Zombie Science - dead but won't lie down

Editorial - Bruce G. Charlton

Zombie science: A sinister consequence of evaluating scientific theories purely on the basis of enlightened self-interest. Medical Hypotheses. 2008; Volume 71: 327-329

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Summary

Although the classical ideal is that scientific theories are evaluated by a careful teasing-out of their internal logic and external implications, and checking whether these deductions and predictions are in-line-with old and new observations; the fact that so many vague, dumb or incoherent scientific theories are apparently believed by so many scientists for so many years is suggestive that this ideal does not necessarily reflect real world practice. In the real world it looks more like most scientists are quite willing to pursue wrong ideas for so long as they are rewarded with a better chance of achieving more grants, publications and status. The classic account has it that bogus theories should readily be demolished by sceptical (or jealous) competitor scientists. However, in practice even the most conclusive ‘hatchet jobs’ may fail to kill, or even weaken, phoney hypotheses when they are backed-up with sufficient economic muscle in the form of lavish and sustained funding. And when a branch of science based on phoney theories serves a useful but non-scientific purpose, it may be kept-going indefinitely by continuous transfusions of cash from those whose interests it serves. If this happens, real science expires and a ‘zombie science’ evolves. Zombie science is science that is dead but will not lie down. It keeps twitching and lumbering around so that (from a distance, and with your eyes half-closed) zombie science looks much like the real thing. But in fact the zombie has no life of its own; it is animated and moved only by the incessant pumping of funds. If zombie science is not scientifically-useable – what is its function? In a nutshell, zombie science is supported because it is useful propaganda to be deployed in arenas such as political rhetoric, public administration, management, public relations, marketing and the mass media generally. It persuades, it constructs taboos, it buttresses some kind of rhetorical attempt to shape mass opinion. Indeed, zombie science often comes across in the mass media as being more plausible than real science; and it is precisely the superficial face-plausibility which is the sole and sufficient purpose of zombie science.

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How do scientists decide whether a theory is ‘valid’?

In contrast to the ideal of impartial and objective analysis, in the real world it looks more like most scientists are quite willing to pursue wrong ideas – so long as they are rewarded for doing so with a better chance of achieving more grants, publications and status.

Thus is ‘enlightened self-interest’ a powerful factor in scientific evaluation. ‘Self-interest’ because the primary criterion of the ‘validity’ of a theory is whether or not acting-upon-it will benefit the career of the individual scientist; ‘enlightened’ because the canny career scientist will be looking ahead a few years in order to prefer that theory which offers the best prospect of netting the next grant, tenure, promotion or prestigious job opportunity.

When a new theory is launched upon the population of scientists, it is unlikely to win converts unless the early-adopters are rewarded in a fairly obvious fashion – usually with a greater chance of generous research funding, the opportunity to publish in prestigious journals (plus a raft of new second-string specialist journals – to provide a home for the more modest and less-important papers), and the hope of increased status exemplified by interest, admiration and respect from other scientists.

How do bogus theories survive?

While it is simply human nature to respond to immediate incentives, this phenomenon does imply that theories may become popular or even dominant purely because of their association with immediate incentives – and despite their scientific weaknesses.

In terms of the classical theory of science; bogus theories should be readily demolished by sceptical (or jealous) competitor scientists, who will denounce the weaknesses of merely-fashionable theories in conferences and in print. However, in practice it seems that even the most conclusive ‘hatchet jobs’ done on phoney theories will fail to kill, or even weaken, them when the phoney theories are backed-up with sufficient economic muscle in the form of funding. Scientists will – at the margin – gravitate to where the money is; and the paraphernalia of specialist conferences (to present results at) journals (to publish in) and academic jobs (to work in) will follow as day follows night; so long as the funding stream is sufficiently deep and sustained.

Classical theory has it that a bogus hypothesis will be rejected when it fails to predict ‘reality’ as determined by controlled observations and experiments. But such a catastrophe can be deferred almost indefinitely by the elaboration of secondary hypotheses to explain why not fitting the facts is not – after all – fatal to the theory; but instead merely implies the need for a more complex theory – which then requires further testing (and generates more work for the bogus believers).

Furthermore, since the new version of the bogus theory, with its many auxiliary secondary hypotheses, is so complex – this complexity makes it that much harder to test: further putting-off the time when the bogus theory needs to be abandoned.

(Meanwhile, a much simpler rival theory – i.e. that the first theory is phoney, and always was phoney, and this is why it so singularly fails to predict reality – is regarded as simplistic, crass, merely a sign of lack of sophistication …)

And anyway, there are massive ‘sunk costs’ associated with the phoney theory including the reputations of numerous scientists who are now successful and powerful on the back of the phoney theory, and who by-now control the peer review process (including allocation of grants, publications and jobs) so there is a powerful disincentive against upsetting the apple cart.

False theories, theories which never did have anything in their favour except careerism, can therefore prove very long-lived. However, they are probably not immortal. Eventually, the branch of science which is underpinned by a bogus hypotheses will be evaluated as a whole.

People will ask: what is the good of all this activity, effort and expense? And the answer will be – no good at all. An area of science underpinned by a bogus theory is really only a species of job-creation or make-work. Perhaps there will be some by-products – for example the development of new methods and technologies. But since these are an accidental spin-off, they do not serve to justify the field as a whole. And the plug may be pulled – so a whole branch of science goes down the drain.

The zombification of science

On the other hand, when a branch of science based on phoney theories is serving a useful but non-scientific purpose it may be kept-going by continuous transfusions of cash from those whose interests it serves.

For example, if a branch of pseudo-science based on a phoney theory is nonetheless valuable for political purposes (e.g. to justify government policies) or for marketing purposes (to provide a rationale for sales) then real science expires and a ‘zombie science’ evolves.

Zombie science is science that is dead but will not lie down. It keeps twitching and lumbering around so that (from a distance, and with your eyes half-closed) zombie science looks much like real science. But in fact the zombie has no life of its own; it is animated and moved only by the incessant pumping of funds.

Proper science finds its use, and gets its validation, from being deployed in technology. So proper medical science is underpinned by the effectiveness of medical treatments based upon its theories and results; proper physics is underpinned by successful engineering – and so on. But the findings of zombie science do not have value for technology because any technology built using bogus theories would likely not work in the first place; and if it did happen to survive construction then would soon fall from the sky, collapse, or otherwise crash and burn.

(Of course, such technical disasters can sometimes themselves be explained-away – and thereby covered-up – by yet further phoney theoretical elaborations, especially when there is monopolistic control of information. However, so long as there are rival competing technologies being chosen by those who use them and depend on them, the inferiority of technologies based on bogus science is usually apparent.)

So, zombie science is not useable by applied science. What, then, is its function? In a nutshell, zombie science is supported because it is useful propaganda. Zombie science is deployed in arenas such as political rhetoric, public administration, management, public relations, marketing and the mass media generally. It persuades, it constructs taboos, it buttresses some kind of rhetorical attempt to shape mass opinion.

Indeed, zombie science often comes across in the mass media as being more plausible than real science; and it is precisely the superficial face-plausibility which in actuality is the sole and sufficient purpose of zombie science.

Can zombie science be killed?

Zombie science can be seen as the ultimate consequence of the practice of scientists evaluating theories in terms of their propensity to enhance scientific careers in the short- to medium-term – when this propensity is unconstrained by the imperative to use science in applied technology. Immediate personal careerist benefits seem easily able to overwhelm the more theoretical and abstract scientific benefits of trying to establish and adhere to the ‘real world’ truth.

What does this mean and what can be done about it? For one thing it suggests that the process by which science moves towards the truth may be much slower and coarser than it apparently used to be. In current science, there seems to be a greater possibility that large scale change may be fashion rather than progress, and such change may be serving propagandistic goals rather than advancing scientific understanding.

The emergent slowness in self-correction may perhaps be a consequence of the greatly increased size of the scientific enterprise as it has grown over recent decades – science now has a great deal of inertia. Science in the past was fast, light and nimble; and as easily redirected as a fleeing antelope. By comparison modern science may have a lumbering pace, but its vast bulk means that once it has begun moving in a particular direction, trying to deflect its path is like stopping a charging rhinoceros.

Any realistic prospect of reversing the expansion of zombie science would seem to involve greater competition among the suppliers of research grants. Where science funders are few, it is easier for a bogus theory to survive uncontested – whereas in situations where there are many potential sources of funding there is likely to be some competition among funders to debunk and replace bogus theories supported by rival grant givers.

(This model assumes that grant-awarders are engaged in some kind of competition to become the agency that supports the best, most revolutionary and most technologically useful scientific research – however, it is uncertain whether funders do in fact operate in this way. Certainly it would be desirable if grant agencies did compete to fund the best science and scientists – but perhaps funders cooperate, coordinate and collude, and therefore should instead be regarded as a cartel.)

In a world of competition among science funders, a particular research foundation (so long as it was sufficiently large and influential) could use its resources to help build-up a rival new theory to challenge, then supplant, an old and scientifically unsuccessful (because phoney) theory. By backing a winner and thereby triggering a scientific revolution, a competitive research foundation could expect to grow in fame and influence.

The natural desire of one scientist to thrive, even at the expense of another scientist’s reputation and livelihood, would in this instance be additionally fuelled by the incentive of new sources of research support.

The resulting combination of individual ambition and acquisitiveness should ensure a sufficient supply of would-be debunkers to keep the gardens of science weeded of bogus theories, and to banish the zombies of science to the graveyards where they belong.

Mavericks versus team players

Mavericks versus team players: The trade-off between shared glory and making a personal contribution

Bruce G. Charlton

Medical Hypotheses. 2008; 71: 165-167.

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Summary

The modern world is characterized by progressive specialization of function and ever-larger-scale coordination of these ever-more-specialized functions. More and more of science is done by increasing-sized teams of specialists, and the ability to engage in ‘teamwork’ is regarded as an almost essential attribute for most scientists. But teamwork does not suit all personality types. Some ‘maverick’ individuals would rather have personal credit for a relatively modest scientific contribution which they achieved (mostly) by themselves, than a share of credit in a much larger scientific contribution generated by a large team. The present system of medical science is organized to discourage mavericks and, on the whole, this is probably justifiable on the basis that scientists are not natural team players. Extra inducements are necessary to get people to adopt the relatively self-effacing behaviours necessary for building the large organizations of complementary specialists that are necessary for tackling many of the most intractable modern scientific problems. However, an ethos of teamwork does carry substantial disadvantages. Although most scientists are dispensable, and do not make a significant personal contribution, the very best scientists do make a difference to the rate of progress of science. And top notch scientists are wasted as team players. The very best scientists can function only as mavericks because they are doing science for vocational reasons. The highest intensity of personal commitment requires individual rewards from distinctive contributions. In conclusion, the current incentive system that encourages teamwork involves a trade-off. The majority of modestly talented scientists can probably achieve more when working as members of a team. But the very best scientists probably need to work as mavericks.

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Science, like most aspects of the modern world, is characterized by progressive specialization of function and ever-larger-scale coordination of these ever-more-specialized functions.

This applies to scientific careers also. More and more of science is done by increasing-sized teams of specialists, and the ability to engage in ‘teamwork’ is regarded as an almost essential attribute for most scientists.

So far, so good. But one consequence of teamwork may be a reduced sense of personal satisfaction for the individual scientist. The direction of research is often dictated by the availability of grants, specific work content and patterns may be scheduled by the needs of the team, interpretation may be a group affair, and publication a compromise between multiple authors (not to mention the potential for further distortion by referees and editors). And the glory from any resulting scientific attainments will also be shared.

This situation resembles that which Karl Marx termed ‘alienation’; in which the ‘worker’ is separated from the product, and where the need to perform as a cog in a complex machine of production strips ‘labour’ of its intrinsic satisfactions.

Of course, for many people there are other sources of satisfaction from scientific work such as (perhaps most importantly) wages, a relatively great degree of discretion in organizing work, the social life of the laboratory, and the satisfactions of a job well done. Nonetheless for some people this is not enough. Those who were drawn into science by a sense of vocation may feel that the life of a typical modern scientist fails to satisfy their yearning to make a personal contribution.

