Wednesday 23 December 2009

David Horrobin's inaugural editorial 1975

[NB: Here is a Christmas meditation from founding editor David F Horrobin on the role and functioning of Medical Hypotheses, as it has existed for the past 34 years - but probably not for very much longer. I doubt whether the real Medical Hypotheses, run on Horrobin's principles, will survive 2010. As Horrobin's successor, the ideals described in his inaugural editorial are the ideals I strive to maintain. As he instructed me, this type of journal can only in practice be run by the editor choosing papers himself (not by delegating decisions), and by his taking responsibility for these choices. This is the traditional sceintific method of editorial review, and entails eschewing the bureaucratic timidities and inefficiencies of mainstream peer review. Horrobin's conviction was that there were two lynch pins of Medical Hypotheses as he founded and maintained it: 1. aiming to publish revolutionary ideas, even when they 'seem improbable and perhaps even faintly ridiculous'; and 2. using editorial review in pursuit of this aim.]


Ideas in biomedical science: reasons for the foundation of Medical Hypotheses

David F. Horrobin, (1939–2003) Founder and first editor of Medical Hypotheses

Adapted from the inaugural editorial which appeared in the first issue of Medical Hypotheses (1975) 1(1), 1–2. Re-published in the first issue edited by Bruce G Charlton - Medical Hypotheses, Volume 62, Issue 1, January 2004, Pages 3-4

It is at least arguable that too much biomedical research is published rather than too little. Why then start a new journal?

Scientific progress depends on the existence of creative tension between ideas and observations. An observation is made which cries out for explanation. A hypothesis is proposed to account for this observation. The hypothesis is tested by making more observations which almost invariably require the abandonment of some part of the hypothesis. A new hypothesis is proposed. And so on…

The physical and chemical sciences long ago recognized that observations are not superior to hypotheses in generating scientific progress nor are hypotheses superior to observations. Both are necessary. While the ideal research worker may be one who is equally able to generate hypotheses and to test them experimentally, these sciences also recognized that such paragons are very rare indeed. Most scientists are much better at either one or the other activity. In physico-chemical fields this is fully accepted and the contributions of both theoretical and experimental scientists are recognized.

In contrast, in the biomedical sciences there seems to me much ignorance of the way in which scientific advance actually occurs. Physical scientists often dismiss biology and medicine as backward and the biologists quite legitimately react by pointing out that they are usually dealing with much more complex phenomena. But I have a suspicion that there is some truth in what the physical scientists say and that biology and medicine are backward because they have relied almost exclusively on observation. They have failed to recognize adequately that observation is always more effective when disciplined and channelled by hypothesis.

Many journals will occasionally publish a theoretical paper from a scientist with an outstanding reputation but will not consider similar papers from relative unknowns. The rule that is almost universally applied biology and medicine is that ideas can be presented or criticized only by those with a record of experimental work in a field. Even then they must be kept strictly to the discussion sections of papers and their presentation must usually be rigorously curtailed because ignorant and pedantic referees and editors object to ‘unjustified speculation’ and complain that the discussion ‘goes beyond the observed facts’. It is hardly surprising that the best physicists and chemists find medicine and biology primitive and unsophisticated.

The situation seems to be to be a tragedy. It leads to a total misrepresentation of the way in which science actually takes place. In 10,000 years time, a historian who had access only to the journals would be unable to build up anything like an accurate picture of what biomedical scientists actually do. This would not matter unduly but what does matter is that many scientists and most students also fail to understand how scientific advance actually occurs. As a result of this antipathy to theory the rate of progress is slowed because there is neither free presentation of new ideas nor open criticism of old ones. Outdated concepts can persist for prolonged periods because the evidence against them is scattered through hundreds of papers and no one is allowed to gather it together in one article to mount a sustained attack.

The refusal to accept the equal importance of ideas and observations leads to inefficiency. Most scientists now active in the biomedical field are competent observers whose ability to generate ideas is either naturally absent or has been stultified by the prevailing philosophy. As a result they spend their time in making more and more detailed observations of the same sorts of phenomena. In contrast, a few have far more ideas than they could possibly investigate but their potential contribution is largely nullified because they are allowed to publish only in those areas where they have done experimental or clinical work. If only these differences of ability and emphasis could be accepted and recognized then the people with ideas (who may often be inept experimenters) could generate a steady flow of new concepts which might rejuvenate the work of those whose primary skill is in observation.

Medical Hypotheses will be primarily devoted to publishing ideas and criticisms of ideas in the biomedical area. It will publish papers from anyone regardless of whether they have done experimental work in the field or not and regardless of the reputation of the authors or the institution from which they come. I shall be biased in favour of articles which clearly have some bearing on medicine. I shall try to ensure that all articles are written in a way which enables any intelligent medical scientist to obtain something useful from them. While specialization in research is essential, obscurity in the presentation of specialized ideas is not. I believe strongly in the ability of apparently unrelated fields to cross-fertilize one another and I hope that as a side result of editorial policy Medical Hypotheses may become an important medium for the continuing education of those medical scientists who have open and lively minds. There will be a correspondence column which I should like to make a major debating area as well as fun to read.

What sorts of papers will be published in Medical Hypotheses? Some will describe theories, ideas which already have a great deal of observational support; and some hypotheses, ideas where the experimental support is as yet fragmentary. Some will criticize theories and hypotheses without necessarily having anything to say in replacement. Some will discuss more philosophical aspects of the logical bases of science and of how science functions in practice. In the biomedical field I believe that ignorance of such philosophical considerations remains a serious impediment to progress.

I shall willingly and proudly plead guilty to the charge that I shall publish some ideas which seem improbable and perhaps even faintly ridiculous. Most scientists seem to be under the impression that the best hypotheses are those which seem most likely to be true. I follow Karl Popper in seeing the virtues of improbability. If a hypothesis which most people think is probably true does turn out to be true (or rather is not falsified by crucial and valid experimental tests) then little progress has been made. If a hypothesis which most think is improbable turns out to true then a scientific revolution occurs and progress is dramatic. Many and probably most of the hypotheses published in the journal will turn out in some way to be wrong. But if they stimulate determined experimental testing, progress is inevitable whether they are wrong or right.

The history of science has repeatedly shown that when hypotheses are proposed it is impossible to predict which will turn out to be revolutionary and which ridiculous. The only safe approach is to let all see the light and to let all be discussed, experimented upon, vindicated or destroyed. I hope the journal will provide a new battlefield open to all on which ideas can be tested and put through the fire.