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CANCER FUNDS, 1945-1954
NATIONAL CANCER INSTITUTE AND AMERICAN CANCER SOCIETY
NCI ACS NCI ACS NCI ACS 1950 1951 1952
NCI ACS NCI
SIXTH ANNUAL REPORT, COMMITTEE ON GROWTH-TRENDS IN CANCER RESEARCH
major part of the annual report of the committee has been devoted to dethe society on the design and direction of this program. In the past the operation for 6 years. The committee on growth is responsible for advising The research program of the American Cancer Society has now been in
NOTE: AMERICAN CANCER SOCIETY RESEARCH FUNDS ARE THOSE ALLOCATED FROM CAMPAIGN FUNDS, STATISTICAL RESEARCH SECTION, MEDICAL AND SCIENTIFIC DEPARTMENT, AMERICAN CANCER SOCIETY
scriptions of outstanding results of a few investigations chosen on the basis of their novelty and promise for the future. It has not been possible to review the great body of solid accomplishment in the field which, though it may not catch the eye, is cumulatively of the greatest significance to the present state of the cancer problem. This year the attempt will be made to take the broader view and, through an analysis of the contemporary scene, to arrive at some definition of current trends in cancer research. The discoveries of tomorrow are latent in the trends of today. Let us take bearings on the direction toward which we appear to be sailing.
THE END AND THE BEGINNING
The end of cancer research is the control of cancer in man. The problem is where to begin. In a recent report of the basic policy committee on research of the American Cancer Society the question has been posed as an antithesis between fundamental and applied research. The report puts it this way:
"One school of thought among scientists holds that the shortest way to the answer to cancer is through increased emphasis on basic research studies of the most fundamental type even though the immediate applicability to cancer may not be full, evident, and demonstrable. In other words, these men feel that until we know much more about life and growth processes than we do now, we cannot hope to find the answer to cancer. Another school of equally eminent scientists holds that the most promising approach to the problem is through a more or less empirical testing of chemical and biological compounds which give promise of control or eradication of cancer, and they hold that the answer will be forthcoming much more rapidly from this empirical approach, and that we may be successful before we know the scientific reason why we are successful."
In the Sixth James Ewing Memorial Lecture1 Dr. C. P. Rhoads has restated the same issue in more forthright and challenging fashion. In the words of Dr. Rhoads:
"Two concepts exist according to which two quite dissimilar types of work are going forward supported by cancer funds. One type, and the one principally in vogue, involves investigation on a random basis. It is designed to increase our knowledge of the natural sciences in general, in the expectation that something applicable to cancer will turn up. The other is a more direct approach originally advocated by Ewing and now achieving new support. This levels at cancer the procedures which have already proved their ability to solve major problems of disease in man. The random plan was adopted in the conviction that cancer is a special case, a mystery. Under this concept, obviously, cancer control cannot be attained by the methods useful in other fields. It is based upon the assumption that some revolutionary disclosure is required before we can approach cancer directly. We frequently hear, indeed, that nothing will serve short of exposing the secret of life itself, whatever that may mean."
In his lecture Dr. Rhoads then turned to a penetrating analysis of the present status of cancer research and concluded with the following encouraging words:
"It has become popular to decry the progress which has been made in the cancer field and to deprecate the possibility of advance in the future. Were history not so full of similar melancholy statements made regarding other disorders at times when irrefutable evidence to the contrary was at hand, the present cries of alarm might give concern. True, the problem is a difficult one and the techniques complex. Recall, however, that most work on cancer has been on a random basis and so has included a broad study of natural phenomena relating to growth in general. This has restricted studies designed specifically to attain chemical control of the disease. In spite of the fact that substantial funds for cancer work have been available only since 1945, and that only a small part of them has been allotted to therapeutic studies, the progress has been gratifying, indeed."
This question of the balance between fundamental and applied research is one which almost always arises when administrative aspects of research are under scrutiny. It is well that it should do so because it is undeniable that those who control the pursestrings of research are in a position to exert a profound in
1 Bull. N. Y. Acad. Med., vol. 27, No. 10, October 1951.
fluence on the areas of investigation on which emphasis is placed. The American Cancer Society invests nearly $4 million annually in research and in the training of men for research. About half of this large sum of money is awarded on the advice of the committee on growth. Those whose business it is to control the disposition of these funds have an obligation to apprehend and to avow the measure of their responsibilities and their limitations.
The committee on growth, from its inception, has affirmed the conviction that, while the research program of the American Cancer Society should be focused on the control of cancer in man, it should be built upon the broadest base of research in the physical and biological sciences. The policies of the committee may be inferred from the foreword to the third volume of reprints recently issued by the American Cancer Society. Reviewing the contents of the volume, the foreword comments:
"This volume is a fair representation of the breadth and sweep of the program as it is today. In it will be found clinical studies which attempt to bring the discoveries of the laboratory to the bedside for the better detection and control of cancer in man. Supporting these, and providing the basis for further clinical applications, are a bewildering diversity of biochemical, biophysical, and morphological studies of experimental tumors and of carcinogenic and carcinolytic agents. These, in their turn, had their origin in still more general studies of the basic phenomena of growth and metabolism in all manner of living systems. Examples of such work will also be found here. Superficially considered, these studies may seem to make no obvious contribution to the problem of malignancy. Yet, without them the stream of clinical progress would soon dry up. New power, new means of control, new tools can be brought to the clinician no more rapidly than the crude ore of knowledge can be mined. "No royal road to the solution of the problem of cancer has yet been opened up. Until that road has been mapped and finger posted we must diligently continue to explore all avenues of approach."
