There was some doubt about this among my friends. Some thought I might do better at scientific journalism—perhaps, one of them suggested, I should attempt to join the staff of Nature, the leading scientific weekly. (I don’t know what the current editor, John Maddox, would think of this idea.) I consulted mathematician Edward Collingwood, under whom I had worked during the war. As always he was reassuring and helpful. He saw no reason why I should not succeed in pure research. I also asked my close friend Georg Kreisel, now a distinguished mathematical logician. I had run across him when he came, at the age of nineteen, to work in the Admiralty under Collingwood. Kreisel’s first paper—an essay on an approach to the problem of mining the Baltic, using the methods of Wittgenstein—Collingwood had wisely locked away in his safe. By this time I knew Kreisel well, so I felt his advice would be solidly based. He thought for a moment and delivered his judgment: ‘Tve known a lot of people more stupid than you who’ve made a success of it.”
Thus encouraged, my next problem was to decide what subject to choose. Since I essentially knew nothing, I had an almost completely free choice. This, as the sixties generation discovered later, only makes the decision more difficult. I brooded over this problem for several months. It was so late in my career that I knew I had to make the right choice the first time. I could hardly try one subject for two or three years and then switch to a radically different one. Whatever choice I made would be final, at least for many years.
Working in the Admiralty, I had several friends among the naval officers. They were interested in science but knew even less about it than I did. One day I noticed that I was telling them, with some enthusiasm, about recent advances in antibiotics—penicillin and such. Only that evening did it occur to me that I myself really knew almost nothing about these topics, apart from what I had read in Penguin Science or some similar periodical. It came to me that I was not really telling them about science. I was gossiping about it.
This insight was a revelation to me. I had discovered the gossip test—what you are really interested in is what you gossip about. Without hesitation, I applied it to my recent conversations. Quickly I narrowed down my interests to two main areas: the borderline between the living and the nonliving, and the workings of the brain. Further introspection showed me that what these two subjects had in common was that they touched on problems which, in many circles, seemed beyond the power of science to explain. Obviously a disbelief in religious dogma was a very deep part of my nature. I had always appreciated that the scientific way of life, like the religious one, needed a high degree of dedication and that one could not be dedicated to anything unless one believed in it passionately.
By now I was delighted by my progress. I seemed to have found the pass through the interminable mountains of knowledge and could glimpse where I wanted to go. But I still had to decide which of the two areas—we would now call them molecular biology and neurobiology—I should choose. This proved to be much easier. I had little difficulty in convincing myself that my existing scientific background would be more easily applied to the first problem—the borderline between the living and the nonliving—and I decided without further hesitation that that would be my choice.
It should not be imagined that I knew nothing at all of either of my subjects. After the war I had spent a lot of my spare time in background reading. The Admiralty had generously allowed me to go once or twice a week to seminars and courses in theoretical physics at University College during my working hours. Sometimes I would sit at my desk at the Admiralty and surreptitiously read a textbook on organic chemistry. I remembered from my school days a little about hydrocarbons, and even about alcohols and ketones, but what were amino acids? In Chemical and Engineering News I read an article by an authority who prophesied that the hydrogen bond would be very important for biology—but what was it? The author had an unusual name—Linus Pauling—but he was quite unknown to me. I read Lord Adrian’s little book on the brain and found it fascinating. Also Erwin Schroedinger’s What Is Life? It was only later that I came to see its limitations—like many physicists, he knew nothing of chemistry—but he certainly made it seem as if great things were just around the corner. I read Hinshelwood’s The Bacterial Cell but could make little of it. (Sir Cyril Hinshelwood was a distinguished physical chemist, later President of the Royal Society and a Nobel Prize winner.)
In spite of all this reading, I must emphasize that I had only a very superficial knowledge of my two chosen subjects. I certainly had no deep insight into either of them. What attracted me to them was that each contained a major mystery—the mystery of life and the mystery of consciousness. I wanted to know more exactly what, in scientific terms, those mysteries were. I felt it would be splendid if I finally made some small contribution to their solution, but that seemed too far away to worry about.
At this point a crisis suddenly arose. I was offered a job! Not a mere studentship, but an actual job. Hamilton Hartridge, a distinguished but somewhat maverick physiologist, had persuaded the Medical Research Council to set up a small unit for him, to work on the eye. He must have heard I was looking for an opening because he asked me to come to see him. I hastily read his wartime paper on color vision—as I recall, he believed, from his work on the psychology of vision, that there were probably seven types of cones in the eye, not the traditional three. The interview went well and he offered me the job. My problem was that only the week before I had decided that my new field of work was to be molecular biology, not neurobiology.
The decision was a hard one. Finally I told myself that my preference for the living-nonliving borderline had been soundly based, that I would have only one chance to embark on a new career, and that I should not be deflected by the accident of someone offering me a job. Somewhat reluctantly, I wrote to Hartridge and told him that, attractive though it was, I must refuse his offer. Perhaps it was just as well because though I found him a lively and engaging character, he seemed to me a little too bouncy and I was not completely sure we would get on. I also doubt if he would have been very understanding if my work had shown his ideas wrong, as time has proved them to be.
