Robert B. Joynson
Society, March-April 1994 v31 n3 p45(8)

Robert B. Joynson is author of The Burt Affair, published by Routledge in 1989. He is a British psychologist who resides at Ormonde House. He was formerly with the department of psychology at the University of Notingham.

Brief Summary: Scientific studies of psychology are particularly vulnerable to subjective interpretation. The false charges of research fraud leveled against Burt, demonstrate how psychological research is too vulnerable to political and social influences.

The British pioneer of educational psychology Cyril Burt (1883-1971) was first publicly accused of scientific fraud in 1976, five years after his death. Oliver Gillie, then medical correspondent to the London Sunday Times (October 24, 1976), reported that "leading scientists are convinced that Burt published false data and invented crucial facts to support his controversial theory that intelligence is largely inherited." The debate that ensued died down only with the publication in 1979 of Leslie Hearnshaw's biography of Burt. Hearnshaw, who had access to Burt's diaries, claimed that these provided decisive evidence of Burt's guilt, and concluded that the chief allegations were true "beyond reasonable doubt." His verdict was endorsed, without further inquiry, by the British Psychological Society in 1980.

In the last few years, there has been a remarkable revival of interest in the case of Cyril Burt, for very serious doubt has been thrown on the validity of the allegations. The evidence was examined independently by Banks in 1983, by Ronald Fletcher in 1987 and the present writer in 1989). These investigators all oncluded that the charges cannot be sustained. The question of Burt's guilt has been thrown wide open and the Council of the British Psychological Society has announced in a Council Statement in 1992 that the Society "no longer has a corporate view on the truth of allegations concerning Burt."

No one can foresee how die debate will continue, but it seems unlikely that it will prove possible to restore the position which existed in 1980. Hearnshaw's confident verdict broke down basically because the evidence is, and must remain, incomplete. The case against Burt could only be substantiated if Burt, and his chief assistant, Conway, were available for questioning; and if Burt's raw data sheets were available for inspection. But Burt and Conway are both dead, and Burt's data have been destroyed. Under these circumstances, accusations of fabrication of data remain questionable.

The way in which Burt was condemned has also been found wanting. There is a basic injustice in condemning a man who cannot defend himself; and the Council of the British Psychological Society has, if a little late in the day, come to the conclusion that "it should not normally attempt to pass corporate judgment on the alleged misconduct of any member now deceased." Thus, even if a strong case against Burt could again be assembled, it is most unlikely that it would again be officially endorsed.

The posthumous condemnation of Burt destroyed his reputation, and undermined his life's work; and it is a matter for grave concern that the evidence should prove to be unreliable, and the procedure unjust. But the grounds for concern go far beyond the issue of justice for an individual, important as that is. The case has aroused wide interest, and much controversy, primarily because of its political dimension. Burt had exercised considerable influence on educational policy, and when he was accused of fabricating his data it was widely asserted that he had done so in order to support right-wing views on selective schooling. If this were true, Burt would have been guilty of a monstrous betrayal of science.

Moreover, the accusation attracted maximum publicity, and Burt's reputation maximum odium, because it was made at a time when controversy concerning the inheritance of intelligence was at its height. The questions of affirmative action and of black-white intelligence in America, and of comprehensive of selective schooling in Great Britain, were among the topics most closely affected. Thus a political interpretation was at once attached to the case, which varied according to the standpoint of the writer. The Times referred darkly to "the ideological foundations of the hereditarian position (November 9, 1976).

Hans Eysenck wrote in a letter to Marion Burt in 1976, "I think the whole affair is just a determined effort on the part of some very left-wing environmentalists to play a political game with scientific facts." Heim commented that "the pre-occupation of the left-wing with extreme environmentalism and of the right-wing with heritability ... largely accounts for the axe-grinding dogmatism of the protagonist." (The Times, November 1, 1976) The relation between these political pressures and the accusations made against Burt is a central and unavoidable issue.

In 1992, Arthur Jensen provided a comprehensive review of the evidence to date. The aim of the present article is not to offer a further review, but to ask what the affair has to teach us about the social sciences in general, and psychology in particular.