Teamwork is, more-or-less, the mainstream mode of modern medical science; but it does not suit all personality types. Not everyone is a ‘team player’ and there are some ‘maverick’ individuals who would (perhaps selfishly) rather have personal credit for a relatively modest scientific contribution which they achieved (mostly) by themselves, than a share of credit in a much larger scientific contribution generated by a large team.

In general, it could be predicted that working as a maverick increases an individual’s potential maximum contribution to science (by generating greater personal motivation); but working as a team player is on avearage more efficient overall.

There is not much doubt that the present system of medical science is organized to discourage mavericks. On the whole, this is probably justifiable on the basis that scientists (and human beings in general) are not naturally team players, so that extra inducements are necessary to get people to adopt the relatively self-effacing behaviours necessary in building the large organizations of complementary specialists that are necessary for tackling many of the most intractable modern scientific problems. However, an ethos of teamwork does carry substantial disadvantages.

The most important way that team players are rewarded over mavericks is the practice of multiple counting. This works at every level in the scientific process.

For instance, everyone associated with a successful grant award typically states the full amount of the grant to their own credit (and not, for example, the amount of the grant divided by all the other grant holders). An unspecified share of a high-profile multi-centre ten million dollar grant (running over several years) sounds very impressive – and this credit is to some extent accrued by all the team players. By contrast, the lone maverick might have attained a much less-impressive-sounding annual grant of one hundred thousand dollars.

However, using another mode of calculation, a maverick’s 100K dollars per year might equal or exceed each team players individual share of a highly publicized lump-sum of ten million pounds, when the money is spread over several institutions and several years. Furthermore, the maverick has control of who is appointed to jobs, and the specific work they do – while a team player may find that these decisions are made by committees over which s/he has little influence.

Credit for publications is another system that rewards team players above mavericks. In round numbers it seems likely that the average production of scientific papers per author has been about one per year for many decades – but the average number of publications credited to each scientist has increased due to larger numbers of authors on each publication.

This implies that a maverick author who publishes two or three single-author papers per year is probably high-performing; yet this productivity can (apparently) be swamped by a large team players who may (with the same, or less, amount of work) have a share in maybe a dozen publications per year – with perhaps one as first author. After a few years the team player may have accumulated a hundred-plus publications while even a gifted maverick may still number just a dozen or so single-author publications.

A further aspect of grant-getting and publication relates to the statistics of small numbers. An individual scientist working (mostly) alone and averaging (say) a grant every two to four years and two or three papers per years would expect – by sheer chance – to have some ‘lean years’: gaps of several years with no grants, and several years with no publications. If a promotion or job application happens to fall during one of these randomly occurring lean years it might-well look bad; as if the maverick had burned-out and become unproductive.

By contrast, an similarly productive team player who worked as part of a ten-plus person team (of similarly productive people) would have these extreme fluctuations in productivity averaged-out, and would not be expected to suffer any lean years without grants or publications. When the time comes for applying for jobs or promotions, the team player can be assured of a decent recent CV.

Does it matter that the current mode of medical science encourages team players at the expense of mavericks? Mostly not, because the harsh truth is that most scientists are dispensable, and most do not make a significant personal contribution. However, the very best scientists do make a difference to the rate of progress of science. And top notch scientists are wasted as team players.

My guess is that the very best scientists can function only as mavericks; in charge of their own activities, or else as collaborators working on a scientific problem with just one other equal partner. The reason is that great scientists are doing science for vocational reasons; and the highest intensity of personal commitment absolutely needs individual rewards from distinctive contributions.

If correct, this means that we need to recognize the downside of current incentives that encourage teamwork in modern medical science. There is a trade-off. Modestly talented people can probably achieve more when working as members of a team. But the kind of intensely vocational motivation necessary for the highest level of scientific work is not an attribute of team players. To have a chance of achieving their greatest potential, the most-talented scientists need to work as mavericks.

False, trivial, obvious - new theories

False, trivial, obvious: Why new and revolutionary theories are typically disrespected

Bruce G. Charlton,

Medical Hypotheses 2008; 71: 1-3

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Summary

An old joke about the response to revolutionary new scientific theories states that there are three phases on the road to acceptance: 1. The theory is not true; 2. The theory is true, but it is unimportant; 3. The theory is true, and it is important – but we knew it all along. The point of this joke is that (according to scientific theorists) new theories are never properly appreciated. The ‘false’ phase happens because a defining feature of a revolutionary theory is that it contradicts the assumptions of already-existing mainstream theory. The second ‘trivial’ phase follows from a preliminary analysis which suggests that the new idea is not in fact contradicted by the major existing evidence, but the new theory seems unimportant because its implications do not seem to lead anywhere interesting when explored in the light of current theory. A stronger version of this second phase happens when the implications of a theory are regarded as not merely unimportant but actually dangerous, because a scientific revolution is certainly destructive (especially of established reputations) yet its potential benefits are conjectural. However, once a new and revolutionary theory is in place, its importance is ‘obvious’ such that it becomes hard to imagine how anybody could ever have believed anything else. Theory for scientists is like water for fish: the invisible medium in which they swim. Observations and experiments, on the other hand, are like toys in the fish tank. New toys are attention-grabbing; but when the tank gets cloudy, its water needs changing.

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Like water for fish

One of the most annoying experiences for those advocating revolutionary new theories occurs when their ideas are prematurely or erroneously rejected. Perhaps even more annoying is when a theory is adopted but its originator is not credited with the discovery.

This is embodied in the cynical description of the acceptance of revolutionary new scientific theories as having three stages in which the idea is first rejected as false, then dismissed as trivial, and finally accepted as obvious.

The three phases of response to a new theory on the road to its acceptance are

1. The theory is not true.

2. The theory is true, but it is unimportant.

3. The theory is true, and it is important – but we knew it all along.

The point of this joke is that (according to scientific theorists) new theories are never properly appreciated.

There is a superficial, but correct and important, level of critique in which premature or incorrect rejection of new theories is often a consequence of either the lack of sufficient attention being paid to the new theory, so that the critic never considers the new theory with sufficient care; or the sheer ignorance or incompetence of the critic such that – even if critics do pay sufficient attention – they are simply unable to comprehend the new theory due to knowledge deficiencies or a lack of brain-power.

Quantitatively, therefore, even when it is not ignored, a new idea tends get buried beneath shallow and dumb criticisms.

1. False: the theory is not true

At a deeper level, however, the ‘false, trivial, obvious’ joke implies that the reason theories are seldom appreciated is related to the primacy of theory in science.

Theories come before facts, since facts only get their ‘factual’ status from the theory in which they are embedded; such that science can most simply be conceptualized as a process of generating and testing theories against observations.

The defining feature of a revolutionary theory is precisely that it seeks to replace the assumptions of an already-existing theory – so a new theory cannot be evaluated on the basis of the assumptions of the old theory. This is why a new and revolutionary theory will almost invariably strike people as false.

In a sense, a new theory is perceived by an old theory as if the new theory were an observation. When a new theory is revolutionary, then it is perceived as an observation which is incompatible with the old theory. From this perspective either the new theory must be rejected, or else the old theory abandoned.

2. Trivial: the theory is true, but it is unimportant

The second phase is dismissing a revolutionary idea as ‘trivial’. This follows from a preliminary analysis which suggests that the new idea is not, after all, contradicted by the major existing evidence – so the new theory cannot simply be rejected as ‘false’.

However, although it may be true, the new theory seems unimportant; because its implications do not seem to lead anywhere interesting from the perspective of current theory.

A new theory may, therefore, seem trivial because it is trivial in the context of the old theory. Only from the perspective of the new theory itself can its importance be recognized.

In this sense, a theory must be ‘accepted’ (at least provisionally) before its importance can be appreciated.

2. (a) Trivial: the theory is true, and it is important, but dangerous

A stronger version of this second ‘trivial’ phase happens when the implications of a theory are regarded not merely as unimportant but actually dangerous.

It is never possible absolutely to exclude in advance the possibility of some catastrophe from a wide range of potential disasters. Nor is it possible to prove that the adoption of a new theory will almost certainly provide greater overall and general benefit compared with the old theory.

New theories often seem dangerous because their destructive effect is proximate and certain, while their potential to serve as a basis for future progress is distal and unpredictable.

In fact, the most compelling ‘danger’ of a new revolutionary theory is the real and present harm its acceptance would inflict on the power, wealth or prestige of adherents to the already-existing theory.

3. Obvious: the theory is true, and it is important – but we knew it all along

However, for reasons good or bad, and against these odds, some revolutionary theories do become adopted and displace the theories that went before.

Once a new theory is in place, its explanatory and predictive power is evident, its importance is ‘obvious’ (since the new theory now forms the framework for scientific investigation and communication), and indeed it becomes hard to imagine how anybody could ever (rationally) have believed anything else.

After a successful scientific revolution it seems (it ‘feels like’) everyone had always known that the new theory was true; because looking-back it is clear that the new theory makes sense-of, is explanatory-of, all observations of current-significance that went before.

Precursors and partial expressions of the new theory apparently abound, and it can become hard to recognize or acknowledge that past (‘pre-revolution’) scientists were operating on the basis of quite different over-arching theories.

Forgotten are the vast difficulties a new theory originally overcame in getting attention, refuting shallow and dumb criticisms, and demonstrating its validity and importance – so the achievement of the originating theorist may seem slight (and this is assuming the discoverer has not by this time been overlooked, forgotten, or robbed of credit by a more powerful colleague).

The path to fame as a theorist surely is long, winding and replete with pitfalls.

Like water for fish

So – theory for scientists is like water for fish: the invisible medium in which they swim. Observations and experiments, on the other hand, are like toys in the fish tank.

New toys are attention-grabbing; but when the tank gets cloudy, its water needs changing.

The James Watson Affair

Editorial

First a hero of science and now a martyr to science: The James Watson Affair – Political correctness crushes free scientific communication

Medical Hypotheses. Volume 70, Issue 6, 2008, Pages 1077-1080

Bruce G. Charlton, Editor-in-Chief – Medical Hypotheses

Available online 16 April 2008.

Summary

In 2007 James D. Watson, perhaps the most famous living scientist, was forced to retire from his position and retreat from public life in the face of international mass media condemnation following remarks concerning genetically-caused racial differences in intelligence. Watson was punished for stating forthright views on topics that elite opinion has determined should be discussed only with elaborate caution, frequent disclaimers, and solemn deference to the currently-prevailing pieties. James Watson has always struck many people as brash; however this blunt, truth-telling quality was intrinsic to his role in one of the greatest scientific discoveries. Much more importantly than ‘good manners’, Watson has consistently exemplified the cardinal scientific virtue: he speaks what he understands to be the truth without regard for the opinion of others. The most chilling aspect of the Watson Affair was the way in which so many influential members of the scientific research community joined the media condemnation directed against Watson. Perhaps the most egregious betrayal of science was an article by editorialists of the premier UK scientific journal Nature. Instead of defending the freedom of discourse in pursuit of scientific truth, Nature instead blamed Watson for being ‘crass’ and lacking ‘sensitivity’ in discussing human genetic differences. But if asked to choose between the ‘sensitive’ editors of Nature or the ‘crass’ genius of James D. Watson, all serious scientists must take the side of Watson. Because when a premier researcher such as Watson is hounded from office by a vicious, arbitrary and untruthful mob; all lesser scientists are made vulnerable to analogous treatment at the whim of the media. A zealous and coercive brand of ‘political correctness’ is now making the biological truth of human genetic differences intolerably difficult to discover and discuss in US and UK. This needs to change. My hope is that truth will prevail over political correctness and James Watson will not just be exonerated but vindicated as an exemplar of the true morality of science: that scientific communication needs to be allowed to be clear, direct – even crass – in the pursuit of truth. James Watson has been a hero of science for the achievements of his career, and also a martyr for science at the end of his career.

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In 2007 James D. Watson, perhaps the most famous living scientist, was forced to retire from his position as Chair of Cold Spring Harbor Laboratory and to retreat from public life in the face of international mass media condemnation following some remarks he made concerning genetically-caused racial differences in intelligence [1].

The substance of Watson’s remark was the speculation that the low average IQ of sub-Saharan Africans may be a contributory cause for slow economic development [1] and [2].

