Fisher and Bradford Hill: a discussion

Edited transcript of discussion (chaired by Iain Chalmers) following presentation of papers by Peter Armitage, Richard Doll, Harry Marks, and Walter Bodmer at the session on ‘Fisher and Bradford Hill: theory and pragmatism?’, 5 September 2002, Osler-McGovern Centre, Green College, Oxford.

Kay Dickersin: I have heard Bradford Hill referred to in two different ways: as Hill and Bradford Hill. I was with Iain when he specifically asked Bradford Hill what his last name was so he could put it correctly in the index under either B or H. I know what he said, but would you guys tell me what you think his name is?

Peter Armitage: His name undoubtedly was Hill. His father gave him the name ‘Bradford’ after a colleague of his father’s whom his father admired. But of course it was never used when he was young. He was called Hill to start with during his career, but during the 1920s there was a distinguished physiologist at University College called AV Hill, and AB Hill tended to get confused with him. So he then adopted the double name Bradford Hill, but without a hyphen. He was usually called Bradford Hill but, on the other hand, he always used Hill in publications—Hill, AB.

Benjamin Djulbegovic: Apparently the first trial carried out by Bradford Hill did not have, as I understand it, a built-in threshold for the rejection or acceptance of the null hypothesis. When was the first randomized trial that used a threshold decision rule?

Iain Chalmers: Good question—I don’t know the answer. Does anyone here know the answer to that?

Walter Bodmer: Well I suppose this is essentially a question of when people started thinking about power considerations—thinking about an alternative hypothesis which it was important not to miss and the requirement of a high probability of achieving that—which then led to the sample size. I don’t know the answer.

Ian Roberts: Can I ask Sir Richard about the streptomycin trial? There wasn’t enough streptomycin to go around. Earlier this morning Iain Chalmers spoke about lots having been used when there’s not enough of something, or when there’s either something bad to be dished out, or something good to be dished out and there isn’t enough of it. To what extent did that rationing situation, in your opinion, influence the choice of randomization as the method of allocation in the streptomycin trial?

Richard Doll: It merely influenced the decision that there should be a trial. Randomization was introduced in order to ensure the avoidance of selection bias. There was quite a bit of streptomycin about, but the British government couldn’t afford it. It was very expensive and there was a very limited amount of money they were prepared to spend on it, so the first supplies went to patients with tuberculous meningitis and miliary tuberculosis. There was so little left over after that that it was feasible and ethical to do a controlled trial. But the randomization was a secondary issue, as a means of avoiding selection bias.

Iain Chalmers: Sometimes it was bought privately. One famous example is George Orwell, whose book sales in the United States meant that he had US dollars with which to purchase the drug.

Andrew Herxheimer: Listening to what you all said about Bradford Hill and Fisher, I was wondering whether the choice of medical topics by Bradford Hill and the avoidance of medical topics by Fisher might be related to the fact that that Bradford Hill had been very ill, with tuberculosis. Was Fisher a very healthy person?

Walter Bodmer: Fisher did not avoid medical topics. Blood groups are a highly important medical topic.

Andrew Herxheimer: Therapeutic topics?

Walter Bodmer: Is dealing with haemolytic disease of the newborn not a therapeutic topic? I don’t think it’s fair to say that Fisher didn’t have an interest in medical topics. He didn’t have an interest, as far as one can tell, in the specifics of drug trials; but he had a major interest in the analysis of human data and medical areas.

Andrew Herxheimer: I’m just comparing his attitude with Iain’s attitude—having a medical card saying—‘Randomize me’. Would Fisher have ever thought of such a thing? He was not interested in treatment, primarily. He wasn’t curious about treatment, was he?

Walter Bodmer: I wouldn’t know about that. Fisher was an extraordinarily knowledgeable individual. For instance, many people think he was an extraordinarily good naturalist. I can’t believe that he didn’t have some knowledge of and interest in treatment.

Andrew Herxheimer: Did he have any serious illness or was there some in his family?

