the sociology of the arts, religion, and education. CSA’s Linguistics and Language Behavior Abstracts covers 1,500 journals, back to 1973.

Lexis/Nexis (http://www.lexisnexis.com) provides access to about five billion documents including hundreds of newspapers and the documents from the Congressional Information Service (CIS). The CIS indexes U.S. House and Senate hearings, reports entered into public access by submission to Congress, and testimony before congressional committees. You can get access to public documents published by the U.S. Congress at http://thomas.loc.gov (the ‘‘thomas’’ refers to Thomas Jefferson), but if you have access to Lexis-Nexis, it’s easier to use that service to find things in the CIS. There are congressional reports on many topics of interest to anthropologists, including reports on current social issues (housing, nutrition, cultural conservation, rural transportation). The proceedings for recognizing American Indian tribes are published in the Congressional Record and are available through CIS, as are reports on the demographics of American ethnic groups.

WorldCat is a product of OCLC (http://www.oclc.org), the Online Computer Library Center. WorldCat contains the catalogs of 71,000 libraries in over a hundred countries. If you find a book or article in the Web ofScience or PsycINFO, etc., and your library doesn’t have it, then WorldCat will tell you which library does have it. Interlibrary loans depend on this database.

WEBSITES

In addition to library databases, many super information resources of interest to anthropologists are available through the Internet pages of international organizations. A good place to start is the University of Michigan Document Center’s page, ‘‘International Organizations and Related Information’’ at http://www.lib.umich.edu/govdocs/intl.html. This page will point you to the portals for thousands of intergovernmental and nongovernmental organizations, like the Union of International Associations’ guide to IGOs and NGOs at http://www.uia.org/website.htm. The Michigan site will also point you directly to international agency sites, like the Food and Agriculture Organization of the UN, with many full-text reports on its projects since 1986. Interested in ‘‘shrimp aquaculture’’? Go to FAO’s archiving site at http://www.fao.org/documents and type that phrase into the search engine to find reports on local farming practices. Go to the site of the United Nations High Commission on Refugees (UNHCR) at http://www.unhcr.ch for the latest statistics on the refugees around the world. Go to the site of the Pan American Health Organization (PAHO) at http://www.paho.org for the latest statistics on health indicators for countries in North and South America.

There is a world of high-quality documents available on the Internet. The Anthropology Review Database at http://wings.buffalo.edu/ARD provides an expanding list of reviews of books, articles, and software of interest to anthropologists. The Scout Report, at http://scout.cs.wisc.edu, is an expanding database of Internet sites. Search the site for ‘‘anthropology’’ and you’ll find lots of useful, full-text resources, like the one at http:// www.nativetech.org, devoted to Native American technology and art.

To find general information about particular countries of the world, start with the Yahoo server http://dir.yahoo.com/Regional/Countries and also consult the CIA Factbook at https://www.cia.gov/library/publications/the-world-factbook. Going to the Manu’a Islands to do fieldwork? Detailed maps for just about every country and region of the world (including the Manu’a Islands) are available online at http://www.lib.utexas.edu/ maps/index.html. For websites developed and maintained by particular countries, start with http://www.library.northwestern.edu/govinfo/resource/internat/foreign.html. All government statistical reports are subject to error. Use with caution (box 3.5).

The logic of Boolean operators is used in database management—about which, more at the end of chapter 13 on field notes.

META-ANALYSIS

Meta-analysis involves piling up all the quantitative studies ever done on a particular topic to assess quantitatively what is known about the size of the effect. The pioneering work on meta-analysis (M. L. Smith and Glass 1977) addressed the question: Does psychotherapy make a difference? That is, do people who get psychotherapy benefit, compared to people who have the same problems and who don’t get psychotherapy? Since then, there have been thousands of meta-analyses, but most of them are in fields like psychology and medicine, where data from experiments lend themselves to direct comparison.

A few anthropologists, though, have done important meta-analyses. Until the 1970s, conventional wisdom had it that hunters and gatherers lived a precarious existence, searching all the time for food, never knowing where their next meal was coming from.

BOX 3.5

T I P S F O R S E A R C H I N G O N L I N E D A T A B A S E S

1. Get the spelling right. Some databases have intelligent spell checkers (if you ask for information on ‘‘New Guinae,’’ they’ll ask if you really meant ‘‘New Guinea’’), but many don’t. If you ask for references on ‘‘apropriate technology’’ and the database comes back, incongruously, with ‘‘nothing found,’’ check the spelling with your word processor’s spell check or with an online dictionary.

2. If there are two or more ways to spell a word, then search with all spellings. Use both Koran and Qur’an (and several other spelling variants) in your searches; behavior and behaviour; Chanukah and Hanukah (and several other spelling variants); Rom and Roma (both are used to refer to Gypsies); Thessaloniki and Salonika; Mumbai and Bombay; Beijing and Peking; and so on.

3. Use wildcards liberally. Search for ‘‘behav* measur*’’ rather than ‘‘behavior measurement.’’ That way, you’ll capture ‘‘behaviour measurement,’’ ‘‘behavioral measurement,’’ ‘‘behavioral measures,’’ and so on. I asked MEDLINE for articles from 1990 until June 2009 on (child* diarrhea) OR (infant* diarrhea) and got 11,541 hits. I used the wildcard asterisk to indicate that I wanted any records with the words ‘‘children’s’’ or ‘‘childhood’’ and any records with the words ‘‘infant’s’’ or ‘‘infantile.’’ Then I remembered that the British spelling of ‘‘diarrhea’’ is ‘‘diarrhoea’’ so I changed the parameters to (child* diarrh*) OR (infant* diarrh*) and got another 4,061 hits.

4. Become really facile with the Boolean operators (AND, OR, NOT) to narrow your searches. Changing the MEDLINE search to [(child* diarrh*) OR (infant* diarrh*) AND (cultural factors)] reduced the number of hits from over 15,000 to 5. I asked MEDLINE for all articles from 1977 to 2009 on (regimen compliance AND malaria). That search brought back abstracts for 81 articles. When I restricted the search to [(regimen compliance AND malaria) NOT Africa], I got back 57 abstracts. The parentheses and brackets in Boolean searches work just like equations in algebra. So, that last search I did fetched all the items that had ‘‘regimen compliance’’ and ‘‘malaria’’ in their titles or abstract. Then, the items were sorted and any of those items that contained the word ‘‘Africa’’ was dropped.

In 1970, Esther Boserup made the important observation that plow agriculture takes more time than does hoe agriculture. And in 1972, Marshall Sahlins generalized this observation, arguing that hunter-gatherer societies had more leisure than anyone else and that people have to work more and more as societies become more complex.

In 1996, Ross Sackett did a meta-analysis of 102 cases of time allocation studies and 207 energy-expenditure studies to test Sahlins’s (1972) primitive-affluence hypothesis. Sackett found that, indeed, adults in foraging and horticultural societies work, on average, about 6.5 hours a day, while people in agricultural and industrial societies work about 8.8 hours a day. The difference, by the way, is statistically very significant (Sackett 1996:231, 547).

Meta-analysis can be delightfully subversive. Morrison and Morrison (1995), for example, found that only 6.3% of the variance in graduate-level GPA is predicted by performance on the GRE quantitative and verbal exams. And White (1980) found that across a hundred studies up to 1979, socioeconomic status explained, on average, an identical 6.3% of the variance in school achievement. The raw correlation across those hundred studies, ranged from .14 (yes, minus .14) to .97.

Meta-analyses are becoming more and more common as electronic databases, including databases of ethnography, develop. Meta-analysis gives us the tools to see if we are making progress on important question. It is, as Hunt (1997) says, the way science takes stock.

FURTHER READING

Anthropology in the military and in intelligence: For contrasting takes on the activities of anthropologists in Thailand during the Vietnam War, see Wolf and Jorgensen (1970) and Hinton (2002). For an exhaustive historical account of the issue, see Wakin (1992). For opposing views of anthropologists’ involvement in the wars in Iraq and Afgahanistan, see Price (2003) and McFate (2005); see also Gonza´lez (2007) and Kilcullen (2007). For a summary of this debate, see Fluehr-Lobban (2008).

Ethical issues in anthropology: Anspach and Mizrachi (2006); Borofsky (2005); Cantwell et al. (2000); Caplan (2003); Carrithers (2005); Cassell and Jacobs (1987); Cushman (2004); Edel and Edel (1968); Einarsdo´ ttir (2006); Feinberg (2007); Fluehr-Lobban (2002); D. Gordon (1991); E. Harrison (2006); F. V. Harrison (1997); Kemper (1997); MacClancy (2002); Montgomery (2007); Pels (2008); Posey (2004); Rynkiewick and Spradley (1976); Silverman (2004).

Research Design: Experiments and Experimental Thinking

Early in the 20th century, F. C. Bartlett, the pioneering psychologist who developed schema theory, went to Cambridge University to study with W.H.R. Rivers—an experimental psychologist who became one of the pioneers of modern anthropology. In 1899, Rivers had been invited to join the Torres Straits Expedition and saw the opportunity to do comparative psychology studies of non-Western people (Tooker 1997:xiv). When Bartlett got to Cambridge, he asked Rivers for some advice. Bartlett expected a quick lecture on how to go out and stay out, about the rigors of fieldwork, and so on. Instead, Rivers told him: ‘‘The best training you can possibly have is a thorough drilling in the experimental methods of the psychological laboratory’’ (Bartlett 1937:416).

Bartlett found himself spending hours in the lab, ‘‘lifting weights, judging the brightness of lights, learning nonsense syllables, and engaging in a number of similarly abstract occupations’’ that seemed to be ‘‘particularly distant from the lives of normal human beings.’’ In the end, though, Bartlett concluded that Rivers was right. Training in the experimental method, said Bartlett, gives one ‘‘a sense of evidence, a realization of the difficulties of human observation, and a kind of scientific conscience which no other field of study can impart so well’’ (Bartlett 1937:417).

I agree. Most anthropologists don’t do experiments, but a solid grounding in the logic of experiments is one of the keys to good research skills, no matter what kind of research you’re doing. At the end of this chapter, you should understand the variety of research designs. You should also understand the concept of threats to validity and how we can respond to those threats.

EXPERIMENTS

Experiments can be done in the laboratory or in the field, but the logic is the same, no matter where they are done. There are, of course, differences in experiments with people versus experiments with rocks or pigeons or plants. But these differences involve ethical issues—like deception, informed consent, and withholding of treatment—not logic. More on these ethical issues later.

The Logic of True Experiments

There are five steps in a classic experiment:

1. Formulate a hypothesis.

2. Randomly assign participants to the intervention group or to the control group.

3. Measure the dependent variable(s) in one or both groups. This is called $\mathrm { O } _ { 1 }$ or ‘‘observation at time 1.’’

4. Introduce the treatment or intervention.

5. Measure the dependent variable(s) again. This is called $\mathrm { O } _ { 2 }$ or ‘‘observation at time $2 . ^ { \circ }$

Later, I’ll walk you through some variations on this five-step formula, including one very important variation that does not involve Step 3 at all. But first, the basics.

Step 1. Before you can do an experiment, you need a clear hypothesis about the relation between some independent variable (or variables) and some dependent variable (or variables). Experiments thus tend to be based on confirmatory rather than exploratory research questions (see box 1.1).

The testing of new drugs can be a simple case of one independent and one dependent variable. The independent variable might be, say, ‘‘taking vs. not taking’’ a drug. The dependent variable might be ‘‘getting better vs. not getting better.’’ The independent and dependent variables can be much more subtle. ‘‘Taking vs. not taking’’ a drug might be ‘‘taking more of, or less $\mathrm { o f } ^ { \mathrm { > } }$ a drug, and ‘‘getting better vs. not getting better’’ might be ‘‘the level of improvement in high-density lipoprotein’’ (the so-called good cholesterol).

Move this logic to agriculture: ceteris paribus (holding everything else—like amount of sunlight, amount of water, amount of weeding—constant), some corn plants get a new fertilizer and some don’t. Then, the dependent variable might be the number of ears per corn stalk or the number of days it takes for the cobs to mature, or the number of kernels per cob.

Now move this same logic to human thought and human behavior: Ceteris paribus, people in Nairobi who take this course in AIDS awareness will report fewer high-risk sex practices than will people who don’t take this course. Ceteris paribus here means that people in both groups—the treatment group and the control group—start with the same amount of reported high-risk sexual activity.

Things get more complicated when there are multiple independent (or dependent) variables. You might want to test two different courses, with different content, on people who come from three different tribal backgrounds. But the underlying logic for setting up experiments and for analyzing the results is the same across the sciences. When it comes to experiments, everything starts with a clear hypothesis.

Step 2. You need at least two groups, called the treatment group (or the intervention group or the stimulus group) and the control group. One group gets the intervention (the new drug, the new teaching program) and the other group doesn’t. The treatment group (or groups) and the control group(s) are involved in different experimental conditions.

In true experiments, people are randomly assigned to either the intervention group or to the control group. This ensures that any differences between the groups are the consequence of chance and not of systematic bias. Some people in a population may be more religious, or more wealthy, or less sickly, or more prejudiced than others, but random assignment ensures that those traits are randomly distributed through all the groups in an experiment.

Random assignment doesn’t eliminate selection bias. It makes differences between experimental conditions (groups) due solely to chance by taking the decision of who goes in what group out of your hands. The principle behind random assignment will become clearer after you work through chapter 6 on probability sampling, but the bottom line is this: Whenever you can assign participants randomly in an experiment, do it.

Step 3. One or both groups are measured on one or more dependent variables. This is called the pretest.

Dependent variables in people can be physical things like weight, height, systolic blood pressure, or resistance to malaria. They can also be attitudes, moods, knowledge, or mental and physical achievements. For example, in weight-loss programs, you might measure the ratio of body fat to body mass as the dependent variable. If you are trying to raise women’s understanding of the benefits of breast-feeding by exposing them to a multimedia presentation on this topic, then a preliminary test of women’s attitudes about breastfeeding before they see the presentation is an appropriate pretest for your experiment.

You don’t always need a pretest. More on this in a bit, when we discuss threats to validity in experiments.

Step 4. The intervention (the independent variable) is introduced.

Step 5. The dependent variables are measured again. This is the posttest.

A Walkthrough

Here’s a made-up example of a true experiment: Take 100 college women (18–22 years of age) and randomly assign 50 of them to each of two groups. Bring each woman to the lab and show her a series of flash cards. Let each card contain a single, three-digit random number. Measure how many three-digit numbers each woman can remember. Repeat the task, but let the members of one group hear the most popular rock song of the week playing in the background as they take the test. Let the other group hear nothing. Measure how many three-digit numbers people can remember and whether rock music improves or worsens performance on the task.

Do you think this is a frivolous experiment? Many college students study while listening to rock music, which drives their parents crazy. I’ll bet that more than one reader of this book has been asked something like: ‘‘How can you learn anything with all that noise?’’ The experiment I’ve outlined here is designed to test whether students can, in fact, ‘‘learn anything with all that noise.’

Now, this experiment is very limited. Only women are involved. There are no graduate students or high school students. There’s no test of whether classic rock helps or hinders learning more than, say, hip-hop, or country music, or Beethoven. And the learning task is artificial. What we know at the end of this experiment is whether college-age women at one school learn to memorize more or fewer three-digit numbers when the learning is accompanied by a single rock tune.

But a lot of what’s really powerful about the experimental method is embodied in this example. Suppose that the rock-music group does better on the task. We can be pretty sure this outcome is not because of the participants’ sex, age, or education, but because of the music. Just sticking in more independent variables (like expanding the group to include men, graduate students, or high school students; or playing different tunes; or making the learning task more realistic), without modifying the experiment’s design to control for all those variables, creates what are called confounds. They confound the experiment and make it impossible to tell if the intervention is what really caused any observed differences in the dependent variable.

Good experiments test narrowly defined questions. This is what gives them knowledgemaking power. When you do a good experiment, you know something at the end of it. In this case, you know that women students at one school memorize or do not memorize three-digit numbers better when they listen to a particular rock tune.

This may not seem like much, but you really know it. You can repeat the experiment at the same school to verify or refute this little bit of knowledge. You can repeat the experiment at another school to see if the knowledge holds up.

Suppose you don’t get the same answer at another school, holding all the other elements of the experiment—age, sex, type of music—constant. The new finding demands an explanation. Perhaps there is something about the student selection process at the two schools that produces the different results? Perhaps students at one school come primarily from working-class families and students from the other school come from upper-middle-class families. Perhaps students from different socioeconomic classes grow up with different study habits or prefer different kinds of music.

Conduct the experiment again but include men this time. Conduct it again and include two music conditions: a rock tune and a classical piece. Take the experiment on the road and run it all over again at different-sized schools in different regions of the country. Then, on to Paraguay . . . (box 4.1).

BOX 4.1

E X P E R I M E N T S A N D V A L I D I T Y

True experiments, with randomized assignment and full control by the researcher, produce knowledge that has high internal validity. This means that changes in the dependent variables were probably caused by—not merely related to or correlated with—the treatment. Continual replication produces cumulative knowledge with high external validity—that is, knowledge that you can generalize to people who were not part of your experiment.

Replication of knowledge is every bit as important as its production in the first place. In fact, it terms of usefulness, replicated knowledge is exactly what we’re after.

KINDS OF CONFOUNDS: THREATS TO VALIDITY

It’s pointless to ask questions about external validity until you establish internal validity. In a series of influential publications, Donald Campbell and his colleagues identified the threats to internal validity of experiments (see Campbell 1957, 1979; Campbell and Stanley 1966; Cook and Campbell 1979). Here are seven of the most important confounds:

1. History

The history confound refers to any independent variable, other than the treatment, that (1) occurs between the pretest and the posttest in an experiment and (2) affects the experimental groups differently. Suppose you are doing a laboratory experiment with two groups (experimental and control) and there is a power failure in the building. So long as the lights go out for both groups, there is no problem. But if the lights go out for one group and not the other, it’s difficult to tell whether it was the treatment or the power failure that causes changes in the dependent variable.

In a laboratory experiment, history is controlled by isolating participants as much as possible from outside influences. When we do experiments outside the laboratory, it is almost impossible to keep new independent variables from creeping in and confounding things.

Here’s an example of an experiment outside the lab. Suppose you run an experiment to test whether monetary incentives help third graders do better in arithmetic. Kids in the treatment classes get a penny for each right answer on their tests; kids in the control classes get nothing. Now, right in the middle of the school term, while you’re running this experiment, the Governor’s Task Force on Education issues its long-awaited report, with a recommendation that arithmetic skills be emphasized during the early school years. Furthermore, it says, teachers whose classes make exceptional progress in this area should be rewarded with 10% salary bonuses.

The governor accepts the recommendation and announces a request for a special legislative appropriation. Elementary teachers all over the state start paying extra attention to arithmetic skills. Even supposing that the students in the treatment classes do better than those in the control classes in your experiment, we can’t tell if the magnitude of the difference would not have been greater had this historical confound not occurred. That’s just the breaks of experimenting in real life without being able to control everything.

2. Maturation

The maturation confound refers to the fact that people in any experiment grow older or get more experienced while you are trying to conduct an experiment. Consider the following experiment: Start with a group of teenagers on a Native American reservation and follow them for the next 60 years. Some of them will move to cities; some will go to small towns; and some will stay on the reservation. Periodically, test them on a variety of dependent variables (their political opinions, their wealth, their health, their family size, and so on). See how the experimental treatments (city vs. reservation vs. town living) affect these variables.

Here is where the maturation confound enters the picture. The people you are studying get older. Older people in many societies become more politically conservative. They are usually wealthier than younger people. Eventually, they come to be more illness prone than younger people. Some of the changes you measure in your dependent variables will be the result of the various treatments—and some of them may just be the result of maturation.

Maturation is not just about people getting older. Social service delivery programs ‘‘mature’’ by working out bugs in their administration. People ‘‘mature’’ through practice with experimental conditions and they become fatigued. We see this all the time in new social programs where people start out being really enthusiastic about innovations in organizations and eventually get bored or disenchanted.

3. Testing and Instrumentation

The testing confound happens when people change their responses in reaction to being constantly examined. Asking people the same questions again and again in a longitudinal study, or even in an ethnographic study done over 6 months or more, can have this effect.

The instrumentation confound results from changing measurement instruments. Changing the wording of questions in a survey is essentially changing instruments. Which responses do you trust: the ones to the earlier wording or the ones to the later wording? If you do a set of observations in the field and later send in someone else to continue the observations you have changed instruments. Which observations do you trust as closer to the truth: yours or those of the substitute instrument (the new field researcher)?

In multi-researcher projects, this problem is usually dealt with by training all investigators to see and record things in more or less the same way. This is called increasing interrater reliability. (More on this in chapter 19 in the section on Cohen’s kappa.)

4. Regression to the Mean

Regression to the mean is a confound that can occur when you study groups that have extreme scores on a dependent variable. No matter what the intervention is, the extreme scores are likely to become more moderate just because there’s nowhere else for them to go.

If men who are taller than $6 ^ { \prime } 7 ^ { \prime \prime }$ marry women who are taller than $6 ^ { \prime } 3 " ,$ , then their children are likely to be (1) taller than average and (2) closer to average height than either of their parents are. There are two independent variables (the height of each of the parents) and one dependent variable (the height of the children). We expect the dependent variable to ‘‘regress toward the mean,’’ since it really can’t get more extreme than the height of the parents.

I put that phrase ‘‘regress toward the mean’’ in quotes because it’s easy to misinterpret this phenomenon—to think that the ‘‘regressing’’ toward the mean of an dependent variable is caused by the extreme scores on the independent variables. It isn’t, and here’s how you can tell that it isn’t: Very, very tall children are likely to have parents whose height is more like the mean. One thing we know for sure is that the height of children doesn’t cause the height of their parents. Regression to the mean is a statistical phenomenon—it happens in the aggregate and is not something that happens to individuals (box 4.2).

BOX 4.2

T H E P R O B L E M O F E X T R E M E V A L U E S

Many social intervention programs make the mistake of using people with extreme values on dependent variables as subjects. Run some irrigation canals through the most destitute villages in a region of a Third World country and watch the average income of villagers rise. But understand that income might have risen anyway, if you’d done nothing, because it couldn’t have gone down. Test a reading program on the kids in a school district who score in the bottom 10% of all kids on reading skills and watch their test scores rise. But understand that their scores might have risen anyway.

5. Selection of Participants

Selection bias in choosing participants is a major confound to validity. In true experiments, you assign participants at random, from a single population, to treatment groups and control groups. This distributes any differences among individuals in the population throughout the groups, making the groups equivalent.

This reduces the possibility that differences among the groups will cause differences in outcomes on the dependent variables. Random assignment in true experiments, in other words, maximizes the chance for valid outcomes—outcomes that are not clobbered by hidden factors.

In natural experiments, however, we have no control over assignment of individuals to groups.

Question: Do victims of violent crime have less stable marriages than people who have not been victims? Obviously, researchers cannot randomly assign participants to the treatment (violent crime). It could turn out that people who are victims of this treatment are more likely to have unstable marriages anyway.

Question: Do migrants to cities from villages in developing nations engage in more entrepreneurial activities than stay-at-homes? If we could assign rural people randomly to the treatment group (those engaging in urban migration), we’d have a better chance of finding out. But we can’t, so selection is a threat to the internal validity of the experiment. Suppose that the answer to question at the top of this paragraph was ‘‘yes.’’ We still don’t know the direction of the causal arrow: Does the treatment (migration) cause the outcome (greater entrepreneurial activity)? Or does having an entrepreneurial personality cause migration?

6. Mortality

The mortality confound refers to the fact that people may not complete their participation in an experiment. Suppose we follow two sets of Mexican villagers—some who receive irrigation and some who do not—for 5 years. During the 1st year of the experiment, we have 200 villagers in each group. By the 5th year, 170 remain in the treatment group, and only 120 remain in the control group. One conclusion is that lack of irrigation caused those in the control group to leave their village at a faster rate than those in the treatment group.

But what about those 30 people in the treatment group who left? It could be that they moved to another community where they acquired even more irrigated land, or they may have abandoned farming altogether to become labor migrants. These two outcomes would affect the results of the experiment quite differently. Mortality can be a serious problem in natural experiments if it gets to be a large fraction of the group(s) under study.

Mortality also affects panel surveys. That’s where you interview the same people more than once to track something about their lives. (More about panel studies in chapter 9.)

7. Diffusion of Treatments

The diffusion of treatments threat to validity occurs when a control group cannot be prevented from receiving the treatment in an experiment. This is particularly likely in quasi-experiments where the independent variable is an information program.

In a project with which I was associated, a group of African Americans were given instruction on modifying their diet and exercise behavior to lower their blood pressure. Another group was randomly assigned from the population to act as controls—that is, they would not receive instruction. The evaluation team measured blood pressure in the treatment group and in the control group before the program was implemented. But when they went back after the program was completed, they found that control group members had also been changing their behavior. They had learned of the new diet and exercises from the members of the treatment group.

CONTROLLING FOR THREATS TO VALIDITY

In what follows, I want to show you how the power of experimental logic is applied to real research problems. The major experimental designs are shown in figure 4.1. The notation is pretty standard. The letter X stands for some intervention—a stimulus or a treatment. R means that participants are randomly assigned to experimental conditions— either to the intervention group that gets the treatment, or to the control group that doesn’t. Several designs include random assignment and several don’t. O stands for ‘‘observation. ${ \bf \vec { \tau } } ^ { , } { \bf \vec { o } } _ { 1 }$ means that some observation is made at Time 1, $\mathbf { O } _ { 2 }$ means that some observation is made at Time 2, and so on.

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
Group 1	$R$	$O_1$	$X$	$O_2$
Group 2	$R$	$O_3$		$O_4$
a.	The Classic Design: Two-Group Pretest-Posttest
Group 1	$R$	$O_1$	$X$	$O_2$
Group 2	$R$	$O_3$		$O_4$
Group 3	$R$		$X$	$O_5$
Group 4	$R$			$O_6$
b.	The Solomon Four-Group Design
Group 1		$O_1$	$X$	$O_2$
Group 2		$O_3$		$O_4$
c.	The Classic Design Without Randomization
Group 1	$R$		$X$	$O_1$
Group 2	$R$			$O_2$
d.	The Campbell and Stanley Posttest-Only Design
			$X$	$O$
e.	The One-Shot Case Study Design
		$O_1$	$X$	$O_2$
f.	The One-Group Pretest-Posttest Design
			$X$	$O_1$
				$O_2$
g.	Two-Group Posttest Only: Static Group Comparison Design
		$O\ O\ O$	$X$	$O\ O\ O$
h.	The Interrupted Time Series Design

Some research designs.

‘‘Observation’’ means ‘‘measurement of some dependent variable,’’ but as you already know, the idea of measurement is pretty broad. It can be taking someone’s temperature or testing their reading skill. It can also be just writing down whether they were successful at hunting game that day.

The Classic Two-Group Pretest-Posttest Design with Random Assignment

Figure 4.1a shows the classic experimental design: the two-group pretest-posttest with random assignment. From a population of potential participants, some participants have been assigned randomly to a treatment group and a control group. Read across the top row of the figure. An observation (measurement) of some dependent variable or variables is made at time 1 on the members of group 1. That is $\mathrm { O } _ { 1 }$ . Then an intervention is made (the group is exposed to some treatment, X). Then, another observation is made at time 2. That is $\mathrm { O } _ { 2 } .$

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
Group 1	$R$	$O_{1}$	$X$	$O_{2}$
Group 2	$R$	$O_{3}$		$O_{4}$

FIGURE 4.1a. The classic design: Two-group pretest-posttest.

Now look at the second row of figure 4.1a. A second group of people are observed, also at time 1. Measurements are made of the same dependent variable(s) that were made for the first group. The observation is labeled $\mathrm { O } _ { 3 } .$ There is no X on this row, which means that no intervention is made on this group of people. They remain unexposed to the treatment or intervention in the experiment. Later, at time 2, after the first group has been exposed to the intervention, the second group is observed again. That’s $\mathrm { O } _ { 4 } .$

Random assignment of participants ensures equivalent groups, and the second group, without the intervention, ensures that several threats to internal validity are taken care of. Most importantly, you can tell how often (how many times out of a hundred, for example) any differences between the pretest and posttest scores for the first group might have occurred anyway, even if the intervention hadn’t taken place.

Patricia Chapman (Chapman et al. 1997) wanted to educate young female athletes about sports nutrition. She and her colleagues worked with an eight-team girl’s high school softball league in California. There were nine 14–18 years olds on each team, and Chapman et al. assigned each of the 72 players randomly to one of two groups. In the treatment group, the girls got two, 45-minute lectures a week for 6 weeks about dehydration, weight loss, vitamin and mineral supplements, energy sources, and so on. The control group got no instruction.

Before the program started, Chapman et al. asked each participant to complete the Nutrition Knowledge and Attitude Questionnaire (Werblow et al. 1978) and to list the foods they’d eaten in the previous 24 hours. The nutrition knowledge-attitude test and the 24-hour dietary recall test were the pretests in this experiment. Six weeks later, when the program was over, Chapman et al. gave the participants the same two tests. These were the posttests. By comparing the data from the pretests and the posttests, Chapman et al. hoped to test whether the nutrition education program had made a difference.

The education intervention did make a difference—in knowledge, but not in reported behavior. Both groups scored about the same in the pretest on knowledge and attitudes about nutrition, but the girls who went through the lecture series scored about 18 points more (out of 200 possible points) in the posttest than did those in the control group.

However, the program had no effect on what the girls reported eating. After 6 weeks of lectures, the girls in the treatment group reported consuming 1,892 calories in the previous 24 hours, while the girls in the control group reported 1,793 calories. A statistical dead heat. This is not nearly enough for young female athletes, and the results confirmed for Chapman what other studies had already shown—that for many adolescent females, the attraction of competitive sports is the possibility of losing weight.

This classic experimental design is used widely to evaluate educational programs. Kunovich and Rashid (1992) used this design to test their program for training freshman dental students in how to handle a mirror in a patient’s mouth (think about it; it’s not easy—everything you see is backward) (Further Reading: the classic experimental design and evaluation research).

The Solomon Four-Group Design

The classic design has one important flaw—it’s subject to testing bias. Differences between variable measurements at time 1 and time 2 might be the result of the intervention, but they also might be the result of people getting savvy about being watched and measured. Pretesting can, after all, sensitize people to the purpose of an experiment, and this, in turn, can change people’s behavior. The Solomon four-group design, shown in figure 4.1b, controls for this. Since there are no measurements at time 1 for groups 3 and 4, this problem is controlled for.

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
Group 1	$R$	$O_{1}$	$X$	$O_{2}$
Group 2	$R$	$O_{3}$		$O_{4}$
Group 3	$R$		$X$	$O_{5}$
Group 4	$R$			$O_{6}$

FIGURE 4.1b. The Solomon four-group design.

Larry Leith (1988) used the Solomon four-group design to study a phenomenon known to all sports fans as the ‘‘choke.’’ That’s when an athlete plays well during practice and then loses it during the real game, or plays well all game long and folds in the clutch when it really counts. It’s not pretty.

Leith assigned 20 male students randomly to each of the four conditions in the Solomon 4-group design. The pretest and the posttest were the same: Each participant shot 25 free throws on a basketball court. The dependent variable was the number of successful free throws out of 25 shots in the posttest. The independent variable—the treatment—was giving or not giving the following little pep talk to each participant just before he made those 25 free throws for the posttest:

Research has shown that some people have a tendency to choke at the free-throw line when shooting free throws. No one knows why some people tend to choking behavior. However, don’t let that bother you. Go ahead and shoot your free throws. (Leith 1988:61)

What a wonderfully simple, utterly diabolic experiment. You can guess the result: There was a significantly greater probability of choking if you were among the groups that got that little pep talk, irrespective of whether they’d been given the warm-up pretest (Further Reading: the Solomon four-group design).

The Two-Group Pretest-Posttest without Random Assignment

Figure 4.1c shows the design for a quasi-experiment—an experiment in which participants are not assigned randomly to the control and the experimental condition. This compromise with design purity is often the best we can do.

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
Group 1		$O_{1}$	X	$O_{2}$
Group 2		$O_{3}$		$O_{4}$

FIGURE 4.1c. The classical design without randomization: The quasi-experiment.

Program evaluation research is usually quasi-experimental. Consider a program in rural Kenya in which women farmers are offered instruction on applying for bank credit to buy fertilizer. The idea is to increase corn production.

You select two villages in the district—one that gets the program, and one that doesn’t. Before the program starts, you measure the amount of credit, on average, that women in each village have applied for in the past 12 months. A year later, you measure again and find that, on average, women in the program village have applied for more agricultural credit than have their counterparts in the control village.

Campbell and Boruch (1975) show how this research design leads to problems. Suppose that the women in the program village have, on average, more land than the women in the control village have. Would you (or the agency you’re working for) be willing to bet, say, $300,000 on implementing the program across the district, in, say, 30 villages? Would you bet that it was the intervention and not some confound, like the difference in land holdings, that caused the difference in outcome between the two villages?

The way around this is to assign each woman randomly to one of the two conditions in the experiment. Then the confound would disappear—not because land holding stops being a factor in how well women respond to the opportunity to get agricultural credits, but because women who have varying amounts of land would be equally likely to be in the treatment group or in the control group. Any bias that the amount of land causes in interpreting the results of the experiment would be distributed randomly and would be equally distributed across the groups.

But people come packaged in villages, and you can’t give just some women in a small village instruction about applying for credit and not give it to others. So evaluation of these kinds of interventions are usually quasi-experiments because they have to be (Further Reading: quasi-experiments).

