Oct98. Theocharis showed me these articles ten years ago. I felt very fortunate to have the opportunity to meet Hiram Caton in London thereafter. Four of the people present, Hillman, Caton, Theocharis, Catt, set up ICAF, the International Committee for Academic Freedom. Nothing came of it. Censorship remains pandemic right across science and other disciplines. In particular, all of the most important disclosures are censored. The key question to establish is whether it is getting worse, as I believe. - Ivor Catt.
Search: The official publication of the Australia and New Zealand Association for the Advancement of Science.
Vol 19 No. 5/6 Sept/Nov 1988, pp242-244
Truth Management in the Sciences
by Hiram Caton
Deprive the average man of his vital lie, and you've robbed him of happiness as well (Henrik Ibsen)
By truth management I mean deception practiced by scientists who use authoritative institutions to perpetrate a distinct type of fraud upon some public. The fraud consists in representing a specific and contingent interpretation of evidence as if it were unalloyed truth enjoying the unanimous endorsement of the relevant cadre of scientists. Truth management, then, is wanton abuse of scientific authority.
Some may be tempted to read the truth management concept as a supposed conspiracy of experts. This presents a certain difficulty in communication since we all know that conspiracies, collusions, and machinations do not exist. These sordid activities are products of the febrile imaginations of literary persons such as C. P. Snow, who opened his Godkin lectures at Harvard University by declaring that 'one of the most bizarre features of an advanced industrial society in our time is that cardinal choices have been made by a handful of men: in secret' (Snow 1961).
As a historian I do not share Lord Snow's perception of this situation as bizarre; to me it seems ordinary. Indeed, it is because collusion is so ordinary - almost, one might say, a constant of organisational dynamics - that it will open no window on the special phenomenon of truth management. It is more promising, I believe, to follow the lead of recent studies of self-deception, which suggests that this curious manoeuvre lies deep in Homo sapiens' evloved psychology, and that it has several distinct adaptive functions (Daniels 1983; Goleman 1985; Mitchell and Thompson 1986; Gruter and Masters 1986; Alexander 1987; Lochard and Paulhus 1988). In this way we may think of truth management as a 'vital lie' to borrow Ibsen's phrase, fostered in specific institutional circumstances.
To indicate that scientists are subject to gross self-deception concerning matters with which they are thoroughly familiar, let us examine the standard response to the phenomenon of fraud in science. Fraud, the fabrication or manipulation of evidence, crosses the common self-image of scientists in the most severe manner. This image pictures the scientist as a sort of saint of truth (Mahoney 1976; Kohn 1986). He or she is an impartial critic. scrupulously reports the experimental findings, carefully weight the evidence, readily acknowledges error, and openly communicates with colleagues. Unlike lesser mortals, the scientist is not motivated by the ordinary forms of avidity, but is led to the secrets of nature by the gentle hand of curiosity. As for the larger purposes of life, the scientist dedicates his or her labors to the amelioration of the human condition.
this image is promulgated through countless channels, including the heroic poetry of science idolatry. Let us sample it. The respected Oxford philosopher of science, Rom Harre, (1986), has written:
"In my view science is not just an epistemological but also a moral achievement ... the scientific community exhibits a model or ideal of rational co-operation set within a strict moral order, the whole having no parallel in any other human activity ... [it] enforces standards of honesty, trustworthiness and good work against which the moral quality of say Christian civilisation stands condemned."
I call this poetry to draw attention to the edifying tone which transports the author's imagination to a vision of moral grandeur. he thrills to the discovery of an ethic so pure that it puts the ethical performance of a world religion to shame. The poet experiences his ecsatsy illuminated by a vision of the world disenchanted by science, yet redeemed by science; for if we have lost religion, we have gained a new ethic superior to the old.
