I once knew a man who was posted as a research scientist at an agricultural institute in what was then British Uganda. He told me with great frustration that he was having extreme difficulty in finding out whether his African assistants had actually carried out the procedures that he had prescribed because they had become so anxious to please their colonial bosses that they always answered “Yes” to every question asked. He claimed, however, that he had thought of a way around the problem. In the future he would always elicit the same information twice in such a way that the correct answer would be “Yes” the first time he asked and “No” the second. It apparently had not occurred to him that if his assistants really always answered “Yes” to every question, his scheme was doomed to failure.

My friend had discovered the fundamental methodological difficulty that faces every historian, biographer, psychotherapist, and reader of autobiography, the problem of self-report. How are we to know what is true if we must depend on what interested parties tell us? The historian and biographer, at least, have access to alternate sources and to the intersection of the independent stories of reporters with different axes to grind. We don’t need Napoleon’s Mémoriale de Sainte-Hélène or Wellington’s papers to know who won at Waterloo, and neither source would have been enough for Hugo’s description of it in Part Two of Les Misérables.

Public events have many private versions, but private events produce only a single public show. The readers of The New York Review of Books need only reread the January 12, 1995 issue to see the problem in two of its manifestations: one, in the autobiography of a scientist who has been engaged in contentious ideological battles over his scientific claims for half of his professional life,1 and the other, in the bitter struggle over the reliability of repressed memories of childhood abuse.2 A third, and even more difficult one, is the attempt to find out what people do in their quest for sexual gratification and why. The famous studies by Alfred Kinsey and his collaborators in the 1940s and 1950s which have become part of everyday reference as “The Kinsey Report,” the later research by Masters and Johnson, and the more popularly read work of Shere Hite, 3 are part of a long history of the science of “sexology.” Vern Bullough’s Science in the Bedroom is an extensive review of that unsatisfactory history. “Bedroom” is, of course, pure synecdoche, since no space that can contain one or more human beings appears to have been excluded from the possible sites of sex. The latest try at knowing who does what to whom, and how often, is the National Opinion Research Center’s The Social Organization of Sexuality, completed just too late to be included in Bullough’s historical survey. Suspecting that Americans would not be wholly indifferent to their findings, the research workers who produced The Social Organization of Sexuality also arranged with the well-regarded science journalist Gina Kolata to collaborate on a popular version, Sex in America, an haute vulgarisation of our basses vulgarités.

We all have created elaborate fictions, both conscious and unconscious, that we try to sell to ourselves and others as the real stories of our lives. The reader of conventional autobiography is, in principle at least, able to test some of the self-indulgences of autobiographers, since much of what is of general interest in a public life has been seen and heard by others who may be consulted. Moreover, autobiographers do not know from the beginning that they will publish a life story, so they may commit to writing, unthinkingly, rather contradictory material. But these provide only a theoretical possibility of looking for the truth, since, with not many exceptions, one must be a Napoleon before anyone will bother to check an author’s memoirs against the record. For the most part, autobiography is a free ride into history. Repressed memories, too, are not entirely liberated from tests of their credibility. First, it may be that repressed memories simply do not exist so that every claim to them must be false. It might indeed be true, as claimed by Frederick Crews, that the entire experience of psychiatry and psychology speaks against the phenomenon. Second, even if repressed memories do, in fact, exist, and can be called to consciousness by appropriate techniques, the credibility of particular repressed memories is strained by their content. Sensible people can only scoff at reports of widespread Satanic rituals in which Babbitts consume the flesh and blood of babies.

There remains, however, one realm of self-report that seems utterly resistant to external verification. Given the social circumstances of sexual activity there seems no way to find out what people do “in the bedroom” except to ask them. But the answers they give cannot be put to the test of incredulity. Surely we believe that there is no sexual fantasy so outrageous and bizarre, no life of profligacy so exhausting, that it has not been realized by someone, somewhere, perhaps even by a reader of the New York Review’s personals. But if by someone, then why not by 17.4 percent of white males with two years of education beyond high school and with an annual income of $43,217? What behavior that is credible in individuals becomes incredible in the mass? The problem is to turn biography into science. If research produced by the National Opinion Research Center (NORC), the organization that epitomizes modern objective statistical social science, designed and analyzed by two distinguished service professors and a past president of the International Academy of Sex Research, carried out by a full time project manager in charge of 220 interviewers, and resulting in a book of 718 pages, including 178 tables, 34 graphs, and 635 references, does not crack the problem of knowledge from self-report, then not just “sexology,” but all of scientific sociology, is in deep trouble.


