• Email
  • Print

Sex, Lies, and Social Science’: An Exchange

In response to:

Sex, Lies, and Social Science from the April 20, 1995 issue

To the Editors:

We are puzzled by the review of our book, The Social Organization of Sexuality [NYR, April 20], because it is professionally incompetent and motivated by such an evident animus against the social sciences in general. We do not think it appropriate for a biologist, even a noted population geneticist whose empirical work is on the Drosophila fruit fly and other “simple” animals, to review a book that describes its principal task as formulating a social perspective on human sexual conduct in the United States. The notion that an economist, a sociologist or a physicist should review professional work on population genetics would properly be greeted with derision. Lewontin’s professional qualifications are of relevance in discussing his review since he himself asserts that his role as a scientist grants him the authority of special expertise for commenting on specific aspects of our book. Nowhere is that basis in expert knowledge evident in the innuendo and diatribe that constitute his review.

The central premise of Lewontin’s review is that people routinely and pervasively lie about sexual behavior—indeed, it would seem all aspects of their lives—and thus none of the data from our survey of 3,432 people can be taken seriously. But Lewontin relates no systematic empirical information to substantiate his claim. Rather, he relies on a set of rhetorical devices that tendentiously advance his assertions.

Lewontin opens the review with an argument based on a false analogy. He discusses at length the problems of credibility in autobiographical statements and then asserts the analogical equivalence of autobiography and the self-reports given in response to our questions. The reader by now is supposed to be thinking, “I certainly would not tell anybody that I had sex with my spouse last night while clutching a yellow rubber ducky. I’d lie—at least about the rubber ducky.” But autobiography, by definition, involves the public disclosure of the identity of the person. This sets in train all the motivations to create a favorable self-image in the minds of others and perhaps some of the outcomes Lewontin asserts. In contrast, we went to great lengths to guarantee the privacy, confidentiality and anonymity of our respondents’ answers as well as to provide a strong rationale for an individual to be candid and honest with us. We spent a great deal of time worrying about how we could check the reliability and honesty of our respondents’ answers. While we readily admit that we were not always successful in securing full disclosure, his false analogy simply misses the point altogether.

Lewontin’s next move is to provide an instance demonstrating the data’s invalidity by discussing the large discrepancy between the average numbers of partners reported by men and women and the logical impossibility of such a situation assuming that they are recruiting their partners from a common pool. In the 52-page chapter devoted to the numbers of sex partners, we explicitly discuss (on p. 174) the undesirability of using averages (means) to summarize the central tendencies of distributions as skewed and narrowly concentrated (with long, unevenly distributed tails) as these are. In addition, we explore in considerable detail the reasons for this discrepancy. Lewontin argues that if we could not get this “simple fact” right, it is evidence that all else is spurious. Error is a problem in all observations (including those in biology), how it is dealt with and its public recognition is the test of science. His decision to rest his case on this single issue without reference to its context forces us to conclude that he willfully misrepresented our analysis.

But he isn’t satisfied with this. In an obscure footnote in the middle of the review that has no obvious relevance to our work at all, he mentions The Bell Curve by Herrnstein and Murray, the controversial book on racial differences in intelligence. Here we are being subjected to guilt by association. All readers of the Review surely know exactly what to think of these infamous social scientists. And we are insidiously being tossed into the pot with them for no other reason than we too are social scientists.

Finally, we have Lewontin’s discussion of our finding that 45 percent of men between the ages of 80 and 84 claim to have sex partners. He chuckles at our credulity in reporting such patent nonsense, being just one more instance of our hopeless gullibility of believing everything we are told by our respondents. Now this is a rather nice instance of his tendentious and misleading use of our data to support his central claim that everybody is lying about their sex lives. The survey in question, the General Social Survey (GSS), is a widely known, high-quality, regularly conducted survey that professionally knowledgeable people rely on for estimating social trends of various sorts. It is sponsored by the National Science Foundation and has been subjected to regular scientific peer review for some twenty years. To the professional social scientist, it is well known to be a household-based sample that excludes the institutionalized parts of the population. Any number of census and other highly regarded survey studies have also noted that, due to differential mortality and other factors, older women are progressively more likely to be living alone. By age 70, about 70 percent of women report, in the GSS, no sex partners in the past year. Older men, in contrast, are far more likely to be living with someone—the sex ratio is increasingly in their favor so far as the surplus of older women to older men is concerned. It is therefore not at all surprising that noninstitutionalized men in their eighties—presumably healthy enough to be living on their own—would have a fair chance of reporting that they have a sex partner. We discuss at length in the book the different meanings of sexuality across age, time and social circumstance. We believe the answers are hardly likely to be crazed lies by sex-starved octogenarians who are posturing like teenagers for the edification of credulous social scientists.

