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(homidium bromide) and Prothidium (pyri- Dr J S G Cox thidium bromide) for the treatment and pro- (Fisons Ltd, Pharmaceutical Division, phylaxis of trypanosomiasis in cattle, and we also R & D Laboratories, Bakewell Road, discovered and developed Entamide (diloxanide) Loughborough, LEJJ OQ Y) and later Furamide (diloxanide furoate) for the treatment of ameebiasis, and these are still It is accepted that research is a very high-risk produced and sold in the areas where these activity, at least as far as the discovery of genuine diseases are problems. But at present my depart- new active drugs is concerned - both on account ment's programme is concerned with pharmaco- of the high uncertainty of its outcome and the logically active synthetic chemicals tackling considerable lead times involved. In spite of this diseases such as rheumatoid arthritis, peptic it is to research fhat the internationally based ulceration, cardiovascular disease and mental drug company looks for its major revenuedisorders. We ourselves do not test compounds earning products. Because of the key role of against cancer but, like many other companies, research in the success of the company as a whole we submit compounds for testing to the National the level of investment and selection of fields of Cancer Institute of the National Institutes of research represents crucial decisions for research Health in the USA, believing that this is the best and development management. way for a company of our size to help with this The overall failure rate of compounds between disease. There are of course some of the larger companies still working on tropical diseases, synthesis and the market is, of course, very high and contributions by the pharmaceutical industry the National Economic Development Office study in general and British companies in particular to in 1972 assessed the failure rate at 99.99%. the pharmacopoeia of physicians working in the However, the time scale involved is perhaps of tropics have been considerable. However, with even greater importance in selecting areas for the extremely high cost involved in developing future research. new drugs the companies have to decide what Today it takes about 15 years frsom the original part of their resources can be devoted to such areas. It is of interest that the WHO is now idea or concept to the widespread use of a new considering the possibility of helping to sponsor drug. The initial investigational studies are research in tropical medicine. There is also the almost invariably based on some known basic or possibility of collaboration between bodies such scientific or medical knowledge so that to project as the MRC and the pharmaceutical industry to too far ahead of existing frontiers would be look at less common diseases as well as tropical unprofitable. Hence about 20 years is an appropriate time span over which to consider the diseases. selection of research projects in the pharmaIn summary, project selection is very much an ceutical industry. The key factor in any selection individual matter for each company, and the for research areas should be the future medical factors concerned are a mix of financial and and social need for new drugs. Therefore a pretechnical ones. Research directors are concerned requisite must be an estimate of the medical and to do their best for their companies and for the social needs some 20 years hence in order that (irrespective of which research project is chosen) community. the conceptual ideas of the present are appropriate The need to export has affected our choice of and geared to this future. One is led, therefore, to projects to some extent, and the pharmaceutical the inescapable conclusion that the new drugs in industry has made a considerable contribution to the twenty-first century will originate from ideas the balance of payments. If we are allowed to in the next few years. From a research point of expand profitably then I am sure the choice can view, the year 2000 is almost upon us. be widened and the less common diseases It is not appropriate here to discuss in depth tackled. In the meantime I welcome any opportunity presented to look at collaborative research the various routes by which new drugs are obwith any other body. I also welcome the oppor- tained; the relative emphasis placed on them is a tunity presented by this Forum to discuss these combination of individual research philosophy problems and look for solutions. Such solutions and the particular needs of a given pharmamust remain in the hands of the pharmaceutical ceutical company, and I will deal later with our industry and our colleagues in medicine, and be .own particular research philosophy. protected from the doctrinaire approach of the It is not easy to predict specific future events, politician. i.e. medical and social wants in the year 2000, REFERENCE but there have been several publications of such Hart A (1965) Chemistry and Industry pp 549-554; (March 27)

