Thursday, September 19, 2019



Part 2 of a series on choosing a research topic.

One of my favorite songs in college was by Natalie Merchant:

Climbing under 
A barbed wire fence 
By the railroad ties 
Climbing over 
The old stone wall 
I am bound for the riverside 
Well I go to the river 
To soothe my mind 
Ponder over 
The crazy days of my life 
Just sit and watch the river flow 

It still brings me joy to hear the song, and more and more it feels like its about my research process. Academics is so hectic: teach, write proposals, publish, committee meetings, editing... where does one find time to contemplate, to let ideas bubble up and mature? Personally, I find that some of the most valuable time is sitting by water, hence my continued love of the song above.

Which leads me to the question, where do ideas come from? What can you do to generate ideas?

Suggestion 1: Go Forth And Observe: I used to teach a class on Research Methods at UT Austin, aimed at future K-12 science teachers. The students had to come up with their own questions in any area remotely science-like, and do a project. Four projects, actually, of increasing complexity. And finding questions was always hard. So we walked them through an exercise: everyone blew up balloons, then all at once we popped our balloons. It wakes them up. As an aside: if you do this, check that nobody has a latex allergy, PTSD that might be triggered by the sound [we had a veteran in the class once and learned this], and don't hold the balloons close to eyes or they can tear corneas. Then, everyone wrote down five observations: it split into 3 pieces, they are different sizes, it was loud, the inside of the balloon is damp, there are little ripples on the edge of the tear. Then, convert those into questions. Then we discussed which questions were testable in the classical sense (yes/no answers), quantitative (numbers are the answer), and which were untestable. We'd talk about how a well phrased question clearly points you towards what you should do to answer it. And about how poorly phrased or vague questions (why did it make a sound) can be broken down into testable and more specific sub-questions. Its a great exercise, not least because my co-instructor Michael Marder, a physicist, had actually spent two decades working on the physics of that sinusoidal ripple at the margin of the torn rubber (inspired by noticing this at a child's birthday party), and discovered it has applications to predicting how earthquake cracks propagate through the earth's crust. So, students could see how a mundane thing like a balloon can lead to big science.

You can do the balloon exercise, or something like it that's more biological: go out in the woods, or snorkle in a stream or ocean. Watch the animals around you. Visit the greenhouse. Write down observations, and turn them into questions. Write down 50. There's got to be a good one in there somewhere, right?

Suggestion 2: Don't take the first idea or question that you can do. The exercise described above will almost surely lead you to a question that you can answer. But, is it the question that you SHOULD answer? Will other people care about it? If so, why?  There's this idea in economics of "opportunity cost". Sure, writing this blog is valuable. But it is taking time I could otherwise be spending on revising that manuscript for Ecology Letters, or writing lectures for my Evolutionary Medicine class, or preparing my lecture for a fast-approaching trip to Bern and Uppsala. Is this blog the best thing I could be doing with this hour of my day? Choosing a research project is even more prone to opportunity costs: you are embarking on a project that may take you six months, a year, or five years. Sure, you can do it, and you can publish some results. But is it the best and most impactful (variously defined) thing you can do with that time? In general I bet that the first idea that crosses your mind isn't the best idea you'll have. Personally, I had two ideas for research when I first entered grad school, then I went through a series of maybe 6 ideas over the course of my first year, and only landed on my actual project in early fall of my second year. The other ideas weren't bad, just not as exciting to me (and, I think, to others).
Opportuity cost, by SMBC Comics' Zach Weinersmith

Suggestion 3: Don't get stuck on local optima. I love to think of self-education in a research field as a Bayesian Monte-Carlo Markov Chain search on an intellectual landscape. Search widely, visit many different topics and ideas and questions. The ones that you keep coming back to, and spend the most time on, are probably a good indicator of a high posterior probability for your future research. But, again, if you start on an actual project too soon, you limit your ability to explore that intellectual landscape by slowing your search rate and might falsely conclude you are on a great peak for an idea, when really you've just stopped making those long jumps to new places in the intellectual landscape of relevant topics.

Suggestion 4: Know your history There are vast number of ideas, and study systems, stashed away in the literature, going back decades and beyond. As a mid-stage graduate student, I read Ernst Mayr's Animal Species and Evolution, and I was struck by how many hundreds of study systems were left lying by the wayside because someone lost interest, retired, left academia, or whatever. The questions were never fully resolved, just left partly answered. There are so many great ideas and systems waiting for your attention. And the great thing is, when pitching an idea to readers or grant reviewers, they tend to love to see the historical context: it helps to justify in their own mind that this is something interesting, if it is a topic people have been thinking of for a long time. Also, knowing your history helps you avoid repeating it. Being scooped by a contemporary is frustrating, but being scooped by somebody 40 years ago because you didn't know it was done already, that's worse.
Ernst Mayr

Suggestion 5: Read theory. A lot of evolution and ecology students are wary of mathematical theory. That's unfortunate, because it means you are cutting yourself off from a major fountain of inspiration. Learn to read theory, including the equations. It is absolutely worthwhile. Here's why. From my viewpoint, theory does a lot of things that an empiricist should pay attention to. 

