Looking back, it can now be seen that “On Protein Synthesis” is a mixture of good and bad ideas, of insights and nonsense. Those insights that have proved correct are the ones based mainly on general arguments, using data established for some time. The incorrect ideas sprang mainly from the more recent experimental results, which in most cases have turned out to be either incomplete or misleading, if not completely wrong.
Even at this stage an erroneous idea had crept in. It is clear that I thought of the RNA in the cytoplasm—in the microsomal particles, as they were then called (the word ribosome had not yet come into general use)—as a “template"; that is, as having a rather rigid structure, comparable to the double helix of DNA though probably having only a single chain. It was only later that I realized that this was too restrictive an idea, and that “tape” might be nearer the truth. Just as a ticker tape has no rigid structure except momentarily when it is actually in the ticker machine, I eventually realized that the RNA directing the synthesis of a protein need not be rigid, but could be flexible, except for that part that coded the next amino acid to be incorporated. Another consequence of this idea was that the growing protein chain did not have to stay on the template but could start to fold itself up as synthesis proceeded, as indeed had been suggested earlier.
There was another more serious mistake in my thinking at that time. I will not spell out all the details (they are given in the paper), but in effect I was making mistakes because I was confusing the mechanism itself (of protein synthesis) with completely separate mechanisms that were controlling it. Thus, in brief, because some experiments suggested that free leucine (one of the amino acids) was needed for RNA synthesis, it was concluded that there were probably common intermediates for protein and RNA synthesis, which could be used to synthesize one or the other, as required. In fact it is the control mechanism that requires free leucine if RNA synthesis is to continue, presumably because new RNA is not needed if the cell is so starved that free leucine is not available. I believe one can easily fall into this mistake of mixing up effects due to the nature of a mechanism itself with effects due to its control when trying to unscramble a complex biological system.
Another mistake in this general category is worth noting at this point. This is to mistake a minor process, evolved to improve the performance of the major process, for the major process itself and hence draw false conclusions about the latter. Alternatively one can be ignorant of the minor process and hence conclude that a postulated mechanism for the major process could not work.
Consider, for example, the rate of making errors in DNA replication. It is not difficult to see that if an organism has a million significant base pairs, then the error rate per step of replication should not be as great as one in a million. (The exact formulation has been given rather elegantly by Manfred Eigen.) Human DNA has about three billion base pairs (per haploid set) and although we now know that only a fraction of these have to be replicated accurately, the error rate cannot be greater than about one in a hundred million (speaking very roughly) or the organism would be torpedoed in evolution by its own errors. Yet there is a natural rate for making replication errors [due to the tautomeric nature of the bases] that it would be difficult to reduce to below about one in ten thousand. Surely, then, DNA cannot be the genetic material since its replication would produce too many errors.
Fortunately we never took this argument seriously. The obvious way out is to assume that the cell has evolved error-correcting mechanisms. Because the double helix carries two (complementary) copies of the sequence information, it is easy to see how this might be done. The observed error rate (the mutation rate) would be due to the errors in the error-correcting mechanism and thus can be reduced to a very low value. Leslie Orgel and I actually wrote a private letter to Arthur Kornberg, pointing this out and predicting that the enzyme he was studying that replicated DNA in the test tube (the so-called Kornberg enzyme) should contain within itself an error-correcting device, as indeed it does. DNA is, in fact, so precious and so fragile that we now know that the cell has evolved a whole variety of repair mechanisms to protect its DNA from assaults by radiation, chemicals, and other hazards. This is exactly the sort of thing that the process of evolution by natural selection would lead us to expect.
There is perhaps one other type of mistake that is worth mentioning. 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.
Consider the following 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.
However, there is a counterargument to this. The X-ray spots do not extend to very small spacings. Why do the spots fall off in this way? It could either be that the structure is highly regular but is distorted in some random manner in the fiber, or it could be that part of the structure is regular and part is irregular. If so, why should not the irregular part carry the genetic information? If this is the case, then solving the regular part of the X-ray structure, using the spots that do exist, will never tell us what we want to know—the nature of the genetic information—so why bother to do it?
Knowing the answer, the fallacy in this negative argument can be seen. It is true indeed that the X-ray data on fibers can never tell us the intimate details of the base sequence. What the data did lead to was the model of the double helix with base pairing as its key feature. At the low resolution associated with these spots, one base pair looks rather like any of the other three, but what the model showed us, for the first time, was the existence of base pairs, and this turned out to be crucial for the rapid development of the subject.