The Posttest-Only Design with Random Assignment

Look carefully at figure 4.1d. It is the second half of the Solomon four-group design and is called the Campbell and Stanley posttest-only design. This design has a lot going for it. It retains the random assignment of participants in the classical design and in the Solomon four-group design, but it eliminates pretesting—and the possibility of a confound from pretest sensitization. When participants are assigned randomly to experimental conditions (control or treatment group), a significant difference on O and O in the posttestonly design means that we can have a lot of confidence that the intervention, X, caused that difference (Cook and Campbell 1979).

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
Group 1	$R$		$X$	$O_{1}$
Group 2	$R$			$O_{2}$

FIGURE 4.1d. The Campbell and Stanley posttest-only design.

Another advantage is the huge saving in time and money. There are no pretests in this design and there are only two posttests instead of the four in the Solomon four-group design.

Here’s an example of this elegant design. McDonald and Bridge (1991) asked 160 female nurses to read an information packet about a surgery patient whom they would be attending within the next 8 hours. The nurses were assigned randomly to one of eight experimental conditions: (1) The patient was named Mary B. or Robert B. This produced two patient-gender conditions. (2) Half the nurses read only a synopsis of the condition of Mary B. or Robert B., and half read the same synopsis as the fourth one in a series of seven. This produced two memory-load conditions. (3) Finally, half the nurses read that the temperature of Mary B. or Robert B. had just spiked unexpectedly to 102, and half did not. This produced two patient stability conditions. The three binary conditions combined to form eight experimental conditions in a factorial design (more on factorial designs at the end of this chapter).

Next, McDonald and Bridge asked nurses to estimate, to the nearest minute, how much time they would plan for each of several important nursing actions. Irrespective of the memory load, nurses planned significantly more time for giving the patient analgesics, for helping the patient to walk around, and for giving the patient emotional support when the patient was a man (box 4.3).

The One-Shot Case Study

The one-shot case study design is shown in figure 4.1e. It is also called the ex post facto design because a single group of people is measured on some dependent variable after an intervention has taken place. This is the most common research design in culture change studies, where it is obviously impossible to manipulate the dependent variable. You arrive in a community and notice that something important has taken place. A clinic or a school has been built. You try to evaluate the experiment by interviewing people (O) and assessing the impact of the intervention (X).

With neither a pretest nor a control group, you can’t be sure that what you observe is the result of some particular intervention. Despite this apparent weakness, however, the intuitive appeal of findings produced by one-shot case studies can be formidable.

In the 1950s, physicians began general use of the Pap Test, a simple office procedure for determining the presence of cervical cancer. Figure 4.2 shows that since 1950, the death rate from cervical cancer in the United States has dropped steadily, from about 18

FIGURE 4.1e.

BOX 4.3

P O S T T E S T O N L Y : T H E U N D E R A P P R E C I A T E D D E S I G N

The posttest-only design, with random assignment, is not used as much as I think it should be, despite its elegance and its low cost. In June 2009, a search of PsycINFO turned up 1,110 examples of studies that used the pretest-posttest design, compared to 133 for studies that used the posttest-only design (with or without random assignment). This preference for the classic design is due partly to the appealing-but-mistaken idea that matching participants in experiments on key independent variables (age, ethnicity, etc.) is somehow better than randomly assigning participant to groups, and partly to the nagging suspicion that pretests are essential to the experimental method. That nagging suspicion (that we can do better than trust the outcome of events to randomness) has been the focus of a lot of research since a paper by Gilovich et al. in 1985 titled: ‘‘The hot hand in basketball—on the misperception of random sequences.’’ The hot-hand phenomenon—the belief that streaks (in sports and in money management, for example) are the result of nonrandom forces—is hard to break. By the same token, so is the belief that small samples, if drawn randomly, are sufficient to warrant generalizing to a population. On this one, see the 600 citations to Tversky and Kahneman (1971) and chapters 6 and 7 on representative and nonrepresentative sampling (Further Reading: the posttest-only design).

	Time 1	Time 2
	Assignment Pretest	Intervention	Posttest
		X	O

The one-shot case study design.

per 100,000 women to about 11 in 1970, to about 8.3 in 1980, to about 6.5 in 1995 and to about 2.4 in 2005. If you look only at the data after the intervention (the one-shot case study X O design), you could easily conclude that the intervention (the Pap Test) was the sole cause of this drop in cervical cancer deaths. There is no doubt that the continued decline of cervical cancer deaths is due largely to the early detection provided by the Pap Test, but by 1950, the death rate had already declined by 36% from 28 per 100,000 in 1930 (B. Williams 1978:16).

Never use a design of less logical power when one of greater power is feasible. If pretest data are available, use them. On the other hand, a one-shot case study is often the best you can do. Virtually all ethnography falls in this category, and, as I have said before, nothing beats a good story, well told (Further Reading: case study methods).

The One-Group Pretest-Posttest

The one-group pretest-posttest design is shown in figure 4.1f. Some variables are measured (observed), then the intervention takes place, and then the variables are measured again. This takes care of some of the problems associated with the one-shot case study, but it doesn’t eliminate the threats of history, testing, maturation, selection, and mortality. Most importantly, if there is a significant difference in the pretest and posttest measurements, we can’t tell if the intervention made that difference happen.

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
	$O_1$		X	$O_2$

FIGURE 4.1f. The one-group pretest-posttest design.

The one-group pretest-posttest design is commonly used in evaluating training programs. The question asked is: Did the people who were exposed to this skill-building program (midwives, coal miners, kindergarten teachers, etc., etc.) get any effect from the program?

M. Peterson and Johnstone (1995) studied the effects on 43 women inmates of a U.S. federal prison of an education program about drug abuse. The participants all had a history of drug abuse, so there is no random assignment here. Peterson and Johnstone measured the participants’ health status and perceived well-being before the program began and after the program had been running for 9 months. They found that physical fitness measures were improved for the participants as were self-esteem, health awareness, and health-promoting attitudes (Further Reading: one-group pretest-posttest design).

The Two-Group Posttest-Only Design without Random Assignment

The two-group posttest-only design without random assignment design is shown in figure 4.1g. This design, also known as the static group comparison, improves on the

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
			X	$O_{1}$
				$O_{2}$

FIGURE 4.1g. Two-group posttest only design without random assignment: Static group comparison design.

one-shot ex postfacto design by adding an untreated control group—an independent case that is evaluated only at time 2. The relation between smoking cigarettes (the intervention) and getting lung cancer (the dependent variable) is easily seen by applying the humble ex post facto design with a control group for a second posttest.

In 1965, when the American Cancer Society did its first big Cancer Prevention Study, men who smoked (that is, those who were subject to the intervention) were about 12 times more likely than nonsmokers (the control group) to die of lung cancer. At that time, relatively few women smoked, and those who did had not been smoking very long. Their risk was just 2.7 times that for women nonsmokers of dying from lung cancer.

By 1988, things had changed dramatically. Male smokers were then about 23 times more likely than nonsmokers to die of lung cancer, and female smokers were 12.8 times more likely than female nonsmokers to die of lung cancer. Men’s risk had doubled (from about 12 to about 23), but women’s risk had more than quadrupled (from 2.7 to about 13) (National Cancer Institute 1997). The death rate for lung cancer has continued to fall among men in the United States, while the death rate for women has increased (http:// apps.nccd.cdc.gov/uscs).

In true experiments run with the posttest-only design, participants are assigned at random to either the intervention or the control group. In the static group comparison design, the researcher has no control over assignment of participants. This leaves the static-group comparison design open to an unresolvable validity threat. There is no way to tell whether the two groups were comparable at time 1, before the intervention, even with a comparison of observations 1 and 3. Therefore, you can only guess whether the intervention caused any differences in the groups at time 2.

Despite this, the static-group comparison design is useful for evaluating natural experiments, where you have no control over the assignment of participants anyway (Further Reading: static group comparison design) (box 4.4).

BOX 4.4

M I G R A T I O N A N D G E N D E R R O L E S : A S T A T I C - G R O U P C O M P A R I S O N D E S I G N

Lambros Comitas and I wanted to find out if the experience abroad of Greek labor migrants had any influence on men’s and women’s attitudes toward gender roles when they returned to Greece. The best design would have been to survey a group before they went abroad, then again while they were away, and again when they returned to Greece. Since this was not possible, we studied one group of persons who had been abroad and another group of persons who had never left Greece. We treated these two groups as if they were part of a static-group comparison design (Bernard and Comitas 1978).

From a series of life histories with migrants and nonmigrants, we learned that the custom of giving dowry was under severe stress (Bernard and Ashton-Vouyoucalos 1976). Our survey confirmed this: Those who had worked abroad were far less enthusiastic about providing expensive dowries for their daughters than were those who had never left Greece. We concluded that this was in some measure due to the experiences of migrants in what was then West Germany.

There were threats to the validity of this conclusion: Perhaps migrants were a self-selected bunch of people who held the dowry and other traditional Greek customs in low esteem to begin with. But we had those life histories to back up our conclusion. Surveys are weak compared to true experiments, but their power is improved if they are conceptualized in terms of testing natural experiments and if their results are backed up with data from open-ended interviews.

Interrupted Time Series Design

The interrupted time series design, shown in figure 4.1h, can be very persuasive. It involves making a series of observation before and after an intervention. Figure 4.3 shows the rate of alcohol deaths, per 100,000 population, in Russia, from 1956 to 2002 (Pridemore et al. 2007:281). The year 1992 marks the formal shift in Russia to a market economy from a centrally planned economy. As it turns out, homicide and suicide rates show very similar patterns—something that Pridemore et al. interpret as outcomes that are predictable from Durkheim’s (1933 [1893], 1951 [1897]) theory of anomie (Further Reading: interrupted time series).

	Time 1		Time 2
	Assignment	Pretest	Intervention	Posttest
	000		X	000

FIGURE 4.1h. The interrupted time series design.

THOUGHT EXPERIMENTS

As you can see, it is next to impossible to eliminate threats to validity in natural experiments. However, there is a way to understand those threats and to keep them as low as possible: Think about research questions as if it were possible to test them in true experiments. These are called thought experiments.

This wonderful device is part of the everyday culture in the physical sciences. In 1972, I did an ethnographic study of scientists at Scripps Institution of Oceanography. Here’s a snippet from a conversation I heard among some physicists there. ‘‘If we could only get rid of clouds, we could capture more of the sun’s energy to run stuff on Earth,’’ one person said. ‘‘Well,’’ said another, ‘‘there are no clouds above the Earth’s atmosphere. The sun’s energy would be lots easier to capture out there.’

‘‘Yeah,’’ said the first, ‘‘so suppose we send up a satellite, with solar panels to convert sunlight to electricity, and we attach a really long extension cord so the satellite was tethered to the Earth. Would that work?’’ The discussion got weirder from there (if you can imagine), but it led to a lot of really useful ideas for research.

Suppose you wanted to know if small farms can produce organically grown food on a

FIGURE 4.2. Death rate from cervical cancer, 1930–2005. SOURCE: Adapted from B. Williams, A Sampler on Sampling. Figure 2.1, p. 17. - 1978, Lucent Technologies. Used by permission of John Wiley & Sons.

FIGURE 4.3. Alcohol deaths in Russia, 1956–2002.

SOURCE: W. A. Pridemore, M. B. Chamlin, and J. K. Cochran, ‘‘An Interrupted Time-Series Analysis of Durkheim’s Social Deregulation Thesis: The Case of the Russian Federation.’’ Justice Quarterly Vol. 24, pp. 272–90, 2007. Reprinted by permission.

scale sufficiently large to be profitable. What would a true experiment to test this question look like? You might select some smallish farms with similar acreage and assign half of them randomly to grow vegetables organically. You’d assign the other half of the farms to grow the same vegetables using all usual technology (pesticides, fungicides, chemical fertilizers, and so on). Then, after a while, you’d measure some things about the farms productivity and profitability and see which of them did better.

How could you be sure that organic or nonorganic methods of farming made the difference in profitability? Perhaps you’d need to control for access to the kinds of market populations that are friendly toward organically produced food (like university towns) or for differences in the characteristics of soils and weather patterns. Obviously, you can’t do a true experiment on this topic, randomly assigning farmers to use organic or hightech methods, but you can evaluate the experiments that real farmers are conducting every day in their choice of farming practices.

So, after you’ve itemized the possible threats to validity in your thought experiment, go out and look for natural experiments—societies, voluntary associations, organizations—that conform most closely to your ideal experiment. Then evaluate those natural experiments.

That’s what Karen Davis and Susan Weller (1999) did in their study of the efficacy of condoms in preventing the transmission of HIV among heterosexuals. Here’s the experiment you’d have to conduct. First, get a thousand heterosexual couples. Make each couple randomly serodiscordant. That is, for each couple, randomly assign the man or the woman to be HIV-positive. Assign each couple randomly to one of three conditions: (1) They use condoms for each sexual act; (2) They sometimes use condoms; or (3) They don’t use condoms at all. Let the experiment run a few years. Then see how many of the couples in which condoms are always used remain serodiscordant and how many become seroconcordant—that is, they are both HIV-positive. Compare across conditions and see how much difference it makes to always use a condom.

Clearly, no one could conduct this experiment. But Davis and Weller scoured the literature on condom efficacy and found 25 studies that met three criteria: (1) The focus was on serodiscordant heterosexual couples who said they regularly had penetrative sexual intercourse; (2) The HIV status of the participants in each study had been determined by a blood test; and (3) There was information on the use of condoms. The 25 studies involved thousands of participants, and from this meta-analysis Davis and Weller established that consistent use of condoms reduced the rate of HIV transmission by over 85%.

TRUE EXPERIMENTS IN THE LAB

Laboratory experiments to test theories about how things work in the real world is the preeminent method in social psychology. Cognitive dissonance theory, for example, predicts that people who come out of a tough initiation experience (marine recruits at boot camp, prisoners of war, girls and boys who go through genital mutilation, etc.) wind up as supporters of their tormentors. In a classic experiment, Elliot Aronson and Judson Mills (1959) recruited 63 college women for a discussion group that ostensibly was being formed to talk about psychological aspects of sex. To make sure that only mature people— people who could discuss sex openly—would make it into this group, some of the women would have to go through a screening test. Well, that’s what they were told.

A third of the women were assigned randomly to a group that had to read a list of obscene words and some sexually explicit passages from some novels—aloud, in front of a man who was running the experiment. (It may be hard to imagine now, but those women who went through this in the 1950s must have been very uncomfortable.) Another third were assigned randomly to a group that had to recite some nonobscene words that had to do with sex and a third group went through no screening at all.

Then, each participant was given headphones to listen in on a discussion that was supposedly going on among the members of the group she was joining. The ‘‘discussion’’ was actually a tape and it was, as Aronson and Mills said, ‘‘one of the most worthless and uninteresting discussions imaginable’’ (Aronson and Mills 1959:179). The women rated the discussion, on a scale of 0–15, on things like dull-interesting, intelligent-unintelligent, and so on.

Those in the tough initiation condition rated the discussion higher than did the women the women in either the control group or the mild initiation group. Since all the women were assigned randomly to participate in one of the groups, the outcome was unlikely to have occurred by chance. Well, the women in the tough initiation condition had gone through a lot to join the discussion. When they discovered how boringly nonprurient it was, what did they do? They convinced themselves that the group was worth joining.

Aaronson and Mills’s findings were corroborated by Gerard and Mathewson (1966) in an independent experiment. Those findings from the laboratory can now be the basis for a field test, across cultures, of the original hypothesis.

Conversely, events in the real world can stimulate laboratory experiments. In 1963, in Queens, New York, Kitty Genovese was stabbed to death in the street one night. According to a local news report, there were supposedly 38 eyewitnesses who saw the whole grisly episode from their apartment windows but did not call called the police. The news stories called the episode an example of ‘‘apathy,’’ but Bibb Latane´ and John Darley had a different explanation. They called it diffusion of responsibility and they did an experiment to test their idea (1968).

Latane´ and Darley invited ordinary people to participate in a ‘‘psychology experiment.’’ While the participants were waiting in an anteroom to be called for the experiment, the room filled with smoke. If there was a single participant in the room, 75% reported the smoke right away. If there were three or more participants waiting together, they reported the smoke only 38% of the time. People in groups just couldn’t figure out whose responsibility it was to do something. So they did nothing.

As it turns out, there probably weren’t 38 witnesses; none of the witnesses could have seen the whole episode; and some of the witnesses did call the police (Manning et al. 2007). Nevertheless, hundreds of studies on what’s known as the bystander effect have been published since Latane´ and Darley did their pioneering work. A real event gave two scientists an idea that they tested in an experiment, and that experiment opened a whole area of research.

TRUE EXPERIMENTS IN THE FIELD

When experiments are done outside the lab, they are called field experiments. Several researchers have been studying the effect of being touched on consumers’ spending. In one experiment (Hornik 1992), as lone shoppers (no couples) entered a large bookstore, an ‘‘employee’’ came up and handed them a catalog. Alternating between customers, the employee-experimenter touched about half the shoppers lightly on the upper arm. The results? Across 286 shoppers, those who were touched spent an average of $15.03; those who were not touched spent just $12.23. (That’s $25 vs. $20 in 2010 dollars.) The difference was across the board, no matter what the sex of the toucher or the shopper.

In another of his experiments, Hornik enlisted the help of eight servers—four waiters and four waitresses—at a large restaurant. At the end of the meal, the servers asked each of 248 couples (men and women) how the meal was. Right then, for half the couples, the servers touched the arm of either the male or the female in the couple for one second. The servers didn’t know it, but they had been selected out of 27 waiters and waitresses in the restaurant to represent two ends of a physical attractiveness scale. The results? Men and women alike left bigger tips when they were touched, but the effect was stronger for women patrons than it was for men. Overall, couples left about a 19% tip when the woman was touched, but only 16.5% when the man was touched.

Field experiments like these can produce powerful evidence for applications projects, but to be really useful, you need to back up results with ethnography so that you understand the process. How did all this tipping behavior play out? Did women who were touched suggest a bigger tip when the time came to pay the bill, or did the men suggest the tip? Or did it all happen without any discussion? Rich ethnographic data are needed here.

Field experiments are rare in anthropology, but not unprecedented. Marvin Harris and his colleagues (Byrne et al. 1995; Harris et al. 1993) ran an experiment in Brazil to test the effect of substituting one word in the question that deals with race on the Brazilian census. The demographers who designed the census had decided that the term parda was a more reliable gloss than the term morena for what English speakers call ‘‘brown,’’ despite overwhelming evidence that Brazilians prefer the term morena.

In the town of Rio de Contas, Harris et al. assigned 505 houses randomly to one of two groups and interviewed one adult in each house. All respondents were asked to say what cor (color) they thought they were. This was the ‘‘free-choice option.’’ Then they were asked to choose one of four terms that best described their cor. One group (with 252 respondents) was asked to select among branca (white), parda (brown), preta (black), and amerela (yellow). This was the ‘‘parda option’’—the one used on the Brazilian census. The other group (with 253 respondents) was asked to select among branca, morena (brown), preta, and amerela. This was the ‘‘morena option,’’ and is the intervention, or treatment in Harris’s experiment.

Among the 252 people given the parda option, 131 (52%) identified themselves as morena in the free-choice option (when simply asked to say what color they were). But when given the parda option, only 80 of those people said they were parda and 41 said they were branca (the rest chose the other two categories). Presumably, those 41 people would have labeled themselves morena if they’d had the chance; not wanting to be labeled parda, they said they were branca. The parda option, then, produces more Whites (brancas) in the Brazilian census and fewer Browns (pardas).

Of the 253 people who responded to the morena option, 160 (63%) said they were morena. Of those 160, only 122 had chosen to call themselves morena in the free-choice option. So, giving people the morena option actually increases the number of Browns (morenas) and decreases the number of Whites (brancas) in the Brazilian census.

Does this difference make a difference? Demographers who study the Brazilian census have found that those who are labeled Whites live about 7 years longer than do those labeled non-Whites in that country. If 31% of self-described morenas say they are Whites when there is no morena label on a survey and are forced to label themselves parda, what does this do to all the social and economic statistics about racial groups in Brazil? (Harris et al. 1993) (Further Research: field experiments) (box 4.5).

NATURAL EXPERIMENTS

True experiments and quasi-experiments are conducted and the results are evaluated later. Natural experiments, by contrast, are going on around us all the time. They are not conducted by researchers at all—they are simply evaluated.

Here are four examples of common natural experiments: (1) Some people choose to migrate from villages to cities; others stay put. (2) Some villages in a region are provided with electricity, some are not. (3) Some middle-class Chicano students go to college, some do not. (4) Some cultures practice female infanticide, some do not.

Each of these situations is a natural experiment that tests something about human behavior and thought. The trick is to ask: ‘‘What hypothesis is being tested by what’s going on here?’’

To evaluate natural experiments—that is, to figure out what hypothesis is being tested—you need to be alert to the possibilities and collect the right data. There’s a really important natural experiment going in an area of Mexico where I’ve worked over the years. A major irrigation system has been installed over the last 50 years in parts of the Mezquital, a high desert valley. Some of the villages affected by the irrigation system are populated entirely by N^˜ a¨hn˜u (Otomı´) Indians; other villages are entirely mestizo (as the majority population of Mexico is called).

Some of the Indian villages in the area are too high up the valley slope for the irrigation system to reach. I could not have decided to run this multimillion-dollar system through certain villages and bypass others, but the instant the decision was made by others, a natural experiment on the effects of a particular intervention was set in motion. There is a treatment (irrigation), there are treatment groups (villages full of people who get the irrigation), and there are control groups (villages full of people who are left out).

BOX 4.5

E C O N O M I C G A M E S

In classical economic theory, it is assumed that Homo economicus is programmed to maximize gain in any bargaining situation. In 1982, however, economists in Germany found evidence that challenged this assumption (Gu¨ th et al. 1982). In what the researchers called the ultimatum game, there are two players who never see each other or find out the other’s identity. Player 1 gets a sum of money, x, and offers some fraction of it, xp, to player 2 through an intermediary. If player 2 accepts, the money is split according to the terms of player 1. If player 2 rejects the offer, then neither player gets anything. Economic theory predicts that player 1 should offer next to nothing and that player 2 should accept anything player 1 offers. As Thaler put it, ‘‘the data are inconsistent with both of these predictions’’ (1988:197). For player 2, it costs nothing to reject very small offers—and to punish player 1—but as the fraction of the offer goes up, player 2 has to weigh the joy of teaching the other player a lesson with the loss of real money. If you’re player 1, the trick is to figure out how much to offer so that you don’t wind up with nothing but you still get what you can.

By the late 1990s, there were hundreds of studies using economics games in developed countries. Then, Joseph Henrich and colleagues (2005) ran the ultimatum game in 15 small-scale societies around the world—from foragers to farmers—as well as with American university students. ‘‘The selfishness axiom,’’ they conclude ‘‘was violated in some way in every society we studied’’ (p. 803). And the violations weren’t random. The more integrated people were into a market economy, the more prosocial behavior they exhibited in the games (p. 795) (Further Reading: economic games in anthropology).

Unfortunately, I can’t evaluate the experiment because I simply failed to see the possibilities early enough. Finkler (1974) saw the possibilities; her ethnographic study of the effects of irrigation on an Indian village in the same area shows that the intervention is having profound effects. But neither she nor I measured (pretested) things like average village wealth, average personal wealth, migration rates, alcoholism, and so on that I believe have been affected by the coming of irrigation.

Had anyone done so—if we had baseline data—we would be in a better position to ask: ‘‘What hypotheses about human behavior are being tested by this experiment?’’ I can’t reconstruct variables from 20 or 30 years ago. The logical power of the experimental model for establishing cause and effect between the intervention and the dependent variables is destroyed.

Some natural experiments, though, produce terrific data all by themselves for evaluation. In 1955, the governor of Connecticut ordered strict enforcement of speeding laws in the state. Anyone caught speeding had his or her driver’s license suspended for at least 30 days. Traffic deaths fell from 324 in 1955 to 284 in 1956. A lot of people had been inconvenienced with speeding tickets and suspension of driving privileges, but 40 lives had been saved.

Did the crackdown cause the decline in traffic deaths? Campbell and Ross (1968) used the available data to find out. They plotted the traffic deaths from 1951 to 1959 in Connecticut, Massachusetts, New York, New Jersey, and Rhode Island. Four of the five states showed an increase in highway deaths in 1955, and all five states showed a decline in traffic deaths the following year, 1956. If that were all you knew, you couldn’t be sure about the cause of the decline. However, traffic deaths continued to decline steadily in Connecticut for the next 3 years (1957, 1958, 1959). In Rhode Island and Massachusetts, they went up; in New Jersey, they went down a bit and then up again; and in New York, they remained about the same.

Connecticut was the only state that showed a consistent reduction in highway deaths for 4 years after the stiff penalties were introduced. Campbell and Ross treated these data as a series of natural experiments, and the results were convincing: Stiff penalties for speeders saves lives.

Natural Experiments Are Everywhere

If you think like an experimentalist, you eventually come to see the unlimited possibilities for research going on all around you. Across the United States, school boards set rigid cutoff dates for children who are starting school. Suppose the cutoff is August 1. Children born at the end of July start kindergarten at age 5. Children born at the beginning of August start at age 6. Since children from 5 to 7 are going through an intense period of cognitive development, Morrison et al. (1996) treat this situation as a natural experiment and ask: Are there short- and long-term impacts on cognitive skills of just missing or just making the cutoff?

Ever notice how people like to tell stories about the time they found themselves sitting next to a famous person on a plane? It’s called BIRGing in social psychology—basking in reflected glory. Cialdini et al. (1976) evaluated the natural BIRGing experiment that is conducted on most big university campuses every weekend during football season. Over a period of 8 weeks, professors at Arizona State, Louisiana State, Ohio State, Notre Dame, Michigan, the University of Pittsburgh, and the University of Southern California recorded the percentage of students in their introductory psychology classes who wore school insignias (buttons, hats, t-shirts, etc.) on the Monday after Saturday football games. For 177 students per week, on average, over 8 weeks, 63% wore some school insignia after wins in football versus 44% after losses or ties. The difference was statistically significant and the finding opened up a whole area of research that continues (Madrigal and Chen 2008).

Here’s another one. On January 1, 2002, 12 of the then-15 members of the European Union gave up their individual currencies and adopted the euro (there are now 16 countries in the eurozone out of 27 in the European Union). Greece was one of the 12, Denmark wasn’t. Some researchers noticed that many of the euro coins were smaller than the Greek drachma coins they’d replaced and thought that this might create a choking hazard for small children (Papadopoulos et al. 2004). The researchers compared the number of choking incidents reported in Danish and Greek hospitals in January through March from 1996 through 2002. Sure enough, there was no increase in the rate of those incidents in Denmark (which hadn’t converted to the euro), but the rate in Greece suddenly more than doubled in 2002 (box 4.6).

TURNING A CONFOUND INTO A NATURAL EXPERIMENT

If you think like an experimentalist you can do what Kathy Oths did—turn what could have been a killer history confound into a research opportunity. From July 1 to December 15, 1988, Oths visited each of the 166 households in Chugurpampa, Peru, several times

BOX 4.6

C A S E C O N T R O L A N D N A T U R A L E X P E R I M E N T S

In a case control design, you compare naturally occurring cases of a criterion (like having a certain illness or injury, or attempting suicide, or being homeless) with people who match the cases on many criteria, but not on the case criterion.

This method is widely used in public health research, and in fact, the classic case-control study in anthropology was done by Art Rubel and colleagues (1984) on the Latin American folk illness known as susto. Among Indian people, the symptoms of susto—anxiety, diarrhea, difficulty breathing, and others—are often said to result from a loss of soul, while among mestizo people the symptoms are often attributed to having experiences some fright (from the verb asustarse, to become frightened). Rubel and his colleagues compared people in two Indian villages and one mestizo village in Mexico, all of whom suffered from susto (the index cases) with people in the same villages who did not (the control cases). There were no statistically significant differences between the 47 index cases and the 48 controls on tests of psychiatric symptoms. Seven years after the study was completed, however, 17% of the index cases had died—and none of the control cases had died. The design in this study makes it thoroughly convincing (Further Reading: case control).

to collect illness histories—what kinds of illnesses people came down with and what they did about them (Oths 1994). When she began the project, the harvest season had just ended in the high Andes and the farmers in Chugurpampa had collected most of the money they would have for the year. But in August, a month into her work, catastrophic inflation hit Peru and the local currency, the Peruvian inti, which was at 40 to the U.S. dollar, was crushed. It hit 683 by November.

Oths continued her household visits. As the hard times dragged on, the people of Chugurpampa continued to report the same number of illnesses (between seven and eight per household per month) but they defined a larger percentage of their illnesses as mild (requiring only home remedies) and a smaller percentage as moderate or severe (requiring visits to doctors or to the hospital). In other words, they spent what little money they had on cases that they thought needed biomedical intervention and stopped spending money on traditional healers (Further Reading: natural experiments).

NATURALISTIC EXPERIMENTS

In a naturalistic experiment, you contrive to collect experimental data under natural conditions. You make the data happen, out in the natural world (not in the lab), and you evaluate the results.

In a memorable experiment, elegant in its simplicity of design, Doob and Gross (1968) had a car stop at a red light and wait for 15 seconds after the light turned green before moving again. In one experimental condition, they used a new car and a well-dressed driver. In another condition, they used an old, beat-up car and a shabbily dressed driver. They repeated the experiment many times and measured the time it took for people in the car behind the experimental car to start honking their horns. It won’t surprise you to learn that people were quicker to vent their frustration at apparently low-status cars and drivers.

Piliavin et al. (1969) did a famous naturalistic experiment to test the ‘‘good Samaritan’ problem. Students in New York City rode a particular subway train that had a 7.5-minute run at one point. At 70 seconds into the run, a researcher pitched forward and collapsed. The team used four experimental conditions: The ‘‘stricken’’ person was either black or white and was either carrying a cane or a liquor bottle. Observers noted how long it took for people in the subway car to come to the aid of the supposedly stricken person, the total population of the car, whether bystanders were black or white, and so on. You can conjure up the results. There were no surprises.

Harari et al. (1985) recruited drama majors to test whether men on a college campus would come to the aid of a woman being raped. They staged realistic-sounding rape scenes and found that there was a significant difference in the helping reaction of male passersby if those men were alone or in groups.

And Walker (2006) rode his bicycle 200 miles through Bristol and Salisbury, England during regular working hours dressed as an ordinary commuter—sometimes wearing a helmet, sometimes not; sometimes wearing a woman’s long-haired wig, sometimes not. Walker outfitted his bike with a hidden distance sensor and a tiny camera and then, systematically varying his distance from the curb, he measured how close cars came as they passed him. The farther from the edge he rode, the closer drivers came; drivers stayed farther from him when he appeared to be a woman; and drivers came closer to him when he wasn’t wearing a helmet than when he was. Fortunately, both times he got hit doing this experiment, he was wearing the helmet (Further Reading: naturalistic experiments).

The Small-World Experiment

Consider this: You’re having coffee near the Trevi Fountain in Rome. You overhear two Americans chatting next to you and you ask where they’re from. One of them says she’s from Sioux City, Iowa. You say you’ve got a friend from Sioux City and it turns out to be your new acquaintance’s cousin. The culturally appropriate reaction at this point is for everyone to say, ‘‘Wow, what a small world!’’

Stanley Milgram (1967) invented an experiment to test how small the world really is. He asked a group of people in the midwestern United States to send a folder to a divinity student at Harvard University, but only if the participant knew the divinity student personally. Otherwise, Milgram asked people to send the folders to an acquaintance whom they thought had a chance of knowing the ‘‘target’’ at Harvard.

The folders got sent around from acquaintance to acquaintance until they wound up in the hands of someone who actually knew the target—at which point the folders were sent, as per the instructions in the game, to the target. The average number of links between all the ‘‘starters’’ and the target was about five. It really is a small world.

No one expects this experiment to actually happen in real life. It’s contrived as can be and it lacks control. But it’s compelling because it says something about how the natural world works. The finding was so compelling that it was the basis for the Broadway play ‘‘Six Degrees of Separation,’’ as well as the movie of the same name that followed and the game ‘‘Six Degrees of Kevin Bacon.’’ It also provoked research, first by social scientists and then by physicists and mathematicians, on the structure of relations in everything from people to corporations to nations to neurons to sites on the Internet. Looking for the structure of relations is another way of saying ‘‘network analysis.’

The Lost-Letter Technique

Another of Milgram’s contributions is a method for doing unobtrusive surveys of political opinion. The method is called the ‘‘lost-letter technique’’ and consists of ‘‘losing’’ a lot of letters that have addresses and stamps on them (Milgram et al. 1965).

The technique is based on two assumptions. First, people in many societies believe that they ought to mail a letter if they find one, especially if it has a stamp on it. Second, people will be less likely to drop a lost letter in the mail if it is addressed to someone or some organization that they don’t like.

Milgram et al. (1965) tested this in New Haven, Connecticut. They lost 400 letters in ten districts of the city. They dropped the letters on the street; they left them in phone booths; they left them on counters at shops; and they tucked them under windshield wipers (after penciling ‘‘found near car’’ on the back of the envelope). Over 70% of the letters addressed to an individual or to a medical research company were returned. Only 25% of the letters addressed to either ‘‘Friends of the Communist Party’’ or ‘‘Friends of the Nazi Party’’ were returned. (The addresses were all the same post box that had been rented for the experiment.)