First, it makes our thinking more rigorous. For example, it is intuitive to think that co-evolution between host and parasite can lead to frequency-dependent cycles where the host evolves resistance to parasite A, so parasite evolves phenotype B, then hosts evolve resistance to B but thereby become susceptible to A again, so the parasites switch back. Cyclical evolution, maintenance of genetic variation in both players. Sure, its possible, but by writing out the math theoreticians identified all sorts of requirements that we might have overlooked in our verbal model. This cyclical dynamic is harder to get that we might think, an the math helps us avoid falling into a trap of sloppy thinking that leads us down a blind alley. 

Second, and related, the math identifies assumptions that we might not realize we were making. Is assortative mating during sympatric speciation based on a magic trait that affects both mating and adaptation, or a sexual-signalling trait unrelated to adaptation? Do individuals really tend to compete for food more strongly with phenotypically similar members of their population? When writing out theory, those assumptions are often brought into the light of day (though sometimes theoreticians are unclear about them, making implicit assumptions too). These assumptions are often things we empiricists don't know much about. How strongly do females prefer phenotypically  like males within a panmictic population? I didn't know. How many stickleback males does a searching female visit before settling on a mate? No idea... Theory brought my attention to these assumptions, and they become something I can go and measure. So, the assumptions underlying the equations are an opportunity for empirical investigation, with a ready-made justification: "Theory assumes X, so we need to know if/when/where/how often this is biologically valid".

Third and hardest, theory makes predictions: if X is true, then Y should happen. These predictions can, in princple, be tested. But beware: If the entire set of assumptions X are true, then the math argues that Y is inevitable. Is it really worth testing, then? If you don't know that all features of X are true, then the theory no longer guarantees Y. If you fail to demonstrate Y, arguably you weren't actually testing the theory.

Suggestion 6: P-hack and prepare to be surprised. Having read theory, read the literature, and been observant, go back out and do something. Do a little experiment, start a little observational pilot study, just get some data. Now, do something everyone tells you not to: P-hack it. Analyze the data in many possible ways, look for relationships that you might not have identified a priori. Sure, this can lead to false positives. A lot of people argue strongly against unguided post-hoc data analysis for this reason. But we aren't at the stage yet of publishing, this is exploration, an information-finding foray. Here's a concrete example: most stickleback biologists like myself have long treated each lake as a single genetic population and assumed it is well-mixed in terms of genotypes and phenotypes (except in a few lakes with 2 species present). This has practical consequences. This past summer I watched colleagues throw 10 traps into a lake, along a mere 10 meter stretch of shoreline, then take the first trap out and it has >100 fish, so we use them and release the fish from the other 9 traps. BAD IDEA. It turns out, we now know, there is a lot of trap-to-trap variation in morphology and size and diet and genotype that arises from microgeographic variation within lakes. Here's how I got clued into this. A graduate student of mine, Chad Brock, hand-collected ~30 nesting male stickleback from each of 15 lakes in British Columbia, and immediately did spectroscopy to measure color wavelength reflectance on each male. He also happened to note the substrate, depth, and so on, of the male's nest. Six months later, back in Texas, he P-hacked, and noticed that in the first lake he was examining intensively, male color covaried with nest depth: males 0.5 meters deep were redder and males 1.5 meters deep (just meters away horizontally) were bluer. The different-colored males were within maybe 10 seconds' swimming distance of each other. This clued us in to the fact that something interesting might be going on, and we later confirmed this pattern in 10 other lakes, replicated it across years, and ultimately replicated it experimentally as well. I'm not here to tell you about our male color work though. The key point is, theory would have told me to never expect trait variation among individuals at this spatial scale, because gene flow should homogenize mobile animals at this spatial scale. But it doesn't, apparently. Here's a case where theory puts blinders on us, telling us to not bother looking for microgeographic variation. Then, when we P-hacked we were surprised and ultimately cracked open what turns out to be a very general phenomenon that we might otherwise have overlooked. 

(a caveat: P-hacking should't be the end-game, and if you do try that, please at least be totally up front when you write about which analyses are predetermined, and which (and how many) were post-hoc analyses).

