Advice to a Young Scientist 
by P.B. Medawar.
Harper and Row, 109 pp., £4.95, February 1980, 0 06 337006 9
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This is a guide book to the scientific scene, full of urbane wisdom, happy phrases and entertaining examples. ‘How can I tell if I am cut out to be a scientist?’ Medawar asks. He dismisses curiosity (it killed the cat) and suggests that scientists need something for which ‘exploratory impulsion’ is not too grand a name. But what about delight and wonder at the works of nature? Without these you might as well join Scotland Yard instead. What else draws people into science? It seems to me that, just as the Church did in former times, science offers a safe niche where you can spend a quiet life classifying spiders, away from what E.M. Forster called the world of telegrams and anger. To the ambitious poor, science offers a way to fame or reasonable wealth that needs no starting capital other than good brains and prodigious energy.

In answer to the question ‘What shall I do research on?’ Medawar tells young people to choose an important problem and to become apprenticed to a senior scientist. I was lucky as a young man to find both. The biochemist husband of a cousin of mine tipped me off about the importance of haemoglobin, the protein of the red blood cells, and I found a scientific father in the physicist W.L. Bragg, who taught me a lot and vouchsafed his great name to secure support for my research during the long lean years before I solved my problem. Others are not always so fortunate. Medawar himself once told me how the geneticist J.B.S. Haldane loved all the world while his technician could enter his room only at the danger of his life. A scientist of my acquaintance threatened to sack a collaborator who wanted to publish an experimental result that confirmed my own rather than my acquaintance’s theory. The French biologist André Lwoff wrote: ‘L’art du chercheur c’est d’abord de se trouver un bon patron.’ To me, this means one who suggests good ideas, helps his students along without spoon-feeding or domineering, gives them public recognition for their work and later helps them to become established as independent scientists. How do you find one? The best way is to ask the older research students.

Medawar counsels beginners not to spend too much time studying books and learning techniques, but rather to get on with their problem. This reminded me of Francis Crick’s motto, written in large letters on the wall behind his desk: ‘Reading Rots the Mind.’ A young theoretician friend of ours stated his reasons more explicitly: ‘I don’t see why I should read the bloody nonsense other people write when I can read my own papers.’ I find that young scientists tend to read too little, especially in subjects that are peripheral to their own narrow problem.

Medawar decries sexism and racism in science. Women should be encouraged, he writes, because the world has become such a complicated place that it cannot be kept going without the intelligence and skill of half the human race. On the other hand, he utters dire warnings to both men and women against marrying a scientist, unless they realise that their spouses will be in the grip of a powerful obsession which they cannot share and which may drive these spouses to their laboratories even on Christmas morning. The passage reminded me of Odile Crick’s complaints about her husband’s prolonged periods of in explicable broodiness. On the question of racism, Medawar reflects on the remarkable number of outstanding Jewish scientists who have emerged from Budapest and Vienna. I often wonder whether they would have reached such heights if they had not been driven out of the narrow confines of their native countries and faced with the stimuli, the opportunities and challenges of a larger world. I find it symbolic that Joy Adamson, when she lived in Vienna in the Thirties, kept a dachshund (I still have a picture of the two in my old photograph album), but after she emigrated to Kenya kept a lioness. In Vienna’s small world I had no idea that scientists of the calibre of J.D. Bernal, W.L. Bragg, David Keilin and Dorothy Hodgkin existed: how then could I have even tried to emulate them? It was Cambridge that made me, not Vienna.

