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
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
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
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
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
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
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
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
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
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
Alexander, R.D. (1987) The Biology of
Moral Systems, Hawthorne, N.Y.: Aldine.
Division of Humanities, Griffith University, Brisbane, Qld
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
Control in the Truth Industry
Division of Humanities, Griffith University, Brisbane, Qld.
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)
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
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
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
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
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
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,
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:
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,
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.