The motivations for the NORC study were two. First, given the evident importance of sex in people’s lives, it is hard to see how there could be an adequate theory of social processes, not to speak of efficacious planning of social policy, without an understanding of the shape of people’s sex lives. Unfortunately, previous social surveys of sex, as documented in Science in the Bedroom, were methodologically unsatisfactory. The flaws in these studies did not arise from a simple lack of technical sophistication. Bullough’s tremendously informative analysis shows that sex surveys did not come out of a general demand by sociologists to document yet another central feature of social life, or from the desire of theoretical sociologists to provide empirical evidence for some overarching theory of social determination. Rather, they were an outgrowth of a variety of theories of the determination of individual sexuality, of ideological convictions about sex and of a concern about sexual pathologies.

A major change took place between the end of the nineteenth century and the early years of the twentieth, as studies of sex ceased being a concern with pathologies and became part of a crusade for sexual liberation. The earlier tradition was represented by Krafft-Ebing’s famous compilation of scores of case histories, Psychopathia Sexualis, regarded as a scandalously raw book by my parents, who could not refer to it except sotto voce, and who would have been indignant to know that we pre-adolescents still tittered over its discreet Latin descriptions. The new “sexology” was epitomized by Havelock Ellis, whose research was in the service of a universal appreciation of human sexuality in all its aspects, including its formerly taboo manifestations in masturbation and homosexuality. For Ellis, the term “abnormal” meant simply a deviation from the average, being descriptive rather than normative in its intent. And between Krafft-Ebing’s ideal of sex and Ellis’s realities falls the shadow of Freud, who began with pathology and wound up with the domestication of incestuous desires. The gathering of case histories by these and other students of sex, like Magnus Hirschfeld in his attempt to establish the normality of homosexuality, was an instrument of argument, a demonstration of perceived truths about sex.

As psychology and social theory became social science, so studies of sex took on more of the methodological apparatus of the natural sciences. What were once compilations of illustrative case studies became large samples in objective surveys with elaborate interview protocols and questionnaires that included information about other social variables such as economic status. Yet these surveys remained in an ideological tradition. Bullough describes Kinsey as an objective scientist:

His two major works, the male study in 1948 and the female study in 1952, serve as effective indicators of the change taking place in American society. Though Kinsey is known for his diligent interviewing and summation of data, his work is most significant because of his attempt to treat the study of sex as a scientific discipline, compiling and examining the data and drawing conclusions from them without moralizing. [my emphasis]

But what Bullough has missed here is that discussing sex “without moralizing” is precisely the moral position that what people do with their erogenous zones is simply part of human natural history, that sex, in Ellis’s sense, is normal, and that notions of abnormality and deviance can have only a statistical meaning. So Kinsey and his epigones do not represent a real break in the smooth history of sexology, which continues to reflect the changing social attitudes toward fun in bed.

Moreover, it seems clear that Kinsey and Masters and Johnson and Shere Hite knew what they would find in their surveys, namely that, putting aside the trivia of percentages, a substantial number of ordinary people will say that they do anything you care to name. The lack of statistical rigor in the sampling techniques of these earlier studies is a revelation not of technical sloppiness, but of the studies as demonstrations of what their planners already believed they knew to be true. So the sexologists didn’t really think it mattered how they got their samples, and it turns out that they were substantially right because, as I will argue, sampling technique is not the important issue.


The second reason that the NORC team thought that a new sex survey was needed was its relevance to the epidemiology of AIDS. Because AIDS is spread largely through certain sexual practices, an accurate estimate of the frequency of such practices, the way they are distributed through the population, and what the network of sexual partners looks like, are all important variables in any model of the spread of the disease. If we are really interested in a useful epidemiological model of AIDS spread, not to speak of one that does not make the situation worse, we had better get the answers right. We have more than an academic interest in knowing whether self-report is a road to truth.