Returning to earth, I observe that this eulogy to honesty is a lie if we, unkindly, read it as the factual description it purports to be. Science, as sociologists know and philosophers of science should know, is just another profession whose organisation, social stratification, career expectations, and justifying mythology can be understood without the supposition of a moral order uniquely its own or the supposition that the pursuit of science builds character. Indeed, scientists, despite the ethic of truthfulness, may be more subject to self-deception than other professionals because reputation counts heavily towards success in status competition. Reputation lives in opinion; and often reputation for achievement substitutes for the thing. Reputation may be built up or diminished by bravado, gossip, and other dubious means. Reflecting on the capriciousness of academic status assignment, Donald Perry (1987) hit upon a thought in marked contrast to Harre's eulogy:
"Now I would like to challenge a simplistic value - that it is wrong to use unscrupulous means to advance one's career in biology.
Before you steadfastly answer yes, look closely at some role models of the profession ... why should less distinguished scientists be honest when unscrupulous behaviour is rewarded with celebrated scientific recognition? Science advances by finding answers to questions about nature. Whether or not a scientist is scrupulous has no bearing at all on scientific discoveries."
Perry's thought may be enlarged by observing that institutional science is adaptable to many values. Research may be directed toward ends trivial or sublime. It may be made to serve profit, mass annihilation, entertainment, and social control. There is no discernable moral order implicit in applications of science.
Although these observations are commonplace, the response of scientists to the fraud phenomenon invoked the image of saintly science in its most unreflective form. When the first damaging cases came to light about 15 years ago, leaders of science formulated a line that soon became orthodox (Broad and Wade 1982; Kohn 1986). The line asserts that fraud is a rare phenomenon. It is said that cheating offends the scientist's credo of complete and veracious disclosure. Those sceptical of the restraining power of conscience in the era of Watergate are assured that the credo is enforced by two strong sanctions. One is that fraud is invariably detected; the other is that disgrace is sure to follow. With fraud thus verbally confined to a minute number, it remained only to find a suitable explanation of the atypical event. The explanation proposed is that fraud is the irrational act of a disturbed mind.
The utility of the psychiatric explanation in helping to extricate scientists from tight spots may be seen in the case of Eugene Braunwald, whose laboratory at the Harvard Medical School was the scene of the most extensive fraud uncovered to date. Braunwald (1987) declared:
"I believe that many instances of scientific fraud represent a form of unconscious self-destructive behaviour which may have aggressive components directed against the perpetrator's supervisors, colleagues and institutions; indeed, it mocks science as a whole."
Braunwald did not substantiate his belief by citing clinical evidence. As a medical scientist he presumably knows that psychiatric explanations made in the absence of clinical examination are of no evidential value. Nevertheless, Braunwald's diagnosis reveals something about his own motives. Observe that he portrays himself, Harvard and science itself as victims. In this way the scientist who presided over the worst fraud uncovered hitherto deflects culpability by attributing it to a chance, uncontrollable event - the subordinate John Darsee's neurosis. This explanation directs attention away from the point at issue, Braunwald's failure adequately to supervise his laboratory.
The psychiatric explanation was snatched from thin air in the early days of the scandal. It continues to be advanced but now indirect evidence is offered. In his highly acclaimed study, False Prophets: Fraud and Error in Science and medicine, virologist Alexander Kohn cited some opinions of L.S. Kubie, a psychiatrist who specialised in scientist clients (Kohn 1986). Kubie found that his patients often suffered from unresolved neurotic anxieties which in cases involved tampering with evidence. This information, nearly three decades old when Kohn's book appeared, is his sole evidence for the neurosis hypothesis. It suggests that some scientists are driven by neurosis to cheat, but furnishes no information on whether persons until now detected in cheating were neurotic.
"[i]n practically every conversation I have had on this subject with heads of laboratories, professors and terachers, they could report attempted cases of falsification or cheating which they had exposed early enough to get rid of the offending individual and bar his access to the halls of science"
Winnowing is nevertheless not an effective safeguard according to the New Scientist survey Kohn cites. The 1976 survey found that 194 respondents (n=201) reported knowledge of cheating. One-fifth of these cases were reported as having been detected, but only 10% of offenders were punished by dismissal. He also reports a survey of 1309 scientists, of whom 25% complained of having their ideas stolen or inadequately acknowledged. One may conclude from Kohn's own data that cheating is the ordinary practice of ordinary people.
