RA Fisher, statistician and geneticist extraordinary: a personal view

Walter Bodmer

Sir Walter Bodmer, Hertford College, Catte Street, Oxford OX1 3BW. E-mail: walter.bodmer{at}hertford.ox.ac.uk

Accepted 29 May 2003

I was among the last of RA Fisher’s students and disciples and, as a result, he had an enormous influence both on my career and on my attitudes to science and scientific research. In the summer before I started taking Fisher’s lecture courses in statistical and mathematical population genetics, I was given a reading list that included Fisher’s three outstanding books, The Genetical Theory of Natural Selection,1 Statistical Methods for Research Workers,2 and The Design of Experiments.3 These formed a little light recommended reading over a summer vacation! Later in that year, I went to see Fisher in the Genetics Department about the possibility of doing research with him. I then wrote in my diary.... ‘very promising, looks as though all will be well. I hope it’s the right subject.’ Well, it undoubtedly was and has remained with me for the following 47 years, and hopefully more to come.

Fisher was very supportive of the young as is evident from Joan Box’s outstanding biography of her father.4 He was disparaging of authority for authority’s sake, and his dismissive statements about distinguished geneticists and statisticians were a lesson in appreciating scientists for their actual contributions rather than their, perhaps sometimes inflated, reputations.

Towards the end of January 1956 I went to see him to get his support for applications for a research studentship stipend to do my PhD with him, starting later that year. In my diary I wrote, ‘He is a nice man. I should almost say "sweet". Went for a long walk with him in pouring rain and talked. Then he dictated two rather good letters applying for a grant for me.’

This was characteristic of his charm and concern for those he wished to help. And yet, as Joan Box says in her biography:

He seemed inhuman sometimes in his lack of consideration for the feelings of others.... Capable of rough handling those who opposed him with ready-made arguments that he treated with contempt: He was sometimes arbitrary and disagreeable: and he was recalcitrant to any form of coercion. (ref. 4, p. 430)

It is this complexity of his character that needs to be understood in order to interpret his relations with other scientists, and so sometimes his attitude to scientific viewpoints that did not coincide with his own.

Fisher is often portrayed as the supreme theoretician and analyst, without reference to his concern for practical applications, which he instilled in his students, including myself. This is a serious misapprehension, as the vast majority of his theoretical work was, as he himself often emphasized, devoted to an understanding of how to deal with real experimental data. He, for example, collected data in the field on the three forms of the primrose, Primula vulgaris, a subject that in the end formed a major part of my initial research in genetics under his guidance. Fisher remained throughout his life a keen observer of the natural world.


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Fisher’s conciseness and obscurity in some of his statistical and mathematical writing are legendary. In my exam at the end of my third year Fisher set a question on interpreting inbreeding by alternate parent offspring matings using his novel approach to handling problems in inbreeding, the theory of junctions. I made a vain attempt to answer the question as I felt I should, but was completely stumped. Later I asked Fisher’s colleague, ARG Owen, who was a lecturer in the department, what Fisher had intended. He said he had tried to dissuade Fisher from setting the question, and when he asked what sort of an answer was expected Fisher came back a few days later with three closely written pages of algebra! WS Gosset, the ‘Student’ of student’s t-test whom Fisher greatly admired, once wrote in a comment on Fisher’s writing, ‘when I come to "evidently" I know that it means two hours hard work at least before I can see why’.5

And yet at times, especially when explaining essentially non-mathematical concepts, he could be a model of clarity, as exemplified most famously in his discussion of the tea tasting experiment as described in The Design of Experiments.3 He there used as a model experiment the attempt to establish whether a lady could discern whether milk had been added to the cup before or after the tea.

Fisher was a proud man in addition to his sensitivity, and this undoubtedly explained some of the antagonistic interactions he developed with scientific colleagues. Notable among these, and sadly, was the antagonism that developed with one of the other great founders of population genetics, Sewall Wright. Wright’s review of Fisher’s The Genetical Selection was extremely positive [4,11] and Fisher acknowledged that Sewall Wright may be one of the few people who could really understand what was in his book. However, Sewall Wright picked up a minor arithmetical error in one of Fisher’s transformations, a missed factor of two, and this I believe was the basis of the antagonism that eventually developed between them.