The National Health and Social Life Survey, to give the NORC study its full and revealing, or, rather, concealing title was designed originally to respond to a federal request for proposals (RFP) issued by the National Institutes of Health on behalf of a coalition of federal agencies concerned with AIDS. The missing “S” word in the title of the survey was a deliberate reflection of the absence of any reference to sex in the ironically misleading title of the RFP, “Social and Behavioral Aspects of Fertility-Related Behavior.” At the very least there is some anatomical confusion here. The attempt to mislead the prudes in the Bush administration did not work, however, and final approval of the project was never given. Nor did the change in administrations help, because the Democratic Congress explicitly prohibited the use of NIH funds for such a survey. In the end it was those fonts of immorality, the Robert Wood Johnson, the Rockefeller, Kaiser, Mellon, MacArthur, and Ford foundations who came to the rescue. Freed from the constraint of asking only about AIDS-related sex, the survey could then really ask about “fertility-related behavior.”

It is a characteristic of the design of scientific research that exquisite attention is devoted to methodological problems that can be solved, while the pretense is made that the ones that cannot be solved are really nothing to worry about. On the one hand, biologists will apply the most critical and demanding canons of evidence in the design of measuring instruments or in the procedure for taking an unbiased sample of organisms to be tested, but when asked whether the conditions in the laboratory are likely to be relevant to the situation in nature, they will provide a hand-waving intuitive argument filled with unsubstantiated guesses and prejudices because, in the end, that is all they can do. The Social Organization of Sexuality is a paradigm of the practice, made all the more objectionable by the air of methodological snootiness assumed by the authors when comparing their techniques with all the studies that have gone before. So they expend immense intellectual energy on the problem of taking a representative sample of Americans for an inquiry into their sex lives, but are rather cavalier about the question of whether people tell them the truth when asked.

The “sample survey” is the most highly developed technique of modern scientific sociology. Its purpose is to replace, by some objective measures, the impressionistic barroom wisdom of an older, more personal and reflective form of social commentary, in which an elaborate theory of social organization is built either on a prioris or on the commentator’s necessarily limited autobiographical experience of what people are like. One can imagine Leviathan written not in 1651 but in 1951: “The condition of the English man between the ages of 16 and 55 with an income of less than £50 is a condition of war of 73.4% of everyone against 58.6% of everyone else.”

A sample survey consists of two general procedures corresponding to the name of the process. First, it tries to characterize a population without examining every individual. That is, it is not a census of the entire population, but an attempt to recover the same information that would appear in a total census from a small (usually very small) sample of the entire group. Even the efforts of the Bureau of the Census and the Internal Revenue Service to get hold of every one of us turn out, in practice, to produce only samples, and therein lies a serious problem. Are the people who are not included different in some systematic way from those who were caught? This issue has plagued the organizers of the decennial Census, who have been accused of undercounting the homeless, the aged, the young, the black, and the poor. And even if they did include everyone, it would not require the unstinting efforts of Pat Robertson to keep them from asking us all about oral sex. A sample survey begins with the assumption that one cannot ask everybody the questions of interest, and devotes considerable statistical sophistication to finding 3,432 people who will accurately represent 200 million post-pubertal Americans.

Second, having decided whom to include in the sample, the survey must find a way of getting information. Sometimes, but remarkably infrequently, information can be acquired without the willing participation of the people sampled. Whether you like it or not, the state knows how much interest you earned in banks last year, and the number of cars per hour going across the George Washington Bridge on summer Sundays can be objectively determined. A good deal has been learned about patterns of consumption by measuring the output of garbage from urban households. But these are exceptions. For the most part social surveys depend on the answers people give on questionnaires, forms, and applications, or from other kinds of voluntary activities, and these are unreliable to different degrees.

