“Can the leopard change his spots?” the prophet asked (Jeremiah, 13: 23), clearly not expecting to be told he can. Nor, indeed, can mice, except under the rather discreditable circumstances now to be outlined.
It is a well-attested truth of observation that except under special and unusual circumstances skin from one mouse or human being will not form a permanent graft after transplantation to another mouse or another human being; for although such a graft heals into place it soon becomes inflamed and ulcerated, and eventually dries up and sloughs off. The exceptional circumstances are: in human beings, when donor and recipient are identical twins, and in mice when prolonged inbreeding (e.g., upward of twenty successive generations of brother/sister mating) has made the mice so closely similar to each other genetically that they almost could be identical twins.
This being so; great surprise was caused in the world of transplantation when Dr. William Summerlin, a member of the largest and in many ways the most important cancer research center in the world, the Sloan-Kettering Institute in New York, with the backing of his chief, Dr. Robert A. Good, made known in 1973 his surprising claim that a comparatively simple procedure—“tissue-culture”—could make a skin graft or a corneal graft from a member of the same or even of a different species acceptable to an organism that would otherwise have rejected it. This claim was specially important because grafting skin from one human being to another has never entered clinical practice, in spite of encouraging successes with the transplantation of kidneys, livers, and sometimes even hearts. Either skin is specially well able to excite the immunological reaction that leads to its own rejection, or it is specially vulnerable to it. This inability to graft new skin from one person to another is the greatest current shortcoming of the surgery of replacement and repair, because the replacement of skin is the only adequate treatment of extensive burns or excoriating wounds.
Summerlin’s treatment, the technical details of which, in spite of exhortation from his director, he seemed suspiciously reluctant to impart to his colleagues, amounted in principle to very little more than the incubation of the intended graft in a suitable nutrient medium outside the body for a matter of days or weeks. This seemed an astonishingly simple solution of a problem no one else had solved, although many of us had been trying since about 1940.
Unfortunately, experienced biologists in other laboratories, and eventually workers in the same institute, were unable to confirm Summerlin’s findings, so that Summerlin eventually had recourse to faking his results to convince his now uneasy chief. He touched up his grafts with a felt pen, so simulating dark skin grafts on white mice. He also claimed that operations had been done which had not been done. The formal end of the story came in 1974 when Dr. John L. Ninnemann and Dr. Good published a paper that in effect demolished the whole story.
This was all a nine days’ wonder in the world of immunology, but the nine days are now up and this is therefore a good moment, on the basis of Hixson’s very readable and, so far as I can tell, very accurate account of the whole story, to stand back and see what lessons can be learned from the whole episode. This is also Hixson’s ambition, for he says at the outset: “I hope that by the time the reader has reached the end of the book, he or she will have enough information to form an opinion about what is good and what is not so good in our current system of medical research as it pertains to cancer.” “If the reader disagrees with the author,” he goes on bravely, “why then, so much the better.”
Summerlin’s sin is not now in doubt; but it is still worth considering precisely why his action was considered so heinous by all his fellow scientists. The reason is this: scientists try to make sense of the world by devising hypotheses, i.e., draft explanations of what the world is like; they then examine these explanations as critically as they know how to, with the result that either they gain confidence in their beliefs or they modify or abandon them.
In the ordinary course of events scientists very often guess wrong, take a wrong view, or devise hypotheses that later turn out to be untenable. This is an ordinary part of human fallibility and calls for no special comment. Nor does it necessarily impede the growth of science because where they themselves guess wrong, others may yet guess right. But they won’t guess right if the factual evidence that led to formulating the hypothesis and testing its correspondence with reality is not literally true. For this reason, any kind of falsification or fiddling with professedly factual results is rightly regarded as an unforgivable professional crime.