My next task was to find some way of entering my new subject. I went around to University College to see Massey, under whom I had worked during the war, to explain my position and to ask for his help. His first guess when I told him I intended to leave the Admiralty was that I wanted him to get me a job in atomic energy (as it was then called), on which he had worked in Berkeley during the latter stages of the war. He looked surprised when I told him of my interest in biology, but he was very helpful and gave me two valuable introductions. The first was to A. V. Hill, also at University College, a Cambridge physiologist who had made for himself a solid reputation studying the biophysics of muscle, especially the thermal aspects of muscular contraction. For this he had been awarded a Nobel Prize in 1922. He liked the idea that I also should become a biophysicist and perhaps, eventually, work on muscle. He arranged an introduction to Sir Edward Mellanby, the powerful secretary of the Medical Research Council (the MRC). He also gave me some advice. “You should go to Cambridge,” he said. “You’ll find your own level there.”
The second person Massey told me to go to see was Maurice Wilkins. Massey smiled to himself as he said this, and I sensed that Maurice was in some way unusual. They had worked together on isotope separation at Berkeley for the atomic bomb. Wilkins had taken a job under his old boss, John Randall in the physics department at King’s College, London, and I went there to see him in the basement rooms in which they all worked.
Randall had persuaded the MRC that they should support the entry of physicists into biology. During the war scientists had acquired much more influence than they had had before it. It was not difficult for Randall, one of the inventors of the magnetron (the crucial development in military applications of radar), to argue that just as physicists had had a decisive influence on the war effort, so they could now turn their hands to some of the fundamental biological problems that
lay at the foundations of medical research. Thus there was money available for “biophysics,” and the MRC had set up one of its research units at King’s College, with Randall as its director.
Exactly what biophysics was, or could usefully become, was less clear. At King’s they seemed to feel that an important step would be to apply modern physical techniques to biological problems. Wilkins had been working on a new ultraviolet microscope, using mirrors rather than lenses. Lenses would have had to have been made of quartz, since ordinary glass absorbs ultraviolet light. Exactly what they hoped to discover with these new instruments was less clear, but the feeling was that any new observations made would inevitably lead to new discoveries.
Most of their work involved looking at cells rather than molecules. At this time the full power of the electron microscope had yet to be developed, so observing cells meant accepting the relatively low resolving power of the light microscope. The distance between atoms is more than a thousand times smaller than the wavelength of visible light. Most viruses are far too tiny to be seen in an ordinary high-powered microscope, except perhaps as a minute spot of light against a dark background.
In spite of Maurice’s enthusiasm and his very friendly explanations, I was not entirely convinced that this was the right way to go. However, at this stage I knew so little of my new subject that I could form only very tentative opinions. I was mainly interested in the borderline between the living and the nonliving, wherever that was, and most of the work at King’s seemed rather far on the biological side of that border.
Perhaps the most useful result of this initial contact was my continued friendship with Maurice. We both had somewhat similar scientific backgrounds. We even looked somewhat alike. Many years later, upon seeing a photograph of Maurice in a textbook that was somewhat confusingly labeled (it was next to one of Jim Watson), a young woman in New York mistook it for one of me, though I was standing in front of her at the time. At one stage I even wondered if we might be distantly related, since my mother’s maiden name was Wilkins, but if we are cousins we must be very distant ones. More to the point, we were both of a similar age and traveling the same scientific path from physics to biology.
Maurice did not seem especially unusual to me. Even if I had known, say, that he had a taste for Tibetan music, I doubt if I would have considered that odd. Odile (who became my second wife) thought he was rather strange because when he first arrived for dinner at her apartment in Earl’s Court he went straight into the kitchen and lifted the lids of the saucepans to see what was cooking. She had become accustomed to dealing with naval officers, and they never did things like that. After she discovered that this was not the impertinent curiosity of a hungry man—scientists seemed to be curious about such odd things—but simply that Maurice was interested in cooking, she looked at him in a new light.
My next problem was to decide what to work on and, at least as important, where to do it. I first explored the possibility of working at Birkbeck College in London with the X-ray crystallographer J. D. Bernal. Bernal was a fascinating character. One can get a vivid idea of him by reading C. P. Snow’s early science novel The Search, since the character Constantine is obviously based on Bernal. It is amusing to note that, in the novel, Constantine wins fame and an F.R.S. by discovering how to synthesize proteins, though Snow wisely didn’t indicate exactly what the process was. The plot of the novel turns on the setting up of a biophysics institute, while the final incident concerns the narrator deciding not to expose a fellow scientist for falsifying results and instead to give up his own career in science and become a writer, an incident I suspect modeled on something similar in Snow’s career.
When I visited Bernal’s laboratory I was discouraged by his secretary, Miss Rimmel, an amiable dragon. “Do you realize,” she said, “that people from all over the world want to come to work with the professor? Why do you think he would take you on?” But a more serious difficulty was Mellanby, who said the MRC could not support me if I worked with Bernal. They wanted to see me doing something more biological. I decided to take A. V. Hill’s advice and try my luck at Cambridge, if someone there would have me.