Walter Bodmer: His daughter turned out to be Rhesus negative. He had his family tested, and his daughter made having the right blood group a condition of marrying her husband. Fisher was extremely short-sighted, but I don’t know about other ailments. He was not, until his last illness, a particularly unwell person.

Doug Altman: Can I come back to the streptomycin trial because something has been said today that has bothered me before. Richard, you stated that it was deemed ethical to do the trial because streptomycin was in limited supply. The corollary of that is that had the supply not been limited, there would not have been a trial. That implies that there was strong evidence of effectiveness beforehand. Even if the stuff was limited, one does wonder if nowadays we would still have the same attitude to doing a trial—a randomized trial—in that way.

Richard Doll: The evidence was not quite as strong as the sulphonamides in the treatment of puerperal fever. But I think it was sufficiently strong to have inhibited anyone doing a trial if they’d had enough material to treat all their patients. If that had been the case, it would have been very unfortunate in terms of finding out about the long term effects of streptomycin. Subsequently, as you know, adding all sorts of other chemicals had to be tried. It was not so easy to work out the best combination of chemicals for the treatment of tuberculosis. It might have been much more difficult to introduce controlled trials to test those combinations than it was in the initial study of streptomycin. But if there had initially been enough of the drug, I don’t think for a moment, they’d have run a trial of it.

Iain Chalmers: Could I ask a related question? It’s been suggested to me that the auditory nerve damage caused by streptomycin was picked up with confidence within the randomized trial. Is that your memory, Richard? Is that anyone else’s memory?

Richard Doll: Yes.

Harry Marks: I don’t know about the British case, but during the Second World War there were many cases in which limited supply, including of penicillin, was used as a justification for restricting drugs to research studies. In that framework, it was very much a choice of the investigators about what the appropriate way to do a study was. Sometimes you got controlled studies using the short supply as the justification, and sometimes you didn’t. But the shortage argument as a justification for investigation as opposed to just clinical dissemination was used in that period. It was extended into the post-War period in Britain because of the shortage of dollars.

Walter Bodmer: That’s a more recent phenomenon, too, with the first DNA products. The first trials with interferon, for instance, were limited by the amount available, so it was only used in research experiments.

Martin Edwards: Can I ask for some detail about who Fisher was writing for?

Walter Bodmer: I think he was read quite widely, but I don’t have any data on this—I don’t know what the sales of his books were. But you have to remember Statistical Methods for Research Workers went into fourteen editions. In its day, I think it became the standard statistical text. I don’t know about his paper in the Journal of the Ministry of Agriculture. That was a rather specialized thing; I imagine it was read by people involved in agriculture, and that it probably wouldn’t have been seen by others. But it was certainly Fisher’s intention to write for a widely interested, scientific audience—I have no doubt about that—both in Statistical Methods for Research Workers and in The Design of Experiments.

Jan Vandenbroucke: To come back for one moment to the streptomycin trial. Streptomycin was developed in the United States. It was sufficiently available in the United States, and rumour has it that there was never a controlled trial there because it was sufficiently available.

Harry Marks: Well actually, that is not correct. There were two studies in the US. One started at about the same time as the MRC study; the other a little later, probably for budgetary reasons. It was certainly published much later. The first study was the VA study. For political reasons, they felt they could not use active controls, so they used passive controls. The second study—a Public Health Service study—had active controls. It is not clear what the allocation mechanism was, but there was a clear insistence on the importance of something like a ‘fair test’ mechanism, which would not permit manipulation, and, if I remember right, blinding. That study was published in 1950, but the planning for it started in 1948 or ‘49. In the States, the initial argument was that there might not be enough of the drug to go around, and that’s why they pushed for a research study to find out how best to use it.

Jan Vandenbroucke: Given all the emphasis on randomization as the basis for inference then, what were Fisher’s thoughts about, say, inference in genetics. Studies about the associations between genetic traits and disease in humans cannot be randomized. Would he consider them as sufficiently ‘pseudo-randomized’?

