In response to Donohue's argument that Fourier analysis of X-ray diffraction data collected by Maurice Wilkins and his
colleagues did not rule out models of DNA with other base pairs than those posited by Watson and Crick, Crick here reviewed
key concepts of crystallography and helical diffraction theory on which the debate hinged. He also cited the biochemical
evidence for his and Watson's model of DNA then available. Crick came to the conclusion that Donohue's "hypothetical
models of base-pairs are theoretically not to be trusted without further justification." As he had in his response to
Donohue in the pages of Science, Crick in his letter once again challenged him to build models of his proposed structures,
which Crick insisted was the only way by which the validity of Donohue's claims could be decided.
Number of Image Pages:
5 (562,010 Bytes)
ca. 15 July 1970
Original Repository: Wellcome Library for the History and Understanding of Medicine. Francis Harry Compton Crick Papers
After reading your letter of 9 June I think we had better go back and start at the beginning.
First a remark about "effectively centric" reflections. These are those for which there are only two alternative
choices for the phase, rather than a continuous choice. It is normally arranged so that this choice is either 0 or pi, but
since phase is partly a matter of convention (since the origin is strictly arbitrary, although convenience may suggest the
easiest choice) this is not a strict requirement. For a structure like DNA, a reflection does not necessarily have to have
B = 0 to be "effectively centric".
However, the important question, to which I do not yet know the exact answer, is what fraction of the intensity of a DNA diffraction
pattern comes from effectively centric reflection? I have asked the people at King's College to look into this. When
I know the answer I will write to you again.
Next I must take up a point from your earlier letter. We would both agree that whether a structure is centric or not it is
possible, under certain circumstances, to arrive at a false solution. However, it is the general opinion of crystallographers
that it is significantly easier to make a mistake in an acentric structure than in a similar centric one. You appear to deny
this, but I cannot believe you really mean it. To make matters precise, do I have your permission to quote your opinion as
follows? "I understand from Donahue (personal communication) that he considers it just as easy to arrive at a false solution
for a centric structure as for a similar acentric one".
Next I should like to make some general remarks about solving crystal structures. In the first place, in spite of the excellence
of the x-ray pictures taken at King's, the resolution is somewhat limited compared to the single crystals of most small
organic molecules. Thus, even if the phases were known rather accurately it is unlikely that atoms would be resolved enough
so that the structure could be deduced without knowing the chemistry of the material. I think you would in any case argue
that it is fair to accept the chemistry as given. The basic reason why this is often acceptable in crystallography is that
there is often no reasonable doubt about the chemistry. So much so that if a first structure contradicts what is firmly established
most people take another look at the structure. In fact, you yourself have done much useful work in spotting incorrect structures,
using just this technique.
You will no doubt want to point out to me that this has dangers. That unless the chemical evidence is overwhelming it can
happen that mistakes will creep in through assuming chemical facts which were actually incorrect. Moreover, you could say
that the fact that a structure does not fit our preconceptions is a hint that it may be wrong, not a proof. Nevertheless,
it is I think legitimate to take certain "chemical" facts as given when trying to solve a structure, and I hope you
will agree that this, in principle, is acceptable. If so, it remains to set out what facts can be accepted in the case of
Now the general chemical formula (as opposed to the detailed base sequence) is surely known beyond reasonable doubt, not only
from many chemical studies, but also for crystal structures of small, related, molecules. Thus, the "topology" of
the molecule is known - i.e. what is connected to what by chemical bonds (as opposed to hydrogen bonds, etc.)?
Next the length of all the chemical bonds is known to sufficient accuracy. That is, if one were in fact incorrect it would
be by such a small amount that it is highly unlikely to affect the problem. The bond angles are also known, but not to such
a high degree of precision. However, I doubt if anyone would accept without special justification a "tetrahedral"
angle of 135 degrees, or 75 degrees.
About the dihedral angles one must be more careful. Although the bases may not be strictly quite planar the deviation from
planarity is likely to be so small that it will not cause any trouble. On the other hand, although both you and I would be
unhappy if the C4 - C5 bonds were in the eclipsed configuration, I think it would be wiser not to forbid this in the first
place and to let the dihedral angle have any value. The same would be said about the planarity or otherwise of the ribose
ring. In short, I should be surprised if we could not sit down and work out a set of acceptable rules for the chemical bonds.
Moreover, these rules would probably approximate very closely to those actually used at King's.
It follows that the totality of "acceptable" configurations is defined by rather few parameters. These are, in fact,
the dihedral angles and the position and orientation of the "monomer" in the unit cell. It is difficult to estimate
the number of "effective" parameters because of the constraints (e. g. the monomers must join head to tail, the ribose
ring must be closed, atoms should not penetrate, etc.) but it is quite small.
The chemical structure is not the only thing that can now be assumed as being beyond reasonable doubt. There are three other
facts which originally could not be assumed, but now have to be considered. They are:
(1) The bases "pair" - the exact way need not be specified - such that A pairs with T, and G with C.