In trying unsuccessfully to get the same results as Summerlin, my colleagues and I wasted a lot of time that might have been much more fruitfully employed. Our failure—and the failure of others—to repeat his results was not in itself irremediably damaging, for this, too, is an ordinary part of scientific life. After Rupert Billingham, Leslie Brent, and I published experiments showing quite clearly that the problem of how to overcome the incompatibility barrier between unrelated individuals was indeed soluble, several people tried to repeat our work and failed. There were, however, always good reasons why they did so; either they had introduced into our techniques little “improvements” of their own, or they were too clumsy or something. These failures did not disturb us in the very least: we knew we were right—and we were—so we did our best to tell those who were struggling with our techniques how best to carry them out. As Hixson makes plain, Summerlin was suspiciously at fault, for he simply would not divulge his methods. Indeed, matters reached such a point that Leslie Brent, one of the world’s foremost experts on transplantation, was driven in desperation to send a whole file of his correspondence with Summerlin to Dr. Good, an action unwillingly taken which led to Summerlin’s being severely reprimanded.
A particularly exasperating characteristic of the whole episode was that Summerlin’s claim could easily have been true and for reasons which Dr. Good described as “trivial.” They would have been trivial only because they did not point to any scientifically exciting phenomenon such as change of genetically programmed characteristics in the graft, for example its makeup of immunity-provoking substances. But from the point of view of clinical usefulness it obviously didn’t matter whether the explanation was profound or trivial. So many of us—even those who like myself shared Good’s view that the reasons for the grafts’ anomalous “take” were trivial—persevered in trying to repeat Summerlin’s work.
I am desperately sorry that Summerlin’s work turned out to be mistaken because its failure means that we are still without means of repairing the skin surface except by piecemeal patching with little fragments of the patient’s own skin—a process that may take weeks or even months during which the patient steadily loses body fluids and is specially vulnerable to infection.
The reader may well want to know what the very distinguished members of the Board of Scientific Consultants of the Sloan-Kettering Institute were up to all this time. My name appears repeatedly in Hixson’s book, partly as an expert on transplantation and partly as a member of the board. I cut a better figure in the pages of Hixson’s book than I did in real life—something for which I bear Hixson no ill will. My reason for saying so is that at several critical points I found myself lacking in moral courage.
Summerlin once demonstrated to our assembled board a rabbit which, he said, had received from a human being a “limbus to limbus” corneal graft—a graft which had been made compatible by his process of culturing. “Limbus to limbus” means extending over the whole dome of the cornea to the extreme rim in which the blood vessels run. Through a perfectly transparent eye this rabbit looked at the board with the candid and unwavering gaze of which only a rabbit with an absolutely clear conscience is capable.
I could not believe that this rabbit had received a graft of any kind, not so much because of the perfect transparency of the cornea as because the pattern of blood vessels in the ring around the cornea was in no way disturbed. Nevertheless, I simply lacked the moral courage to say at the time that I thought we were the victims of a hoax or confidence trick. It is easy in theory to say these things, but in practice very senior scientists do not like trampling on their juniors in public. Besides, it was still possible that for some reason, “trivial” or otherwise, the story was true. However we made no secret of our inability to repeat some of Summerlin’s experiments, so far as we were able on the basis of the very inadequate information we had.
On the one occasion when I visited Summerlin in his laboratory with his immediate coworkers and technical helpers, and asked a number of hostile questions, I noticed with some surprise that our duologue was causing the others quite a lot of amusement. In retrospect, and after learning from Hixson the part Summerlin’s technicians and immediate coworkers played in showing up the counterfeit, I can now see that they were sardonically amused at Summerlin’s being interrogated in this way. But the equally plausible hypothesis I formed at the time was that, being only human, they were in reality amused at the obvious discomfiture of an eminent visiting scientist who, from the nature of his position on the board, was “one of them” rather than “one of us.” But for whatever reason, I did not forthrightly express any grave doubts about the probity of the whole enterprise.
