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Mice and Men in Medical Research

THE PRESIDENT, THE EARL OF HALSBURY, in opening the proceedings welcomed the Members of the Society and their guests who were present to hear Dr. Reid deliver the 34th Stephen Paget Memorial Lecture entitled "Mice and Men in Medical Research".

In introducing the lecturer, he said that Dr. Reid, a Scot who was educated, trained and first practised in Scotland, served during the war in the medical and research branch of the Royal Air Force and afterwards, in 1946, settled down to academic life. Since then his subject had been epidemiology at the London School of Hygiene and Tropical Medicine, where he still taught.

He then invited Dr. Reid to deliver his lecture and thanked him for the trouble he had taken to prepare it.


Mice and Men in Medical Research



Professor of Epidemiology,LondonSchoolof Hygiene and Tropical Medicine


My Lord Chairman, Ladies and Gentlemen:

The invitation from your Council to give the Stephen Paget Memorial Lecture was doubly welcome. In the first place, it is an honour for me, and for the branch of medicine which I represent, that I much appreciate. More im­portant, however, is the opportunity it gives me of recording my respect for two former Secre­taries of this Society. One is, of course. Stephen Paget himself and he must be given pride of place; for he was a man of remarkable courage in the defence of the often unpopular cause of a disciplined freedom to pursue knowledge through experiments on animals. All who care about the prevention of disease, whether in animals or humans, must certainly feel themselves in his debt.


Someone of Paget's generosity of spirit would not, I am sure, protest at sharing his place in our high regard with one of his successors in the Society—the late Dr. J. Douglas Robertson. Through our joint work on standards of basal metabolism, I came to know him well; and it is clear from the obituary notices of both men that they had much in common. Paget was des­cribed as the "vital spirit of the Society" and "passionate in his warfare". Robertson cer­tainly "combined integrity with a puckish humour; great wisdom with Celtic fire: provocativeness with a compellingly lovable charac­ter". Both men sacrificed health and life to the interests of this Society and to the science of medicine; and I think that they should be remembered and honoured together tonight.




One of the occupational hazards of a Secre­tary of the Research Defence Society is that he is the target for personal abuse by anti-vivisectionists such as George Bernard Shaw. Of Paget and his Society, Shaw said ". . . The Crucifixion having resulted in the establishment of the Christian religion and European civiliza­tion, why not impress the gospel of the Research Defence Society on all nations by executing its secretary? . . . lean supply Mr. Paget with pages and pages of such additions to his stock of arguments in favour of vivisection. He will find them quite convincing to vivisectors, criminals, imbeciles, and children under the age of three" . . . and so on. As Sir Almroth Wright (of whom more anon) remarked, "Shaw has great gifts, but absolutely no desire to get at the Truth—he only wants to do circus tricks".

These were, of course, verbal fireworks in the manner of the time. Today, we seem mercifully less prone to such high-flown invective. But the problem remains. Especially in the practice of preventive medicine, we are increasingly dependent on the public's understanding of the methods of scientific medicine and of the need to use animal experiment as well as human observation to divine the causes and plan the prevention of disease. The intelligent layman has u right to question our motives, our methods and our conclusions; for he may reasonably suspect that if the medical profession is to be its own judge, it is unlikely to be its own exe­cutioner. Only if he is convinced of the justice of the case will he give his support to vaccination against poliomyelitis or to fluoridation of water supplies. There is, therefore, a need to consider the sort of scientific debate that exer­cised the mind and passions of lay observers like Shaw, so that we may learn from past experience how to achieve the understanding of our work by the laity without which the practice of preventive medicine in a free society is impossible.


At this point I should interject a personal note. The interests of this Society and the title of this lecture both bear on animal experi­mentation and progress in medicine. I should therefore confess at once that the last animal experiment I performed was on a frog's leg during my undergraduate training in physiology. My whole professional life has been taken up with observations on man. Nevertheless, as a teacher of epidemiology my interests inevitably hover, often a little uncertainly, between the sciences of microbiology and clinical and experimental medicine on the one hand and the discipline of biometry or medical statistics on the other. It is thus hardly surprising that, like other epidemiologists before me, I have been fascinated by the separate contributions made by observations on mice and on men to the pre­vention or cure of illness in either, and by the way in which the results of animal experiment can, and cannot, be transferred to man. I believe that experiments in the laboratory and epi­demiological studies in the field are comple­mentary. Neither is a self-sufficient answer to the problem of disease causation or disease control: and my purpose is to illustrate this by examples both old and new.