Psychology of Scientific Investigation

How did it happen that first Burt's original accusers, then his biographer, and finally the Council of the British Psychological Society itself, all made such apparently fallible judgments in a matter of such exceptional importance, a matter in which psychology's reputation for scientific detachment was at stake? First, we must ask how mistakes and errors arise in the interpretation of scientific data in general. Indeed, all allegations of fraud and deception in science need to be considered in this context, for we can be sure that culpable deception has occurred only after the possibility of human error, whether in the accuser or the accused, has been eliminated. William James had some wise words on the subject of scientific discovery. In his essay "The Will to Believe," James stated that the investigator must care deeply about the outcome of his inquiry: "[S]cience would be far less advanced than she is if the passionate desires of individuals to get their own faiths confirmed had been kept out of the game." By contrast, indifference to the outcome of an inquiry was fatal: "[I]f you want an absolute duffer in an investigation, you must ... take the man who has no interest whatever in its results: he is the warranted incapable, the positive fool."

But the "passionate desire" to confirm our own faith makes us prone to ignore evidence to the contrary, unless we are constantly on our guard. James concluded: "The most useful investigator, because the most sensitive observer, is always he whose eager interest in one side of the question is balanced by an equally keen nervousness lest he become deceived. Science has organized this nervousness into a regular technique."

Social scientists thus should not to be for their political or social values, whether of the right or the left, nor for their desire to see those values confirmed. Criticism should be reserved for those whose eager interest in one side of the question is not balanced by an equally keen nervousness lest he become deceived. Those who claim the authority of science must be prepared to demonstrate that they regard its "regular technique" as paramount; and that they are not ignoring or abusing that technique in order to further their own faith. But at this point an acute difficulty arises. The "regular technique" of science does not provide a rigid routine which, if slavishly followed, guarantees a valid outcome. There is always some latitude for fallible individual judgment, both in the application of the method and in the interpretation of its findings. Consequently, there may be disagreement about what the regular technique requires; and when passionate desires are involved, the disagreement can rapidly turn into furious recrimination.

In the aftermath of Burt's condemnation, the British Psychological Society organized a symposium to discuss "Burt's deceptions ... in the wider context of scientific method in psychology." Blackman in 1980 drew attention to the role of personal judgments about experimental data, especially in relation to the assessment of the reliability, the validity, and the scientific significance of data. He concluded that "there are no fixed rules which provide even experimentalists with security and safety from making false or inappropriate inductive inferences about their data."

Selection begins in perception, in attending to some things and ignoring others. The process continues in experiment, with its carefully restricted and controlled situation. It is carried still further in describing the experimental results, for it is impossible to include everything which happens; and even if it were possible, it would be intolerably tedious. We have to select what we consider most relevant and ignore the rest; and what we choose to include, and what we choose to omit, can only be, to a large and uncertain extent, a matter of personal judgment. This long and unavoidable process of selection provides "the passionate desires of individuals to get their own faiths confirmed" with a magnificent opportunity to seize on every scrap of favorable evidence, and brush everything else aside.

The judgment of size and distance, like many perceptual topics, raises questions about the subject's "attitude." Roughly speaking, a subject may either attend to the sheer sensory input, such as the apparent size, shape, or color of an object (often called an "analytic" judgment); or he may report his perceptual impression of the true properties of the object, as he might judge in everyday life (sometimes called a "naive" judgment.)

Gestalt psychologists, who made so many important contributions in this field, have always maintained that analytic judgments are artificial constructions, only introduced to prove a theory, and never occurring without special instructions and training; and accordingly their theories were based entirely on "naive" judgments. In my own experiments I found that analytic judgments frequently appeared quite spontaneously, with no special instructions or training at all. What we like to call the given, the experimental datum, the observed fact, may be, not the whole truth, but just that part of which we like the look - an apt phrase in this context.

Even when we agreed what data are significant, there may be genuine disagreements over how they are to be interpreted. In the following instance, the data were obtained in an experiment originally undertaken with a view to confirming Helson's views on "central tendency" effects. In the case of size and distance, this would involve showing that, if the subject is presented with a series of target objects of varying size, targets around the average value of the series would tend to be judged accurately, whereas targets deviating from the average value would be judged with increasing inaccuracy; these tendencies varying with distance in predictable ways.

