Advice: weak reasons for choosing a research project

This is the first of what I hope will be an occasional series of posts on ‘random advice for graduate students’. I will make no attempt to be comprehensive; if you want comprehensive, have a look at How to do ecology and the excellent set of resources compiled by Spencer Hall. Instead, I’ll just be tossing out occasional tips that I haven’t seen offered, or sufficiently emphasized, elsewhere.

I emphasize that these tips spring from my own personal values and preferences as a scientist; not all of those values and preferences are universally shared. So treat these tips as food for thought, not as the word of your god of choice.

Today I’m going to talk about weak reasons for choosing a research project. There are lots of reasons for choosing a research project from the infinite universe of possibilities. Some reasons are better than others. Here are some reasons that I’ve encountered often, both as a member of student committees, and as an editor and referee, but that (in my view) are weak or incomplete.

1. Lots of ecologists have long been interested in, or are currently interested in, X. Lots of ecologists are interested in boring and unimportant things (I’m no exception). The fact that lots of people have been, or are, interested in X is not in itself a good reason to study X. Choose your research on the basis of ecology, not based on what ecologists think about ecology. If lots of people study X because X is interesting or important, then you should be able to explain why X is interesting or important. Invoking the authority of other ecologists is not going to convince anyone that X is interesting or important, or demonstrate that you know why X is interesting or important. Because if you don’t know that, how do you know you’re not just jumping on the latest trendy bandwagon?

2. Not much is known about X. Which means you’ll probably struggle to learn much about it. We learn new things by building on what we already know. Plus, there’s an infinity of things we don’t know much about. Why, out of all those things, do you want to know more about X?

3. People have never studied X in system Y. Ah, the good old “But in my system, things might be different” argument! Sorry, but if that’s your reason for studying X, you’ve immediately raised some questions for anyone who doesn’t already share your fascination with system Y. For instance, is there any reason to think that X works any differently in system Y than in any other system? This is an especially big issue if X is already well-studied in other systems. Note that one common but mistaken response to this concern is to list reasons why system Y is different than other systems, without specifying why those differences would matter for X. For instance, if you say you want to study resource competition in phoenixes, and you say that phoenixes are different than other organisms because they reproduce via spontaneous combustion, you still haven’t explained why you expect resource competition in phoenixes to work differently than in any other organism.

Also, is Y a good model system in which to study X? Maybe nobody’s studied X in system Y because system Y has features that make it difficult to study X. Is there even any reason to think that X occurs, or applies, or matters in system Y? People who are mostly interested in X, as opposed to system Y, will be particularly keen to have these questions answered.

4. People have studied X, and they’ve studied Y, but they’ve never studied X and Y together. There is an infinity of things we’ve never studied in combination. You need some independent reason to study X and Y together (and “X and Y are both important” is not a good reason). For instance, if X and Y are known or thought to be the only two things that affect the response variable of interest, then it make sense to study both together because now you’re exhaustively considering all the possible factors affecting your response variable, rather than just two arbitrarily-chosen ones.

5. Does X or Y have a bigger effect on Z? As stated, this question makes no sense. It only makes sense to ask whether x units of X has a bigger effect than y units of Y. And even though this modified question makes sense, that doesn’t necessarily mean it’s a good question. You still have to explain why your answer isn’t simply a function of your choice of x and y. X may have a weak per-unit effect, and Y may have a strong per-unit effect, but if you use a lot of X and only a little of Y, X will still have a bigger effect on Z. Which seems rather trivial.

6. Do X and Y have independent or interactive effects on Z? I may be in a minority here, but to me, just asking whether two factors have statistically-independent effects seems like a pretty boring question in most circumstances. In general, the effect of anything on anything is going to depend on other things. Now, if X and Y are known to be the only two factors affecting Z, then this question often is a good one, especially if you also have some a priori theoretical reason to expect that X and Y will, or will not, affect Z independently.