In the field of cancer no valid distinction can be drawn between pure and applied research. The investigator in the basic sciences is constantly developing new ideas, devising new tools and exploring new methods of approach which he refines and passes on to the clinical investigator. The latter, as constantly, is redefining problems, passing back new leads, testing out ideas at the clinical level and, thereby channeling the effort of the random investigator. The direct and oblique approaches are not so much competitive as complementary. The issue is not between alternative strategies. If you are faced by a stubborn enemy, a frontal assault is strengthened, not weakened, by a simultaneous and sustained attack upon his lines of communication and his source of supply. Concentration of effort is good strategy when you have taken the measure of your opponent, have counted his resources and has found his weaknesses. It is poor strategy in a war of maneuver when you are still feeling him out, still seeking out his main line of defense. In this situation, pressure must be maintained on all fronts. One must probe continually anywhere and everywhere looking for the weak spots. The war on cancer is still a war of maneuver. enemy is not yet pinned down. We are not yet in position for the grand assault. We are not yet sure what types of weapons will be most effective in subduing him.
RESEARCH BY REMOTE CONTROL
There is a place for planned research in the field of cancer. There is a place, a more important place, for the random investigator. The role of the former is to consolidate ground already won, that of the latter is to seek out new worlds to conquer. Planned research can take a defined body of knowledge and lay out a set of experiments which will exploit this knowledge to its foreseeable limits. It can take a set of postulates and drive them home to their rational conclusions. It can do this with exhaustive thoroughness, economy, and speed. Within its limitations it is efficient, expedite, and authoritative.
In the world of ideas, planned research is research in blinders. Organized research is inclined to follow the fashions. As Henry Allen Moe has remarked, "It is precisely when a field has become modish and accepted, when its vested interests are at their highest, that it tends to become sterile." One cannot plan new ideas because one cannot plan for the unexpected. Now, if there be one lesson which the faithful disciple of science learns the hard way, it is that new ideas are to be sought down the road of the unexpected. An experiment that fails is the beginning of understanding. It tells the alert investigator that the reasoning behind his experiment was inadequate. It tells him that his original
idea must be abandoned, that he must go off on a fresh tack, following the unexpected clue wherever it may lead, in the faith that he will finally emerge with a new, more valid, principle. The remote controller, on the other hand, tends to be impatient of experiments that fail. They upset his well-laid plans. He is inclined to dismiss them as irrelevancies, as irritating eccentricities of nature. The imaginative investigator who has actually made the unexpected observations welcomes them because he knows that nature betrays herself in her eccentricities rather than in her adherence to conventional behavior.
The business of the administrator in research is to choose the men to do the work, to apprehend the significance of their ideas, to provide them with the tools, and to keep open the lines of communication. One cannot chart the unknown. The individual investigator must be given the freedom to seek out new knowledge in his own way. The experiments which he will conduct must be left to his own intuitive compulsions. They cannot be directed by remote control. Interests will change and emphasis will shift as new techniques and new ideas remold his thoughts. The wind bloweth where it listeth. One cannot control the changing winds of ideas. The best that the administrator can do is to be alert to the shifting climate of thought so that he may trim the sails of his effort to the best advantage.
PREVENTION OR CURE?
Although no valid distinction can be drawn between pure and applied research in the field of cancer, the issue can be restated in a form that does appear to have some cogency. Should the major effort be concentrated on the prevention or on the cure of cancer? Should the American Cancer Society encourage the pursuit of investigations directed toward a better understanding of the root causes of cancer or should it throw the main weight of its support behind such therapeutic approaches as offer the greatest immediate promise?
Cancer is a disease of individual cells. The weight of evidence points to the conclusion that malignant cells are not merely normal cells "on the loose." They are abnormal specifically modified cells. They are disordered rather than disorderly. This is implicit in the fact that their abnormal characteristics, once established, are passed on to the progeny of the aberrant cells. The cells have suffered what appears to be an irreversible physical change. A physical change must have a physical cause. If we could but discover the indigenous causes of these malignant changes we would be entitled to hope that we may be able to devise rational means to neutralize these causes.