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Statisticians and those who know of Fisher largely through statistical applications often do not appreciate that Fisher’s contributions to genetics were in many ways as original, revolutionary, and important as his contributions to statistics. He founded the field of population genetics, together with Sewall Wright and JBS Haldane. Many a terse paragraph in his classical work The Genetical Theory of Natural Selection,1 a true successor to Darwin’s The Origin of Species, has been the basis for a whole new field of experimental and theoretical analysis. An example of this was his description of a model involving selective interactions between alleles at two linked loci that could favour closer linkage between the genes, a field to which I first contributed in the early 1960s and which became a major interest of mine.5 This is now the basis for the whole excitement about the way that the almost unlimited number of polymorphisms detectable at the DNA level can be used in the attempt to analyse the specific genetic basis for multifactorial disease susceptibility in human populations.

His interests in genetics paralleled those in statistics from a very early age, following perhaps from his reading of Darwin’s work as a schoolboy. He was an active member of the Eugenics Society as a student in Cambridge. In the same year, 1922, for example, in which he published his monumental work On the Mathematical Foundations of Theoretical Statistics6 he also published his paper On the Dominance Ratio,7 in which he derived for the first time the classical result that, in a one locus two allele system, heterozygote advantage leads to a stable balanced polymorphism. His interests in genetics and statistics did not, however, develop independently but interacted strongly with each other. The most notable of these interactions was the use of the word ‘variance’ and the development of the analysis of variance, and the stimulus for the ideas for factorial experimentation.

His first substantial, and indeed seminal paper on genetics was that on The Correlation Between Relatives on the Supposition of Mendelian Inheritance.8 The paper opens with the sentence, ‘Several attempts have already been made to interpret the well-established results of biometry in accordance with the Mendelian scheme of inheritance’. That is indeed what this paper achieved. On the first page just a few sentences further down he says:

It is therefore desirable in analysing the causes of variability to deal with the square of the standard deviation as the measure of variability. We shall term this quality the Variance of the normal population to which it refers, and we may now ascribe to the constituent causes fractions or percentages of the total variance which they together produce.

Here in one sentence was the introduction of the word variance as it is now commonly used in statistics, and of the notion of the analysis of variance. This paper has an interesting history. It was first submitted for publication to the Royal Society of London some 2 years earlier, but rejected. It was eventually published by the Royal Society of Edinburgh through the intervention of Leonard Darwin, Charles Darwin’s youngest son and a strong influence and mentor of Fisher’s, who paid £50 towards the cost of the paper’s publication. Fisher later learnt that the referees were Karl Pearson, then Galton Professor of Eugenics at University College, and RC Punnett, the Arthur Balfour Professor of Genetics in Cambridge. He delighted to recount, as I heard him say myself, that these two rejected his paper, ‘both of whom I later succeeded’.

In his Bateson Lecture, delivered in 1951, Fisher made clear the fact that his ideas on factorial experimentation had been stimulated by his knowledge of genetics. The title of the lecture was Statistical Methods in Genetics.9 He said:

And here I may mention a connection between our two subjects which seems not to be altogether accidental, namely that the ‘factorial’ method of experimentation, now of lively concern so far afield as the psychologists or the industrial chemists, derives its structure, and its name, from the simultaneous inheritance of Mendelian factors.


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Fisher’s interests in randomization, and the development of his ideas on the design of experiments, grew out of his first appointment as a statistician at the Rothamsted Experimental Station. He was initially to spend 6 months or so there to find out whether useful analyses could be made of the extensive data on crop yields that had been obtained at Rothamsted over many years. The first specific explanation of the principle of randomization published by Fisher was in the first edition of Statistical Methods for Research Workers in 1925.2 Fisher said:

The first requirement which governs all well planned experiments is that the experiment should yield not only a comparison of different manures, treatments, varieties, etc., but also a means of testing the significance of such differences as are observed.

He then later says:

For our test of significance to be valid the differences in fertility between plots chosen as parallels must be truly representative of the differences between plots with different treatment; and we cannot assume that this is the case if our plots have been chosen in any way according to a pre-arranged system; ... The direct way of overcoming this difficulty is to arrange the plots wholly at random.

Thus, from this initial exposition of the principles of randomization it is clear that Fisher places an overwhelming emphasis on the need for randomization in order to obtain valid estimates of error so that a proper test of the significance of the effects of different treatments can be made.

An extension of Fisher’s ideas on randomization, again emphasizing the need for valid estimates of error, but in an exemplary clear way without any use of formulae, was his classic paper on The Arrangement of Field Experiments.10 This was published in 1926 in the Journal of the Ministry of Agriculture as a rebuttal to his Director, Sir John Russell’s, advocacy of systematic designs. In this paper Fisher explains with great clarity the idea of using a 5% significance level, what is a variance, that the main purpose of replication is to provide a valid estimate of error and, as he puts it:

One way of making sure that a valid estimate of error will be obtained is to arrange the plots deliberately at random, so that no distinction can creep in between pairs of plots treated alike and pairs treated differently.