888 Proc. roy. Soc. Med. Volume 69 December 1976 technological forecasts. For example, the Office of Health Economics published in 1969 a technological forecast of Medicines in the 1990s, and more recently Professor Smith at the University of Mississippi has collected together some predicted drug developments. The results of such forecasts are, as we might expect, inevitably somewhat uneven. But despite this a clear and interesting picture emerges on many aspects of the progress and problems which can be expected. In particular they highlight some of the sociological problems which may arise as pharmacology moves into new fields. Several trends seem to be identifiable which will pose very difficult and new problems on the marketing side of the drug industry, even if the research side is successful. Unless these can be overcome then they may in turn inhibit or at least have a selective effect on the choice of future research programmes. The trends for the future seem to be: the increasing emphasis on preventive medicine and hence early diagnosis; the increasing relationships between drug use and social (moral) values; and the greater use of drugs as 'modifiers' rather than for treatment, i.e. their use in healthy people rather than in those who are ill (the oral contraceptive was perhaps the first example). Of course, some of the greatest problems concern the brain and the mind. We must achieve an understanding of the mechanisms of intelligence and learning so that we can identify the faults which underlie mental illness. Most of the present drug advances in psychiatry have been by 'serendipitous' leads in clinical research. But even when substantially all disease has been brought under control, there would still be a need for pharmaceutical research, because there would remain a need to find the means for controlling normal function: for example, the control of intellectual development. As the world becomes an increasingly complex place in which to live, and as the speed of change accelerates, we are going to need more and more able people to control events, so we need to discover how to hasten the learning process. We may not have time in the future for our present rather slow training programmes. We shall need to be able to put younger people in charge of demanding processes and situations before they have spent something like a third of their life span at school and university or in apprenticeship. We also need to discover how to improve the intellectual calibre of less gifted people. Divisions in society are largely the fruit of an uneven distribution of intelligence. If we could arrange for a more equitable use of our brains, we could perhaps hope for a dramatic reduction in the tensions, jealousies and frustrations which are a present cause of strife.

Man's innate behaviour is a constant source of trouble. We need to find ways of satisfying his more disruptive appetites in a socially acceptable fashion. This must not be merely a matter of attacking the mind with drugs in order to make the human animal passive; we must discover how to keep alert but adjusted and happy. Clearly we will be facing many moral and ethical questions as well as scientific issues. It seems to me that there is an enormous range of challenging scientific and medical problems which warrant solution. The basic dilemma is one of choice and priorities in research and development. Thus, should priorities be consciously deter-mined, as they have been until now, by the relative weight of social needs, rather than emerging unpredictably as knowledge reveals new practical possibilities of diagnosis or therapy? Should greater emphasis be placed on research whose results will have the widest impact, such as enquiries into the control of reproduction, into the safety of drugs, into the simpler ailments like the common cold or the crippling troubles of old age, such as arthritis and backache? Such progress might well be at the expense of dramatic new surgical advances, such as heart transplantation, or medical enquiries into those rare ailments whose cure may be easier to achieve than that of many common ailments. Of course we do not have a free run of options. Some research problems are more easily solved than others. Some may be insoluble anyway. It is always possible to hope for a breakthrough, but we cannot rely on it nor even plan for it. It would perhaps not matter so much if there were no limit to the economic and human resources which could be directed to a particular medical research programme. But clearly there are limits even in the richest countries. It seems indisputable that priorities have to be set, and it is very pertinent to ask who should set these priorities. At present it is left for an individual pharmaceutical company to decide, and therefore it is appropriate for me to illustrate today how it is done in my own organization. We believe that the decisions for preselected research projects for the future should be based on an amalgam of the following criteria.

Preselected Research Projects Medical need: size of potential market; timing of new product; other drugs available. Probability ofsuccess: size and capability of team; motivation or individuality of team; expertise available; time and finance invested; competitive activity. Profitability: return on research investment; pricing structure; other investments needed