I visited the physiologist Richard Keynes, who talked to me as he ate his sandwich lunch in front of his experiment. He was working on ion movement in the giant axon of the squid. I talked to the biochemist Roy Markham, who showed me an interesting result he had recently obtained with a plant virus. Typically he described it in such a cryptic manner (I was not yet familiar with the way nucleic acid absorbed ultraviolet light) that I could not at first grasp what he was telling me. Both were helpful and friendly but neither had any space to offer me. Finally I visited the Strangeways Laboratory, headed by Honor Fell, where they did tissue culture. She introduced me to Arthur Hughes. They had had a physicist at the Strangeways—D. E. Lea—but he had died recently and his room was still vacant. Would I like to work there? The MRC agreed and gave me a studentship. My family also helped me financially so that I had enough to live in lodgings and still had some money to buy books.
I stayed at the Strangeways for the better part of two years. While I was there I worked on a problem they were interested in. Hughes had discovered that chick fibroblasts in tissue culture could engulf, or phagocytose, small crumbs of magnetic ore. Inside the cell these tiny particles could be moved by an applied magnetic field. He suggested I use their movements to deduce something about the physical properties of the cytoplasm, the inside of the cell. I was not deeply interested in this problem but I realized that in a superficial way it was ideal for me, since the only scientific subjects I was fairly familiar with were magnetism and hydrodynamics. In due course this led to a pair of papers, one experimental and one theoretical, in Experimental Cell Research—my first published papers. But the main advantage was that the work was not too demanding and left me plenty of time for extensive reading in my new subject. It was then that I began in a very tentative way to form my ideas.
Some time during this period I was asked to give a short talk to some research workers who had come to the Strangeways for a course. I recall the occasion vividly, since I tried to describe to them what the important problems in molecular biology were. They waited expectantly, with pens and pencils poised, but as I continued they put them down. Clearly, they thought, this was not serious stuff, just useless speculation. At only one point did they make any notes, and that was when I told them something factual—that irradiation with X rays dramatically reduced the viscosity of a solution of DNA. I would dearly love to know exactly what I said on that occasion. I think I know what I would have said, but the memory is so overlaid with the ideas and developments of later years that I feel I can hardly trust it. Nor, as far as I know, have my notes for the talk survived. However, what I probably discussed was the importance of genes, why one needed to discover their molecular structure, how they might be made of DNA (at least in part), and that the most useful thing a gene could do would be to direct the synthesis of a protein, probably by means of an RNA intermediate.
After a year or so I went to Mellanby to report progress. I told him that I was getting results on the physical properties of cytoplasm but that I had spent much of my time in trying to educate myself. He looked rather skeptical. “What does the pancreas do?” he asked. I had only the vaguest ideas about the function of the pancreas but I managed to mumble something about it producing enzymes, hastily adding that my interests did not lie so much in organs as in molecules. He seemed temporarily satisfied.
I had visited him at a fortunate moment. On his desk lay the papers proposing the establishment of an MRC unit at the Cavendish to study the structure of proteins using the method of X-ray diffraction. It was to be headed by Max Perutz, under the general direction of Sir Lawrence Bragg. To my surprise (because I was still very junior), he asked me what I thought about it. I said I thought it was an excellent idea. I also told Mellanby that now that I had a background in biology, I would like to work on protein structure, since I felt my abilities lay m
ore in that direction. This time he raised no objection, and the way was cleared for me to join Max Perutz and John Kendrew at the Cavendish.
3
The Baffling Problem
IT IS TIME to step aside from the details of my career to consider the main problem. Even a cursory look at the world of living things shows its immense variety. Though we find many different animals in zoos, they are only a tiny fraction of the animals of similar size and type. J. B. S. Haldane was once asked what the study of biology could tell one about the Almighty. “I’m really not sure,” said Haldane, “except that He must be inordinately fond of beetles.” There are thought to be at least 300, 000 species of beetles. By contrast, there are only about 10, 000 species of birds. We must also take into account all the different types of plants, to say nothing of microorganisms such as yeasts and bacteria. In addition, there are all the extinct species, of which the dinosaurs are the most dramatic example, numbering in all perhaps as many as a thousand times all those alive today.
The second property of almost all living things is their complexity and, in particular, their highly organized complexity. This so impressed our forebears that they considered it inconceivable that such intricate and well-organized mechanisms would have arisen without a designer. Had I been living 150 years ago I feel sure I would have been compelled to agree with this Argument from Design. Its most thorough and eloquent protagonist was the Reverend William Paley whose book, Natural Theology—or Evidence of the Existences and Attributes of the Deity Collected from the Appearances of Nature, was published in 1802. Imagine, he said, that crossing a heath one found on the ground a watch in good working condition. Its design and its behavior could only be explained by invoking a maker. In the same way, he argued, the intricate design of living organisms forces us to recognize that they too must have had a Designer.
What Mad Pursuit Page 3