He also introduces the idea of blocks and randomization within blocks, gives an example of Latin squares, and emphasizes his view ‘... that large and complex experiments have a much higher efficiency than simple ones’. This is in line with his advocacy of factorial experimentation.

Fisher’s ideas on experimental design and randomization and its applications were greatly enlarged in his book The Design of Experiments,3 the first edition of which appeared in 1935. It is perhaps only here that he first indicates clearly how randomization may avoid bias in his comment that:

... for the full procedure of randomisation, by which the validity of the test of significance may be guaranteed against corruption by the causes of disturbance which have been eliminated.

Thus, in effect, his view appears to be that randomization to provide a valid estimate of error on the one hand, and to eliminate biases on the other, are really two sides of the same coin.


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It seems sometimes to be assumed that, because Fisher did not apply his ideas on randomization and experimental design to clinical trials, he had no interest in the analysis of human data. Nothing, of course, could be further from the truth. His major interests were in the experimental possibilities that were opened up by blood group serology, and the possibilities of using genetic polymorphisms to analyse patterns of inheritance of diseases in families. Fisher had had his attention called to the genetical interest of serological studies by JBS Haldane. His correspondence4,11 with the serologist, Todd, reveals that he was the first to suggest that the antigens detected by serological agglutination assays may be ‘the direct products of individual genes rather than have secondary reactions’. He suggested a wide variety of experiments to Todd, and expressed his impatience with the slow rate at which the experimental results were produced. Fisher had an enormous influence on the development of blood group research in Britain, stimulating the pioneering researches of Rob Race and Ruth Sanger with their Medical Research Council support. He formulated an extraordinarily imaginative interpretation of the Rhesus blood groups and it was perhaps largely through the stimulus of this that I came to my work, with my late wife, on the human leukocyte antigen (HLA) system. Fisher indeed gave up work on human biometrical genetics because he believed that the development of the serological work:

... is going to lead to a greater advance, both theoretical and practical, in the problems of human genetics than can be expected from any further work on biometrical or genealogical lines.

Fisher’s other great contribution to practical human genetics was his analysis of linkage in human pedigrees, which paralleled that of JBS Haldane. In a remarkable note given, strangely, at an International Congress on Life Assurance Medicine in 1935, entitled Linkage Studies and the Prognosis of Hereditary Ailments,12 he effectively anticipated what is now called positional cloning. Thus he said:

It is therefore of great importance that these linkage groups should be sorted out, in order that common and readily recognisable factors may be used to trace the inheritance and predict the occurrence of other factors of greater individual importance, such as those producing insanity, various forms of mental deficiency, and other transmissible diseases.

He realized the power of using polymorphisms in human families for linkage analysis, but could not then have been aware of the extraordinary possibilities that have opened up more recently through our knowledge of the human genome. This has led to the uncovering of essentially unlimited numbers of polymorphisms sufficiently close to each other to enable accurate linkage analysis, and so the identification of gene mutations that underlie genetic disease, simply from genetic linkage analysis in families.5

I wonder whether the puzzling fact that the ideas of factorial experimentation have hardly penetrated into clinical trials was ultimately due to Fisher’s own lack of interest in this area. Fisher’s message that factorial experiments can give you much more information, including that on interactions, than simple one-factor experiments seems not to have been heeded by the medical trialists. On the other hand, perhaps it was Bradford Hill’s understandable emphasis on simplicity and pragmatism in carrying out randomized clinical trials, in order to capture medical interests, which led to this lack of application of the principles of factorial experimentation in clinical trials.


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Correspondence clearly indicates that Fisher and Bradford Hill remained on friendly terms until well after the publication in 1937 of Bradford Hill’s celebrated book on The Principles of Medical Statistics.13 In my, all too brief, contact with Bradford Hill, I became aware of the extent to which he appeared to be bemused by his relationship with Fisher and not in any way antagonistic to him.

It is clear that from their earliest interaction in the 1920s, Fisher was positively supportive of Bradford Hill. He had offered to put him forward for election as a Fellow of the Eugenics Society and then about 2 years later, offered him a position at Rothamsted. The fact that Bradford Hill turned the offer down did not, apparently, influence their relationship. Bradford Hill congratulated Fisher on his appointment as Galton Professor at University College, and in doing so said:

I shall look forward to having you within a stone’s throw (though I hope it will never come to that!) and within reach when my statistical woes are too much for me, and your mathematics defeats me (which is invariable).

