jeff smith

So far, most of my research with bacteria has been experimental—experimental in the sense that I manipulate the genes or environment of bacteria in the laboratory and look at how those manipulations affect fitness, population dynamics, and evolution. One of the great strengths of experimental science is that it lets you change one variable at a time and keep everything else constant. That way, you can be sure that your results are caused by that variable and not something else. And because microbes evolve so quickly, you can use experiments to directly test the predictions of evolutionary theory. All these things are great.

One of the big disadvantages of the experimental approach, though, is that it tells you how evolution can happen—not necessarily how it does happen in the natural world. The best we can do in the lab is often still very different than an organism’s natural habitat. Experimental approaches also don’t tell you how general a result is. When you get a result, you hope that it holds for other bacteria in other environments, but there’s no guarantee that it should be so. Only by repeating those experiments in other systems do you get an idea about generality—and no one wants to perform, publish, or fund work that’s just repeating what other people did and getting the same results.

For these reasons, I’ve been becoming more interested in molecular evolution. The information in DNA and protein sequences reflects the actual evolutionary history of organisms in their real-world environment. It’s hard to observe or experiment on microbes in their natural habitat, but it’s not that hard to look at their DNA. And there’s lots of sequence data already available. Of course, sequence analysis has its disadvantages, too. Correllation is not causation, so if you see that two things are associated with each other it’s always possible that the real cause is some unknown third thing. It can also be difficult to exclude alternative explanations for results. Some people in my field feel these problems to be large and dismiss sequence-based studies as “retrospective evidence” and thus inferior to “prospective” experimental studies. But the way I see it, we have so much of this data these days—why not use it? Anything we can use to better understand out how the natural world works is a good thing, in my book. Why can’t experimental and sequence-based approaches complement each other?

This has been on my mind recently after reading an interesting paper by Fidelma Boyd, Salvador Almagro-Morenoand, and Michelle Parent.

Bacterial genomes are fluid things. Something like 30% of the genes in an E. coli cell may not even be present in the E. coli cell next to it. Often these differences in gene content are viruses laying dormant in the genome, waiting for the right trigger to emerge and find a new host. In other cases, they are clusters of genes called genomic islands that kind of look like viruses—they have a few genes with similar sequences—but don’t seem to have all the pieces necessary to make viruses on their own. What are they doing there? Microbiologists are interested in genomic islands because, aside from containing virus-like genes, they often also have genes that make bacteria more harmful or resistant to antibiotics.

Phage P2 (right) and its freeloader P4 (left). © Institute for Molecular Virology, U. Wisconson-Madison.

There are at least two possible answers. One is that genomic islands are degraded phage (viruses of bacteria). They were once infectious, but at some point mutation inactivated one or more genes necessary for that lifestyle. Now, as the mutations continue to accumulate, they’re sliding toward evolutionary oblivion and their own inevitable deletion. Another possibility is that genomic islands are mobilizeable. This means that they can’t make phage particles on their own, but they can use the proteins made by other phage in the same cell. They’re a kind of freeloader. Phage P4 is a well-known example.

How do we tell? Boyd and coauthors addressed this question using the tools of molecular evolution. If genomic islands were degraded phage, phylogenetic trees made from their protein and DNA sequences would show genomic islands scattered among the other phage. Because they’re degraded and nonfunctional, they’d be recent derivatives and wouldn’t persist long over evolutionary time. All the branches leading to genomic islands would be near the tips of the tree. If, on the other hand, genomic islands are mobilizeable and have a long evolutionary history of freeloading on self-sufficient phage, then phylogentic trees would show them clustering together on their own branch.

Boyd and coauthors made phylogenetic trees using the sequences of integrase (Int) genes from many different genomic islands and phage. They found that virtually all the genomic islands clustered together in their own branch that included P4. This evidence is consistent with the mobilizeable hypothesis and inconsistent with the degradation hypothesis. Boom—we’ve managed to exclude one hypothesis, the other one survived an empirical test, and we’ve made a tiny step forward in understanding the natural world. Science in action.

I wish Boyd and company tested another prediction of the degradation hypothesis: that degraded phage should show evidence of relaxed selection. Once phage get inactivated, natural selection no longer weeds out harmful mutations in their sequences. One kind of evidence for relaxed selection is a larger fraction of pseudogenes—sequences of DNA that once used to be genes but are now prematurely truncated or shifted so that they no longer make functional proteins. Another is that more of the DNA sequence changes should cause differences in the protein sequence (dN/dS, for those who know such things). Not finding these things, or at least putting lower limits on how much they occur, would be another strike against the degradation hypothesis and more support for the mobilizeable hypothesis. The data’s already there—the analysis just needs to be done.

It’s also wierd that this paper is published as a review article rather than a peer-reviewed results paper in a molecular evolution journal. Because it’s not, and because the paper glosses over many of the details of the phylogenetic analysis, I find myself taking the results with a grain of salt. Hopefully this work can at some point be redone or extended at some point so I can be more confident in the results.