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(marketing, production, selling); ability to reach customer. Balanced portfolio: consistent with organization's aims in terms of expected profit and risk. Of these, perhaps deciding on medical need is the most difficult, particularly when you remember that we are not talking about the needs of today but those of 15-20 years ahead. We must consider whether, and to what extent, the diseases or conditions to be treated are already being managed successfully or satisfactorily and therefore the likely number of patients who would benefit. We must consider also the likely cost of the new treatment as compared with existing therapy and the bearing of this on its availability to groups of patients at present not satisfactorily treated. Similarly, full account must be accorded to the safety and efficacy of existing therapies and of the new ones. So far I have just dealt with the deliberate choice to enter a fresh therapeutic field, but there are other factors to be considered, especially the need for an individual pharmaceutical company to defend its existing business. Indeed, this is perhaps the first priority of any research-based pharmaceutical company. When a company has had success it tends to stay in that particular area for the defence of its products, and often this results in investigation of the disease in greater depth and may lead to completely new technology. Sometimes a firm may enter a new research field because it obtains a product on licence and thus becomes more aware of the opportunities and technology necessary for further new drugs. Similarly it may enter a new research area because of a company acquisition. Entry to a new research area may provide a drug company with new drugs in that area, but they may not necessarily provide any significant or obvious benefit to the patient. It would be quite incorrect to infer that successful research in the drug field stems solely from detailed assessment of medical needs, profitability, probability of success, defence of existing business, etc. I must emphasize again that new knowledge or technology in the medical or biological field rarely arises on the basis of market needs. Consequently, in all research portfolios it is essential to have a proportion of what one might call 'non-targeted research', those leads which emerge unpredictably as new knowledge reveals new practical possibilities of therapy. Such research projects are not, therefore, deliberately selected and the research programme should be geared in such a manner as to-encourage this approach. There are several ways of pursuing this research philosophy. As we all know the most difficult problem in discovering new drugs is to find compounds a

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which have qualitatively new types of drug action likely to form the basis of novel drug therapy. At present we rely mainly on accidental clinical observations, but the aim must be to discover new drug action by design rather than chance. In recent years increasing emphasis has been placed upon the value of research in clinical pharmacology in drug development, but so far there is no consensus about its potentially most useful role. One reason for this is the difficulty of deciding how to select new compounds for such research. Drug research must begin in animal species because of the need to ensure safety for man. But models to identify new types of drug action can only be developed in animals after such actions have first been identified in man. Existing animal models will identify variants of known drugs, which may be quantitatively different from the originals; but any qualitatively new types of drug action possessed by the compounds being screened are not likely to be discovered. It is necessary as a matter of research policy to select therapeutic areas for which new drugs are to be developed, and to identify compounds for testing in man in accordance with this. However, many new compounds developed for a particular therapeutic use may also possess other new and unexpected types of drug action which are not recognized because they are not looked for. Research in clinical pharmacology offers the most likely means of discovering such actions at as early a stage as possible and has a number of

objectives: (1) To orientate drug development round experiments in man by processing as many new compounds for evaluation by clinical pharmacological experiments as possible. (2) To evaluate every compound in depth in order to look for new or unsuspected drug actions of potential therapeutic value. (3) To investigate such actions and evaluate their therapeutic potential irrespective of predetermined research policy. (4) To identify and investigate any adverse effects. (5) To select compounds with potential for new drug therapy for further development. (6) To feed back results for the development of new animal models. The first stage of investigation, carried out in normal volunteers is designed to discover new types of drug action, and considerable attention is paid during this stage to ethical considerations. All experimental protocols are submitted to an ethical review committee. In order to process as many new compounds as possible through this

890 Proc. roy. Soc. Med. Volhme 69 December 1976 stage, preliminary safety evaluation in animals is limited and therefore the administration of doses to human subjects is restricted to a maximum of three days. The general pharmacological profile of a new compound is established by investigating its effects on all systems of the body. The investigation comprises pharmacodynamic recordings, metabolic studies, pharmacokinetics, biochemical pharmacology and clinical biochemistry and hematology. The whole range of recordings is repeated at intervals in a series of cycles before, during and after administration of the compound. Each study involves 5-10 subjects, to whom the dose is administered by slow intravenous infusion if possible. There are many problems inherent in such a screening system and the conduct of experiments depends upon integrating all procedures into an experimental design, developing reliable methodology and selecting apparatus adequate for the purpose. Data handling requires computerization. The main problem of identifying drug-induced effects depends upon accumulating reliable baseline control observations. This is being done by establishing physiological profiles of a panel of normal volunteers. All the accumulated data for each subject are used for analysing the results of experiments in which the subject takes part. We have excluded the use of standard normal ranges for measured parameters as 'normal' control data. Computer programming research has indicated that by using cumulative control data it is possible to identify drug effects, and that furthermore it is possible to establish doserelated trends between subjects. This research has not yet been completed, but the results suggest that the Primary Screening System can fulfil its function as a method of alerting the investigator to drug effects. Since the experiments are open studies, final proof is not to be expected.