To return to our intelligent lay critic, George Bernard Shaw. When we consider his volatile temperament, his agile iconoclastic mind and the intoxicating intellectual climate ofLondonat the turn of the century it was hardly sur­prising that he would write thus of "the inocula­tion craze".


If the consequences were not so serious, it would be impossible to present the current medical tests of the efficacy of prophylactics otherwise than as a roaring farce. Take the case of the army inoculations . . . The troops are inoculated against typhoid, and assured they are safe from it. ...The bacteriologists imme­diately investigate these cases and announce that what the men have died of is not the work of the typhoid bacillus, but of another bacillus, which produces a new disease called para­typhoid. They combine this new bacillus with the old one in preparation of a new "vaccine". . . the troops suffer from typhoid and paratyphoid as before. A fresh investigation is made, and it is discovered that there is yet another bacillus . . . called paratyphoid B . . . The whole inoculation craze ... is a craze of the most extravagant kind. At one end you have the desperate empiricism of vaccination . . . then you have anti-toxin . . . Then the phago­cytes ... It will be seen that the whole practice of Prophylaxis is still crude and confused".




As usual when he had his teeth in an ad­versary, Shaw was neither entirely accurate nor completely fair. But there was, unfortunately, some substance to his views for he had twisted to his own use some of the arguments1 used in the then current controversy between Professor Karl Pearson and Sir Almroth Wright. The repercussions of that notable debate still rumble on so that the outline is worth repeating. Sir Almroth Wright. Professor of Bacteriology at St. Mary's was the initiator and driving force behind the anti-typhoid immunisation campaign. Karl Pearson. Professor of Statistics inUniver­sityCollege, was the founder of the school of biometricians to whose influence on the science of medicine Lord Cohen has recently paid a graceful tribute.


In 1904, Pearson published in the British Medical Journal a "Report on certain Enteric Fever Inoculation Statistics". This report questioned the validity of certain statistical material which Sir Almroth Wright was using to press for the adoption of anti-typhoid inoculation in the British Army. Pearson pointed out that because the vaccine had been given almost haphazardly to some units and not to others, and only to those who had volun­teered to accept it, the comparisons Wright had made between inoculated and non-inoculated might have been biased. Those accepting inoculation, for example, might have included more cautious men who took special care not to eat outside the camp and in general not to expose themselves unduly to infection. In short, like had not been compared to like. He pointed out, too, that the presumptive benefits of inoculation were not uniformly seen in all units and that the possible influence of environmental factors had been ignored. He concluded that anti-typhoid inoculation pro­cedure was an encouraging development but that the method required improvement before it was adopted on a universal scale. Before any such adoption, he urged, it should be subjected to a rigorously controlled field trial.


To this and the accompanying editorial, Wright reacted with characteristic vigour. (This was to be anticipated: he was a formidable and potent mixture—half Irish, half Swedish!) He dodged some of Pearson's questions about the apparent inconsistencies in his own statistical evidence protesting that "the standard of perfection which he (Pearson) exacts is im­measurably above the standard to which we can hope to attain in connection with immunity against typhoid fever".


Pearson reproved him for his emotional language, adding—"Frankly I know absolutely nothing about Dr. Wright's capacity as a bac­teriologist; I do realise his capacity as a statis­tician, and also a certain readiness on his part to accept mythical reports: both of these things seem to me to disqualify him from being plain­tiff and judge alike in a matter which has great national importance".


Beneath the Edwardian gloss, Pearson was insinuating that Wright was applying a double standard by choosing to accept results favourable to his case and dismissing others which con­tradicted it. At this point, Lt. Col. Simpson, who had provided the data to both the com­batants, interjected a letter explaining some of the inconsistencies and refuting Wright's in­sinuation that "the statistics have been in plain language 'cooked'."


The exchange of letters that followed went on in much the same vein. Pearson hammered at the inadequacy of the data. Wright, re­inforced by his experience of watching the whole almost miraculous process of agglutination in his mice and his patients, stigmatised Pearson as a pedantic obstructionist with no under­standing of the practical limits inherent in biological material. In a virulent attack on the use of medical statistics in medicine he instanced the errors introduced by inadequate controls, or poor observers.