One cannot know, for example, how many women suffer domestic assault by asking their husbands, or even count the ridership on the New York subways by the number of tokens taken in at the end of the day, although one of these estimates is clearly more reliable than the other. Nearly all the information that one would like to get about people is affected in some degree by the problem of self-report. The reader might try to imagine how he or she would get absolutely reliable information about the ages of living Americans independent of other social variables. Birth certificates do not tell who is still alive. Drivers’ licenses only find people who drive, under-representing, like social security records, the urban poor.

There are, moreover, different depths of unreliability in the answers to different implied questions. If people lie when we ask their ages, they are misleading us about their actual ages, and they are revealing something, although we are not quite sure what, about their attitudes toward age. If they lie when we ask them about their attitudes, say, whether they dislike blacks, we will not only under-estimate racism as a conscious prejudice, but also fail to estimate accurately the amount of practiced discrimination. More subtly, the answer to the question contains information about attitudes toward attitudes, about whether people consider their prejudices to be shameful, yet we have no way of knowing how to disentangle this self-reflexive aspect of human consciousness.

The National Health and Social Life Survey’s chief claim for its superiority over previous sex studies lies in its sampling methodology. The work of Kinsey, and of Masters and Johnson, were the efforts of “sexologists,” investigators whose training and interest were not statistical but descriptive. It was sufficient for them that non-negligible fractions of Americans engaged in a diversity of different practices. Kinsey, in particular, thought that picking people out of a hat would produce a sample of recalcitrant subjects who were unlikely to tell him what he wanted to know. Given Kinsey’s liberatory ideology, it was not of the utmost importance to him whether his estimate of 10 percent for male homosexuality was accurate. It was true to life. Kinsey’s samples made no pretense to be somehow numerically accurate representations of the entire population, but were what Edward O. Laumann and his colleagues in the NHSLS call “convenience samples,” consisting of patients, friends, neighbors, relatives, employees, people who have answered ads soliciting subjects for an experiment, or who have filled in a questionnaire sent to them because they are on the list of a periodical or an organization.

In contrast, the NHSLS sample was a so-called “probability sample” meant to make precise the chance that any American would be included. The process occurred in two stages. First a “random sample” of nine thousand addresses drawn from the Census was taken so that every household in the nation was equally likely to be included. Of these, about 3,700 were useless because no one lived there, or were excluded because the household had no English speakers or anyone between the ages of eighteen and fiftynine. The second stage was to increase the representation of black and Hispanic households by a known amount, producing a so-called “stratified sample,” because it was felt that these groups would be insufficiently represented in the random address sample to get accurate statistics on them.

The very words “address sample” and “probability sample” seem to promise a technological process that is ideologically neutral and objective, yet the sampling process itself, meant to be the study’s strongest point, is laden with social theory that is replicated and enlarged in the later analysis of the data. Social theory enters first at the moment of stratification. The claim that some groups need to be over-represented in the sample is based on a prior theoretical commitment to the relevance of those group identifications as variables in the eventual analysis. If one believed that religion was likely to be an important variable in determining people’s sexual behavior, then a study ought to include enough Buddhists, Confucians, Hindus, and Jews, to see whether belief in Original Sin really matters. In view of the preponderance of Christians, it would be necessary to add in extra heathens, since there might not be any Hindus at all in a random sample of five thousand households. Some of the readers of The New York Review may be disappointed to learn that there were so few Jews in the NHSLS sample that nothing can be said about whether they get more kicks from vaginal intercourse, anal touching, oral sex, using vibrators, watching other people, or ten other categories of potentially stimulating practices.

But why choose religion a priori as a relevant variable except that there is a mass of conventional social theory that claims its importance? Laumann et al. say that although they wanted to study what they call “sexual scripts,” the detailed network of relationships and practices, they could not because it was too hard. So,

Much fine grained cultural (and, to some extent, regional) variation in these scripts was beyond our grasp. Similarly, our ability to measure people’s networks was also quite limited. We could not ask them about…their relationships with specific persons other than their sex partners.

Their solution was to sample and analyze sexual behavior according to a set of prior categories that is easy to define and accord with standard notions of social causation.