Such evidence concerning the prevalence of fraud, being largely anecdotal, is of limited value. More significant indicators perhaps are where fraud is occurring and how it occurs.
* Fraud is not being detected in institutions of low repute, but in the laboratories of eminent scientists holding appointments at prestige institutions.
* Evidence does not support the view that the detection of fraud is inevitable. Hundreds of papers reporting fabricated research have slipped through the main line of defence, peer review, despite tell-tale inconsistencies, some quite gross (Kohn 1986; Stewart and Feder 1987). Journal readers do not detect fraud either. Indeed, even the co-authors of articles reporting faked data did not detect it in the articles they signed. In the Harvard case, there were 100 publications involving 47 co-authors, yet none detected cheating (Stewart and Feder 1987). Who did? A lab technician.
Despite all this, Daniel E. Koshland, Jr, editor of Science, recently stated that 'we must recognize that 99.9999% of [scientific papers] are accurate and truthful' (Koshland 1987).
This confident assertion exemplifies the ease with which scientists fabricate data in good conscience. The impressive certainty to four decimal places handily exceeds the precision possible in social measurement. Even if this figment were of real magnitude, it could not be obtained in the present case because the data requisite for a quantitive estimate of the incidence of fraud have not been collected. Koshland's intoxicated certainty registers the will to believe in the integrity of science regardless of evidence.
If the editor of Science furnished an example of deception in the course of denying that scientists deceive, Alexander Kohn has adduced a singular case of misconduct which strongly suggests that it is pandemic. It is the case of Alexander Kohn himself.
In the Preface of the new edition of False Prophets, Kohn states that he has withdrawn a chapter on the Samosa controversy published in the first edition because Derek Freeman presented evidence that certain facts and judgements in it are incorrect.
This brief acknowledgement scarcely hints at what actually transpired. In Kohn's 1500 word account of the controversy, Freeman detected 20 errors, most of which tended to diminish Freeman's scholarship and reputation (Freeman 1987). So many errors bespeak culpable failure to observe scholarly standards. But in addition, Kohn groomed his evidence by altering a quotation to make it a substantially sharper jab at Freeman than the original had been.
Kohn stated in response to Freeman's first, exploratory letter that he intended, and believed that he wrote, an even-handed account of the Samoa controversy (Kohn 1987a). Freeman's second letter was a blistering indictment of Kohn's integrity, based on detailed demonstration of the bias of Kohn's account and on an enumeration of errors. Kohn offered no defence in response to this letter. He simply agreed to withdraw the chapter (Kohn 1987b).
Kohn's investigation of the Samoa controversy was superficial in the sense that undergraduate essays are superficial. He was unaware that his balanced account merely reproduced the line taken by Margaret Mead's defenders. The altered quotation seems damning, as Freeman showed with devastating effect. Yet when the evidence is closely considered, one is inclined to conclude that Kohn only practised the usual improvement of data, free from malicious intent (Caton 1988).
This case is singular in that it poses the question Kohn himself raises in the new concluding chapter of his book, Where does it end? If a respected virologist in a highly acclaimed book professing to expose the roots of cheating is caught cheating himself, who among the saints of truth is without sin?
The answer of course is 'none' or 'few'. Either way, the Kohn case suggests that the prevailing approach to the cheating phenomenon may be fundamentally mistaken. The prevailing approach focuses on the worst case, fraud, with glances at other forms of cheating. It declares fraud to be rare, and analyses the problem as an ethical deficit to be remedied by the application of new safeguards and renewed exhortation.