Walter Bodmer: The nature of the genetic situations he was interested in didn’t involve testing treatments, but they did involve estimation. So the two areas I mentioned—blood groups and linkage in families—both were in a sense estimation problems, of frequencies and of linkage. I think the issue of randomization as it relates to trials didn’t arise there because he used his likelihood-based ideas in devising those inferences. Inference about the Rhesus blood groups was a purely logical argument from his knowledge of genetics, looking for alternatives, and it has turned out to be nearly right in terms of modern knowledge of molecular biology.

Virginia Berridge: On smoking and lung cancer, I was interested in what Sir Walter had to say on Fisher’s stance, and Harry gave us an idea of the kind of political medium within which that stance was taken. But I wonder if our other two speakers, Sir Richard and Professor Armitage, could give us some comment on their view on the significance of that debate, in particular, in relation to Fisher.

Richard Doll: Of course, it had an international significance and the tobacco industry made a very big use of it; not, I’m sure, with Fisher’s blessing, but to claim that it was a controversial subject. And that was done right up to the 1960s. From the beginning, Fisher didn’t accept the relationship, but he didn’t get really involved in attacking those that held that the relationship was causal until, as Walter said, an article in the BMJ said that every effort should be made to discourage people from smoking. That’s what made him come into the fray in the way he did.

Walter Bodmer: That’s an interesting point. That was actually the ticket for his antagonism. The other arguments developed subsequently. And I can imagine that would be the case.

Iain Chalmers: Can I press you a little bit, Richard, because I think you remember that you and Bradford Hill were the butt of a similar public attack to the one that Fisher launched at Neyman.

Richard Doll: Yes, well, I have to preface this by saying I cannot give you a published reference, although I believe that what I am saying is true, and that it was published somewhere. In the correspondence to which Walter referred, Fisher continually asked Bradford Hill for the 1950 data on inhaling, which had shown that there was a statistically significant deficiency of inhalers amongst the patients with lung cancer—just very marginal, but it was there. Fisher wanted to do more refined tests on that association; we had simply given the percentages in the paper. But by the time he was asking for the data, which was only when he became heavily involved because of the BMJ article (calling for tobacco control), we had twice as much data. And the second lot of data were pointing in the same direction. Actually it made a good deal of sense, because when we looked at the 1400 cases, we found that inhaling was positively related with cancers in the periphery of the lung and was negatively related with cancers in the large bronchi. And this was slightly different to the original report, which Fisher said should have led to the conclusion that inhaling was good for you and would prevent lung cancer.

But Fisher refused to accept the 1952 data that Bradford Hill kept on offering him. And he went so far—and this is what I have to qualify by saying I can’t give the reference—to put in writing in some publication that we were intentionally suppressing the information. I am sure this is true because I remember discussing with Bradford Hill whether this statement wasn’t one that we ought take up for libel. The accusation, in print, that we were suppressing data, was to me a very serious one. But Bradford Hill, very sensibly, said, ‘No, you don’t want to go into that sort of thing‘, and we didn’t do anything about it. Unfortunately I can’t find it, but I believe Fisher is in print somewhere accusing us of deliberate suppression of information.

Postscript, added by Peter Armitage and Iain Chalmers after the meeting: Fisher’s published allegation of deliberate suppression of information, which is clearly recalled by Richard Doll, has so far proved elusive. The publications reprodued in Fisher’s ‘Collected Papers’ do not apparently include any such allegations. Richard Doll remembers the allegations having been published in The Economist, The New Scientist, or some other journal directed at a general readership. One of us (IC) has looked at the 1957 and 1958 volumes of those publications, but was unable to uncover Fisher’s allegation.

Following two unclear words, an entry in Bradford Hill’s diary for 18 July 1957 reads ‘...v. angry over RA Fisher’, and a letter from Bradford Hill to Fisher sent on 30 October the following year (1958) reads:

‘I do not normally take notice of hearsay but I have recently been told on good authority that you are suggesting that Doll and I are deliberately "concealing" some of the data which we gathered about inhaling in our retrospective study of patients with lung cancer. That would be an extremely serious allegation and, of course, utterly untrue. We published six years ago what we considered to be of value and interest in that inquiry and since then we have provided any further information that could be extracted from the data whenever the request has come from reputable scientists. If you yourself require further information I would expect you to follow the customary procedure of reputable scientists, namely to specify what it is that you require and to ask me whether it is or could be made available. I shall await that request. Meanwhile I am reluctant to believe that such hearsay has any foundation in fact.’