The questions at issue are difficult to settle because the "regular technique" of science does not provide an infallible set of rules which can be automatically applied. individual judgment is required. It is also not difficult to understand how suspicions of dishonesty might arise, however unjustified. But the accusation of dishonesty should always be the last resort. First, we should explore the innumerable ways in which honest differences of opinion may arise.

Most of us resist the temptations to invent data because we do not merely want to confirm our own faiths, we also want to convince ourselves, as well as others, that we are good scientists. The omission of data, by contrast, offers an almost unlimited field for self-justificatory ingenuity. Omission, as we have seen, is part and parcel of the normal process of experiment, and a thousand innocent reasons spring to mind for omitting what does not seem to fit in. Did the subject understand the instructions? Was he distracted? Was there some failure in the apparatus? Were the responses correctly recorded? The possibilities are endless.

Even the decision when to conclude an experiment may be affected. There may often be excellent reasons for eliminating errant subjects. But it is the experimenter who makes the decision, and it is fatally easy to confuse good reasons with welcome excuses. In the matter of the omission of data, then, there is a large area where moral and technical issues are mixed up together, and where even the wisdom of Solomon might be strained.

Confrontation of Facts and Values

The condemnation of Cyril Burt took place when the debate concerning the inheritance of intelligence was at its height, and it will be instructive to recall some observations on the controversy which were made by a natural scientist who was not himself involved in it. In 1977 (that is, after the initial accusations had been made against Burt, but before they had been endorsed by Leslie Hearnshaw and the British Psychological Society), the presidential address to the British Association for the Advancement of Science was delivered by Sir Andrew Huxley, a Royal Society Research Professor in the department of physiology at University College London and grandson of the eminent Victorian scientist Thomas Huxley. The lecture was concerned with the importance of basing conclusions upon scientifically established facts, whatever our political or social values may be.

Huxley began by distinguishing "clues" from "evidence." Aclue, he said, is an isolated fact, recognized as possibly significant to the problem in hand, but capable of various interpretations. Clues are indispensable in the early stages of research, when the scientist is considering what observations to make, and what hypotheses to frame. But clues remain capable of many interpretations, and further facts are needed to decide among them; they are suggestive not decisive.

Evidence, by contrast, is an organized arrangement of well-attested facts, if possible experimentally established, which leads to a compelling interpretation. It is easy to be led astray, especially in the early stages of research, by assumptions which lead to false expectations. It is important that the scientist not confuse clues with evidence, or reach premature conclusions through treating clues as if they were evidence. Thus Darwin collected many clues to evolution during his voyage on the Beagle in 1839, but spent twenty years testing and correcting his ideas before he was ready to publish in 1859. This was surely a classic instance of "eager interest" in the establishment of a preferred hypothesis being balanced by "keen nervousness."

Motive, if we are not careful, may disrupt the patient process of converting clues into evidence. Darwin's habit of recording observations unfavorable to evolution, lest he forget them, is well known. In his case, motive also featured spectacularly in the emotional opposition which his ideas aroused, both from conservative scientists who clung to the long-accepted principle of the fixity of species, and from theologians and others who saw a threat to the authority of the Bible and to morality. The question at issue in the famous confrontation of 1860 between the Bishop of Oxford and Thomas Huxley was whether a scientific question should be decided by factual evidence, or by what we might wish to believe for other reasons.

Andrew Huxley then said that he had sometimes asked himself whether any contemporary question could lead to a similarly dramatic and emotional confrontation between facts and values; and suggested that an instance was indeed to be found in the contemporary debate concerning the inheritance of intelligence. Any assertion of large natural differences in ability between individuals, or classes, or ethnic groups, was seen by some people, he said, as a threat to political ideals of equality, and was denounced as elitist or racist. Huxley delivered a scathing denunciation of "scientists who regard the assumption of equal inherited ability as something which does not require experimental evidence to establish - and which it is politically wicked to question, because the conclusion might disagree with their social and political preconceptions."

Huxley went on to say that the scientist has "a special claim to be listened to as long as what he says is soundly based on actual evidence, but he forfeits that claim if he presents preliminary or uncertain results - that is to say, clues - as if they were well supported by evidence, or, more important, if he selects or slants his results so as to support a view which he holds on other grounds, however meritorious or otherwise that view may be."