Given these limitations, we adopted a primarily inductive approach using the types of information that are easier to collect accurately with large surveys, such as information about the respondent’s gender, race (and ethnic background), age, education, marital status, and religious affiliation. Each of these characteristics or “statuses” is a basic component of the self-identity of the individuals who possess them, organizes the patterning of social relationships, and organizes people’s understanding of the social world around them [my emphasis]. Of course, many other characteristics also possess these features; however, this basic set is both universally recognized and, in many cases, arguably most salient—hence the term master statuses.

“In many cases, arguably most salient”? So are these really the masters of our social and sexual lives or aren’t they? This is not the last time in The Social Organization of Sexuality that the authors try to finesse a deep question with a shallow phrase. As a matter of fact, these are not the only social variables that the survey asked about.

In a section of the questionnaire labeled with the ideologically neutral term “Demography,” the survey asked detailed questions about what can only be described as “social class”: Did your father or mother work for pay when you were fourteen? What did they actually do on the job? What kind of place did they work for? What was their education? How many hours a week do you work for pay? Describe in detail your job, your duties, what kind of place you work for, your wage rate?

Yet social class or anything like it is never discussed in the book, nor do these variables ever appear in the 178 tables and 34 graphs. Apparently it is not a “master status” variable. Indeed, reference of any kind to income appears only twice when we learn (Table 10.2) that “rich” people are slightly happier and much healthier than “poor” people, and that they are much more likely to be interested in sex and to succeed at it (Table 10.8). Perhaps poor people are just too tired out from trying to get through life. The authors make no comment. It might be claimed that the importance of the “master status” variables is justified after the fact by the results, since there are differences in reported sexual activity and practices among individuals falling in different groups. But aside from the obvious differences by sex, age, and marital status, the other “master variables” show surprisingly little variation in the answers given. For example, as a measure of promiscuity, one can ask what proportion of respondents report having had more than one sex partner in the last year. The answers were: 23.4 percent of males but only 11.7 percent of females, 32.2 percent of those aged 18–24 dropping to 18.5 percent at age 30–34, and 34.7 percent of never-marrieds but a mere 4.1 percent of those currently married. In contrast, there is hardly a difference between those who never finished high school and those with graduate school degrees (17.2 percent as opposed to 13.4 percent) and even less variation by professed religion: Jews (18.2 percent), fundamentalist Protestants (17.0 percent), Catholics (15.4 percent) or liberal Protestants (who at 15.0 percent seem the least “liberal” of all).

More important from a theoretical standpoint is the problem of proxy variables and the lack of independence between categories. To what extent are race and ethnicity, years of schooling, and even religion, proxies for social class? To what extent are these variables themselves interrelated? Being black, poor, unemployed, and without a high-school diploma go together, so which of these “master variables” is really the master, or are they all just ways of saying “lower class”?4 Laumann et al. make some attempt to deal with the correlation between these variables when they analyze the causes of the stability of unions and the age at which people enter them, but for the most part the categories are taken at their face value. From the very moment that a social survey sample is designed, the theoretical assumptions of the investigators about causal pathways in social determination come to dominate the study.

There is another peculiarity of the NHSLS sample that is particularly relevant because the study is said to be motivated by the need to make epidemiological models of the spread of AIDS. Because the sample is based on household address, the survey does not include the 3 percent of Americans (about 7.5 million) who do not live in households but are in institutions or are homeless. For many purposes ignoring 3 percent of the population is trivial, but for the epidemiology of AIDS it is precisely those in prison, in homeless shelters and on the streets, and in college dormitories who are most relevant. The prevalence of homosexual rape in prisons, the indiscriminate prostitution that characterizes drug addiction, and the relentless sexuality of college age adolescents all mean that these ways of living are characterized by unusually complex networks of sexual contacts within the institutions, and with sexual practices that are likely to spread AIDS.

The authors of Sexuality take note of the exclusion of the institutionalized but pass it off by suggesting that “it would be wise to design and execute specialized research projects designed to study these groups separately.” But studying these groups separately is precisely what it would not be wise to do. The prison, military, and college populations have a constant turnover, so that a very large fraction of the entire population has spent some protracted period as part of them. Perhaps the most important question that could have been asked of a male in the survey was “Have you ever spent time in prison?” If the answer were “yes,” then the appropriate next question would not be about his sex practices in the last year, but about what happened to him in Dannemora.