In any case, this is an example of how sequence analysis lets us get at an evolutionary question—how does natural selection act on genomic islands?—that can’t be answered by experiments alone. We need both types of data. The experiments show us that mobilization can happen and the sequences show us that these elements have been persisting and evolving just fine without their own phage-producing genes.

I’ve been helping a friend who’s writing their first scientific papers. Scientists almost always read papers for the content and pay little attention to the craft of what they’re reading. So when it comes to writing your own for the first time, it’s not always obvious how to proceed.

It helps to know that most scientific writing is pretty formulaic. Journal articles and grant applications have a pretty set structure that journals and funding agencies expect you to follow. The abstract/introduction/methods/results/discussion format is pretty ingrained these days. Even within those sections there are standard ways of doing things. Nature, for example, gives authors a sentence-by-sentence template to follow in their abstracts. Only in review articles or perspective pieces do you have much leeway in terms of large-scale organization.

In a way, scientific writing is like Bebop. Bebop song structures are pretty rigid and predictible. It’s always head/solos/head. The creativity is all in the melody, the chord changes, and the solos. For scientists, the interesting part of a paper isn’t the writing or organization—it’s the experiments, the results, and what they say about the natural world. Everything else is secondary.

Normally when you submit a paper to a journal, you include a cover letter as a kind of formality. It’s the equivalent of a handshake and an exchange of basic information: number of words in the paper, suggestions for reviewers, contact information, stuff like that. With prominent journals, though, these cover letters are a Big Deal. Most submissions to Science and Nature don’t even get sent out for review, and the cover letter is where you make the case that your paper is interesting and important enough to pass the first cut. The fate of your paper depends on less than a page of text that only a couple people may ever read. It’s crazy.

In preparation for our imminent submission, I read whatever I could find about these letters. Pamela Hines, senior editor of Science, gives a talk on how to publish in Science that I found useful. Some things these editors ask themselves when they get a submission are: How is this novel? Is it a big enough scientific advance? Is it widely interesting? They look for work that solves a long-standing problem, overturns conventional wisdom, or has wide implications. It’s your job to figure out what’s most interesting about your work to the largest number of people and put that front and center. It’s a kind of self-promotion that a lot of people find difficult.

Nature asks authors for a 100-word summary of their paper for nonscientists. I found a forum post by a Nature staffer claiming that these summaries aren’t actually used by the journal—they’re to help authors think about what makes their findings interesting to a wide audience. It’s funny, a little bit devious, and I think it works.

I’m of a mixed mind about the whole process. I can see how high non-review rates can lead to spin being valued more than content. In my field these journals have published several papers that really didn’t deserve such high visibility. But at the same time, I can see how revising my current manuscript with these journals in mind has made it a stronger, clearer work. I guess we’ll soon see if the editors agree.

While putting my Myxo work together into a talk, and trying to present it all with some semblance of coherence, I had the opportunity to think about where the evolution of microbial cooperation is as a field and where I think it should go.  The way I see it, the most important open are these:

Is shared genes the primary evolutionary mechanism maintaining cooperation in microbes? By shared genes I mean that the benefits of cooperation are preferentialy experienced by individuals who also share the alleles for expressing the cooperative trait.  This process can be described as kin selection or group selection.  Shared genes is widely thought to be the primary mechanism for the evolution of cooperation in animals—is it true for microbes, too?  And what role do other mechanisms like enforcement, direct benefits, or pleiotropic constraint play?

What is the primary cause of genetic correlations among individuals? Limited dispersal, kin recognition, green-beard genes, infectious gene transfer, or something else?  Do cooperative traits themselves create genetic correlations through their effect on migration and motility?  The important part of these questions is getting at what IS happening, not just what CAN happen.

How does social evolution shape microbial traits? Many traits seem to involve interactions between individuals (quorum sensing, biofilms, and so on), but are these traits cooperative in the evolutionary sense of increasing the fitness of other individuals?  How does the magnitude, regulation, or form of these traits differ from that what they would evolve to be if they did not have social effects?  To what extent do microbes actively alter their behavior in response to social conditions?  Which traits are adaptations and which are only side-effects of some other function?

How do social traits change over evolutionary time? Are social traits under stabilizing selection or do they evolve in evolutionary arms races?  How often are they lost?  If cheaters occur in natural habitats, do they persist because of selection or recurrent mutation?

What are the origins of microbial cooperation? What traits were co-opted into becoming the building blocks of cooperation?  Worker behavior in social insects, for example, is a modified form of maternal behavior.  Are the benefits of cooperative traits the same now as they were originally?  How many times have similar cooperative traits originated?  Are cooperative traits usually acquired by horizontal gene transfer or invented de novo?

We’ve been considering submitting one of our recent projects to one of the prominent journals (Science, Nature, PLoS Biology and so forth). The process is somewhat different than normal. Not just the formatting, but also the focus on how interesting the work is to people outside the field and to a non-science audience. I’m a bit averse to the press release, spin-heavy mentality that can go along with these things sometimes, but it has helped me focus better on the bigger picture.

Since this is my first time doing this sort of thing, it’s also been a little bit intimidating. I’ve found it helps to mentally compare our work with other related papers that have been published in these journals, rather than some imaginary standard. That helps.