In his response to Huxley's lecture, Young alleged, in an article in 1977 in the Times Higher Education Supplement, that so far as Burt was concerned "the values, theory and policy came first" and the findings were created, embroidered or tidied up to suit them. Huxley replied that, if this were true, it would be an instance of that which he condemned. But, he added, "I do not myself believe it is true."

Huxley's parallel with the events of 1860 likened the hereditarians to the Darwinians, as the party of those who appeal to factual evidence; and the environmentalists to the theologians, as the party of those who prefer "what we mightwish to believe for other reasons." But historical parallels rarely hold exactly, and the position today is by no means so black-and-white as when Thomas Huxley did battle with the Bishop of Oxford (if indeed it was quite so black-and-white then). We are all to an extent torn between facts and values.

Huxley himself pointed to a significant divergence when he said that the evidence to support the case for or against the inheritance of ability was not to be compared with the overwhelming body of evidence which Darwin had amassed in 1860: "Even the strongest proponent of substantial inherited differences is aware that a large social component also exists."

A further important distinction to be made is that the case for heredity in the 1970s was not, as was the case for natural selection in the 1860s, a new challenge to an old orthodoxy. It goes back to Galton's hereditary genius of 1869; and among the pioneers of psychometrics there was from the beginning a widespread belief that mental tests came close to measuring a "natural" level of intelligence, independent of schooling. There was also a readiness to accept favorable "clues" which today we should find unconvincing, as when Spearman wrote to Burt about the latter's first paper in 1909 that "the evidence as to heredity of intelligence is very striking."

In spite of the uncertainties, mental tests were soon used to select out those believed to be naturally gifted or naturally backward; and by the 1920s and 1930s this had become a widely accepted practice, especially in Great Britain where psychologists were often consulted on issues of national education. A belief in the importance of heredity was thus part-and-parcel of the whole psychometric movement; and by mid-century was well established despite the limitations of the evidence.

Psychometrics, however, had always had its critics, and they remained vocal today. At Cambridge, England, objections focussed on the statistical analysis of tests and their reliability, while Otto Zangwill expressed concern in 1950 about premature application. In America, too, there was interest in the role of the environment, especially in early development. During the 1960s and 1970s, it was increasingly asserted that the psychometric movement in general, and the belief in the importance of inheritance in particular, were inspired, not by cogent scientific evidence, but by right-wing political convictions.

Leon Kamin's book Science and Politics of IQ was a notable expression of this critique. Kamin interviewed the whole body of hereditarian evidence in great detail, and concluded: "There are no data sufficient for us to reject the hypothesis that differences in the way in which people answer the questions asked by testers are determined by their palpably different life experiences." He also argued that the whole mental testing movement had been fostered by men with strong right-wing values who had misused it for political purposes as in the control of immigration to the United States. Pseudo-science was being used to justify and implement political policies.

Kamin's conclusions were seen by many as a travesty of the empirical evidence in the field. But an experimental psychologist at Cambridge, considered that Kamin had performed "a notable service by subjecting the evidence on die heritability of intelligence to searching and critical analysis," and added that "both in quality and quantity the evidence for the heritability of IQ is very much less than had generally been suggested. The data are sparse rather than plentiful, and at best persuasive rather than decisive." It seems, then, that a not implausible case might be made for inverting Huxley's parallel. Might not hereditarians be seen as a premature orthodoxy, swayed by wishful thinking, and environmentalists as the new scientific challenge?

There is much to support Kamin's argument. His fundamental criticism - that the hereditarian standpoint may sometimes be adapted in part for political rather than empirical reasons - is both true and unimportant. Rose warned in an article in the Times Literary Supplement in 1992, against assuming that "hereditarian educational psychologists are scientists following where the data inexorably lead, unmoved by their social and political implications." In this respect, then, Huxley's parallel needs qualification. But we must equally beware of assuming that environmentalists are scientists "following where the data inexorably lead, unmoved." There is an obvious possibility in Kamin's case that the bias derives from loyalty to the left. Indeed, Rose, Kamin, and Lewontin, in Not in Our Genes, preface their critique by announcing their politics: "We share a commitment to the prospect of the creation of a more socially just - a socialist - society." The beam in their own eye bears a remarkable resemblance to that which they detect in the eye of their opponents.