Secondary screening tests are designed to investigate in depth selected actions detected by the primary screen, and to provide objective evidence to support their validity. Double-blind controlled experiments with normal volunteers are carried out, in which new compounds are administered in single doses, or daily for up to three days. The results are analysed for statistical significance. These experiments may be direct recordings of the effects cf compounds on particular parameters such as the PEG, or they may involve developing experimental models in the subjects, as by altering autonomic mechanisms. The system is in operation, but has not yet been fully developed or validated. Nevertheless several unexpected types of drug action have been identified in compounds under study. These are

varied in character, including for instance an action on the central nervous system of potential psychotropic interest, and a biochemical change of potential therapeutic value. We recognize that this approach does not constitute a comprehensive solution to the problem of identifying new drug actions. For instance, some therapeutic effects cannot be predicted by a study of the pharmacological actions of a compound. However, under the conditions of our research we think that it is possible to maximize the chance of discovering new drug actions in man at an early stage. We believe that this type of non-target orientated research can nevertheless be planned by deliberate research philosophy. Other examples can be found in animal pharmacology and other biological and chemical fields of research. In conclusion, it seems to me that research projects in the pharmaceutical industry are of a number of different types. The balance of these is a matter for the individual company. I believe that the most important, yet perhaps the least recognized, components are those which emerge unpredictably as new knowledge reveals new practical possibilities of therapy. It is from this area that the really novel drugs will arise.

DISCUSSION

Dr Andrew Herxheimer (London Hospital Medical College, London El 2AD)': Would the speakers give some examples of actual drugs to illustrate the points

they made? Dr Main: I said that we were involved in the investigation of ibuprofen (Brufen) as a nonsteroidal antiinflammatory drug, and that we are now looking at the rheumatoid disease process. Instead of looking at simple experimental models such as, for example, guinea-pig erythema or inflammation, rat-foot analgesia or adjuvant arthritis, we are considering the possibility of understanding the rheumatoid process in more detail. If a company does have some success - as we have with Brufen - it is good that the company should look at the more fundamental aspects of the disease process. Dr Herxheimer: There are vast numbers of antiinflammatory drugs, and it would not be very useful to have another one. One of the problems which came out clearly is that the long gestation period frequently leads to a shoal of rather similar products arriving on the scene together. How do you stop all those being actually marketed and descending on the unfortunate prescriber ? 'Present address: Charing Cross Hospital Medical School, London W6 8RF

Medico-Pharmaceutical Forum Dr Main: There are a large number of nonsteroidal anti-inflammatories about and perhaps it indicates a 'flush' of companies thinking at about the same time that aspirin was not the ideal drug for the treatment of rheumatoid arthritis. When corticosteroids came along you will all remember how we welcomed them and thought they were the answer to all those problems, but of course they are not. Ibuprofen has been around a long time. It was marketed in 1969 and clearly the drug has been of value. Dr Herxheimer: It seems as though there are two kinds of research scientist. One says he has a test, and the other that he has a drug, and he wishes he could find a test that would show him what that drug can really do - and prove it. It is extremely difficult to patent a test, but it is possible to patent a drug. You mentioned that you are looking for tests, but do not know whether you have a drug. Can you expand on that? Dr Cox: I should like to reply to Dr Herxheimer on the extension of research. One example, as I said, was cromoglycate in asthma. It certainly led us to understand a great deal about the etiology of asthma. We know very well that the drug does not work in certain types of asthma, and this has led to a greater understanding of the importance of the classification of asthma. We have spent a lot of time studying the mast cell because we feel that it is important in asthma, and in allergy in general. But we have also come to realize the importance of other cells, such as the eosinophils, and we have done a lot of basic work on these. Our pharmacologists have also done some studies on irritant lung receptors in nonallergic conditions, which have led us to a greater understanding of the mechanisms involved. We would not have entered this area if we had not had a drug of this kind. We could not have contributed to some of the important basic knowledge without cromoglycate. As a result I am certain there is potential spin-off for other drugs in this field. Mr J A Smith (Upjohn Ltd, Crawley, West Sussex): It seems to me that the products of the industry today lead to innovation of improved products for treatment of diseases in the future. In order to achieve profitability it is the greatest good for the greatest number that is the important criterion. The industry provides medicines where it is obvious that they are needed - for instance, antibiotics in a country where bronchitis is endemic. But what about minor diseases? What guides companies to cater for small, less revenueproducing enterprises which might, in terms of human need, be extremely valuable to a number of indi-