The review is a pastiche of ill-informed personal opinion that makes unfounded claims of relevant scientific authority and expertise. Readers of The New York Review of Books deserve better.

Edward O. Laumann
John H. Gagnon
Robert T. Michael
Stuart Michaels

Department of Sociology

The University of Chicago

Chicago, Illinois

To the Editors:

In the course of Richard Lewontin’s brilliant essay “Sex, Lies, and Social Science” he remarks that if the study he reviewed is typical of American scientific sociology, then this discipline must be in “deep trouble.” That’s putting it mildly. American sociology has become a refuge for the academically challenged. Some universities have closed their sociology departments; many have decided the discipline merits little new money.

Yet mere stupidity cannot explain the analytic weaknesses of studies like the NORC sexuality project; nor do social scientists so very gainfully employed in such shops simply misunderstand the scientific enterprise. The difficulties with this research, like the larger troubles of sociology, are political.

The British prime minister Margaret Thatcher famously declared a generation ago, “There is no society, only individuals and their families.” In an eerie way, much positivistic sociological research subscribes to this anti-social nostrum. It does so, as in the NORC study, by not probing subjects which resist quantification; the usual disclaimer is that while such matters as the relation of sex and love may be important, they cannot be scientifically researched. Here is where politics enters; there’s something comforting about sacrificing reality on the altar of research. The “dull science”—as Michel Foucault called American sociology—legitimates dissociation from the entanglements, contradictions, and difficulties of actual social experience. Dull knowledge has the same positive political value in Gingrich’s America as it did in Thatcher’s Britain. Lewontin complains of the superficiality of the NORC analysis, but maybe the very promise of a calming superficiality is what attracted so much money to this project.

However, if Lewontin’s exposé is just, he uses a meat cleaver where a scalpel would have served him better. Is quantifying social phenomena an inherent evil, as at points in his essay he seems to suggest? Lewontin surely wouldn’t deny that the Census Bureau provides useful and necessary information. In principle, survey research has its uses, in revealing how people think about themselves. (I found it both interesting and cheering that 45 percent of men between the ages of 80 and 84 in the NORC study reported still having sex with a partner, even if the aged have confused fantasy with fact.) Method per se isn’t the issue.

I wish Lewontin had put his attack in a larger historical context. From its origins in Social Darwinism and the Progressive movement, American sociology has struggled with the contrary claims of those afflicted with physics envy and researchers—whether deploying numbers or words—more engaged in the dilemmas of society. In that struggle, midwestern Protestant mandarins of positivist science often came into conflict with East Coast Jews who in turn wrestled with their own Marxist commitments; great quantitative researchers from abroad, like Paul Lazarsfeld at Columbia, sought to disrupt the complacency of native bean counters. In the last twenty years, more interesting “hard” sociological research has been done in medical, planning, and law schools, and better research on culture and society in the humanities departments, than in sociology departments. The intellectual enterprise of sociology is hardly represented by the dumbed-down study Lewontin rips apart.

What places like NORC command, like other reactionary enterprises, is money. To defend themselves, the minions of these institutions will undoubtedly attack Lewontin for being anti-empirical, which will miss exactly his point, that their brand of science represses trenchant social evidence. My worry is that this repression is more than an academic evil. Sociology in its dumbed-down condition is emblematic of a society that doesn’t want to know too much about itself.

Richard Sennett

New York University

New York City

R.C Lewontin replies:

It should come as no surprise to the readers of The New York Review that the authors of The Social Organization of Sexuality did not like what I wrote. I confess to having amused myself over the last couple of weeks by imagining what their inevitable letter would contain. I was sure that they would challenge the competence of a biologist to judge social science, as indeed they have. I also imagined, and hoped, that they would raise a series of substantive objections to my characterization of their methodology, backed by various pieces of evidence of which the review took no account, so that we might engage in a revealing unpacking of the issues. In this, alas, I was too sanguine. Their letter makes no arguments, but relies on their disciplinary authority while repeating unsubstantiated and doubtful claims.