The truth is surely that none can claim a monopoly of scientific virtue. All are exposed to a struggle between political preference and loyalty to science. There is a very real possibility that supposedly scientific findings may be a cloak for political values, whether of the right or left. This raises acute problems for a scientific psychology. We have to recognize that the "regular techniques" of science cannot yet provide, in this field, an objective assessment of the evidence wholly independent of human judgment; and where human judgment is involved, social and political values may enter.

If we follow William James, we shall not condemn an "eager interest in one side of the question." We shall recognize that this may be the spur to discovery. J. M. Today, head of the department of genetics at Cambridge, contended in an article, "Probity of Science: The Case of Cyril Burt," in Nature in 1981: "[I]deological motivation may have a place in science. If strong distaste for scientific conclusions leads to honest and intelligent criticism of the data base or logical base for those conclusions, this is to the good." Yes, indeed; but who is going to tell us when the criticism is honest and intelligent and when not? The "elitists" or the "egalitarians"? The "eager interest" of the parties is unfortunately not always balanced by an equally "keen nervousness."

Kamin and those who think like him are, of course, politically correct, but their language has sometimes been distinctly unparliamentary. Kamin was not content to point to prejudice; he charged dishonesty. His book The Science and Politics of IQ begins with a sweeping insinuation against hereditarians in general: "Patriotism, we have been told, is the last refuge of scoundrels. Psychologists and biologists might consider the possibility that heritability is the first."

In the 1970s to be accused of dishonesty had become an occupational hazard for hereditarians, and there was an audience ready and willing to believe such accusations, however flimsy the evidence. So there is an obvious alternative to supposing that Cyril Burt fabricated his data, namely, that he was a victim of left-wing hostility. There is strong evidence for such bias in at least some of Burt's accusers, notably Barbara Tizard.

In a memoir of her husband, Child Development and Social Policy: The Life and Work of Jack Tizard, she describes him as a "passionate egalitatian ... for many years a member of the Communist Party" and also as "believing he could most effectively help to improve society through his research." It is not suggested that any of Burt's critics deliberately accused him of fraud, believing the charge to be false; only that their "passionate desires to get their own faiths confirmed" swayed their judgment, leading them to seize on every scrap of evidence, however implausible, to assault those who disagree with them.

It is remarkable that Hearnshaw never seems to have taken this possibility seriously, the more remarkable still since he rejected the claim that Burt himself was inspired by right-wing motives; and pointed out that, in so far as Burt had political preferences at all, they were liberal rather than conservative. Burt belonged to an earlier generation of progressive thinkers whose ideal was "equal opportunity." Heredity provided a rationale for the ideal, and mental testing a means of implementing it; so that, for them, equal opportunity was a happy combination of scientific fact and social value. The assumption that belief in heredity automatically entails right-wing views seems to be a relatively recent delusion, no more justified than the assumption that belief in environment necessitates left-wing sympathies. Of course, if Burt did not possess right-wing motives, he had other possible incentives to fraud, such as the desire to justify his Iife-long commitment to heredity. But it should not be forgotten that his critics had their motives too. However, the issue - scientific fraud or false accusation? - can only be decided, if it can be decided at all, by the evidence itself.

A Keen Nervousness

Scientists have a duty to be honest, like everyone else; and like everyone else, they are entitled to the presumption of innocence - the onus of proof lies with the accuser. But scientists also have a duty peculiar to themselves: to observe the regular technique of science. This is not a moral duty, but a professional obligation. If they fail, they are not wicked; they are incompetent. However eminent a scientist may be, the onus of proving competence still lies with him.

Burt published his account of his twin data in 1966 in an article in the British Journal of Educational Psychology, "The Evidence for the Concept of Intelligence." Much of the data had been collected many years before, during the 1920s and 1930s, in the course of his well-known survey of the abilities of London school children. The survey encountered many twins, and in the 1940s Burt extracted this material for special study and supplemented it with additional data. Several preliminary references to the twin data appeared before the final report of 1966. These occur in books and papers which were preliminary concerned with more general questions; they are appended at points where evidence concerning heredity would be relevant; and they are brief - at most a couple of pages or so - omitting much of the information properly to be expected in experimental reports.