The longest chapter in Medawar’s book concerns scientific life and manners. I like his admonition not to regard manual work as inferior, and not to expect to be able to carry out experimental work by ‘issuing instructions to lesser mortals who scurry hither and thither to do one’s bidding’: he looks upon experimentation as a form of thinking. He tells scientists to be humble, because ‘it is no longer taken for granted that science and civilisation stand shoulder to shoulder in a common endeavour to work for the betterment of mankind.’ He warns scientists against turning into overbearing knowalls, against pretending to a wide culture they don’t possess, against boasting of atheism, against one-upmanship – science-manship, he calls it – and against the snobbism that holds up pure as against applied research as the more noble pursuit. Medawar explains that in the 17th century ‘pure’ was used for those sciences of which the axioms were known, not through experiments, but through intuition, revelation and self-evidence. This kind of pure scientist felt one-up on a man who dissected dead animals – a snobbism which has lasted more than 300 years. He quotes Thomas Pratt, one of the founders of the Royal Society, writing in 1667: ‘The first thing that ought to be improved in the English nation is their industry ... by works and endeavours, and not by the prescription of words.’ Le plus ça change, le plus c’est la même chose.

Medawar tells scientists to defend science against philistine prejudice, to be tolerant and generous towards collaborators, and to treat technicians as colleagues rather than underlings. ‘There is nothing about being a scientist that should or need deafen him to the entreaties of conscience ... If he does enter upon morally questionable research and then publicly deplores it, his beating of the breast will have a hollow and unconvincing sound.’ Medawar is adamant about scientific truthfulness. A wrong interpretation of an experiment, a wrong hypothesis, are forgivable, but an unrepeatable experimental result is not. In science, as in other walks of life, temptation and sin take many guises. Medawar relates the case of a scientist who submitted a fellowship thesis to an Oxford college with results cribbed from one of the fellowship electors. Scientific plagiarism, as immortalised in Tom Lehrer’s song ‘Nicolai Ivanovich Lobachevsky’, is becoming more common because generally the victim has no redress.

Medawar admonishes the young to formulate hypotheses, but not to identify with them. ‘The intensity of a conviction that a hypothesis is true has no bearing on whether it is true or false.’ Voltaire put it more strongly: ‘In fact, no opinion should be held with fervour. No one holds with fervour that 7 × 8 = 56 because it can be shown to be the case. Fervour is only necessary in commending an opinion which is doubtful or demonstrably false.’ I am told that when anybody contradicted Einstein he thought it over, and if he was found wrong he was delighted, because he felt that he had escaped an error. Such behaviour needs great self-control: hypotheses are often conceived only after passionate and prolonged endeavour to get at the truth.

Scientists therefore feel possessive about the priority of their work. During the 22 years it took me to solve the structure of haemoglobin I was often beset by fears that someone else might get there first. Artists, Medawar argues, are at an advantage here, because the problems that confront them do not have unique solutions. Yet despite that fear, free discussion of one’s ideas is always preferable to keeping them to oneself. Medawar quotes the saying: ‘Anyone who shuts his own door keeps out more than he lets out.’ I am suspicious of scientists who tell me that others have pinched their ideas: far from preventing people from stealing it, I have always had to ram any new idea of mine down their throats. Even scientists are unbelievably conservative.

Medawar devotes a chapter to the giving of lectures and the writing of scientific papers. He tells speakers whose listeners fall asleep ‘to get some comfort from the thought that no sleep is so deeply refreshing as that which, during lectures, Morpheus invites us so insistently to enjoy.’ ‘I feel disloyal,’ he notes, ‘but dauntlessly truthful in saying that most scientists do not know how to write.’ He therefore tells young scientists to read, to study good models and to practise. Good writing, he says, is almost always shorter than bad, and the short is also more memorable, as exemplified by Lord Bacon’s comment on an ambitious political rival: ‘He doth like the ape, that the higher he climbs the more he shows his arse.’ For models Medawar suggests various philosophers and essayists who wrote or still write brilliant prose – but a young man may find it hard to emulate Bertrand Russell. I sometimes tell people to read Rutherford’s papers on radioactivity and the structure of atoms: all his experiments were conclusive, and he presented them without artifice, but with unrivalled logic and clarity, leaving no conceivable loophole. Another sound piece of advice would be to read Medawar’s books. A young American once wrote that he wanted to spend a year with me ‘in order to participate in the total work of the laboratory at the conversational level’. I have been helped to avoid such circumlocution by a pamphlet called ‘Plain Words’ which Churchill asked Sir Ernest Gowers to write in order to teach civil servants better style. Medawar chides scientists for putting off the hard task of writing up their research, but he overlooks the real reason for their stalling, which is that before the results have been formulated, their meaning may not have been clarified in the investigator’s own mind. It is this hard thinking that some – but not all – scientists shun. W.L. Bragg, rather like Mozart, who composed the overture to The Marriage of Figaro in a single night, used to take the material for a paper home in the evening and return next morning with a lucid and crisp manuscript in which not a word had to be altered.