viduals? Dr Cox: Success is not determined solely by 'profitability'. Success can be measured in a number of ways, including the financial. Dr Main mentioned the success of the people doing the work and the motivation and satisfaction which they receive from seeing illness healed. One cannot talk purely in terms of profitability but there has to be financial success in order for the company to invest further money in research. Mr Smith asked how we decide to go into areas in which there is not much potential for financial

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success, but in which there may be a great medical need - the short answer is that we do not. Fortunately, or unfortunately, whichever way one looks at it, there is such a large range of. medical problems that are worth tackling that we can pick those problems which meet all the criteria of success. When we reach a stage at which all the problems are solved - or almost all, so that only a few are left, the question will arise. At the nmoment we are able to select those problems which will meet all the criteria of success, and one of the most important criteria is certainly financial. Sir John Richardson (London): Dr Main mentioned briefly that he thought there was some cooperation possible between the MRC and the industry in the field of the less common diseases. Would he like to take up that point? Dr Main: We have held one meeting with research directors from the industry and attempts are being made to arrange another meeting soon. On the agenda for that meeting is the discussion of the less common complaints, and also tropical diseases. We should like to listen and help where we can. We can get into the less common diseases if the technology is available. Most of our research is objective-orientated. However, sometimes one sets off to do a certain thing but something turns up which does not meet the objective but which looks very interesting. For example, if we came across something which might affect demyelinating diseases we would certainly investigate it. Dr D Jack (Allen & Hanbury Research Ltd, Ware): One often hears about this problem of uncommon diseases which are inadequately investigated. I should be grateful if the physicians present could tell me about these diseases, on which we should be working. Often, people who talk about uncommon diseases illustrate their case by mentioning multiple sclerosis. The reason we do not work on the problem of multiple sclerosis - at least in Allen & Hanbury Research is not because there is not a great need for a new drug, but simply that we do not know how to start to find it. I think that is true of most of the uncommon diseases. In order to start research work there has to be some working proposition about the disease, or about the nature of cellular control mechanisms which are likely to affect the progress of the disease. By and large, the best projects are those in which the cellular control mechanisms are chemically defined because, otherwise, it is difficult to make progress. There are many great problems affecting mankind. Indeed, with the possible exception of acute infections and a few specific deficiency diseases, I cannot think of any common human ailments which are particularly well treated today. We ought not to waste our time talking about rare diseases. Dr Herxheimer: I agree. We have to have research ideas, and most good research ideas are in short

supply. Dr Cox: The industry would welcome the sort of collaboration being discussed. Perhaps through the National Research Development Corporation, WHO,

892 Proc. roy. Soc. Med. Volume 69 December 1976 or some similar body, one might be able to finance some of this work. A product not meeting its original objective might deserve further support and collaboration for it to be developed for minor diseases. This should be explored. Dr Herxheimer: I should like to put the case for the use of existing products in new ways. One example is the use of alternate-day corticosteroid therapy. Corticosteroids have been with us for very many years and alternate-day therapy, which is much safer in many situations, was suggested in 1963. Yet hardly anybody uses it; far more people could do so. This is the kind of thing which probably does not concern research directors at all. Please correct me if I am wrong, but it seems that pharmaceutical manufacturers are loath to spend any of their research resources on products already on the market. Apparently this kind of research must be done by other people. Dr Main: I do not agree with Dr Herxheimer. We do spend a fair bit of money on drugs already on the market. My company has been involved in the manufacture of nitrogen mustard for several decades. I do not think we make one penny out of nitrogen mustard, but people keep wanting to use it in new ways. I read a report the other day about a trial concerning some aspects of psoriasis in Australia using the nitrogen mustard, mustine. Companies spend a good deal on old products. Obviously, research directors tend to be looking forward rather than back to products on the market, but a fair amount of money goes into this area.