Burt left himself open to strong criticism for these anticipatory statements. He was expecting the reader to take his conclusions on trust, providing little or no information for critical assessment. He was treating clues as if they were evidence. Burt left himself open to the charge of arrogance, and it is not at all surprising to find J. Shields in his book Monozygotic Twins: Brought Up Apart and Brought Up Together commenting pointedly on the lack of detail in Burt's article, "Ability and Income," in British Journal of Educational Psychology in 1943. Burt's 1966 paper was a great improvement. It is not seriously deficient - at least by the standards of the time - with regard to the main types of information to be expected; though as with all such reports it is easy to find matters on which one would like more information. But is there in this whole series of publications, any evidence of deliberate fabrication? It should be borne in mind that the correlations Burt reported are very similar to those of other investigators, so there are no grounds for accusing him of attempting to deceive with respect to the strength of any hereditary effect. Kamin (1974) claimed that many of the correlations for intelligence Burt reported over the years had remained the same even though the number of subjects on which they were based had altered considerably. Such a finding is so unlikely as to be wholly unbelievable; and Kamin suggested that Burt had fabricated these correlations to give the impression of accuracy and reliability to his data on the inheritance of intelligence.

Undoubtedly many correlations remain the same in Burt's successive reports; indeed, there are even more than Kamin noticed. But Kamin seems to be mistaken in supposing that in all these cases the number of subjects had changed. The mistake arose largely because Burt did not always make clear, in his aforesaid inadequate preliminary reports, the number of subjects on which correlations were based. When these reports are compared with the 1966 report, it is easy to jump to conclusions that are, on more careful examination, found to be unjustified.

Burt reported three categories of correlation - for intelligence, for educational attainment, and for physique. The invariants are in fact found predominantly among the physical correlations, to a lesser extent among the educational, and least of all among those for intelligence. Kamin does not seem to have noticed this imbalance, though of the thirteen cases of invariance which he reports no less than eleven concerned physique or educational attainment; and of the two instances which concerned intelligence, one was corrected by Burt before he died, and the other may well have been a coincidence.

A possible explanation for the uneven distribution of the invariants would be that, as Burt gradually collected more data, there would come a time when he possessed as many measurements for physique and educational attainment as he needed to give reliable results, but when more measurements of the crucial intelligence levels were still advisable. In subsequent cases, the measurements for education and physique would then be dropped and attention concentrated on the assessment of intelligence.

Thus, when the final report was made public in 1966, the correlations for physique and educational attainment would be based on the smaller numbers collected at an earlier stage, and would therefore remain unchanged; whereas the correlations for intelligence would be based on larger numbers, and would therefore have altered. Something very like the observed distribution of repeated and new correlations would naturally result. Burt made clear both the 1955 and 1966 article that some of the correlations for physique were based on smaller numbers, but he did not explain why this was, nor did he give details of the precise numbers on which all the correlations were based on all occasions. Kamin seems to have been misled in part because he overlooked the distribution of the invariants, but also, and very excusably, by Burt's omission of sufficiently clear information about numbers.

But the omission of this information is a flimsy ground for accusing Burt of fabricating or manipulating his data. It is hard to see what Burt could have gained by the omission, because if anyone had wanted to know they could have asked him. The motive which Kamin ascribed to him is highly implausible. Correlations which remain constant even when numbers change are a statistical anomaly and suggest that something is wrong. The idea that Burt, an expert statistician, would concoct such results deliberately to demonstrate reliability, is absurd. He would know perfectly well that any such claim would be immediately rejected. The competent scientist produces a competent fabrication. Burt is certainly to be criticized for his omissions; but Kamin jumped to his conclusions altogether too quickly.

