Discouraging Hypotheses Slows Progress

If Einstein had been a biomedical scientist in the last part of the 20th century, he probably would have died without publishing anything and without making any contribution to science. Einstein was an entirely theoretical scientist: He never did an experiment and showed no interest in conducting experiments personally. The journal referees would have said that he had no experience in the field and that his ideas were mere speculations. Could biomedical science be losing Einsteins and near-Einsteins because of its practitioners' absurd attitudes toward hypothesis and theory? All recent studies on the history and philosophy of science have emphasized that hypotheses and theories always come before observation and always condition what will be observed. The idea that scientists observe in a theoretical vacuum and only then incorporate their observations into a hypothesis or theory has been utterly discredited. All observations are theory-laden, and what is observed will always depend on the hypothesis held by the observer. Paradoxically, those most in thrall to theory are those who deny its importance: They fail to recognize that their own observations are dependent on the theories they hold. Take one very simple example of which I have just become aware. In the late 18th and early 19th centuries one theory of brain organization held that the convolutions of the cerebral cortex were expressions of individuality and hence could exhibit no consistent pattern from person to person. Otherwise reliable observers carefully studied series of human brains and noted this lack of pattern. Their theory prevented them from seeing what was before their eyes; namely, that while the convolutions differ in detail, their overall pattern is remarkably consistent. The concept of the dependence of observation on theory is thoroughly understood in physics, chemistry, and related sciences. In these fields there is a balanced and creative tension between hypothesis and theory on the one hand and experiment on the other. It is recognized that discovery in science almost always begins either with a hypothesis or with an observation that can be seen to be anomalous against the background of a clearly defined theoretical construct. It is also recognized that while occasional scientists may be equally good at hypothesis and at experiment, this is not true of the vast majority. Most are much better at one than at the other. The contributions of both sides are honored, and progress is known to depend on the contributions of both. While theoreticians and experimentalists not infrequently make snide comments about each other, neither states that the efforts of the other are worthless. Advances depend absolutely on this creative tension. Hypothetical and theoretical papers are readily published, even when written by those who have never done an experiment in their lives. Progress would slow drastically if no one was allowed to hypothesize. The situation in biomedical science could hardly be more different. Theoretical papers of any sort are almost impossible to publish unless carefully disguised as reviews. It is even difficult to get theoretical comments into the discussion sections of experimental papers. Almost all imaginative scientists have at some time received a ref-eree's report that says something like: "The discussion is too speculative and much of it should be eliminated." Scientists who have never done any experimental work in a field are almost absolutely precluded from publishing any theoretical work in that field. To future historians of biomedical science, the behavior of the discipline in the second half of the 20th century will be seen as absurd. We treat ideas in the absence of observations, or ideas that are proposed on the basis of other people's observations, as pornography--something that might corrupt the innocent children of the scientific world and that must not be allowed to see the light of the day. There is an inexplicable fear among mainstream scientists that if such ideas are published they may infect science. That attitude can only be an indication of deep malaise in biomedical science, of an inchoate, unexpressed fear that the theoretical structures are so lacking in robustness that they could be brought crashing down by a stray idea. There can be little doubt that physics and chemistry would be crippled if they followed the publication practices of the biomedical sciences. What are we in medicine missing by our attitudes to theory and hypothesis? * We, more than any other scientists, labor under the misapprehension that our observations are theory-free. Because we are so little conscious of theory we fail to develop coherent underlying concepts against which our observations are clearly tested. Biomedical science may be more complex than physics and chemistry and therefore a more difficult field in which to theorize. But if we do not try we shall certainly not succeed. * We have no tradition of analytical criticism of existing theoretical concepts. As a result, general beliefs persist within the biomedical community long after the evidence is available to destroy them. * We deprive our science of perhaps its major source of innovation, the ideas of scientists who may not be very good experimentalists in that field, or who may not be experimentalists at all, but who nevertheless are capable of spinning off a myriad of new concepts. Why do we cripple ourselves in this way? I confess that the answer is beyond me, but here are some possibilities. The first is that we think biomedical science is too complex for a coherent theoretical base to be established. This is a recipe for continuing failure and is based on the misguided notion that a theoretical structure in science is supposed to be "right." No scientist with any humility could ever pretend that any theoretical structure is anything more than a way station on a road to an unattainable end. But it should be a statement that describes with clarity our present position and that makes testable predictions. Complexity is no excuse for avoiding the duty of thinking with clarity. Another possibility is that most established scientists do not actually want to make rapid progress. A state of atheoretical confusion is agreeable to them because in that state almost nothing can ever be shown to be wrong. Atheoretical biomedicine is a relatively risk-free world because its absence of precision ensures an absence of real failure. Related to this fear of failure is the fact that what most scientists want out of life is to be hailed as the originator of a new scientific concept. But most biomedical scientists are simply incapable of generating new ideas and feel threatened by those who can. They feel more comfortable in a world in which theory and hypothesis are not respected because the development of concepts is an ability they do not have. I suspect that the near failure of biomedical science to understand the central importance of ideas has been partly responsible for our relative failure to improve medical care. We like to trumpet our successes, but the fact is that in the field of treating common diseases we are little better off then we were in 1960. Death and illness are enormously more expensive and are documented by ever-increasing tests and diagnostic techniques, but the sad fact is that most people die of much the same diseases at much the same ages as they did in 1960. The same could certainly not be said of the difference between 1930 and 1960, when, in spite of trivial expenditure on research, progress was considerable. Something has gone sadly astray. It was against this background that in 1974 I set up Medical Hypotheses, a journal devoted to ideas and criticism of ideas in biomedical science. The aim was to provide a forum in which authors could criticize existing theories and develop new ones without having to report at the same time the results of experimental observations. The journal gave researchers the opportunity to develop those discussions of experimental work that other journal referees dismissed as too speculative. It also gave nonexperts the opportunity to present and develop ideas relating to fields in which they had done no experimental work. I approached several publishers with the idea, but none was interested. They all thought that the concept was too dangerous to be successful. On the other hand, I did receive support from some of the most eminent scientists, who had a better grasp than most of the importance of theories and ideas in medicine. Arthur Guyton and Linus Pauling gave strong support from the beginning. So also did John Eccles, Macfarlane Burnet (since his death replaced by James Black on the editorial board), and Karl Popper. Their enthusiasm encouraged me to take the risk of publishing the journal myself, though I am happy to say that five years later the publishing task was taken over by Churchill Livingstone, with whom I now have a happy relationship. When refereeing papers for Medical Hypotheses, we are looking for different things than those sought in the average experimental paper. First, we want to know whether the idea is interesting and stimulating. Secondly, we want the idea to be expressed in a way that relates it to the existing body of knowledge, thus building a bridge to current concepts in the field. Thirdly, we want the idea to be presented in a way that makes it accessible to as broad a group of biomedical scientists as possible. We are totally uninterested in whether the idea is "right": we do not think that is an appropriate criterion for an idea. The "rightness" can be judged only after exposure to the comments of many others and to the test of experiment. We want to inject change and progress into science, not to maintain the status quo. In one sense my dearest wish is that the need for Medical Hypotheses should disappear because of a major change in the attitudes of other journals to the publication of new ideas. Unfortunately, I suspect that it will be a long time before such a change takes place in biomedicine. Endocrinologist David Horrobin is research director at Efamol Research Institute in Kentville, Nova Scotia, and editor of Medical Hypotheses.

Discouraging Hypotheses Slows Progress

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