Académie royale de Médecine de Belgique


Texte Christian de Duve, membre titulaire

(Séance du vendredi 27 septembre 1985)


par Christian de DUVE (Prix Nobel 1974), membre titulaire. 

Some 25 years age, the Swiss geneticist Werner Arber became intrigued by a rather esoteric phenomenon called restriction.  When different strains of bacteria are exposed to different varieties of the DNA-containing bacteriophage (a bacterial virus), not all bacterial strains are infected and this restriction depends both on the bacterium and on the bacteriophage.  Out of Arber’s analysis of this phenomenon came the realization that bacteria have enzymes that are capable of cutting DNA chains at specific sites provided these sites are not methylated.  They use these “restriction enzymes” to destroy the unshielded DNA of invading bacteriophages while protecting their own DNA by methylation of the sensitive restriction sites.  Of great biological interest in itself, this work has had as unexpected outcome the development of tools of immense practical value : enzymes whereby DNA chains can be cut into defined pieces, making possible, among other applications, the sequencing of long DNA chains and genetic engineering.  Human hormones, interferon, vaccines against malaria, leprosy, hepatitis, and other diseases, the identification and dissection of oncogenes, diagnostic probes of great sensitivity, perhaps some day the correction of genetic deficiencies, are among the benefits medicine is in the process of gaining from this unlikely chain of events.

Take another recent development that is having a major incidence on medical research : monoclonal antibodies.  When Cesar Milstein and Georges Kohler first fused an antibody-making lymphocyte with a myeloma cell ten years ago, their objective was exactly the opposite of what they achieved.  They wanted to find out how fast antibody diversity would be generated by somatic mutations in the dividing cells.  The process of diversification of immunoglobulin genes by splicing of precursor pieces was not known at that time and somatic : mutation seemed the most likely mechanism whereby the enormous number of immunoglobulin genes required by the clonal selection theory could be generated during lymphocyte maturation. As it turned out, the expected mutations did not occur.  Instead, clones of cells making a single kind of antibody were obtained.  Today, a flourishing industry totally undreamed of by the investigations in supplying invaluable aids to research, diagnosis, therapy, and many other areas of activity.

So here we have two discoveries of immense importance to medicine – probably the two most important ones to be made in many years – that have developed in a totally unpredictable and serendipitous fashion from research that was carried out for a completely different purpose – mainly to satisfy the investigators curiosity – and that did not even directly concern the medical field.  Note that the benefits of these discoveries are not just to medicine.  They extend to many kinds of industries, as well as to basic research itself, which has gained tools of exceptional usefulness.  Indeed, the very future of mankind may be affected, and it was all unforeseen, unplanned, and unprogrammed.

Such stories, of which there are many others, illustrate the essence of basic research : it moves into the unknown and therefore, what it will discover is, by definition, unpredictable.  What, if any, practical applications may come out of it its, a fortiori, impossible to predict, or even to imagine.  Needless to add, not every piece of basic research has such far-reaching consequences as those I have mentioned.  As a rule, basic research just adds a modest stone to the edifice of human knowledge, with little or no practical impact.  But if the stones are modest, the edifice is not and it is because it is being built slowly and patiently by the collective efforts of scientists all over the world that major breakthroughs occasionally happen.

Generations of scientists have used such examples to impress officials responsible for the allocation of funds with the need of supporting free, untrammeled basic research.  I can’t say that the effort has been entirely unsuccessful.  But it certainly stumbles against the almost invincible reluctance of orderly and prudent minds to approve the spending of money on something that is not explicity directed toward an identifiable useful goal.  Yet, the facts are there.  If you want an authentic discovery, you cannot possibly ask the investigator to tell you beforehand what is it going to be and, even less, what it is going to be useful for.  You cannot select the goals.  But at least, you can select the investigators, and this is where the thrust should be, rather than on programs.  Take the best investigators you can find, give them the freedom to pursue their own research interests, provide them with sufficient means, a good infrastructure, and a stimulating environment – and wait. Something will turn up.  It may not be what you had hoped for, but it could be more interesting, because unforeseen, and possibly more valuable in terms of practical offshoots.  However, this cannot be guaranteed, except statistically.