By losing letters in a sample of communities, then, and by counting the differential rates at which they are returned, you can test variations in sentiment. Two of Milgram’s students distributed anti-Nazi letters in Munich. The letters did not come back as much from some neighborhoods as from others, and they were thus able to pinpoint the areas of strongest neo-Nazi sentiment (Milgram 1969:68). The lost-letter technique has sampling problems and validity problems galore associated with it. But it’s still an interesting way to infer public opinion about emotionally charged issues, and you can see just how intuitively powerful the results can be (Further Reading: the lost-letter technique).

COMPARATIVE FIELD EXPERIMENTS

Naturalistic field experiments appeal to me because they are excellent for comparative research, and comparison is so important for developing theory. Feldman (1968) did five field experiments in Paris, Boston, and Athens to test whether people in those cities respond more kindly to foreigners or to members of their own culture.

In one experiment, the researchers simply asked for directions and measured whether foreigners or natives got better treatment. Parisians and Athenians gave help significantly more often to fellow citizens than to foreigners. In Boston, there was no difference.

In the second experiment, foreigners and natives stood at major metro stops and asked total strangers to do them a favor. They explained that they were waiting for a friend, couldn’t leave the spot they were on, and had to mail a letter. They asked people to mail the letters for them (the letters were addressed to the experiment headquarters) and simply counted how many letters they got back from the different metro stops in each city. Half the letters were unstamped.

In Boston and Paris, between 32% and 35% of the people refused to mail a letter for a fellow citizen. In Athens, 93% refused. Parisians treated Americans significantly better than Bostonians treated Frenchmen on this task. In fact, in cases where Parisians were asked to mail a letter that was stamped, they treated Americans significantly better than they treated other Parisians! (So much for that stereotype.)

In the third experiment, researchers approached informants and said: ‘‘Excuse me, sir. Did you just drop this dollar bill?’’ (or other currency, depending on the city). It was easy to measure whether or not people falsely claimed the money more from foreigners than from natives. This experiment yielded meager results.

In the fourth experiment, foreigners and natives went to pastry shops in the three cities, bought a small item and gave the clerk 25% more than the item cost. Then they left the shop and recorded whether the clerk had offered to return the overpayment. This experiment also showed little difference among the cities or between the way foreigners and locals are treated.

And in the fifth experiment, researchers took taxis from the same beginning points to the same destinations in all three cities. They measured whether foreigners or natives were charged more. In neither Boston nor Athens was a foreigner overcharged more than a local. In Paris, however, Feldman found that ‘‘the American foreigner was overcharged significantly more often than the French compatriot in a variety of ingenious ways’’ (1968:11).

Feldman collected data on more than 3,000 interactions and was able to draw conclusions about cultural differences in how various peoples respond to foreigners as opposed to other natives. Some stereotypes were confirmed; others were crushed. Since Feldman’s pioneering work, dozens of studies have been done on cross-cultural differences in helping strangers (see Levine et al. [2001], for example).

Bochner did a series of interesting experiments on the nature of Aboriginal-white relations in urban Australia (see Bochner [1980:335–40] for a review). These experiments are clever, inexpensive, and illuminating, and Bochner’s self-conscious critique of the limitations of his own work is a model for field experimentalists to follow. In one experiment, Bochner put two classified ads in a Sydney paper:

Young couple, no children, want to rent small unfurnished flat up to $25 per week. Saturday only. 759–6000.

Young Aboriginal couple, no children, want to rent small unfurnished flat up to $25 per week. Saturday only. 759–6161. (Bochner 1972:335)

Different people were assigned to answer the two phones, to ensure that callers who responded to both ads would not hear the same voice. Note that the ads were identical in every respect, except for the fact that in one of the ads the ethnicity of the couple was identified and in the other it was not. There were 14 responses to the ethnically nonspecific ad and two responses to the ethnically specific ad (three additional people responded to both ads).

In another experiment, Bochner exploited what he calls the ‘‘Fifi effect’’ (Bochner 1980:336). The Fifi effect refers to the fact that urbanites acknowledge the presence of strangers who pass by while walking a dog and ignore others. Bochner sent a white woman and an Aboriginal woman, both in their early 20s, and similarly dressed, to a public park in Sydney. He had them walk a small dog through randomly assigned sectors of the park, for 10 minutes in each sector.

Each woman was followed by two observers, who gave the impression that they were just out for a stroll. The two observers independently recorded the interaction of the women with passersby. The observers recorded the frequency of smiles offered to the women; the number of times anyone said anything to the women; and the number of nonverbal recognition nods the women received. The white woman received 50 approaches; the Aboriginal woman received only 18 (Bochner 1971:111).

There are many elegant touches in this experiment. Note how the age and dress of the experimenters were controlled, so that only their ethnic identity remained as a dependent variable. Note how the time for each experimental trial (10 minutes in each sector) was controlled to ensure an equal opportunity for each woman to receive the same treatment by strangers. Bochner did preliminary observation in the park and divided it into sectors that had the same population density, so that the chance for interaction with strangers would be about equal in each run of the experiment, and he used two independent observer-recorders.

As Bochner points out, however, there were still design flaws that threatened the internal validity of the experiment (1980:337). As it happens, the interrater reliability of the two observers in this experiment was nearly perfect. But suppose the two observers shared the same cultural expectations about Aboriginal-white relations in urban Australia. They might have quite reliably misrecorded the cues that they were observing.

Reactive and unobtrusive observations alike tell you what happened, not why. It is tempting to conclude that the Aboriginal woman was ignored because of active prejudice. But, says Bochner, ‘‘perhaps passersby ignored the Aboriginal . . . because they felt a personal approach might be misconstrued as patronizing’’ (Bochner 1980:338).

In Bochner’s third study, a young white or Aboriginal woman walked into a butcher’s shop and asked for 10 cents’ worth of bones for her pet dog. The dependent variables in the experiment were the weight and quality of the bones. (An independent dog fancier rated the bones on a 3-point scale, without knowing how the bones were obtained, or why.) Each woman visited seven shops in a single middle-class shopping district.

In both amount and quality of bones received, the white woman did better than the Aboriginal, but the differences were not statistically significant—the sample was just too small so no conclusions could be drawn from that study alone. Taken all together, though, the three studies done by Bochner and his students comprise a powerful set of information about Aboriginal-white relations in Sydney. Naturalistic experiments like these have their limitations, but they often produce intuitively compelling results. And since Bochner’s work, nearly 40 years ago, dozens of other field studies have been done testing for discrimination in housing, lending, and hiring (Ahmed and Hammarstedt 2008; Sharpe 1998).

ARE FIELD EXPERIMENTS ETHICAL?

Field experiments come in a range of ethical varieties, from innocuous to borderline to downright ugly. I see no ethical problems with the lost-letter technique. When people mail one of the lost letters, they don’t know that they are taking part in an experiment, but that doesn’t bother me. Personally, I see no harm in the experiment to test whether people vent their anger by honking their car horns more quickly at people they think are lower socioeconomic class. These days, however, with road rage an increasing problem, I don’t recommend repeating Doob and Gross’s experiment.

Randomized field experiments, used mostly in evaluation research, can be problematic. Suppose you wanted to know whether fines or jail sentences are better at changing the behavior of drunk drivers. One way to do that would be to randomly assign people who were convicted of the offense to one or the other condition and watch the results. Suppose one of the participants whom you didn’t put in jail kills an innocent person?

The classic experimental design in drug testing requires that some people get the new drug, that some people get a placebo (a sugar pill that has no effect), and that neither the patients nor the doctors administering the drugs know which is which. This double-blind placebo design is responsible for great advances in medicine and the saving of many lives. But suppose that, in the middle of a double-blind trial of a drug you find out that the drug really works. Do you press on and complete the study? Or do you stop right there and make sure that you aren’t withholding treatment from people whose lives could be saved? The ethical problems associated with withholding of treatment are under increasing scrutiny (Storosum et al. 2003; Walther 2005; Wertz 1987).

There is a long history of debate about the ethics of deception in psychology and social psychology (see Hertwig and Ortmann [2008] for a review). My own view is that, on balance, some deception is clearly necessary—certain types of research just can’t be done without it. When you use deception, though, you run all kinds of risks—not just to research participants, but to the research itself. These days, college students (who are the participants for most social psych experiments) are very savvy about all this and are on the lookout for clues as to the ‘‘real’’ reason for an experiment the minute they walk in the door.

If you don’t absolutely need deception in true behavioral experiments, that’s one less problem you have to deal with. If you decide that deception is required, then understand that the responsibility for any bad outcomes is yours and yours alone.

The experiments by Piliavin et al. (1969) and Harari et al. (1985) on whether people will come to the aid of a stricken person, or a woman being raped, present real ethical problems. Some of the participants (who neither volunteered to be in an experiment nor were paid for their services) might still be wondering what happened to that poor guy on the subway whom they stepped over in their hurry to get away from an uncomfortable situation—or that woman whose screams they ignored. In laboratory experiments, at least, participants are debriefed—told what the real purpose of the study was—to reduce emotional distress. In the guerrilla theater type of field experiment, though, no debriefing is possible.

Even debriefing has its dark side. People don’t like to find out that they have been duped into being part of an experiment, and some may suffer a terrible loss of self-esteem if they do find out and conclude that they acted badly. How would you feel if you were one of the people who failed to respond to a rape victim and then were told that you were just part of an experiment—that no real rape ever took place, and thank you very much for your help? (Further Reading: deception and debriefing).

If you think some of these cases are borderline, consider the study by West et al. (1975) on whether there is a little larceny in us all.

THE WATERGATE EXPERIMENT

In the Watergate affair of 1974, men loyal to then President Richard Nixon broke into the headquarters of the Democratic Party at the Watergate Hotel in Washington, DC, to photograph documents pertinent to the 1972 election campaign. Their bungling of the job, and the subsequent cover-up by Nixon and his staff at the White House, led to the unprecedented resignation of the president of the United States from office in 1974. Soon thereafter, West et al. conducted their experiment.

They confronted 80 different students with a proposition to burglarize a local advertising firm. Participants were randomly assigned to one of four conditions. In the first condition, participants were told that the job was to be done for the Internal Revenue Service. The IRS, it seemed, needed to get the goods on this company to bring them to trial for tax evasion. If the participants were caught in the act, then the government would guarantee immunity from prosecution. In the second condition, participants were told that there was no immunity from prosecution.

In the third condition, participants were told that another advertising agency had paid $8,000 for the job, and that they (the participants) would get $2,000 for their part in it. (Remember, that was $2,000 in 1979—about $6,000 today.) Finally, in the fourth condition, participants were told that the burglary was being committed just to see if the plan would work. Nothing would be taken from the office.

Understand that this was not a ‘‘let’s pretend’’ exercise. Participants were not brought into a laboratory and told to imagine that they were being asked to commit a crime. This was for real. Participants met the experimenter at his home or at a restaurant. They were all criminology students at a university and knew the experimenter to be an actual local private investigator. The private eye arranged an elaborate and convincing plan for the burglary, including data on the comings and goings of police patrol cars, aerial photographs, blueprints of the building—the works.

The participants really believed that they were being solicited to commit a crime. Just as predicted by the researchers, a lot of them agreed to do it in the first condition, when they thought the crime was for a government agency and that they’d be free of danger from prosecution if caught. What do you suppose would happen to your sense of selfworth when you were finally debriefed and told that you were one of the 36 out of 80 (45%) who agreed to participate in the burglary in the first condition? (See Cook [1975] for a critical comment on the ethics of this experiment.) (box 4.7).

BOX 4.7

R E S E A R C H A N D I N S T I T U T I O N A L R E V I E W B O A R D S

The key ethical issue in the conduct of all social research is whether those being studied are placed at risk by those doing the studying. This goes for field research—including surveys, ethnographies, and naturalistic experiments—as much as it does for laboratory studies. All universities in the United States have long had Institutional Review Boards, or IRBs. These are internal agencies whose members review and pass judgment on the ethical issues associated with all research on people, including biomedical and psychosocial. The concept of informed consent has developed and matured over the years. All researchers are asked by the IRBs to describe clearly and precisely what steps will be taken to ensure that people who participate in research will be protected from harm. And not just physical harm. Research participants should not experience emotional harm or financial harm, either.

With regard to the protection of human subjects, most research in cultural anthropology is covered by the Common Rule, from the National Science Foundation (http://www.nsf.gov/bfa/dias/policy/docs/45cfr690.pdf). For more information about NSF’s policies, go to http://www.nsf.gov/bfa/dias/policy/human .jsp. The rules of the protection of human subjects in biomedical research come from the National Institutes of Health and its constituent funding agencies (the National Institute on Drug Abuse, the National Institute of Mental Health, and so on). Go to http://ohsr.od.nih.gov/info/sheet5.html and http://www.hhs.gov/ohrp.

FACTORIAL DESIGNS: MAIN EFFECTS AND INTERACTION EFFECTS

Most experiments involve analyzing the effects of several independent variables at once. A factorial design lays out all the combinations of all the categories of the independent variables. That way you know how many participants you need, how many to assign to each condition, and how to run the analysis when the data are in.

It is widely believed that a good laugh has healing power. Rotton and Shats (1996) developed an experimental design to test this. They recruited 39 men and 39 women who were scheduled for orthopedic surgery. The patients were assigned randomly to one of nine groups—eight experimental groups and one control group. The patients in the eight treatment groups got to watch a movie in their room the day after their surgery.

There were three variables: choice, humor, and expectancy. The participants in the high-choice group got a list of 20 movies from which they chose 4. The participants in the low-choice group watched a movie that one of the people in the high-choice group had selected. Half the participants watched humorous movies and half watched action or adventure movies. Before watching their movie, half the participants read an article about the benefits of humor and half read an article about the healthful benefits of exciting movies.

Figure 4.4 is a branching tree diagram that shows how these three variables, each with two attributes, create the eight logical groups for Rotton and Shats’s experiment. Table 4.1 shows the same eight-group design, but in a format that is more common. The eight nodes at the bottom of the tree in figure 4.4 and the sets of numbers in the eight boxes of table 4.1 are called conditions.

FIGURE 4.4. The eight conditions in Rotton and Shats’s $2 \times 2 \times 2$ design. SOURCE: J. Rotton and M. Shats, ‘‘Effects of State Humor, Expectancies, and Choice on Postsurgical Mood and Self-Medication: A Field Experiment,’’ Journal of Applied Social Psychology, Vol. 26, pp. 1775–94, 1996. Copyright - 1996 by V. H. Winston & Son, Inc. Reprinted with permission.

The dependent variables in this study included a self-report by patients on the amount of pain they had and a direct measure of the amount of pain medication they took. All the patients had an access device that let them administer more or less of the analgesics that are used for controlling pain after orthopedic surgery.

In assessing the results of a factorial experiment, researchers look for main effects and interaction effects. Main effects are the effects of each independent variable on each dependent variable. Interaction effects are effects on dependent variables that occur as a result of interaction between two or more independent variables. In this case, Rotton and Shats wanted to know the effects of humor on postoperative pain, but they wanted to know the effect in different contexts: in the context of choosing the vehicle of humor or not, in the context of being led to believe that humor has healing benefits or not, and so on.

As it turned out, being able to choose their own movie had no effect when patients saw action films. But patients who saw humorous films and who had not been able to make their own choice of film gave themselves more pain killer than did patients who saw humorous films and had been able to make the selection themselves (Rotton and Shats 1996).

Table 4.1 Three-Way, $2 \times 2 \times 2 ,$ , Factorial Design

		Variable 3
		Variable 2	Attribute 1	Attribute 2
Variable 1	Attribute 1	Attribute 1	1,1,1 Condition 1	1,1,2 Condition 2
		Attribute 2	1,2,1 Condition 3	1,2,2 Condition 4
	Attribute 2	Attribute 1	2,1,1 Condition 5	2,1,2 Condition 6
		Attribute 2	2,2,1 Condition 7	2,2,2 Condition 8

We’ll look at how to measure these effects when we take up ANOVA, or analysis of variance, in chapter 21.

FURTHER READING

The classic experimental design and evaluation research: Cotton and Byrd-Bredbenner (2007); R. Jones (2008); Klass and Cothers (2000); Mishra et al. (1999).

Solomon four-group design: Holmes and Keffer (1995); Jorgensen et al. (1985); Probst (2003).

Quasi-experiments: Coleman (1999); Rotton et al. (1990); Shadish and Cook (2008); Yildirim et al. (2007).

Posttest-only design: Goodall and Appiah (2008); Ortberg et al. (2001); J. A. Robinson (1996); Trockel et al. (2008).

Case study methods: Gerring (2007); Merriam (2009); Naumes and Naumes (2006); Wolcott (2001, 2005); Yin (2008).

One group pretest posttest design: Chan et al. (2007); D’Eramo-Melkus et al. (2004); Derrick et al. (2008).

Static group comparison design: Coast (2002); Marlanai (2008); Pinkleton et al. (2008).

Interrupted time series design: Gorman and Huber (2007); Ramirez and Crano (2003); Villaveces et al. (2000).

Field experiments: Banerjee et al. (2009); Knecht and Martinez (2009); Scheerer et al. (2009).

Economic games in anthropology: Alvard (2004); Cronk (2007); Gil-White (2004); Lesorogol (2007); Wiessner (2009).

Case control: Beautrais et al. (1998); Pfeiffer et al. (2001).

Natural experiments: Becker et al. (2002); Morrison and Clements (1997); Zhu et al. (2007).

Naturalistic experiments: Gue´guen et al. (2008); Keating et al. (2003); Levine et al. (2001); Walters and Curran (1996).

Lost-letter technique: Bridges and Coady (1996); Bridges et al. (2002); Hedge and Yousif (1992); Keating et al. (2003); D. S. Wilson et al. (2009).

Ethics of deception and debriefing: Barchard and Williams (2008); Korn (1997); Riach and Rich (2004).

Sampling I: The Basics

WHAT ARE SAMPLES AND WHY DO WE NEED THEM?

Informant accuracy, data validity, and ethical questions—like whether it’s alright to deceive people in conducting experiments—are all measurement problems in research. The other big class of problems involves sampling: Given that your measurements are credible, how much of the world do they represent? How far can you generalize the results of your research?

The answer depends, first of all, on the kind of data in which you’re interested. There are two kinds of data of interest to social scientists: individual attribute data and cultural data. These two kinds require different approaches to sampling.

Individual data are about attributes of individuals in a population. Each person has an age, for example; each person has an income; and each person has preferences for things like characteristics of a mate. If the idea to estimate the average age, or income, or preference in a population—that is, to estimate some population parameters—then a scientifically drawn, unbiased sample is a must.

By ‘‘scientifically drawn,’’ I mean random selection of cases so that every unit of analysis has an equal chance of being chosen for study.

Cultural data are different. We expect cultural facts to be shared, so cultural data require experts. If you want to understand a process—like breast-feeding, or the making up of a guest list for a wedding, or a shaman’s treatment of a sick person—then you want people who can offer expert explanations about the cultural norm and about variations on that norm (Handwerker et al. 1997). It’s one thing to ask: ‘‘How many cows did you give to your in-laws as bride price when you got married?’’ It’s quite another thing to ask: ‘‘Why do men who get married around here deliver cows to their in-laws? . . . And how many do men usually give?’’

Individual attribute data require probability sampling; cultural data require nonprobability sampling. This chapter is about the basics of probability sampling, which will take us into a discussion of probability theory, variance, and distributions in chapter 6. We’ll get to nonprobability sampling in chapter 7.

WHY THE UNITED STATES STILL HAS A CENSUS

If samples were just easier and cheaper to study but failed to produce useful data, there wouldn’t be much to say for them. A study based on a random sample, however, is often better than one based on the whole population.

Since 1790, the United States has conducted a census once every 10 years in which every person in the country is supposed to be counted in order to apportion seats in the House of Representatives to the states. Lots of things can go wrong with counting. Heads of households are responsible for filling out and returning the census forms, but in 1990, only 63% of the mailed forms were returned, and that was down from 78% in 1970. The Bureau of the Census had to hire and train half a million people to track down all the people who had not been enumerated in the mailed-back forms. Even then, there were problems with the final numbers. Some college students were counted twice: Their parents had counted them on the mailed-back census form and then, on census day, some of those same students were tracked down again by enumerators who canvassed the dorms. Meanwhile, lots of other people (like illegal immigrants and people living in places to which the census takers would rather not go) were not being counted at all.

In 1997, the Bureau of the Census asked the U.S. Congress to allow sampling instead of counting for at least some parts of the 2000 Census. This caused a serious political problem: If sampling produced more accurate (and, presumably, higher) estimates of the number of citizens who are, say, homeless or who are migrant farm workers, this would benefit only certain states and might benefit the Democratic Party over the Republican Party. So, Congress rejected the proposal, citing the Article 1, Section 2 of the Constitution, which refer to the Census as an ‘‘actual Enumeration’’ (with a capital E, no less).

No getting around it: Actually enumerating means counting, not estimating, and the U.S. Supreme Court agreed, in 1999. To deal with the inaccuracies of a head count, the Bureau of the Census publishes adjustment tables, based on samples. In 2000, for example, the bureau determined that it had undercounted American Indians who live off reservations by about 53,000 (see U.S. Bureau of the Census n.d.).

IT PAYS TO TAKE SAMPLES AND TO STICK WITH THEM

If you are doing all the work yourself, it’s next to impossible to interview more than a few hundred people. Even in a community of just 1,000 households, you’d need several interviewers to reach everyone. Interviewers may not use the same wording of questions; they may not probe equally well on subjects that require sensitive interviewing; they may not be equally careful in recording data on field instruments and in coding data for analysis. The more personnel there are on any project, the greater the instrumentation threat and the more risk to the validity of the data.

Most important, you have no idea how much error is introduced by these problems. A well-chosen sample, interviewed by people who have similarly high skills in getting data, has a known chance of being incorrect on any variable. (Careful, though: If you have a project that requires multiple interviewers and you try to skimp on personnel, you run a big risk. Overworked or poorly trained interviewers will cut corners; see chapter 8.)

Furthermore, studying an entire population may pose a history threat to the internal validity of your data. If you don’t add interviewers, it may take you so long to complete your research that events intervene that make it impossible to interpret your data.

For example, suppose you are interested in how people in a community feel about being relocated in anticipation of a new dam coming on line and their land being flooded. You decide to interview all 210 adults in the community. It’s difficult to get some people at home, but you figure that you’ll just do the survey, a little at a time, while you’re doing other things during your year in the field.

About 6 months into your fieldwork, you’ve gotten 160 interviews on the topic—only 50 to go. Just about that time, the courts adjudicate a particularly sore point that has been in dispute for a decade regarding access to a particular sacred site. All of a sudden, the picture changes. Your ‘‘sample’’ of 160 is biased toward those people whom it was easy to find, and you have no idea what that means. And even if you could now get those remaining 50 informants, their opinions may have been radically changed by the court judgment. The opinions of the 160 informants who already talked to you may have also changed.

Now you’re really stuck. You can’t simply throw together the 50 and the 160, because you have no idea what that will do to your results. Nor can you compare the 160 and the 50 as representing the community’s attitudes before and after the judgment. Neither sample is representative of the community.

If you had taken a representative sample of 60 people in a single week early in your fieldwork, you’d now be in much better shape because you’d know the potential sampling error in your study. (I’ll discuss how you know this later on in this chapter.) When historical circumstances (the surprise court judgment, for example) require it, you could interview the same sample of 60 again (in what is known as a panel study), or take another representative sample of the same size and see what differences there are before and after the critical event.

In either case, you are better off with the sample than with the whole population. By the way, there is no guarantee that a week is quick enough to avoid the problem described here. It’s just less likely to be a problem.

SAMPLING FRAMES

If you can get it, the first thing you need for a good sample is a good sampling frame. (I say, ‘‘If you can get it,’’ because a lot of social research is done on populations for which no sampling frame exists. More on this at the end of this chapter.) A sampling frame is a list of units of analysis from which you take a sample and to which you generalize.

A sampling frame may be a telephone directory, or the tax rolls of a community, or a census of a community that you do yourself. In the United States, the city directories (published by R. L. Polk and Company) are available for many towns and cities at the local library or Chamber of Commerce. Professional survey researchers in the United States often purchase samples from firms that keep up-to-date databases just for this purpose.

For many projects, though, especially projects that involve field research, you have to get your own census of the population you are studying. Whether you work in a village or a hospital, a census gives you a sampling frame from which to take many samples during a research project. It also gives you a basis for comparison if you go back to the same community later.

SIMPLE RANDOM SAMPLES

To get a simple random sample of 200 out of 640 people in a village, you number each individual from 1 to 640 and then take a random grab of 200 out of the numbers from 1 to 640. Most packages for statistical analysis have built in random-number generators (Internet addresses for several programs are given in appendix E), and you can create random samples by using one of the random-number generators on the Internet—like the one at http://www.randomizer.org/form.htm.

When you have your list of random numbers, then whoever goes with each one is in the sample. Period. If there are 1,230 people in the population and your list of random numbers says that you have to interview person 212, then do it. No fair leaving out some people because they are members of the elite and probably wouldn’t want to give you the time of day. No fair leaving out people you don’t like or don’t want to work with. None of that.

In the real world of research, of course, random samples are tampered with all the time. (And no snickering here about the ‘‘real world’’ of research. Social research—in universities, in marketing firms, in polling firms, in the military—is a multibillion-dollara-year industry in the United States alone—and that’s real enough for most people.) A common form of meddling with samples is when door-to-door interviewers find a sample selectee not at home and go to the nearest house for a replacement. This can have dramatically bad results.

Suppose you go out to interview between 10 a.m. and 4 p.m. People who are home during these hours tend to be old, or sick, or mothers with small children. Those same people are home in the evening, too, but now they’re joined by all the single people home from work, so the average family size goes down.

Telephone survey researchers call back from three to 10 times before replacing a member of a sample. When survey researchers suspect (from prior work) that, say, 25% of a sample won’t be reachable, even after call-backs, they increase their original sample size by 25% so the final sample will be both the right size and representative.

SYSTEMATIC RANDOM SAMPLING

If you have a big, unnumbered sampling frame, like the 51,413 students at the University of Florida in 2008, then simple random sampling is nearly impossible. You would have to number all those names first. Instead, you can do systematic random sampling. For this, you need a random start and a sampling interval, N. You enter the sampling frame at the random start and take every Nth person (or item) in the frame. If you have a printout of 51,413 names, listed 400 to a page, select a single random number between 1 and 51,413. If the random number is 9,857, the listing will be 257 names down from the top of page 25.

The sampling interval depends on the size of the population and the number of units in your sample. If there are 51,413 people in the population, and you are sampling 400 of them, then after you enter the sampling frame (the list of 51,413 names) you need to take every 128th person (400 128  51,200) to ensure that every person has at least one chance of being chosen. If there are 640 people in a population, and you are sampling 200 of them, then you would take every 4th person. If you get to the end of the list and you are at number 2 in an interval of 4, just go to the top of the list, start at 3, and keep on going (box 5.1).

Sampling from a Telephone Book

Systematic sampling is fine if you know that the sampling frame has 51,413 elements. What do you do when the size of the sampling frame is unknown? A big telephone book is an unnumbered sampling frame of unknown size. To use this kind of sampling frame, first determine the number of pages that actually contain listings. To do this, jot down the number of the first and last pages on which listings appear. Most phone books begin with a lot of pages that do not contain listings.

Suppose the listings begin on page 30 and end on page 520. Subtract 30 from 520 and add 1 (520  30 1  491) to calculate the number of pages that carry listings.

Then note the number of columns per page and the number of lines per column (count all the lines in a column, even the blank ones).

Suppose the phone book has three columns and 96 lines per column (this is quite typical). To take a random sample of 200 nonbusiness listings from this phone book, take a random sample of 400 page numbers (yes, 400) out of the 491 page numbers between 30 and 520. Just think of the pages as a numbered sampling frame of 491 elements. Next,

BOX 5.1

P E R I O D I C I T Y A N D S Y S T E M A T I C S A M P L I N G

Systematic sampling usually produces a representative sample, but be aware of the periodicity problem. Suppose you’re studying a big retirement community in South Florida. The development has 30 identical buildings. Each has six floors, with 10 apartments on each floor, for a total of 1,800 apartments. Now suppose that each floor has one big corner apartment that costs more than the others and attracts a slightly more affluent group of buyers. If you do a systematic sample of every 10th apartment, then, depending on where you entered the list of apartments, you’d have a sample of 180 corner apartments or no corner apartments at all.

David and Mary Hatch (1947) studied the Sunday society pages of the New York Times for the years 1932–1942. They found only stories about weddings of Protestants and concluded that the elite of New York must therefore be Protestant. Cahnman (1948) pointed out that the Hatches had studied only June issues of the Times. It seemed reasonable. After all, aren’t most society weddings in June? Well, yes. Protestant weddings. Upper-class Jews married in other months. The Times covered those weddings, but the Hatches missed them.

You can avoid the periodicity problem by doing simple random sampling, but if that’s not possible, another solution is to make two systematic passes through the population using different sampling intervals. Then you can compare the two samples one a few independent variables, like age or years of education. Any differences should be attributable to sampling error. If they’re not, then you might have a periodicity problem.

take a sample of 400 column numbers. Since there are three columns, you want 400 random choices of the numbers 1, 2, 3. Finally, take a sample of 400 line numbers. Since there are 96 lines, you want 400 random numbers between 1 and 96.

Match up the three sets of numbers and pick the sample of listings in the phone book. If the first random number between 30 and 520 is 116, go to page 116. If the first random number between 1 and 3 is 3, go to column 3. If the first random number between 1 and 96 is 43, count down 43 lines. Decide if the listing is eligible. It may be a blank line or a business. That’s why you generate 400 sets of numbers to get 200 good listings.

Telephone books don’t actually make good sampling frames—too many people have unlisted numbers (which is why we have random digit dialing—see chapter 9). But because everyone knows what a phone book looks like, it makes a good example for learning how to sample big, unnumbered lists of things, like the list of Catholic priests in Paraguay or the list of orthopedic surgeons in California.

STRATIFIED SAMPLING

Stratified random sampling ensures that key subpopulations are included in your sample. You divide a population (a sampling frame) into subpopulations (subframes), based on key independent variables and then take a random (unbiased), sample from each of those subpopulations. You might divide the population into men and women, or into rural and urban subframes—or into key age groups (18–34, 35–49, etc.) or key income groups. As the main sampling frame gets divided by key independent variables, the subframes presumably get more and more homogeneous with regard to the key dependent variable in the study.

In 2009, for example, the Quinnipiac University Poll asked a representative sample of 2,041 registered voters in the United States the following question: Do you think abortion should be legal in all cases, legal in most cases, illegal in most cases or illegal in all cases? Across all voters, 52% said that abortion should be legal in all (15%) or most (37%) cases and 41% said it should be illegal in all (14%) or most (27%) cases. (The remaining 7% had no opinion.)

These facts hide some important differences across religious, political, and other subgroups. Among Catholic voters, 50% said that abortion should be legal in all (8%) or most (42%) cases; among Jewish voters, 86% said that abortion should be legal in all (33%) or most (53%) cases. Among registered Democrats, 66% favored legal abortion in all or most cases; among registered Republicans, 30% took that position (Quinnipiac University 2009). Sampling from smaller chunks (by age, gender, and so on) ensures not only that you capture the variation, but that you also wind up understanding how that variation is distributed.

This is called maximizing the between-group variance and minimizing the withingroup variance for the independent variables in a study. It’s what you want to do in building a sample because it reduces sampling error and thus makes samples more precise.

This sounds like a great thing to do, but you have to know what the key independent variables are. Shoe size is almost certainly not related to what people think is the ideal number of children to have. Gender and generation, however, seem like plausible variables on which to stratify a sample. So, if you are taking a poll to find out the ideal number of children, you might divide the adult population into, say, four generations: 15–29, 30–44, 45–59, and over 59.

With two genders, this creates a sampling design with eight strata: men 15–29, 30–44, 45–59, and over 59; women 15–29, 30–44, 45–59, and over 59. Then you take a random sample of people from each of the eight strata and run your poll. If your hunch about the importance of gender and generation is correct, you’ll find the attitudes of men and the attitudes of women more homogeneous than the attitudes of men and women thrown together.

Table 5.1 shows the distribution of gender and age cohorts for St. Lucia in 2001. The numbers in parentheses are percentages of the total population 15 and older (106,479), not percentages of the column totals.

Table 5.1 Estimated Population by Sex and Age Groups for St. Lucia, 2001

Age cohort	Males	Females	Total
15–29	21,097 (19.8%)	22,177 (20.8%)	43,274 (40.6%)
30–44	15,858 (14.9%)	16,763 (15.7%)	32,621 (30.6%)
45–59	8,269 (7.8%)	8,351 (7.8%)	16,620 (15.6%)
>59	7,407 (7%)	6,557 (6.2%)	13,964 (13.1%)
Total	52,631 (49.5%)	53,848 (50.5%)	106,479 (100%)

SOURCE: Govt. Statistics, St. Lucia. http://www.stats.gov.lc/cen2001.htm.

A proportionate stratified random sample of 800 respondents would include 112 men between the ages of 30 and 44 (14% of 800  112), but 120 women between the ages of 30 and 44 (15% of 800  120), and so on.

Watch out, though. We’re asking people about their ideal family size and thinking about stratifying by gender because we’re accustomed to thinking in terms of gender on questions about family size. But gender-associated preferences are changing rapidly in late industrial societies, and we might be way off base in our thinking. Separating the population into gender strata might just be creating unnecessary work. Worse, it might introduce unknown error. If your guess about age and gender being related to desired number of children is wrong, then using table 5.1 to create a sampling design will just make it harder for you to discover your error (box 5.2).