In cases such as Summerlin’s it is the usual thing to go over the culprit’s career to find premonitions in his early life of how he behaved later. Hixson has done a good job here, reporting upon an unproved charge that Summerlin cheated in exams during his sophomore year at Emory University School of Medicine. It is, of course, possible that Summerlin was what is known in the world of criminology as a “bad apple,” but this diagnosis lacks psychological depth.
I believe that there is a fairly simple explanation of Summerlin’s egregious folly. It is this: in his early experiments Summerlin did actually obtain, with mice, the results that later aroused so many misgivings. Mice can sometimes get muddled up even in the best regulated laboratories, and it is just conceivable that in his earliest experiments the recipient mice which Summerlin believed to be genuinely incompatible with their donors were in reality hybrids between the strain of the graft donor and some other mouse.
For genetic reasons, such hybrids would have accepted the donor’s skin grafts anyway—irrespective of the “tissue culture”; if this is what happened then Summerlin would naturally have been distraught when, on repeating his experiments with genuinely compatible mice, he found they didn’t work. Being absolutely convinced in his own mind that he was telling a true story, he thereupon resorted, disastrously, to deception. A mistake exactly analogous to this was once made by a securely established American expert on transplantation who reported an equally implausible result to the Transplantation Society; so far from losing face—except perhaps in his own mirror—this young man gained some credit for withdrawing his results and frankly admitting that he had made a booboo.
Every scientist is at all times aware of his own fallibility and of the special safeguards that must be taken to avoid biasing the interpretation of results in a way that favors some hypothesis he may be temporarily in love with. “Leaning over backward” is a well-known formula for avoiding self-deception—it stands for making sure that errors of observation arising from uncontrollable sources always tell against the hypothesis we should like to see corroborated. It is for this reason, too, that clinical trials of new remedies have to be done “double blind.” Neither the patients nor the clinicians must know which patients are receiving a new wonder drug and which a mere placebo. A disinterested third party holds the key and will not unlock the code until clinical assessments are complete, after which it may, unhappily, turn out that 250 mg per day of placebic acid is as good a preventative of common colds as ascorbic acid (vitamin C).
My interpretation of Summerlin’s behavior is not intended to depreciate the importance and incentive to a scientist of public recognition and the esteem of one’s colleagues. Election into the Fellowship of the Royal Society or its equivalent elsewhere is an honor because it is a public recognition of the fact that one’s colleagues admire and applaud one’s work. What is still mysterious is that a man of Summerlin’s obvious intelligence and ability could have supposed he would get away with it, unless indeed, as I have suggested, he did once get the results he ultimately faked and thus felt perfectly confident that workers elsewhere would, in the fullness of time, uphold his claims.
How does Robert Good, the director of Summerlin’s institute, come out of all this?
There is no more important position in medical science than the directorship of the Sloan-Kettering Institute, a position for which Dr. Robert Good was qualified by being enormously knowledgeable, brilliantly clever, persuasively eloquent, and indefatigably hard-working. Such a man naturally accumulates enemies, many of whom must have felt several inches taller when the Summerlin affair threw discredit upon him. Quite the most sickening aspect of the whole business was the way in which so many people whose lives had, until then, been devoted single-mindedly to self-advancement sprang into moral postures, pursed their lips, and moralized in a vein of excruciating triteness and dullness.
The Summerlin affair, we were told, was the natural consequence of the prosecution of science in an abrasively competitive world with limited research funds. If Good attached such importance to the work and sponsored his colleague so eloquently in public, then why did he not take more pains to supervise the research and make sure that everything was as it professed to be?
The answers to these questions do not wholly exculpate Good (and he himself does not think they do), but they show him in a very much better light than his enemies would like. In the first place it is a very much more endearing trait in the head of an institute to champion and promote the interests of his young than to let them get on with it while he busies himself with his own affairs. It was, indeed, Good’s patronage in Minneapolis that made it possible for Summerlin to have a career at all. In the second place it is not physically possible for the head of an institute of several hundred members to supervise intently the work of each one. Most such directors assume—and as a rule rightly—that young recruits from good schools and with good references will abide by the accepted and well-understood rules of professional behavior. I write here with the authority of someone who has been the head of a large research institute, and who has himself been once or twice deceived by an impostor.