The effect of this approach is to scapegoat a few hapless individuals. Their punishment creates the impression that science is putting its house in order. This effect has already become clear in the pattern of institutional response to fraud: the low ranking postdoc who faked the data is ruined, while the eminent supervisor is merely admonished (Perry 1986, 1987; Kohn 1986); or, as seems to be the latest fashion, the supervisor is actually praised by the review board in bringing the postdoc to book (Palca 1988). This adaptive strategy will come as no surprise to Sir Fred Hoyle (1986), who states that 'fraud, provided it is directed to what is considered a worthy cause, is never seriously punished.'
These remarks have I hope furnished a critical framework for the self-images of scientists as heroes of truth. their feeling of moral excellence stems no doubt in part from the euphoria of success in the rigours of professional competition. Sportsmen and businessmen boost their self-esteem for similar reasons. The valorization of this delusion serves a multitude of public relations functions tending to support the public credibility of science. In this it is like the self-images of other professions, which function as professional conscience and define the profession's norms relative to its public. While professional norms are subjectively and sociologically significant, they must not be mistaken for actual behaviour.
(The sequel to this paper will review studies of science publishing that throw light on what actual behaviour is.)
Alexander, R.D. (1987) The Biology of Moral Systems, Hawthorne, N.Y.: Aldine.
Hiram Caton, Division of Humanities, Griffith University, Brisbane, Qld 4111.
Search: The official publication of the Australia and New Zealand Association for the Advancement of Science.
Vol 20 No. 1 Jan-Feb 1989, pp 24-26
Product Control in the Truth Industry
Hiram Caton, Division of Humanities, Griffith University, Brisbane, Qld. 4111
Uncompromising, indefatigable pursuit of truth, then, is the hallmark that distinguishes science from the charlatan. It constitutes the indispensible ethic of modern science. (Max Born)
Max Born's motto 'uncompromising, indefatigable pursuit of truth' expresses the will of an earlier phase of science in which there was a linkage of feeling between the arduous effort to clarify the mind and the political struggle for freedom and justice. That era is past. With the institutionalisation of science on a large scale, truth has triumphed. By collective fiat, the individual scientist is deemed to be among the elect; any serious deviation from the consensus, as may happen should he discover something new and profound, accordingly marks him as unsound and wayward.
Thus the young scientist who today took Born's dictum to heart would seriously handicap his career. His list of publications would be too short to warrant promotion, because he would attend to non-trivial problems, shun the rush into print, and reject honorary authorship. However deferential he might be to seniors, his independence would be noticed and make him suspect to the guardians of right thinking. Should he make a discovery that unsettles the consensus, damaging rumours would make those who formed a good opinion of him think carefully about the cost to themselves of continued loyalty. Cabals would sabotage the symposium he wanted to organise; grant panels would question the validity of the research he proposed; and peer review would purge his best ideas. If despite these penalties he refused to compromise, the ultimate sanction, ostracism, would likely be imposed.
The powerful conformist pressure in the truth industry can be read from its organisation of the mode of production. A scientist's quality is measured in the first instance by the quality of his output. Number of publications is a handy index for grant panels whose members do not have the time to read the applicant's research. This is not an arbitrary judgement. Quantity of publications means that the individual has been certified by numerous peers to be a reliable producer of approved words. It is therefore probable that he will continue to produce approvable words and will shun discoveries that force a revision of what all know is right and true.
The preference for triviality in the truth industry appears from the production statistics. There are 40000 scientific journals with an output of 2800 articles per day. This mighty deluge of truth is however apparently not consumed. Studies of readership indicate that the average scientific article has less than one reader - 0.6 to be artificially precise, based on citation counts. Half of all reading is in less than 1% of journals, indicating a steep status gradient on the pyramid of approved words (Mahoney 1987).