What, then, was the proper argument that should have been used? Surely it is that the chemical nature of genes is a subject of overwhelming importance. Genes were known to occur on chromosomes, and that was where DNA is found. Thus anything to do with DNA should be pursued as far as it can be, since one can never be sure in advance what may turn up. While one should certainly try to think which lines are worth pursuing and which are not, it is wise to be very cautious about one’s own arguments, especially when the subject is an important one, since then the cost of missing a useful approach is high.
My father, Harry Crick, as a young man.
(Author’s collection.)
My mother, Anne Elizabeth Crick, in 1938.
(Author’s collection.)
Myself with my younger brother Tony.
(Author’s collection.)
My uncle Arthur Crick, who helped me financially.
(Author’s collection.)
Odile during the Second World War, just before we met.
(Author’s collection.)
My son Michael, at Stockholm, 1962.
(Author’s collection.)
Our house, “The Golden Helix,” 19-20 Portugal Place, Cambridge.
(Author’s collection.)
Myself with our two daughters, Gabrielle [left] and Jacqueline, taken about 1956.
(Author’s collection.)
Invitation to one of our parties, 1960.
(Author’s collection.)
Jim Watson [left] with me in front of our demonstration model of the DNA double helix, summer 1953. (From J. D. Watson’s The Double Helix, Atheneum, New York, 1968.)
Jim Watson, as he appeared in the August 1954 edition of Vogue “with the bemused look of a British poet.”<
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(Courtesy of Diana Edkin.)
Myself in 1956. The strange tie is that of the RNA Tie Club.
(Courtesy of Francis DiGennaro & Son, Baltimore, Md.)
A studio portrait of Rosalind Franklin, taken when she was about twenty-six.
(Courtesy of Jenifer Glynn, Cambridge.)
Maurice Wilkins, about 1955.
[Courtesy of Maurice Wilkins.)
J. D. Bernal, known to his Mends as “Sage.”
(Courtesy of the Royal Society, London.)
Sir Lawrence Bragg—Willie to his close friends.
(Courtesy of the Royal Society, London.)
Linus Pauling in the 1950s, holding models of two molecules.
(Courtesy of the Archives, California Institute of Technology.)
Max Delbrück in conversation, June 1959.
(Courtesy of the Archives, California Institute of Technology.)
Meeting of the RNA Tie Club
[from left to right: myself, Alex Rich, Leslie Orgel, Jim Watson).
(Courtesy of Alex Rich, Cambridge, Mass.)
Max Perutz (right) handing over the MRC Laboratory of Molecular Biology to Sydney Brenner in 1979.
(Author’s collection.)
Maurice Wilkins, Max Perutz, myself, John Steinbeck, Jim Watson, and John Kendrew at the Nobel ceremony, 1962.
(Courtesy of Svenskt Pressfoto, Stockholm.)
King Gustaf VI Adolf of Sweden, with Odile at the Nobel banquet, 1962.
(Courtesy of Svenskt Pressfoto, Stockholm.)
Myself dancing with my elder daughter Gabrielle at the Nobel Prize celebration, 1962.
(Courtesy of International Magazine Service, Stockholm.)
The example just given about DNA was a hypothetical one, but I have been caught in this way more than once. Experiments had shown that transfer RNA (tRNA) molecules existed, that amino acids were associated with them, and that there were probably many types of tRNA molecules, each with its own particular amino acid. The obvious next step was to purify at least one type of tRNA away from all the others so that more could be learned about it, as it was obviously better to work where possible on a pure species than on a mixture.
The problem was how to fractionate such a mixture. I argued to myself that since all tRNA molecules had to do a similar job and in particular to fit into the same place, or set of places, at the ribosome, they would all be very similar to each other and thus difficult to separate. The only way to separate them, I felt, was to use some method that tried to latch onto the amino acid joined to the RNA, by going for the particular side group of that amino acid and choosing one, such as cysteine, that was chemically both active and unique. I even tried to do this experimentally.
The argument was not totally silly, but it turned out I was wrong. Though I could not know it at the time, most tRNA molecules have many modified bases. These modifications alter their chromatographic behavior and so make it possible to separate them by much simpler fractionation methods since, in the first instance, only one of them is wanted. There is no need to specify in advance which tRNA to study, one simply experiments on the one that is easiest to get hold of. As the molecular biologist Bob Holley found, this turned out to be the tRNA for alanine, since it ran differently on a chromatography column from all the others. Again the message to experimentalists is: Be sensible but don’t be impressed too much by negative arguments. If at all possible, try it and see what turns up. Theorists almost always dislike this sort of 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 (see the one described on page 97). 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.