On paper at least, Pearson had the last word by pointing out that this was in effect where he had come in in the first place and that if Wrights statistics were indeed subject to such errors they were not really fit to be used at all. "I think" he said, "that Dr. Wright can hardly be conscious of the manner in which his latest proposition destroys his own case". "I opine" he went on, "that the ship 'Routine Inoculation" if built on the present design, stands a fair chance of hogging badly if she is ever launched!" In practice, however, launched it was. Wright was knighted: the Army inFrancewas inocu­lated and the death rate from typhoid fever fell from the level of 14-6 per 1,000 current during the South African war to 0-1 per 1,000 during the war of 1914-18. Some incorrigible doubting Thomases continued to mutter darkly into their beards that sanitary measures such as the intro­duction of the chlorination of water supplies to the Army might have been equally responsible. But compared with the un-inoculated French Army in 1914, the British forces fared well, and the favourable view of the value of the vaccine was apparently unassailable. In theSecond WorldWaranti-typhoid inoculation was a routine.


From 1943 onwards, however, reports began to appear of the onset of typhoid fever among men presumed to be protected against it. An outbreak of enteric fever among Italian prisoners of war led Sir John Boyd to express doubts about the protection afforded by the Italian TAB vaccine. Later, Marmion, Naylor and Stewart reported that nearly half of the men who contracted the disease had been inoculated with the most up-to-date form of British vaccine. This was something quite new. What had gone wrong?


The explanation lay further back in the history of the development of the type of vaccine in use towards the end of World War II. Felix and Pitt, who were primarily responsible for that development, were aware that "doubts will be voiced as to whether the facts established in experiments with mice are also valid with regard to disease in man . . ." But they then went on to say that "The basic element in the pathogenesis of typhoid fever is the bacteraemia. And there is no reason to suppose that the anti-bacterial defense mechanisms evolved in one animal species are not at work when another animal species is invaded". Felix demonstrated that an alcoholised vaccine in­jected into rabbits produced more of the Vi antibodies and appeared to give better protection than the older heat-killed phenol preserved type used by Almroth Wright. On the basis of these experiments, the new alcoholised form of the vaccine was widely adopted without any appeal to arbitration by a field trial in human subjects.


The shock produced by the appearance of the typhoid fever among troops presumed to be effectively immunised against it emphasised the need for a cool reappraisal of the whole prob­lem. Dr. Charles Cockburn raised the cry "Back to Pearson" and advocated a massive field trial along the lines proposed by Pearson and elaborated and codified by his disciple Bradford Hill. Such a trial was in fact carried out in 1954 by the Yugoslav Typhoid Com­mission with the encouragement of the World Health Organization. Some 35,508 people between the ages of 5 and 50 and living in the Osijekarea of Yugoslavia, where typhoid fever was endemic, were divided randomly into three groups. One group received the older phenol preserved heat-killed type, another was given the new alcoholised type vaccine, while a third, or control group, were vaccinated against Shigella flexneri alone. In the subsequent six years, the protection rate afforded by the new alcoholised vaccine was only 42 per cent, compared with the 71 per cent, protection given by the older Wright type of vaccine. More recently, Ash-croft has shown by field trials among children in British Guiana how, despite the contrary indications given by animal experiments, a newer acetone-treated type of vaccine gave even higher rates of protection (93 per cent.) than either of the earlier forms.


Looking back over this chapter in the evolu­tion of preventive medicine we can, by the exercise of hindsight, see the Pearson-Wright controversy in better perspective. Wright's biographer, Leonard Colebrook. makes a con­trast between Wright being "prepared to act on probability . . . rather than on mathematically established certainty". He implies that only Wright realised the fallacies which might invalidate the statistical method in medicine and that Pearson underestimated the very real difficulties in obtaining reliable data on human disease. As later experience has shown, Pearson was indeed right in pointing out that haphazard observation was no substitute for rigorously planned and competently conducted field trials, and that what held for mice did not necessarily always hold for men. His complaint was, not that Wright had failed to use the newly forged statistical tools for the assessment of the possible effects of chance, but that he had failed to conduct properly designed trials where everything had been done to remove obvious sources of bias such as the self-selection of men who volunteered for inoculation. Such trials have since been shown to be entirely practicable in field conditions and to give clear and decisive answers on the degree to which laboratory experiments can be transferred to man.


My own views agree entirely with those of Parrish who summed up this melee in his recent book on the History of Immunisation by saying that "the statistical approach in evaluating a biological agent is an essential requirement" and that "no laboratory test in vitro or in vivo should receive premature recognition as a means of assay". On the other hand, Pearson did appreciate the immense potential of Wright's work and the crucial significance of the animal experiments from which it all began. Today, we all recognise that, without these experiments, the modern miracle of disease prevention by immunisation would have been impossible and that field trials in man played a subsidiary, although important, role.