It is reasonable that Laumann et al. would have preferred to have their work reviewed by a member of their own school of sociology, someone sharing the same unexamined methodological assumptions. They could then avoid the always unpleasant necessity of justifying the epistemic basis on which the entire structure of their work depends. Their assertion of my incompetence, however, is off the mark. It is both temperamentally and ideologically repugnant to me to provide advertisements for myself, but as I do not want Laumann and his colleagues, or other readers of the review, to avoid confronting the issues by a facile dismissal of my expertise, I am obliged to provide a CV. Although a biologist, I have a graduate degree in mathematical statistics and have taught the subject for forty years. About 10 percent of my technical publications, including a textbook of statistics, have been devoted to problems of statistical sampling, estimation, and hypothesis testing. More important, my biological work must be classified as methodological, my chief contribution to the field having been an analysis of the deep epistemological difficulties posed by the data of evolutionary genetics and the introduction of new experimental approaches specifically designed to overcome the ambiguities. Finally, my work on epistemological problems, produced both alone and together with philosophers of science, appears in standard philosophical journals.1 Whatever may be at issue here, it is not competence.

Laumann et al. complain that the results of sample surveys were falsely analogized with autobiography. Either they do not understand the structure of analogical reasoning or, as is more likely, they were so annoyed by the review that they read it only impressionistically. No such analogy was drawn, nor was any argument from analogy made. On the contrary, autobiography, repressed memory, and survey interviews were given as three different examples of a general problem of deriving objective information from self-report. I drew a contrast between the possibility of verification in the first two cases and the virtual impossibility in the last. Here our authors touch on the central methodological issue. It is their view that, although people may lie or exaggerate in autobiographies because they are trying to create a public persona, they will tell the truth in anonymous interviews, because there is no motivation to manipulate the impression that strangers have of us. Is it really true that quantitative sociologists are so divorced from introspection and so insensitive to social interactions that they take such a naive view of human behavior? Do they really believe all those things they hear from the person on the next bar stool or the seat next to them in the airplane? The Yellow Kid, who made a living from fleecing the gullible, used to say that anyone who could not con a banker ought to go into another line of work. Maybe, but before giving up, they should try professors of sociology. Putting aside subjective questions, haven’t they even read the voluminous literature on the sociology of fashion? It is ironic that a student of “simple organisms” has to instruct those who inquire about human beings about the complexity of their objects of study.

First, Professor Laumann, people do not tell themselves the truth about their own lives. The need to create a satisfying narrative out of an inconsistent and often irrational and disappointing jumble of feelings and events leads each of us to write and rewrite our autobiographies inside our own heads, irrespective of whether anyone else is ever privy to the story. Second, these stories, which we then mistake for the truth, become the basis for further conscious manipulation and manufacture when we have exchanges with other human beings. If the investigators at NORC really do not care what strangers think of them, then they are possessed of an insouciance and hauteur otherwise unknown in Western society. It is precisely in the interaction with strangers who are not part of their social network, and who will never interest their lives again, that people feel most free to embroider their life stories, because they will never be caught out.

Laumann et al. try to minimize the impact of the observed discrepancy in the number of sexual partners reported by men and by women. There is an attempt at obfuscation in a remark by Laumann and his colleagues about averages not containing as much information as more detailed frequency descriptions. True, but irrelevant, because in their data men consistently report more partners across the entire frequency distribution. Anyway, Laumann et al. do not deny the discrepancy. Indeed it is they who brought it up and discussed it in the book, and it is they, not I, who offered as the most likely explanation that men “exaggerate” and women “minimize” their sexual promiscuity. Then they try to discount the impact of the discrepancy on the study as a whole. After all, it is just one false note, and we cannot expect perfection. People may lie or fantasize about how many sexual partners they have, but we can take everything else they say at face value.