BOX 5.2

T H E R U L E S O N S T R A T I F Y I N G S A M P L E S

Here are the rules on stratification: (1) If differences on a dependent variable are large across strata like age, sex, ethnic group, and so on, then stratifying a sample is a great idea. (2) If differences are small, then stratifying just adds unnecessary work. (3) If you are uncertain about the independent variables that could be at work in affecting your dependent variable, then leave well enough alone and don’t stratify the sample. You can always stratify the data you collect and test various stratification schemes in the analysis instead of in the sampling.

Disproportionate Sampling

Disproportionate stratified random sampling is appropriate whenever an important subpopulation is likely to be underrepresented in a simple random sample or in a stratified random sample. Suppose you are doing a study of factors affecting grade-point averages among college students. You suspect that the independent variable called ‘‘race’’ is, in some way, associated with the dependent variable.

Suppose further that 5% of the student population is African American and that you have time and money to interview 400 students out of the population of 8,000. If you took 10,000 samples of 400 each from the population (replacing the 400 each time), then the average number of African Americans in all the samples would approach 20—that is, 5% of the sample.

But you are going to take one sample of 400. It might contain exactly 20 (5%) African Americans; on the other hand, it might contain just 5 (1.25%) African Americans. To ensure that you have enough data on African American students and on white students, you put the African Americans and the Whites into separate strata and draw two random samples of 200 each. The African Americans are disproportionately sampled by a factor of 10 (200 instead of the expected 20).

Native Americans comprise just 1.3% of the population of the United States. If you take 1,000 samples of 1,000 Americans at random, you expect to run into about 13 Native Americans, on average, across all the samples. (Some samples will have no Native Americans and some may have 20, but on average you’ll get about 13.) Without disproportionate sampling, Native Americans would be underrepresented in any national survey in the United States. When Sugarman et al. (1994) ran the National Maternal and Infant Health Survey in 1988, they used birth certificates dated July 1–December 31, 1988, from 35

Native American health centers as their sampling frame and selected 1,480 eligible mothers for the study of maternal and infant health in that population.

Weighting Results

One popular method for collecting data about daily activities is called experience sampling (Csikszentmihalyi and Larson 1987; Hektner et al. 2007). You give a sample of people a beeper or a cell phone. They carry it around and you beep or call them at random times during the day. They fill out a little form (either on paper or on a PDA) about what they’re doing at the time. (We’ll look more closely at this method in chapter 14.)

Suppose you want to contrast what people do on weekends with what they do during the week. If you beep people, say, eight times during each day, you’ll wind up with 40 reports for each person for the 5-day workweek but only 16 forms for each person for each 2-day weekend because you’ve sampled the two strata—weekdays and weekends— proportionately.

If you want more data points for the weekend, you might beep people 12 times on Saturday and 12 times on Sunday. That gives you 24 data points, but you’ve disproportionately sampled one stratum. The weekend represents 2/7, or 28.6% of the week, but you’ve got 64 data points and 24 of them, or 37.5%, are about the weekend. Before comparing any data across the strata, you need to make the weekend data and the weekday data statistically comparable.

This is where weighting comes in. Multiply each weekday data point by 1.50 so that the 40 data points become worth 60 and the 24 weekend data points are again worth exactly 2/7 of the total.

You should also weight your data when you have unequal response rates in a stratified sample. Suppose you sample 200 farmers and 200 townspeople in a rural African district where 60% of the families are farmers and 40% are residents of the local town. Of the 400 potential informants, 178 farmers and 163 townspeople respond to your questions. If you compare the answers of farmers and townspeople on a variable, you’ll need to weight each farmer’s data by 178/163  1.09 times each herder’s data on that variable. That takes care of the unequal response rates.

Then, you’ll need to weight each farmer’s data as counting 1.5 times each townsperson’s data on the variable. That takes care of the fact that there are half again as many farmers as there are people living in town. Weighting is a simple procedure available in all major statistical analysis packages.

CLUSTER SAMPLING AND COMPLEX SAMPLING DESIGNS

Cluster sampling is based on the fact that people act out their lives in more or less natural groups, or ‘‘clusters,’’ like geographic areas (counties, precincts, states), and institutions (like schools, churches, brotherhoods, credit unions, and so on). By sampling from these clusters, we narrow the sampling field from large, heterogeneous chunks to small, homogeneous ones that are relatively easy to find. This minimizes travel time in reaching scattered units of data collection. It also lets you sample populations for which there are no convenient lists or frames.

For example, there are no lists of schoolchildren in large cities, but children cluster in schools. There are lists of schools, so you can take a sample of them, and then sample children within each school selected.

Laurent et al. (2003) wanted to assess the rate of sexually transmitted diseases among unregistered female sex workers in Dakar, Senegal. By definition, unregistered means no list, so the researchers used a two-stage cluster sample. They created a sampling frame of all registered and all clandestine bars in Dakar, plus all the unregistered brothels, and all the nightclubs. They did this over a period of several months with the help of some women prostitutes, some local physicians who had treated those women, and two social workers, each of whom had worked with female sex workers for over 25 years. Laurent et al. calculated that they needed 94 establishments, so they chose a simple random of places from the list of 183. Then they went in teams to each of the 94 places and interviewed all the unregistered prostitutes who were there at the time of the visit.

Anthony and Suely Anderson (1983) wanted to compare people in Bacabal County, Brazil, who exploited the babassu palm with those who didn’t. There was no list of households, but they managed to get a list of the 344 named hamlets in the county. They divided the hamlets into those that supplied whole babassu fruits to new industries in the area and those that did not. Only 10.5% of the 344 hamlets supplied fruits to the industries, so the Andersons selected 10 hamlets randomly from each group for their survey. In other words, in the first stage of the process they stratified the clusters and took a disproportionate random sample from one of the clusters.

Next, they did a census of the 20 hamlets, collecting information on every household and particularly whether the household had land or was landless. At this stage, then, they created a sampling frame (the census) and stratified the frame into landowning and landless households. Finally, they selected 89 landless households randomly for interviewing. This was 25% of the stratum of landless peasants. Since there were only 61 landowners, they decided to interview the entire population of this stratum.

PROBABILITY PROPORTIONATE TO SIZE

The best estimates of a parameter are produced in samples taken from clusters of equal size. When clusters are not equal in size, then samples should be taken PPS—with probability proportionate to size.

Suppose you had money and time to do 800 household interviews in a city of 50,000 households. You intend to select 40 blocks, out of a total of 280, and do 20 interviews in each block. You want each of the 800 households in the final sample to have exactly the same probability of being selected.

Should each block be equally likely to be chosen for your sample? No, because census blocks never contribute equally to the total population from which you will take your final sample. A block that has 100 households in it should have twice the chance of being chosen for 20 interviews as a block that has 50 households and half the chance of a block that has 200 households.

When you get down to the block level, each household on a block with 100 residences has a 20% (20/100) chance of being selected for the sample; each household on a block with 300 residences has only a 6.7% (20/300) chance of being selected.

Lene´ Levy-Storms wanted to talk to older Samoan women in Los Angeles County about mammography. The problem was not that women were reticent to talk about the subject. The problem was how do you find a representative sample of older Samoan women in Los Angeles County?

From prior ethnographic research, Levy-Storms knew that Samoan women regularly attend churches where the minister is Samoan. She went to the president of the Samoan Federation of America in Carson, California, and he suggested nine cities in L.A. County where Samoans were concentrated. There were 60 churches with Samoan ministers in the nine cities, representing nine denominations. Levy-Storms asked each of the ministers to estimate the number of female church members who were over 50 years old. Based on these estimates, she chose a PPS sample of 40 churches (so that churches with more or fewer older women were properly represented). This gave her a sample of 299 Samoan women over 50. This clever sampling strategy really worked: Levy-Storms contacted the 299 women and wound up with 290 interviews—a 97% cooperation rate (Levy-Storms and Wallace 2003).

PPS sampling is called for under three conditions: (1) when you are dealing with large, unevenly distributed populations (such as cities that have high-rise and single-family neighborhoods); (2) when your sample is large enough to withstand being broken up into a lot of pieces (clusters) without substantially increasing the sampling error; and (3) when you have data on the population of many small blocks in a population and can calculate their respective proportionate contributions to the total population.

PPS Samples in the Field

What do you do when you don’t have neat clusters and neat sampling frames printed out on a computer by a reliable government agency? The answer is to place your trust in randomness and create maximally heterogeneous clusters from which to take a random sample.

Draw or get a map of the area you are studying. Place 100 numbered dots around the edge of the map. Try to space the numbers equidistant from one another, but don’t worry if they are not. Select a pair of numbers at random and draw a line between them. Now select another pair of numbers (be sure to replace the first pair before selecting the second) and draw a line between them. In the unlikely event that you choose the same pair twice, simply choose a third pair. Keep doing this, replacing the numbers each time. After you’ve drawn about 50 lines, you can begin sampling.

Notice that the lines drawn across the map in figure 5.1 create a lot of wildly uneven spaces. Because you don’t know the distribution of population density in the area you are studying, this technique maximizes the chance that you will properly survey the population, more or less PPS. By creating a series of (essentially) random chunks of different sizes, you distribute the error you might introduce by not knowing the density, and that distribution lowers the possible error.

FIGURE 5.1. Creating maximally heterogeneous sampling clusters in the field.

Number the uneven spaces created by the lines and choose some of them at random. Go to those spaces, number the households, and select an appropriate number at random. Remember, you want to have the same number of households from each made-up geographic cluster, no matter what its size. If you are doing 400 interviews, you would select 20 geographic chunks and do 20 interviews or behavioral observations in each.

My colleagues and I used this method in 1986 to find out how many people in Mexico City knew someone who died in that city’s monster earthquake the year before (Bernard et al. 1989). Instead of selecting households, though, my interview team went to each geographic chunk we’d selected and stopped the first 10 people they ran into on the street at each point. This is called a street-intercept survey (box 5.3).

BOX 5.3

S T R E E T - A N D M A L L - I N T E R C E P T S A M P L I N G

K. W. Miller et al. (1997) sampled blocks of streets in a city and did a streetintercept survey of African American men. They compared the results to a random-digit dialing telephone survey in the same city. The street-intercept survey did a better job of representing the population than did the telephone survey. For one thing, the response rate for the street intercept survey was over 80%. Compare that to the typical telephone survey, where half or more of the respondents may refuse to be interviewed. Also, with telephone surveys, the socioeconomic profile of respondents is generally higher than in the population (partly because more affluent people agree more often to be interviewed on the telephone). A variant of this method is mall-intercept sampling, used widely in marketing (Further Reading: street and mall intercept surveys).

Handwerker (1993) used a map-sampling method in his study of sexual behavior on Barbados. In his variation of map sampling, you generate 10 random numbers between 0 and 360 (the degrees on a compass). Next, put a dot in the center of a map that you will use for the sampling exercise, and use a protractor to identify the 10 randomly chosen compass points. You then draw lines from the dot in the center of the map through all 10 points to the edge of the map and interview people (or observe houses, or whatever) along those lines. (See Duranleau [1999] for an empirical test of the power of map sampling.)

If you use this technique, you may want to establish a sampling interval (like every fifth case, beginning with the third case). If you finish interviewing along the lines and don’t have enough cases, you can take another random start, with the same or a different interval and start again. Be careful of periodicity, though (box 5.4).

Camilla Harshbarger (1995) used another variation of map sampling in her study of farmers in North West Province, Cameroon (1995). To create a sample of 400 farmers, she took a map of a rural community and drew 100 dots around the perimeter. She used a random number table to select 50 pairs of dots and drew lines between them. She numbered the points created by the crossing of lines, and chose 80 of those points at

BOX 5.4

In chapter 4, I mentioned a study in which Lambros Comitas and I compared Greeks who had returned from what was then West Germany as labor migrants with Greeks who had never left their country (Bernard and Comitas 1978). There were no lists of returned migrants, but we thought we could do a cluster sample by locating the children of returned migrants in the Athens schools and then use the children to select a sample of their parents.

The problem was, we couldn’t even get a list of schools in Athens. So we took a map of the city and divided it into small bits by laying a grid over it. Then we took a random sample of the bits and sent interviewers to find the school nearest each bit selected. The interviewers asked the principal of each school to identify the children of returned labor migrants. (It was easy for the principal to do, by the way. The principal said that all the returned migrant children spoke Greek with a German accent.) That way, we were able to make up two lists for each school: one of children who had been abroad, and one of children who had not. By sampling children randomly from those lists at each school, we were able to select a representative sample of parents.

random. Then, Harshbarger and her field assistants interviewed one farmer in each of the five compounds they found closest to each of the 80 selected dots. (If you use this dot technique, remember to include the points along the edges of the map in your sample or you’ll miss households on those edges.)

There are times when a random, representative sample is out of the question. After Harshbarger did those interviews with 400 randomly selected farmers in North West Province, Cameroon, she set out to interview Fulani cattle herders in the same area. Here’s what Harshbarger wrote about her experience in trying to interview the herders:

It was rainy season in Wum and the roads were a nightmare. The grazers lived very far out of town and quite honestly, my research assistants were not willing to trek to the compounds because it would have taken too much time and we would never have finished the job. I consulted X and he agreed to call selected people to designated school houses on certain days. We each took a room and administered the survey with each individual grazer.

Not everyone who was called came for the interview, so we ended up taking who we could get. Therefore, the Wum grazer sample was not representative and initially that was extremely difficult for me to accept. Our team had just finished the 400-farmer survey of Wum that was representative, and after all that work it hit me hard that the grazer survey would not be. To get a representative sample, I would have needed a fourwheel drive vehicle, a driver, and more money to pay research assistants for a lengthy stay in the field. Eventually, I forgave myself for the imperfection. (personal communication)

The lessons here are clear: (1) If you are ever in Harshbarger’s situation, you, too, can forgive yourself for having a nonrepresentative sample. (2) Even then, like Harshbarger, you should feel badly about it (Further Reading: space sampling).

Maximizing Between-Group Variance: The Wichita Study

Whenever you do multistage cluster sampling, be sure to take as large a sample as possible from the largest, most heterogeneous clusters. The larger the cluster, the larger the between-group variance; the smaller the cluster, the smaller the between-group variance. Counties in the same state in the United States are more like each other for many variables—such as average income, distribution of racial and ethnic groups, average age, etc.—than states are. Towns within a county are more like each other than counties are; neighborhoods in a town are more like each other than towns are. And blocks within a neighborhood are more like each other than neighborhoods are. In sampling, the rule is: maximize between-group variance.

What does this mean in practice? Following is an actual example of multistage sampling from John Hartman’s study of Wichita, Kansas (Hartman 1978; Hartman and Hedblom 1979:160). At the time of the study, in the mid-1970s, Wichita had a population of about 193,000 persons over the age of 16. This was the population to which the study team wanted to generalize. The team decided that they could afford only 500 interviews. There are 82 census tracts in Wichita from which they randomly selected 20. These 20 tracts then became the actual population of their study. We’ll see in a moment how well their actual study population simulated (represented) the study population to which they wanted to generalize.

Hartman and Hedblom added up the total population in the 20 tracts and divided the population of each tract by the total. This gave the percentage of people that each tract, or cluster, contributed to the new population total. The researchers were going to do 500 interviews, so each tract was assigned that percentage of the interviews. If there were 50,000 people in the 20 tracts, and one of the tracts had a population of 5,000, or 10% of the total, then 50 interviews (10% of the 500) would be done in that tract.

Next, the team numbered the blocks in each tract and selected blocks at random until they had enough for the number of interviews that were to be conducted in that tract. When a block was selected it stayed in the pool, so in some cases more than one interview was to be conducted in a single block. This did not happen very often, and the team wisely left it up to chance to determine this.

This study team made some excellent decisions that maximized the heterogeneity (and hence the representativeness) of their sample. As clusters get smaller and smaller (as you go from tract to block to household, or from village to neighborhood to household), the homogeneity of the units of analysis within the clusters gets greater and greater. People in one census tract or village are more like each other than people in different tracts or villages. People in one census block or barrio are more like each other than people across blocks or barrios. And people in households are more like each other than people in households across the street or over the hill.

This is very important. Most researchers would have no difficulty with the idea that they should only interview one person in a household because, for example, husbands and wives often have similar ideas about things and report similar behavior with regard to kinship, visiting, health care, child care, and consumption of goods and services. Somehow, the lesson becomes less clear when new researchers move into clusters that are larger than households.

But the rule stands: Maximize heterogeneity of the sample by taking as many of the biggest clusters in your sample as you can, and as many of the next biggest, and so on, always at the expense of the number of clusters at the bottom where homogeneity is greatest. Take more tracts or villages and fewer blocks per tract or barrios per village. Take more blocks per tract or barrios per village and fewer households per block or barrio. Take more households and fewer persons per household.

Many survey researchers say that, as a rule, you should have no fewer than five households in a census block. The Wichita group did not follow this rule but only had enough money and person power to do 500 interviews and they wanted to maximize the likelihood that their sample would represent faithfully the characteristics of the 193,000 adults in their city.

The Wichita team drew two samples—one main sample and one alternate sample. Whenever they could not get someone on the main sample, they took the alternate. That way, they maximized the representativeness of their sample because the alternates were chosen with the same randomized procedure as the main respondents in their survey. They were not forced to take ‘‘next door-neighbors’’ when a main respondent wasn’t home. (This kind of winging it in survey research has a tendency to clobber the representativeness of samples. In the United States, at least, interviewing only people who are at home during the day produces results that represent women with small children, shutins, telecommuters, and the elderly—and not much else.)

Next, the Wichita team randomly selected the households for interview within each block. This was the third stage in this multistage cluster design. The fourth stage consisted of flipping a coin to decide whether to interview a man or a woman in households with both. Whoever came to the door was asked to provide a list of those in the household over 16 years of age. If there was more than one eligible person in the household, the interviewer selected one at random, conforming to the decision made earlier on sex of respondent.

Table 5.2 shows how well the Wichita team did. All in all, they did very well. In addition to the variables shown in the table here, the Wichita sample was a fair representation of marital status and occupation, though it was off a bit on education. For example, at the time, 8% of the population of Wichita had less than 8 years of schooling, but only 4% of the sample had this characteristic. Only 14% of the general population had completed from 1 to 2 years of college, but 22% of the sample had that much education.

Table 5.2 Comparison of Survey Results and Population Parameters for the Wichita Study by Hartman and Hedblom

	Wichita in 1973	Hartman and Hedblom's Sample for 1973
White	86.8%	82.8%
African	9.7%	10.8%
Chicano	2.5%	2.6%
Other	1.0%	2.8%
Male	46.6%	46.9%
Female	53.4%	53.1%
Median age	38.5	39.5

SOURCE: Methods for the Social Sciences: A Handbook for Students and Non-Specialists, by J. J. Hartman and J. H. Hedblom, 1979, p. 165. Reproduced with permission of Greenwood Publishing Group.

All things considered, though, the sampling procedure followed in the Wichita study was a model of technique, and the results show it. Whatever they found out about the

500 people they interviewed, the researchers could be very confident that the results were generalizable to the 193,000 adults in Wichita.

In sum: If you don’t have a sampling frame for a population, try to do a multistage cluster sample, narrowing down to natural clusters that do have lists. Sample heavier at the higher levels in a multistage sample and lighter at the lower stages (box 5.5).

BOX 5.5

M U L T I S T A G E C L U S T E R S A M P L I N G I N T H E F I E L D

Just in case you’re wondering if you can do this under difficult field conditions, Oyuela-Cacedo and Vieco-Albarracı´n (1999) studied the social organization of the Ticuna Indians of the Colombian Amazon. Most of the 9,500 Ticuna in Colombia are in 32 hamlets, along the Amazon, the Loreta Yacu, the Cotuhe´, and the Putumayo Rivers. The Ticuna live in large houses that comprise from one to three families, including grandparents, unmarried children, and married sons with their wives and children. To get a representative sample of the Ticuna, Oyuela-Cacedo and Vieco-Albarracı´n selected six of the 32 hamlets along the four rivers and made a list of the household heads in those hamlets. Then, they numbered the household heads and randomly selected 50 women and 58 men. Oyuela-Cacedo and Vieco-Albarracı´n had to visit some of the selected houses several times to secure an interview, but they wound up interviewing all the members of their sample.

Is the sample representative? We can’t know for sure, but take a look at figure 5.2. Figure 5.2a shows the distribution of the ages of the household heads in the sample; figure 5.2b shows the distribution of the number of children in the households of the sample. Both curves look very normal—just what we expect from variables like age and number of children (more about normal distributions in chapter 6). If the sample of Ticuna household heads represents what we expect from age and number of children, then any other variables the research team measured are likely (not guaranteed, just likely) to be representative, too.

HOW BIG SHOULD A SAMPLE BE?

There are two things you can do to get good samples. (1) You can ensure sample accuracy by making sure that every element in the population has an equal chance of being selected—that is, you can make sure the sample is unbiased. (2) You can ensure sample precision by increasing the size of unbiased samples. We’ve already discussed the importance of how to make samples unbiased. The next step is to decide how big a sample needs to be.

Sample size depends on: (1) the heterogeneity of the population or chunks of population (strata or clusters) from which you choose the elements; (2) how many population subgroups (that is, independent variables) you want to deal with simultaneously in your analysis; (3) the size of the phenomenon that you’re trying to detect; and (4) how precise you want your sample statistics (or parameter estimators) to be.

1. Heterogeneity of the population. When all elements of a population have the same score on some measure, a sample of 1 will do. Ask a lot of people to tell you how many days there are in a week and you’ll soon understand that a big sample isn’t going to uncover a lot of heterogeneity. But if you want to know what the average ideal family size is, you may need to cover a lot of social ground. People of different ethnicities, religions, incomes, genders, and ages may have very different ideas about this. (In fact, these independent variables may interact in complex ways. Multivariate analysis tells you about this interaction. We’ll get to this in chapter 22.)

FIGURE 5.2a. Distribution of the ages of Ticuna household heads. SOURCE: Adapted from data in A. Oyuela-Cacedo and J. J. Vieco Albarracı´n, ‘‘Approximacio´ n cuantitativa a la organizacio´ n social de los Ticuna del trapecio amazo´ nico colombiano,’’ Revista Colombiana de Antropologı´a, Vol. 35, pp. 146–79, figure 1, p. 157, 1999.

FIGURE 5.2b. Distribution of the number of children in Ticuna households. SOURCE: Adapted from data in A. Oyuela-Cacedo and J. J. Vieco Albarracı´n, ‘‘Approximacio´ n cuantitativa a la organizacio´ n social de los Ticuna del trapecio amazo´ nico colombiano,’’ Revista Colombiana de Antropologı´a, Vol. 35, pp. 146–79, table 6, p. 159, 1999.

2. The number of subgroups in the analysis. Remember the factorial design problem in chapter 4 on experiments? We had three independent variables, each with two attributes, so we needed eight groups $( 2 ^ { 3 } = 8 )$ . It wouldn’t do you much good to have, say, one experimental subject in each of those eight groups. If you’re going to analyze all eight of the conditions in the experiment, you’ve got to fill each of the conditions with some reasonable number of subjects. If you have only 15 people in each of the eight conditions, then you need a sample of 120.

The same principle holds when you’re trying to figure out how big a sample you need for a survey. If you have four age groups and two genders, you wind up with an eightcell sampling design.

If all you want to know is a single proportion—like what percentage of people in a population approve or disapprove of something—then you need about 100 respondents to be 95% confident, within plus or minus 3 points, that your sample estimate is within 2 standard deviations of the population parameter (more about confidence limits, normal distributions, standard deviations, and parameters in a minute). But if you want to know whether women factory workers in Rio de Janeiro who earn less than $300 per month have different opinions than, say, middle-class women in Rio whose family income is more than $600 per month, then you’ll need a bigger sample.

3. The size of the subgroup. If the population you are trying to study is rare and hard to find, and if you have to rely on a simple random sample of the entire population, you’ll need a very large initial sample. A needs assessment survey of people over 75 in Florida took 72,000 phone calls to get 1,647 interviews—about 44 calls per interview (Henry 1990:88). This is because only 6.5% of Florida’s population was over 75 at the time of the survey. By contrast, the monthly Florida survey of 600 representative consumers takes about 5,000 calls (about eight per interview). That’s because just about everyone in the state 18 and older is a consumer and is eligible for the survey. [Christopher McCarty, personal communication]

The smaller the difference on any measure between two populations, the bigger the sample you need to detect that difference. Suppose you suspect that Blacks and Whites in a prison system have received different sentences for the same crime. Henry (1990:121) shows that a difference of 16 months in sentence length for the same crime would be detected with a sample of just 30 in each racial group (if the members of the sample were selected randomly, of course). To detect a difference of 3 months, however, you need 775 in each group.

4. Precision. This one takes us into sampling theory.

FURTHER READING

Street intercept surveys: Ross et al. (2006); Waltermaurer et al. (2003).

Mall-intercept survey: Bruwer and Haydam (1996); Bush and Hair (1985); Gates and Solomon

(1982); Hornik and Ellis (1988); Wang and Heitmeyer (2006).

Space sampling: Daley et al. (2001); Lang et al. (2004).

Sampling II: Theory

DISTRIBUTIONS

At the end of this chapter, you should understand why it’s possible to estimate very accurately, most of the time, the average age of the 228 million adults in the United States by talking to just 1,600 of them. And you should understand why you can also do this pretty accurately, much of the time, by talking to just 400 of them. Sampling theory is partly about distributions, which come in a variety of shapes. Figure 6.1 shows what is known as the normal distribution.

FIGURE 6.1.

The normal curve and the first, second, and third standard deviations.

THE NORMAL CURVE AND Z-SCORES

The so-called normal distribution is generated by a formula that can be found in many intro statistics texts. The distribution has a mean of 0 and a standard deviation of 1. The standard deviation is a measure of how much the scores in a distribution vary from the mean score. The larger the standard deviation, the more dispersion around the mean. Here’s the formula for the standard deviation, or sd. (We will take up the sd again in chapter 20. The sd is the square root of the variance, which we’ll take up in chapter 21.)

$$ \mathrm{sd} = \sqrt {\frac {\sum (x - \bar {x}) ^ {2} }{n - 1} }\tag{Formula 6.1} $$

The symbol x¯ in formula 6.1 is read ‘‘x-bar’’ and is used to signify the mean of a sample. The mean of a population (the parameter we want to estimate), is symbolized by μ (the Greek lower-case letter ‘‘mu,’’ pronounced ‘‘myoo’’). The standard deviation of a population is symbolized by σ (the Greek lower-case letter ‘‘sigma’’), and the standard deviation of a sample is written as SD or sd or s. Read formula 6.1 as follows: The standard deviation is the square root of the sum of all the squared differences between every score in a set of scores and the mean, divided by the number of scores minus 1.

The standard deviation of a sampling distribution of means is the standard error of the mean, or SEM. The formula for calculating SEM is:

$$ S E M \frac {s d}{\sqrt {n} } $$

Formula 6.2

where n is the sample size. In other words, the standard error of the mean gives us an idea of how much a sample mean varies from the mean of the population that we’re trying to estimate.

Suppose that in a sample of 100 merchants in a small town in Malaysia, you find that the average income is RM12,600 (about $3,500 in 2009 U.S. dollars), with a standard deviation of RM4,000 (RM is the symbol for the Malaysian Ringgit). The standard error of the mean is:

$$ 1 2, 6 0 0 \pm \frac {4 0 0 0}{\sqrt {1 0 0} } = 1 2, 6 0 0 \pm 4 0 0 $$

Do the calculation:

$$ \begin{array}{l} 1 2, 6 0 0 + 4 0 0 = 1 3, 0 0 0 \ 1 2, 6 0 0 - 4 0 0 = 1 2, 2 0 0 \end{array} $$

In normal distributions—that is, distributions that have a mean of 0 and a standard deviation of 1—exactly 34.135% of the area under the curve (the white space between the curve and the baseline) is contained in between the perpendicular line that represents the mean in the middle of the curve in figure 6.1 and the line that rises from the baseline at 1 standard deviation above and 1 standard deviation below the mean.

Appendix A is a table of z-scores, or standard scores. These scores are the number of standard deviations from the mean in a normal distribution, in increments of 1/100th of a standard deviation. For each z-score, beginning with 0.00 standard deviations (the mean) and on up to 3.09 standard deviations (on either side of the mean), appendix A shows the percentage of the physical area under the curve of a normal distribution. That percentage represents the percentage of cases that fall within any number of standard deviations above and below the mean in a normally distributed set of cases.

We see from appendix A that 34.13% of the area under the curve is one standard deviation above the mean and another 34.13% is one standard deviation below the mean. Thus, 68.26% of all scores in a normal distribution fall within one standard deviation of the mean. We also see from appendix A that 95.44% of all scores in a normal distribution fall within two standard deviations and that 99.7% fall within three standard deviations.

Look again at figure 6.1. You can see why so many cases are contained within 1 sd above and below the mean: The normal curve is tallest and fattest around the mean and much more of the area under the curve is encompassed in the first sd from the mean than is encompassed between the first and second sd from the mean.

If 95.44% of the area under a normal curve falls within two sd from the mean, and if 99.7% fall within 3 sd, then exactly 95% (a nice, round number) should fall within slightly less than two and exactly 99% should fall within slightly less than three standard deviations. And indeed, from appendix A, we see that 1.96 standard deviations above and below the mean account for 95% of all scores in a normal distribution and that 2.58 sd account for 99% of all scores. This, too, is shown in figure 6.1.

The normal distribution is an idealized form. In practice, many variables are not distributed in the perfectly symmetric shape we see in figure 6.1. Figure 6.2 shows some other shapes for distributions. Figure 6.2a shows a bimodal distribution. Suppose the xaxis in figure 6.2a is age, and the y-axis is the percentage of people who respond ‘‘yes’’ to the question ‘‘Did you like the beer commercial shown during the Superbowl yesterday?’’ The bimodal distribution shows that people in their 20s and people in their 60s liked the commercial, but others didn’t.

a. Bimodal distribution

FIGURE 6.2. b. Skewed to the right

c. Skewed to the left Bimodal and skewed distributions.

Figure 6.2b and figure 6.2c are skewed distributions. A distribution can be skewed positively (with a long tail going off to the right) or negatively (with the tail going off to the left). Figures 6.2b and 6.2c look like the distributions of scores in two very different university courses. In figure 6.2b, most students got low grades, and there is a long tail of students who got high grades. In figure 6.2c, most students got relatively high grades, and there is a long tail of students who got lower grades.

a. A leptokurtic distribution

b. A normal distribution

c. A platykurtic distribution FIGURE 6.3. Three symmetric distributions including the normal distribution.

The normal distribution is symmetric, but not all symmetric distributions are normal. Figure 6.3 shows three variations of a symmetric distribution—that is, distributions for which the mean and the median are the same. The one on the left is leptokurtic (from Greek, meaning ‘‘thin bulge’’) and the one on the right is platykurtic (meaning ‘‘flat bulge’’). The curve in the middle is the famous bell-shaped, normal distribution. In a leptokurtic, symmetric distribution, the standard deviation is less than 1.0; and in a platykurtic, symmetric distribution, the standard deviation is greater than 1.0. The physical distance between marriage partners (whether among tribal people or urbanites) usually forms a leptokurtic distribution. People tend to marry people who live near them, and there are fewer and fewer marriages as the distance between partners increases (Sheets 1982). By contrast, we expect the distribution of height and weight of athletes in the

National Basketball Association to be more platykurtic across teams since coaches are all recruiting players of more-or-less similar build.

The shape of a distribution—normal, skewed, bimodal, and so on—contains a lot of information about what is going on, but it doesn’t tell us why things turned out the way they did. A sample with a bimodal or highly skewed distribution is a hint that you might be dealing with more than one population or culture.

THE CENTRAL LIMIT THEOREM

The fact that many variables are not normally distributed would make sampling a hazardous business, were it not for the central limit theorem. According to this theorem, if you take many samples of a population, and if the samples are big enough, then:

1. The mean and the standard deviation of the sample means will usually approximate the true mean and standard deviation of the population. (You’ll understand why this is so a bit later in the chapter, when we discuss confidence intervals.)

2. The distribution of sample means will approximate a normal distribution.

We can demonstrate both parts of the central limit theorem with some examples.

Part 1 of the Central Limit Theorem

Table 6.1 shows the per capita gross domestic product (PCGDP) for the 50 poorest countries in the world in 2007.

Here is a random sample of five of those countries: Uzbekistan, Senegal, Guinea, Rwanda, and Liberia. Consider these five as a population of units of analysis. In 2007, these countries had an annual per capita GDP, respectively of $704, $908, $452, $354, and $195 (U.S. dollars). These five numbers sum to $2,613 and their average, 2613/5, is $522.60.

There are 10 possible samples of two elements in any population of five elements. All 10 samples for the five countries in our example are shown in the left-hand column of table 6.2. The middle column shows the mean for each sample. This list of means is the sampling distribution. And the right-hand column shows the cumulative mean.

Notice that the mean of the means for all 10 samples of two elements—that is, the mean of the sampling distribution—is $522.60, which is exactly the actual mean per capita GDP of the five countries in the population. In fact, it must be: The mean of all possible samples of size 2 is equal to the parameter that we’re trying to estimate.