Summerlin’s attitude toward Good is made clear by his statement that he went to the Sloan-Kettering because Good was there:
“In retrospect I have to plead guilty to an overdose of hero worship. You know, I felt very close to this man. Regrettably, it wasn’t mutual, as it turned out.”
If this last, mean-minded comment is characteristic of Summerlin, it makes much else intelligible.
An especially attractive feature of Hixson’s book is the evidence of the way in which science writers collude with each other and with scientists to create an atmosphere that will help them raise funds for their research. Summerlin was evidently a beneficiary of this process and it shows great forbearance on Hixson’s part that he is not more indignant than he is on behalf of his fraternity of science writers.
Hixson’s writing is of the quality we have come rather complacently to expect nowadays from first-rate professional science writers, although there are occasional lapses. On one page Summerlin is described as a “tall, balding young skin specialist,” in the idiom Time magazine has accustomed us to. Would it have mattered if Summerlin had been stocky and bushy-haired? Perhaps, for elsewhere Hixson makes it pretty clear that Summerlin’s charm, enthusiasm, and general plausibility were not the least important part of his over-all strategy for self-advancement.
The help science writers can give is very important since nearly all bio-medical research—and particularly cancer research—is enormously costly, and the passages in which Hixson describes how it is financed will particularly interest not only potential private benefactors but also those needy scholars, especially in the humane arts, who follow less richly endowed pursuits. By one means or another—whether by private benefactions or fiscal levies—it is the general public that finances all cancer research, and this is how it should be, for they are ultimately the beneficiaries.
By the standards prevailing in humanistic studies the sums available are very large, but they are not to be had merely for the asking: one or more—sometimes a tier—of expert committees, all notoriously hard to please, stand between the applicant and the moneybags. Administrative committees refer a grant application to the expert body most highly qualified to express an informed opinion upon it and sometimes to other experts interested in cognate research.
Service on the National Institute of Health Study Sections in America and on various boards of the Research Councils in England is enormously laborious and time-consuming, particularly as it may sometimes, as with Summerlin’s application, entail personal visits to the laboratories in which the applicants are working. But so well understood is the importance of the task these study boards perform that it is possible to recruit to them extremely busy and able young scientists, often at stages in their careers when they can ill afford to give up their time for the purpose. Among these young bloodhounds are often a number of seniors who, having themselves probably been beneficiaries, have seen it all before and can therefore help to prevent hasty or injudicious decisions.
The study group that visited Summerlin’s laboratories evidently had some misgivings about the authenticity of the work, but however deep-seated these may have been Summerlin was funded both by the NIH and by other benefactors. Does this point to something deeply wrong with the present system of research funding—to something which, for the protection of the public, should be remedied right away?
Speaking as a man who has been a beneficiary of NIH research funds and who has served many severe sentences on grant-giving bodies, I should say not. In cost benefit, I should say that the most successful grant-giving bodies and research sponsors in the world are the Max Planck Gesellschaft in Germany and the Medical and Agricultural Research Councils in Great Britain. They have made grievous blunders, of course—including blunders of the kind that grant-giving bodies most greatly dread, i.e., the failure to fund research that has ultimately turned out to be of the greatest importance. But in the main they do whatever can be expected of bodies of highly informed and concerned scientists. Fortunately, clairvoyance and mind-reading are beyond them. It is not logically possible to predict future theories or future ideas, or, therefore, to be sure that a particular theory proposed for investigation will yield a harvest of fruitful ideas that will stand up to determined self-criticism.