(2) There are two chains in the structure.
(3) The (pairing) chains run in opposite directions.
I shall argue that (1) and (3) are established beyond reasonable doubt, and that (2) is probable though not perhaps quite
The original evidence for "pairing" of the bases came from the base composition of DNA. This evidence still stands,
supplemented by the additional evidence that single-stranded DNA does not usually show one-to-one ratios. However, the overwhelming
evidence comes from the synthesis of synthetic DNA, mainly by Khorana. The original evidence was from repeating sequences,
but more recently, in synthesizing the DNA for a tRNA gene he has constructed many non-repeating sequences. These firmly
establish that for two chains to go together the pairing rules must be obeyed, and also that the two sequences must run in
opposite directions - he has even done a special experiment to prove that if the complementary sequence runs in the same direction
the chains do not pair. These experiments do not, by themselves, say what the mechanism of pairing is, nor do they rule out
the possibility of other base pairs in small amounts, but since the x-ray data looks at the average structure these can safely
be ignored for the time being. There is, of course, lots of other evidence which suggests base-pairing for RNA, such as the
relationship between codon and anticodon, and the paired regions in tRNA (the latter is basically a statistical argument).
Both these lines of evidence, incidentally, suggest that G - U pairs can occur. However, I am ignoring all this data as too
The question of the number of chains is not really in serious doubt, but because of Cavalieri there has been some controversy
about it. What is not in doubt is the mass per unit length. This can, of course, be obtained direct from the crystal data.
It can also be deduced from such techniques as the sedimentation velocity in solution, or the length of a piece of DNA of
known molecular weight as seen in the electron microscope. All these methods agree that the value is near 200 daltons/A,
or two residues per 3A, approximately. However, it is just possible that the structure has four chains, each with a residue
every 6A or so. The best evidence for two chains is from circular DNA molecules which form super coils, and which relax to
a simple circular form after a single break. There is a lot of other indirect evidence, but I am not sufficiently up-to-date
in the subject. If you insisted that four-chain models should not be excluded I would have to agree with you, while saying
that I think them very unlikely.
Now we must come to the screw axis and the symmetry. Do you have any serious doubts about the helical parameters (except
for RNA, where there is an uncertainty)? The argument depends on the absences in the pattern, and is therefore statistical,
but then, curiously enough, so are all arguments for the deduction of symmetry from the x-ray data. The only question is,
is the evidence strong enough? It seems to me it is, but perhaps you have other views.
I would not wish to argue that the symmetry of the unit cell can be deduced from intensity statistics, since this is rather
technical. I would take the view that since other evidence shows the chains run in opposite directions, and since the shape
of the unit cell and the intensity statistics are at least compatible with this, it would be highly surprising if the molecule
did not have (pseudo) dyads perpendicular to the fibre axis, and rather unlikely that the cell would not use them. Obviously
models having parallel chains, with molecules statistically up and down need not now be considered.
What then, is required from the x-ray data, since so much of the general properties of the structure have been established
by other methods? What the x-ray data is required to do is
(1) show that it is compatible with a possible model
(2) establish the stereochemical nature of the base-pairing.
Now, as you know, base-pairing has been observed in single crystals of small molecules. These show the G - C pair to be as
predicted, but the A - T pair usually in a different form, using the N7 of adosine. Thus, the exact pairing of the bases
is a problem, and it would be most useful if we could say that the x-ray data made it highly probable.
We now come to the question set out in your letter. "Does model building followed by electron density calculations furnish
proof of a structure?" I think this question is, at the moment, in too strong a form. We would agree that if the effective
parameters were few, the experimental data very extensive, and the result completely acceptable stereochemically, then the
structure was probably correct. You have had a lot of experience with small crystals, but practically none with such awkward
polymers as DNA. Thus, it is very difficult to arrive at criteria which we can agree are acceptable in this case. That is
why any alternative model, preferably produced by someone other than the original worker, is preferable. (See the history
of the structure of collagen if you want an amusing example!) However, we have a more limited problem immediately before
us. Can the x-ray data for DNA eliminate a model, and in particular one with a different specified base-pairing?
The King's people claim they can eliminate it. I claim that your counter-examples are not relevant, because you over-simplify
the problem by considering only base-pairs, and not the complete structure, and because you consider acentric examples, whereas
the DNA structure is, to some extent, effectively centric. To what extent it is effectively centric and how much this matters
remains to be determined.
However, I have established to my own satisfaction that you do not yet have an adequate theoretical grasp of helical diffraction
theory, that your arguments from hypothetical models of base-pairs are theoretically not to be trusted without further justification,
that the theoretical position is complicated and indeed likely to lead to "long acrimonious arguments", whereas the
production of an acceptable alternative model by you would settle the argument in your favour. I still cannot see any other
way for you to prove your point. What about it? After all, it would be very useful experience for you to have a shot at
it. I am sure I could persuade the King's group to make the experimental data available if you have not got it already.