However, these were not regarded as “master status” variables. I would have thought that there is nothing like having been raped in prison to “organize people’s understanding of the social world around them.” The authors do not discuss it, and they may not even realize it, but mathematical and computer models of the spread of epidemics that take into account the real complexities of the problem often turn out, in their predictions, to be extremely sensitive to the quantitative values of the variables. Very small differences in variables can be the critical determinant of whether an epidemic dies out or spreads catastrophically, so the use of an inaccurate study in planning counter-measures can do more harm than does total ignorance.

The second major problem of sample surveys is to know what questions to ask and how to go about asking them. The founder of modern sociological research, William Fielding Ogburn, said that the central question for any claim of social theory was, “How do you know it?” 5 The answer, alas, cannot be, “Because I asked.” The problem for every sample survey is to know whether the answers are systematically untrue. Surveyed populations can lie in two ways. They can answer untruthfully, or they can fail to answer at all. This latter problem is known in the trade as “non-response bias.” No matter how hard one tries, a significant portion of the sample that has been chosen will fail to respond, whether deliberately, through accident, lack of interest, or by force of circumstance.

It is almost always the case that those who do not respond are a non-random sample of those who are asked. Sometimes the problem is bad design. If you want to know how many women work outside the home you will not try to find out from a telephone survey that makes calls to people at home between nine AM and six PM. Much of the expertise of sample survey designers is precisely in knowing how to avoid such mistakes. The real problem is what to do about people who deliberately avoid answering the very questions you want to ask. Are people who refuse to cooperate with sex surveys more prudish than others, and therefore more conservative than the population at large in their practices? Or are they more outrageous, yet sensitive to social disapprobation? Because they do not answer, and self-report is the only tool available, one can never know how serious the nonresponse bias may be. The best that can be done is to try to minimize the size of the non-responding population by nagging, reasoning, and bribing. The NHSLS team tried all these approaches and finally got a response of 79 percent (3,432 households) after repeated visits, telephone calls, videotapes, and bribes ranging from $10 to an occasional $100. The result was that there were now three sample populations, those who were cooperative from the start, those who were reluctant but finally gave in, and those who refused to the end.

From an analysis of the eager and the reluctant it was concluded that for most questions there was no difference between the two, but that still leaves in the air the unanswerable question about the sex lives of those who found $100 an insufficient payment for their true confessions. If I can believe even half of what I read in The Social Organization of Sexuality, my own sex life is conventional to the point of being old-fashioned and I wouldn’t have cooperated for any price the NORC was likely to find in its budget.

Finally, we cannot avoid the main question, whether those who did respond, reluctantly or eagerly, told the truth. Far from avoiding the issue, the study team came back to this central question over and over, but their mode of answering it threatens the claim of sociology to be a science. At the outset they give the game away.

In the absence of any means to validate directly the data collected in a survey of sexual behavior, these analyses assess data quality by checking for bias in the realized sample that might result from potential respondents’ unwillingness to participate because of the subject matter, as well as by comparing results with other surveys. In every case, the results have greatly exceeded our expectations of what would be possible. They have gone a long way toward allaying our own concerns and skepticism…. [emphasis added].

In other words, people must be telling the truth because other people have said it before and they say the same thing even if reluctant to answer. That many people at many times have independently claimed to have been present at Satanic rituals or seen Our Lady descend at Fatima, and that some of these witnesses have been reluctant to testify at first, will presumably convince Professor Laumann and his colleagues of the reality of those events.

Again and again the problems of how we elicit the truth when both conscious and unconscious distortions may be suspected are dealt with disingenuously. Men and women were interviewed by women and men indiscriminately, and there was no attempt to match race of interviewer and race of the respondent.

Will men and women respondents be affected in similar or different ways [by this mixing of sexes of interviewer and respondent]? Will people who have engaged in socially disapproved activities (e.g., same-gender sex, anal sex, prostitution, or extramarital sex relations) be equally likely to tell this to a male as to a female interviewer? At present, these questions remain unresolved empirically…. Although this issue is certainly important,…we did not expect the effect of gender matching to be especially large or substantively noteworthy. The experience and belief among NORC survey research professionals was that the quality of the interviewer was important but that it was not necessarily linked to gender or race.