Since the days or Pearson and Wright, the subject matter of epidemiology has changed greatly. It is still concerned with the description of the distribution of disease in human popu­lations and with a search for causes. But instead of diphtheria and enteric fever, it deals more with the modern epidemics of diseases like coronary thombosis. peptic ulcer and lung cancer. In a weak moment. I once referred obliquely toMilton's phrase about New Presbyter being but Old Priest writ large by calling this change in scope "the New Epi­demiology". Some time later, an irate American critic berated me as "D. D. Reid—the intransigent proponent of the New Epidemiology". Despite this, I maintain my argument that the New is not so different from the Old and that, in the New, we can legitimately use animal experimen­tation to complement the evidence on the cause of diseases that we obtain from epidemiological surveys.

Professor Haddow, speaking of research in cancer causation in his previous lecture in this series, remarked that "Although we are entirely dependent for progress on animal experiment and the application of the basic sciences, it is notable that the key leads have so often come from clinical observation . . ." This, of course, is true of many fields besides cancer; and, more and more often, we reverse the judicial process seen when vaccines, developed by experiments on mice, were submitted to trial in human populations. Now, we take the circumstantial evidence on causation derived from epidemio­logical observations on men and put the resulting hypotheses to the test of strictly controlled animal experiments.


Two possible uses of animal experiment are at once apparent. Even when the circumstantial evidence seems overwhelming (as in the causal relationship of cigarette smoking to lung cancer), recalcitrant critics will demand that the process be repeated in animals. Here one might sound a note of caution on the basis of our sobering experience with the different forms of typhoid vaccine in mouse and man. Quite apart from the practical difficulty of persuading a mouse to smoke like a man there remains the strong possibility of major differences in lung tissue response in the two species. Thus the produc­tion of malignant lung disease in animals by exposing them to cigarette smoke would be a satisfying addition to the sum of the assembled evidence; but a negative result certainly should not be taken as disproving the strong hypothesis built up on the observation of man.


To my mind, the most important role of animal experimentation in studies of causation, however, is in the elucidation of possible mechanisms and in distinguishing causal from coincidental circumstances. Since experiments on disease causation in man himself are usually unthinkable, epidemiological enquiry is restric­ted to observation of human disease experience in different environmental or other circumstan­ces. From these observations one can usually make at least an educated guess about the major factors that are likely to be involved. But without the power to manipulate environment, which is the hall-mark of the experimental method, we are sometimes at a loss to know which of two or more factors is really the primary cause and which is simply coincidental. Moreover, when two or more factors each seem to play a part, observation alone may not be enough to tell whether the result of their com­bined action is greater than the sum of their separate effects.


In the field of chronic obstructive and malig­nant lung disease, for example, many intriguing observations have been made on the distribution of mortality both from chronic bronchitis and its complications and from lung cancer. One of these is the definite urban excess in chronic bronchitis mortality which is apparent in both this country and theUnited States: although, of course, the general level is so much higher here. The same general pattern holds for malignant diseases of the lung. Now that the dominant role of cigarette smoking in these various dis­orders of the lung has been clearly recognized, our attention is turning to the other social and environmental factors which may promote their onset or hasten their evolution. One of these is "the urban factor" in general and the "British urban factor" in particular. The special quality of British urban life is also presumably reflected in the interesting gradient in lung cancer death rates seen in Table 1 from the low rates among Norwegians living in a pre­dominantly rural country to the highest rates among those born and bred and spending their whole lives in this highly industrialised and largely urban island. Observations like these have been the starting point for a whole series of investiga­tions in which our department has been involved.


In one of these studies, we have been using various clinical measures of respiratory dis­ability in middle-aged men doing the same job as motor-vehicle drivers in the postal and telegraph services in centralLondonand in country towns inEnglandsuch asGloucester. At the same time a careful smoking history is taken. The idea is to control major variables such as age, sex, job and smoking habits and then to see whether there remains any difference in respiratory disability which could be reason­ably associated with the different local atmos­pheric and other conditions to which these men are exposed at work.


Taking the frequency of excessive phlegm production as one of the alternative indices of lung function, we can first observe in Table 2 the usual increase in respiratory disability associated with increased cigarette consumption. Next we may note the difference, among smokers, between theLondonmen and those from less polluted areas. Finally, there is a hint (and it is no more than that) of an aggrava­tion of the effect of smoking among the men also exposed to theLondonenvironment and, pre­sumably, the associated levels of air pollution: for the urban-rural gap, which is absent among non-smokers, is especially marked among moderate and heavy cigarette smokers. This would imply that the combined results of air pollution and cigarette smoking may be greater than the sum of their separate effects.