The Watson Affair is, so far, the most shocking example of coercive ‘political correctness’ imposed by the US and UK ‘mandarin’ intellectual class (i.e. the cultural elite who run public administration, education and the media). In other words, Watson was pilloried and punished for stating forthright views on topics (which include sexual, class and racial differences) that elite opinion has determined should be discussed only with elaborate caution, frequent disclaimers, and solemn deference to the currently-prevailing pieties.
Watson’s ‘brash’ personal style has also been his scientific strength

But ‘nuance’ has never been Watson’s style. Watson has always struck many people as disturbingly bold, direct, and brash [3], [4] and [5]. Not to put too fine a point on it, Watson has apparently often been rude and harsh in his personal relationships, and terse to the point of being elliptical or ambiguous in his pronouncements – seeming especially so to the vast majority of people whose intellectual powers are nowhere near a match for Watson’s, or who do not pick-up on his unusual sense of humor.

However, in the conduct of science, there are many things which are much more important than good manners, and many of the greatest scientists have been difficult characters [6]. But James Watson displays – in extreme and stark form – the cardinal scientific virtue: he speaks what he understands to be the truth, and does so without regard for the opinion of others [3] and [7].

And of course this blunt, truth-telling quality was absolutely intrinsic to his role in one of the greatest scientific discoveries – establishing the structure of DNA in 1953 [3] and [4]. And Watson’s directness/brashness was essential to other great career achievements including his role in establishing the science of molecular biology from a base in Harvard, in fund-raising and building-up the Cold Spring Harbor Laboratory, and in launching the human genome project [5].

Indeed the world has abundant cause to be grateful for James Watson’s brash personal style since this was inherent in his achievement, and few individuals have contributed more to human well-being.

Nature’s editorialists betray science

While it is perfectly understandable that non-scientific zealots of political correctness (as well as those who have been hurt or offended by Watson’s brashness in the past) would be delighted at the opportunity to destroy James Watson’s career and reputation – the most chilling aspect of the Watson Affair was the way in which so many powerful and influential members of the scientific research community joined the howling mob of media condemnation directed against Watson [1].

Perhaps the most egregious example was the article by editorialists of the premier UK scientific journal Nature – that same journal where Crick and Watson published the original paper describing structure of DNA [8].

Instead of publishing a clear and uncompromising defence of the freedom of untrammelled discourse in pursuit of the scientific truth; in an editorial entitled ‘Watson’s folly’ Nature instead chose to support political correctness as being more important than science.

In the context of just 500 words, the anonymous Nature authors spent most of the space attacking Watson’s interpersonal style, with a veritable diatribe of outrage. The editorial included such comments as: ‘his notorious propensity for making outrageous statements’, ‘a track record of making distasteful remarks’, ‘on many previous occasions voiced unpalatable views tinged with racism and sexism’, ‘his views have finally been deemed beyond the pale’, ‘demonstrates a sheer unacceptable offensiveness’, ‘unpleasant […] utterances’, and ‘crass comments’.

In a brief respite from attacking Watson’s personality, the Nature editorialists make two factually incorrect statements. Firstly they wrongly state that ‘Watson has apologized and retracted’ his ‘outburst’. Secondly they state that Watson ‘acknowledged that there is no evidence for what he claimed about racial differences in intelligence’. This is doubly false in that Watson never made such retractions or acknowledgments [9], and for the very good reason that any such retraction or acknowledgement would be untrue.

Indeed, the opposite is more nearly true, as Jason Malloy describes in the current issue of Medical Hypotheses [1]. There is no evidence that all human races have identical intelligence despite many generations of genetic separation and with widely different selection pressures, and on good theoretical grounds it is extremely unlikely. On the contrary, there is a very large and robust literature documenting significant racial and ethnic differences in average IQ [1]. But the Nature editorialists did not even attempt to argue the falsity of this large evidential database – instead, they simply denied its existence.

‘Sensitivity’ versus truth-telling

What the Nature editorialists advocate is described in the subtitle: ‘Debate about scientific issues needs to be forthright but not crass’. It is Watson’s ‘crassness’ that Nature seems to hate more than anything else.

This is later amplified in remarks about the investigation of racial differences which is described as a ‘sensitive task’; “‘race” is an emotive and unscientific word’ – according to Nature; and so is the investigation of the ‘equally sensitive genetics of ‘desirable’ traits’.

It is clear that Nature sees the crucial issue of the Watson Affair as one of crassness versus sensitivity. It is the ‘sensitive’ people (such as the Nature editorialists – i.e., the people who have ‘deemed’ Watson’s views ‘beyond the pale’) who stand as a bulwark against a ‘crass’ individual whose ‘outbursts’ are ‘lending succour and comfort to racists around the globe’, and whose behaviour will ‘undermine our very ability to debate such issues’.

In other words, Nature states that genetic differences can only be studied and discussed within a framework of political correctness as defined by the cultural mandarins of the US and UK, or else such matters had better not be studied or discussed at all.

If scientists are now being asked to choose between being sensitive or crass – between picking sides with either the anonymous editors of Nature or the ‘crass’ genius of James D. Watson – then it should be no contest: serious scientists must take the side of Watson.

But if Nature’s editorial comments are an index of elite intellectual opinion in the Anglosphere – which sadly seems to be the case – then this is evidence of an anti-scientific ‘fifth column’ of coercive, dishonest and vindictive political correctness which has infiltrated into the very heart of high-level scientific discourse.

The real ‘Science Wars’ of our time

When asking who it really is that is most likely to ‘undermine the ability to debate race and sex differences’, it seems clear that the US and UK zealots of coercive political correctness are the ones causing the problems, not people like Watson who are trying to move the science of human genetics forward as fast as possible.

When a premier league researcher such as Watson is hounded by elite commentators in such a vicious, arbitrary and untruthful fashion, then any and all scientists are potentially vulnerable to similar treatment at the whim of the mass media if – for whatever reason – they happen to step over a line defining the boundary of sufficiently ‘sensitive’ discourse. And any single such step over the sensitivity-line into ‘crassness’ is enough to undo a lifetime of stratospheric attainment.

This, then, is the real ‘science war’ of our era: a war of the ‘sensitive’ versus the ‘crass’ – in other words, the escalating conflict by which coercive political correctness in the UK and USA increasingly-successfully intimidates and controls scientific communication.

Biology is poised on the brink of extraordinary insights into the genetic determinants of human differences [10]; including sexual, class and racial differences. In order to make progress on all fronts (whether scientific, medical or social), we need to know the facts about humanity and genetics. But political correctness is making this truth harder to discover and discuss: almost impossibly hard in the US and the UK where scientists are at constant risk of being ‘denounced’ and demonized at the caprice of the mass media in collaboration with the cultural elite. This needs to change.

If UK and US mandarins are too squeamish even to mention or discuss research into the most exciting areas of human genetics in a clear and honest fashion, perhaps they should stand aside and allow other nations – for example from East Asia – to get-on with this vital work without harassment. If the anonymous Nature editorialists are too ‘sensitive’ to hear the truth about genetics from ‘crass’ individuals such as James D. Watson, then they should perhaps make way for those who are more emotionally-robust.

The scientific necessity for a major journal such as Nature is not merely to allow discussion of human genetic differences under sufferance and hedged-about with complex linguistic constraints; but actually to encourage straightforward and forceful scientific communication on human genetic differences without the slightest regard to notions of political correctness. Nature should be fighting political correctness on behalf of science, not joining a vigilante gang of self-appointed moral guardians who are crushing forthright scientific discourse under the banner of ‘sensitivity’.

From hero to martyr

James Watson has – for more than 60 years – been an exemplar of the essential morality of science; advocating by his words and displaying in his deeds the necessary freedom that scientific communication must be allowed to be clear, direct – even crass – in the pursuit of truth.

I believe that science is the most powerful cognitive system yet discovered by humanity [6] and [7], so that eventually truth will prevail and James Watson will be not just exonerated but vindicated. My hope is that soon there will be general recognition among scientists that James Watson was not just a hero of science for the achievements of his career, but also a martyr for science at the end of his career.
References

[1] J. Malloy, James Watson tells the inconvenient truth: faces the consequences, Med Hypotheses 70 (2008), pp. 1081–1091.

[2] Milmo C. Fury at DNA pioneer’s theory: africans are less intelligent than Westerners. The Independent, ; Published 17 October 2007 [accessed 10.03.08].

[3] Watson JD. In: Gunther S. Stent, editor (critical edition). The double helix; a personal account of the discovery of the structure of DNA. London, UK: Weidenfeld and Nicolson; 1981.

[4] H.F. Judson, The eighth day of creation: makers of the revolution in biology, Jonathan Cape, London (1979).

[5] V. McElheny, Watson and DNA: making a scientific revolution, John Wiley and Sons, London, UK (2003).

[6] D.L. Hull, Science as a process, Chicago University Press, Chicago (1988).

[7] J. Bronowski, The ascent of man, BBC, London (1973).

[8] Editorial. Watson’s folly. Nature 2007;449:948.

[9] J. Watson. To question genetic intelligence is not racism. The Independent, ; Published 19 October 2007 [accessed 10.03.08].

[10] E. Pennisi, Breakthrough of the year: human genetic variation, Science 318 (2007), pp. 1842–1843.

Death can be cured!

A book of ideas collected from Medical Hypotheses: Death can be cured by Roger Dobson

Bruce G. Charlton

Medical Hypotheses. 2008; 70: 905-9.

Summary

A new collection of ideas from Medical Hypotheses by Roger Dobson is entitled Death can be cured and 99 other Medical Hypotheses. It consists of humorous summaries of Medical Hypotheses articles from the past 30 years. The book’s humour derives mainly from the subject matter, although sometimes also from the ‘unconventional’ approach of the authors with respect to matters such as evidence, argument or inference. Medical Hypotheses has generated such a lot of apparently- or actually-bizarre ideas because it aims to be open to potentially revolutionary science. The journal’s official stance is that more harm is done by a failure to publish one idea that might have been true, than by publishing a dozen ideas that turn out to be false. Bizarre ideas tend to catch attention, and may stimulate a valuable response – even when a paper is mostly-wrong. A paper may be flawed but still contain the germ of an idea that can be elaborated and developed. The journal review process is susceptible to both false positives and false negatives. False positives occur when we publish an idea that is wrong; false negatives occur when we fail to publish an important idea that is right, and a potential scientific breakthrough never happens. False positives are more obvious, since the paper will be ignored, refuted, or fail to be replicated – and often attracts criticism and controversy. Editors may therefore take the more cautious path of avoiding false positives more assiduously than false negatives; however, this policy progressively favours less-ambitious science. Consequently, in Medical Hypotheses the ‘set point’ of risk is nearer to the false positive end of the spectrum than for most journals – and the publication of many apparently-bizarre papers is a natural consequence of this policy.

***


A new book of ideas from Medical Hypotheses

Roger Dobson’s collection of ideas from Medical Hypotheses is entitled Death can be cured and 99 other Medical Hypotheses [1], [2], [3], [4], [5], [6], [7], [8], [9], [10], [11], [12], [13], [14], [15], [16], [17], [18], [19], [20], [21], [22], [23], [24], [25], [26], [27], [28], [29], [30], [31], [32], [33], [34], [35], [36], [37], [38], [39], [40], [41], [42], [43], [44], [45], [46], [47], [48], [49], [50], [51], [52], [53], [54], [55], [56], [57], [58], [59], [60], [61], [62], [63], [64], [65], [66], [67], [68], [69], [70], [71], [72], [73], [74], [75], [76], [77], [78], [79], [80], [81], [82], [83], [84], [85], [86], [87], [88], [89], [90], [91], [92], [93], [94], [95], [96], [97], [98], [99] and [100].

This delightful volume consists of gently-humorous summaries of Medical Hypotheses articles published since the journal’s foundation by the late David Horrobin in 1975.

The book’s humour derives mainly from the subject matter, although sometimes also from the ‘unconventional’ approach of the authors with respect to matters such as evidence, argument or inference. The apparently-bizarre nature of the science is of many types. In most instances the subject matter and conclusions are quite mainstream and serious from a scientific perspective, but from the perspective of an outsider they may seem strange. In other instances the ideas really are bizarre, from almost any perspective. And there are theories from all points in-between.

Bizarre ideas tend to catch attention, and may stimulate a valuable response – even when a paper is mostly-wrong. When reading what I think is a mostly-wrong idea submitted to Medical Hypotheses, I sometimes find myself provoked into formulating exactly where and why the idea is wrong – which can be a valuable experience. A paper may be flawed but still contain the germ of an idea that can be elaborated and developed – the reader feels they can do a better job than the author, and might embark on a new line of investigation.

