As Crick noted in this letter, the details of the structure of DNA were not yet conclusively established in 1977, beyond the
base pairing and the antiparallel arrangement of the sugar-phosphate backbones, more than two decades after Watson and Crick
proposed that it was a double helix. In the absence of definitive experimental proof, some researchers continued to suggest
alternative structures. In this instance, Crick responded to an argument by Rodley that the two chains of DNA were straight
rather than helical. He found such a structure unlikely, but nonetheless suggested how experimental proof for it might be
produced, if at all.
Item is a photocopy.
Number of Image Pages:
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1977-05-11 (May 11, 1977)
Rodley, G. A.
Original Repository: Wellcome Library for the History and Understanding of Medicine. Francis Harry Compton Crick Papers
Well, you are certainly trying hard but you'll have to do a lot better before most people will believe it, if only because
your structure is so ugly (though ingenious) and ours is so pretty! However you are quite right that while the base-pairing
is well established and there's no doubt the chains run in opposite directions, the details of the structure are less
well supported. For the reasons that Aaron Klug set out in his letter of 25 March to Richard Bates I don't think much
of most of the general diffraction agruments that you are using. Nor am I impressed with a series of weak bits of evidence
or plausibility arguments. What we need is a striking experiment that everybody will be able to recognize as correct. So
far I have been only been able to think of two.
1) If your structure were really side-by-side, then a relaxed unnicked circular DNA should, on melting, come apart into two
separate circles. This could easily be shown with present techniques using SV40, polyomer or better still, a deletion mutant
with a smaller size. You should consult the two papers, by Depew and Wang, and by Pulleybank et al in PNAS (1975) 72, 4275----4284,
and the other papers (for example, by Keller) quoted there. They show the Gaussian distribution of L (see my PNAS (1976)
73, 2639) produced by temperature. For a true SBS structure one of those relaxed, or nearly relaxed bands, would, on denaturing
give two separate chains, as is indeed found for a circular DNA with one nick in it but is not found if both chains are intact.
(The sedimentation co-efficients are very different -- consult the literature.) This would be a completely convincing demonstration
of the general truth of your idea and a disproval of our structure.
Unfortunately your structure, as described, is not exactly SBS but has a slow twist in it. To prove this idea (which, incidentially,
is surely less "appealing" than a true SBS) you have to use ethidium bromide plus the nicking-closing enzyme, etc.,
to produce a "supercoiled" molecule for which L has been reduced from the small value you predict to zero. This is
possible but rather harder work.
I must stress, however, that without this evidence no hardheaded molecular biologist is likely to believe your idea so I suggest
you promote this type of experiment instead of trying to prove your structure with a lot of rough model building and rather
2) The only other way I can see that would carry conviction would be to obtain (largish) quantities of a short (10 to 15 bp)
stretch of DNA with a defined sequence -- preferably with a couple of G-C pairs at each end, crystallize it and solve the
structure by isomorphous replacement to a highish resolution -- in effect what was done for tRNA (which, please note, in spite
of your remarks about irregular backbone arrangement, etc., has no trace of your structure and plenty of the double helix
predicted by the fibre x-ray work. But one must concede this is RNA, not DNA). The best way would be for someone to synthesize
such a DNA (as Khorana does) for then an unusual base or two could be included to which a heavy atom could conveniently be
attached. The main points are that the structure should be solved, by isomorphous replacements, without any assumptions about
helices or SBS and that the resolution should be adequate. (Both conditions were fulfilled for the tRNA crystals.) I realize
that this is not easy but without such data who will believe your detailed model, even if the first experiment were to work.
I should stress that we are concerned with the (approximate) configuration of "normal" DNA in solution. As I explained
previously, if the double helix is correct in solution then your model cannot be correct for most of the DNA on the nucleosome,
because the |L| between the two is too small. Whether your model ever occurs in special circumstances is another
matter which we can, I feel, usefully postpone for the moment.
Finally I should add that John Cairns has written to me that Wally Gilbert claims that your model has already be disproved
because "D-loops remove exactly the right number of supercoils for the classical B form model". I know what a D-loop
is -- it occurs in the replication of mitochondrial DNA and possibly elsewhere -- but at this moment I cannot put my hand
on the evidence Gilbert quotes. However I hope to track it down, possibly when I am at Cold Spring Harbor in early June,
and if I do I will let you know.
Forgive me for being so discouraging. I will be most surprised if your model turns out to be correct but you have done a
useful job (more useful than Donohue did) in pointing out the rather fragile nature of some of the x-ray evidence.