Suggestion 7: Have a portfolio. In financial investment theory, it is always recommended that you invest in a portfolio. Some investments (e.g., stocks of start-ups) have the potential to go sky-high, but also the potential to crash out entirely. Other investments are solid safe bets with little risk. If you put all your money in the former, you will either be spectacularly wealthy or lose everything. If you put all your money in the latter, you are guaranteed to have some savings in the future, but maybe just keeping up with inflation. The recommendation, therefore, is to have a portfolio that mixes these alternatives. The same is true in research. There are projects you can do that would be super-cool if they suceeded and gave you a particular answer. They'd make you famous, get you that Nobel Prize your mom has been pestering you about. But, either it might not work at all, or perhaps a negative result is just uninterpretable or uninteresting. High potential reward, high risk.  Or, you could go to the nearest 10 populations of your favorite organism, and do some sequencing and build a phylogenetic tree or a phylogeographic model. Guaranteed to work, not very exciting. Low reward, no risk. Pick some of each to work on, and be aware which is which.

Note also that in economics the optimal ratio of risky to safe investments shifts with time: as you age, you have less time before retirement to recover from a crash, so you want to shift your investments increasingly into the safe category. In science I'd say the opposite is true. A consequence of the tenure system is that once people get tenure, they become less risk-averse, more likely to shoot the moon (a card game reference, not a ballistic one) for that wildly risky but high-reward idea. As a grad student, though, if you want to end up at an R1 university (disclaimer, other careers are great too!) don't get sucked into a safe-bet-only philosophy, because it probably won't make the splash you need to be recognized and excite people.

Suggestion 8: Have a toolbox. Whatever question you pick, you'll need a toolkit of skills to answer it. Bioinformatics. Bayesian hierarchical modeling. ABC. Next generation sequencing. GIS. CRISPR. These skills are "just tools". But, sometimes academic departments choose to hire faculty who can bring in skill sets that existing faculty lack (e.g., so we can have you help us analyze the data we collected but don't really know how to use). And, those "just tools" are often highly sought-after by industry. So, if you are thinking of moving into NGOs, or the private sector, often the skills you gain along the way turn out to be far more valuable for landing a job, than the splashy journal article you published.

Suggestion 9: Don't be dissuaded. Here's the riskiest advice yet. If you have a truly transformative idea, don't be dissuaded by nay-sayers. There will be people on your PhD committee, or among your colleagues and peers, who think you are full of $#it, on the wrong track, or it just won't be feasible.  Listen to them. And defend yourself, rather than just abandoning your idea. Sure, you might be wrong. But, they might be wrong too. A personal example. Tom Schoener was on my PhD committee. I was intimidated by him, he was so foundational to ecology, so smart, so prolific. So when I presented my research plan, I was initially dismayed by his response. My ideas on disruptive selection and competition depended on the assumption that individuals within a population eat different foods from each other. So, whoever eats commonly-used foods competes strongly, whoever eats rarely-used foods escapes competition, and voila, you have disruptive selection. Tom, however, pointed to a series of theoretical papers from the 1980s by Taper and Case, and by Rougharden, to argue that selection should ultimately get rid of among-individual diet variation. Therefore, Tom said, most natural populations should be ecologically homogenous: every individual eating pretty much the same thing as every other individual if they happen to encounter it. But, that didn't jive with my reading of the fish literature. So, I assembled a group of fellow graduate students (as yet uncontaminated by preconceptions on the topic) and we did a review / meta-analysis of diet variation within populations. In a sense, I did it just to prove to myself, and to Tom Schoener, that the real core of my dissertation wasn't a wild goose chase. The resulting paper has turned out to be my most-cited article by far (Bolnick et al 2003 American Naturalist). And I did it to prove a PhD committee member wrong, on a minor point of disagreement. To be clear: Tom loved that paper and assigns it in his ecology graduate course, and we get along great. But the point is, your committee members and peers have both accumulated wisdom that you should draw on, but also have preconceptions and biases that may be wrong. Defend your ideas, and if you are able to, you might really be on to something.
Tom Schoener

1 comment:

  1. I had a lot of fun reading this post, because I confirm some of (what I thought that were) my unique and original perceptions, and because I learned a lot of several other nice tips.
    Regarding "Suggestion 3: Don't get stuck on local optima", and "Suggestion 7: Have a portfolio", I made a small contribution in spanish in relation to long term public strategies in science (MONTERO, R. PolĂ­ticas cientĂ­ficas, optimalidad y sistemas complejos. Cuad. herpetol. 2015; it can be downloaded from


A 25-year quest for the Holy Grail of evolutionary biology

When I started my postdoc in 1998, I think it is safe to say that the Holy Grail (or maybe Rosetta Stone) for many evolutionary biologists w...