The merits of system-based research

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.

12 thoughts on “The merits of system-based research

  1. I think that a similar dichotomy exists in non-experimental work between questions and tools. Sometimes this dichotomy can become institutionalized in the form of whole fields like applied mathematics or statistics that specialize in tools but not any specific questions. Sometimes this can go even further and more meta by fields developing that ask questions about the properties of tools (theories of theories; this is propagating in theoretical computer science and physics right now).

    I’ve struggled a lot with this tool-vs-question dilemma. On the one hand, I really like the sort of questions asked in theoretical biology (especially evolutionary ones), but I find the theoretical tools used to be boring. On the other hand, I really like the tools offered by theoretical computer science, but find the typical questions asked in the field to be no fun. Since a clear field unifying the two does not exist (yet!), this has made my learning rather schizophrenic; I keep bouncing between learning the tools deeply or understanding the questions well. This is further complicated by the two areas belonging to different departments (and sometimes different faculties!). Ahh!

    The only thing I would like to add to your post, is another upside for concentrating on questions. In fields without a strong and coherent theory, any given question is usually addressed with a mess of different heuristic models that are often incompatible or not directly comparable. In an experimental setting, I would assume this is equivalent to a question that is studied with many fundamentally different systems that tend to yield contradictory results. Without a strong concentration on the question, it is often impossible to know which of these heuristics are best, and if you specialize only in tools, it is too easy to see everything as a nail… even when it isn’t!

  2. These sorts of questions haunt my fields of geomorpology/hydrology as well. Not so much organisms, obviously, but “places.” Becoming an expert on a particular place can be a wonderful experience, but is not such a wonderful way to get funding…unless you can compellingly explain why your place is best-suited to answer a more generalizable question. One of PhD supervisors said to me: “Notice how most paper titles are along the lines of ‘Effects of X on Y in Place Z.’ Your work will be more likely to be noticed if you get rid of the Place Z in the title so that people just see the question and don’t immediately dismiss your work because they aren’t interested in Place Z.” I have some titles with very specific places in them, because the particular place is very important to understanding the motivation of the work, but I’ve tried to bear it in mind. When I wrote a paper about climate change effects on seasonal and transient snow in the Pacific Northwest, my paper title said it was about maritime mountains…because it was and there’s lots of reasons to think my results are transferable to other places. At least until someone works in one of those places proves me wrong and the science advances.

    We also have the tools versus questions tension in my field too. From watching a friend who is a leader on a particular tool, I’d say that becoming an expert on a particular tool makes you a sought-out collaborator with lots of mid-list authorships, but when you’ve got a zillion collaborative projects going in a zillion directions it can be hard to find the time to work on the questions that most interest you.

  3. Thanks for the advice to grad students! I think about this question quite a bit, mostly wondering whether it is still feasible to establish new systems, and at what stage of a career one might dare to work in novel systems (a system that hasn’t been worked in at all, as opposed to simply one you haven’t worked in but others have). One has to be an unabashedly system-oriented person to do the basic biology necessary to establish novel systems, but it seems to me that, in part because of the downsides you list, there can be little incentive to take the risk of doing this work. Even in a system that seems promising for answering generalizable questions, there can be many years of work between seeing and realizing that promise. When is the right time to do that work?

    • I just realized I missed this comment (thanks to trying to clean out my inbox!) Sorry for the very delayed reply. You are right that it’s hard to do the basic biology necessary to establish novel systems. There is a certain amount of natural history that needs to be worked out, and natural history (on its own) can be hard to publish. So, yes, when setting up a new field system, this is a problem. Avoiding needing to repeat this work is one of the advantages of system-based work, in my opinion.

      In terms of setting up new systems: when I tried to set up a new system looking at disease in Asplanchna rotifers, I did it on top of my regular work on Daphnia. I knew I couldn’t put all my eggs in that basket, in case it didn’t work out. That was good, because it didn’t.😉 One thing I did was have undergrads work on different aspects of the system as part of their undergraduate research projects. It still required a lot of time to mentor them, but not as much time as if I was doing all that work (e.g., figuring out how to culture them) on my own. That’s a partial solution, but only works for some systems and at some times.

  4. It seems like the key is to have a good match of question and system. You can achieve that match by being a question-first person, a system-first person, or somewhere in between.

    Achieving that match isn’t always easy. I suspect that part of the appeal of what I’ve called “shortcut” methods in ecology is that they seem to offer the promise of letting you ask big, general questions in any system, particularly the many systems that aren’t amenable to certain sorts of manipulative experiments or to the collection of long-term population dynamical data. They offer the promise of letting you have your cake and eat it too, sticking with a system you know and love while also getting to ask questions of general interest. Of course, the problem is that “shortcut” methods hardly ever work:

    Another thought: can you think of ecologists who’ve switched systems after becoming profs, in order to ask different questions, or to get better or different answers to the same questions? I restrict it to “after becoming profs” because I think it’s pretty common to switch systems when going from an MSc to a PhD, or from a PhD to a postdoc. My supervisor Peter Morin is one. Switched from mesocosms of anuran and insect larvae to protist microcosms because he wanted to ask questions about population dynamics, which you can’t really ask easily with anurans and dragonflies. Dave Tilman is another–switched from chemostats to grassland plants. In his case, he kept asking the same broad questions about resource competition and its consequences. Although I’m not sure of the timing of his switch relative to when he got his first faculty position. And Andre de Roos switched from working on Daphnia to working on fish in order to be able to build from knowledge of individual life history and demography up to an understanding of population dynamics. It’s difficult to track the life history and demography of individual Daphnia, though it can be done. There must be many others I’m not thinking of, though.

    Relatedly, there are people who’ve worked in a wide range of systems on a wide range of questions, often with collaborators but sometimes on their own. Tony Ives is a great example, but there are many others, not all of them modelers. Phil Warren used to do protist microcosms and still does a bit, but these days I think he mostly does urban ecology.

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