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Is There A Best Way To Choose A PhD Dissertation Topic?

For every new graduate student, the first major headache is what their dissertation will be about. In many areas of science, graduate students have very little choice. The laboratory leader essentially assigns a topic to the student, based on funding requirements and the laboratory structure.

However, in ecology, evolution and behavior, most laboratories still work on the principle that each graduate student must develop their own thesis topic.  Of course this is done in consultation with their dissertation supervisor, and it is often closely associated with other research that is being done by others in the laboratory.  It may even form a part of the larger project of the laboratory.  However, the student must develop the questions.  In this post, I want to discuss the two main ways that students in these disciplines approach this most important of problems for them.

When a student asks their supervisor for advice about how to develop a dissertation topic, they are typically given two options: question first or system first. 

From talking to people over the years,  I’d guess the vast majority of graduate students are told to develop a question first, and then go out and try to find a biological system where this question appears to be important.  

Developing a question first and then finding a system is perfectly reasonable advice, and probably in the short term the best strategy for a student to take.  A student wants to be working on a big issue in their chosen field, and there is no better way to end up working on a big issue than to focus on “what’s the big idea” from the start. Moreover, choosing an empirical system that is tractable and in which the question appears to be imminently relevant is also increasing the probability that the project will be successful.  And so from the student’s perspective, the “question first” strategy is probably the best approach for the student to developing a successful dissertation topic.

However, this approach has a number of disadvantages for the student in the longer term and more importantly for science in general.   A long term disadvantage for the student is that once this project is completed, the cycle begins again.  Either the newly minted Ph.D. must go find another system to address the same question, or the newly minted Ph.D. must return to start and come up with another compelling question to begin the cycle again.  Obviously, this is not a problem until the dissertation is completed.  However, the best dissertation topics will set the scientist for many years of exciting and important work after the dissertation, and this strategy has is not an obvious way to do so.  

I also think this approach has detrimental consequences for our science in general. First, one has to question whether this is actually doing science at all.  Let me use past history in my field of community ecology as a guide.  In the 1960’s, the major theoreticians at the time were developing models to show that species should be different from one another in particular ways to reduce the strength of resource competition between species.  This theory went under many names, such as limiting similarity and niche theory.  Graduate students around the world were developing dissertations to test this theory, and the literature filled with papers from these dissertations.  A signature of limiting similarity was to find a set of closely related species that live together, that eat the same foods, and that are very different in some aspect having to do with feeding.  For example, species that are different in body size tend to have diets that are only partially overlapping.  In fact, this theory predicted that species would differ according to Hutchinson’s ratios.  The literature literally filled up with papers reporting Hutchinson’s ratios, and communities where species had similar diets but differed in body size.  

So if theory predicts “XX”, and then a scientist goes out to find some place where “XX” is apparent and only studies that place, has that scientist actually tested that theory?  Or has that scientist merely confirmed that “XX” is apparent in the system that they chose to work on? I think this is not a valid scientific test whatsoever!  If a scientist chooses based on the answer that they want to get, the problem is rigged from the start.  

This approach to choosing a dissertation topic also greatly limits what scientists see in the world.  The mania about finding Hutchinson’s ratios in nature was broken when a number of people started pointing out that most species in most communities do not display Hutchinson’s ratios, and in fact competition for resources is frequently not important for many species.  If all you look at is what you want to see, you develop a very distorted view of the world.  

The corollary of this problem is that it creates a bandwagon mentality among scientists for “what’s the hot topic” and limits inquiries into new subjects and systems.

The other strategy is to choose a system first, and then answer an important question to address in that system.  Another way of stating this strategy is to find something out in nature to explain, and then explain it.  

This is the strategy I have always used in developing research projects, and I used this strategy to develop my dissertation topic.  The pattern I wanted to explain was why Enallagma damselfly species segregated between lakes where fish are the top predators and lakes where dragonflies are the top predators, and why Ischnura species are common in both these lake types.  I developed a number of competing hypotheses that could explain this distributional pattern, and then designed a series of experiments to test these hypotheses.  Doesn’t that sound like doing science?

This approach is clearly more demanding of the student.  The explanation for the pattern being addressed may be trivial or largely uninteresting.  Moreover, the student develop a place for their work in a broader conceptual context so that their results have meaning for scientists studying other systems.  In effect, the student must develop the big conceptual question after the fact that makes the work more than some facts about a particular system.  

However, the advantages to to the scientist in the long term and to science overall are clear.  For the scientist, this approach forces them to think across a broad conceptual landscape in search of relevant ideas. As a consequence, it also leads the scientist to make connections among what may seem to be disparate ideas.  I know this approach to developing questions has done this for me.

A discipline also does not get stuck on a single idea for long periods of time. Scientists search for new patterns to explain in nature, and bring those interconnections to their work.  In fact, some of the most interesting questions to emerge are comparative: why is this pattern seen in this type of system, but not in this type of system.

So my advice to incoming graduate students has always been to find some interesting pattern in nature and explain why its there.  This also explains why empirical results come first to me and theory later.  One must advance big conceptual issues to be a successful scientist, but those big conceptual issues must come from nature.  It doesn’t work the other way round.



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  1. I’m very late to this, but very interesting Mark. Made me stop and think.

    I think you’ve identified the “failure modes” of question-first research. Meaning, when question-first research gets difficult or goes off the rails entirely, yeah, that’s often how it happens. Without wanting to disagree, wouldn’t you say “system first” research has its own failure modes? Most (in)famously, there’s a certain sort of system first ecologist who’s almost aggressively disinterested in generalities, sometimes to the point where it hurts their own ability to do system-first research. More commonly, it’s my anecdotal impression that system-first researchers are at least as prone to bandwagon-jumping as question-first researchers. Because if you’re a system-first researcher who wants to do work that’s not *just* of interest to others working on the same system, well, one way to do that is to jump on a certain sort of bandwagon. The sort of bandwagon based on a broadly-applicable, “crank the handle” approach to inferring process from pattern, that purportedly works in any system with no customization or even the need for much thought on the part of whoever’s applying it. Think of local-regional richness relationships as a tool purportedly allowing you to infer whether interspecific competition is strong enough to limit community membership (many other examples could be given).

    But this is just my question-first instincts talking; I’m probably not the best person to identify the “failure modes” of system-first work. What do you think those are?

  2. I think you’re right that both approaches have pitfalls, and the one you identify for the “system first” approach is exactly the trap that people can fall into. However, I’d emphasize that I think “system first” is the appropriate term for it. Scientific research is nothing without fundamental conceptual questions at the core of any research program. So even if you’re interested in the gory details of some species or ecosystem, it will make little contribution until you make those conceptual generalities from it.

    I think, more generally, the trap for either approach is that one never moves on to the issues inherent in the other. For the “question first” approach, the really cool and important things typically emerge from the details of the natural history of the system. And for the “system first” approach, the really cool and important things don’t typically emerge until the details are placed in that larger conceptual context.
    See also

  3. marcrobe

    Do the two always need to be mutually exclusive? 😉

    • Not at all. In fact, I think they are both essential. I just think the more productive place to start is based on letting the system tell you what the important conceptual questions that system are.

      I think the critical issue for science is to work forcefully against simply collecting data on what you think you already know.

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