At this stage, we sometimes reach a logical impasse in epidemiological studies. For, since we are observing are not experimenting, we can never be entirely sure that our observations may not have more than one possible inter­pretation. In this context, for example, it could be postulated that the urban-rural differences result from some selective migration of the less fit from country to town or from the greater risk of respiratory infections in the congested city rather than from any specific effect of urban air pollution on the respiratory tract.


Since we cannot experiment by ordering some to smoke and some to give up, some to move into town and some to move out, we must turn to the artificial world of the mouse colony where the rigorous rules of experimentation can be more readily applied. Quite recently, Dr. Roe and Miss Kearns of the Chester Beatty Institute have carried out an experiment designed to answer the question: is it reasonable to suppose, on the basis of experience with mice, that tobacco smoke and urban air pollution are separately and conjointly concerned in the production of malignant tumours in man?

They treated the skin of groups of about 36 mice with different dosages of a condensate of cigarette tobacco smoke and a solution in acetone of the particulate matter found in the street air ofLondon. They then observed the number of tumours that developed. Although the statistical significance of the results in Table 3 has still to be decided, the inference is clear. Both these agents produce malignant change in mice. More important, perhaps, is the suggestion in the data of some synergism in the combined effect of the two applications.


Encouraged by such results, we can go back to our labours in the field in pursuit of new evidence of this interaction between factors such as smoking, air pollution and infection in the causation of serious lung disease. Our current enquiries are concentrated on the vast natural experiment provided by the movement of British- and Norwegian-born migrants who are now in theUnited States. By comparing their experience of cardiorespiratory disease with that of either native-born Americans or of the bro­thers and sisters they have left still living in British and Norwegian conditions, we hope to elucidate these relationships between the several factors linked to chronic lung disease whether malignant or not. We hope to establish, for example, whether the gradient of respiratory morbidity or mortality associated with cigarette consumption is more marked among the British siblings who have stayed in the British city than among the brothers who have migrated to the very different urban conditions of theUnited States. Again, does the imprint of a British urban childhood remain in the form of an enhanced risk of cancer of the lung among the British migrant over the rates for his Ameri­can contemporary living in the same area and smoking the same number of cigarettes? These are some of the questions we seek to answer and we are encouraged in our search by the stimulus of animal experiments such as those that I have just described.




It ill becomes me as a Scot to speak well of Dr. Samuel Johnson who seldom spoke kindly of us. Like his Scottish biographer, however, I am incurably addicted to his pronouncements. One has long given me pleasure and consolation. Writing to a Miss Sophie Thrale in 1783 he said:

"Nothing amuses more harmlessly than com­putation, and nothing is oftener applicable to real business or speculative enquiries. A thousand stories which the ignorant tell, and believe, die away at once when the computist takes them in his grip". Certainly, modern epidemiological studies of large human popu­lations demand computation but, more than that, they need the stern intellectual discipline which Pearson and the whole school of bio-metricians who followed him imposed on medical thought and practice.

On the other hand, likeGreenwood, I am far from believing that statistical investigation and wisdom are synonyms. There are other aids to progress "through the jungle to the palace of the Sleeping Beauty''. Epidemiology may draw its inspiration from the experience of clinical medicine and the tabulations of vital statistics: but it must also continually appeal to animal experiment for the testing of old theories of disease causation and the suggestion of new concepts.


"Man is born", said Goethe, “not to solve the problems of the universe, but to find out where the problem begins, and then to restrain himself within the limits of the comprehensible". This seems to me to sum up the contributions to medical knowledge that can be made in turn by epidemiological observations and by animal experiment. By observations on man we isolate the disease problem and guess at a range of possible causes. These possibles are then refined into probables by animal experiment and so, inch by laborious inch, progress is made. The dialogue between the lineal academic descendants of Pearson and Wright now goes on civilly, even cordially. Ideas are generated and concepts refreshed by the unceasing to and fro between the observation of man and experiments on mice. The result is that continuing extension of the limits of the comprehensible which Goethe desired and which Stephen Paget did so much to bring about.


Table I


31 48 72 94 151

per 100,000 per annum (MALES AGED 35-74)

Norwegians in Norway
Norwegian-born in the USA
Native-born citizens of USA
British-born in USA
British inBritain        

Table 2



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