A response from Fisher to Bradford Hill dated the following day begins: ‘What a stuffy letter! I thought I had given the impression that you were rather honest, though mistaken. However, if you are willing to give the data on which the results in the B.M.J. September 30th 1950 were based, I am sure it will remove any impression of concealment.’ Fisher’s letter goes on to specify the data he wishes to examine.

Bradford Hill’s reply dated 4 November concludes: ‘We will be glad to make this tabulation—and we would have made it any time in the past if we had been specifically asked for it. But any suggestion of concealment I shall continue to resist with "stuffy" letters.’

A letter from Fisher to Bradford Hill dated the next day (5 November) begins:

‘There was more than a suggestion that the original facts should be revealed when I spoke with Doll now a considerable time ago. No doubt this was not revealed to you, and I think you are old enough not to want to pose at being insulted when nothing of the kind has occurred.’

[Richard Doll (discussion with IC, August 2003) remembers only one occasion when he encountered Fisher in person, namely when the Cambridge medical students had asked them to debate the smoking and lung cancer association. Richard Doll spoke first. Fisher left the meeting immediately after giving his talk, thus not making himself available for questioning by the audience. Richard Doll remembers feeling rather vindicated by Fisher’s apparent unwillingness to submit to cross examination.]

A further letter from Fisher to Bradford Hill about seven weeks later (22 December) reads:

‘I do not know whether you have considered my letter of November 5th, or whether I am to take your silence as a refusal to supply what I asked for, and which from your letter in October one might think had only to be asked for to be received.

‘I think you ought to make up your mind as to whether you want to withhold your observational findings from publication and take the responsibility for doing so, or whether you want to allow them to be known to other scientists interested in the problem.’

On 30 December, Bradford Hill replied: ‘the tabulations had been in hand since November 5th and should be completed in the relatively near future.’ They were sent two weeks later with a letter dated 14 January, which noted: ‘The original punch cards were worn out and the tabulation has had to be made specially for you by hand sorting.’

In spite of the fact that Fisher received the data less than two months after requesting them, his 1959 pamphlet ‘Smoking: the Cancer Controversy’, not only accuses Doll and Hill of ‘timidity’ in not pursuing the inhalation question more assiduously, but also claims that it had taken ‘some years’ to elicit the tables he goes on to reproduce in his article. The records we have examined suggest that this is a mischievous misrepresentation of the facts.

Peter Armitage: When we are talking about Fisher’s character, his propensity for attacking people and so on, could I say that personally I was the recipient only of considerable goodwill from him. He was very charming to young people against whom he had no grievance, but he was really quite appalling to people of more seniority against whom he had a grievance. I was present at a meeting at the National Institutes of Health in the late 1950s in which he gave a seminar on smoking and lung cancer, among other things. He actually said there that Bradford Hill did not deserve to have been made a Fellow of the Royal Society. That seems an incredibly vicious sort of remark to me.

Walter Bodmer: It’s extraordinary given the fact that he almost certainly was instrumental in getting Bradford Hill elected to the Royal Society.

James LeFanu: Very briefly, a couple of points: back to streptomycin again. My understanding of the streptomycin trial is that its triumph was really rhetorical rather than a triumph of randomization, in the sense that it demonstrated the importance of looking at questions systematically. The most important finding of the streptomycin trial was that, although the drug worked initially, it showed that a lot of people eventually became resistant to streptomycin. Had one not looked at that question in the way that they did look at it in the trial, it wouldn’t have become nearly as clear as it did become. That then logically linked to the next trial, which studied the combination of streptomycin with PAS; and that if you added the two drugs together, then you solved the problem of resistance, or at least part of the problem of resistance. The triumph of the streptomycin trial was that its most important finding was, in a sense, a surprising one, an unanticipated one—this very high rate of resistance.