This is the goal of prevention. A few extraneous causes of cancer, such as undue exposure to ionizing radiations and to a variety of industrial chemicals are already known. To avoid these it is necessary only to exercise proper care. The natural causes of cancer are more elusive. The geneticists have established, beyond doubt, that the susceptibility of particular tissues in animals to particular tumors is influenced by hereditary factors. At the same time, it has been shown that susceptibility to some of these tumors is also influenced by certain of the hormones of the host. A few animal cancers, moreover, can be transmitted from animal to animal by viruslike bodies. These facts are clues to the causes of cancer which are being intensively pursued at the present time. How far they will take us we know not. We do not yet see clearly what the relations are between hereditary susceptibility and the actions of invading inciters such as the viruses and the chemical cancerogens. We do not understand the ways in which the aging process and the hormone balance in the host modify his susceptibility to cancer. It may transpire that malignant changes are a hazard intrinsic to the very nature of living cells. The elimination of the hazard may not be compatible with life. The secret of cancer may lie so close to the secret of life itself that its quest is hopeless. This may prove to be so, but we can scarcely give up the quest before we have well begun. The search for the natural causes of cancer is and will be intensively and unremittingly pursued. It is the ultimate objective of cancer research.
Cancer, however, is not a potential hazard. It is a very present scourge for which a present cure must be sought. We know that cancer can be cured if it is localized and is accessible to the surgeon's knife or to the X-ray beam. The urgent and compelling challenge of cancer is the detection and control of hidden and diffuse malignancies. This is a dual problem in diagnosis and in cure. The presence and distribution of the malignancy must first be established. Some chemical agent must then be found which will be carried by the blood stream to the cancer cells and will destroy them without destroying essential functions of normal tissues. This is the challenge of cancer chemotherapy.
The seeker after causes starts from the premise that some physical causesome inciter agent-has imposed upon the cell a heritable change in the normal processes of growth and differentiation. He studies the effects of radiation, of carcinogenic chemicals, of viruses and of hormones on the physicochemical machinery of the cell in the hope that these will provide clues to the nature of the malignant disorder. He is particularly interested in the nucleus of the cell because it is the nucleus which is the dea ex machina of heredity. It also appears to be the controller of the synthetic processes which are essential to growth and multiplication. At the same time, he recognizes that the nucleus and the cytoplasm are so interrelated that agents ultimaely modifying the functions of the nucleus may have their origin or their primary effect in the cytoplasm. Consequently, he is forced to concern himself with all of the functional activities of the cell in his search for the root causes of the malignancy. In a word, the whole field of cellular physiology is his province.
The object of the seeker after cures is to find some chemical agent which will arrest the multiplication of cancer cells without destroying normal tissues. Faced with millions of available chemical compounds he will not be expected to engage in the enterprise on a purely hit-or-miss basis. The odds are all against him unless he is provided with some clues to the selection of plausible candidates. It is possible that he may stumble upon an effective agent by chance, that is to say, by being alert to apprehend the significance of some unexpected observation. But he does not plan to leave it to chance. He begins by selecting some metabolic reaction on which he has reason to believe the malignant cell is more dependent than are normal cells and he then selects chemical compounds which may be expected to inhibit this essential reaction. He is, naturally, concerned to know how radiations and known chemical cancerolytic agents destroy cancer because he wishes to imitate and improve upon their actions. He studies the effects of those hormones that control the growth of tumors for the same reason. At the present time he is particularly interested in the metabolism of the nucleus because he has reason to hope that this may be the most vulnerable point of attack on the malignant cell.
The seeker after diagnostic tests soon finds himself exploring the same territory. Many of the tests that have been devised for the detection of cancer appear to have been purely empirical in origin arising from some chance observation. Others have been rationally based upon inferences drawn from observed metabolic anomalies in cancer patients. Such chemical tests as are available at present are not very discriminating. The hope for the future surely lies in a fuller understanding of the chemical details of metabolism and the anomalies that may be associated with cancer.
The substance of the argument which has been developed above is that the seekers for causes and the seekers for cures or for tests may pose their questions differently. They may start with different objectives but they find themselves exploring the same ground. Their paths are not separated. They cross and recross. Each in the pursuit of his own quest depends upon the progress made by his fellow explorers. It is quite possible that the next major advance in chemotherapy will arise from a chance observation made in the course of a general study of the metabolism of growth. It is equally possible that the next new idea about the natural causes of cancer may emerge from systematic chemotherapeutic investigations in man.
THE CORE OF THE PROBLEM
The cancer problem is a problem in the behavior of living cells. Now, the living cell is a chemical machine. It lives and moves and has its being by the energy which it derives from the chemical reactions carried out within itself, using the chemicals on which it feeds as its fuel. Moreover, it renews its own structure, it keeps its machinery in good working order by repair processes which use these same foods as construction materials. Each type of cell has its own peculiar structure and its own particular functions and conducts its chemical transactions in its own unique way. If its structure or its activities change its chemical traffic will also change. If some cells of a tissue continue to grow and multiply when their neighbors have ceased to do so it is because the aberrant cells are pursuing a pattern of chemical behavior different from that of the community. A malignant cell must differ chemically from a normal cell because it behaves differently. If we are to control the growth of tumors by means other than complete removal we can do so only by controlling their chemical reactions.
In the final issue, the cancer problem is a biochemical problem. In no degree does this statement detract from the importance of biological studies which