It’s proposal development season: all the graduate students who started earlier this fall are starting to come up with project ideas. If you’re one of those students, here’s some advice to help you out.
In order to decide what to do, you need to know–and I mean really know–why it’s worth doing. You need to run your ideas by smart, broadminded, thoughtful, critical people who won’t take for granted that even your most basic choices (like framing of the issue and choice of study system) are good ones. I can’t help you too much with this (well, unless you’re doing phylogenetic community ecology, in which case I’ve probably given you more “help” than you wanted). But I can help you out a bit. A while back, I did a list of some common bad reasons for choosing a research project. Here, I’m going to complement that with a list of good reasons. I don’t know that this list will help you come up new ideas, but in combination with that old list, it should help you evaluate the ideas you come up with.
I encourage you to have a look at this list even if your adviser has handed you an already-designed project. You still ought to understand, at least as well as your adviser does, why your project is worth doing. Talk to your adviser about how your work fits into the broader research program of the lab, and with the field as a whole. Read the literature (and not just review papers). Ask to see the grant proposal that funded your project. Etc.
Note that the advice below is aimed primarily at students designing fundamental, question-driven research projects. Justifying applied projects is different. Not necessarily easier, but different.
This list is by no means exhaustive. Good thesis project ideas do tend to run to type, I think, but there are surely more types than I was able to think of off the top of my head just now. Hopefully commenters will chime in with other suggestions.
Note as well that quality of execution matters. Just because your project idea falls into one of these categories doesn’t guarantee that it’s a good project. For instance, if you set out to “explain a pattern”, but it’s an already well-studied pattern, that’s probably not a very good project idea.
Explain a pattern. Take as your starting point some pattern in nature, the stronger, more general, or more striking, the better. Develop and/or test one or more explanations for it. The pattern gives others a good reason to care about your work. A pattern is a signal. It’s a sign that there’s something other than “noise” going on. Setting out to figure out what that something is is a good starting point for a project. One hazard with this type of project: if there are already a whole bunch of non-mutually-exclusive explanations for the pattern, adding one more to the list isn’t really very interesting or useful, especially not if it’s also difficult to test those explanations. This is why “explain the latitudinal species richness gradient” probably isn’t a good project idea.
Explain a surprising phenomenon. This is really just a variation on the previous item. Find some feature of the world that isn’t as we’d expect it to be. Develop and/or test some explanations for why. Maybe some organism or system that appears to be an exception to some general rule. Maybe an organism that has an apparently-maladaptive phenotype or engages in an apparently-maladaptive behavior. Maybe an organism or system represents the extreme of some range of variation, raising the question of why it is that way, and perhaps how it manages to function at all. Maybe some feature of the world is changing for no apparent reason, or changing in the opposite way to how one might naively expect. Etc.
Explain variation. The world is full of striking variation–over space, over time, among individuals, populations, species, communities, and ecosystems, etc. Try to explain some of it. Note that, to pull this off, you’re going to have to have an eye for tractable variation, as opposed to intractable noise.
Test the consequences of some process or processes. This is the flip side of pattern-inspired work. Start from some process or processes. Develop and/or test hypotheses about the consequences of those processes. The tricky thing about this sort of work is that you also need some good motivation for choosing which process or processes to study.
Conduct the first test of some hypothesis. Conducting the first empirical test of some interesting and important theoretical hypothesis is usually a winner. This was what I set out to do for my PhD.
Conduct the first experimental test of some hypothesis. If some interesting or important hypothesis has previously been tested only via non-experimental evidence, conducting a direct experimental test often is a valuable thing to do. It’s for good reason that manipulative experiments remain the gold standard for testing causation. Often, doing this will require you to find an appropriate model system that has features making it feasible to conduct whatever experiment you need to conduct.
Conduct the first test of one particular aspect of some hypothesis. For instance, if hypothesis X has several implications, only some of which have been tested, test the ones that haven’t. This is a good idea if doing so has the potential to greatly change our views on hypothesis X.