However, there is an ignorance—amounting sometimes almost to contempt—of scientific philosophy not only among scientists but also among people, professedly critical thinkers, who ought to know, and often profess to know, better. This has led to the widespread misconception that the scientist works according to the rules of some cut and dried intellectual formulary known as “the scientific method.” It has therefore come to be widely believed that given money and resources a scientist can bend the scientific method to the solution of almost any problem that confronts him. If he does not, it can only be because he is lazy or incompetent. In real life it is not like that at all. It cannot be too widely understood that there is no such thing as a “calculus of scientific discovery.” The generative act in scientific discovery is a creative act of mind—a process as mysterious and unpredictable in a scientific context as it is in any other exercise of creativity.
We cannot devise hypotheses to order. Shelley would have understood this perfectly, for in his Defence of Poetry he wrote:
A man cannot say “I will compose poetry”; The greatest poet even cannot say it….
Nor can even the greatest scientist undertake to have illuminating ideas upon any problem he is confronted with, though he will know probably from experience how to put himself in the right frame of mind for getting ideas, and what reading and discussions will help him have them.
For these reasons most grant-giving bodies have come empirically to understand that they are most likely to do good by supporting people rather than projects, though I myself think this is a confession of weakness, for while conceding that no committee can do research, I nevertheless think that a committee which really knows its business should be able not merely to formulate a problem but also to indicate the lines along which it is most likely to be solved. Even if it were wrong, as very likely it would be, its thinking on the matter might easily spark off some fruitful idea in the mind of the investigator it commissioned to undertake its project.
I do not, however, think there is anything radically wrong with our present grant-giving procedures or that the grant-giving agencies can be convicted of anything more serious than of sometimes making mistakes. The romantic view of the creative process of science as something cognate with poetic invention is often sneered at by people who pride themselves as shrewd, practical-minded men of the world with a sound sense of the value of money. But they don’t do any better than the rest of us, and it is they, indeed—people who believe that there is a cut and dried scientific method and that they can buy scientific results by paying for them—who are the incurable daydreamers with their heads in the clouds and no real understanding of the way the mind works.
It is characteristic of Hixson’s balanced and fair-minded account of the Summerlin affair, which is likely to be the definitive account of the whole business, that he cites criticisms of his own profession. His discussion of the relationship between scientists and the press during an annual meeting of the Federation of American Societies for Experimental Biology makes it obvious that science writers want clear stories without the cagey reservations scientists are always introducing, and this may do something to incite people of Summerlin’s temperament—though goodness knows he needed little encouragement.
How do scientists come out of it all? When the Summerlin affair became known, laymen shook their heads regretfully and exchanged long, significant looks as if to imply that they had learned something profoundly new about the scientific life and the morals of scientists. This is because two stereotypes of scientists dominate the lay imagination: the first is a figure like Martin Arrowsmith with a chronically dedicated expression on his face, who is willing to sacrifice wealth and an easy life, even love and personal advancement, to the discovery of the new serum upon which he is covertly working after his colleagues have left college or laboratory for the night. The second is a Gothic figure intent on devising ever more expeditious means of destroying the human race—a man who, as his work comes to fruition, cries out in a strong Central European accent (for no American or Britisher could be guilty of such behavior), “And soon ze whole vorld vill be in my power” (maniacal laughter). In reality there are all kinds of different people who are scientists. I once put the matter thus:*
Scientists are people of very dissimilar temperaments doing very different things in very different ways. Among scientists are collectors, classifiers and compulsive tidiers-up; many are detectives by temperament and many are explorers. Some are artists and others are artisans. There are poet-scientists and philosopher-scientists, and even a few mystics.
If only I had thought to add “…and just a few odd crooks,” then I should have drawn a clear distinction between the scientific profession and the pursuit of mercantile business, politics, or the law, professions of which the practitioners are inflexibly upright all the time. As it is, I am afraid no great truth about scientific behavior is to be learned from the Summerlin affair except perhaps that it takes all sorts to make a world.
April 15, 1976