But this neatly ignores the fact that this comparison provides the only internal check on consistency that the study allows. I nowhere claimed that “all else is spurious,” but rather that we are left in the unfortunate position of not knowing what is true when our only test fails. Then, in an extraordinary bit of academic chutzpah that turns the usual requirement for validation on its head, Laumann et al. say that it is up to those who question the data to demonstrate their unreliability. For years those of us who work on “simple” organisms have sheepishly accepted the burden of supporting our own claims, and the failure of the sole internal check on the validity of the data usually creates a certain difficulty in getting one’s work published. Autres pays, autres moeurs.

I would not want to claim that we learn nothing from people’s answers in sex surveys. One thing that they seem to establish is that individual fantasies follow cultural stereotypes. In the French equivalent of the NORC study involving over 20,000 telephone interviews, French men reported four times as many partners as French women!2 Of course, it may be that with the greater distance offered by the telephone, men feel freer to “exaggerate,” but that explanation doesn’t offer much solace to those who think that anonymity breeds truthfulness.

While Laumann and his colleagues believe that men exaggerate while they are aged between eighteen and fifty-nine, they (backed by the peer review panels of the National Science Foundation) seem to have complete confidence in the frankness of octogenarians. Perhaps, as men contemplate their impending mortality, the dread of something after death makes lying about sex seem risky. We must, however, at least consider the alternative that affirming one’s continued sexual prowess in great age is a form of whistling in the dark.

Far from having “an animus against the social sciences,” I have considerable sympathy for the position in which sociologists find themselves. They are asking about the most complex and difficult phenomena in the most complex and recalcitrant organisms, without that liberty to manipulate their objects of study which is enjoyed by natural scientists. In comparison, the task of the molecular biologist is trivial. Living organisms are at the nexus of a large number of weakly determining causal pathways, and the classic method of studying such systems is to exaggerate the effect of one pathway while holding the others constant. When such experimental manipulation is not possible we have no recourse but to stand off and describe the system in all its complexity. The inevitable consequence is that the structure of inference is much looser and it becomes extremely difficult to test our explanations. How much worse is the situation of those observers whose objects of study have consciousness and who depend on the objects themselves to report on their own state.

The division between those who try to learn about the world by manipulating it and those who can only observe it has led, in natural science, to a struggle for legitimacy. The experimentalists look down on the observers as merely telling uncheckable just-so stories, while the observers scorn the experimentalists for their cheap victories over excessively simple phenomena. In biology the two camps are now generally segregated in separate academic departments where they can go about their business unhasseled by the unbelievers. But the battle is unequal because the observers’ consciousness of what it is to do “real” science has been formed in a world dominated by the manipulators of nature. The observers then pretend to an exactness that they cannot achieve and they attempt to objectify a part of nature that is completely accessible only with the aid of subjective tools.

Richard Sennett has formulated better, and with more authority than I could, the ideological issues in sociology. (Is he, too, incompetent?) He is, of course, right when he insists that quantitative information is important in sociology. Data on birth, death, immigration, marriage, divorce, social class, neighborhood, causes of mortality and morbidity, occupations, wage rates, and many other variables are indispensable for sociological investigations. My “meat cleaver” was never meant to sever those limbs from the body of knowledge. But it does not follow that collecting statistics, especially survey statistics with their utter ambiguity of interpretation, is sociology. A better model is Chevalier’s Classes laborieuses et classes dangereuses.3 Chevalier’s realization was that social phenomena could not be understood without the demographic statistics, but that these numbers can have no interpretation in themselves without a coherent narrative of social life. For contemporary life we have our own experience to help us understand the numbers. For the past we depend on literature, so the locales, characters, and events in the novels of Balzac, Hugo, and Sue form as much a part of the evidence about nineteenth-century Paris as the schedules of mortality and the tables of wage rates.

Even though the world is material and all its phenomena, including human consciousness, are products of material forces, we should not confuse the way the world is with our ability to know about it. Like it or not, there are a lot of questions that cannot be answered, and even more that cannot be answered exactly. There is nothing shameful in that admission.

  1. 1

    For a less technical and more generally accessible example, see “Facts and the Factitious in the Natural Sciences” in Critical Inquiry 18 (1991), pp. 140–153.

  2. 2

    A. Spira and N. Bajos, Les comportements sexuels en France (Paris: Documentation Française, 1993).

  3. 3

    Louis Chevalier, Classes laborieuses et classes dangereuses à Paris pendant la première moitié du XIXème siècle (Paris: Plon, 1958).

  • Email
  • Print