Another aspect was the case of the missing assistants. In 1976 Oliver Gillie, his suspicions aroused by reading Kamin, attempted to trace two female assistants with a view to questioning them about the kinship research. He contacted Tizard at the University of London Institute of Education who told him that he, Tizard, had already tried to find them, without success. Had Burt perhaps invented them? Gillie's search was equally unsuccessful, and in a Sunday Times article he promptly suggested that they may never have existed. Hearnshaw eventually added to these suspicions through his account of Burt's post-war diaries. These diaries, according to him, provided an extremely thorough and detailed account of Burt's activities, yet curiously failed to furnish any evidence that Burt had been in contact with his supposed assistants, or that they had been involved in collecting twin data, during this period. The absence of such evidence was in Hearnshaw's view decisive.

Burt recorded little information about the two assistants, and questions can certainly be asked to which Burt's papers contain no answer. As presented by Hearnshaw, the gaps in the record were made to seem very suspicious, especially in the context of Kamin's earlier doubts. But the "decisive evidence" of the diaries, as Hearnshaw called it, has proved to be nothing of the sort, as was shown by Ronald Fletcher as well as by Charlotte Banks and the present writer. They are far from being a complete or detailed record of Burt's activities.

Sometimes they are entirely empty for weeks and months on end; large stretches contain mainly domestic details, appointments, notes on the weather, and so on; detailed information about psychological matters is infrequent. The absence of reference to twins means virtually nothing. In any case, Burt himself said that most was collected earlier, before 1950, hence even if the diary record had been as complete as Hearnshaw alleges, twin references would probably be rare. In addition, the major gap - the missing assistants - has been remedied, at least to the extent of demonstrating that they really did exist.

Why, if most of Burt's data was collected before 1950, did he delay full publication until 1966? There are a number of possible explanations. He may have been collecting some additional cases (he was still appealing for more in 1955). He may have, as Banks suggests, been searching for some of his earlier data mislaid in wartime moves; competing pressures may have distracted him; increasing age and illness did not help. It is possible that he started inventing data in the 1950s or 1960s in order to present a stronger case for heredity. Hearnshaw accepts that Burt was working with authentic data up to and including 1955; but he thinks it possible that some at least of the additional cases reported subsequently were based ed on "reconstruction."

However, there is no positive evidence that Burt was doing this, and possibilities do not constitute evidence. There seems to be no strong reason for thinking that Burt could not have given a satisfactory answer to the questions that have been raised, if anyone had asked him. The onus of proof for fraud is on those who make the charge. There are many gaps in the record and Burt himself must take some responsibility for these, especially those in his preliminary reports. But omissions and misleading assertions are to be found among the critics, too, as was seen.

One of the most remarkable omissions concerns Jack Tizard and Alan and Ann Clarke. All played a prominent role in supporting the public attack on Burt's integrity in 1976, when Tizard was vice-president of the British Psychological Society, and Alan Clarke was president-elect; yet neither one provided a detailed account of their evidence, commensurate with the importance of the case. The Clarkes "worked mostly privately" as they state in 1980 in "Comments on Professor Hearnshaw's Balance Sheet on Burt," published in A Balance Sheet on Burt, Supplement to the Bulletin of the British Psychological Society.

When Eysenck asked for an inquiry in 1977, the Council of the British Psychological Society refused. When Hearnshaw in 1979 concluded that Burt was guilty, the Council accepted his conclusions forthwith, making no attempt to discover what might be said in Burt's defense. That Burt was unjustly treated has been recognized by writers as diverse as F. Samelson, who wrote in 1992 in an article, "Rescuing the Reputation of Sir Cyril Burt," in the Journal of the History of the Behavioral Sciences: "Joynson and Fletcher have a valid and important point to make when they raise the issue of the fairness of Burt's treatment." As Arthur Jensen remarked: "If ever there was a kangaroo court, this was it." The precise apportionment of praise and blame in the case of Cyril Burt may well have to be left to the day of judgment, when it will provide a severe test of the infallibility of the Almighty.

Meanwhile the significance of the affair lies in what it teaches us about the social sciences in general and psychology in particular. It reminds us that, even in the most advanced areas of experimental psychology, we do not possess objective methods which are wholly uninfluenced by fallible, personal judgment. In many other areas of psychology, especially in the applied field, the role of judgment may be even more extensive and still harder to control; and hence supposedly scientific conclusions may be profoundly affected by innumerable needs and interests, not least our political and social values.

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