Herein clearly lies a clue as to their fundamental difference of character. Bradford Hill was the pragmatist and clearly considered Fisher a theoretician whose mathematical powers were well beyond his comprehension. Bradford Hill must have read the first edition of Fisher’s Statistical Methods for Research Workers and could not have failed, therefore, to have become aware of Fisher’s arguments for randomization. It is intriguing that in a letter of 8 April 1937, he tells Fisher of his intention to publish a book:

... on elementary statistical methods as applied to medical statistics, in a probably vain attempt to put them in words of one syllable for the benefit of the kind of medical graduate we have to struggle with here.

He ends the letter by saying:

I do not think for a moment it would encroach on your sales as your audience is far more erudite than any I hope (or deserve) to attract.

Fisher in his reply (9 April), while happily giving permission for Bradford Hill to use the {chi}2 table that he wished to use in his book, opens by saying:

You are mistaken about the erudite character of the buyers who have made Statistical Methods a successful book. They are practical men who want handy methods simply explained. I regard the legend that it is an advanced book as an injurious one, put about carelessly by some, and deliberately by others.

Bradford Hill and Fisher’s relationship remained friendly, and indeed became more so, over the subsequent years. In March of 1952 it was Bradford Hill who informed Fisher that he had been nominated the next President of the Royal Statistical Society, ironically to succeed Bradford Hill himself. In a letter from Fisher to Bradford Hill, towards the end of 1955, in response to his suggestions about responding to a Royal Statistical Society Presidential address, Fisher writes:

I have never developed the technique ... of delivering a savage attack disguised as a vote of thanks, and I do not particularly wish to try my hand at this sort of artistry.

This is perhaps a somewhat ingenuous comment considering how acerbic could be Fisher’s attacks on those with whom he did not agree, perhaps a foretaste of their later relationship.4


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It is clear from the correspondence starting towards the end of 1958, that the relationship between Fisher and Bradford Hill soured as a result of Bradford Hill and Doll’s studies on the relationship between smoking and lung cancer. Fisher’s attack on Bradford Hill arose not from any intrinsic animosity, indeed quite the opposite, but at least in part because of his libertarian views as applied to the then smoking and lung cancer controversy. He himself was an inveterate pipe smoker, but did not, to my knowledge, smoke cigarettes.

Fisher’s antagonistic response to the data on the relationship between smoking and lung cancer was influenced by two strong beliefs. The first, and perhaps foremost, came from his firmly developed views on the nature of statistical and scientific inference. Correlation must not be taken as proof of causation. He thus sought common causes such as genetic factors, but without at the time really being aware of the strength of the association and the unlikelihood of it being due to a common cause rather than a direct effect. His second response was based on his libertarian views. He believed strongly that people should be left freely to come to their own conclusions and simply be given the data. He was strongly against the publicity that was put out about the dangers of smoking. In an article for the Centennial Review published in September 1959,14 he talks about:

... an annotation published by the British Medical Association’s journal, leading up to the almost shrill conclusion that it was necessary that every device of modern publicity should be employed to bring home to the world at large this terrible danger.

He was perfectly happy for individuals to make their own decisions that they should consider giving up smoking, but this in the absence of what he considered convincing data of a causal effect. Many have accused Fisher of a conflict of interest in these arguments because in 1956 he had already accepted the invitation of the tobacco manufacturers standing committee to be their scientific consultant. However, as Joan Box points out in her biography, Fisher was naive enough to believe that he was free to give advice in whatever way he wanted and that receiving payment for so doing should not influence the nature of this advice.


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Are randomized clinical trials always needed when testing a new therapeutic modality? When antibiotics were first introduced, and patients survived following infections that had previously almost always led to death, was there really a need for a randomized trial? A more recent example would be the success of kidney dialysis and transplantation. The clinical trials were then not whether or not to transplant, but how to do it.

I believe that both Fisher and Bradford Hill were well aware of this issue. Thus, in his 1926 paper on The Arrangement of Field Experiments10 Fisher says at one point ‘... nevertheless if he had only ten previous year’s records he might still make out a case, if you could claim that on the uniform treatment, the difference had never come near to 10%’. This effectively sounds like an argument for the appropriate use of historical controls when an effect is sufficiently large that it is unlikely to be due to the biases that could be involved in historical comparisons, in the absence of randomization. Likewise, Bradford Hill on page 7 of his book on The Principles of Medical Statistics writes, ‘if the results of such a measure are dramatic in the light of all past experience, then clearly the trial period will not need to be prolonged’.13 This was written in the context of discussing a clinical trial on the serum treatment of lobar pneumonia.