Advice to a Young Scientist contains chapters on Experiment and Discovery, and on the Scientific process, in which Medawar summarises the philosophy set out in his earlier books. He has always tried to elevate the scientific process in the public mind by stressing its imaginative and passionate character. Here he writes: ‘The truth is not in nature waiting to declare itself, and we cannot a priori know which observations are relevant and which are not. Every discovery, every enlargement of the understanding, begins as an imaginative preconception of what the truth might be.’ It is a romantic representation of some kinds of scientific activity such as Jacques Monod’s search for the mechanisms that control the growth of bacteria. One of Monod’s former colleagues wrote of him: ‘With Jacques I learned that in science one gets excited every day: either by a new hypothesis or by the results supporting it, or by those which one day later will shake the hypothesis and require a new one.’

On the other hand, Fred Sanger, who has just won his second Nobel Prize in Chemistry, or Dorothy Hodgkin, the only British woman Nobel Laureate, approached their problems differently. They started to explore the chemical formula and three-dimensional structure of insulin without any preconception: worse, they didn’t even have any clear idea of how they were going to find out what they wanted to know. Fred Sanger does not work, à la Popper, by formulating hypotheses and then performing experiments to test them by falsification. Instead, he invents new chemical methods capable of solving problems that no one else had even approached, since it was believed that they would defy solution. He did not measure his discoveries against existing paradigms because they opened new worlds where no paradigms existed: no one had thought of overlapping genes before he found them. The process of invention is imaginative, but so far as I know, no philosopher has thought it worth his while to analyse it, because the mind’s creative process is impenetrable.

Medawar writes that the generative process in science is imaginative guesswork, and that heroic feats of intellection are rarely needed. During the first 33 years of my own research imaginative guesswork proved useless: only after my colleagues and I had solved the structure of haemoglobin by X-ray analysis could I begin to guess how the molecule worked. Such classic studies as W.L. Bragg’s solutions of the structures of the common minerals, or Sir Robert Robinson’s elucidation of the chemical formulae of the flower pigments, did involve imaginative guesswork, but coupled to intellection of the highest order. Those were fantastic feats of puzzle-solving. Great feats of the intellect are surely the very pillars of many scientific advances, and not only in the physical sciences.

This brings me back to scientific method. According to Popper and Medawar, research consists in the formulation of imaginative hypotheses that are open to falsification by experiment. They call this the hypothetico-deductive method. They argue that no hypothesis can ever be completely proved, but that it can be disproved experimentally or modified so that it gradually corresponds more and more closely to the truth. Medawar writes: ‘A scientist is a searcher after truth, but complete certainty is beyond his reach.’ This applies to relativity, quantum mechanics and some aspects of immunology, Medawar’s own subject, but not to most of chemistry. Bragg’s structures and Robinson’s formulae are not approximations to the truth subject to revision: they are as solid as the ground we stand on. Any student who sets out to redetermine the atomic structures of calcite, quartz or beryl is likely to be disappointed. Even so, scientists should take heed. All too often they begin their papers by advancing a hypothesis and then describe experiments designed to prove it, which implies that already at the outset they have closed their minds to the possibility that it might be false.