There are also technical issues with this kind of question, because whether or not you get a statistical interaction term in your analysis is going to be sensitive to the units in which you measure X, Y, and Z, meaning that (e.g.) otherwise-innocuous data transformations can change the answer. My suggestion would be to frame this kind of question in mechanistic, process-based terms rather than statistical terms. For instance, don’t ask whether predation and competition have statistically-independent effects on diversity, ask if the mechanisms by which competition affects diversity operate any differently in the presence vs. absence of predation, and whether there are any diversity-affecting mechanisms that only operate when both competition and predation are present. This kind of framing is often more informative than a purely statistical framing. Your statistics should be a means to help you answer your scientific question, they shouldn’t define your scientific question.

24 thoughts on “Advice: weak reasons for choosing a research project

  1. Hi Jeremy, First let me begin by saying that I thing you have a fantastic blog going here, and your posting output is quite impressive. I especially liked your last post, but there is some serious narcissism in that feeling because I just graduated a month ago from Nick’s lab :). Let me move on to my real comment though. I agree with much of your advice for graduate students, but as a recent graduate student I take some exception with your first point. As graduate students we face increasing competition both for grants and jobs. You say: “Choose your research on the basis of ecology, not based on what ecologists think about ecology. ” But other ecologists decide if we as students and young scientists are funded or not. If I want to study the effects of horn size on the demography of unicorns because its a fascinating ecological question, that may be great, but we have to believe that we are doing science that will further our careers and our careers do not happen in a vacuum.

    It’s not that I think your first point is bad advice (I think its great advice), but as a graduate student looking at their future, I think its a gamble. Yes, I may have a break through that catapults my career, but most likely I might doom myself to obscurity. As I look back on my own dissertation on climate change and food web structure, I sometimes get a bit queasy because I did just what you advised people not to do: “Because if you don’t know that, how do you know you’re not just jumping on the latest trendy bandwagon?” But that said I’ve successfully published some of the work (in Oikos), I’ve received grants (including an NSF DDIG) in part because as an NSF PO said to Nick and I: “This is the sort of climate change research we are interested in funding.” I think that we face difficult choices as graduate students between our scientific passions and what will make you a success (i.e. well funded, well published, having a job). The truth is that very few graduate students I know (myself included) have some George Price in us, that willingness to sacrifice themselves for their career.

    I love science, I love getting up everyday and working, but I also have to look to the future and how I will get a good job and support my family. I think that riding that trend is your best bet to establish yourself, though certainly not the only way. Your #1 is certainly one of the most difficult tensions I think all scientists face, and why Kuhn’s paradigm shifts are so hard to achieve. Anyway, keep up the great posts, I love reading your blog with my morning coffee before starting work, and I look forward to more thought provoking posts.

    • Hi Edmund,

      Glad you’re liking the blog. Thank you for your very thoughtful comments. You’ve raised some very difficult issues, to which I’m not sure there are any cut-and-dried answers.

      In advising ‘choose your research on the basis of ecology, not what ecologists think about ecology’, I didn’t necessarily mean ‘do whatever you personally find interesting, even if no one else care’s about it’. It’s fine if you want to study horn size of unicorns, but if you do that you need to go in with your eyes open and honestly assess how many other people care about horn size of unicorns, and (crucially) whether they *ought* to care. For some people, this leads them to search for some kind of ‘angle’ or ‘spin’ they can place on their research to make it seem to be of more general interest than it is. In my experience, that kind of spin usually (not always) gets seen through by search committees, funding agencies, and editors of leading journals. The point is that you need to be able to explain to other people, who share your broad interest in ecology but not necessarily your own personal preferences, why they should care about your work. ‘You should care about unicorn horn size because lots of other people care’ and ‘you should care about unicorn horn size because I personally care’ are both very weak reasons for other people to care about unicorn horn size.