I am not suggesting that only this kind of research should be supported.  Once discoveries have been made, a considerable amount of goal-directed research, often requiring a great deal of innovative imagination and ingenuity, is usually called for to turn the discoveries into useful applications.  This, of course, is the king of research industries mostly invest in.  And it is also quite proper for governmental agencies to do the same within the framework of a general economic or technological policy.  But to do so at the expense of basic research is self-defeating, because basic research is the main source of the discoveries that are exploited by applied research.  It also provides the universities, where most of it is carried out, with an indispensable intellectual ferment and an irreplaceable means of training competent scientists.  For obvious reasons, basic research must be supported mainly by public funds. A country that refuses to do this not only refuses to participate in one of the most important collective endeavours of mankind – the search for truth – but also condemns itself to progressive underdevelopment. And let me add here that to live off the basic research of other countries – a policy I have heard advocated for small countries such as Belgium – is not just a rather sordid form of exploitation.  In the long run it does not pay.

What I have said so for concerns basic research in general.  In the medical field, we often consider basic research in a more narrow sense, as a strategy, not just for acquiring knowledge, but for solving a medical problem rationally with the help of that knowledge.  The question I would like to address now concerns the relative value of this sort of approach, as compared to other approaches of a more empirical kind, in accomplishing the main aim of medical research : to prevent or cure human diseases, or, expressed in the more positive terms preferred by WHO, to maintain and improve human health.  The problem is best illustrated by an example.

Take atherosclerosis, the number-one killer in our country.  Aside from clinical research dealing directly with individual patients, which is, of course, the obligatory and indispensable starting point of any kind of medical research, two main strategies have been adopted in atherosclerosis research.  One is the epidemiological strategy.  Using a technology based essentially on the gathering, classification, and statistical analysis of information that was, or could be made, readily available, epidemiological studies of atherosclerosis have tried to establish correlations between the incidence of some assessable manifestation of the disease, for example, death from a heart attack, and a number of variables such as the dietary content of cholesterol or of saturated fatty acids, the overall caloric intake, cigarette smoking, alcohol consumption, sedentary habits, geographical location, familial frequency of the disease, sex, age, association with other property of the patients the investigator chooses as possibly relevant.  The rationale behind such surveys is that they may reveal causality links and may thereby help decreasing the incidence of the disease by measures, such as dietary and other recommendations, aimed at eliminating or reducing its causes.

The other strategy is basic research.  It aims at understanding the cellular and molecular mechanisms that bring about arterial disease, for instance, through studies of plasma lipoproteins and of their cellular uptake and processing, such as have been carried out in the last few years by Michael Brown and Joseph Goldstein.  Here, the reasoning is that understanding of the pathogenic mechanism will enable the rational development of means to control it.

The same two approaches also figure prominently in the field of cancer, another major medical problem.  The epidemiological approach has given us radiation, industrial carcinogens, smoking, and environmental pollutants as causes of different types of cancers, together with various genetic, dietary, hormonal, and other factors that either increase of decrease the vulnerability of the organism to carcinogens.  The present excitement about oncogenes is, of course, a product of basic research.

These two examples may be generalized.  There are few areas of medical research that are not approached concurrently by the two strategies : the one that looks for causes by means of mass surveys of various kinds and the one that scrutinizes mechanisms through basic research.  Something of a similar dichotomy exists in pharmaceutical research between mass screening and rational design as ways of developing new drugs.

The two strategies obviously complement each other and they have, in many cases, been mutually supportive.  The results of epidemiological research, together with the les structured, but often valuable, observations of watchful clinicians, have frequently helped to orient basic research in a fruitful direction.  On the other hand, basic research has often influenced the choice of variables that were taken into consideration in epidemiological surveys.  Nevertheless, the two approaches are fundamentally different.  They rest, one might say, on different philosophies and require different trainings.  As they compete for the same funds, the question of their relative merits is an important one.

The main merit of the epidemiological approach, or of etiological research in general, is that is can be highly successful without the benefit of knowledge.  For example, it has established with a high degree of probability that cigarette smoking is responsible for more than 90 percent of lung carcinomas – and has thereby provided society with a simple means of decreasing cancer mortality by more than 30 percent – even though we may have no idea of how cigarette smoking causes lung cancer nor of what has gone wrong in the transformed cells.  Another advantage of this kind of strategy lies in its simple and straightforward logic, which makes it intellectually attractive both to busy physicians who have no time for molecular biology and to meat-minded administrators who like to know where they are going : if you wish to eliminate a disease, all you need to do is to identify its cause, and then suppress it.  To understand what you are doing is, of course, not without interest.  But it is irrelevant to the final result.