Medawar encourages young people to enter science by describing it as an unending frontier. This is still true of immunology or tumour biology, but it would be misleading to say the same of all subjects: many of the ablest physicists are now turning either to biophysics or to astrophysics or geophysics for lack of fundamental problems in pure physics. Nonphysicists argue that physics was believed to be a closed subject in the 1880s, and that in the following 20 years radioactivity, the quantum and relativity opened new worlds. It does not look as though there exists today a whole world of physical phenomena that has escaped detection, though great advances are still possible in applied physics in its widest sense. In other subjects, too, it has become hard to find an important problem that is not already being worked on by crowds of people in several continents.

Partly because of the overcrowding and partly because of the fantastic sophistication of modern scientific methods, young people entering science now need more talent and determination to make their way than they did in the 1930s, when Medawar and I started off. Good science is no rosebed, but the romance is still there. The thrill of discovery outweighs the drudgery, the despair at one’s inadequacy, the fight for financial support, the setbacks and mistakes, the long hours and the nagging fear of being overtaken. A discovery is like falling in love and reaching the top of a mountain after a hard climb all in one, an ecstasy induced not by drugs but by the revelation of a face of nature that no one has seen before, and that often turns out to be more subtle and wonderful than anyone had imagined. A true scientist derives this feeling not only from his own discoveries, but also from those of his colleagues.

Research is supported by the state and by industry, not primarily to finance such expensive ecstasy, but in the hope that it will produce useful results. During the past ten years there has been much discussion about the proportion of funds that ought to be allocated to basic and to goal-oriented research, and it has become difficult for young people to decide which way they should turn, especially since it is much easier to get funds for the latter. In the biomedical field, which Medawar and I have in common, the way to goal-oriented research has often been opened by an unforeseen result emerging from the pursuit of a basic problem.

In the early 1960s, for example, Baruch Blumberg, an American biochemist, set out to search for unusual proteins in the blood serum of different people, because he believed that the appearance of a new protein in a given population would provide a clue to the way evolution works. One day he examined the blood of a haemophilic patient and found a protein which he had never encountered before. His evolutionary theories caused him to wonder whether other people’s blood might exhibit an immune reaction against that protein, but the only one he found that did so was the blood of an Australian aborigine. Why? Blumberg was determined to find the answer. He travelled to the Australian bush to collect samples from aborigines and examined thousands of other blood samples from all over the world. Three years of intensive detective work led Blumberg and his colleagues to the discovery that the strange protein in the haemophiliac’s serum was a virus: the long-searched-for hepatitis B virus. This disease was common among Australian aborigines, so that the blood of many of them contained antibodies that reacted against the virus. Hepatitis B used to be transmitted frequently by blood transfusion because there was no way of finding out whether the donor was a carrier. Thanks to Blumberg’s isolation of the virus, hospitals can now detect the virus in blood offered for transfusion, which has much reduced the incidence of hepatitis B. Blumberg’s discovery has also opened the way to research on the production of a vaccine, which is now about to bear fruit. Blumberg has said: ‘I could not have planned the investigation at its beginning to find the cause of hepatitis B. This experience does not encourage an approach to research which is based exclusively on goal-oriented programmes.’ Blumberg’s story does, however, encourage young scientists to keep their eyes open.

Medawar writes that ‘a senior scientist ... should always hear behind him a voice such as that which reminded a triumphant Roman emperor of his mortality, a voice that should now remind a scientist how easily he may be, and how often he probably is, mistaken.’ One of my teachers, the great biologist David Keilin, started his career reading zoology in Paris. His PhD supervisor told him to work on the sex organs of the earthworm. One day Keilin brought his professor a worm whose sex organs had been invaded by a parasite. The professor told Keilin to throw it away and get on with his thesis, but Keilin threw away the worm and studied the parasite. He discovered it to be the larva of a fly that laid its eggs on the earthworm. The larvae hatched there and then ate up the worm. This observation solved the riddle of the life cycle of that fly and set Keilin on a trail of discoveries which made him famous. This leads me to my final advice to young scientists. Take no notice of what your elders tell you. Since I have now become an elder myself I shall leave it to a young logician to make what he can of this paradox.

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