Bizarre or flawed papers that provoke the reader may therefore stimulate correspondence to the author or journal in response, may turn-up later as a citation, or may have an important but invisible effect on another scientist’s attitudes, teaching or direction of research. This is all a contribution to the dynamic process of science – and science should always be regarded as a dynamic process, not a fixed body of facts and laws.
False positives and negatives in reviewing

The reason that Medical Hypotheses has generated such a lot of apparently- or actually-bizarre ideas is that it aims to be open to potentially revolutionary science. The journal’s official stance is that more harm is done by a failure to publish one idea that might have been true, than by publishing a dozen ideas that turn out to be false.

It may easily be forgotten that the review processes of science are susceptible both false positives and false negatives. False positives occur when we publish an idea that is wrong; false negatives occur when the journal fails to publish an idea that is right. False positives are more obvious, since the paper will be ignored, refuted, or fail to be replicated. This attracts criticism because it may waste the time and resources of other scientists.

But false negatives – when we fail to publish an idea which would (in an imaginary alternative universe) have led to some kind of breakthrough – are a more devastating mistake. But the false negative problem is seldom acknowledged, because the consequences may be invisible. Failure to publish might lead to an idea being lost altogether, or being published somewhere less appropriate (increasing the possibility that it would be unnoticed or ignored).

The fact that false positives attract more rapid and certain criticism and controversy than false negatives exerts a constant drip–drip of pressure on editors to take the more cautious and less controversy-generating path of avoiding false positives more assiduously than false negatives. This is prudent, but constitutes a sinister trade-off in the long term because it progressively favours less ambitious and more conservative science.

Consequently, in Medical Hypotheses the ‘set point’ of risk is nearer to the false positive end of the spectrum than it is for most journals. This is why the journal deploys editorial review (where journal contents are chose mainly by the editor) rather than the commoner but more cautious and negative peer review system.

On top of this, the Medical Hypotheses editorial policy constitutes an implicit contention concerning the style in which science should be conducted. Our idea is that it is sometimes (but not always) better to be interestingly wrong than boringly right; sometimes better to err on the side of tolerance rather than exclusion, sometimes better to stimulate than to reinforce closure.

It takes many personality types to make the world of science, and the same applies to journals. Science would not work efficiently if all journals were like Medical Hypotheses: there would be too much ‘noise’ in the system. But science does not work properly when journals will only publish papers that are regarded as completely correct by a panel of peers – because such papers cannot be bold and speculative, and because gems of insight may come from bizarre or flawed research.

Currently, the pendulum has probably swung too far in the direction of excess caution in mainstream medical science; such that the imperative to exclude noise has slipped-over into a too-rigid exclusion of diversity and dissent. The majority of journals publish only ultra-cautious papers that report dependable but cringingly-modest, incremental extrapolations of solidly-established knowledge.

One consequence is that although medical science has expanded hugely in funding and production over recent decades, there has probably been a declining frequency of major breakthroughs which seems to have slowed the rate of medical progress.
The future of bizarre ideas

These are some of the reasons why Medical Hypotheses publishes (apparently) bizarre papers, and how it was possible for Roger Dobson to collect 100 such ideas into an entertaining volume.

However, in the internet era of open-access to international publication, the role of Medical Hypotheses has inevitably become more specialised: it is now more like a place where bold scientific speculation meets the mainstream.

Since Medical Hypotheses has recently entered the realms of respectability with its 2006 impact factor of 1.29, monthly internet downloads running at about 32,000, and the rejection rate currently hovering around 80% or 90% – my challenge as editor will be to build on this success while maintaining the traditional open-ness and genial eccentricity of the journal which have characterized its first three decades.

This goal of avoiding false negatives more assiduously than false positives will almost-inevitably mean that Medical Hypotheses shall need to continue rejecting some probably-correct papers that are worthy-but-somewhat-dull, in favour of publishing some bizarre or flawed papers that just might (but – it must be admitted – probably will not) stimulate a break-though of some sort.

By holding to this principle, I hope to ensure that in another thirty years, a future science writer can produce an equally entertaining and edifying volume as Roger Dobson’s Death can be cured.

References

What follows are the 100 papers from Medical Hypotheses featured in Death can be cured and 99 other Medical Hypotheses, by Roger Dobson – Cyan Books, 32–38 Saffron Hill, London, EC1N 8FH, UK, 2007. ISBN 978-1-905736-31-7. Chapter titles are appended in italics.

[1] Mak MWM, Kwan TS, Cheng KH, Chan RTF, Ho SL. Myopia as a latent phenotype of a pleiotropic gene positively selected for facilitating neurocognitive development, and the effects of environmental factors in its expression. 2006;66:1209–15 [Short-sighted people are more intelligent].

[2] Arzy S, Idel M, Landis T, Blanke O. Why revelations have occurred on mountains. Linking mystical experiences and cognitive neuroscience. 2005;65:841–5 [Revelations always happen on mountains].

[3] Oinonen KA, Mazmanian D. Does body fat protect against negative moods in women? 2001;57:387–8 [Fat people really are more jolly].

[4] Melles RB, Katz B. Night terrors and sudden unexplained nocturnal death. 1988;26:149–54 [Nightmares can kill you].

[5] Stevenson I. The phenomenon of claimed memories of previous lives: possible interpretations and importance. 2000;54:652–9 [Birthmarks are proof of reincarnation].

[6] Fisch H, Andrews HF, Fisch KS, Golden R, Liberson G, Olsson CA. The relationship of long-term global temperature change and human fertility. 2003;61:21–8 [Global warming reduces fertility].

[7] Elsner RJF, Spangler JG. Neurotoxicity of inhaled manganese: public health danger in the shower? 2005;65:607–16 [Showers are bad for the brain].

[8] Samaras TT, Storms LH. Secular growth and its harmful ramifi cations. 2002;58:93–112 [Small people can save the world].

[9] Sri Kantha S. Total immediate ancestral longevity (TIAL) score as a longevity indicator: an analysis on Einstein and three of his scientist peers. 2001;56:519–22 [The date you will die can be calculated].

[10] Katz G, Durst R, Zislin Y, Barel Y, Knobler HY. Psychiatric aspects of jet lag: review and hypothesis. 2001;56:20–3 [Jet lag triggers mental illness].

[11] Harris JR. Parental selection: a third selection process in the evolution of human hairlessness and skin colour. 2006;66:1053–9 [Why humans are not furry].

[12] Verhaegen MJB. The aquatic ape theory and some common diseases. 1987;24:293–9 [The purpose of ear wax].

[13] Bobrow RS. Paranormal phenomena in the medical literature sufficient smoke to warrant a search for fire. 2003;60:864–8 [Hearing voices could save your life].

[14] Ichim I, Kieser J, Swain M. Tongue contractions during speech may have led to the development of the bony geometry of the chin following the evolution of human language? A mechanobiological hypothesis for the development of the human chin. 2007;69:20–24 [The reason for chins].

[15] Howe NE. The origin of humour. 2002;59:252–4 [Humour increases survival].

[16] Fessler DMT, Abrams ET. Infant mouthing behaviour: the immunocalibration hypothesis. 2004;63:925–32 [Babies suck to avoid asthma].

[17] Vardi P, Pinhas-Hamiel O. The young hunter hypothesis: age-related weight gain – a tribute to the thrifty theories. 2000;55:521–3 [Beer bellies protect men in old age].

[18] Kolettis TM, Kolettis MT. Winter swimming: healthy or hazardous? Evidence and hypotheses. 2003;61:654–6 [Why winter swimmers don’t shiver].

[19] Manning JT, Bundred PE. The ratio of 2nd to 4th digit length: a new predictor of disease predisposition? 2000;54:855–7 [Finger lengths predict disease].

[20] Mobley JL. Is rheumatoid arthritis a consequence of natural selection for enhanced tuberculosis resistance? 2004;62:839–43 [Arthritis is the price of having healthy ancestors].

[21] Rubio-Godoy M, Aunger R, Curtis V. Serotonin – a link between disgust and immunity? 2007;68:61–6 [Feeling disgusted is healthy].

[22] Miric D, Hallet-Mathieu A-M, Amar G. Aetiology of antisocial personality disorder: benefits for society from an evolutionary standpoint. 2005;65:665–70 [Psychopaths are a necessary evil].

[23] Cassano WF. Cystic fibrosis and the plague. 1985;18:51–2 [Cystic fibrosis is a legacy of the Black Death].

[24] Sontag SJ, Wanner JN. The cause of leg cramps and knee pains: a hypothesis and effective treatment. 1988;25:35–41 [Modern toilets ruin legs].

[25] Bakan R. Queen Elizabeth I: a case of testicular feminization? 1985;17:277–84 [Queen Elizabeth I was part man].

[26] Bark N. Did schizophrenia change the course of English history? The mental illness of Henry VI 2002;59:416–21 [Schizophrenia changed the course of English history].

[27] Clarkson JDB. A possible origin for the Turin shroud image. 1983;12:11–16 [Jesus, the Turin Shroud and spontaneous combustion].

[28] Størmer FC, Mysterud I. Cave smoke: air pollution poisoning involved in Neanderthal extinction? 2007;68:723–4 [Smoke made Neanderthals extinct].

[29] McSweegan E. Anthrax and the aetiology of the English Sweating Sickness. 2004;62:155–7 [English Sweating Disease was really anthrax].

[30] Walsh GP. The history of the herring and with its decline the significance to health. 1986;20:133–7 [Herrings saved us from heart disease].

[31] Hollander DH. Beef allergy and the Persian Gulf syndrome. Med Hypothesis 1995;45:221–2 [Gulf War Syndrome is an allergy to burgers].

[32] Platek SM, Gallup GG, Fryer BD. The fi reside hypothesis: Was there differential selection to tolerate air pollution during human evolution? 2002;58:1–5 [Prehistoric fires protected man from lung cancer].

[33] Sri Kantha S. Could nitroglycerine poisoning be the cause of Alfred Nobel’s anginal pains and premature death? 1997;49:303–6 [Alfred Nobel was killed by dynamite].

[34] Passie T, Hartmann U, Schneider U, Emrich HM. On the function of groaning and hyperventilation during sexual intercourse: intensification of sexual experience by altering brain metabolism through hippomania. 2003;60:660–3 [Why women groan during sex].

[35] Gofrit ON. The evolutionary role of erectile dysfunction. 2006;67:1245–9 [The importance of being impotent].

[36] Marx GF, Naushaba SH, Schulman H. Is pre-eclampsia a disease of the sexually active gravida? 1981;7:1397–9 [Sex causes high blood pressure in pregnancy].

[37] Sheth R, Panse GT. Can vasectomy reduce the incidence of prostatic tumour? 1982;8:237–41 [Vasectomy lowers the risk of prostate cancer].

[38] Shoja MM, Tubbs RS, Ansarin K. A cure for infatuation? The potential ‘therapeutic’ role of pineal gland products such as melatonin and vasotocin in attenuating romantic love. 2007;68:1172–3 [A cure for infatuation].

[39] Eagles JM. Seasonal affective disorder: a vestigial evolutionary advantage? 2004;63:767–72 [Winter depression stops sex].

[40] Ramachandran VS. Why do gentlemen prefer blondes? 1997;48:19–20 [Gentlemen prefer blondes].

[41] Burger J, Gochfeld M. A hypothesis on the role of pheromones on age of menarche. 1985;17:39–46 [House smells turn teenage girls into women].

[42] Ney PG. The intravaginal absorption of male generated hormones and their possible effect on female behaviour. 1986;20:221–31 [Baby blues are caused by lack of sex].

[43] Xiong X, Buekens P, Vastardis S, Wu T. Periodontal disease as one possible explanation for the Mexican paradox. 2006;67:1348–54 [Gum disease causes small babies].

[44] Gjorgov N. Barrier contraceptive practice and male infertility as related factors to breast cancer in married women. 1978;4:79–88 [Condoms increase the risk of breast cancer].

[45] Schreiber G, Avissar S, Tzahor Z, Barak-glantz I, Grisaru N. Photoperiodicity and annual rhythms of wars and violent crimes. 1997;48:89–96 [Sunny days make men violent].