Sir John Richardson: I think that Dr Herxheimer made the fair point that it is really up to industry to contribute to such work as alternate-day corticosteroid therapy. Dr B W Cromie (Hoechst UK Ltd, London): I would like to make a few points. Firstly, I spent three years trying to prove that alternate-day steroid therapy produced the same clinical effect without retarding growth. My biggest problem was to find clinicians to take an interest in this form of therapy. Secondly, I was extremely glad to hear Dr Jack talking about the greatest need for the greatest number. After all, we all realize that there will be economic sanctions on the National Health Service and on the delivery of health care generally. Therefore, if we spend all our time investigating minor diseases, and not trying to improve the greatest number, we are not serving mankind in the way that we should. Further, if the number of sufferers is really so small, it is almost impossible to test a drug for the disease involved. At present we have a drug for a minor disease. It is called Factor XIII and it is for use in Factor XIII deficiency. I understand that there are about 53 people in this country with Factor XIII deficiency, so now we have the great problem of having a magnificent drug which is specific for 53 people. How can we price that? In fact we end up by almost giving it away. Thirdly, Dr Herxheimer suggested that it was a bad thing for a number of drugs for a similar condition to appear on the market at the same time. I wonder

whether it really is, because if research were limited to one company, there would be only one 'chance', as it were, of improving therapy for patients with the particular disease. On the other hand, if there are three, four or five, there is a real possibility that both qualitative and quantitative differences will occur between- the drugs that are marketed, and that the patients will benefit by having a choice of several drugs. All of us know that even if one of those drugs ends up by doing the greatest good for the greatest number, some of the others will be extremely useful alternative drugs and therefore have a place in therapy too. However, duplication is becoming less common. As research is becoming so expensive, and as research teams tend to build up special expertise, as we have heard today, there is a tendency for cooperation, not only with the MRC and similar bodies, but between companies themselves. We now have a number of cases in which two, sometimes even three companies get together and pool their resources and experiences so as to have the optimum chance of producing a new drug for research. We have done this, and I know that a number of other companies have. It seems to be a way in which the expertise available in the industry comes together and gives the greatest chance of producing a new drug. Unfortunately, of course, once the two companies have produced the drug, the decision then has to be made about which one will market it. It seems only reasonable, if two companies pool their resources to carry out research in this way, that both should be allowed to market the new drug. Once that happens there follow .the usual criticisms of two companies marketing the same drug.

Professor R H Girdwood (University Department of Therapeutics, Royal Infirmary, Edinburgh): Occasionally, in postgraduate lectures I refer to Factor XIII deficiency. I would not have known that Dr Cromie had a drug to treat it if I had not come here today. Mr S M Peretz (Cyanamnid of Great Britain Ltd, Gosport, Hampshire): Somebody wrote the other day that presidents of the ABPI have to be replaced every two years because they get so bored with hearing the same uninformed criticisms from laymen about the industry. One of the common criticisms that is made, on which Dr Cromie has touched, is that we as an industry, because we are so highly competitive, have no interest in rationalizing our research programmes. It is thought that if somebody in authority could bang the industry about the head, tell one company to deal with rheumatoid arthritis, a second with asthma and a third with infectious diseases, no two companies should be doing research on the same lines and all would be well. This criticism is commonly ntade; I should like to hear the speakers comment on it. Dr Cox.: Even within our own research organization we have competitive approaches to the same drug. If we could be certain that there was only one way in which to find a drug in any particular therapeutic area, the argument would be valid. There are many different approaches to the same problem, and the competitive spirit is an extremely important aspect in determining success.

Medico-Pharmaceutical Forum The fact that we are competing with colleagues within our own research organization as well as outside is an important factor in success. Competition leads to success more quickly. Dr E H Harries (Association of British Pharmaceutical Industry, London): The word has not yet been used this afternoon, but 'serendipity' is extremely important in this. No matter what the inventive chemist may have done, it is the observant biologist who may cause objectives to be changed. If one company is active in a field, such as asthma, but finds a lead which suggests that this drug would be useful in rheumatoid arthritis, that company will move in that direction. People cannot be directed into going in one way only. Dr Jack: I wanted to say a few words about restricting the number of research organizations, so that they might be bigger and might specialize in particular areas. People who propose this kind of thing have failed to understand that sound ideas simple enough to be reduced to practice are the real limiting factors for progress in the finding of new drugs. I might be convinced by their argument if I thought that centralization would be likely to increase the number of such ideas. But, frankly, I have no reason to suppose so. Ideas come from individuals, and the more individuals who are free to express themselves, the better the chance of something worth while emerging. In fact, I can think of extremely few drugs that have been discovered as a result of a major set piece by a large organization; but I can think of a fair number of set pieces that have failed. The onus should be on the proposers of this kind of change to prove how centralization of drug research would be more productive than what we have now.