In the sense that it does not require basic knowledge to be successful, the epidemiological strategy may be seen as continuing in a more sophisticated form the general empirical approach that has allowed medicine to make major advances at a time when little or nothing was known of biological mechanisms.  Vaccination, for example, was introduced long before antibodies and the lymphocytes that produce them were discovered, and even, in the case of smallpox vaccination, before the role of microbes and viruses in the causation of infectious diseases was recognized.  Many remedies were discovered and used successfully without the benefit of chemistry or pharmacology.  Even some of the most advanced products of the pharmaceutical industry, from aspirin to penicillin, have helped countless patients before something came to be known of their mechanism of action.

The fact is that the medical revolution started one hundred years before the biological revolution, of which there is so much talk today.  Admittedly, the discoveries that launched the medical revolution at the turn of the century happened to be in themselves epoch-making contribution to knowledge.  But the significant point is that they were made before the knowledge became available, not as a fruit of it, and that they owed their inception to an essentially empirical research strategy that accepted to bypass, or cut across, vast zones of ignorance in the pursuit of its practical aim.

These successes should not, however, blind us to the fact that the empirical strategy also has serious weaknesses.  Epidemiological surveys can, at best, bring to light statistical correlations between the incidence of a disease and some investigated variable.  Such correlations may suggest possible causality relationships, but definitely do not establish them.  The continuing debates concerning the relative importance of various “risk factors” in the causation of atherosclerosis illustrate these uncertainties.  Even when the cause of a disease in known with some certainty, this does not necessarily suffice to prevent the disease.  The example of cigarette smoking and lung cancer is striking in this respect.  The causal relationship between the two leaves little doubt.  Yet, for a number of reasons, mostly of social and economic nature, prevention by suppressing the cause is proving very difficult to achieve.  Even infectious diseases in known with some certainty, this does not necessarily suffice to prevent the disease.  The example of cigarette smoking and lung cancer is striking in this respect. The causal relationship between the two leaves little doubt.  Yet, for a number of reasons, mostly of social and economic nature, prevention by suppressing the cause is proving very difficult to achieve.  Even infectious diseases, the greatest triumph of empirical prophylaxis, still confront us with many problems.  We know the causes of most of them, yet many, whether caused by viruses, by parasites, or even by bacteria, remain difficult to control because of the lack of appropriate drugs and of the difficulty of preparing effective vaccines.  Even easily controllable diseases remain a threat in some parts of the world, simply for the lack of elementary sanitation.

A word must also be said about the cost of a research strategy that, however sophisticated its tools, perforce has to rely on the collection and sifting of vast amounts of information, which is the case both of epidemiological surveys and of the mass-screening of drugs.  As long as knowledge of basic biological mechanisms was rudimentary and the available instruments and techniques inadequate, the empirical strategies were the best available and their high cost was justified by the even higher value of the stake : saving human lives.  But the question may validly be asked whether the recent revolutionary advances in biological knowledge and technology have not deeply modified the situation.

In my opinion, they have.  Our understanding of basic biological mechanisms in cellular and molecular terms has increased immeasurably in cellular and molecular terms has increased immeasurably in the last decades and these advances have spawned biotechnological tools of remarkable sensitivity and efficiency.  The exploitation of the new knowledge and new tools for the benefit of medicine has already produced important results and is likely to produce many more in the future.  There are thus solid reasons supporting a shift in the strategy of medical research toward a more basic approach.  For such a shift to occur, it is necessary to enlist new forces, including biochemists, cell biologists, molecular biologists, immunologists, microbiologists, virologists, and geneticists, to join the clinicians, the physiologists, the epidemiologists, the chemists, and the pharmacologists already engaged in the war against disease, and to provide them with adequate means.  Indeed, and fortunately, this is happening in many parts of the world, including our own country.

In conclusion, I certainly would not like to leave the impression that I fail to appreciate the value of the traditional approaches of medical research.  On the contrary, they have, as I have mentioned, yielded many of the achievements of modern medicine.  In many cases, they have also brought forth key discoveries that opened new avenues to basic research.  Recent advances as, for example, in immunosuppression, in the control of hypertension, or in the dietary protection against certain cancers, indicate that the traditional strategies continue to be fruitful.  On the other hand, the prospects of basic research have now become so promising.  Its achievements already so encouraging, as to deserve strong support.

And since the funds available for medical research are necessarily limited, this support can only be provided at the expense of a reduction in the support of the more traditional strategies.  In my opinion, such a shift is amply justified and it is our duty to make the appropriate recommendations.