In other words, they don’t know and hope the problem will go away. While sex and race are “master status” variables, “organizing the pattern of social relationships,” apparently being interviewed about your sex life is not part of social relationships. Instead of investigating the problem, the team “concentrated our time and money on recruiting and training the best interviewers we could find.” That meant three days of a “large-scale” training session in Chicago.

Anyway, why should anyone lie on a questionnaire that was answered in a face-to-face interview with a total stranger? After all, complete confidentiality was observed. It is frightening to think that social science is in the hands of professionals who are so deaf to human nuance that they believe that people do not lie to themselves about the most freighted aspects of their own lives, and that they have no interest in manipulating the impression that strangers have of them. Only such deafness can account for their acceptance, without the academic equivalent of a snicker, of the result of a NORC survey reporting that 45 percent of men between the ages of eighty and eighty-four still have sex with a partner.

It is not that the research team is totally unaware of sensitivities. In addition to about a hundred face-to-face interview questions, respondents were asked to fill out four short printed forms that were placed by them in sealed “privacy” envelopes for later evaluation by someone other than the interviewer. Many of the questions were repetitions of questions asked in the personal interviews, following the common practice of checking on accuracy by asking the same question twice in different ways. Two matters were asked about, however, that were considered so jarring to the American psyche that the information was elicited only on the written forms: masturbation and total household income. Laumann et al. are not so deaf to American anxieties as it seemed.

There is, in fact, one way that the truth of the answers on a sex survey can be checked for internal consistency. A moment’s reflection makes it clear that, discounting homosexual partners, the average number of sex partners reported by men must be equal to the average number reported by women. This is a variant on the economist Robert Solow’s observation that the only law in economics is that the number of sales must be equal to the number of purchases. Yet, in the NHSLS study, and other studies like it, men report many more partners than women, roughly 75 percent more during the most recent five years of their lives. The reaction of the authors to this discrepancy is startling. They list “in no particular order” seven possible explanations including that American men are having lots of sex out of the country, or that a few women are having hundreds of partners (prostitutes are probably underrepresented in an address sample, but prostitution was not regarded as a “master status” variable to be inquired about since presumably it is not a “basic concept of self-identity”). Our authors then say,

We have not attempted to reconcile how much of the discrepancy that we observe can be explained by each of these seven logical possibilities, but we conjecture that the largest portion of the discrepancy rests with explanation 6.

Explanation 6 is that “Either men may exaggerate or women may understate.” So, in the single case where one can actually test the truth, the investigators themselves think it most likely that people are telling themselves and others enormous lies. If one takes the authors at their word, it would seem futile to take seriously the other results of the study. The report that 5.3 percent of conventional Protestants, 3.3 percent of fundamentalists, 2.8 percent of Catholics, and 10.7 percent of the non-religious have ever had a same-sex partner may show the effect of religion on practice or it may be nothing but hypocrisy. What is billed as a study of “Sexual Practices in the United States” is, after all, a study of an indissoluble jumble of practices, attitudes, personal myths, and posturing.

The social scientist is in a difficult, if not impossible position. On the one hand there is the temptation to see all of society as one’s autobiography writ large, surely not the path to general truth. On the other, there is the attempt to be general and objective by pretending that one knows nothing about the experience of being human, forcing the investigator to pretend that people usually know and tell the truth about important issues, when we all know from our own lives how impossible that is. How, then, can there be a “social science”? The answer, surely, is to be less ambitious and stop trying to make sociology into a natural science although it is, indeed, the study of natural objects. There are some things in the world that we will never know and many that we will never know exactly. Each domain of phenomena has its characteristic grain of knowability. Biology is not physics, because organisms are such complex physical objects, and sociology is not biology because human societies are made by self-conscious organisms. By pretending to a kind of knowledge that it cannot achieve, social science can only engender the scorn of natural scientists and the cynicism of humanists.

This Issue

April 20, 1995