Figure 6.4 (left) is a frequency polygon that shows the distribution of the five actual GDP values. A frequency polygon is just a histogram with lines connecting the tops of the bars so that the shape of the distribution is emphasized. Compare the shape of this distribution to the one in figure 6.4 (right) showing the distribution of the 10 sample means for the five GDP values we’re dealing with here. That distribution looks more like the shape of the normal curve: It’s got that telltale bulge in the middle.

Part 2 of the Central Limit Theorem

Figure 6.5 shows the distribution of the 50 data points for GDP in table 6.1. The range is quite broad, from $118 to $978 per year per person, and the shape of the distribution is multimodal.

The actual mean of the data in table 6.1—that is, the parameter we want to estimate—is $533.28. There are 2,118,760 samples of size 5 that can be taken from 50 elements. Table 6.3 shows the means from 10 samples of five countries chosen at random from the data in table 6.1.

Table 6.1 Per Capita Gross Domestic Product (PCGDP) in U.S. Dollars for the 50 Poorest Countries in the World, 200

Country	PCGDP	Country	PCGDP
Burundi	118	Burkina Faso	483
DR-Congo	151	Mali	554
Zimbabwe	159	Tajikistan	555
Liberia	195	Comoros	556
Ethiopia	201	Cambodia	598
Guinea-Bissau	211	Haiti	612
Malawi	257	Benin	618
Eritrea	271	N. Korea	618
Niger	289	Ghana	647
Somalia	291	Chad	692
Sierra Leone	330	Kyrgyzstan	704
Afghanistan	345	Uzbekistan	704
Rwanda	354	Laos	711
Mozambique	362	Kiribati	762
Tanzania	368	Kenya	786
Gambia	377	Lesotho	797
Madagascar	377	Viet Nam	815
Myanmar	379	Mauritania	874
Togo	386	Senegal	908
Timor-Leste	393	Sao Tome and Principe	912
Central African Rep.	394	Papua New Guinea	953
Uganda	403	Yemen	967
Nepal	419	Zambia	974
Bangladesh	428	India	976
Guinea	452	Solomon Islands	978

SOURCE: United Nations, Dept. of Economic and Social Affairs, Economic and Social Development. http:// unstats.un.org/unsd/demographic/products/socind/inc-eco.htm.

Table 6.2 All Samples of Two from Five Elements

Sample	Mean	Cumulative mean
Uzbekistan and Senegal	(704 + 908)/2 = 806.0	806.0
Uzbekistan and Guinea	(704 + 452)/2 = 578.0	1,384.0
Uzbekistan and Rwanda	(704 + 354)/2 = 529.0	1,913.0
Uzbekistan and Liberia	(704 + 195)/2 = 449.5	2,362.5
Senegal and Guinea	(908 + 452)/2 = 680.0	3,042.5
Senegal and Rwanda	(908 + 354)/2 = 631.0	3,673.5
Senegal and Liberia	(908 + 195)/2 = 551.5	4,225.0
Guinea and Rwanda	(452 + 354)/2 = 403.0	4,628.0
Guinea and Liberia	(452 + 195)/2 = 323.5	4,951.5
Liberia and Rwanda	(195 + 354)/2 = 274.5	5,226.0
	$\bar{x} = 5,226/10 = 522.6$

Even in this small set of 10 samples, the mean is $504.72—quite close to the actual mean of $533.28. Figure 6.6 (left) shows the distribution of these samples. It has the look of a normal distribution straining to happen. Figure 6.6 (right) shows 20 samples of five from the 50 countries in table 6.1. The strain toward the normal curve is unmistakable and the mean of those 20 samples is $505.18.

The problem is that in real research, we don’t get to take 10 or 20 samples. We have to make do with one. The first sample of five elements that I took had a mean of $522.60—pretty close to the actual mean of $533.28. But it’s very clear from table 6.3 that any one sample of five elements from table 6.1 could be off by a lot. They range, after all, from $434.40 to $652.80. That’s a very big spread, when the real average we’re trying to estimate is $533.28. Still, as you can see from figure 6.6, as we add samples, the mean of the samples gets closer and closer to the parameter we’re trying to estimate and the distribution of the means of the samples looks more and more like the normal distribution.

FIGURE 6.4.

Five cases and the distribution of samples of size 2 from those cases.

FIGURE 6.5. The distribution of the 50 data points for GDP in table 6.1.

Table 6.3 10 Means from Samples of Size 5 Taken from the 50 Elements in Table 6.1

522.60	652.80
434.40	461.20
586.20	489.20
468.20	458.60
465.00	509.00

Mean  504.72 Standard Deviation  67.51

We are much closer to answering the question: How big does a sample have to be?

THE STANDARD ERROR AND CONFIDENCE INTERVALS

In the hypothetical example on page 131 we took a sample of 100 merchants in a Malaysian town and found that the mean income was RM12,600, standard error 400. We know from figure 6.1 that 68.26% of all samples of size 100 from this population will produce an estimate that is between 1 standard error above and 1 standard error below the mean— that is, between RM12,200 and RM13,000. The 68.26% confidence interval, then, is $400.

We also know from figure 6.1 that 95.44% of all samples of size 100 will produce an estimate of 2 standard errors, or between RM13,400 and RM11,800. The 95.44% confidence interval, then, is RM800. If we do the sums for the example, we see that the 95% confidence limits are:

$$ \mathrm{RM} 1 2, 6 0 0 \pm 1. 9 6 (\mathrm{RM} 4 0 0) = \mathrm{RM} 1 1, 8 1 6 \text { to } \mathrm{RM} 1 3, 3 8 4 $$

and the 99% confidence limits are:

$$ \mathrm{RM} 1 2, 6 0 0 \pm 2. 5 8 (\mathrm{RM} 4 0 0) = \mathrm{RM} 1 1, 5 6 8 \text { to } \mathrm{RM} 1 3, 6 3 2 $$

Our ‘‘confidence’’ in these 95% or 99% estimates comes from the power of a random sample and the fact that—by the central limit theorem—sampling distributions are known to be normal irrespective of the distribution of the variable whose mean we are estimating.

FIGURE 6.6.

Visualizing the central limit theorem: The distribution of sample means approximates a normal distribution. Means for 10 (left) and 20 (right) samples of 5 from the 50 GDP values in table 6.1.

What Confidence Limits Are and What They Aren’t

If you say that the 95% confidence limits for the estimated mean income are RM11,816–13,384, this does not mean that there is a 95% chance that the true mean, μ, lies somewhere in that range. The true mean may or may not lie within that range and we have no way to tell. What we can say, however, is that:

1. If we take a very large number of suitably large random samples from the population (we’ll get to what ‘‘suitably large’’ means in a minute); and

2. If we calculate the mean, x¯, and the standard error, SE, for each sample; and

3. If we then calculate the confidence intervals for each sample mean, based on 1.96 SE; then

4. 95% of these confidence intervals will contain the true mean, μ.

Calculating Sample Size for Estimating Means

Now we are really close to answering the question about sample size. Suppose we want to get the standard error down to RM200 instead of RM400. We need to solve the following equation:

$$ S E \frac {s d}{\sqrt {n} } = 4 0 0 0 / \sqrt {n} = 2 0 0 $$

Solving for n:

$$ \sqrt {n} = \frac {4 0 0 0}{2 0 0} = 2 0 \quad n = 2 0 ^ {2} = 4 0 0 $$

In other words, to reduce the standard error of the mean from RM400 to RM200, we have to increase the sample size from 100 to 400 people.

Suppose we increase the sample to 400 and we still get a mean of RM12,600 and a standard deviation of RM4000. The standard error of the mean would then be RM200, and we could estimate, with 95% confidence, that the true mean of the population was between RM12,208 and 12,992. With just 100 people in the sample, the 95% confidence limits were RM11,816–13,384. As the standard error goes down, we get narrower—that is, more precise—confidence limits.

Let’s carry this forward another step. If we wanted to get the standard error down to RM100 and the 95% confidence interval down to RM200 from RM400, we would need a sample of 1,600 people. There is a pattern here. To cut the 95% confidence interval in half, from RM800 to RM400, we had to quadruple the sample size from 100 to 400. To cut the interval in half again, to RM200, we’d need to quadruple the sample size again, from 400 to 1,600.

There is another pattern, too. If we want to increase our confidence from 95% to 99% that the true mean of the population is within a particular confidence interval, we can raise the multiplier in formula 6.2 from roughly 2 standard deviations to roughly 3. Using the confidence interval of RM400, we would calculate:

$$ \sqrt {n} = 3 \left(\frac {4 0 0 0}{4 0 0}\right) = 3 0 \quad n = 3 0 ^ {2} = 9 0 0 $$

We need 900 people, not 400, to be about 99% confident that our sample mean is within RM400, plus or minus, of the parameter.

SMALL SAMPLES: THE t-DISTRIBUTION

In anthropology, even doing surveys, we often have no choice about the matter and have to use small samples.

What we need is a distribution that is a bit more forgiving than the normal distribution. Fortunately, just such a distribution was discovered by W. S. Gossett, an employee of the Guinness brewery in Ireland. Writing under the pseudonym of ‘‘Student,’’ Gossett described the distribution known as Student’s t. It is based on a distribution that takes into account the fact that statistics calculated on small samples vary more than do statistics calculated on large samples and so have a bigger chance of misestimating the parameter of a continuous variable.

FIGURE 6.7. Variability in a t distribution and a normal distribution.

The t distribution is found in appendix B. Figure 6.7 shows graphically the difference in the two distributions. In a normal distribution, plus or minus 1.96 sd covers 95% of all sample means. In a t-distribution, with 5 degrees of freedom, it takes 2.571 sd to cover 95% of all sample means.

The confidence interval for small samples, using the t distribution is given in formula 6.3:

$$ \text { Confidence Interval } = \bar {x} \pm (t _ {\alpha / 2}) \left[ \frac {s d}{\sqrt {n} } \right]\tag{Formula 6.3} $$

where alpha (α) is the confidence interval you want. If you want to be 95% confident, then $\mathrm { ~ a ~ } = \mathrm { ~ . 0 5 ~ }$ . Since half the scores fall above the mean and half below, we divide alpha by two and get .025.

Look up what’s called the critical value of t in appendix B. In the column for .025, we see that the value is 2.571 with 5 degrees of freedom. Degrees of freedom are one less than the size of the sample, so for a sample of six we need a t statistic of 2.571 to attain 95% confidence. (The concept of degrees of freedom is described further in chapter 20 in the section on t-tests. And keep in mind that we’re interested in the modulus, or absolute value of t. A value of 2.571 is just as statistically significant as a value of 2.571.)

Thus, with small samples—which, for practical purposes, means less than 30 units of analysis—we use appendix B (for t) instead of appendix A (for z) to determine the confidence limits around the mean of our estimate. You can see from appendix B that for large samples—30 or more—the difference between the t and the z statistics is negligible. (The t-value of 2.042 for 30 degrees of freedom—which means a sample of 31—is very close to 1.96.)

The Catch

Suppose that instead of estimating the income of a population with a sample of 100, we use a sample of 10 and get the same result—RM12,600 and a standard deviation of RM4000. For a sample this size, we use the t distribution. With 9 degrees of freedom and an alpha value of .025, we have a t value of 2.262. For a normal curve, 95% of all scores fall within 1.96 standard errors of the mean. The corresponding t value is 2.262 standard errors. Substituting in the formula, we get:

$$ \mathrm{RM} 1 2, 6 0 0 \pm 2. 2 6 2 \left(\frac {\mathrm{RM} 4 0 0}{\sqrt {1 0} }\right) = \mathrm{RM} 9, 7 3 9 \text { to } 1 5, 4 6 1 $$

But there’s a catch. With a large sample (greater than 30), we know from the central limit theorem that the sampling distribution will be normal even if the population isn’t. Using the t distribution with a small sample, we can calculate the confidence interval around the mean of our sample only under the assumption that the population is normally distributed.

In fact, looking back at figure 6.5, we know that the distribution of the real data is not perfectly normal. It is somewhat skewed (more about skewed distributions in chapter 20). In real research, we’d never take a sample from a set of just 50 data points—we’d do our calculations on the full set of the actual data. When we take samples, it’s because we don’t know what the distribution of the data looks like. And that’s why sample size counts.

CALCULATING SAMPLE SIZE FOR ESTIMATING PROPORTIONS

And now for proportions. What we’ve learned so far about estimating the mean of continuous variables (like income and percentages) is applicable to the estimation of proportions as well.

In April 2009, the ABC News/Washington Post poll reported that 41% of Americans over 18 years of age said they had one or more guns in their home. The poll included 1,072 respondents and had, as the media say, a ‘‘margin of sampling error of plus-orminus three percentage points.’’ The point estimate of 41% means that 440 of the 1,072 people polled said that they had at least one gun in their house.

We can calculate the confidence interval around this point estimate. From the central limit theorem, we know that whatever the true proportion of people is who keep a gun in their home, the estimates of that proportion will be normally distributed if we take a large number of samples of 1,072 people each. The formula for determining the 95% confidence limits of a point estimator is:

$$ P (\text { the true proportion }) = \pm 1. 9 6 \sqrt {\mathrm{PQ} / n} $$

Formula 6.4

We use an italicized letter, P, to indicate the true proportion. Our estimate is the regular upper-case P and Q is 1–P. Table 6.4 shows what happens to the square root of PQ as the true value of $P$ goes up from 10% to 90% of the population.

Table 6.4 Relation of P and Q and $\sqrt { \mathsf { P O } }$

If the value of P is really	Then PQ is	and $\sqrt{PQ}$ is
.10 or .90	.09	.30
.20 or .80	.16	.40
.30 or .70	.21	.46
.40 or .60	.24	.49
.50	.25	.50

We can use our own estimate of P in the equation for the confidence limits. Substituting .41 for P and .59 (1–.41) for Q, we get:

$$ P = \mathrm{P} \pm 1. 9 6 \sqrt {(. 4 1) (. 5 9) / 1 0 7 2} = . 0 2 9 4 4 $$

which, with rounding error, is the familiar ‘‘plus or minus three percentage points.’’ This means that we are 95% confident that the true proportion of adults in the United States who had at least one gun in their home (or at least said they did) at the time this poll was conducted was between 38% and 44%.

Suppose we want to estimate P to within plus-or-minus 2 percentage points instead of 3 and we still want to maintain the 95% confidence level. We substitute in the formula as follows:

$$ P = \mathrm{P} \pm 1. 9 6 \sqrt {(. 4 1) (. 5 9) / n} = . 0 2 $$

and we solve for n:

$$ \begin{array}{c} n = 1. 9 6 ^ {2} (. 4 1) (. 5 9) /. 0 2 ^ {2} \ n = (3. 8 4 2) (. 4 1) (. 5 9) /. 0 0 0 4 = 2, 3 2 4 \end{array} $$

Generalizing, then, the formula for ‘‘sample size when estimating proportions in a large population’’ is:

$$ n = z ^ {2} (\mathrm{P}) (\mathrm{Q}) / (\text { confidence interval }) ^ {2}\tag{Formula 6.5} $$

where z is the area under the normal curve that corresponds to the confidence level we choose. When the confidence level is 95%, then z is 1.96. When the confidence level is 99%, then z is 2.58. And so on.

If we start out fresh and have no prior estimate of P, we follow table 6.4 and set P and Q to .5 each. This maximizes the size of the sample for any given confidence interval or confidence level. If we want a sample that produces an estimate of a proportion with a confidence interval of 2 percentage points and we want to be 95% confident in that estimate, we calculate:

$$ n (\text { sample size }) = (1. 9 6) ^ {2} (. 5) (. 5) / (. 0 2) ^ {2} = 2, 4 0 1 $$

In time allocation studies, we estimate the proportion of various behaviors by observing a sample of behaviors. We’ll deal with this in chapter 14, on methods of direct observation (see especially table 14.2).

Estimating Proportions in Samples for Smaller Populations

This general formula, 6.5, is independent of the size of the population. Florida has a population of about 18 million. A sample of 400 is .000022 of 18 million; a sample of 2,402 is .00013 of 18 million. Both proportions are microscopic. A random, representative sample of 400 from a population of 1 million gets you the same confidence level and the same confidence interval as you get with a sample of 400 from a population of 18 million.

Often, though, we want to take samples from relatively small populations. The key word here is ‘‘relatively.’’ When formula 6.4 or 6.5 calls for a sample that turns out to be 5% or more of the total population, we apply the finite population correction. The formula (from Cochran 1977) is:

$$ n ^ {\prime} = \frac {n}{1 + (n - 1 / N)} $$

Formula 6.6

where n is the sample size calculated from formula 6.5; n- (read: n-prime) is the new value for the sample size; and N is the size of the total population from which n is being drawn.

Here’s an example. Suppose you are sampling the 540 resident adult men in a Mexican village to determine how many have ever worked illegally in the United States. How many of those men do you need to interview to ensure a 95% probability sample, with a 5% confidence interval? Answer: Because we have no idea what the percentage is that we’re trying to estimate, we set P and Q at .5 each in formula 6.4. Solving for n (sample size), we get:

$$ n = (1. 9 6) ^ {2} (. 5) (. 5) / (. 0 5) ^ {2} = 3 8 4. 1 6 $$

which we round up to 385. Then we apply the finite population correction:

$$ n ^ {\prime} = \frac {3 8 5}{1 + (3 8 4 / 5 4 0)} = 2 2 5 $$

This is still a hefty percentage of the 540 people in the population, but it’s a lot smaller than the 385 called for by the standard formula (box 6.1).

BOX 6.1

S E T T L I N G F O R B I G G E R C O N F I D E N C E I N T E R V A L S

If we were willing to settle for a 10% confidence interval, we’d need only 82 people in this example, but the trade-off would be substantial. If 65 out of 225, or 29%, reported that they had worked illegally in the United States, we would be 68% confident that from 24% to 34% really did, and 95% confident that 19% to 39% did. But if 24 out of 82 (the same 29%) reported having worked illegally in the United States, we’d be 68% confident that the true figure was between 19% and 39%, and 95% confident that it was between 9% and 49%. With a spread like that, you wouldn’t want to bet much on the sample statistic of 29%.

If it weren’t for ethnography, this would be a major problem in taking samples from small populations—the kind we often study in anthropology. If you’ve been doing ethnography in a community of 540 people for 6 months, though, you may feel comfortable taking a confidence interval of 10% because you are personally (not statistically) confident that your intuition about the group will help you interpret the results of a small sample.

Another Catch

All of this discussion has been about estimating single parameters, whether proportions or means. You will often want to measure the interaction among several variables at once. Suppose you study a population of wealthy, middle-class, and poor people in India. That’s three kinds of people. Now add two sexes, male and female (that makes six kinds of people) and two religions, Hindu and Muslim (that makes 12 kinds). If you want to know how all those independent variables combine to predict, say, average number of children desired, the sampling strategy gets more complicated.

Representative sampling is one of the trickiest parts of social research. I recommend strongly that you consult an expert in sampling if you are going to do complex tests on your data (Further Reading: sampling theory and sample design).

FURTHER READING

Sampling theory and sample design: Jaeger (1984); Kish (1965); Levy and Lemeshow (1999); Sudman (1976).

Sampling III: Nonprobability Samples and Choosing Informants

If your objective is to estimate a parameter or a proportion from a sample to a larger population, and your research calls for the collection of data about attributes of individuals (whether those individuals are people or organizations or episodes of a sitcom), then the rule is simple: Collect data from a sufficiently large, randomly selected, unbiased sample. If you know that you ought to use an unbiased sample and you have the means to get an unbiased sample and you still choose to use a nonprobability sample, then expect to take a lot of flak.

There are, however, three quite different circumstances under which nonprobability samples are exactly what are called for:

1. Nonprobability samples are always appropriate for labor-intensive, in-depth studies of a few cases. Most studies of narratives are based on fewer than 50 cases, so every case has to count. This means choosing cases on purpose, not randomly. In-depth research on sensitive topics requires nonprobability sampling. It can take months of participant observation fieldwork before you can collect narratives about topics like sexual and reproductive history or bad experiences with mental illness or use of illegal drugs.

Come to think of it, just about everything is a sensitive topic when you dig deeply enough. Sexual history is an obviously sensitive topic, but so is the management of household finances when you get into how people really allocate their resources. People love to talk about their lives, but when you get into the details of a life history, you quickly touch a lot of nerves. Really in-depth research requires informed informants, not just responsive respondents—that is, people whom you choose on purpose, not randomly.

2. Nonprobability samples are also appropriate for large surveys when, despite our best efforts, we just can’t get a probability sample. In these cases, use a nonprobability sample and document the bias. That’s all there is to it. No need to agonize about it.

3. And, as I said at the beginning of chapter 5, when you are collecting cultural data, as contrasted with data about individuals, then expert informants, not randomly selected respondents, are what you really need. Think of the difference between asking someone ‘‘How old was your child when you first gave him an egg to eat?’’ versus ‘‘At what age do children here first eat eggs?’’ I deal with the problem of selecting cultural experts (people who are likely to really know when most mothers introduce eggs around here) later in this chapter.

The major nonprobability sampling methods are: quota sampling, purposive sampling (also called judgment sampling), convenience sampling, and chain-referral (snowball) sampling. A special kind of mixed method, that combines elements of probability and nonprobability sampling, is the case control design (see box 4.6).

QUOTA SAMPLING

Quota sampling is stratified sampling without random selection. It is used widely in election polls as well as in studies that rely on qualitative data, like in-depth interviews.

The key to quota sampling is the development of a sampling design, or sampling grid. Suppose you are studying the lived experiences of labor migrants to the United States who are back home in their community in Mexico. You want to compare the experiences of (1) people who spent time on jobs in the United States but were caught by the U.S. Border Patrol and deported with those of (2) people who managed to stay on their jobs until they’d accumulated enough money to return on their own. You also want to compare the experiences of Indians and Mestizos and of men and women. That’s three binary independent variables: deported/not deported; Indian/Mestizo; male/female. Figure 7.1 shows that there are eight cells in this design. If you want at least five informants in each cell, you’ll need to do 40 interviews.

Mexicans who have worked in the United States and returned home
Deported				Returned voluntarily
Mestizo		Indian		Mestizo		Indian
Male	Female	Male	Female	Male	Female	Male	Female

FIGURE 7.1. Quota sampling grid with three binary independent variables.

Tinsley et al. (2002) interviewed 437 elderly users of Lincoln Park in Chicago. They selected quota samples of about 50 men and 50 women from each of the four major ethnic groups in the area, Blacks, Whites, Hispanics, and Asian Americans. Besides gender and ethnicity, Tinsley et al. stratified on place and time. They divided the park into three zones (north, south, and middle) and three time periods (6 a.m. to 10 a.m., 11 a.m. to 3 p.m., and 4 p.m. to 8 p.m.). There were, then, nine zone-time strata in which interviewers selected respondents. The interviewers were also told to make sure they got some weekday and some weekend users of the park.

When it’s done right, quota samples often do a good job of reflecting the population parameters of interest. In other words, quota sampling is an art that often approximates the results of probability sampling at less cost and less hassle than strict probability sampling (box 7.1).

Quota samples are biased toward people you can find easily—which means, for example, that they’re biased against really poor and really rich people and against single people who aren’t home as much (Marsh and Scarborough 1990)—so quota sampling is dangerous when it comes to making predictions about close election outcomes—or estimating any population parameter, for that matter, if you need precise results.

On the other hand, quota sampling is appropriate in the study of cultural domains. If you want to know how junior sports—Little League Baseball, Pop Warner football, Youth Soccer, junior and senior high school football—function in small communities across the United States, you’d ask people who have children playing those sports. There will be some intracultural variation, but open-ended interviews with four or five really knowl-

BOX 7.1

F A M O U S P O L L I N G D E B A C L E S F R O M Q U O T A S A M P L E S

In 1948, pollsters predicted, on the basis of quota sampling, that Thomas Dewey would beat Harry Truman in the U.S. presidential election. The Chicago Tribune was so confident in those predictions that they printed an edition announcing Dewey’s victory—while the votes were being counted that would make Truman president.

Skip to 1992. In the general election in Britain that year, four different polls published on the day of the election put the Liberal Party, on average, about 1 point ahead of the Conservative Party. All the polls were based on quota sampling. The Conservatives won by 8 points. In fact, from 1992 to 1997, political polls using quota samples in Britain systematically overestimated the support for the Liberals (Curtice and Sparrow 1997). A similar polling debacle happened in the 2002 presidential election in France. Twelve polls predicted that Jacques Chirac and Lionel Jospin would defeat the far-right candidate, Jean-Marie Le Pen in the first round of voting and face each other in a run-off. No one predicted that Le Pen would trounce Jospin and face Chirac in the run-off (Durand et al. 2004).

edgeable people will produce the relevant cultural data—including data on the range of ideas that people have about these institutions (Further Reading: quota sampling).

PURPOSIVE OR JUDGMENT SAMPLING

In purposive sampling, you decide the purpose you want informants (or communities) to serve, and you go out to find some. This is somewhat like quota sampling, except that there is no overall sampling design that tells you how many of each type of informant you need for a study. You take what you can get.

I used purposive sampling in my study of the Kalymnian (Greek) sponge-fishing industry (1987). I knew I had to interview sponge merchants, boat owners, and divers, but my first interviews taught me that I had to interview people whom I had never considered: men who used to be divers but who had quit, gone to Australia as labor migrants, and returned to the island. It was very easy to find those returned migrants: Everyone on Kalymnos either had one in their family or knew people who did.

There are many good reasons for using purposive samples. They are used widely in (1) pilot studies, (2) intensive case studies, (3) critical case studies, and (4) studies of hardto-find populations.

1. Pilot studies. These are studies done before running a larger study. In 1999, Katherine Browne, Carla Freeman, and Zobeida Bonilla began a comparative ethnographic study of women entrepreneurs in Martinique, Barbados, and Puerto Rico—that is, in the French-, English-, and Spanish-speaking Caribbean. In a large, multisite study like this, it pays to spend time on pilot research. Each member of the team did 30 in-depth interviews with women who were engaged in a wide range of enterprises, who were of different ages, and who came from one- and two-parent homes. This helped the team develop their research instruments and provided the baseline for the larger project (Browne 2001).

And speaking of instruments, when you do surveys to test hypotheses, make sure that you test all your scales with a pilot sample. More about all this in chapter 11, on scales.

2. In intensive case studies, the object is often to identify and describe a cultural phenomenon. Dickerson et al. (2000) studied the experiences of American Indian graduate nursing students and cultural barriers that might lead the students to drop out of their training. Dickerson et al. found and interviewed 11 students who were enrolled in an advanced nurse practitioner program. Samples don’t get much more purposive than this, and they don’t get much more appropriate, either.

Life history research and qualitative research on special populations (drug addicts, trial lawyers, shamans) rely on judgment sampling. Barroso (1997), for example, studied a purposive sample of 14 men and six women in the Tampa, Florida, area, all of whom had lived with AIDS for at least 3 years.

Finally, researchers don’t usually pull research sites—villages, tribal encampments, hospitals, school systems—out of a hat. They rely on their judgment to find one that reflects the things they are interested in.

3. Critical case studies. These are done in all fields of science and have long been the basis, by deduction, for the development of theory. Freud based his theory of psychosexual development on a few critical cases from his practice. Steward based his theory of multilineal evolution on a few critical cases from archeology. Political scientists study cases like the Orange Revolution in Ukraine for clues about the transition from autocracy to democracy (McFaul 2007).

Choosing key informants in ethnographic research is a form of critical-case sampling. It would be pointless to select a handful of people randomly from a population and try to turn them into trusted key informants.

4. We almost always have to rely on purposive sampling in the study of hard-to-find populations.

Think about locating and interviewing refugees from Somalia and Ethiopia living in a large American city. Many of these people experienced torture and don’t exactly welcome researchers who want to ask them a lot of questions. This was the problem facing researchers in Minneapolis (see Jaranson et al. 2004; Spring et al. 2003). The study design called for a quota sample of 1,200 respondents, including 300 Oromo women, 300 Oromo men, 300 Somali women, and 300 Somali men. The study team recruited male and female interviewers from the community—people who shared ethnicity, language, and religion with the people they were trying to locate and interview. The project team sent out fliers, placed announcements in church bulletins, and made presentations at meetings of Oromo and Somali organizations. The interviewers also used their own social networks to locate potential respondents. Over 25 months, the team built trust in the community and wound with 1,134 of the 1,200 interviews called for in the study.

Kimberly Mahaffy (1996) was interested in how lesbian Christians deal with the cognitive dissonance that comes from being rejected by mainstream Christian churches. Mahaffy sent letters to gay Christian organizations, asking them to put an ad for potential respondents in their newsletters. She sent flyers to women’s bookstores and to lesbian support groups, asking for potential respondents to get in touch with her.

Eventually, Mahaffy got 163 completed questionnaires from women who fit the criteria she had established for her research, including 44 from women who self-identified as born-again or evangelical Christians. Mahaffy could not possibly have gotten an unbiased sample of lesbian Christians, but the corpus of data that she collected from her respondents had all the information she needed to answer her research questions (Further Reading: purposive sampling).

CONVENIENCE OR HAPHAZARD SAMPLING

Convenience sampling is a glorified term for grabbing whoever will stand still long enough to answer your questions. Sometimes, convenience samples are all that are available, and you just have to make do. Studies of the homeless are usually done with convenience samples, for obvious reasons, as are studies of people who are in intensive care units in hospitals. All samples represent something. The trick is to make them representative of what you want them to be. That’s what turns a convenience sample into a purposive one.

Al-Krenawi and Wiesel-Lev (1999) wanted to understand the emotions of Israeli Bedouin women who had experienced genital mutilation. They interviewed a convenience sample of 12 women who had been through the ritual and 12 who had not but had either seen it first-hand or had heard about women in their own extended families going through it. We wouldn’t put much stock in the fact that a specific percentage of the women reported sexual problems or relationship problems with various members of their family, but the list of problems is very instructive because it is the basis for more in-depth research.

If you want to estimate a parameter, then you know what you have to do: Get a random, representative sample. If you want to know the percentage of adult men in a matrilateral, cross-cousin society who have actually married their biological mother’sbrother’s-sister (MBZ), you’ll either have to count them all or take a random, unbiased sample of sufficient size to be able to make that generalization.

Key informants will tell you that the rule is broken regularly, but not by how much. A convenience sample of women who gather at the village well each day will tell you the range of options for men who don’t have a biological MBZ, but not how many choose each option. And if you want to know the effect of a new road on some peasants and you only interview people who come to town on the road, you’ll miss all the people who live too far off the road for it to do them any good (Further Reading: convenience sampling).

CHAIN REFERRAL, OR NETWORK SAMPLING: THE SNOWBALL AND RDS METHODS

Snowball and respondent-driven sampling (RDS) (also known, generically, as chain referral methods) are two network sampling methods for studying hard-to-find or hardto-study populations. Populations can be hard to find and study for at least four reasons: (1) they contain very few members who are scattered over a large area (think strict vegans in rural Georgia, or bilingual deaf children in Texas who are fluent in signing English and Spanish); and/or (2) they are stigmatized and reclusive (HIV-positive people who never show up at clinics until they are sick with AIDS) or even actively hiding (transgendered people who have been physically attacked, men who have battered their female partners);

and/or (3) they are people who really have something to hide (Richardson [1988], for example, used snowball sampling to locate single or divorced women who were in longterm relationships with married men); and/or (4) they are members of an elite group (surgeons, professional athletes) and don’t care about your need for data.

Charles Kadushin (1968) laid out the snowball method in his study of elites in modern, complex societies, but elites can just as well be ‘‘people in this village whose opinions really count’’ or ‘‘wood carvers in this district whose work is respected’’ or ‘‘native curers who see more than 10 patients a month.’’ Using key informants and/or documents, you locate one or two people in a population. Then you ask those people to (1) list others in the population and (2) recommend someone from the list whom you might interview. You get handed from informant to informant and the sampling frame grows with each interview. Eventually, the sampling frame becomes saturated—that is, no new names are offered. Ostrander (1980) used snowball sampling in her study of class consciousness among upper-class women in a midwestern U.S. city. She selected her first informant by looking for someone who had graduated from an elite women’s college, was listed in the social register, was active in upper-class clubs—and who would talk to her. At the end of the interview, she asked the informant to ‘‘suggest another woman of your social group, with a background like yours, who might be willing to talk to me.’’

Thomas Weisner has been following 205 counterculture women and their families since 1974. Weisner built this sample by recruiting women in California who were in their third trimester of pregnancy. He used snowball sampling, but to ensure that participants came from all over the state and represented various kinds of families, he used no more than two referrals from any one source (Weisner 2002:277) (box 7.2).

BOX 7.2

S O M E T I M E S Y O U J U S T H A V E T O S T A R T O V E R

David Griffith and his colleagues used two snowball samples in their study of food preferences in Moberly, Missouri. They chose an initial ‘‘seed’’ household in a middle-income neighborhood and asked a man in the house to name three people in town with whom he interacted on a regular basis. The first person cited by the informant lived in a lower-income neighborhood across town. That person, in turn, named other people who were in the lower-income bracket.

After a while, the researchers realized that, though they’d started with a middle-income informant who had children at home, they were getting mostly lower-income, elderly people in the snowball sample. So they started again, this time with a seed from an elite, upper-middle-income neighborhood. By the time they got through, Griffith et al. had a well-balanced sample of 30 informants with whom they did in-depth interviews (reported in J. C. Johnson 1990:78).

Respondent-Driven Sampling

Snowball sampling is popular and fun to do, but it does not produce a statistically representative sample in a large population. In a small community, like practitioners of alternative medicine in a town, the members are likely to be in contact with one another.