Develop the mathematical version of some verbal idea or hypothesis. Ecology is chock-a-block with influential ideas that haven’t been much developed mathematically. Often, when you try to do the math, you’ll discover key implicit assumptions that weren’t previously recognized, or else you’ll discover that the assumptions don’t actually imply the conclusions they are thought to imply. At worst, you’ll at least make the idea much more precise, and so much more testable. Now, if only someone had had a project idea along these lines back in 1979 or so…
Show how an idea from one field applies to an apparently-unrelated problem in a different field. Good ideas for this sort of project are quite difficult to come up with. Loose analogies between problems in different fields are a dime a dozen, and not very useful. But if the analogy is sufficiently precise for ideas from one field to be “translated” to another field, you may well have an idea that will lead to big advances. You may be able to suggest novel answers to existing questions, reframe existing questions, and propose entirely new questions. For instance, what can we learn about food webs by viewing them as mathematical “
networks” EDIT: “graphs” is more precise (an idea for which I believe Joel Cohen can take much of the credit, and which spawned a whole subfield of research)? What can we learn about patterns of diversity and abundance in ecology by drawing on neutral models from population genetics? What can we learn about microbes by asking if they exhibit the same biogeographic patterns in their distributions as macroorganisms (currently a very hot area of microbial ecology)? What can we learn about biodiversity and ecosystem function by viewing ecosystems as analogous to populations evolving via natural selection (Fox 2006)? Etc.
Use a fundamental idea to address an applied problem in a novel way. This is pretty much an inexhaustible source of project ideas for ecologists and evolutionary biologists. Find some applied biological problem that people are trying to solve without thinking about the obvious (well, obvious to you!) ecological or evolutionary aspects. One general “recipe” here is to ask “why” questions that others aren’t asking, and tease out the implications of the “why” questions for the answers to the “how” questions that others are asking. From pest control efforts that are naive about resistance evolution, to algal biofuel projects that are naive about the ecological and evolutionary obstacles to trying to grow herbivore-free monocultures of high-lipid algae, to biomedical research that treats genetic and phenotypic variation as an annoyance to be controlled or eliminated rather than a crucial phenomenon to be studied, the possibilities are endless. One nice thing about pursuing this sort of work is that you can tap into pools of money (from governments, NGOs, and private companies) aimed at solving the applied problem.
Revisit classic work with modern approaches. Many classic, textbook studies in ecology wouldn’t even get published today–the sample sizes are too small, the experiments too badly designed, and the analyses too crude. Reanalyze some classic dataset with modern methods and see if the conclusions hold up. Resurvey some classic study sites and see if they still look the same today. Repeat some classic experiment with a better design. Now, the risk here is that if the classic result holds, or if it breaks down for uninteresting reasons, your project probably turns out to be boring. For instance, Travisano and Shaw (in press; open access) argue powerfully that genome sequencing has merely reconfirmed our decades-old knowledge that quantitative trait variation is underpinned by many loci of small effect. But if the classic result doesn’t hold up, your project will catch a lot of attention, and for good reason–you’ll be changing how everyone thinks about some important topic. And there are happy cases where the outcome will be interesting no matter what you find. For instance, if you resurvey some classic study sites and find nothing’s changed, you can tell a story about their remarkable stability. If you find that everything’s changed, you can tell a story about those changes.
Bonus! Here’s are more bad reason for choosing a research project, that I forgot to list in that old post.
Pretending that your project has an application when in fact it doesn’t. Just because your study manipulates temperature doesn’t mean it’s relevant to climate change. Just because your study includes a species richness gradient doesn’t mean it has implications for the current extinction crisis. Etc. Every fundamental researcher, including me, sometimes bullshits about the relevance of their work to pressing applied problems. Which doesn’t mean it isn’t bullshit. There are good reasons to do fundamental research in a world with pressing applied problems. Don’t bullshit that your fundamental work is really applied. Try to be better than the rest of us; don’t pretend you’re working on climate change when in fact you’re not.
Filling in minor details. If we already have a good big-picture understanding of something, filling in minor gaps in that understanding isn’t worth your time. Now, one person’s minor gap may be another’s gaping chasm, but still, this point is worth keeping in mind. For instance (and this is just the first example I could think of), consider the “diversity-invasibility paradox”. In nature, more diverse native communities also tend to harbor more invasive species, but in theoretical models and controlled experiments, increased resident diversity typically inhibits invasion of new species. Jon Levine pretty much solved this paradox: in nature, any environmental factor that enhances the ability of new species to colonize and establish populations is going to increase both resident diversity and invader diversity. All else being equal, increased resident diversity inhibits invasion, but in nature all else is not equal, and that effect mostly gets swamped by variation in environmental factors. From my perspective as a broadly curious, question-oriented, big picture kind of ecologist, there’s nothing else really interesting or important to be learned about the diversity-invasibility paradox (feel free to argue otherwise in the comments if you think I’m totally off base here). For instance, there are plenty of systems where we can’t yet specify the relevant environmental factors in great detail–but there’s no reason to think that learning the identity of those factors would change the basic picture. So while there still seem to be lots of people working on various things to do with the diversity-invasibility paradox, personally I think you should look elsewhere if you’re looking to address some big unanswered question in fundamental community ecology or invasion biology.