Lionel Penrose, who died in 1972, was a distinguished geneticist who in his later years held the prestigious Galton chair at University College, London. He was interested in the possible structure of the gene (which not all geneticists were at that time). He also loved doing “fretwork” (as it is called in England), making objects out of plywood with a fine saw. He constructed a number of such models to demonstrate how genes might replicate. The wooden parts had ingenious shapes, with hooks and other devices, so that when shaken they would come apart and join together in an amusing way. He published a scientific paper describing them and also a more popular article in Scientific American. An account by his son, Roger Penrose, the distinguished theoretical physicist and mathematician, appears in his father’s obituary written for The Royal Society.
I was taken to meet Lionel Penrose and his models by the zoologist Murdoch Mitchison. I tried to show a polite interest but had some difficulty in taking it all seriously. What to me was bizarre was that this was in the middle 1950s, after the publication of the DNA double helix. I tried to bring our model to Penrose’s attention but he was far more interested in his own “models.” He thought that perhaps they might be relevant for a pre-DNA period in the origin of life.
His wooden pieces, as far as I could see, had no obvious relation to known (or unknown) chemical compounds. I cannot believe that he thought genes were made of pieces of wood, yet he didn’t seem at all interested in organic chemicals as such. Why, then, was his approach of so little use? The reason is that his model did not approximate the real thing closely enough. Of course, any model is necessarily a simplification of some sort. Our DNA model was made of metal, but it embodied very closely the known distances between chemical atoms and, in the hydrogen bonds, took into account the different strengths of the various chemical bonds. The model did not itself obey the laws of quantum mechanics, but it embodied them to some extent. It did not vibrate, due to thermal motion, but we could make allowance for such vibrations. The crucial difference between our model and Penrose’s was that ours led to detailed predictions on matters that had not been explicitly put into the model. There is perhaps no precise dividing line between a demonstration and a model, but in this case the difference is very clear. The double helix, since it embodied detailed chemical features, was a true model, whereas Penrose’s was no better than a demonstration, a “don’t worry” theory.
It was all the more odd that his “model” came well after ours. What was its fascination for him? I think, at bottom, he liked to do fretwork, to play with little pieces of wood, and he was delighted that his favorite hobby could be used to illuminate one of the key problems in his professional life—the nature of the gene. I suspect that, on the other hand, he disliked chemistry and didn’t want to be bothered with it.
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.”
A good model in biology, then, not only should address the problem in hand but if at all possible should serve to unite evidence from several different approaches so that various sorts of tests can be made of it. This may not always be possible to do straight away—the theory of natural selection could not immediately be tested at the cellular and the molecular level—but a theory will always command more attention if it is supported by unexpected evidence, particularly evidence of a different k
ind.
11
The Missing Messenger
THE NEXT EPISODE I want to touch on concerns what we now call messenger RNA. The double-helical structure of DNA had given us a theoretical framework that was invaluable as a guide to research, since it not only tied together approaches that at first sight seemed to have no connection with each other, but it suggested radically new experiments that could not have been conceived without the DNA model as a guide. Unfortunately, our thinking contained one major error. It was uncertain at that time whether any protein synthesis took place in the nucleus of the cell (where most of the DNA was), but everything suggested that the majority of it took place in the cytoplasm. In some way the sequence information in the nuclear DNA had to be made available outside the nucleus, in the cytoplasm. The obvious idea, which predated the DNA model, was that this messenger was RNA. This was the basis of the slogan coined by Jim Watson: “DNA makes RNA makes protein.”
It was known that cells very active in protein synthesis had more RNA in their cytoplasm than cells that were less active. By the late 1950s it had been shown that most of their RNA was in small particles, now named ribosomes, that consisted of RNA molecules plus a mixture of proteins. What more natural than to assume that each ribosome synthesized just one protein and that its RNA was the postulated messenger RNA? We assumed that each active gene produced a (single-stranded) RNA copy of itself, that this was packaged in the nucleus with a set of proteins to help it do its job and then exported to the cytoplasm where it directed the synthesis of the particular polypeptide chain coded for by this RNA. Each ribosome, working in concert with the transfer-RNA molecules (see appendix A), would in some way embody the details of the genetic code (surmised, but not yet discovered) so that the four-letter language of the RNA could be translated into the twenty-letter language of the proteins.
What Mad Pursuit Page 14