I have always found Fisher’s view on smoking and lung cancer extraordinarily perverse—and I’m not the only one. And it makes me wonder about some of his other important observations. I wonder whether Sir Richard might be able to provide insight here? By my understanding, by the mid- ’50s and ’60s, the argument was not merely a statistical one. It was that the smoking and lung cancer data were internally coherent? They made sense, every way you looked at them.

Walter Bodmer: Can I just comment? I was alive and kicking at that time, and very close to Fisher at that time. And as I mentioned, and as Richard says, I think it may have been that Fisher was stimulated to react the way he did by his libertarian views. But to criticize him the way you do is totally and utterly unfair. He never questioned the actual association, as I understood it. He questioned the interpretation of it. I think it is terribly important to realize that. He didn’t question the observation of the association. He made the formal argument that correlation was not proof of causation.

James LeFanu: My point was that it wasn’t just a simple correlation.

Walter Bodmer: What do you mean, ‘it wasn’t just a simple correlation?’

James LeFanu: Not simple in the sense that, by the late 1950s, Bradford Hill and others had accumulated a whole body of evidence encapsulated in his guidelines for causal inference. Whichever way you looked at the question of tobacco and lung cancer, as it were, it pointed in the same direction. It was not just looking at a single statistic.

Walter Bodmer: But if you understand the statistics, the formal situation is that there could be a common cause of the correlation, or it could be a direct cause of the smoking. That was Fisher’s logical point. Now he may have been coloured in making that point because of his libertarian views, but I think one has to accept that there was a formal point there. My interpretation would be that he didn’t realize at the time—I think he did begin to accept it before he died—that the correlation was so strong that it was very unlikely that it was due to a common cause.

Richard Doll: That was the reason why I told the story about the nickel cancer first of all. That was a correlation, but nobody, to my knowledge, has ever suggested that there was some factor that caused Welshmen to become nickel miners and to develop cancer of the nose independently. But that could have been said. It wasn’t said because the correlation was so strong. Yet Fisher suggested a common factor for smoking and lung cancer. Apart from anything else, the ‘common factor’ idea didn’t account for the increased mortality from lung cancer throughout the world. It just didn’t. If you looked at the whole picture, this wasn’t a sensible suggestion. But a similar objection, if you then make it on theory, could have been made about the cancer and working in the nickel refinery in Wales.

Walter Bodmer: Fisher did come up with a plausible idea on what could lead to some correlation, namely genetic factors. I think the possibility that genetic factors may influence whether you smoke or not, and indeed the response to smoking, is plausible, and they probably do exist; but they are not nearly enough to explain the strength of the association. I think the likelihood of something similar in the case of nickel workers is pretty slim.

Richard Doll: Genetic factors couldn’t have accounted for the increase in mortality.

Walter Bodmer: Well that’s true.

Harry Marks: I think there is a point about the streptomycin study that may also be relevant to this cancer discussion. You need to be very careful when looking at these things not to read back in the light of what we know now. I have looked very intensively at the American discussions of streptomycin, and there was great concern over a period of several years about the fact that there had been a long history of putative treatments for tuberculosis that looked good for a while and turned out not to work. There was a lot of concern about the clinical variability and unpredictability of pulmonary tuberculosis and that’s the reason they did those studies. The effects of streptomycin weren’t obvious, something that didn’t need a study to be done. That may have some bearing also, I think, on the cancer and smoking debate.

Walter Bodmer: Can I just make one other comment on the bacterial resistance question? From around about the mid to late 1940s, bacterial geneticists knew very well that resistance to antibiotics would develop. On the basis of experiments with bacteria they were advocating the use of two antibiotics to reduce the probability of getting resistance. Of course, at that time they didn’t know about plasmids that could carry multiple resistance. From the point of view of those who were working in the laboratory, therefore, I don’t think there was a lack of awareness of the problem of developing resistance.

Thanks to Maureen Malowany for her transcription of the unedited discussion.





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