[46] Richardson-Andrews RC. Sunspots and the recency theory of schizophrenia. 1995;44:16–19 [The sun causes schizophrenia].

[47] Davis GE, Lowell WE. Solar cycles and their relationship to human disease and adaptability. 2006;67:447–61 [The sun fixes lifespan].

[48] Yeung JWK. A hypothesis: sunspot cycles may detect pandemic influenza A in 1700–2000 ad. 2006;67:1016–22 [Flu epidemics are affected by the sun].

[49] Mikulecky M, Rovensky J. Gout attacks and lunar cycle. 2000;55:24–5 [Gout attacks are caused by the moon].

[50] Sok M, Mikulecky M, Erzen J. Onset of spontaneous pneumothorax and the synodic lunar cycle. 2001;57:638–41 [Chest pains are caused by the moon].

[51] Sher L. Effects of the weather conditions on mood and behaviour: the role of acupuncture points. 1996;46:19–20 [How weather affects mood].

[52] Erren TC, Piekarski C. Does winter darkness in the Arctic protect against cancer? The melatonin hypothesis revisited. 1999;53:1–5 [Why Greenlanders have less cancer].

[53] Pauley SM. Lighting for the human circadian clock: recent research indicates that lighting has become a public health issue. 2004;63:588–96 [Lights at night cause cancer].

[54] Laumbacher B, Fellerhoff B, Herzberger B, Wank R. Do dogs harbour risk factors for human breast cancer? 2006;67:21–6 [Dogs give women breast cancer].

[55] Milham S, Ossiander E. Electric typewriter exposure and increased female breast cancer mortality in typists. 2007;68:450–1 [Electric typewriters cause breast cancer].

[56] Komarova SV. A moat around castle walls: the role of axillary and facial hair in lymph node protection from mutagenic factors. 2006;67:698–701 [Hairy people have less cancer].

[57] Kumar A, Mallya K, Kumar J. Are lung cancers triggered by stopping smoking? 2007;68:1176–7 [Quitting smoking too fast triggers lung cancer].

[58] Steindal Hykkerud, Porojnicu AC, Moan J. Is the seasonal variation in cancer prognosis caused by sun-induced folate degradation? 2007;69:182–5 [Cancer is best diagnosed in the summer].

[59] Donovan M, Tiwary CM, Axelrod D, Sasco AJ, Jones L, Hajek R, et al. Personal care products that contain estrogens or xenoestrogens may increase breast cancer risk. 2007;68:756–66 [Hairsprays cause cancer].

[60] Manning JT, Caswell N. Constitutive skin pigmentation: a marker of breast cancer risk? 2004;63:787–9 [Skin colour and breast cancer].

[61] Hoseini SS, Gharibzadeh S. Squeezing the glans penis: a possible manoeuvre for improving the defecation process and preventing constipation. 2007;68:925–6 [A cure for constipation].

[62] Weber C. Eliminate infection (abscess) in teeth with cashew nuts. 2005;65:1200 [Nuts cure toothache].

[63] Robinson A. Electrolysis between the feet and the ground and its probable health effects. 1979;5:1071–7 [Leather shoes cure diseases].

[64] Kumar A. Gag reflex for arrest of hiccups. 2005;65:1206 [A cure for hiccups].

[65] Eby GA. Strong humming for one hour daily to terminate chronic rhinosinusitis in four days: a case report and hypothesis for action by stimulation of endogenous nasal nitric oxide production. 2006;66:851–4 [Humming 120 times a day cures blocked noses].

[66] Kolettis J, Kumar A. Sustained repulsive magnetic force for bone lengthening. 2005;65:630 [Magnets can make you taller].

[67] Mathur RK. The role of hypersomolal food in the development of atherosclerosis. 2005;64:579–81 [Drinking water lowers the risk of heart disease].

[68] Dehmelt H. Healthiest diet hypothesis: How to cure most diseases? 2005;64:882 [A cure for most diseases].

[69] Olson CB. A possible cure for death. 1988;26:77–84 [A cure for death].

[70] Patronek GJ, Glickman LT. Pet ownership protects against the risks and consequences of coronary heart disease. 1993;40:245–9 [Pets prevent heart attacks].

[71] Sabayan B, Zolghadrasli A, Mahmoudian N. Could taking an up-elevator on the way to the delivery room be a potential novel therapy for dystocia? 2007;68:227 [Taking the elevator for a natural birth].

[72] Teas J, Hebert JR, Helen Fitton J, Zimba PV. Algae – a poor man’s HAART? 2004;62:507–10 [Seaweed may prevent AIDS].

[73] Magen E, Borkow G, Bentwich Z, Mishal J, Scharf S. Can worms defend our hearts? Chronic helminthic infections may attenuate the development of cardiovascular diseases. 2005;64:904–9 [Worms prevent heart disease].

[74] Smith W, Skilling DE, Castello JD, Rogers SO. Ice as a reservoir for pathogenic human viruses: specifically, caliciviruses, influenza viruses, and enteroviruses. 2004;63:560–6 [Killer viruses are hiding in the ice].

[75] Robinson A. Heart disease, cancer and vehicle travel. 1979;5:323–8 [Car travel causes heart disease].

[76] Seely S. The recession of gastric cancer and its possible causes. 1978;4:50–7 [How soft drinks prevent stomach cancer].

[77] Fischer KM. Hypothesis: tobacco use is a risk factor in rheumatoid arthritis. 1991;34:116–7 [Smoking caused rheumatoid arthritis].

[78] van Woerden H. Dust mites living in human lungs – the cause of asthma? 2004;63:193–7 [Tiny bugs living in the lungs cause asthma].

[79] Blondell JM. Pesticides and breast cancer, popcorn and colorectal cancer: innovation versus fashion in dietary epidemiology. 1983;12:191–4 [Killer popcorn].

[80] Lim ECH. RCS Seet, Botulinum toxin injections to reduce adiposity: possibility, or fat chance? 2006;67:1086–9 [Botox makes you thinner].

[81] Ahmad Aziz N, Ibrahim Aziz M. Losing weight by defecating at night. 2006;67:989 [Defecate at night to lose weight].

[82] Johnson JB, Laub DR, John S. The effect on health of alternate day calorie restriction: eating less and more than needed on alternate days prolongs life. 2006;67:209–11 [Diet every other day to lose weight and live longer].

[83] Tekol Y. Salt addiction: a different kind of drug addiction. 2006;67:1233–4 [Salt, the cocaine of the kitchen?].

[84] Moishezon-Blank N. Commentary on the possible effect of hormones in food on human growth. 1992;38:273–7 [Why American heads are getting smaller (and the French bigger)].

[85] Nanji A, Narod S. Multiple sclerosis, latitude and dietary fat: Is pork the missing link? 1986;20:279–82 [Eating pork causes multiple sclerosis].

[86] Shaw CA, Bains JS. Did consumption of flour bleached by the agene process contribute to the incidence of neurological disease? 1998;51:477–81 [Mad flour disease].

[87] Ganmaa D, Li XM, Qin LQ, Wang PY, Takeda M, Sato A. The experience of Japan as a clue to the aetiology of testicular and prostatic cancers. 2003;60:724–30 [Milk causes cancer].

[88] Concepcion GP, Padlan EA. Are humans getting ‘mad-cow disease’ from eating beef, or something else? 2003;60:699–701 [Rats spread mad cow disease to humans].

[89] Surja Agus S, El-Mallakh RS. Fertility and childhood bipolar disorder. 2007;69:587–9 [How a prescription drug increased depression in children].

[90] Cook RD. Multiple sclerosis: Is the domestic cat involved? 1981;7:147–54 [MS and the domestic cat].

[91] Cane RH. The role of soap and nutrition in producing human diseases. 1983;11:251–4 [Soap causes heart disease].

[92] Previc FH. Prenatal influences on brain dopamine and their relevance to the rising incidence of autism. 2007;68:46–60 [Autism and city life].

[93] Henshaw DL. Does our electricity distribution system pose a serious risk to public health? 2002;59:39–51 [Power lines cause depression].

[94] Flensmark J. Is there an association between the use of heeled footwear and schizophrenia? 2004;63:740–7 [Heeled shoes cause schizophrenia].

[95] Sutton PRN. Can water fluoridation increase orthodontic problems? 1988;26:63–4 [Fluoride makes teeth crooked].

[96] Clauss R, Mayes J, Hilton P, Lawrenson R. The influence of weather and environment on pulmonary embolism: pollutants and fossil fuels. 2005;64:1198–1201 [Rain causes blood clots].

[97] Moalem S, Storey KB, Percy ME, Peros MC, Perl DP. The sweet thing about type 1 diabetes: a cryoprotective evolutionary adaptation. 2005;65:8–16 [Climate change caused diabetes].

[98] Aronson M. Does excessive television viewing contribute to the development of dementia? 1993;41:465–6 [TV shows cause dementia].

[99] Sutton PRN. Psychosomatic dental disease: Is mental stress in adults followed by acute dental caries in all racial groups? 1993;41:279–81 [Stress can seriously damage your teeth].

[100] Worth J. Neonatal sensitization to latex. 2000;54:29–33 [Gloves cause asthma].

Mega-cash prizes for revolutionary science

Editorial

Stimulating revolutionary science with mega-cash prizes

Bruce G. Charlton (a) and Peter Andras (b)

Medical Hypotheses - Volume 70, Issue 4, 2008, Pages 709-713

(a) Editor-in-Chief – Medical Hypotheses, Newcastle University, NE1 7RU, UK and (b) Editorial Advisory Board – Medical Hypotheses, Newcastle University, NE1 7RU, UK

Available online 5 March 2008.

Summary

We argue that the most ambitious science is intrinsically riskier science, more likely to fail. It is almost always a safer career strategy for the best scientists to seek to extend knowledge more modestly and to build incrementally on existing ideas and methods. Therefore, higher rewards for success are a necessary incentive to encourage top scientists to work on the most important scientific problems, ones where the solution has potentially revolutionary implications. We suggest that mega-cash prizes (measured in tens of millions of dollars) are a suitable reward for those individuals (or institutions) whose work has triggered radically new directions in science.

***

Rewards for successful revolutionary science

Revolutionary science may be distinguished from ‘normal’ science in that revolutionary science aims at generating qualitative advances on established science while normal science aims at incremental progress [1]. While there is a grey borderline, there is a clear distinction between research that aims at transformation of a scientific discipline and that which aims at extension of that discipline [2].

Naturally, since revolutionary science is more ambitious, it is more likely to fail. For every successful instance of revolutionary science there are likely to be manifold examples of failure [3]. By contrast, ‘normal’ incremental science is much more likely to succeed, especially when it is performed by able and well-trained scientists working in well-resourced institutions.

Given that revolutionary science is a high risk endeavour which usually fails; it is likely to thrive only when the incentives rewarding the rare instances of success are greater than for normal science. Therefore we would argue that it is insufficient for successful revolutionary scientists merely to get the usual rewards of prestigious professorships, respect from within the scientific profession, and a modestly high level of reasonably secure income. Something more is needed: lots of money.

The money incentive in science

To compensate for the intrinsically greater risk of failure, successful revolutionary science requires greater rewards than normal science; rewards such as higher prestige, better jobs and/or more money. We suggest that more money is the most promising incentive to encourage revolutionary science, because it is the factor which is most-controllable.

Historically, the main reward for scientific success was high prestige. It was possible for a successful genius to transform a whole science – as Darwin transformed biology and Newton transformed physics. After such success these scientists became public figures so there was an incentive of ‘immortality’ (e.g. Darwin and Newton have appeared on UK banknotes). But now that science is divided into numerous sub-specialties there is less prospect of general public esteem and the rewards of high status are confined to recognition within what may be a relatively small and specific scientific discipline.

Nor is revolutionary science likely to be rewarded with better jobs, except at the very top stratum of eminence such as Nobel laureates. The prospect of rewarding successful revolutionary scientists with better jobs than successful normal scientists is unlikely to happen. Economists usually suggest that the basis of the salary and conditions of a job are the (probable) marginal effects that an individual has on future productivity of an organization [4]. This implies that salaries are not given for past achievement, except when this enhances future prospects for the organization. For example, the top research universities in the USA seem to compete to have Nobel laureates on their faculty as a symbol of their scientific eminence. This signal is apparently effective even when the laureates are semi-retired and unproductive.

