What Mad Pursuit

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.

The main difference of approach was that Jim and I had an intimate knowledge of the way the α helix was discovered. We appreciated what a strong set of constraints the known interatomic distances and angles provided and how postulating that the structure was a regular helix reduced the number of free parameters drastically. The King’s workers were reluctant to be converted to such an approach. [...] I believe there were at least two others. Neither Jim nor I felt any external pressure to get on with the problem. This meant that we could approach it intensively for a period and then leave it alone for a bit. Our other advantage was that we had evolved unstated but fruitful methods of collaboration, something that was quite missing in the London group. If either of us suggested a new idea the other, while taking it seriously, would attempt to demolish it in a candid but nonhostile manner. This turned out to be quite crucial. [...] However, I don’t believe all this amounts to much. 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. Both of us had decided, quite independently of each other, that the central problem in molecular biology was the chemical structure of the gene. The geneticist Hermann Muller had pointed this out as long ago as the early 1920s, and many others had done so since then. What both Jim and I sensed was that there might be a shortcut to the answer, that things might not be quiteas complicated as they seemed. Curiously enough, I believed this partly because of my very detailed grasp of the current knowledge of proteins. 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.

I think that there is a lesson here for those wanting to build a bridge between two distinct but obviously related fields (a possible modern example would be cognitive science and neurobiology). I am not sure that reasoned arguments, however well constructed, do much good. They may produce an awareness of a possible connection, but not much more. Most geneticists could not have been easily persuaded to learn protein chemistry, for example, just because a few clever people thought that was where genetics ought to go. They thought (as functionalists do today) that the logic of their subject did not depend on knowing all the biochemical details. The geneticist R. A. Fisher once told me that what we had to explain was why genes were arranged like beads on a string. I don’t think it ever occurred to him that the genes made up the string!

What makes people really appreciate the connection between two fields is some new and striking result that obviously connects them in a dramatic way. One good example is worth a ton of theoretical arguments. Given that, the bridge between the two fields is soon crowded with research workers eager to join in the new approach.

The path to success in theoretical biology is thus fraught with hazards. It is all too easy to make some plausible simplifying assumptions, do some elaborate mathematics that appear to give a rough fit with at least some experimental data, and think one has achieved something. The chance of such an approach doing anything useful, apart from soothing the theorist’s ego, is rather small, and especially so in biology. Moreover I have found, to my surprise, that most theorists do not appreciate the difference between a model and a demonstration, often mistaking the latter for the former.
In my terminology, a “demonstration” is a “don’t worry” theory [...] That is, it does not pretend to approximate to the right answer, but it shows that at least a theory of that general type can be constructed. In a sense it is only an existence proof. Curiously enough, there exists in the literature an example of such a demonstration in relation to genes and DNA.

Physics is also different because its results can be expressed in powerful, deep, and often counterintuitive general laws. There is really nothing in biology that corresponds to special and general relativity, or quantum electrodynamics, or even such simple conservation laws as those of Newtonian mechanics: the conservation of energy, of momentum, and of angular momentum. Biology has its “laws,” such as those of Mendelian genetics, but they are often only rather broad generalizations, with significant exceptions to them. The laws of physics, it is believed, are the same everywhere in the universe. This is unlikely to be true of biology. We have no idea how similar extraterrestrial biology (if it exists) is to our own. We may certainly consider it likely that it too will be governed by natural selection, or something rather like it, but even this is only a plausible guess.
What is found in biology is mechanisms, mechanisms built with chemical components and that are often modified by other, later, mechanisms added to the earlier ones. While Occam’s razor is a useful tool in the physical sciences, it can be a very dangerous implement in biology. It is thus very rash to use simplicity and elegance as a guide in biological research. While DNA could be claimed to be both simple and elegant, it must be remembered that DNA almost certainly originated fairly close to the origin of life when things were necessarily simple or they could not have got going.
Biologists must constantly keep in mind that what they see was not designed, but rather evolved. It might be thought, therefore, that evolutionary arguments would play a large part in guiding biological research, but this is far from the case. It is difficult enough to study what is happening now. To try to figure out exactly what happened in evolution is even more difficult. Thus evolutionary arguments can usefully be used as hints to suggest possible lines of research, but it is highly dangerous to trust them too much. It is all too easy to make mistaken inferences unless the process involved is already very well understood.