Is analysis of 'functional design' bad science?

Yesterday I gave a talk about my research to a three-lab group of evolutionary biologists at the university across town. The audience was quite skeptical of both my results and my conclusions. At the time this was quite stimulating (the question period went on for half an hour), but it left a bad taste in my mouth. I think I'm going to send them the email below.

Subject: Well, that was interesting...

Hi everyone,

Although I quite enjoyed Friday's extended discussion of my methods and my conclusions, I think the critiques were largely unfounded.

I was unfamiliar with the term 'functional design' as a method of investigating adaptation, and B—'s negative attitude to it left me wondering if I had misunderstood his explanation. But after reading up on it I agree that my approach is indeed analysis of functional design - I'm using a detailed study of a phenomenon to draw inferences about how selection has acted on it - and I don't understand the objections. Surely this is a sensible first step in understanding the evolution of any attribute or process. Before undertaking complex and time-consuming analyses using the comparative method or Lenski-style laboratory evolution experiments, we should always closely examine the attribute or behaviour we're interested in, to see if such studies are warranted, and to clarify the hypotheses that such studies would test.

Here's a made-up example: Suppose we want to know why lizards of some species sometimes rapidly nod their heads up and down. The behaviour is too specific to just be chance. Should we immediately start traveling the world to find out which species nod their heads on a diagonal, and which with a circular motion? And should we populate an island with a mix of lizards, assigning a series of grad students to see if the head-nodders slowly increase in frequency? Of course not. First we should find out the circumstances where head-nodding occurs, and the events that precede and follow it. If only males nod their heads, and only when females are present, and if copulation is always preceded by nodding, then we would sensibly hypothesize that head-nodding is a courtship behaviour. And we would test this hypothesis directly, perhaps by presenting females with plastic model males that did or didn't nod, or by seeing whether males prevented from nodding failed to reproduce. If these experiments left some important questions unanswered, more difficult studies might be warranted.

The same logic applies for molecular and microbiological phenomena, where we need to bring an evolutionarily-knowledgeable mind to the phenomenon in question.

Here's a real example. In this case, initial observations suggested selection for recombination, but this was not supported by more thorough analysis. The E. coli recBCD genes were first discovered because mutations in them dramatically reduced the efficiency of homologous recombination in conjugation experiments. That is, when the conjugative plasmid F is used to transfer DNA from a 'donor' cell into a recBCD-mutant cell, the DNA rarely recombines with the homologous sequences in the recipient chromosome. Initially researchers assumed that the function of these genes was to promote recombination, and mechanistic studies found that the RecBCD complex acted sometimes as a nuclease (degrading one DNA strand) and sometimes as a helicase (unwinding two DNA strands). This seemed to make sense: because homologous recombination is initiated by single DNA strands, these activities increase the recombination frequency.

Because the researchers assumed that these genes evolved for recombination, at first they didn't pay much attention to another phenotype of the recBCD mutants - most of the cells in a mutant colony or culture were dead. And the lethality wasn't associated with recombination of DNA from donor cells, but occurred under conditions where no gene transfer could happen. Years later, when they got around to investigating the cause of the lethality, they found that recBCD mutants were severely defective for DNA replication, because the nuclease and helicase activities are needed to repair double-strand breaks in DNA and to restart replication forks after they encounter DNA damage. Furthermore, the recombination-promoting activities appear to be exactly the same as those that facilitate DNA replication and repair.

Many molecular biologists still treat the two consequences of RecBCD action (recombination and replication/repair) as equally important, but as evolutionary biologists we know that the strength of selection matters. The selection coefficients for the recombination consequence can be estimated by the frequency with which conjugation transfer of chromosomal alleles occurs, multiplied by the frequency with which transferred alleles will increase recipient fitness, and divided by the frequency with which they will decrease recipient fitness. This is going to be a very small number, both because transfer of chromosomal genes by conjugation is rare in natural populations and because evolution-of-sex theory shows that recombination's benefits are typically small. A generous estimate of its upper limit might be 0.0001, but it could be negative if transferred alleles are more often harmful than beneficial, or if the incoming DNA triggers harmful repair reactions. On the other side, although the selection coefficient for the repair/replication consequence of RecBCD activity hasn't been directly measured, in lab cultures it's probably somewhere between 0.1 and 0.3.

So, is it worth doing comparative-method and lab-evolution studies of the hypothesized recombination benefit of the recBCD genes? I say no, for two reasons. First, the hypothesis is unfounded. The above analysis (of functional design) has identified a very large selective force arising from the need for DNA replication and repair, and provides no evidence of selection for the ability to promote recombination. Second, because the replication/repair selection is so strong, if the comparative-method and lab-evolution studies did find any apparent effects of selection for recombination, we would have to suspect that these arose from confounding effects of selection for replication and repair. Excluding these effects would be very difficult given the relative magnitudes of the selection forces.

I should clarify that the molecular analysis of RecBCD and of other proteins that influence recombination is not my work but that of many molecular biologists, and that these experts share the conclusion that these proteins primary (and perhaps only) selected function is DNA replication and repair.   That is, over evolutionary time, any selection arising from recombination must have been far weaker than selection arising from replication and repair.  The mechanistic information about conjugation and transduction that I provided in my talk was not my work either, and although I'm the only one who has formalized the evolutionary considerations, the conclusions are also shared by these experts. When I began independent research I chose to focus on transformation because the limited information available about its mechanism and regulation was not enough to support any conclusions about its function. Now I think there is.

I wonder if the fundamental problem the group had with my talk was that you found my conclusion distasteful (F— literally so, judging by the faces he was making). To clarify, my conclusion was that, in bacteria, no processes have been selected for the ability to promote homologous recombination between different lineages. I'm not saying that homologous recombination is never beneficial for bacteria - clearly sometimes it is and sometimes it isn't. And I'm not saying that lateral gene transfer between distant lineages has never been beneficial - analysis of genome sequences has revealed many examples where it has. But the benefits of recombination have not fed back on the processes responsible for it in any way that can be easily detected.

Thanks for inviting me. The discussion after my talk was stimulating, and I'd be happy to continue it either by email or in another talk.

Rosie

p.s. I'm attaching a pdf of a old review I wrote.

p.p.s. F—'s suggestion that I should qualify my unpalatable conclusion by adding something like 'the available data suggests' smacks of the kind of 'teach the controversy' strategy used by creationists. All scientific conclusions are based on the available data, and mentioning this serves only to imply that in this case the available data is weak or otherwise suspect.