There will, as a result of the application of our knowledge of the human genome, be an enormous variety of possible treatments, often applied to a much narrower range of disease. There then will simply not be enough patients, or resources, to subject all promising treatments independently to randomized clinical trials. And yet, arbitrary decisions on which treatment should be given an extensive trial may easily miss those treatments that are destined to be most successful. I therefore believe that, firstly, in making the choice of treatments to be tried on patients more emphasis must be given to appropriate pre-clinical animal models, (which can now be much more sophisticated using, for example, mouse transgenic technology), and to an intrinsic biological understanding of the likely mechanism of action of any agent or procedure. Secondly, I believe that it will be necessary to heed Fisher’s advocacy of complex multifactorial experiments so that several treatments can be evaluated at the same time with higher efficiency, and with the added bonus of exploring potential interactions. Thirdly, I believe that it will be necessary to do smaller initial studies which may involve only limited randomization, but which will depend on an appropriate choice of perhaps several sets of historical controls. Then, only those treatments giving an indication of large effects in such limited studies will be the ones that are subsequently submitted to randomized controlled clinical trials. But this must be with the strong proviso, as advocated by Bradford Hill himself, that as soon as there is an obvious level of efficacy observed, alternative forms of trial, for example, based on dosage escalation but at a Phase II/Phase III level, need to be considered.


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The last time I saw Fisher was when he visited Stanford University in September 1961 on his way back to Adelaide, Australia. He had proposed as the topic of his planned seminar the theory of junctions in inbreeding and sadly I was too timid to suggest that this would be of limited interest and that perhaps he should give a talk on his views on smoking and lung cancer. However, my diary notes ‘there was a big audience for seminar on junctions, far too specialised for most of them’. I took Fisher to the airport the following evening. In waiting for check-in we got into a lively discussion about a test I had devised for two extreme deviates in a set of proportions. As time went by I suddenly realized that the plane was soon to leave, and in a panic, went to the check-in desk to explore the situation. But it was too late. The great man had missed his plane and I was mortified. He, however, was not! He took it in his stride, stayed another day with us, which we spent going around San Francisco, and this time he did not miss his flight. But our older son to this day remembers Fisher’s kindness and friendship and the description of how he was knighted by the Queen. Those last 3 days I had in his company illustrated both the complexity of personality and the greatness of this extraordinary scientist.


    Acknowledgments
 
Access to Fisher’s papers at the University of Adelaide, Australia was made available by the Special Collections librarian of the Barr Smith Library.


    References
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 Fisher’s personality
 The interplay between...
 Randomization and experimental...
 Fisher’s interests in...
 Fisher’s relationship with...
 Smoking and lung cancer
 The need for randomized...
 Envoy
 References
 
1 Fisher RA. The Genetical Theory of Natural Selection. Oxford: Clarendon Press, 1930.

2 Fisher RA. Statistical Methods for Research Workers. Edinburgh: Oliver & Boyd, 1925.

3 Fisher RA. The Design of Experiments. Edinburgh: Oliver & Boyd, 1935.

4 Fisher-Box J. RA Fisher: The Life of a Scientist. New York, Chichester, Brisbane, Toronto: John Wiley & Sons, 1978.

5 Bodmer WF. Genetic sequences. Proc Roy Soc 1990;241:85–92.[ISI]

6 Fisher RA. On the mathematical foundations of theoretical statistics. Philos Trans 1922;222:309–68.

7 Fisher RA. On the dominance ratio. Proc Roy Soc Edinb 1922; 42:321–41.

8 Fisher RA. The correlation between relatives on the supposition of Mendelian inheritance. Trans Roy Soc Edinb 1918;52:399–433.

9 Fisher RA. Statistical methods in genetics. Heredity 1952;6:1–12.[ISI]

10 Fisher RA. The arrangement of field experiments. J Ministry of Agriculture Great Britain 1926;33:503–13.

11 Fisher RA. In: Bennett JH (ed.). Natural Selection, Heredity and Eugenics. Oxford: Clarendon Press, 1983.

12 Fisher RA. Linkage Studies and the Prognosis of Hereditary Ailments. International Congress on Life Assurance Medicine, London, 1935.

13 Bradford Hill A. Principles of Medical Statistics. London: The Lancet, 1937.

14 Fisher RA. Cigarettes and cancer. Centennial Review 1959:60–66.





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