Here, snowball sampling is an effective way to build an exhaustive sampling frame from which you can select people at random to interview—or elect to interview all of them. In large communities, though—like all the native curers in a city such as Nairobi—the members who are well known have a better chance of being named in a snowball procedure than members who are less well known. And in large populations, people who have large networks name more people than do people who have small networks. For large populations, then, snowball sampling can produce useful nonprobability samples, but every person does not have the same chance of being included.

Douglas Heckathorn (1997) developed respondent-driven sampling to deal with this problem. Like snowball sampling, RDS begins with a few informants who act as seeds. The informants are paid for being interviewed and are then asked to recruit up to three members of their networks into the study. To move this process along, Heckathorn paid each of his seed informants $10 (this might be $50 today, but you get the idea) and he gave them three coupons. Anyone who came to Heckathorn to be interviewed and who had one of those coupons was paid the same $10. (He upped the bounty to $15 for referring a female drug injector because they were harder to find.) Those informants, in turn, got several coupons and recruited others into the study.

There are two improvements to snowball sampling here. (1) The people whom an informant names in a snowball interview may not want you even to know about their existence, much less be anxious to grant you an interview. In respondent-driven sampling, the initial members of the sample are volunteers as are the people they recruit. (2) When it’s done right, the RDS method produces samples that are less biased than are traditional snowball samples (Salganik and Heckathorn 2004) (Further Reading: chain referral, snowball, and RDS sampling) (box 7.3).

BOX 7.3

G A M I N G T H E R D S

RDS is now widely used in the study of injection drug users and other populations at high risk for HIV/AIDS. Scott (2008) interviewed 70 injection drug users in Chicago who had participated in the full entire RDS sequence: They had received $20 for completing an interview and had collected $30 more for bringing in three associates (at $10 each) who had also completed an interview. Forty-eight of the 70 had sold at least one of their coupons to someone else because they could not trust three people in their network to complete the interview. This may introduce some distortion to the samples, but RDS remains the best available method for locating and studying populations at risk for HIV/ AIDS.

CHOOSING INFORMANTS

Across the social sciences, you’ll see references to research participants as ‘‘respondents,’ or ‘‘subjects,’’ or ‘‘informants.’’ These terms tend to be used by sociologists, psychologists, and anthropologists, respectively. Respondents respond to survey questions, subjects are the subject of some experiment, and informants . . . well, informants tell you what they think you need to know about their culture.

There are two kinds of informants: key informants and specialized informants. Key informants are people who know a lot about their culture and are, for reasons of their own, willing to share all their knowledge with you. When you do long-term ethnography, you develop close relationships with a few key informants—relationships that can last a lifetime. You don’t choose these people. They and you choose each other, over time.

Specialized informants have particular competence in some cultural domain. If you want to know the rules of Balinese cockfighting, or how many cows must be given to a Lumasaba bride’s parents, or when to genuflect in a Roman Catholic Mass, or what herb tea to give children for diarrhea, you need to talk to people who can speak knowledgeably about those things.

KEY INFORMANTS

Good key informants are people whom you can talk to you easily, who understand the information you need, and who are glad to give it to you or get it for you. Pelto and Pelto (1978:72) advocate training informants ‘‘to conceptualize cultural data in the frame of reference’’ that you, the researcher, use.

In some cases, you may want to just listen. But when you run into a really great informant, I see no reason to hold back. Teach the informant about the analytic categories you’re developing and ask whether the categories are correct. In other words, encourage the informant to become the ethnographer.

I’ve worked with Jesu´ s Salinas since 1962. In 1971, I was about to write an ethnography of his culture, the N^˜ a¨hn˜u of central Mexico, when he mentioned that he’d be interested in writing an ethnography himself. I dropped my project and taught him to read and write N^˜ a¨hn˜u. Over the next 15 years, Salinas produced four volumes about the N^˜ a¨hn˜u people—volumes that I translated and from which I learned many things that I’d never have learned had I written the ethnography myself. For example, N^˜ a¨hn˜u men engage in rhyming duels, much like the ‘‘dozens’’ of African Americans. I wouldn’t have thought to ask about those duels because I had never witnessed one (see Bernard and Salinas Pedraza 1989).

Just as Salinas has influenced my thinking about Mexican Indian life, Salinas’s ethnography was heavily influenced by his association with me. We’ve discussed and analyzed parts of N^˜ a¨hn˜ u culture over the years and we’ve even argued over interpretation of observed facts. (More about all this in the section on native ethnography in chapter 18, plus a different perspective by Harry Wolcott [2008].)

Finding Key Informants

One of the most famous key informants in the ethnographic literature is Doc in William Foote Whyte’s Street Corner Society (1981 [1943]). Whyte studied ‘‘Cornerville,’’ an Italian American neighborhood in a place he called ‘‘Eastern City.’’ (Cornerville was the North End of Boston.) Whyte asked some social workers if they knew anyone who could help Whyte with his study. One social worker told Whyte to come to her office and meet a man whom she thought could do the job. When Whyte showed up, the social worker introduced him to Doc and then left the room. Whyte nervously explained his predicament, and Doc asked him ‘‘Do you want to see the high life or the low life?’’ (Whyte 1989:72).

Whyte couldn’t believe his luck. He told Doc he wanted to see all he could, learn as much as possible about life in the neighborhood. Doc told him:

Any nights you want to see anything, I’ll take you around. I can take you to the joints— the gambling joints. I can take you around to the street corners. Just remember that you’re my friend. That’s all they need to know. I know these places and if I tell them you’re my friend, nobody will bother you. You just tell me what you want to see, and we’ll arrange it. . . . When you want some information, I’ll ask for it, and you listen. When you want to find out their philosophy of life, I’ll start an argument and get it for you. (Whyte 1989:72)

Doc was straight up; he told Whyte to rely on him and to ask him anything, and Doc was good to his word all through Whyte’s 3 years of fieldwork. Doc introduced Whyte to the boys on the corner; Doc hung out with Whyte and spoke up for Whyte when people questioned Whyte’s presence. Doc was just spectacular.

Or was he? Boelen (1992) visited Cornerville 25 times between 1970 and 1989, sometimes for a few days, other times for several months. She tracked down and interviewed everyone she could find from Street Corner Society. Doc had died in 1967, but she interviewed his two sons in 1970 (then in their late teens and early 20s). She asked them what Doc’s opinion of Whyte’s book had been and reports the elder son saying: ‘‘My father considered the book untrue from the very beginning to the end, a total fantasy’’ (Boelen 1992:29).

Whyte (1996a, 1996b) refuted Boelen’s report, as did another of Whyte’s key informants (Orlando 1992). We’ll never know the whole truth. Whyte certainly made mistakes, but the same can be said for all ethnographers. For some scholars, mistakes invalidate a positivist stance in ethnography. For others, it does not (box 7.4).

BOX 7.4

D O C M A Y B E F A M O U S , B U T H E ’ S N O T U N I Q U E

He’s not even rare. All successful ethnographers will tell you that they eventually came to rely on one or two key people in their fieldwork. What was rare about Doc is how quickly and easily Whyte teamed up with him. It’s not easy to find informants like Doc. When Jeffrey Johnson began fieldwork in a North Carolina fishing community, he went to the local marine extension agent and asked for the agent’s help. The agent, happy to oblige, told Johnson about a fisherman whom he thought could help Johnson get off on the right foot.

It turned out that the fisherman was a transplanted northerner; he had a pension from the Navy; he was an activist Republican in a thoroughly Democratic community; and he kept his fishing boat in an isolated moorage, far from the village harbor. He was, in fact, maximally different from the typical local fisherman. The agent had meant well, of course (J. C. Johnson 1990:56).

In fact, the first informants with whom you develop a working relationship in the field may be ‘‘deviant’’ members of their culture. Agar (1980b:86) reports that during his fieldwork in India, he was taken on by the naik, or headman of the village. The naik, it turned out, had inherited the role, but he was not respected in the village and did not preside over village meetings. This did not mean that the naik knew nothing about village affairs and customs; he was what Agar called a ‘‘solid insider,’’ and yet somewhat of an outcast—a ‘‘marginal native,’’ just like the ethnographer was trying to be (Freilich 1977). If you think about it, Agar said, you should wonder about the kind of person who would befriend an ethnographer.

In my own fieldwork (at sea, in Mexican villages, on Greek islands, in rural communities in the United States, and in modern American bureaucracies), I have consistently found the best informants to be people who are cynical about their own culture. They may not be outcasts (in fact, they are always solid insiders), but they say they feel somewhat marginal to their culture, by virtue of their intellectualizing of and disenchantment with their culture. They are always observant, reflective, and articulate. In other words, they invariably have all the qualities that I would like to have myself.

Don’t choose key ethnographic informants too quickly. Allow yourself to go awash in data for a while and play the field. When you have several prospects, check on their roles and statuses in the community. Be sure that the key informants you select don’t prevent you from gaining access to other important informants (i.e., people who won’t talk to you when they find out you’re so-and-so’s friend). Good ethnography is, at its best, a good story, so find trustworthy informants who are observant, reflective, and articulate— who know how to tell good stories—and stay with them. In the end, ethnographic fieldwork stands or falls on building mutually supportive relations with a few key people.

Informants Sometimes Lie

Don’t be surprised if informants lie to you. Jeffrey Johnson, a skilled boat builder, worked in an Alaskan boatyard as part of his field study of a fishing community. At one point in his fieldwork, two other ethnographers showed up, both women, to conduct some interviews with the men in the boatyard. ‘‘The two anthropologists had no idea I was one of them,’’ Johnson reports,

since I was dressed in carpenter’s overalls, with all the official paraphernalia—hammer, tape measure, etc. I was sufficiently close to overhear the interview and, knowing the men being interviewed, recognized quite a few blatant lies. In fact, during the course of one interview, a captain would occasionally wink at me as he told a whopper of a lie. (personal communication)

This is not an isolated incident. A Comox Indian woman spent 2 hours narrating a text for Franz Boas. The text turned out to be nothing but a string of questions and answers. Boas didn’t speak Comox well enough to know that he was being duped, but when he found out he noted it in his diary (Rohner 1969:61). And Margaret Mead’s adolescent informants probably lied to her about their sex lives—more about that in chapter 12.

In 1938, Melville Herskovits published his massive, two-volume work on the ancient West African kingdom of Dahomey (today Benin). According to Herskovits, there was an annual census and the data from these efforts were used in administering the state. The counting involved the delivery of sacks of pebbles from around the kingdom to the palace at Abomey, with each pebble representing a person. Roger Sandall (1999) has shown that the informant who told Herskovits about this elaborate accounting system may have made it all up.

This sort of thing can happen to anyone who does participant observation ethnography, but some cultures are more tolerant of lying than are others. Nachman (1984) found that the most articulate informants among the Nissan of New Guinea were great truth tellers and accomplished liars at the same time. Among the Nissan, says Nachman, people expect big men to give speeches and to ‘‘manipulate others and to create socially acceptable meanings,’’ even if that means telling outright lies (Nachman 1984:552 and see Salamone 1977).

SELECTING CULTURALLY SPECIALIZED INFORMANTS

The search for formal and systematic ways to select focused ethnographic informants— people who can help you learn about particular areas of a culture—has been going on for a very long time. In 1957, Marc-Adelard Tremblay was involved in a Cornell University survey research project on poverty in Nova Scotia. He wanted to use ethnographic informants to help the team’s researchers design a useful questionnaire, so he made a list of some roles in the community he was studying—things like sawmill owners, doctors, farmers, bankers—and chose informants who could talk to him knowledgeably about things in their area of expertise. Tremblay had no external test to tell him whether the informants he selected were, in fact, the most competent in their areas of expertise, but he felt that on-the-spot clues made the selection of informants valid (Tremblay 1957).

Michael Robbins and his colleagues studied acculturation and modernization among the Baganda of Uganda, using a more formal method to select informants who might be competent on this topic (Robbins et al. 1969). First, they ran a survey of households in a rural sector, asking about things that would indicate respondents’ exposure to Western culture. Then they used the results of the survey to select appropriate informants.

Robbins et al. had 80 variables in the survey that had something to do with acculturation and they ran a factor analysis to find out which variables package together. We’ll look a bit more at factor analysis in chapter 22. For now, think of factor analysis as a way to reduce those 80 variables to just a handful of underlying variables around which individual variables cluster. It turned out that 14 of the original 80 variables clustered together in one factor. Among those original variables were: being under 40 years of age, drinking European beer, speaking and reading English, having a Western job, and living in a house that has concrete floors and walls.

Robbins et al. called this cluster the ‘‘acculturation factor.’’ They chose informants who had high scores on this factor and interviewed them about acculturation. Robbins et al. reversed Tremblay’s method. Tremblay used key informants to help him build a survey instrument; Robbins et al. used a survey to find key informants.

Poggie’s Study of Ciudad Industrial

In any given domain of culture, some people are more competent than others. In our culture, some people know a lot about the history of baseball; some people can name the actors in every sitcom since the beginning of television in the 1940s. Some people are experts on medicinal plants; others are experts on cars and trucks. John Poggie (1972) did an early study of informant competence. He selected one informant in each of seven Mexican communities. The communities ranged in size from 350 to 3,000 inhabitants. The informants were village or town presidents, or judges, or (in the case of agricultural communities) the local commissioners of communal land. Poggie asked these informants questions about life in the communities, and he compared the answers with data from a high-quality social survey.

For example, Poggie asked the seven informants: ‘‘How many men in this town are workers in Ciudad Industrial?’’ (Ciudad Industrial is a fictitious name of a city that attracted many labor migrants from the communities that Poggie studied.) In his survey, Poggie asked respondents if they had ever worked in Ciudad Industrial. The correlation between the answers given by Poggie’s expert informants and the data obtained from the survey was .90.

Table 7.1 Agreement between Informants and Survey Data in Seven Villages

Questions asked of informants	Correlation with questionnaire data
Number of men from this town who are workers in Ciudad Industrial	0.90
Percentage of houses made of adobe	0.71
Percentage of households that have radios	0.52
Percentage of people who eat eggs regularly	0.33
Percentage of people who would like to live in Ciudad Industrial	0.23
Percentage of people who eat bread daily	0.14
Percentage of people who sleep in beds	0.05

SOURCE: J. J. Poggie, ‘‘Toward Quality Control in Key Informant Data,’’ Human Organization, Vol. 31, pp. 26–29, 1972. Reprinted with permission of the Society for Applied Anthropology.

Poggie also asked: ‘‘What percentage of the houses here are made of adobe?’’ This time, the correlation between the informants and the survey was only .71. Table 7.1 shows the seven questions Poggie asked, and how well his informants did when their answers were compared to the survey.

Overall, informants produced answers most like those in the survey when they were asked to respond to questions about things that are publicly observable. The survey data are not necessarily more accurate than the informants’ data. But as the questions require informants to talk about things inside people’s homes (such as what percentage of people eat eggs), or about what people think (what percentage of people would like to work in Ciudad Industrial), informants’ answers look less and less like those of the survey.

Poggie concluded that ‘‘There is little reason to believe that trust and rapport would improve the reliability and precision concerning what percentage sleep in beds, who would like to live in the new industrial city, or what percentage eat bread daily’’ (Poggie 1972:29). (For more on selecting informants who have high competence in specialized domains, see the discussion of consensus analysis in chapter 16.)

SAMPLE SIZE IN NONPROBABILITY SAMPLING

There is growing evidence that 10–20 knowledgeable people are enough to uncover and understand the core categories in any well-defined cultural domain or study of lived experience. Morse (1994) recommended a minimum of six interviews for phenomenological studies and 30–50 interviews for ethnographic studies and grounded theory studies. The data from two recent studies support Morse’s experience-based guess.

M. G. Morgan et al. (2002:76) did in-depth interviews with four different samples of people about various risks in the environment. As they coded the interviews for concepts, Morgan et al. plotted the number of new concepts in each interview across the four samples. In all four cases, the first few interviews produce a lot of new data, but by 20 interviews, hardly any new information is retrieved.

Guest et al. (2006) interviewed 30 sex workers in Ghana and another 30 in Nigeria. They coded the transcripts in batches of six, working first on the interview from Ghana and then on the ones from Nigeria, and plotted the number of new themes uncovered in the coding. Of the 114 themes identified in the entire corpus, 80 turn up in the first six interviews in both Ghana and Nigeria. Another 20 themes turned up in the second batch of six interviews. Only 5 new themes were added to the codebook to accommodate the 30 interviews from Nigeria.

And, as we’ll see in tables 16.13 and 16.14 (when we get to consensus analysis), Weller and Romney (1988:77) showed that just 10–13 knowledgeable informants are needed to understand the contents of a well-defined cultural domain. This is all very good news for ethnographers (and see Handwerker 2001:93–96).

AND FINALLY . . .

Particularly in ethnographic research, you learn in the field, as you go, to select the units of analysis (people, court records, whatever) that will provide the information you need. This is what Russell Belk et al. (1988) did in their detailed ethnographic study of buyers and sellers at a swap meet. When you study a process, like bargaining over goods, and you’re doing the research in the field, in real time (not under simulated conditions in a lab), then selecting informants who meet certain criteria is the right thing to do.

The credibility of research results comes from the power of the methods used in measurement and sampling. Good measurement is the key to internal validity and representative sampling is the key to external validity. Well-done nonprobability sampling is actually part of good measurement. It contributes to credibility by contributing to internal validity. When someone reads a research report based on really good measurement of a nonprobability sample, they come away thinking, ‘‘Yep, I believe those conclusions about the people who were studied in that piece of research.’

That’s plenty. If you want the credibility of your conclusions to extend beyond the group of people (or countries, or organizations, or comic books) you studied, then either: (1) Repeat the study one or more times with nonprobability samples; or (2) Use a probability sample. Remember: Every sample represents something. An unbiased sample represents a population with a known probability of error. A nonprobability sample lacks this one feature. For a very, very large number of research questions, this is simply not a problem.

FURTHER READING

Quota sampling: Alaimo et al. (2008); Berinsky (2006); Me´jean et al. (2009); Morrow et al. (2007); Weinberger (1973).

Purposive sampling: Auerswald et al. (2004); Topp et al. (2004).

Convenience sampling: Hultsch (2002); Pruchno et al. (2008); Sousa et al. (2004).

Chain referral, snowball and respondent driven sampling: Draus et al. (2005); Heckathorn (2002); Heckathorn and Jeffri (2001); Heckathorn and Wejnert (2008); Kendall et al. (2008); Malekinejad et al. (2008); J. L. Martin and Dean (1993); Penrod et al. (2003); Sudman and Kalton (1986).

Interviewing I: Unstructured and Semistructured

THE BIG PICTURE

The concept of ‘‘interviewing’’ covers a lot of ground, from totally unstructured interactions, through semistructured situations, to highly formal interactions with respondents. Interviewing is done on the phone, in person, by mail and—more and more—by computer or on the Internet. This chapter is about unstructured and semistructured face-toface interviewing, including the management of focus groups.

Unstructured interviewing goes on all the time and just about anywhere—in homes, walking along a road, weeding a millet field, hanging out in bars, or waiting for a bus. Semistructured, or in-depth interviewing is a scheduled activity. A semistructured interview is open ended, but follows a general script and covers a list of topics.

There is a vast literature on how to conduct effective interviews: how to gain rapport, how to get people to open up, how to introduce an interview, and how to end one. You can’t learn to interview by reading about it, but after you read this chapter and practice some of the techniques described, you should be well on your way to becoming an effective interviewer. You should also have a pretty good idea of how much more there is to learn, and be on your way to exploring the literature.

INTERVIEW CONTROL

There is a continuum of interview situations based on the amount of control we try to exercise over people’s responses (Dohrenwend and Richardson 1965; Gorden 1987; Spradley 1979). These different types of interviews produce different types of data that are useful for different types of research projects and that appeal to different types of researchers. For convenience, I divide the continuum of interviews into four large chunks.

1. Informal Interviewing

At one end there is informal interviewing, characterized by a total lack of structure or control. The researcher just tries to remember conversations heard during the course of a day in the field. This requires constant jotting and daily sessions in which you sit at a computer, typing away, unburdening your memory, and developing field notes. Informal interviewing is the method of choice at the beginning of participant observation fieldwork, when you’re settling in. It is also used throughout ethnographic fieldwork to build greater rapport and to uncover new topics of interest that might have been overlooked.

When it comes to interviewing, never mistake the adjective ‘‘informal’’ for ‘‘light-

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weight.’’ This is hard, hard work. You have to remember a lot; you have to duck into private corners a lot (so you can jot things down); and you have to use a lot of deception (to keep people from knowing that you’re really at work, studying them). Informal interviewing can get pretty tiring.

Still, in some kinds of research, informal interviewing is all you’ve got. Mark Connolly (1990) studied gamines, or street children, in Guatemala City, Guatemala, and Bogota´, Colombia. These children live, eat, and sleep on the street. Hanging out and talking informally with these children was an appropriate way to do this research. Informal ethnography can also be combined with more structured methods, when circumstances allow it. In fact, Rachel Baker (1996a, 1996b) was able to collect anthropometric data on street children in Kathmandu, Nepal, while doing informal ethnography.

2. Unstructured Interviewing

Next comes unstructured interviewing, one of the two types covered in this chapter. There is nothing at all informal about unstructured interviewing, and nothing deceptive, either. You sit down with another person and hold an interview. Period. Both of you know what you’re doing, and there is no shared feeling that you’re just engaged in pleasant chitchat.

Unstructured interviews are based on a clear plan that you keep constantly in mind, but are also characterized by a minimum of control over the people’s responses. The idea is to get people to open up and let them express themselves in their own terms, and at their own pace. A lot of what is called ethnographic interviewing is unstructured. Unstructured interviewing is used in situations where you have lots and lots of time—like when you are doing long-term fieldwork and can interview people on many separate occasions (box 8.1).

BOX 8.1

P A Y I N G I N F O R M A N T S

Should anthropologists pay their informants? If so, how much? I’m a firm believer in paying for people’s time, but there are exceptions. If you are studying people who are worth millions of dollars, paying them is inappropriate. You can’t possibly pay them enough to compensate them financially for their time. It’s better to make a donation to a charity that they support. This will vary from case to case, but the general rule, for me at least, is that if you want to interview people formally—sit down with them, voice recorder on the table and/or notebook in hand—they should be paid at least the local rate for their time. With key informants, the rule for me is that there’s always a culturally appropriate way—money, job training, buying cement for a new school—to compensate people for their contribution to your career.

3. Semistructured Interviewing

In situations where you won’t get more than one chance to interview someone, semistructured interviewing is best. It has much of the freewheeling quality of unstructured interviewing and requires all the same skills, but semistructured interviewing is based on the use of an interview guide. This is a written list of questions and topics that need to be covered in a particular order.

This is the kind of interview that most people write about—the kind done in professional surveys. The interviewer maintains discretion to follow leads, but the interview guide is a set of clear instructions—instructions like this one: ‘‘Probe to see if informants (men and women alike) who have daughters have different values about dowry and about premarital sex than do people who have only sons.’

Formal, written guides are an absolute must if you are sending out several interviewers to collect data. But even if you do all the interviewing on a project yourself, you should build a guide and follow it if you want reliable, comparable qualitative data.

Semistructured interviewing works very well in projects where you are dealing with high-level bureaucrats and elite members of a community—people who are accustomed to efficient use of their time. It demonstrates that you are fully in control of what you want from an interview but leaves both you and your respondent to follow new leads. It shows that you are prepared and competent but that you are not trying to exercise excessive control.

4. Structured Interviewing

Finally, in fully structured interviews, people are asked to respond to as nearly identical a set of stimuli as possible. One variety of structured interviews involves use of an interview schedule—an explicit set of instructions to interviewers who administer questionnaires orally. Instructions might read: ‘‘If the informant says that she or he has at least one daughter over 10 years of age, then ask questions 26b and 26c. Otherwise, go on to question 27.’’

Self-administered questionnaires are a kind of structured interview. Other structured interviewing techniques include pile sorting, frame elicitation, triad sorting, and tasks that require informants to rate or rank order a list of things. I’ll deal with these in chapter 10.

UNSTRUCTURED INTERVIEWING

Unstructured interviewing is truly versatile. It is used equally by scholars who identify with the hermeneutic tradition and by those who identify with the positivist tradition. It is used in studies that require only textual data and in studies that require both textual and numerical data. Ethnographers may use it to develop formal guides for semistructured interviews, or to learn what questions to include, in the native language, on a highly structured questionnaire (see Werner and Schoepfle [1987] for a good discussion of this). I say that ethnographers may use unstructured interviewing in developing structured interview schedules because unstructured interviewing also stands on its own.

When you want to know about the lived experience of fellow human beings—what it’s like to survive hand-to-hand combat, how you get through each day when you have a child dying of leukemia, how it feels to make it across the border into Texas from Mexico only to be deported 24 hours later—you just can’t beat unstructured interviewing.

Unstructured interviewing is excellent for building initial rapport with people, before moving to more formal interviews, and it’s perfect for talking to informants who would not tolerate a more formal interview. The personal rapport you build with close informants in long-term fieldwork can make highly structured interviewing—and even semistructured interviewing—feel somehow unnatural. In fact, really structured interviewing can get in the way of your ability to communicate freely with key informants.

But not always. Some people want very much to talk about their lives, but they really don’t like the unstructured interview format. I once asked a fisherman in Greece if I could have a few minutes of his time to discuss the economics of small-scale fishing. I was about 5 minutes into the interview, treading lightly—you know, trying not to get too quickly into his finances, even though that’s exactly what I wanted to know about—when he interrupted me: ‘‘Why don’t you just get to the point?’’ he asked. ‘‘You want to know how I decide where to fish, and whether I use a share system or a wage system to split the profits, and how I find buyers for my catch, and things like that, right?’’ He had heard from other fishermen that these were some of the topics I was interviewing people about. No unstructured interviews for him; he was a busy man and wanted to get right to it.

A Case Study of Unstructured Interviewing

Once you learn the art of probing (which I’ll discuss in a bit), unstructured interviewing can be used for studying sensitive issues, like sexuality, racial or ethnic prejudice, or hot political topics. I find it particularly useful in studying conflict. In 1972–1973, I went to sea on two different oceanographic research vessels (Bernard and Killworth 1973, 1974). In both cases, there was an almost palpable tension between the scientific personnel and the crew of the ship. Through both informal and unstructured interviewing on land between cruises, I was able to establish that the conflict was predictable and regular. Let me give you an idea of how complex the situation was.

In 1972–1973, it cost $5,000 a day to run a major research vessel, not including the cost of the science. (That would be about $26,000 today.) The way oceanography works, at least in the United States, the chief scientist on a research cruise has to pay for both ship time and for the cost of any experiments he or she wants to run. To do this, oceanographers compete for grants from institutions like the U.S. Office of Naval Research, NASA, and the National Science Foundation.

The spending of so much money is validated by publishing significant results in prominent journals. It’s a tough, competitive game and one that leads scientists to use every minute of their ship time. As one set of scientists comes ashore after a month at sea, the next set is on the dock waiting to set up their experiments and haul anchor.

The crew, consequently, might only get 24 or 48 hours shore leave between voyages. That can cause some pretty serious resentment by ships’ crews against scientists. And that can lead to disaster. I found many documented instances of sabotage of expensive research by crew members who were, as one of them said, ‘‘sick and tired of being treated like goddamn bus drivers.’’ In one incident, involving a British research vessel, a freezer filled with Antarctic shrimp, representing 2 years of data collection, went overboard during the night. In another, the crew and scientists from a U.S. Navy oceanographic research ship got into a brawl while in port (Science 1972:1346).

The structural problem I uncovered began at the top. Scientists whom I interviewed felt they had the right to take the vessels wherever they wanted to go, within prudence and reason, in search of answers to questions they had set up in their proposals. The captains of the ships believed (correctly) that they had the last word on maneuvering their ships at sea. Scientists, said the captains, sometimes went beyond prudence and reason in what they demanded of the vessels.

For example, a scientist might ask the captain to take a ship out of port in dangerous weather because ship time is so precious. This conflict between crew and scientists has been known—and pretty much ignored—since Charles Darwin sailed with HMS Beagle and it will certainly play a role in the productivity of long-term space station operations.

Unraveling this conflict at sea required participant observation and unstructured (as well as informal) interviewing with many people. No other strategy for data collection would have worked. At sea, people live for weeks, or even months, in close quarters, and there is a common need to maintain good relations for the organization to function well.

It would have been inappropriate for me to have used highly structured interviews about the source of tension between the crew and the scientists. Better to steer the interviews around to the issue of interest and to let informants teach me what I needed to know. In the end, no analysis was better than that offered by one engine room mechanic who told me, ‘‘These scientist types are so damn hungry for data, they’d run the ship aground looking for interesting rocks if we let them.’’

Getting Started

There are some important steps to take when you start interviewing someone for the first time. First of all, assure people of anonymity and confidentiality. Explain that you simply want to know what they think, and what their observations are. If you are interviewing someone whom you have come to know over a period of time, explain why you think their opinions and observations on a particular topic are important. If you are interviewing someone chosen from a random sample, and whom you are unlikely to see again, explain how they were chosen and why it is important that you have their cooperation to maintain representativeness.

If people say that they really don’t know enough to be part of your study, assure them that their participation is crucial and that you are truly interested in what they have to say (and you’d better mean it or you’ll never pull it off). Tell everyone you interview that you are trying to learn from them. Encourage them to interrupt you during the interview with anything they think is important. And always ask for permission to record personal interviews and to take notes. This is vital. If you can’t take notes, then, in most cases, the value of an interview plummets. (See below, on using a recorder and taking notes.)

Keep in mind that people who are being interviewed know that you are shopping for information. There is no point in trying to hide this. If you are open and honest about your intentions, and if you are genuinely interested in what people have to say, many people will help you.

This is not always true, though. When Colin Turnbull went out to study the Ik in Uganda, he found a group of people who had apparently lost interest in life and in exchanging human kindnesses. The Ik had been brutalized, decimated, and left by the government to fend for themselves on a barren reservation. They weren’t impressed with the fact that Turnbull wanted to study their culture. In fact, they weren’t much interested in anything Turnbull was up to and were anything but friendly (Turnbull 1972).

Letting the Informant or Respondent Lead

If you can carry on ‘‘unthreatening, self-controlled, supportive, polite, and cordial interaction in everyday life,’’ then interviewing will come easy to you, and informants will feel comfortable responding to your questions (Lofland 1976:90). But no matter how supportive you are as a person, an interview is never really like a casual, unthreatening conversation in everyday life. In casual conversations, people take more or less balanced turns (Spradley 1979) and there is no feeling that somehow the discussion has to stay on track or follow some theme (see also Hyman and Cobb 1975; Merton et al. 1956). In unstructured interviewing, you keep the conversation focused on a topic, while giving the respondent room to define the content of the discussion.

The rule is: Get people on to a topic of interest and get out of the way. Let the informant provide information that he or she thinks is important.

During my research on the Kalymnian sponge fishermen in Greece, I spent a lot of time at Procopis Kambouris’s taverna. (A Greek taverna is a particular kind of restaurant.) Procopis’s was a favorite of the sponge fishermen. Procopis was a superb cook, he made his own wine every year from grapes that he selected himself, and he was as good a teller of sea stories as he was a listener to those of his clientele. At Procopis’s taverna, I was able to collect the work histories of sponge fishermen—when they’d begun their careers, the training they’d gotten, the jobs they’d held, and so on. The atmosphere was relaxed (plenty of retsina wine and good things to eat), and conversation was easy.

As a participant observer, I developed a sense of camaraderie with the regulars, and we exchanged sea stories with a lot of flourish. Still, no one at Procopis’s ever made the mistake of thinking that I was there just for the camaraderie. They knew that I was writing about their lives and that I had lots of questions to ask. They also knew immediately when I switched from the role of participant observer to that of ethnographic interviewer.

One night, I slipped into just such an interview/conversation with Savas Ergas. He was 64 years old at the time and was planning to make one last 6-month voyage as a sponge diver during the coming season in 1965. I began to interview Savas on his work history at about 7:30 in the evening, and we closed Procopis’s place at about 3 in the morning. During the course of the evening, several other men joined and left the group at various times, as they would on any night of conversation at Procopis’s. Savas had lots of stories to tell (he was a living legend and he played well to a crowd), and we had to continue the interview a few days later, over several more liters of retsina.

At one point on that second night, Savas told me (almost offhandedly) that he had spent more than a year of his life walking the bottom of the Mediterranean. I asked him how he knew this, and he challenged me to document it. Savas had decided that there was something important that I needed to know and he maneuvered the interview around to make sure I learned it.

This led to about 3 hours of painstaking work. We counted the number of seasons he’d been to sea over a 46-year career (he remembered that he hadn’t worked at all during 1943 because of ‘‘something to do with the war’’). We figured conservatively the number of days he’d spent at sea, the average number of dives per trip, and the average depth and time per dive. We joked about the tendency of divers to exaggerate their exploits and about how fragile human memory is when it comes to this kind of detail.

It was difficult to stay on the subject, because Savas was such a good raconteur and a perceptive analyst of Kalymnian life. The interview meandered off on interesting tangents, but after a while, either Savas or I would steer it back to the issue at hand. In the end, discounting heavily for both exaggeration and faulty recall, we reckoned that he’d spent at least 10,000 hours—about a year and a fourth, counting each day as a full 24 hours— under water and had walked the distance between Alexandria and Tunis at least three times.

