This post is a guest contribution from John Stanton-Geddes, a postdoctoral associate in the Department of Plant Biology at the University of Minnesota. John currently studies the genetic architecture of legume-rhizobium symbiosis in Medicago truncatula, as part of the same lab group as NiB contributor Jeremy Yoder.
If you’d like to write a guest post for Nothing in Biology Makes Sense!, email Jeremy.
Two weeks ago I was fortunate to attend the Evolution Society Conference in Ottawa. I saw many great talks, missed even more great talks and had the opportunity to hobnob with many luminaries of evolutionary biology. One theme that emerged through the meeting was “The genetic basis for [insert trait here]. While this goal of mapping phenotype to genotype has been a primary goal of many evolutionary ecologists since the first QTL mapping studies, it has recently come under strong criticism, notably in a fantastic paper by Matthew Rockman in the journal Evolution last year, but also by Pritchard and Di Rienzo 2010 and in a forthcoming article by Ruth Shaw (full disclosure: Ruth was my PhD advisor) and Mike Travisano. Here’s my take on the current state of Genotype to Phenotype (G-P) research from Evolution 2012, and where I’m excited to see it go.
G-P: stuck on Mendelian traits
Much of the leading G-P work is being done with the usual suspect of ecological genetic model organisms: monkeyflower, sticklebacks, sunflowers, butterflies and mice, as well as some agricultural species (rice). No surprise here, as answering the big questions requires considerable time and resources that won’t be available to each lab’s pet system (at least until 3rd generation sequencing rolls into town).
I didn’t catch all the talks at Evolution 2012, and am certainly leaving some out, but here are two examples that had premier billing. Robin Hopkins, from the University of Texas, presented very elegant work that identify two genes underlying changes in flower color between sympatric populations of Phlox in Texas, and showed that fitness differences among these may maintain reproductive isolation. Rowan Barrett had a double-header with armour in sticklebacks, and color polymorphism in field mice. With sticklebacks he explained how a single gene jointly influenced armour development and growth rate, and showed rapid evolution for rapid growth and reduced armour in freshwater sticklebacks. With deer mice, he described a large field project to examine natural selection on coat color, presumably adaptive as camouflage. For those who’ve followed the Hoekstra lab work, no surprise that they’re closely following the Agouti gene.
This is great work and took a lot of time and energy, but it leaves me a bit disappointed. Specifically – do any of these studies address the challenges Rockman made in his paper? Here’s a key quotation from the abstract of his paper:
Although their [quantitative trait nucleotides, QTNs] pursuit is often invoked as a means of addressing the molecular basis of phenotypic evolution or of estimating the roles of evolutionary forces, the QTNs that are accessible to experimentalists, QTNs of relatively large effect, may be uninformative about these issues if large-effect variants are unrepresentative of the alleles that matter.
The clear answer is NO. All of these examples are of traits that are effectively Mendelian, created by genes of large effect, thus if we agree with Rockman’s argument (and if it’s not clear by this point, I do) then these are interesting case studies, but do not tell us about the process of evolution in general. This research was cutting edge 10 years ago when Bradshaw and Schemske (1999) reported a large effect allele (note that this is also a Mendelian trait) putatively responsible for pollinator shifts in monkeyflowers (Mimulus), but should the cutting edge of our field (e.g. Science and Nature publications) still be showing that Mendelian traits that segregate in populations have large effects? It seems that evolutionary ecology work is largely stuck in the “QTN program challenged by Rockman.
To emphasize my point, here’s an incomplete list of talks exploring the genetic basis of a trait compiled by fellow postdoc Jeremy Yoder and myself, categorized by whether the traits are Mendelian or polygenic:
- Phlox flower color
- Mimulus flower color
- Deer mouse pigmentation
- Beach mouse pigmentation
- Stickleback armour
- Heliconius color pattern
- White Sands lizards
- Mimulus annual/perennial life history (though only a few large effect QTLs were discovered)
- Mimulus flower size
- Rice flowering time (Note – though quantitative, it seems that a relatively small number of genes underlies phenotypic differences in flowering time).
- Arabidopsis trichome density
- Lycaedes male genitalia, oviposition preferences
I’d appreciate any contributions to filling in this list, but it’s fairly clear that there is an overemphasis on Mendelian traits relative to polygenic traits proportional to their importance for adaptation in general.
Back to the future? – Fisher’s polygenic model of adaptation
There were a number of talks at the conference that pointed to a direction forward. The most promising work I saw was by John Kelly and colleagues. Kelly experimentally evolved large and small flowered monkeyflowers that differed by many phenotypic standard deviations over 9 generations. In yet to be published work, he described how this (ecologically important!) phenotypic difference was caused by shifts in allele frequency by only 2-5% from the ancestral population. These small differences would likely not be detected by current whole-genome scan methods. While these results are sobering, I think it is important because this sets the bar for studying polygenic adaptation, which is (back on the soapbox) what we should be studying.
Admittedly, some of us may not be interested in experimental evolution. One approach that takes advantage of natural ecotypes is pooled population resequencing Turner et al. 2010. Martin Fischer presented on population re-sequencing of ecotypes of Arabidopsis halleri and found a number of promising genomic regions. There are statistical problems based on the sampling process in this type of experiment that were pointed out by John Kelly, but it sounds like he’s worked out the method to account for this using Fisher’s angular transformation.
So why write this as my first contribution to Nothing in Biology Makes Sense!?
Is the overemphasis of studying Mendelian traits by evolutionary ecologists a problem? I’m not sure. On one hand, studying evolution in natural settings is challenging, so having a few ‘proofs of principle’ can’t be bad. I could further argue that this is the best work out there, so it deserves this premier billing, even if the theoretical basis for major effect alleles is shaky at best.
On the other hand, these studies are being published in high-impact journals and getting top billing at the premier conference in evolution. Young grad students would be foolish to ignore the signaling that “this is what great work that will get you published in Science looks like. Yet this research is no longer cutting edge – it’s been over ten years since Bradshaw and Schemske mapped the first Mendelian trait segregating between species. It’s time that we started studying the true ‘stuff’ of evolution – polygenic traits. Studying these traits will require exciting new research projects, at least partially returning to whole organism experimental quantitative genetics, while continuing to develop genomic methods that can detect polygenic adaptation. A focus on Mendelian traits distracts from this goal.
By writing this, I’m not trying to criticize research that is being done, but hoping to inspire fellow researchers to think of creative experiments to study polygenic adaptation, and encourage grant reviewers, advisors and editors to foster this research.