Authorship is also compacted. Fewer than 10% of scientists account for 50% of publications (Cole and Cole 1972; Cole 1979; Mahoney 1987). This productivity is not necessarily an indication of brilliance or quality (Lindsay 1987; Garfield 1979). It is just as likely to indicate skill in penetrating or organising Associations for the Curriculum Vitae expansion. These networks arrange what is politely called 'honorary authorship', or sometimes 'sham authorship'. Bibliographic multiplication on individual CVs is sanctioned by the convention that the slightest connection with the subject reported in an article justifies co-authorship. Leading journals do not scruple to accept 10 or more co-authors on a 2000 word article, or 25 co-authors for long articles, say 4000 words. The reward for this 'insatiable greed for CV expansion (Perry 1986) is not only the increase of assets; co-authorship greatly enhances collaborators' standing in the citation index sweepstakes. If each of 15 co-authors cite their publication in five other publications, they score 75 citations - an impressive showing. It also enables a minority of scientists to dominate publication, thanks only to their skill in manipulating the word-certifying process. Authorship in the truth industry therefore does not mean what the noramtive image of scientific integrity would have it mean, namely, that each co-author warrants the validity of the information contained in the article. The Harvard scandal, and a similar one at the University of California, revealed that co-authors might not have seen the article prior to submission for publication; or if they did, failed to read it with sufficient care to detect obvious discrepancies (Perry 1986; Stewart and Feder 1987).
The success of techniques for CV expansion is a commentary on the value of the quality control mechanism, peer review. The objective of peer review is the production of information sufficiently reliable that it may be used as building blocks for the accumulation of knowledge. But to be usable as a building block, the proffered information must fit whatever design is currently in fashion. It must, in other words, conform to expectations of how consensual information should look.
Studies of peer review have detected some of the criteria reviewers use to judge the good looks of truth. Douglas Peters and Stephen Ceci set out to test whether institutional prestige of submitting authors influenced referee judgement. They selected numbers of articles published by persons at prestige institutions and resubmitted them, slightly altered, to the same journals, disguised by fictitious names of authors and institutions. The interesting result was that all the previously published articles were rejected. The most often mentioned criticism was that the methodology was defective. Thus, the same article whose methodology was judged to be adequate when submitted from Yale was judged to be defective when submitted from North Dakota. Institutional prestige, then , was one criterion of the good looks of truth. Another criterion is positive experimental results that support a current theory. Psychologist Michael Mahoney conducted an experiment to test this hypothesis. He altered the conclusions of previously published articles from positive evaluation to inconclusive or negative evaluation. All these articles were rejected by reviewers on methodological grounds (Mahoney 1987).
These two experiments do not encourage confidence in referee reliability. Not only was the same data oppositely evaluated in the two experiments, but 92% of the editors and 87% of referees failed to detect plagiarism, even though the articles were resubmitted to the same journals within 18-36 months of publication (Peters and Ceci 1982). Admittedly, these experiments were based on very small samples. But the results are consistent with studies of referee reliability based on large samples (Cicchetti 1982). Their telling effect is indicated by the response of seniors when the results of the experiments were disclosed. Peters and Cecci were ostracised, support services were withdrawn by the department chairman, and one of them was denied tenure (later revfersed) (Mahoney 1987). The Stewart and Feder study of the Harvard scandal was held up for 3 years by threats of defamation. When it finally went into print in Nature, the editors published a disclaimer (unprecedented?), and they altered certain statements of the authors (readers were so advised).
Reviewer reliability is apparently better in the physical sciences, but not that much better. The editor of the prestigious Physical Review and Physical Review Letters states that referees score only 10-15% agreement on acceptance the first time round (Lazarus 1982). In medicine, one editor rates two-thirds of the referees reports he receives as unreliable (Horrobin 1982). 'What constantly astonishes me,' he says, 'is the intemperate language in which many reports ... are couched. The lack of sound judgement among the people who have the fate of science and the lives of others in their hands is appalling.'
Another bias factor in peer review is the editor. The editor of the American Anthropologist, H. Russell Bernard, expressed what everyone knows when he declared: 'It is really quite simple for me as editor to guarantee that an article will be killed by referees. All I need to do is to select referees I know can be trusted to clobber a particular manuscript' (Bernard 1982). bernard uses a randomised reviewer selection procedure to prevent this happening.