The exact numbers really didn’t matter. What did matter was that Savas Ergas had a really good sense of what he thought I needed to know about the life of a sponge diver. It was I, the interviewer, who defined the focus of the interview; but it was Savas, the respondent, who determined the content. And was I ever glad he did.

PROBING

The key to successful interviewing is learning how to probe effectively—that is, to stimulate a respondent to produce more information, without injecting yourself so much into the interaction that you only get a reflection of yourself in the data. Suppose you ask, ‘‘Have you ever been away from the village to work?’’ and the informant says, ‘‘Yes.’’ The next question (the probe) is: ‘‘Like where?’’ Suppose the answer is, ‘‘Oh, several different places.’’ The correct response is not, ‘‘Pachuca? Quere´taro? Mexico City?’’ but, ‘‘Like where? Could you name some of the places where you’ve gone to get work?’’

There are many kinds of probes that you can use in an interview. (In what follows, I draw on the important work by Briggs [1986], Dohrenwend and Richardson [1965], Gorden [1987], Hyman and Cobb [1975], Kahn and Cannell [1957], Kluckhohn [1945], Merton et al. [1956], Reed and Stimson [1985], Warwick and Lininger [1975], Whyte [1960], Whyte and Whyte [1984], and on my own experience and that of my students.)

The Silent Probe

The most difficult technique to learn is the silent probe, which consists of just remaining quiet and waiting for an informant to continue. The silence may be accompanied by a nod or by a mumbled ‘‘uh-huh’’ as you focus on your note pad. The silent probe sometimes produces more information than does direct questioning. At least at the beginning of an interview, informants look to you for guidance as to whether or not they’re on the right track. They want to know whether they’re ‘‘giving you what you want.’’ Most of the time, especially in unstructured interviews, you want the informant to define the relevant information.

Some informants are more glib than others and require very little prodding to keep up the flow of information. Others are more reflective and take their time. Inexperienced interviewers tend to jump in with verbal probes as soon as an informant goes silent. Meanwhile, the informant may be just reflecting, gathering thoughts, and preparing to say something important. You can kill those moments (and there are a lot of them) with your interruptions.

Glibness can be a matter of cultural, not just personal style. Gordon Streib reports that he had to adjust his own interviewing style radically when he left New York City to study the Navajo in the 1950s (Streib 1952). Streib, a New Yorker himself, had done studies based on semistructured interviews with subway workers in New York. Those workers maintained a fast, hard-driving pace during the interviews—a pace with which Streib, as a member of the culture, was comfortable.

But that style was entirely inappropriate with the Navajo, who were uniformly more reflective than the subway workers (Streib, personal communication). In other words, the silent probe is sometimes not a ‘‘probe’’ at all; being quiet and waiting for an informant to continue may simply be appropriate cultural behavior.

On the other hand, the silent probe is a high-risk technique, which is why beginners avoid it. If an informant is genuinely at the end of a thought and you don’t provide further guidance, your silence can become awkward. You may even lose your credibility as an interviewer. The silent probe takes practice to use effectively. But it’s worth the effort.

The Echo Probe

Another kind of probe consists of simply repeating the last thing someone has said, and asking them to continue. This echo probe is particularly useful when an informant is describing a process, or an event. ‘‘I see. The goat’s throat is cut and the blood is drained into a pan for cooking with the meat. Then what happens?’’ This probe is neutral and doesn’t redirect the interview. It shows that you understand what’s been said so far and encourages the informant to continue with the narrative. If you use the echo probe too often, though, you’ll hear an exasperated informant asking, ‘‘Why do you keep repeating what I just said?’’

The Uh-huh Probe

You can encourage an informant to continue with a narrative by just making affirmative comments, like ‘‘Uh-huh,’’ or ‘‘Yes, I see,’’ or ‘‘Right, uh-huh,’’ and so on. Matarazzo (1964) showed how powerful this neutral probe can be. He did a series of identical, semistructured, 45-minute interviews with a group of informants. He broke each interview into three 15-minute chunks. During the second chunk, the interviewer was told to make affirmative noises, like ‘‘uh-huh,’’ whenever the informant was speaking. Informant responses during those chunks were about a third longer than during the first and third periods. If you use the uh-huh or the silent probe, be sure to stay engaged and look directly at your informants.

The Tell-Me-More Probe

This may be the most common form of probe among experienced interviewers. Respondents give you an answer, and you probe for more by saying: ‘‘Could you tell me more about that?’’ Other variations include ‘‘Why exactly do you say that?’’ and ‘‘Why exactly do you feel that way?’’ You have to be careful about using stock probes like these. As Converse and Schuman point out (1974:50), if you get into a rut and repeat these probes like a robot, don’t be surprised to hear someone finishing up a nice long discourse by saying, ‘‘Yeah, yeah, and why exactly do I feel like that?’’ (I can guarantee personally that the mortification factor only allows this sort of thing to happen once. The memory of the experience lasts a lifetime.)

The Long Question Probe

Another way to induce longer and more continuous responses is by making your questions longer. Instead of asking, ‘‘How do you plant a home garden?’’ ask, ‘‘What are all the things you have to do to actually get a home garden going?’’ When I interviewed sponge divers on Kalymnos, instead of asking them, ‘‘What is it like to make a dive into very deep water?’’ I said, ‘‘Tell me about diving into really deep water. What do you do to get ready and how do you descend and ascend? What’s it like down there?’’

Later in the interview or on another occasion, I would home in on special topics. But to break the ice and get the interview flowing, there is nothing quite as useful as what Spradley (1979) called the grand tour question.

This does not mean that asking longer questions or using neutral probes necessarily produces better responses. They do, however, produce more responses, and, in general, more is better. Furthermore, the more you can keep an informant talking, the more you can express interest in what they are saying and the more you build rapport. This is especially important in the first interview you do with someone whose trust you want to build (see Spradley 1979:80). There is still a lot to be learned about how various kinds of probes affect what informants tell us.

Threatening questions—those asking for sensitive information—should be short but preceded by a long, rambling run-up: ‘‘We’re interested in the various things that people do these days in order to keep from getting diseases when they have sex. Some people do different kinds of things, and some people do nothing special. Do you ever use condoms?’ If the respondents says, ‘‘Yes,’’ or ‘‘No,’’ or ‘‘Sometimes,’’ then you can launch that series of questions about why, why not, when, with whom, and so on. The wording of sensitive questions should be supportive and nonjudgmental. (See below for more on threatening questions.)

Probing by Leading

After all this, you may be cautious about being really directive in an interview. Don’t be. Many researchers caution against ‘‘leading’’ an informant. Lofland (1976), for example, warns against questions like, ‘‘Don’t you think that . . . ?’’ and suggests asking, ‘‘What do you think about . . . ?’’ He is, of course, correct. On the other hand, any question an interviewer asks leads an informant. You might as well learn to do it well.

Consider this leading question that I asked a N^˜ a¨hn˜u Indian: ‘‘Right. I understand. The compadre is supposed to pay for the music for the baptism fiesta. But what happens if the compadre doesn’t have the money? Who pays then?’’ This kind of question can stop the flow of an informant’s narrative stone dead. It can also produce more information than the informant would otherwise have provided. At the time, I thought the informant was being overly ‘‘normative.’’ That is, I thought he was stating an ideal behavioral custom (having a compadre pay for the music at a fiesta) as if it were never violated.

It turned out that all he was doing was relying on his own cultural competence— ‘‘abbreviating,’’ as Spradley (1979:79) called it. The informant took for granted that the anthropologist knew the ‘‘obvious’’ answer: If the compadre didn’t have enough money, well, then there might not be any music.

My interruption reminded the informant that I just wasn’t up to his level of cultural competence; I needed him to be more explicit. He went on to explain other things that he considered obvious but that I would not have even known to ask about. Someone who has committed himself to pay for the music at a fiesta might borrow money from another compadre to fulfill the obligation. In that case, he wouldn’t tell the person who was throwing the fiesta. That might make the host feel bad, like he was forcing his compadre to go into debt.

In this interview, in fact, the informant eventually became irritated with me because I asked so many things that he considered obvious. He wanted to abbreviate a lot and to provide a more general summary; I wanted details. I backed off and asked a different informant for the details. I have since learned to start some probes with ‘‘This may seem obvious, but . . .’’ (box 8.2).

BOX 8.2

L I S T E N F O R W H A T ’ S L E F T O U T

Informants abbreviate all the time, and this means that you have to listen carefully for what’s left out, not just what’s in the interview narrative. Laurie Price (1987) collected tales of misfortune from very poor people in Quito, Ecuador. In one story, Maria talks about her crippled 6-year-old daughter. As Price tells it, Maria does not mention that, for months, she carried her daughter every day ‘‘down a 200-step flight of public stairs and 4 blocks to the nearest bus stop so the girl could go to physical therapy’’ (p. 318). The child’s father, it turns out, drives a bus that he parks every night next to their house, but during the Herculean effort to help the daughter, the father never pitches in or rearranges his schedule. ‘‘Such efforts are the unmarked case for mothers,’’ says Price (p. 319).

Directive probes (leading questions) may be based on what an informant has just finished saying, or may be based on something an informant told you an hour ago or a week ago. As you progress in long-term research, you come to have a much greater appreciation for what you really want from an interview. It is perfectly legitimate to use the information you’ve already collected to focus your subsequent interviews.

This leads researchers from informal to unstructured to semistructured interviews and even to completely structured interviews like questionnaires. When you feel as though you have learned something important about a group and its culture, the next step to test that knowledge—to see if it is idiosyncratic to a particular informant or subgroup in the culture or if it can be reproduced in many informants.

Baiting: The Phased-Assertion Probe

A particularly effective probing technique is called phased assertion (Kirk and Miller 1986), or baiting (Agar 1996:142). This is when you act like you already know something to get people to open up.

I used this technique in a study of how N^˜ a¨hn˜u Indian parents felt about their children learning to read and write N^˜ a¨hn˜u. Bilingual (Spanish-Indian) education in Mexico is a politically sensitive issue (Heath 1972), and when I started asking about it a lot of people were reluctant to talk freely.

In the course of informal interviewing, I learned from a schoolteacher in one village that some fathers had come to complain about the teacher trying to get the children to read and write N^˜ a¨hn˜u. The fathers, it seems, were afraid that studying N^˜ a¨hn˜u would get in the way of their children becoming fluent in Spanish. Once I heard this story, I began to drop hints that I knew the reason parents were against children learning to read and write N^˜ a¨hn˜u. As I did this, the parents opened up and confirmed what I’d found out.

Every journalist (and gossip monger) knows this technique well. As you learn a piece of a puzzle from one informant, you use it with the next informant to get more information, and so on. The more you seem to know, the more comfortable people feel about talking to you and the less people feel they are actually divulging anything. They are not the ones who are giving away the ‘‘secrets’’ of the group.

Phased assertion also prompts some informants to jump in and correct you if they think you know a little but that you’ve ‘‘got it all wrong.’’ In some cases, I’ve purposely made wrong assertions to provoke a correcting response.

Verbal Respondents

Some people try to tell you too much. They are the kind of people who just love to have an audience. You ask them one little question and off they go on one tangent after another, until you become exasperated. Converse and Schuman (1974:46) recommend ‘‘gentle inattention’’—putting down your pen, looking away, leafing through your papers. Nigel King (1994:23) recommends saying something like: ‘‘That’s very interesting. Could we go back to what you were saying earlier about . . .’

You may, however, have to be a bit more obvious. New interviewers, in particular, may be reluctant to cut off informants, afraid that doing so is poor interviewing technique. In fact, as William Foote Whyte notes, informants who want to talk your ear off are probably used to being interrupted. It’s the only way their friends get a word in edgewise. But you need to learn how to cut people off without rancor. ‘‘Don’t interrupt accidentally . . . ,’’ Whyte said, ‘‘learn to interrupt gracefully’’ (1960:353, emphasis his). Each situation is somewhat different; you learn as you go in this business.

Nonverbal Respondents

One of the really tough things you run into is someone telling you ‘‘I don’t know’’ in answer to lots of questions. In qualitative research projects, where you choose respondents precisely because you think they know something of interest, the ‘‘don’t know’’ refrain can be especially frustrating. Converse and Schuman (1974:49) distinguish four kinds of don’t-know response: (1) I don’t know (and frankly I don’t care); (2) I don’t know (and it’s none of your business); (3) I don’t know (actually, I do know, but you wouldn’t be interested in what I have to say about that); and (4) I don’t know (and I wish you’d change the subject because this line of questioning makes me really uncomfortable). There is also the ‘‘(I wish I could help you but) I really don’t know.’’

Sometimes you can get beyond this, sometimes you can’t. You have to face the fact that not everyone who volunteers to be interviewed is a good respondent. If you probe those people for information when they say, ‘‘I don’t know,’’ you tempt them to make something up just to satisfy you, as Sanchez and Morchio (1992) found. Sometimes, you just have to take the ‘‘don’t know’’ for an answer and cut your losses by going on to someone else (box 8.3).

LEARNING TO INTERVIEW

It’s impossible to eliminate reactivity and subjectivity in interviewing, but like any other craft, you get better and better at interviewing the more you practice. It helps a lot to practice in front of others and to have an experienced interviewer monitor and criticize your performance. Even without such help, however, you can improve your interviewing technique just by paying careful attention to what you’re doing. Harry Wolcott (1995) offers excellent advice on this score: Pay as much attention to your own words as you do to the words of your respondents (p. 102).

Wolcott also advises: Keep interviews focused on a few big issues (1995:112). More good advice from one of the most accomplished ethnographers around. Here’s a guaranteed way to wreck rapport and ruin an interview: An informant asks you, ‘‘Why do you ask? What does that have to do with what we’re talking about?’’ You tell her: ‘‘Well, it just seemed like an interesting question—you know, something I thought might be useful somehow down the road in the analysis.’

Here you are, asking people to give you their time and tell you about their lives and you’re treating that time with little respect. If you can’t imagine giving a satisfactory answer to the question: ‘‘Why did you ask that?’’ then leave that out.

Do not use your friends as practice informants. You cannot learn to interview with friends because there are role expectations that get in the way. Just when you’re really rolling, and getting into probing deeply on some topic that you both know about, they are likely to laugh at you or tell you to knock it off.

Practice interviews should not be just for practice. They should be done on topics you’re really interested in and with people who are likely to know a lot about those topics. Every interview you do should be conducted as professionally as possible and should produce useful data (with plenty of notes that you can code, file, and cross-file).

The Importance of Language

Most anthropologists (and an increasing number of sociologists and social psychologists) do research outside their own country. If you are planning to go abroad for research, find people from the culture you are going to study and interview them on some topic of interest. If you are going to Turkey to study women’s roles, then find Turkish students at your university and interview them on some related topic.

It is often possible to hire spouses of foreign students for these kinds of ‘‘practice’ interviews. I put ‘‘practice’’ in quotes to emphasize again that these interviews should

BOX 8.3

T H E E T H I C S O F P R O B I N G

Are these tricks of the trade ethical? Peter Collings (2009) asked Inuit hunters: ‘‘Name all of the people you share country food with.’’ The response was usually a very short list, so, when informants stopped listing names, Collings would ask ‘‘What about your x? Surely you share food with your x,’’ where x was a category of relative in Innuinaqtun, the local language. This, said Collings, reminded people that he had command of the kinship terminology and that he knew his informant had an x. Later in the interview, Collings would refer to one of the people whom the informant had named and say ‘‘So-and-so is your older brother,’’ using the Innuinaqtun term. ‘‘Just as the fieldworker is studying the community,’’ says Collings, ‘‘so, too, is the community studying the fieldworker’’ to find out if he or she is culturally competent (pp. 149–50). By demonstrating cultural competence, Collings argues, phased assertion helps establish rapport—at least where he works (p. 139).

Still, getting people to open up creates responsibilities for your informants. First, there is no ethical imperative in social research more important than seeing to it that you do not harm innocent people who have provided you with information in good faith. Not all respondents are innocents, though. Some people commit wartime atrocities. Some practice infanticide. Some are HIVpositive and, out of bitterness, are purposely infecting others. Do you protect them all? Are any of these examples more troublesome to you than others? These are not extreme cases, thrown in here to prepare you for the worst, ‘‘just in case.’’ They are the sorts of ethical dilemmas that field researchers confront all the time.

Second, the better you get at making people open up, the more responsible you become that they don’t later suffer some emotional distress for having done so. Informants who divulge too quickly what they believe to be secret information can later come to have real regrets and even loss of self-esteem. They may suffer anxiety over how much they can trust you to protect them in the community.

It is sometimes better to stop an informant from divulging privileged information in the first or second interview and to wait until both of you have built a mutually trusting relationship. If you sense that an informant is uncomfortable with having spoken too quickly about a sensitive topic, end the interview with light conversation and reassurances about your discretion. Soon after, look up the informant and engage in light conversation again, with no probing or other interviewing techniques involved. This will also provide reassurance of trust.

Remember: The first ethical decision you make in research is whether to collect certain kinds of information at all. Once that decision is made, you are responsible for what is done with that information, and you must protect people from becoming emotionally burdened for having talked to you.

produce real data of real interest to you. If you are studying a language that you’ll need for research, these practice interviews will help you sharpen your skills at interviewing in that language.

Even if you are going off to the interior of the Amazon, this doesn’t let you off the hook. It is unlikely that you’ll find native speakers of Yanomami on your campus, but you cannot use this as an excuse to wait until you’re out in the field to learn general interviewing skills. Interviewing skills are honed by practice. Among the most constructive things you can do in preparing for field research is to practice conducting unstructured and semistructured interviewing. Learn to interview in Portuguese or Spanish (depending on whether the Yanomami you are going to visit live in the Brazilian or Venezuelan Amazon) before heading for the field and you’ll be way ahead. (See the section on language in chapter 12 for more on using interpreters.)

Pacing the Study

Two of the biggest problems faced by researchers who rely heavily on semistructured interviews are boredom and fatigue. Even small projects may require 30–40 interviews to generate sufficient data to be worthwhile. Most field researchers collect their own interview data, and asking the same questions over and over again can get pretty old. Gorden (1987) studied 30 interviewers who worked for 12 days doing about two tape-recorded interviews per day. Each interview was from 1 to 2 hours long.

The first interview on each day, over all interviewers, averaged about 30 pages of transcription. The second averaged only 25 pages. Furthermore, the first interviews, on average, got shorter and shorter during the 12-day period of the study. In other words, on any given day, boredom made the second interview shorter, and over the 12 days boredom (and possibly fatigue) took its toll on the first interviews of each day.

Even anthropologists who spend a year in the field may have focused bouts of interviewing on a particular topic. Plan each project, or subproject, in advance and calculate the number of interviews you are going to get. Pace yourself. Spread the project out if possible, and don’t try to bring in all your interview data in the shortest possible time— unless you’re studying reactions to a hot issue, in which case, spreading things out can create a serious history confound (see chapter 4).

Here’s the tradeoff: The longer a project takes, the less likely that the first interviews and the last interviews will be valid indicators of the same things. In long-term, participant observation fieldwork (6 months to a year), I recommend going back to your early informants and interviewing them a second time. See whether their observations and attitudes have changed, and if so, why.

PRESENTATION OF SELF

How should you present yourself in an interview? As a friend? As a professional? As someone who is sympathetic or as someone who is nonjudgmental? It depends on the nature of the project. When the object is to collect comparable data across respondents, then it makes no difference whether you’re collecting words or numbers—cordial-butnonjudgmental is the way to go.

That’s sometimes tough to do. You’re interviewing someone on a project about what people can do to help the environment, and your respondent says: ‘‘All those eco-Nazis want is to make room for more owls. They don’t give a damn about real people’s jobs.’ (Yes, that happened on one of my projects.) That’s when you find out whether you can probe without injecting your feelings into the interview. Professional interviewers (the folks who collect the data for the General Social Survey, for example) learn to maintain their equilibrium and move on (see Converse and Schuman 1974).

Some situations are so painful, however, that it’s impossible to maintain a neutral facade. Gene Shelley interviewed 72 people in Atlanta, Georgia, who were HIV-positive (Shelley et al. 1995). Here’s a typical comment by one of Shelly’s informants: ‘‘I have a lot of trouble watching all my friends die. Sometimes my whole body shuts down inside. I don’t want to know people who are going to die. Some of my friends, there are three or four people a week in the obits. We all watch the obits.’

How would you respond? Do you say: ‘‘Uh-huh. Tell me more about that’’? Do you let silence take over and force the respondent to go on? Do you say something sympathetic? Shelley reports that she treated each interview as a unique situation and responded as her intuition told her to respond—sometimes more clinically, sometimes less, depending on her judgment of what the respondent needed her to say. Good advice.

On Just Being Yourself

In 1964, when we were working on the island of Kalymnos, my wife Carole would take our 2-month-old baby for daily walks in a carriage. Older women would peek into the baby carriage and make disapproving noises when they saw our daughter sleeping on her stomach. Then they would reach into the carriage and turn the baby over, explaining forcefully that the baby would get the evil eye if we continued to let her sleep on her stomach.

Carole had read the latest edition of The Commonsense Book of Baby and Child Care (the classic ‘‘baby book’’ by Dr. Benjamin Spock). We carried two copies of the book with us—in case one fell out of a boat or something—and Carole was convinced by Dr. Spock’s writings that babies who sleep on their backs risk choking on their own mucous or vomit. Since then, medical opinion—and all the baby books that young parents read nowadays— have flip-flopped about this issue several times. At the time, though, not wanting to offend anyone, Carole listened politely and tried to act nonjudgmental.

One day, enough was enough. Carole told off a woman who intervened and that was that. From then on, women were more eager to discuss child-rearing practices in general. When we let our baby crawl around on the floor and didn’t bundle her up when we took her out for walks, Greek mothers were unhesitant in telling us that they disapproved. The more we challenged them, the more they challenged us. There was no rancor involved, and we learned a lot more than if Carole had just kept on listening politely and had said nothing. This was informal interviewing in the context of long-term participant observation. If we had offended anyone, there would have been time and opportunity to make amends—or at least come to an understanding about cultural differences.

Little Things Mean a Lot

Little things are important in interviewing, so pay attention to them. How you dress and where you hold an interview, for example, tell your respondent a lot about you and what you expect. The ‘‘interviewing dress code’’ is: Use common sense. Proper dress depends on the venue. Showing up with a backpack or an attache´ case, wearing jeans or a business suit—these are choices that should be pretty easy to make once you’ve made the commitment to accommodate your dress to different circumstances.

Same goes for venue. I’ve held interviews in bars, in business offices, in government offices, on ferry boats, on beaches, in homes. . . . I can’t give you a rule for selecting the single right place for an interview, since there may be several right places. But some places are just plain wrong for certain interviews. Here again, common sense goes a long way (Further Reading: interviewing).

USING A VOICE RECORDER

Don’t rely on your memory in interviewing; use a voice recorder in all structured and semistructured interviews, except where people specifically ask you not to. If you sense some reluctance about the recorder, leave it on the table and don’t turn it on right away. Start the interview with chitchat and when things get warmed up, say something like ‘‘This is really interesting. I don’t want to trust my memory on something as important as this; do you mind if I record it?’’ Charles Kadushin (personal communication) hands people a microphone with a shut-off switch. Rarely, he says, do respondents actually use the switch, but giving people control over the interview shows that you take them very seriously.

Sometimes you’ll be recording an interview and things will be going along just fine and you’ll sense that a respondent is backing off from some sensitive topic. Just reach over to the recorder and ask the respondent if she or he would like you to turn it off. Harry Wolcott (1995:114) recommends leaving the recorder on, if possible, when the formal part of an interview ends. Even though you’ve finished, Wolcott points out, your respondent may have more to say.

Recording Equipment

For simple recording and transcribing of interviews, in a language you understand well, you can get away with a basic audio recorder for under $50. (But buy two of them. When you skimp on equipment costs, and don’t have a spare, this almost guarantees that you’ll need one at the most inconvenient moment.) Basic recorders, with 256mb of flash memory hold about 150 hours of voice recording. You can also use your iPod as a digital audio recorder with a plug-in microphone. A gigabyte of disk space holds about 400 hours of voice recordings, so an 80-gigabyte iPod has plenty of room for both music and interviews.

Whatever kind of work you do, remember to upload your data regularly to a computer and to store your data in several places—CDs, external hard drives, or online. And if you are in an isolated field site and don’t have reliable power, take along a solar battery charger so you can get your data offline and onto a CD.

Some of the better voice recorders come with up to four built-in microphones that capture 360-degree sound. If you use a low-end recorder, then use a good, separate microphone. Some people like wearing a lavalier microphone—the kind you clip to a person’s lapel or shirt collar—but many people find them intrusive. I prefer omnidirectional microphones because they pick up voices from anywhere in a room. Sometimes, people get rolling on a topic and they want to get up and pace the room as they talk. Want to kill a really great interview? Tell somebody who’s on a roll to please sit down and speak directly into the mike. Good microphones come with stands that keep the head from resting on any surface, like a table. Surfaces pick up and introduce background noise into any recording. If you don’t have a really good stand for the mike, you can make one easily with some rubbery foam (the kind they use in making mattresses).

Test your recorder before every interview. And do the testing at home. There’s only one thing worse than a recorder that doesn’t run at all. It’s one that runs but doesn’t record. Then your informant is sure to say at the end of the interview: ‘‘Let’s run that back and see how it came out!’’ (Yes, that happened to me. But only once. And it needn’t happen to anyone who reads this.)

Pay attention to the battery indicator. Want another foolproof way to kill an exciting interview? Ask the informant to ‘‘please hold that thought’’ while you change batteries. When batteries get slightly low, throw them out or recharge them. If you are working in places that have unstable current, you’ll rely on batteries to ensure recording fidelity. Just make sure that you start out with fresh batteries for each interview. (You can save a lot of battery life by using house current for all playback, fast forward, and rewind operations— reserving the batteries only for recording.) If you prefer household current for recording, then carry along a couple of long extension cords so you have a choice of where to set up for the interview. (See Ives [1995] for more good tips.)

In voice activation mode, the recorder only turns off during long pauses—while an informant is thinking, for example. Holly Williams (personal communication) recommends not using the voice activation feature for interviews. She finds that the long breaks without any sound make transcribing easier. You don’t have to shut the machine off and turn it on as many times while you’re typing.

Transcribers and VR software

It takes 6–8 hours to transcribe 1 hour of a recorded interview, depending on how closely you transcribe (getting all the ‘‘uhs’’ and ‘‘ers’’ and throat clearings, or just capturing the main elements of speech), how clear the recording is, and how proficient you are in the language and in typing. If you have to transcribe interviews yourself, there are several choices for equipment. Transcription software lets you control the recorder (start, stop, move forward and backward) using the keyboard. Transcriber machines let you do this using a foot pedal. This lets you listen to a couple of seconds of recording at a time, type everything into the computer, and then move on to the next chunk. The technology lets you go back and repeat chunks, all while keeping your hands on the keyboard.

With voice recognition (VR) software, you listen to an interview through a set of headphones and repeat the words—both your questions and your informant’s responses—out loud, in your own voice. The software listens to your voice and types out the words across the screen. You go over each sentence to correct mistakes (tell it that the word ‘‘bloat’’ should be ‘‘float’’ for instance) and to format the text (tell it where to put punctuation and paragraph breaks). The process is slow at first, but the software learns over time to recognize inflections in your voice, and it makes fewer and fewer mistakes as weeks go by. It also learns all the special vocabulary you throw at it. The built-in vocabularies of current VRS systems are enormous—something like 300,000 words—but, though they may be ready to recognize polygamy, for example, you’ll have to teach it polygyny or fraternal polyandry and words from the language of your field site. So, if you say, ‘‘Juanita sold eight huipiles at the market this week,’’ you’ll have to spell out ‘‘Juanita’’ and ‘‘huipiles’’ so the software can add these words to its vocabulary.

As the software gets trained, the process moves up to 95%–98% accuracy at about 100–120 words per minute. With a 2%–5% error rate, you still have to go over every line of your work to correct it, but the total time for transcribing interviews can be reduced by half or more. (More about VR software in appendix E) (Further Reading: transcription).

Recording Is Not a Substitute for Taking Notes

Finally, never substitute recording for note taking. Take notes during the interview about the interview. Did the informant seem nervous or evasive? Were there a lot of interruptions? What were the physical surroundings like? How much probing did you have to do? Take notes on the contents of the interview, even though you get every word on the machine.

A few informants will let you use a recorder but will balk at your taking notes. Don’t assume, however, that informants will be offended if you take notes. Ask them. Most of the time, all you do by avoiding note taking is lose a lot of data. Informants are under no illusions about what you’re doing. You’re interviewing them. You might as well take notes and get people used to it, if you can.

FOCUS GROUPS

Focus groups are recruited to discuss a particular topic—anything from people’s feelings about brands of beer to their experience in toilet training their children. The method derives from work by Paul Lazarsfeld and Robert Merton in 1941 at Columbia University’s Office of Radio Research. A group of people listened to a recorded radio program that was supposed to raise public morale prior to America’s entry into World War II. The listeners were told to push a red button whenever they heard something that made them react negatively and to push a green button when they heard something that made them react positively. The reactions were recorded automatically by a primitive polygraph-like apparatus. When the program was over, an interviewer talked to the group of listeners to find out why they had felt positively or negatively about each message they’d reacted to (Merton 1987) (box 8.4).

BOX 8.4

N O T A L L G R O U P I N T E R V I E W S A R E F O C US G R O UP I N T E R V I E W S

Sometimes, you just find yourself in an interview situation with a lot of people. You’re interviewing someone and other people just come up and insert themselves into the conversation. This happens spontaneously all the time in longterm fieldwork in small communities, where people all know one another. Rachel Baker (1996a, 1996b), for example, studied homeless boys in Kathmandu. When she interviewed boys in temples or junkyards, others might come by and be welcomed into the conversation-interview situation. If you insist on privacy, you might find yourself with no interview at all. Better to take advantage of the situation and just let the information flow. Just be sure to take notes on who’s there, who’s dominant, who’s just listening, and so on, in any group interview.

The commercial potential of Lazarsfeld and Merton’s pioneering work was immediately clear. The method of real-time recording of people’s reactions, combined with focused interviewing of a group, is today a mainstay in advertising research and product design. MCI, the now defunct long-distance phone company, used focus groups to develop their advertising when they were just starting out. They found that customers didn’t blame AT&T for the high cost of their long-distance phone bills; they blamed themselves for talking too long on long-distance calls. MCI came out with the advertising slogan: ‘‘You’re not talking too much, just spending too much.’’ The rest, as they say, is history (Krueger 1994:33).

Why Are Focus Groups So Popular?

The focus group method was a commercial success from the 1950s on, but it lay dormant in academic circles for more than 20 years. This is probably because the method is virtually devoid of statistics. Beginning in the late 1970s, however, interest among social researchers of all kinds boomed as researchers came to understand the benefits of combining qualitative and quantitative methods.

Focus groups do not replace surveys, but rather complement them. You can convene a focus group to discuss questions for a survey. Do the questions seem arrogant to respondents? Appropriate? Naive? A focus group can discuss the wording of a particular question or offer advice on how the whole questionnaire comes off to respondents. And you can convene a focus group to help interpret the results of a survey. But focus groups are not just adjuncts to surveys. They are widely used to find out why people feel as they do about something or the steps people go through in making decisions.

Two Cases of Focus Groups

Knodel et al. (1984), for example, used focus groups to study the fertility transition in Thailand. They held separate group sessions for married men under 35 and married women under 30 who wanted three or fewer children. They also held separate sessions for men and women over 50 who had at least five children. This gave them four separate groups. In all cases, the participants had no more than an elementary school education.

Knodel et al. repeated this four-group design in six parts of Thailand to cover the religious and ethnic diversity of the country. The focus of each group discussion was on the number of children people wanted and why.

Thailand was going through fertility transition in the 1980s, and the focus group study illuminated the reasons for the transition. ‘‘Time and again,’’ these researchers report, ‘‘when participants were asked why the younger generation wants smaller families than the older generation had, they responded that nowadays everything is expensive’’ (Knodel et al. 1984:302).

People also said that all children, girls as well as boys, needed education to get the jobs that would pay for the more expensive, monetized lifestyle to which people were then becoming accustomed. It is, certainly, easier to pay for the education of fewer children. These consistent responses are what you’d expect in a society undergoing fertility transition.

Ruth Wilson et al. (1993) used focus groups in their study of acute respiratory illness (ARI) in Swaziland. They interviewed 33 individual mothers, 13 traditional healers, and 17 health care providers. They also ran 33 focus groups: 16 male groups and 17 female groups. The groups had from 4 to 15 participants, with an average of 7.

Each individual respondent and each group was presented with two hypothetical cases. Wilson et al. asked their respondents to diagnose each case and to suggest treatments. Here are the cases:

Case 1. A mother has a 1-year-old baby girl with the following signs: coughing, fever, sore throat, running or blocked nose, and red or teary eyes. When you ask the mother, she tells you that the child can breast-feed well but is not actively playing.

Case 2. A 10-month-old baby was brought to a health center with the following signs: rapid/difficult breathing, chest indrawing, fever for one day, sunken eyes, coughing for three days. The mother tells you that the child does not have diarrhea but has a poor appetite.

Many useful comparisons were possible with the data from this study. For example, mothers attributed the illness in Case 2 mostly to the weather, heredity, or the child’s home environment. The male focus groups diagnosed the child in Case 2 as having asthma, fever, indigestion, malnutrition, or worms.