Dr Herxheimer: The arguments against centralization are quite convincing, but the problem is not quite as simple as Dr Cromie made it sound: namely, one may usefully like to have, say, four drugs available which do a particular thing. The first one may help 60% of the people, the second another 20 %, the third another 10 % and so on. But when we have arrived at five drugs, that is enough. How can we stop the sixth to the twelfth drugs of the same kind being marketed? This is the kind of situation which leads people to talk about cutting out wasteful research. There is a simple way of cutting it out which is not to allow the sixth to the twelfth drugs to be marketed. That research would then fold up automatically without any sort ofcentralization because it would not be rewarded. Dr Cromie: One of the problems which people may find difficult to understand is that they think we market drugs with full knowledge of all their properties, adverse reactions, interactions and so on. Unfortunately, this is absolutely untrue. By the time we market a drug, we have experience of it in a relatively small number of patients, often under relatively artificial conditions. We certainly do not have experience of the drug used in normal clinical practice in patients in their tens of thousands. Therefore, when we market a drug, we really know relatively little about it. It is absolutely impossible to

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say, at the stage when a drug is being marketed, how it will measure up to the other drugs available at that time. The only way to find this out is to allow it to be used on a widespread scale. Once they have been used in that way all drugs find their true position. I can think of many examples -and I am sure that Dr Herxheimer can also - where there were developments in a certain field and it might almost have been said that we had come to the end of progress in that field then, a relatively small modification of a molecule produces a dramatic change. It is always this unexpected enormous leap, or sometimes a series of smaller leaps, which produce therapeutic benefit that would never have come about if this sort of premarketing selection had been allowed, as suggested by Dr Herxheimer. Another point against centralized direction of research is that decisions taken by any sort of centralized function tend to be compromise decisions. It is only an individual who will take his courage in both hands and follow a lead all the way through, committing to it enormous funds, people, and so on. All who talk about research in the pharmaceutical industry today, must recognize this tremendous responsibility and the contribution now being taken by research directors. It is becoming increasingly difficult because of the increased time and expenditure. I cannot see any centralized, semi-bureaucratic system ever taking that responsibility, pushing it through and getting the results we are obtaining today. Dr Cox: Research is an extremely high-risk area and unless one feels in control of all the factors, one is very unlikely to take decisions of this sort. We all know the problems that arise if decisions on research projects are put to a large committee. Certainly the initial decisions are best taken by key individuals with the benefit of advice from many quarters, because there are enormous barriers to overcome before a drug or an idea becomes accepted and is successful. Anything which destroys the individuality, as far as

research is concerned, will certainly destroy its creativity too. Mr Ivor Boden (E R Squibb & Sons Ltd, Twickenham): Clinical trials take place in the hospital environment with double-blind studies. This is so different from what may happen in general practice. It is sometimes the seventh or eighth drug tested which becomes the most practical in the long run. This is not because it seemed to be the most spectacular under the perfect trial conditions, but because it may not cause the side effects, and this, of course, means that patients are less trouble to the doctor. Does the research team function better in an academic atmosphere, or in one with all the combined resources of a business enterprise ? Dr Main: In my own organization I can think of some people who are totally oblivious of production, marketing, balance of payments and everything else. Their noses are down and they are totally absorbed in moving particles of a molecule around. There are others who are extremely interested in what is going on in the industry. However, if there is a product candidate on the horizon, we soon hear from people

894 Proc. roy. Soc. Med. Volume 69 December 1976 of the first type because they then want resources at the drop of a hat.

produce a usable, prescribable drug. I should like to firmly endorse what Dr Main has just said.