It might seem that a review process made porous by the chance effects of inattention, ignorance, bias, and favoritism, would be a poor tool for imposing orthodoxy. This does not appear to be the case. Editors as well as students of peer review agree that whatever else they do, referees bring to bear a strongly stereotyped set of requirements. Among them are: proper grooming (the right mix of co-authors, the right mix of citations, the best way to present data); the right sort of conclusion (one that confirms average expectations); a show of originality strictly confined within current beliefs (Mahoney 1986; Lyttleton 1979; Armstrong 1982).
Many editors have independently observed that its effect is to level the average. Their thought was voiced by medical journal editor David F. Horrobin when he said that 'the referee system as it is currently constituted is a disaster. What is most disastrous is its built-in bias against highly innovative work' (Horrobin 1982). Editor estimates are confirmed by the testimony of many creative scientists. Among them are Thomas Gold (pers. comm. 1987), who in a recent reflection on his career had this to say:
"I have had to face a large amount of opposition in virtually every case in which I have produced anything of novelty. In 1948 when we proposed the steady state theory of cosmology, Bondi, Hoyls and I found all the official astronomers extremely hostile. My theory of hearing was totally ignored and now 40 years later, when it has been found to be correct, the original paper on the subject is mostly forgotten. In the meantime someone who espoused the opposing and incorrect theory received a Nobel Prize for it."
Astrophysicist R.A. Lyttleton diagnoses the problem as a mass of bad coins driving out the good. 'Science journals today abound,' he says, ' with elaborate theories of alleged phenomena quite inadequately established other than by often intemperate asservation, and before the prime requirement of any theory has been found, namely an engine or cause of the phenomenon.' He likens scientific information exchange to a club that aggressively excludes those who do not adhere to the creed or please those whose egos require constant grooming. Of peer review he says:
"it is ... short-sighted to leave the management of the production of the end-product, which is the publication of results for general dissemination, in entirely irresponsible hands answerable to no one beyond their immediate coterie for their conduct, or in some cases hands concerned with commercial success. Unrestrained censorship goes on in all directions, but the system [of peer revue] is widely regarded as one of freedom when it is really no better than anarchic suppression to keep in countenance manifest rubbish claimed to represent scientific research.' (Lyttleton 1979)
Unrestrained censorship? Retaliation? This is beginning to sound like a Mafia theory of science. Perhaps. Sir Fred Hoyle, who has been involved in many controversies, and who resigned as director of the Institute of Theoretical Astronomy after 'certain academic maneuvering took place,' had this to say about his fellows:
"Political rivalries are small passions compared to the hatred the average solid scientist has for the heterodox, hatred that has surely not been equalled in its fury since the days of the Spanish Inquisition ... Pressures are so great towards orthodoxy that it is unwise for a young scientist to report an observation or experiment should it happen to favour a declared heresy.' (Hoyle 1986)
This assessment may be somewhat overdrawn. Halton Arp was allowed to continue in his heresy (that the red shift is not a measure of cosmological distance) for two decades before his colleagues excluded him from the Mt Wilson telescope (Arp 1987; Burbidge 1988). nevertheless, the evidence I have collected suggests that the value of knowledge for its own sake has been swamped by values attaching to power, reputation, and money. The Arp case illustrates where the priorities lie when these values come into competition; research of great theoretical significance was dismissed as valueless, and his standing was degraded. Not long ago such an incident would have occasioned an outcry. Today we prefer not to notice. We have learned that what counts is not ideas but institutional power. The growth of the sciences since 1945 has been accompanied by an enormous increase of the institutional power exercised by scientists. Truth management is the consequence.