Wilson et al. (1993) acknowledge that a large number of individual interviews make it easier to estimate the degree of error in a set of interviews. However, they conclude that the focus groups provided valid data on the terminology and practices related to ARI in Swaziland. Wilson and her coworkers did, after all, have 240 respondents in their focus groups; they had data from in-depth interviews of all categories of persons involved in treating children’s ARI; and they had plenty of participant observation in Swaziland to back them up.

Note some very important things about these studies. First, neither of them was based on a single focus group but on a series offocus groups. Second, in both studies, the groups were homogeneous with respect to certain independent variables—gender, number of children desired or produced, ethnicity—just as we saw with respect to experimental and sampling design. Finally, in the study by Knodel et al., the 24 groups were chosen to represent a subgroup in a factorial design—again just as we saw with experiments in chapter 4 and with sampling design in chapter 5. In other words, these focus group studies were designed to provide not only in-depth data about the reasons behind people’s behavior, but data that could be systematically compared across groups.

Are Focus Groups Valid?

Ward et al. (1991) compared focus group and survey data from three studies of voluntary sterilization (tubal ligation or vasectomy) in Guatemala, Honduras, and Zaire. Ward et al. report that, ‘‘Overall, for 28% of the variables the results were similar’’ in the focus group and survey data. ‘‘For 42% the results were similar but focus groups provided additional detail; for 17% the results were similar, but the survey provided more detail. And in only 12% of the variables were the results dissimilar’’ (p. 273).

In the Guatemala study, 97% of the women surveyed reported no regrets with their decision to have a tubal ligation. The ‘‘vast majority’’ of women in the focus groups also reported no regrets. This was counted as a ‘‘similar result.’’ Ten percent of the women surveyed reported having had a tubal ligation for health reasons. In the focus groups, too, just a few women reported health factors in their decision to have the operation, but they provided more detail and context, citing such things as complications from previous pregnancies.

This is an example of where the focus group and survey provide similar results, but where the focus group offers more detail. Data from the focus groups and the survey confirm that women heard about the operation from similar sources, but the survey shows that 40% of the women heard about it from a sterilized woman, 26% heard about it from a health professional, and so on. Here, the survey provides more detail, though both methods produce similar conclusions.

Gillespie (1992) compared the results of four focus groups with data from a survey of the same population and found that results were dissimilar in 18% of the variables. The bottom line: Focus groups—like participant observation, in-depth interviews, and other systematic qualitative methods—should be used for the collection of data about content and process and not for estimating population parameters of personal attributes. The belief that a woman has or does not have a right to an abortion is a personal attribute, like gender, age, annual income, or religion. If you want to estimate the proportion of people in a population who believe that a woman has a right to an abortion, then focus groups are not the method of choice.

A proportion is a number, and if you want a good number—a valid one, a useful one—you need a method that produces exactly that. A survey, based on a representative sample, is the method of choice here. But if you want information about content—about why people think a woman should or should not have the right to an abortion—then that’s just the sort of thing a focus group can illuminate.

RUNNING A FOCUS GROUP

The group moderator gets people talking about whatever issue is under discussion. Leading a focus group requires the combined skills of an ethnographer, a survey researcher, and a therapist. You have to watch out for people who want to show off and close them down without coming on too strongly. You have to watch out for shy people and draw them out, without being intimidating. Tips on how to do all this, and a lot more, are in The Focus Group Kit, a series of six how-to books (D. L. Morgan and Krueger 1998). Don’t even think about getting into focus group management without going through this kit (box 8.5).

BOX 8.5

C O M P O S I T I O N O F A F O C U S G R O U P

Focus groups typically have 6–12 members, plus a moderator. Seven or 8 people is a popular size. If a group is too small, it can be dominated by 1 or 2 loudmouths; if it gets beyond 10 or 12, it gets tough to manage. Smaller groups are better when you’re trying to get really in-depth discussions going about sensitive issues (D. L. Morgan 1997). Of course, this assumes that the group is run by a skilled moderator who knows how to get people to open up and how keep them opened up.

The participants in a focus group should be more or less homogeneous and, in general, should not know one another. Richard Krueger, a very experienced focus group moderator, says that ‘‘familiarity tends to inhibit disclosure’’ (1994:18). It’s easy to open up more when you get into a discussion with people whom you are unlikely ever to see again (sort of like what happens on long air flights). Obviously, what ‘‘homogeneous’’ means depends on what you’re trying to learn. If you want to know why a smaller percentage of middle-class African American women over 40 get mammograms than do their white counterparts, then you need a group of middle-class African American women who are over 40.

In a focus group about sensitive issues like abortion or drug use, the leader works at getting the group to gel and getting members to feel that they are part of an understanding cohort of people. If the group is run by an accomplished leader, one or more members will eventually feel comfortable about divulging sensitive information about themselves. Once the ice is broken, others will feel less threatened and will join in. Moderators should not be known to the members of a focus group, and focus group members should not be employees of a moderator. Hierarchy is not conducive to openness.

In running a focus group, remember that people will disclose more in groups that are supportive and nonjudgmental. Tell people that there are no right or wrong answers to the questions you will ask and emphasize that you’ve invited people who are similar in their backgrounds and social characteristics. This, too, helps people open up (Krueger 1994:113).

Above all, don’t lead too much and don’t put words in people’s mouths. In studying nutritional habits, don’t ask a focus group why they eat or don’t eat certain foods; do ask them to talk about what kinds of foods they like and dislike and why. In studying risky sexual behavior, don’t ask, ‘‘Do you use condoms whenever you visit a prostitute?’’; do ask people to talk about their experience with prostitutes and exactly what kind of sexual practices they prefer. Your job is to keep the discussion on the topic. Eventually, people will hit on the nutritional habits or the sexual acts that interest you, and you can pick up the thread from there.

Analyzing Data from Focus Groups

You can analyze focus group data with the same techniques you would use on any corpus of text: field notes, life histories, open-ended interviews, and so on. As with all large chunks of text, you have two choices for very different kinds of analysis. You can do formal content analysis, or you can do qualitative analysis. See chapters 18 and 19 for more about this.

As with in-depth interviews, it’s best to record (or videotape) focus groups. This is a bit tricky, though, because any audio of a focus group, whether digital or tape, is hard to understand and transcribe if two or more people talk at once. A good moderator keeps people talking one at a time. Don’t hide the recorder or the microphones. Someone is sure to ask if they’re being recorded, and when you tell them, ‘‘Yes’’—which you must do—they’re sure to wonder why they had to ask.

If you are just trying to confirm some ideas or to get a general notion of how people feel about a topic, you can simply take notes from the audio and work with your notes. Most focus groups, however, are transcribed. The real power of focus groups is that they produce ethnographically rich data. Only transcription captures a significant part of that richness. But be prepared to work with a lot of information. Any single hour-and-a-half focus group can easily produce 50 pages or more of text.

Many focus groups have two staff members: a moderator and a person who does nothing but jot down the name of each person who speaks and the first few words they say. This makes it easier for a transcriber to identify the voices. If you can’t afford this, or if you feel that people would be uncomfortable with someone taking down their names, you can call on people by name, or mention their name when you respond to them. Things can get rolling in a focus group (that’s what you want), and you’ll have a tough time transcribing the audio if you don’t know who’s talking (Further Reading: focus groups).

RESPONSE EFFECTS

Response effects are measurable differences in the responses of people being interviewed that are predictable from characteristics of the interviewers and those being interviewed— like whether the sex or race or age of interviewer and of the respondent are the same or different—and dozens of other things (box 8.6).

As early as 1929, Stuart Rice showed that the political orientation of interviewers can effect what they report people told them. Rice was doing a study of derelicts in flop houses

BOX 8.6

T H E E X P E C T A N C Y E F F E C T

In 1966, Robert Rosenthal and Lenore Jacobson (1968) conducted an experiment. At the beginning of the school year, they told some teachers at a school that the children they were about to get had tested out as ‘‘spurters.’’ That is, according to tests, they said, those particular children were expected to make significant gains in their academic scores during the coming year. Sure enough, those children did improve dramatically—which was really interesting, because Rosenthal and Jacobson had matched the ‘‘spurter’’ children and teachers at random.

This experiment showed the power of the expectancy effect, or ‘‘the tendency for experimenters to obtain results they expect, not simply because they have correctly anticipated nature’s response but rather because they have helped to shape that response through their expectations’’ (Rosenthal and Rubin 1978:377).

Strictly speaking, the expectancy effect is not a response effect at all. But for fieldworkers, it is an important effect to keep in mind. If you are studying a small community, or a neighborhood in a city, or a hospital or clinic for a year or more, interacting daily with a few key informants, your own behavior can affect theirs in subtle (and not so subtle) ways, and vice versa. Don’t be surprised if you find your own behavior changing over time in relation to key informants.

and he noticed that the men contacted by one interviewer consistently said that their down-and-out status was the result of alcohol; the men contacted by the other interviewer blamed social and economic conditions and lack of jobs. It turned out that the first interviewer was a prohibitionist and the second was a socialist (cited in Cannell and Kahn 1968:549). Katz (1942) found that middle-class interviewers got more politically conservative answers in general from lower-class respondents than did lower-class interviewers, and Robinson and Rhode (1946) found that interviewers who looked non-Jewish and had non-Jewish-sounding names were almost four times more likely to get anti-Semitic answers to questions about Jews than were interviewers who were Jewish looking and who had Jewish-sounding names.

Since these pioneering efforts, hundreds of studies have been conducted on the impact of things like race, sex, age, and accent of both the interviewer and the informant; features of the environment where the interview takes place (like whether the interview is done in private or in the presence of a third party); the nature of the task that people are asked to perform (like whether the respondent is asked to write out an answer, in text, or to just circle a number on a form); the mode of the interview (like comparing face-to-face, telephone, and Internet interviews about the same topic).

Sex-of-interviewer effects have been the focus of many studies. Hyman and Cobb (1975), for example, found that female interviewers who took their cars in for repairs themselves (as opposed to having their husbands do it) were more likely to have female respondents who reported getting their own cars repaired. Zehner (1970) found that when women in the United States were asked by women interviewers about premarital sex, they were more inhibited than if they were asked by men. Male respondents’ answers were not affected by the gender of the interviewer. McCombie and Anarfi (2002) found the same sex-of-interviewer effect 30 years later in Ghana: Young men (15–18 year olds) were equally likely to tell male or female interviewers that they had had sex, but young women were more likely to divulge this to male interviewers than to female interviewers. In the Tamang Family Research Project in Nepal, William Axinn (1991) found that women were simply better than men as interviewers: The female interviewers had significantly fewer ‘‘don’t know’’ responses than did the male interviewers. Axinn supposes this might be because the survey dealt with marital and fertility histories. In a multi-year study in Kenya of women’s networks and their AIDS-related behavior, Alex Weinreb (2006) found that the most reliable data were collected by female-insider interviewers—that is, women from the local area who were trained to be interviewers for the project— compared to the stranger-interviewers who were brought in from the outside (box 8.7).

The Deference Effect

When people tell you what they think you want to know, so as not to offend you, that’s called the deference effect. Aunger (1992, 2004) may have experienced this in Zaire (see box 8.7). In fact, it happens all the time, and researchers have long been aware of the problem. In 1958, Lenski and Leggett embedded two contradictory questions in a faceto-face interview, half an hour apart. Respondents were asked whether they agreed or disagreed with the following two statements: (1) It’s hardly fair to bring children into the world, the way things look for the future; (2) Children born today have a wonderful future to look forward to. Just 5% of Whites agreed with both statements compared to 20% of African Americans. Lenski and Leggett concluded that this was the deference effect in action: Blacks were four times more likely than Whites to agree to anything, even contradictory statements, because the interviewers were almost all white and of higher perceived status than the respondents (Lenski and Leggett 1960).

In the National Black Election Study, 872 African Americans were polled before and after the 1984 presidential election. Since interviewers were assigned randomly to respondents, some people were interviewed by a white person before the election and an African American after the election. And vice versa: Some people were interviewed by an African American before the election and a white person on the second wave. When African American interviewers in the preelection polls were replaced by white interviewers in the postelection surveys, African Americans were more likely to say that Blacks don’t have the power to change things, that Blacks can’t make a difference in local or national elections, that Blacks cannot form their own political party, and that Whites are not responsible for keeping Blacks down—very powerful evidence of a race-of-interviewer effect (D. W. Davis 1997) (box 8.8).

Reese et al. (1986:563) tested the deference effect in a telephone survey of Anglo and Mexican American respondents. When asked specifically about their cultural preference, 58% of Hispanic respondents said they preferred Mexican American culture over other cultures, irrespective of whether the interviewer was Anglo or Hispanic. Just 9% of Anglo respondents said they preferred Mexican American culture when asked by Anglo interviewers, but 23% said they preferred Mexican American culture when asked by Hispanic interviewers.

Questions about gender and gender roles produce deference effects, too. When you ask people in the United States how most couples actually divide child care, men are more likely than women to say that men and women share this responsibility—if the interviewer is a man (Kane and McCaulay 1993:11). Do women have too much influence, just

T H E I N S I D E R - I N T E R V I E W E F F E C T I N T H E I T U R I F O R E S T

Robert Aunger (1992, 2004:145–62) studied three groups of people in the Ituri forest of Zaire. The Lese and Budu are horticultural, and the Efe are foragers. Aunger wanted to know if they shared the same food avoidances. He and three assistants, two Lese men and one Budu man, interviewed a total of 65 people. Each of the respondents was interviewed twice and was asked the same 140 questions about a list of foods.

Aunger identified two types of errors in his data: forgetting and mistakes. If informants said in the first interview that they did not avoid a particular food but said in the second interview that they did avoid the food, Aunger counted the error as forgetfulness. If informants reported in interview two a different type of avoidance for a food than they’d reported in interview one, then Aunger counted this as a mistake.

Even with some missing data, Aunger had over 8,000 pairs of responses in his data (65 pairs of interviews, each with up to 140 responses), so he was able to look for the causes of discrepancies between interview one and interview two. About 67% of the forgetfulness errors and about 79% of the mistake errors were correlated with characteristics of informants (gender, ethnic group, age, and so on). However, about a quarter of the variability in what informants answered to the same question at two different times was due to characteristics of the interviewers (ethnic group, gender, native language, etc.), and about 12% of variability in forgetting was explained by interviewer experience. As the interviewers interviewed more and more informants, the informants were less likely to report ‘‘no avoidance’’ on interview one and some avoidance on interview two for a specific food. In other words, interviewers got better and better with practice at drawing out informants on their food avoidances.

Of the four interviewers, though, the two Lese and the Budu got much better, while the anthropologist made very little progress. Was this because of Aunger’s interviewing style, or because informants generally told the anthropologist different things than they told local interviewers, or because there is something special about informants in the Ituri forest? We’ll know when we add variables to Aunger’s study and repeat it in many cultures, including our own (Further Reading: response effects).

the right amount of influence, or too little influence in today’s society? When asked this question by a male interviewer, men are more likely to say that women have too much influence; when asked the same question by a female interviewer, men are more likely to say that women have too little influence. And similarly for women: When asked by a female interviewer, women are more likely to say that men have too much influence than when asked by a male interviewer (Kane and Macaulay 1993:14–15).

Lueptow et al. (1990) found that women gave more liberal responses to female interviewers than to male interviewers on questions about gender roles. Men’s attitudes about gender roles were, for the most part, unaffected by the gender of the interviewer—except

BOX 8.8

B A R A C K O B A M A A N D T H E B R A D L E Y E F F E C T

In 1982, Tom Bradley, the mayor of Los Angeles, ran against George Deukmejian for the office of governor of California. Bradley was ahead in the polls for the governorship of California right up to election day—and lost. Some voters had told pollsters that they were for Bradley, who is black, and then voted for Deukejian, who is white. The so-called Bradley effect was at work in 1989, when Douglas Wilder, an African American, ran against Marshall Coleman, who is white, for the governorship of Virginia. Preelection polls showed that Wilder was far ahead, but in the end, he won by only a slim margin. White voters were more likely to claim Wilder as their choice if the interviewer was African American than if the interviewer was white (Finkel et al. 1991). Barack Obama is widely credited with ending the Bradley Effect, but he lost the 2008 New Hampshire primary to Hillary Clinton by three points after being ahead in the polls by eight points—right up to election day (Kohut 2008).

that highly educated men gave the most liberal responses about gender roles to female interviewers. ‘‘It appears,’’ said Lueptow et al., ‘‘that educated respondents of both sexes are shifting their answers toward the socially desirable positions they think are held by female interviewers’’ (p. 38). Attitudes about gender roles sure are adaptable. That was in 1990. In 2008, about 26% of the American public was ‘‘angry or upset’’ at the prospect of a woman president, even though, at the time almost 90% of Americans told pollsters that they would vote for a qualified woman foir president (Streb et al. 2008:77).

Questions that aren’t race related, by the way, are not affected much by the race or the ethnicity of either the interviewer or the respondent. Still, whenever you have multiple interviewers, keep track of the race, ethnicity, and gender of the interviewer and test for response effects. Identifying sources of bias is better than not identifying them, even if you can’t eliminate them (Further Reading: the deference effect).

The Social Desirability Effect

When people tell you what they think will make them look good, especially according to prevailing standards of behavior and thought, that’s the social desirability effect. Hadaway et al. (1998) went to a large Protestant church and found 115 people in attendance at the Sunday school. On Monday morning, when Hadaway et al. polled the whole church membership, 181 people claimed to have been in Sunday school the previous day. Headcount experiments like this one typically produce estimates of church attendance that are 55%–59% of what people report (T. W. Smith 1998).

The social desirability effect is influenced by the way you ask the question. Major surveys, like the Gallup Poll, ask something like: ‘‘How often do you attend religious services?’’ Then they give the people choices like ‘‘once a week, once a month, seldom, never.’’ Presser and Stinson (1998) asked people on Monday to list everything they had done did from ‘‘midnight Saturday to midnight last night.’’ When they asked the question this way, 29% of respondents said that they had gone to church. Asking ‘‘How often do you go to church?’’ produced estimates of 37%–45%. This is a 28%–50% difference in reported behavior and is statistically very significant (Further Reading: social desirability effect).

The Third-Party-Present Effect

We sort of take it for granted that interviews are private conversations, conducted one on one, but in fact, many face-to-face interviews have at least one third party in the room, often the spouse or partner of the person being interviewed. Does this affect how people respond to questions? As with other response effects, the answer is yes, sometimes. Zipp and Toth (2002), for example, analyzed data from a household survey in Britain and found that when the spouses are interviewed together, they are much more likely to agree about many things—like who does what around the house—than when they are interviewed separately. Apparently, people listen to each other’s answers and modify their own answers accordingly, which puts on a nice, unified face about their relationship.

As you’d expect, there is a social desirablity effect when a third party is present. Casterline and Chidambaram (1984) examined data from 24 developing countries in the World Fertility Study and found that women in those countries are less likely to admit using contraception when a third party is present at the interview. Anthropologists face this situation a lot: trying to get people to talk about sensitive topics and assuring them of privacy, but unable to find the privacy for an interview.

On the other hand, Aquilino (1993) found that when their spouse is in the room, people report more marital conflict than when they are interviewed alone. They are also more likely to report that they and their spouse lived together before marriage if their spouse is in the room. Perhaps, as Mitchell (1965) suggested 45 years ago, people own up more to sensitive things like this when they know it will be obvious to their spouse that they are lying. Seems like a good thing to test (Further Reading: third-party-present effect).

Threatening Questions

In general, if you are asking someone a nonthreatening question, like whether they have a library card, then response effects are minimal. But if you ask people about their alcohol consumption, or whether they ever shoplifted when they were children, or whether they have family members who have had mental illness, or how many sexual partners they’ve had, then response effects are really important. One key finding on this problem is, intuitively, that disclosure of information about socially undesirable behavior increases with the perception people have of their anonymity (Tourangeau and Yan 2007). So, people open up more on questionnaires about illegal or embarrassing behavior that are self-administered than in surveys conducted face-to-face, and still more when they think that a survey is truly anonymous. (See the section on the randomized response technique and the section on computerized interviews in chapter 9).

Asking about other people increases reports about socially undesirable behavior. Katz and Nare´ (2002) asked 1,973 single Muslim women between the ages of 15 and 24 in Dakar, Senegal, if they had ever been pregnant. Three percent of the women said they had. But 25% of the same women said that at least one of their three closest friends had been pregnant—more than eight times what they reported about themselves. (See Sudman et al. [1977:147–51] on the three-closest-friends technique.)

Asking the interviewers on a project to record their interviews produces a higher response rate, particularly to sensitive questions about things like sexual behavior. Apparently, when interviewers know that their work can be scrutinized (from the recordings), they probe more and get informants to open up more (Billiet and Loosveldt 1988).

And if you give people choices that include a big number of any behavior, you’ll probably get reports of more of that behavior. Tourangeau and Smith (1996) asked men and women: ‘‘During the last 12 months, that is, since August/September 1993, how many men [women], if any, have you had intercourse with?’’ Some people were asked simply to tell the interviewer a number. Others were asked to choose one of the following: 0, 1, 2, 3, 4, 5 or more. And still others were asked to choose one of the following: 1–4, 5–9, 10–49, 50–99, 100 or more. People reported more sex partners when given high-end choices than when given low-end choices or an open-ended question (Tourangeau and Smith 1996:292). In Germany, people reported watching more television when they were given choices that included a big number of hours (Schwarz et al. 1985).

You might be surprised, though, at what counts as a threatening question. R. A. Peterson (1984) asked 1,324 people one of the following questions: (1) How old are you? (2) What is your age? (3) In what year were you born? or (4) Are you 18–24 years of age, 25–34, 35–49, 50–64, 65 or older? Then Peterson got the true ages for all the respondents from reliable records. There was no significant difference in the accuracy of the answers obtained with the four questions, but almost 10% of respondents refused to answer question 1, while only 1% refused to answer question 4, and this difference is significant (Further Reading: asking threatening questions).

ACCURACY

Even when people tell you what they think is the absolute truth, there is still the question of whether the information they give you is accurate.

A lot of research—ethnographic and survey research alike—is about mapping opinions and attitudes. When people tell you that they approve of how the chief is handling negotiations for their village’s resettlement, or when they tell you that they prefer a particular brand of beer to some other brand, they’re talking about internal states. You pretty much have to take their word for such things.

But when we ask people to tell us about their actual behavior (How many times did you take your baby to the clinic last month? How many times last year did you visit your mother’s village?), or about their environmental circumstances (How many hectares of land do you have in maize? How many meters is it from your house to the well?), we can’t just assume informant accuracy (box 8.9).

We see reports of behavior in our local newspapers all the time: College students today are binge drinking more than they did 5 years ago. Americans are going to church less often than they did a decade ago.

In back of findings like these are questions like these:

Circle one answer:

How many times last month did you consume five or more beers or other alcoholic drinks in a single day?

Never Once Twice Three times More than three times

How often do you go to church?

Never Occasionally—once a month or less About once a week More than once a week

BOX 8.9

D I E T A R Y R E C A L L

Studies of diet and human nutrition mostly rely on informants to recall what they’ve eaten over the past 24 hours or what they usually eat for various meals. They often produce dreadfully inaccurate results.

C. J. Smith et al. (1996) compared the responses of 575 Pima and Papago Indians (in Arizona) to a 24-hour recall instrument about food intake with responses to a very detailed survey called the Quantitative Food Frequency questionnaire. In the QFF, interviewers probe for a list of regularly consumed foods in a community. Smith et al. also assessed the energy expenditure of 21 people in the research group using the doubly labeled water technique. The DLW technique involves giving people special water to drink—water with isotopes that can be tracked in blood and urine samples—and then testing, over time, their actual intake of nutrients.

The correlation, across the 21 participants, between the energy intake measured by the DLW technique and the energy intake estimated by the informants’ responses to the QFF, was 0.48. This correlation is statistically significant, but it means that just 23% (0.48²) of the variation in actual energy intake across the 21 people was accounted for by their responses to a very detailed interview about their food consumption. And the correlation of actual energy intake with estimates from the 24-hour recall data was much worse.

R. K. Johnson et al. (1996) also found no useful relation between individual 24-hour recall measurements of energy intake among children in Vermont and measurements of those same children by the DLW technique. But, in the all-isnot-lost department, Johnson et al. found that averaging the data for energy intake across three 24-hour recalls in 14 days (on day 1, day 8, and day 14) produced results that were very similar to those produced by the DLW technique. So, people hover around giving accurate answers to a question about calorie intake and if you get at least three answers for three time windows and take the average, you may get a useful result (Further Reading: measuring food intake and physical activity).

La Pierre Discovers the Problem

We’ve known for a long time that we should be suspicious of this kind of data. From 1930 to 1932, Richard La Pierre, accompanied by a Chinese couple, crisscrossed the United States, twice, by car. The threesome covered about 10,000 miles, stopping at 184 restaurants and 66 hotels. And they kept records. There was a lot of prejudice against Chinese in those days, but they were not refused service in a single restaurant and just one hotel turned them away (La Pierre 1934).

Six months after the experiment ended, La Pierre sent a questionnaire to each of the 250 establishments where the group had stopped. One of the things he asked was: ‘‘Will you accept members of the Chinese race as guests?’’ Ninety-two percent—230 out of 250—replied ‘‘No.’’

By today’s standards, La Pierre’s experiment was crude. He could have surveyed a control group—a second set of 250 establishments that they hadn’t patronized but that were in the same towns where they’d stopped. With self-administered questionnaires, he couldn’t be sure that the people who answered the survey (and who claimed that they wouldn’t serve Chinese) were the same ones who had actually served the threesome. And La Pierre didn’t mention in his survey that the Chinese couple would be accompanied by a white man.

Still, La Pierre’s experiment was terrific for its time. It made clear that what people say they do (or would do) is not a proxy for what they actually do or will do (see Deutscher 1973). This basic finding shows up in what you might think were the most unlikely places: In the 1961 census of Addis Ababa, Ethiopia, 23% of the women underreported the number of their children. Apparently, people there didn’t count babies who die before reaching the age of 2 (Pausewang 1973:65). People in the United States often omit newborns when they fill out the Decennial Census form (Dillman et al. 2009b:225), and in China today, if a child dies soon after birth, couples may decide to report neither the birth nor the death and instead try to conceive again as quickly as possible. And, under the one-child policy, the births of female babies may not be reported at all because of the desire by couples to have a son (Merli and Rafferty 2000:110).

Why People Are Inaccurate Reporters of Their Own Behavior

People are inaccurate reporters of their own behavior for many reasons. Here are four:

1. Once people agree to be interviewed, they have a personal stake in the process and usually try to answer all your questions—whether they understand what you’re after or not.

2. Human memory is fragile, although it’s clearly easier to remember some things than others.

Cannell et al. (1961) found that the ability to remember a stay in the hospital is related to the length of the stay, the severity of the illness that lands you there, and whether or not surgery is involved. It’s also strongly related to the length of time since discharge. Cannell and Fowler (1965) found that people report accurately 90% of all overnight hospital stays that happened 6 months or less before being interviewed.

It’s easy for people to remember a rare event, like surgery, that occurred recently. But, as Sudman and Schwarz (1989) point out, if you ask people to think about some common behavior going back months at a time, they probably use estimation rules. When Sudman and Schwartz asked people ‘‘How many [sticks] [cans] of deodorant did you buy in the last 6 months?’’ they started thinking: ‘‘Well, I usually buy deodorant about twice a month in the summer, and about once a month the rest of the year. It’s now October, so I suppose I must have bought 10 deodorants over the last 6 months.’’ And then they say, ‘‘10,’’ and that’s what you write down.

3. Interviews are social encounters. People manipulate those encounters to whatever they think is their advantage.

Adolescent boys tend to exaggerate, and adolescent girls tend to minimize, reports of their own sexual experience (see Catania et al. 1996).

4. People can’t count a lot of behaviors, so they use rules of inference.

In some situations, they invoke D’Andrade’s ‘‘what goes with what’’ rule (1974) and report what they suppose must have happened, rather than what they actually saw. Freeman et al. (1987) asked people in their department to report on who attended a particular colloquium. People who were usually at the department colloquium were mentioned as having attended the particular colloquium—even by those who hadn’t attended (and see Shweder and D’Andrade 1980).

Reducing Errors: Jogging Informants’ Memories

Loftus and Marburger (1983) found that landmarks help reduce forward telescoping— where people report that something happened 1 month ago when it really happened 2 months ago (backward telescoping is rare). The title of their article says it all: ‘‘Since the Eruption of Mt. St. Helens, Has Anyone Beaten You Up? Improving the Accuracy of Retrospective Reports with Landmark Events.’’ Means et al. (1989) asked people to recall landmark events in their lives going back 18 months from the time of the interview.

Once the list of personal landmark events was established, people were better able to recall hospitalizations and other health-related events. In the field, as you do life history interviews, try to establish personal milestones for each informant—like their first hunting kill or their clitoridectomy or, for older informants, burying their parents or becoming grandparents—and ask them to report on what has happened since each landmark.

Aided recall increases the number of events recalled, but also appears to increase the telescoping effect (Bradburn 1983:309). In studies where you interview people more than once, you can correct for telescoping by reminding them what they said last time in answer to a question and then asking them about their behavior since their last report.

Event history and life history calendars are effective aids to recall and are particularly useful in societies where there are no written records. Leslie et al. (1999:375–78), for example, developed an event calendar for the Ngisonyoka section of the South Turkana pastoralists in northwestern Kenya. The Turkana name their seasons rather than their years. Based on many interviews between 1983 and 1984, Leslie et al. were able to build up a list of 143 major events associated with seasons between 1905 and 1992. Events include things like ‘‘no hump’’ in 1961 (it was so dry that the camels’ humps shrank), ‘‘bulls’’ in 1942 (when their bulls were taken to pay a poll tax), and ‘‘rescue’’ in 1978 (when rains came). This painstaking work has made it possible for many researchers to gather demographic and other life history data from the Ngisonyoka Turkana. William Axinn and colleagues (1999:252) also used multiple event cues in Nepal and, like Leslie et al., report that this was particularly helpful for older informants (Further Reading: event- and life-history calendars).

If you are working in an industrialized environment with literate informant, you can ask people to review their credit card statements and long-distance phone bills and to remember events, places, and people associated with each credit or phone event. College transcripts help people think about what they were doing and the people they met along the way. Still . . . Horn (1960) asked people to report their bank balance. Of those who did not consult their bankbooks, just 31% reported correctly. Those who consulted their records didn’t do that much better. Only 47% reported correctly (reported in Bradburn 1983:309).

It’s different, of course, in nonindustrialized societies. When Elliot Fratkin (2004:19) asked Ariaal warriors in northern Kenya how many cattle they owned, the answer was always ‘‘many.’’ Veterinary studies showed that the herds of the Samburu (a group closely related to the Ariaal) were two-thirds female and that 50% of those cattle were lactating at any time. A household with 6 nursing calves, Fratkin calculated, would have, on average, 12 cows and 4 female calves, plus 8 male cattle.

Informant accuracy remains a major problem. Gary Wells and colleagues (2003)

showed a video of a staged crime to 253 students. Then they showed the students a photo lineup of six people and asked the students to pick out the culprit. Every single student picked one of the six photos, but there was a small problem: The culprit wasn’t in the six photos. We need a lot more research about the rules of inference that people use when they respond to questions about where they’ve been, who they were with, and what they were doing (Further Reading: informant accuracy).

FURTHER READING

Transcription: Bailey (2008); Bucholtz (2000); Du Bois (1991); Duranti (2006); Maloney and Paolisso (2001); Matheson (2007); McLellan et al. (2003); Ochs (1979).

Interviewing: Graham (2000); Gubrium and Holstein (2002); Kvale and Brinkman (2009); McCracken (1988); Mishler (1986); Rubin (2005); Seidman (2006); Wengraf (2001).

Focus groups: Krueger (1994); Morgan (1997); Morgan and Krueger (1998); Sayles et al. (2007); Stewart and Shamdasani (1990); Vaughn et al. (1996).

Response effects: Borgers et al. (2004); Bradburn (1983); Cannell et al. (1979); Christian et al. (2009); Javeline (1999); Johnson and Delameter (1976); Schaeffer and Presser (2003); Schuman and Presser (1979, 1981); Schwarz (1999); Schwarz et al. (1991); Singer et al. (1983); Sudman and Bradburn (1974); Tourangeau et al. (2000).

Deference effect: Dotinga et al. (2005); Krysan and Couper (2003).

Social desirability effect: DeMaio (1984); Kreuter et al. (2008); Phillips and Clancy (1972); Press and Townsley (1998); W. W. Smith (2006); van de Mortel (2008).

Third-party present effect: Aquilino (1997); Aquilino et al. (2000); Blair (1979); Boeije (2004); Bradburn (1979); Hartmann (1994); Pollner and Adams (1997); T. W. Smith (1997).

Asking threatening questions: Bradburn et al. (1978); Bradburn, Sudman et al. (1979); Catania et al. (1996); Gribble et al. (1999); Hewitt (2002); Johnston and Walton (1995); Makkai and McAllister (1992); Mooney and Gramling (1991); Wiederman et al. (1994).

Event- and life-history calendars: Belli (1998); Caspi et al. (1996); Freedman et al. (1988); Glassner and van der Vaart (2009); Kessler and Wethington (1991); Martyn and Belli (2002); Yoshihama et al. (2005).

Measuring food intake and physical activity: Graham (2003); Hebert et al. (2002); Hill and Davies (2001); Leenders et al. (2000); Pelto et al. (1989); Prince et al. (2008); Quandt and Rittenbaugh (1986); Schoenberg (1997, 2000); Subar et al. (2003).

Informant accuracy: see Further Reading, chapter 2.