But this is due to the extreme rarity of Nobel laureates [5], and at lower levels of eminence there is little advantage for an institution to employ people who were, in the past, successful at revolutionary science – and to employ them at the enhanced rates of pay and privileged conditions of service which are necessary to compensate them for having chosen the high-risk path of revolutionary science.

A scientist of high ability who chooses revolutionary science as a career will probably and on average attain lower outputs, lower numbers of citations, lower-impact publications and less professional prestige than if they put the same efforts and abilities into normal science. (To put in another way, a scientist would probably gain a higher rate of science production by aiming directly at attaining high science production, than by aiming to solve a major problem.)

An able and committed scientist choosing a normal science path would therefore usually be able to out-perform himself as a revolutionary scientist, in terms of immediate and measurable performance measures. A longer term strategy will tend to generate results and produce rewards later. Even if everything goes perfectly and a successful revolutionary scientist ends-up with a Nobel prize, the chances are that this will come near or after the end of their professional career.

But the prospect of a major prize such as a Nobel is surely too unlikely, too remote and too uncertain to be a widespread or realistic motivation in the career paths of young scientists in their twenties or thirties. And it is at this age when scientists must decide whether or not to pursue revolutionary science [6].

Incentives for the best young scientists to pursue revolutionary science

The critical decision to embark on a high-risk strategy of revolutionary science would typically come not much later than a scientist’s late-twenties – just after they have finished their PhD or equivalent research training [6]. Of course, some young scientists will be so idealistic (or so unrealistic) that they ignore the potential rewards or costs of their career choices. Nonetheless, incentives usually make a difference to human behaviour, and if there were more powerful incentives, then presumably more scientists would opt to practice revolutionary science. So, what are the incentives which might affect a young and gifted scientist’s career selection?

Let us imagine an outstanding young scientist who has the potential to be first rate. He or she is faced by a choice between a high risk strategy of trying to make a revolutionary contribution to their branch of science, or else to ‘down-shift’ to a less ambitious but lower-risk path of doing a large volume of high-quality normal science. The best scientists are, in other words, in a position to choose between a small chance of success at the goal of making a first rate qualitative breakthrough, and a much better chance of success as a second rank scientist – perhaps making numerous incremental and quantitative advances in the most prestigious areas of existing science.

As argued above, at this age the small chance of a Nobel prize at (say) 65 years old would strike most objective people as hopelessly unlikely, and vastly remote compared with the much more immediate prospect of generating high-impact, highly-cited, well-funded normal science leading reliably to a job at a prestigious institution within the decade. Our feeling is that the only effective incentive to encourage this young scientist into the high-risk strategy of revolutionary science is the prospect of becoming fabulously rich at a stroke – in other words the prospect of winning a mega-prize for revolutionary science.

The prospect of vast riches in the near-ish future is an important motivation to encourage high achievement in creative areas of popular culture in fields such as music, acting and sports. The competition in these areas is intense, and the percentage chance of success is very low – but ‘the mass market’ rewards success very highly and the reward comes while the person is still young – so the incentive is that much more powerful. Music, acting and sports are among the few fields in which young people can become fabulously rich while still young, and there is therefore no shortage (indeed, a huge surplus) of young people competing in these areas of endeavour while eschewing safer and more secure careers [7].

Our point is not that it is necessarily socially beneficial to have so many young people chasing so few niches in music, sports and acting – rather to emphasize that a large and not-too-distant financial reward seems to be a powerful incentive in creative activities. If it works in the arts, we believe the motivating effect of riches would also work in the sciences. We see no reason why revolutionary science would be an exception.

Why mega-cash prizes for revolutionary science?

Traditional science prizes gain their prestige from their extreme rarity – for example, Nobel prizes are awarded to a maximum of three people per year in each discipline (and this rarity would still apply even if the number of Nobel prizes were expanded, as we have advocated [2] and [5]). So, Nobel prizes are essentially prestige rewards. The financial reward attached to Nobel prizes (although it is fairly generous – over one million US dollars shared among the recipients) is of such little motivational significance that media reports often neglect to mention the sum of money.

But in the early days of Nobel prizes, the large amount of money attached to each award was a major reason for the prestige of the prize. If mega-cash prizes became used as an incentive to promote revolutionary science, then the intrinsic status of the prize would again be dependent mainly on the amount of money (rather than the sheer status of winning the prize) because the intention of using mega-cash prizes is that there be many such prizes without the large numbers diluting the motivational effect of the prize.

Traditional science prizes (such as Nobels) therefore constitute a zero sum game in which the more prizes are awarded the less prestige attaches to each prize – because there is only a fixed amount of status to be shared. But this does not apply to monetary rewards – a prize of one hundred million dollars remains well-worth winning whether it is unique or whether 10 or 100 other people also get a 100 million dollar prize. This is important because there need to be enough prizes for revolutionary science that competitors should feel they have a realistic chance of winning one of these prizes so long as their research succeeds in its aims. This would enable there to be a significant incentive to do revolutionary science across as many scientific disciplines as there are mega-cash prizes.

Our feeling is that mega-prizes to stimulate revolutionary science would need to be of the order of magnitude of tens of millions of US dollars in order to replicate the kind of incentives seen in popular creative activities such as music and sports.

Potential problems with mega-cash prizes

There are (at least) two major problems in using mega-prizes to stimulate revolutionary science. However both problems are potentially soluble.

The first problem is that the prizes must have a basis in objective fact, to guard against the prizes being awarded for subjective reasons (for example for political reasons – as has arguably been the case for the MacArthur ‘genius’ fellowships (www.macfound.org) – where significant numbers of recipients seem to have been chosen for their symbolic value rather than their measurable achievement).

To guard against this possibility, our proposal is that mega-prizes should be awarded only to those who have objective evidence of having performed successful revolutionary science. This could be accomplished by specifying objective scientometric criteria which must be satisfied before a person or group can be considered eligible for a prize.

A second difficulty is that mega-prizes must be awarded early enough in a person’s lifespan to act as an incentive to aspiring scientists who are planning their career strategy in their mid-twenties. We think this implies that these prizes should usually be awarded before the age of fifty.

The paradox is that revolutionary science prizes are intended to promote ambitious long term strategic research. Yet to be an effective incentive the prize must be awarded in the medium term (and not the long term). In other words, a compromise is necessary.

In practice, a mega-cash prize before fifty would encourage the brightest 25–35 year old scientists to adopt a time horizon of about ten years for research coming to fruition – on the assumption that a decade-level of long-termism is worthwhile in a context of normal science which typically rewards achievement in units of more like 3–5 years.

A prize awarded before fifty would allow post-doctoral scientists to work on a problem for about a decade, then would allow approximately another decade for the importance of this work to become apparent and for a revolutionary breakthrough measurably to influence the research practices of other scientists.

Scientometrics as a basis for revolutionary science prizes

To be an effective incentive, a prize needs to be relatively transparent and objective, so that the aspiring scientist can be reasonably confident that if they do in fact achieve success in revolutionary science, then this will probably be noticed and they will in likelihood be considered for a prize.

The necessary level of transparency and objectivity can best be achieved by having a first stage selection process based on objective scientometric criteria. This, in turn, requires the development of scientometric instruments for measuring revolutionary science [2] and [8]. Such scientometric instruments are not currently available, and the development and testing of scientometric methods for measuring revolutionary science would – we hope – be a very valuable by product or spin-off benefit of using mega-prizes to reward revolutionary science.

A proper consideration of the topic of scientometric methods for detecting and measuring revolutionary science requires separate treatment, but for the present is may suffice to say that the basis of objective recognition of successful revolutionary science is that the success of revolutionary science can be defined by the fact that revolutionary science affects the direction of normal science. In other words, what makes revolutionary science a success is that is changes normal science then becomes normal science.

In terms of scientometrics, this means that revolutionary science can (in principle) be identified retrospectively from the fact that a small set of revolutionary science communications generate a much larger set of normal science communications which are referenced-back to that originating revolutionary science. In a nutshell, successful revolutionary science can be defined as the work that leads to the evolution of a new scientific specialty.

A new scientific specialty is typically either a sub-specialty of a previous science or a hybrid science. A sub-specialty example is when new branch of medical science develops around a class of disease – e.g. lung disease or liver disease; further new sub-specialty sciences may then arise from sub-classes of these disease classes – e.g. asthma sub-specializing from lung diseases, or hepatitis from liver diseases; and then the process may continue. An example of a hybrid science would be biochemistry – when a new specialty was created by the simultaneous application of theories, techniques and other forms of knowledge from both sub-sets of biology and chemistry knowledge.

This means that some revolutionary science (although not all of it) should be identifiable from a sophisticated analysis of citations within the scientific literature. For example, there may be an observation that over a specified period of time (between, say, 5–10 years) a new cluster of inter-referenced science communications has emerged. This could be detected by the emergence of a new set of specialized conferences, journals and papers – detected using specific terms and methods. More sophisticated methods could include the analysis of emerging citation clusters representing new foci of scientific activity [e.g. [9] and [10]].

The main difficulty is that not all scientific communications are accessible to analysis. For example, as well as formal scientific papers and other public communications there are many un-recorded informal interactions between scientists occurring verbally and by ephemeral or inaccessible media such as notes, letters and private e-mails – not to mention the thoughts inside each scientists head! So scientometrics will only sample from a sub-set of science communications, and it is inevitable that some examples of revolutionary science will remained undetected or under-estimated.

Nonetheless, given the advantages of objective quantification, we would advocate that the field of possible recipients of revolutionary science mega prizes should initially be defined by scientometric methods. After this potential field has been defined, then expert peer review methods could be used to determine whether the identified potential examples of successful revolutionary science were primarily the work of a small number of individual scientists (potential prize recipients); or alternatively the work of teams within a small number of research institutions (in which case the prize could be awarded to the institutions).

Prizes instead of program grants

In conclusion, we suggest that revolutionary science could be encouraged by increasing the monetary incentives for successful revolutionary science – especially the incentives as they operate on the best young scientists as they choose their career paths in their mid twenties to early thirties.

This could be accomplished by a change in behaviour of the large grant awarding bodies – a shift from funding research programs with grants and towards rewarding successful revolutionary science with prizes. For example, a research foundation working in a specific scientific field might at present spend 100 million dollars per year – and might spread this money among ten 10 million dollar program grants. In all likelihood, this money will at present be spent on normal science, and will produce modest incremental progress.

We are suggesting that such a research foundation might instead spend 100 million dollars in a single prize, awarded to a relatively young scientist or a few scientists in recognition of a significant success in revolutionary science.

In the short term, this kind of prize would serve merely as a retrospective recognition of research which had been done anyway – but after a few years the mega-cash prize would begin to work as a prospective incentive; shaping the behaviour of young scientists towards more ambitious scientific problems which (if successfully solved) would be eligible for such prizes.

There is a previous literature on the use of prizes to stimulate scientific research [11], [12], [13] and [14] – however, these types of prizes have either implicitly or explicitly been orientated towards problem solving as quickly as possible and therefore using the simplest possible methods – since this ‘research and development’ approach is most likely to win the prize.

What is novel about our argument here, is that we are suggesting that prizes may also be set-up such that they encourage revolutionary science. Furthermore, we advocate the use of scientometrics as a screening mechanism before peer review as a method of preventing corruption and ensuring that the research being rewarded has had an objectively verifiable consequence of revolutionizing (i.e. changing the direction of, or opening-up new fields for) the practice of science.

In other words, mega-cash prizes might encourage some of the very best young scientists to make more long-term and high risk career choices. The real winner of this would be society as a whole; since normal science can successfully be done by second rate scientists – but if the first rate scientists do not make the decision to tackle the toughest scientific problems, then solutions to these tough problems may be delayed, or they may never be solved.

References

[1] T.S. Kuhn, The structure of scientific revolutions, Chicago University Press, Chicago (1970).

[2] B.G. Charlton and P. Andras, Evaluating universities using simple scientometric research output metrics, Sci Publ Policy 34 (2007), pp. 555–563.


[3] D.L. Hull, Science as a process, Chicago University Press, Chicago (1988).

[4] Caplan B. George Mason University – Econ 103: Labour markets and labour regulation. [accessed 02.01.08].

[5] B.G. Charlton, Why there should be more science Nobel prizes and laureates, Med Hypotheses 68 (2007), pp. 471–473.