The occurrence of truth management may be identified by the following observation. Consider some question of public moment that significantly involved science - the AIDS epidemic, for example. This disease is complex in its etiology, transmission, and effects on public health. Many uncertainties have surrounded it from the beginning and continue to do so. Devising a strategy to protect public health involves the weighted estimate of unknowns and a host of value judgements that assign fiscal, legal, social, and health priorities. Imperfect knowledge together with the latitude of choice implies a variety of policy responses, and the logical contingency of them all.
Given these initial conditions, the expectation of reasonable presponse is that scientists and public health authorities would present governments a variety of policy options. We might also expect the experts to conduct an on-going airing of differences about the scientific facts and about public choices. Yet this is not what we observe in the American AIDS policy. Scientists and health officials present a united voice for a single policy option, which they vigorously advocate as the only rational and humane policy (Institute of Medicine 1986). This was done with such energy that public debate between experts never occurred.
An important effect of this process is the pre-emption of public choice by experts, although in a democracy that choice is supposed to lie with elected officials. Politicians have not particularly resisted the pre-emption and in some cases have abetted it. The reason is that the political process cannot cope with the deep divisions in modern society on a number of questions. Politicians have been happy to transfer the power of decision and policy enforcement to bureaucratic authorities and courts, which are not accountable to the public.
That in these circumstances the truth conveyed to the public is likely to be heavily managed may be read from the organisational configuration. Characteristically, research, policy formulation, and policy implementation are amalgamated under central control, usually operating from a government agency. This configuration subordinates research and policy advice to the exigencies [of] policy implementation. The reason is this. A prime requirement for policy managers is certainty, especially in dealing with issues as complex and anxiety-ridden as atomic energy, exotic weapons systems, or AIDS. It is deemed to be vital that the public be indoctrinated in a single point of view and that all others be branded with epithets that intimidate and marginalise opponents. Practically, it comes down to good guys and bad guys, leaving no grey areas that critics might use to assault the citadel.
Are there remedies? It might be proposed to make it a formal requirement that alternative scientific and policy models be developed and vigorously argues in documents available to the public. Governments aren't likely to embrace this idea, for reasons already mentioned. Even if one did, the minority view, as it would soon come to be known, would be easily tamed by bureaucratic power, as happened with Freedom of Information acts and ombudsmen.
Remedies, if we are to have them, will need to be applied where the deficiency essentially lies - with the individual. This is a long march but in the end the only one likely to be of enduring value. Some steps have already been taken. Hiroshima registered with atomic scientists that they have responsibility for the consequences of their research. The environmental movement considerably extended and legitimated the sense of science citizenship. Perhaps it is not idle to hope that the sting of fraud will goad scientists to restore knowledge for its own sake to first place in their lersonal table of values.
After completing this script, I learned that the Harvard Medical School has promulgated guidelines intended to prevent recurrence of the misconduct that came to light in the Darsee case. They include criteria for assignment of authorship, proposals for the supervision of laboratory personnel, suggestions regarding the preservation of experimental data, and limitation on the number of publications reviewed for faculty appointment or promotion (Angell and Relman 1988). The National Institutes of Health and the Association of American Medical Colleges are also developing quidelines. These are encouraging signs. That they come 7 years after Darsee shows that the wheels of reform turn slowly and that vigilance must not be relaxed.
Angell, M., and Relman, A.S. (1988) Fraud in Biomedical Research, N. Engl. J. Med. 318, 1462-1463.
Armstrong, J. Scott. (1982) Barriers to scientific contributions: the author's formula, Behavioural and Brain Sciences 5: 197
Arp, Halton. (1987) Quasars, redshifts, and controversies, Berkeley: Interstellar Media.
Bernard, H. Russell, (1982) "Computer-assisted referee selection as a means of reducing potential editorial bias," Behavioural and Brain Sciences 5: 202.
Burbidge, Geoffrey. (1988) Review of Quasars, redshifts, and controversies, Sky and Telescope, January.
Cicchetti, Domenic V. (1982) On peer review: 'We have met the enemy and he is us'. Behavioural and Brain Sciences 5: 205.
Ivor Catt's lecture to the Ethical Society, London.