Dr Cox: Different people require different environments. The biggest problem is trying to create the right environment for invention. When an idea reaches a certain stage it is very healthy and important that other parts of the organization are brought in. I feel that it would be a disaster to have research groups totally isolated from the rest of the organization, but it requires a lot of skill to make sure that the atmosphere is right for creation and then to change this, depending on the development of the project.

Sir John Richardson: Can you elaborate a little for us on any possibilities for a profitable, proper commercial extension into these areas where collaboration with official bodies is really so absolutely vital?

Dr Herxheimer: Dr Cromie misunderstood me on one point. When I said that the sixth to the twelfth products which were doing the same thing should not be given permission for marketing, I meant if they cannot be distinguished from the previous five products. If the manufacturer produces any evidence that they differ, of course that has to be considered on its merit. For very many products, however, which have been marketed recently, at the time of marketing there was not even any theoretical advantage. It was purely optimism on the producers' part. To load this onto the medical profession is not a service. Dr Cromie: I do not think that I did misunderstand Dr Herxheimer. Both Mr Boden and I tried to make the point that it is not possible to tell. I remember, as I am sure most people do, that when the thiazides were well established, many people thought that frusemide was no better, but was just another thiazide. Just how wrong they were! We have talked a lot about research, but the development side which produces the drug in an acceptable form should not be ignored. If Intal had not been developed at the same time as the 'spinhaler', we should not have had that breakthrough.

Dr Cox: It is very important that the question of the form in which the drug is developed is considered at an early stage. We use a multidisciplinary team involving marketing, production and development. Dr Main: There are many definitions of development, but perhaps we might define it as all those activities which take place after the discovery, all of which allow the drug to appear. What we have done is to gear ourselves to doing research and development. I can think of few bodies outside the pharmaceutical industry which can do the complete job of making the discovery and making the drug available. Everyone has a right to discover new drugs. We should love to develop them if others are interested in discovering them. Mr Peretz: Perhaps it is not sufficiently generally known - although there are some representatives here from Glaxo who are well 'aware of the facts of the matter - that cephalosporin, which is now the major revenue-producer for the NRDC, may have been the discovery of the NRDC but it would not have been worth one penny without the development work which has been done by companies such as Glaxo, Lilly and many other pharmaceutical companies to

Dr Main: The record ofthe industry in tropical diseases has been a good one. There are still companies working in the area of tropical medicine - and I wish them well. They obviously feel that they will get the returns. Thirdly, I do not think companies avoid tropical medicine because it is difficult. As someone who joined the industry to do tropical medicine, let me say that I think it is an easy area for drug research. On the whole there is an organism, a parasite, a worm or something like that, and an attempt is made to kill it withou't killing the host. There is a relatively simple model on which work can be done. It is not that the technology is not there.- But in certain tropical areas we have seen whole businesses disappear overnight. Therefore, there is some hesitation about putting major research projects into tropical medicine. The WHO has set up some working groups to consider the possibility of helping at the development stage - if certain companies are prepared to do the experimental model testing. The suggestion is that the WHO would then be prepared to put in finance at the development stage. This is something at which we should look carefully. Possibly some companies will wish to collaborate in this way. Dr Jack: One of the reasons why we in the Glaxo group have not worked recently to any extent on tropical diseases is that we see the problem mainly as sociological rather than specifically medical because the problem is, in principle, solvable within existing technology. Unfortunately, it is difficult, even in the Western world, to have drugs used correctly. It is even more difficult in underdeveloped countries. I think that what money is available to help the underdeveloped countries should go towards dealing with sociological problems - changing their agriculture, plumbing &c. rather than into research for improved medicines. It would do more good if used in that way. Mr Peretz: Mr Boden and I were part of a pharmaceutical team that went to China in November 1975. I thought that what we saw in that country bore out absolutely what Dr Jack says. The success China has had in tackling its tropical diseases - such diseases as schistosomiasis - has come almost entirely from the use of simple hygenic measures, certainly much more than from the use of medicine. The Chinese are a large part of the world's population and seem to be prepared to accept the disciplines that are needed to tackle the problems in that sort of way. I am not quite so sure that the same solution could be adopted in darkest Africa.

Sir John Richardson: Yes, there is absolutely no question that the great advances are the sociological ones. In many ways, the advances in this country in health have been based on sociological factors.