[6] F.L. Holmes, Investigative pathways, Yale University Press, New Haven (USA) (2004).

[7] R.H. Frank and P. Cook, The winner take all society, The Free Press, New York (1995).

[8] Charlton B, Andras P. The ‘down-shifting’ of UK science? – The decline of ‘revolutionary science’ and the rise of ‘normal science’ in the UK compared with the USA. Med Hypotheses, in press. doi:10.1016/j.mehy.2007.12.004.

[9] A.F.J. Van Raan, Reference-based publication networks with episodic memories, Scientometrics 6393 (2005), pp. 549–566.

[10] Van Raan AFJ. Scaling rules in the science system: influence of field-specific citation characteristics on the impact of research groups. ; 2007.

[11] D.F. Horrobin, Glittering prizes for research support, Nature 324 (1986), p. 221. Full Text via CrossRef

[12] Davis LN. Should we consider alternative incentives for basic research? Patents vs. prizes. Presented at DRUID summer conference 2002. ; 2002 [accessed 02.01.08].

[13] B.G. Charlton, Mega-prizes in medicine: big cash awards may stimulate useful and rapid therapeutic innovation, Medi Hypotheses 68 (2006), pp. 1–3.

[14] J.E. Stiglitz, Scrooge and intellectual property rights: a medical prize fund could improve the financing of drug innovations, BMJ 333 (2006), pp. 1279–1280.

UK scientists down-shift to second rate research

Charlton BG, Andras P. ‘Down-shifting’ among top UK scientists? - The decline of ‘revolutionary science’ and the rise of ‘normal science’ in the UK compared with the USA. Medical Hypotheses. 2008; 70: 465-472 - doi: 10.1016/j.mehy.2007.12.004

[I apologize that the tables are not properly formatted - but I believe they can be understood with some extra effort. The Figure is missing from this pre-print, but it merely summarizes Table 1].

Editorial

‘Down-shifting’ among top UK scientists – The decline of ‘revolutionary science’ and the rise of ‘normal science’ in the UK compared with the USA

Bruce G. Charltona, , Editor-in-Chief – Medical Hypotheses and Peter Andrasa
aMedical Hypotheses, Newcastle University, Henry Wellcome Building, NE1 7RU, UK

Available online 28 January 2008.



Summary
It is sometimes asserted that UK science is thriving, at other times that it has declined. We suggest that both assertions are partly true because the UK is thriving with respect to the volume of ‘normal’ science production but at the same time declining in the highest level of ‘revolutionary’ science. Revolutionary science may be distinguished from normal science in that revolutionary science aims at generating qualitative advances which change the direction of established science, while ‘normal’ science aims at incremental progress extrapolating from established science. Revolutionary science has been measured by counting national numbers of science Nobel laureates and ISI Highly Cited (HiCi) scientists; normal science has been measured using the total volume of scientific publications and citations at both national and institutional levels. By these criteria the UK has been progressively catching-up with the USA in terms of normal science since the 1990s. At the same time the UK has declined in revolutionary science over recent decades by a significant brain drain of future Nobel laureates and HiCi scientists, and a sharply reduced success (both in absolute and compared with the USA) at winning science Nobel prizes. One possible cause for this pattern could be a time-lag, such that the UK’s improved science production since about 1990 may eventually work-through into improved UK performance in revolutionary science. More pessimistically, this pattern may reflect a strategic down-shift of the best UK-resident scientists away from revolutionary science and towards less-ambitious and safer normal science which is more productive in the short term.

Introduction

It is sometimes asserted that UK science is thriving, at other times that it has declined. We suggest that both assertions are partly true, and that the UK is thriving with respect to the volume of science production and at the same time UK performance has declined at the highest level of ‘revolutionary’ science.

We suggest that the UK pattern of catching-up with the US in normal science while declining in revolutionary science can be explained by reduced ambition among the best UK scientists – a ‘down-shift’ from aiming at a breakthrough in revolutionary science and towards incremental progress in normal science.

Revolutionary science versus normal science

Revolutionary science is a term coined by Thomas Kuhn in his book The Structure of Scientific Revolutions (Chicago University Press, 1970) to describe research which changes the fundamental structures of science by making new theories, discoveries or technologies (i.e., new ‘paradigms’).

Revolutionary science may be a breakthrough which changes the fundamental structures of a whole science (as achieved by Einstein, Newton or Darwin) or, more often, which develops a significant sub-speciality of a major science (as Crick and Watson developed molecular biology). Revolutionary science is therefore the cutting-edge which solves problems that are intractable to the incremental gradualism of normal science, and thereby allows each science to continue to grow in rapid bursts, and over the long term to become qualitatively more accurate and useful in its predictions.

But normal science does not attempt to establish new directions or to develop qualitatively new explanations or technologies, or to make paradigm-shattering discoveries. Instead, normal science is the incremental extrapolation of already-existing paradigms – and it comprises building on established research by procedures such as checking, trial-and-error and gradual improvement in the precision of measurement.

The great bulk of research in modern developed societies such as the USA, UK, France, Germany, China or Japan is ‘normal science’ [1]. Normal science attempts to improve on established science and to extend its capabilities step-by-step further in the direction towards which it is already tending. This means that normal science can be planned and managed. Normal science is also amenable to evaluation by peer-review processes because much science is so modest in its ambition, and its methods are so well-tested, that even newly-published research can be regarded as ‘pre-validated’, and may be ready for implementation without the necessity for further corroboration [2].

The intrinsically high risk of failure in revolutionary science
Revolutionary science aims at generating qualitative advances – new theories, techniques or discoveries which change the direction of established science, while by contrast normal science aims at incremental progress extrapolating from established science.

Since revolutionary science is much more ambitious than normal science, it is intrinsically riskier and more likely to fail in its aims. The biographies of even the most prestigious revolutionary scientists typically contain many failures both before and after the success for which they became famous – for example Crick and Watson’s botched DNA model of 1951 [3], and Andrew Wiles’ mistaken announcement of 1993 that he had proved Fermat’s last theorem [4]. In both cases, despite these psychologically-devastating setbacks, the scientists continued to work on the problem and produced a correct solution within a couple of years. But the fact that even the very best scientists fail when doing the most ambitious work emphasizes the riskiness of revolutionary science.

Since outcomes are so unpredictable, revolutionary science should be defined by its aspirations rather than by its outcomes. A system of revolutionary science therefore consists of the scientists actively working on a problem of potentially-revolutionary scope and the scientific communications between these scientists (including all their relevant verbal and written communications: conversations, e-mails, letters, formal publications, specialist journals, seminars, conferences, etc.). Recognized revolutionary scientists should therefore be regarded as merely the clearest and most visible tip of a much larger iceberg of ambitious researchers who are engaged in endeavours to solve tough scientific problems. So although the majority of revolutionary scientists never succeed in their objectives and never attain fame or success, their co-operation, competition, checking and critique nonetheless plays a crucial role in the process of scientific advance [5].

By contrast with revolutionary science, normal science is much more likely to succeed than to fail, especially when normal science is conducted by able and well-trained scientists working in large multi-disciplinary teams located in well-resourced institutions. In this sense, normal science resembles industrial research and development, which can reliably accumulate numerous small incremental improvements built upon already-established science.

Of course there is an overlap between revolutionary and normal science, for example when one of the increments of progress in normal science unexpectedly turns out to have revolutionary implications. This is ‘serendipity’, but even here chance favours only the prepared mind, and scientific happy accidents may be neither noticed nor exploited unless discoverers recognize their potentially revolutionary implications. On the whole, cautious, modestly-ambitious research which aims at incremental extension of existing knowledge along established lines is very unlikely to lead to a scientific revolution, and if something hinting at a scientific revolution does crop–up it may well be ignored because it was unpredicted, and not part of the plan.

In a nutshell, the greater short term productivity and greater chance of a successful outcome that are characteristics of normal science are attainable only at the cost of diminution in the potential importance of successful research [2].

Measuring revolutionary and normal science

Science production can be measured and analyzed quantitatively using standard scientometric research outputs such as number and share of publications and citations counted over a period of time; with credit allocated to a specified unit of production such as a nation, an institution, a research group or an individual scientist. This activity comprises the discipline of scientometrics [6], [7] and [8].

But successful revolutionary science is rare – indeed entirely absent from many research situations – and in modern, developed societies revolutionary science is swamped by the much larger volume of normal science [5] and [8]. Furthermore, successful revolutionary science can usually only be detected retrospectively and after a time lag of many years. In the short term it is not possible accurately to pick-out the successful revolutionary science from the much larger pool of speculative theories, apparently anomalous observations and radical suggestions for technological improvements.

Only after the revolutionary science has proven itself in terms of triggering new developments which have spread through into normal science can it be confidently assumed that a scientific revolution has indeed occurred. For example, the occurrence of revolutionary science can be retrospectively detected by observing a new direction or change in the direction of research; which may be visible in terms of new types of subject matter for study, new methods or technologies, new conference topics and journals, and eventually new types of research unit and educational specializations within universities (such as new modules or degree programmes).

The problem of discriminating between revolutionary and normal science has become even more difficult since the advent of Big Science [1] and [6]. Big Science comprises quasi-industrial forms of research organization. It arose initially in physics during the 1939–1945 world war (for example the development of radar in the UK or the much larger Manhattan project for developing the atomic bomb in the USA); but Big Science organization now characterizes biomedical research [9], which is currently the dominant world science.

Big Science is almost inevitably a type of normal science, since it needs to be planned and predicted, hence it must be modestly incremental. Furthermore, Big Science tends to be ‘applied’ in its aims, and similar to industrial Research and Development in its methods.

Therefore, different scientometric methods are needed to detect and measure the rare but potentially more-important examples of paradigm-transforming Kuhnian ‘revolutionary science’. We suggest that scientometric measurement of revolutionary science might focus on identifying and counting successful revolutionary scientists instead of measuring the total of scientific production.

Normal science trends – UK versus US

Normal science can be measured using the total number of scientific publications or citations to publication listed in databases such as Thomson Scientific’s Web of Knowledge (http://portal.isiknowledge.com) or Elsevier’s Scopus (www.scopus.com). While the total number of citations and publications includes revolutionary science as well as normal science, it seems likely that – given the rarity of successful revolutionary science – the proportion of publications and citations attributable to revolutionary science from the total of all publications and citations will not be insignificant.

Using data on number of scientific publications and their citations it seems that the UK (and also Europe generally) has been increasing its market share relative to the USA over recent years. For example, King reports [10] that from 1993–1997 to 1997–2001 the percentage UK share of total world publications was second only to the USA (the UK has since been overtaken by China [11]), and increased from 9.29 up to 9.43 while citations increased from 10.87 up to 11.39. At the same time, US percentage shares were declining for both publications (37.46 down to 34.86) and citations (52.3 down to 49.43). So this represents a significant catch-up of the UK with the US in normal science production throughout recent years.

To examine normal science at an institutional level, we measured science production of publications and citations at the most successful UK and US scientific research universities using the ISI Web of Science (WoS) Science Citation Index (SciCitI) data for the period 1975–2004. We determined publication and citation counts for 94 UK universities and 299 US universities (national universities and top-50 liberal arts colleges – derived from US News) for all years between 1975–2004.

The WoS was searched for each university and each year to determine the number of publications published by members of the given university in the given year and the number of citations that these papers received since they were published up to the time of data collection (February 2006). Total counts for five year periods were pooled to reduce yearly fluctuations. This method means that each publication and its citations will be multiply-credited to all institutions that are listed in its author affiliations.

UK and US universities were ranked for the six five-year periods for publication and citation counts. The top-20 universities were determined for each of these 12 UK rankings. For the top-20 UK universities in each UK ranking we calculated their average rank in the corresponding UK–US ranking (see Table 1 and Fig. 1). This generated a statistic for the average UK–US rank of the top-20 UK universities at each five year period for SciCitI-listed publications and citations.

Table 1.

Average ranking (to nearest integer) of total volume of publications and citations for top-20 ranked UK universities when included with 299 top-ranked US universities and colleges 1975–2004 in five year segments 1975–1979 1980–1984 1985–1989 1990–1994 1995–1999 2000–2004
Publications average rank UK top-20 81 81 79 77 65 62
Citations average rank UK top-20 76 83 84 83 70 65


Figure 1. Average ranking of top-20 UK universities relative to 299 top US universities in five year segments 1975–2005.


