(or: “The most important thing is choosing what to work on”)
Francis Crick started a scientific career late, and deliberated for some time about what field to go into. He’d previously done some postgraduate research in experimental physics…
… the dullest problem imaginable, the determination of the viscosity of water, under pressure, between 100° and 150° C…
… but mercifully, the Luftwaffe intervened:
By good fortune a land mine had blown up the apparatus I had so laboriously constructed at University College, so after the war I was not obliged to go back to measuring the viscosity of water.
This lead to some time in “scientific intelligence” at the Admiralty, and a bit of pondering about what to do next.:
By this time I was reasonably sure that I didn’t want to spend the rest of my life designing weapons, but what did I want to do? I took stock of my qualifications. A not-very-good degree, redeemed somewhat by my achievements at the Admiralty. A knowledge of certain restricted parts of magnetism and hydrodynamics, neither of them subjects for which I felt the least bit of enthusiasm. No published papers at all. The few short Admiralty reports I had written at Teddington would count for very little. Only gradually did I realize that this lack of qualification could be an advantage. By the time most scientists have reached age thirty they are trapped by their own expertise. They have invested so much effort in one particular field that it is often extremely difficult, at that time in their careers, to make a radical change.
He ended up picking a line of work by observing himself gossip with others, and keeping track of what he talked about the most:
One day I noticed that I was telling [my friends], with some enthusiasm, about recent advances in antibiotics—penicillin and such … 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.
Through a few connections from his Admiralty and physics work, this lead him to molecular biology. It seems he carried with him a high standard for the rate of scientific progress:
What I had acquired, however indirectly, was the hubris of the physicist, the feeling that physics as a discipline was highly successful, so why should not other sciences do likewise?
Crick obviously spent a lot of time thinking about why people end up where they do. One interesting phenomenon he mentions is selection for optimism:
It is interesting to note the curious mental attitude of scientists working on “hopeless” subjects. Contrary to what one might at first expect, they are all buoyed up by irrepressible optimism. I believe there is a simple explanation for this. Anyone without such optimism simply leaves the field and takes up some other line of work.
One thing Crick is very clear about — if he and Watson excelled in anything, it was in figuring out which problems were the most important, and just sticking to them. For example, this is how he describes Watson figuring out the A-T, C-G pairing scheme:
…most discoveries have an element of luck in them. The more important point is that Jim was looking for something significant and immediately recognized the significance of the correct pairs when he hit upon them by chance—”chance favors the prepared mind.”
And again, on why nobody writes books about the discovery of collagen:
What was important was not the way [DNA] was discovered but the object discovered—the structure of DNA itself. You can see this by comparing it with almost any other scientific discovery. Misleading data, false ideas, problems of personal interrelationships occur in much if not all scientific work. Consider, for example, the discovery of the basic structure of collagen… Its discovery had all the elements that surrounded the discovery of the double helix. The characters were just as colorful and diverse. The facts were just as confused and the false solutions just as misleading. Competition and friendliness also played a part in the story. Yet nobody has written even one book about the race for the triple helix. This is surely because, in a very real sense, collagen is not as important a molecule as DNA.
The major credit I think Jim and I deserve, considering how early we were in our research careers, is for selecting the right problem and sticking to it. It’s true that by blundering about we stumbled on gold, but the fact remains that we were looking for gold.
And again (on DNA structure):
We could not at all see what the answer was, but we considered it so important that we were determined to think about it long and hard, from any relevant point of view. Practically nobody else was prepared to make such an intellectual investment…
I also enjoyed Crick’s thoughts on the process of making theories. You shouldn’t be too quick to shoot them down:
One should not be too clever. Or, more precisely, it is important not to believe too strongly in one’s own arguments. This particularly applies to negative arguments, arguments that suggest that a particular approach should certainly not be tried since it is bound to fail.
Here’s a fascinating example:
As far as I know this argument was never made but it could easily have been in, say, 1950. Rosalind Franklin had shown that fibers of DNA, especially when pulled carefully and mounted under conditions in which the humidity was controlled, could give an X-ray diffraction pattern of the so-called A form, which has many fairly sharp spots. Using the theory of Fourier Transforms, it can be seen immediately that these spots show the existence of a structure with a regular repeat. If DNA were the genetic material it could hardly have a regular repeat, since it could carry no information. Thus DNA cannot be the genetic material.
In the same vein, he stresses the importance of being able to create new approaches quickly:
It is amateurs who have one big bright beautiful idea that they can never abandon. Professionals know that they have to produce theory after theory before they are likely to hit the jackpot. The very process of abandoning one theory for another gives them a degree of critical detachment that is almost essential if they are to succeed.
Yet — and on this point he is quite vociferous — you mustn’t fall in love with your own models:
I cannot help thinking that so many of the “models” of the brain that are inflicted on us are mainly produced because their authors love playing with computers and writing computer programs and are simply carried away when a program produces a pretty result. They hardly seem to care whether the brain actually uses the devices incorporated in their “model.”
This made me say “huh”:
In parenthesis let me say that the English school of molecular biologists, when they needed a word for a new concept, usually use a common English word such as “nonsense” or “overlapping,” whereas the Paris school like to coin one with classical roots, such as “capsomere” or “allosterie.” Ex-physicists, such as Seymour Benzer, enjoyed inventing new words ending in “-on,” such as “muton,” “recon,” and “cistron.” These new words often obtained rapid currency.
This made me laugh:
[Lawrence Bragg] was one of those scientists with a boyish enthusiasm for research, which he never lost. He was also a keen gardener. When he moved in 1954 from his large house and garden in West Road, Cambridge, to London, to head the Royal Institution in Albemarle Street, he lived in the official apartment at the top of the building. Missing his garden, he arranged that for one afternoon each week he would hire himself out as a gardener to an unknown lady living in The Boltons, a select inner-London suburb. He respectfully tipped his hat to her and told her his name was Willie. For several months all went well till one day a visitor, glancing out of the window, said to her hostess, “My dear, what is Sir Lawrence Bragg doing in your garden?”