Over the summer, there was some discussion of two basic approaches to doing ecological and evolutionary research. There’s the “question first” approach, where you identify a question of interest, and then figure out a system well-suited to studying that question. And then there’s the “system-based” approach, where you work on a particular system, identifying questions of interest in that system. At first glance, it can seem like the question first approach is superior – after all, if we’re interested in discovering general principles about nature, we shouldn’t be tied down to one system, right? And, in theory, this makes sense. But, in practice, I think it’s not that clear cut. This is not to say that a question first approach is bad – just that it might not be obviously better than a system-based approach.
One major advantage to a system-based approach is that working extensively in one system allows you to identify phenomena that it never would have occurred to you to look for or think about. Take our work on Daphnia-parasite interactions in lakes. This work originated out of observations that my PhD advisor, Alan Tessier, made while doing research on the Daphnia system, on a set of unrelated questions. While Dieter Ebert had done a lot of work on Daphnia-parasite interactions in European pond Daphnia, parasites hadn’t really been studied in lake Daphnia or in North America. So, 15 years ago, a purely question-driven researcher interested in the ecology and evolution of infectious diseases would have been rather unlikely to start working on stratified lakes in the Midwestern US. However, while working on an entirely different project, Alan noticed that some Daphnia appeared to be infected, particularly in one population; when he next sampled that population, he found that the host density had crashed. That was certainly interesting and noteworthy and – most importantly for this post – unexpected. He then did some follow up experiments in the lab and field to show that the system was experimentally tractable (and to further establish some important patterns). Without that base, none of our research on Daphnia-parasite interactions in lakes would exist. And, again, it all stemmed from observations that occurred while working on other projects in the same system. I think this sort of serendipity is a really important part of science, and is a real asset of system-based research.
The other major advantage of systems-based research is that, in my opinion, moving between systems while taking a question first approach makes it more likely that you will overlook an important, potentially confounding aspect of the system, or make mistakes while collecting data. Presumably you would figure out some of these things along the way (assuming you were paying attention), but knowing a system well could help avoid false starts. Having expertise in a system can be more efficient – if I suddenly decided to switch to working on, say, coral diseases, I’d need to identify field sites, figure out how to access them, learn how to sample corals, order all the appropriate gear and supplies, etc. And, if three years after that I decided that bats were the best system for answering the next question I had in mind, I’d have to redo all of that yet again. And, most likely, I’d make mistakes, because there is tons of stuff that you learn about how to sample a particular system (most of which does not get written in the methods sections of papers), navigate a particular field site, etc. That hard-earned knowledge comes with experience. If I had to go sample a coral reef in 6 months, even with extensive preparation, I’m sure I’d make a lot of mistakes.
Of course, there are downsides to system-based approaches, too. One of those is being labeled as someone who is system-based. You are never going to get funded if you submit a grant proposal saying, essentially, “Please give me money to study these cool field systems for 3 years. I’m sure I’ll figure out an interesting pattern and try to explain it during that time.” And you also won’t get funded if you say, “I found this cool pattern in lake X and want to study it more”, unless you can also argue for how that pattern is likely to be a general one in many systems, or to give us important insights into a generally interesting question. Saying, “Please give me money to study pattern X in organism Y because that has never been studied before” is a sure way to NOT get funded. The key is to figure out what general questions are well-suited to study in that particular system, and to write a proposal that is ground firmly in general theory.
In the end, the dichotomy between question-first and system-based approaches is probably a false one. I imagine that most people – myself included – do a hybrid of the two. I’ve worked on Daphnia since I was an undergraduate, and, while I’ve tried to start working on other systems, I keep coming back to Daphnia. But the reason I keep coming back to Daphnia is because I think they’re really well-suited to the general types of questions I’m most interested in. And I have shifted things around to follow particular questions – for example, I’ve started working on additional parasites that let me answer questions that I was interested in but couldn’t study with the first parasite I started working on. I’m also sure that people who take a question first approach have occasions where they notice an interesting, unrelated question, and follow up on it, even though that question was driven by an observation they made on that particular system.
So, my advice to new graduate students would be to both get to know a system well – really well – and also to read really broadly so that you can identify questions that are generally interesting. You will only be able to capitalize on the opportunities that present themselves while working in a system if you can both recognize them as opportunities and relate the phenomena you observe to general theory. As Louis Pasteur said, chance favors the prepared mind.