The table and graph demonstrate that the top US universities are much more productive of publications and citations than are the top UK universities, since the average top-20 UK university never ranks higher than 62nd place at any timepoint. Therefore, on average the best US universities are much more productive of normal science than the best UK universities.

But again the UK seems to be catching-up with the US in recent years. The average top-20 UK University showed improving average UK–US ranking in both publications and citations from the 1975–1979 period to the 2000–2004 period. Thirty years ago the average top-20 university would be ranked in 81st place for publications and 76th place for citations whereas most recently this average top-20 UK university has moved up 19 places in the rankings for publications and 11 places in the ranking for citations.

On closer inspection, the UK citation ranking worsened in the first 15 years, then sharply improved in 1990–2004 period with an average top-20 UK university improving by 19 places relative to the US (see Fig. 1 and Table 1).

The conclusion from both national-level and institutional-level Web of Science data is that in terms of normal science production the UK is worse than the USA, but the UK has been catching-up over the past two decades.

Revolutionary science trends – UK versus US Nobel prizes

The scientometrics of revolutionary science is vestigial; and the subject has until recently been the domain of historians of science who have worked by detailed and discipline-specific study of documentary material, sometimes supplemented by retrospective interviews [5], [12] and [13].

But this historical method suffers from being labour intensive and piecemeal; and simpler, more quantitative methods would be desirable. Here we have measured revolutionary science by counting successful individual revolutionary scientists using science Nobel prizes and data on the migration of ‘Highly Cited’ (HiCi) scientists from the Thomson Scientific database (previously the Institute of Scientific Information – ISI).

The award of a Nobel prize in one of the four recognized sciences (Physics, Chemistry, Physiology/Medicine and Economics) seems likely to be the best current evidence of a significant achievement in revolutionary science [14]. We are making the assumption that national success at generating Nobel-quality revolutionary science in these four scientific domains is indicative of success across a broader range of top-notch science. Although the small annual number of Nobel prize-winners (‘laureates’ – maximum of three per discipline equal to twelve per year) means that many significant achievements go unrecognized; nonetheless the perceived validity of these awards is high within the scientific community, and only a small proportion of awards are regarded as controversial or unjustified.

However, it must be remembered that counting Nobel laureates only measures the most highly-visible and most fully-validated tip of a presumed iceberg of revolutionary science. The prize credits successful revolutionary science which has changed the direction of a discipline in a big way, and where credit for this can be allocated to a single person or a few individuals. It is almost certain, on general theoretical grounds derived from complex systems theory [15] and [16], that the process of generating major breakthroughs in revolutionary science must be supported by a much larger submerged base of revolutionary science research which is harder to identify with confidence, and where credit for achievements is spread between many individual scientists.

When the number of Nobel laureates in the UK and the US are counted for 20 year segments [17] we can see that the UK has suffered a sharp decline in the past twenty years, from 25 prizes 1967–1986 to just 9 prizes from 1987 to 2006. By contrast the US has increased the number of laureates from 88 in 1967–1986 to 126 in 1987–2006. In other words, over a period of 60 years the UK has declined from being broadly equal to the USA in terms of Nobel prizes per capita, and holding undisputed second place (by a large margin) in terms of total Nobel prizes, down to the current position of winning similar numbers of Nobel prizes to other comparable large developed nations such as Germany (9 prizes) or France (5 prizes).

To illustrate this, we can observe that in the past 20 years, the USA has 16 institutions which have won three or more prizes, compared with a complete absence of such treble-Nobel institutions in the UK. From 1967 to 1986 University of Cambridge, the MRC Molecular Biology Unit at Cambridge, University of Oxford and Imperial College, London won an impressive total of 17 Nobel prizes between them – however since 1986 they have all-together won just 3 [17].

In a separate study of the official biographies and autobiographies of Nobel laureates on http://nobelrpize.org, Charlton examined the pattern of national migration for the past 60 years (where this could be established). Each laureate’s prize was allocated to a nation on the basis of the working address at the time the prize was awarded. Some laureates were omitted because their biographies were incomplete, some laureates were retired, and some worked at unclassifiable multinational units such as CERN.

Table 2 shows the numbers of US versus UK laureates for 20 year segments 1947–2006. ‘Total immigrant laureates’ is the number of scientists who graduated from university elsewhere then migrated either to the US or UK where they were working at the time when they received the Nobel prize. This data suggests that in the past 20 years the UK has lost its previous ability to attract future Nobel-prize-winning scientists from elsewhere.

Table 2.

US:UK science Nobel laureates – immigration and migration trends 1947–2006 1947–1966 1967–1986 1987–2006
Total laureates included 45:20 85:24 112:9
Total immigrant laureates 11:3 25:6 21:0
UK–US migration 0 5 5



The row ‘UK–US migration’ shows the number of scientists during each 20 year segment who were educated in the UK then migrated to the USA where they were awarded a Nobel prize. (The reverse US to UK migration did not happen during the past 60 years.) This trend suggests that the US has become increasingly attractive to UK educated scientists over the past 60 years, such that for 1987–2006 five out of fourteen (36%) of all UK-educated laureates had moved to the USA by the time they won the Nobel prize.

UK versus the US – Highly Cited scientists
Nobel laureates might be regarded as a very partial and biased sample of successful revolutionary scientists; although Nobel differentials are maintained when other comparably prestigious prizes, medals and awards are added to the analysis (e.g., for disciplines such as clinical medicine, mathematics and computing science [18] and [19]). A more objective and complete sample of high status scientists can be derived from scientometric data concerning the most frequently-cited academics in specific scientific disciplines.

Highly Cited (HiCi) scientists are defined by Thomson Scientific as those researchers who have received the highest number of citations in their field of research [20]. Highly Cited status is likely to be less correlated with revolutionary science than winning a Nobel prize, since a scientist can accumulate many citations without making a revolutionary breakthrough but instead by exceptionally high productivity, or by doing research that is very useful while not being revolutionary in import. Nonetheless, many HiCi academics do go-on to win Nobel prizes and similar awards [7].

Ioannidis reported that during 1981–1999, 56% of UK-born HiCi academics had migrated to another country compared with only 2% of US born HiCi academics [21]. This demonstrates that the US is much more able to retain its best quality scientists than is the UK. In amplification of these results, Ali et al. have recently examined migration and productivity of HiCi academics in economics, physics and biosciences – which confirms that the US is a net gainer of HiCi academics while the UK is a net loser [22]. Furthermore, a preliminary study by Pierson and Cotgreave, which examined a cohort of UK science Ph.D.’s from 1988 to 2000, suggested that those who had migrated to the USA were able to generate more citations per article than those who remained in the UK [23].

In conclusion, studies of the migration patterns of Highly Cited scientists in the Thomson Scientific (previously ISI) Web of Science database are consistent with the Nobel laureate data in demonstrating that the US is nowadays a much more significant focus of revolutionary science than the UK. While the field remains undeveloped, the pattern of scientometric evidence which plausibly measures national attainment in revolutionary science strongly indicates that the UK has substantially declined relative to the USA.

In other words, although the UK remains probably the third most productive scientific country in the world, the UK has now declined in revolutionary science to the point where the nation is unable either to attract or to hold-onto the very best revolutionary scientists – whether these are measured by HiCi status or by Nobel prizes.

Time-lag or down-shift

Our conclusion is that the UK has been progressively catching-up with the USA in terms of normal science production since about the 1990s, but the UK has sharply declined in revolutionary science achievements over recent decades. Optimistic and pessimistic interpretations of this pattern are possible.

An optimistic interpretation would be that the pattern is the result of a time-lag between improvement in normal science and revolutionary science. In this case the divergence between normal and revolutionary science would be regarded as temporary, and simply a consequence of insufficient time for the short term improvement in normal science since about 1990 to work through into improved performance in the longer-term indices measuring revolutionary science. If this optimistic interpretation is correct, the UK should soon see a rapid increase in the number of Nobel laureates and the Highly Cited scientists, a reversal of the brain drain of the best UK scientists, and also a renewed ability of the UK to attract the very best scientists from around the world.

However, on balance we would favour a more pessimistic interpretation of these results since the above analysis indicates a significant brain drain of the very best UK scientists [21] and [22]. It is likely that this loss of talent has contributed to a reduced UK level of activity in revolutionary science research. But the magnitude of decline in UK revolutionary science may indicate that additional factors are at work, such that the top quality scientists who remain in the UK may have redirected their efforts from revolutionary science to normal science.

One hypothesis is that there may have been a ‘down-shift’ strategy of the most-able UK scientists to direct their efforts into solving easier and less-important scientific problems than they are capable of tackling. For reasons discussed earlier, the numbers of ‘most-able’ scientists is likely to be large and comprise easily enough people to influence scientometric measures (for instance, we have informally observed that the science production of a single large research team is sufficient to move a UK university up by several places in the rankings for publications and especially citations – unpublished observations).

Probably, there are many hundreds of potentially-elite professional scientists working in the UK. Their choices, such as the choice between working on revolutionary or normal science problems, will have a large impact precisely because their productivity is so much higher than average. For instance, we suggest that potential UK Nobel prize-winners may, over recent decades, have re-orientated their research away from the riskier strategy of pursuing revolutionary science and towards less ambitious projects that are more immediately productive. In other words we propose that these top UK scientists may – on average - have shifted down a gear, to accelerate their careers by solving more, smaller or easier problems over the short term.

Since these are some of the ablest and best-trained scientists in the world, by down-shifting into normal science they are typically able to out-perform their competitors in terms of producing large quantities of high quality normal science. This would have the effects of enhancing scientometric measures of normal science at the top universities specifically and also boosting national level statistics for publications and citations. This move improves the prospects of a swift accumulation of grant income to invest in manpower and equipment, and fuel further research that would tend to attract citations early in the scientist’s career.

A strategy of top scientists increasingly eschewing risk and pursuing the more certain rewards of normal science could therefore account for the UK pattern of declining revolutionary science and improving normal science.

Conclusion

Our conclusion is that UK revolutionary science has declined over the past sixty years. Yet at the same time the production of UK science as a whole has actually grown faster than US science in terms of the number of publications and citations. Our speculative interpretation of this pattern of simultaneous rise and fall focuses upon the down-shifting of ambition of UK scientists. We also assume that a similar down-shift has not occurred to the same extent in the USA.

Given that revolutionary science is a high risk and long-term endeavour which usually fails, it is likely to thrive only when the incentives rewarding success are much greater than for normal science. Our hypothesis entails that the incentives to encourage the best scientists to pursue revolutionary science would be more powerful in the USA [24]. Such US incentives might in principle include less severe punishment for failure when aiming high in science; and greater rewards for success in revolutionary science than for success in normal science. Such rewards for revolutionary scientists might include higher pay, more favourable working conditions, greater chance of employment at elite institutions, longer-term grant support, and a bigger chance of winning prestigious prizes.

To test this hypothesis requires empirical investigation. For example, matched cohorts of the best UK and US scientists could be interviewed and compared in terms of their career choices, scientific ambitions and their perceived incentives. We predict that the best US scientists would demonstrate a stronger orientation towards working in revolutionary science than would the best UK scientists. The position, pay and conditions of successful revolutionary scientists over recent decades could be compared with the most successful normal scientists. We predict that in the USA the rewards for revolutionary science were relatively greater compared with normal science than in the UK.

Is the decline of the UK in revolutionary science a genuine cause for concern We believe it may be. The whole scientific world benefits from US achievements in revolutionary science, but the sheer scale of US dominance in revolutionary science may contain the seeds of its own destruction. Since the short term incentives will always favour normal science, there seems to be a potential danger of lack of international competition eventually leading to declining US standards of revolutionary science in the long term.

We suspect that over recent decades the UK has become an increasingly-efficient factory for producing normal science at a high quality and volume. But apparently the UK no longer specializes in revolutionary science in the way that it did until recent decades; and the UK now mainly serves as an incubator of talented personnel who must usually transfer to the US to fulfil their scientific potential. To regenerate the UK as a base for revolutionary science would probably require increasing the incentives that would reward success in revolutionary science, thereby encourage greater scientific ambition and risk-taking.

Acknowledgement

Thanks are due to Neil Herald for his work on the analysis of the top-20 UK university production relative to the US.

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