      Whether one should choose one’s research based on what funding agencies want is a hard issue, one I’m fortunate not to have to worry about because I’m in Canada. If it’s any consolation, the issue is even more serious in other countries–I’m told that NERC in the UK has a short list of priority funding topics, and research on anything else has essentially no chance of being funded. I suppose all I would say is that, even if funding agencies want research in certain areas, hopefully that still allows us enough scope to identify our own questions, rather than just cynically giving funding agencies whatever it is we think they want. For instance, here in Alberta (and in other jurisdictions, I’m sure), the government has to determine ‘in-stream flow needs’, which basically means how much water to leave in the river in order to preserve the river’s ecology. Traditionally, this has been regarded as an engineering problem, the question being how much water can we take from the river while still leaving enough to cover the fish. But as my colleague Ed McCauley and his co-workers have pointed out, there are strong ecological arguments for reframing in-stream flow needs as a really interesting problem in fundamental population ecology, to do with population growth and persistence in advection-diffusion environments.

      I would never advise anyone to do ecology a certain way even if it means being unable to provide for yourself or your family. But as anyone who wants to go into academia knows, there are a lot of people chasing very few jobs, and that’s never going to change even after the economy improves. Success is unlikely no matter how good you are or what you decide to work on. I’m very, very fortunate to have my current position (it was initially offered to someone else, who turned it down), and had I not gotten it I was planning to quit science. My advice to anyone seeking to go into academia is that, if that’s what you’d love to do, and if it seems like you might be good enough, have a go at it, because otherwise you’ll go through the rest of your life wondering what might have been. But recognize that success is unlikely (not just uncertain, unlikely), and have a Plan B. Yes, following my advice is a gamble–but the decision to try to go into academia at all is the big gamble.

      p.s. George Price was a unique individual (and not just in the way each of us is unique). He certainly sacrificed himself, though I wouldn’t say he did so for his career. I certainly wouldn’t recommend that anyone take him as a model.

  2. Hi Jeremy,

    Thank you for your reply. I am glad that you did decide to stay in science, the Oikos blog has become one of my favorites, I’ve found your posts really thoughtful and fascinating. I really enjoyed the MaxEnt one and I went and read quite a few posts on the physics blog you linked to. And yes, George Price was unique and certainly a brilliant man. He came to mind because I’ve been reading a really interesting book about him, and a great book about evolution in the first 3/4’s of the 20th century called “The Price of Altruism”. I highly recommend it. Thanks again for your reply.

    • George Price is probably a leading candidate for the title of ‘greatest amateur scientist since 1900’. I enjoyed Harman’s The Price of Altruism as well, mostly for all the new details Harman dug up on Price’s life. Harman’s potted history of debates about the evolution of altruism was less interesting to me because it was already familiar to me, and I think it might be rough sledding for anyone not already familiar with it, because Harman loves ‘jump-cutting’ in order to introduce the reader to some new person or incident whose relevance is only gradually revealed. And like Steven Frank (see his review of The Price of Altruism in Science), I was put off by Harman’s insistence on drawing a Big Conclusion at the end, in this case about the purported links between a scientist’s personality and the content of his science. For a more interesting and nuanced engagement with that claim, I highly recommend Marek Kohn’s A Reason for Everything: Natural Selection and the English Imagination, a history of adaptationist thinking in England. Wallace, Fisher, Haldane, Maynard Smith, Hamilton, and Dawkins were (are) very different men (although Kohn does argue for their shared ‘Englishness’ ). But their science, and their sense of the larger meaning of that science, was very much of a piece.

  3. Thank you for the advice on making a meaningful project. I think that the approach of identifying weak reasons is more practical than some other (also helpful) guides (like Lanyon 1995). As a new ecology grad student, I will await more posts like this and also check out the Hall book!

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  8. I get excited about my research when its on a topic that is understudied, or a well known phenomenon that’s not studied in my system, though I don’t believe I am making these errors. For example, I am studying herbivory effects in undisturbed forest systems. While grazing is well studied in grasslands, these plant-animal interactions are not well understood in subalpine forests, or forests in general to my knowledge. While its exciting to have found a knowledge gap to try to fill with my research, the underlying reason I study these interactions is because I suspect high herbivory impacts are accelerating succession and contributing to major ecosystem changes. You gave lots of information on what not to do, but what do you recommend actually doing? Where do you think my example fits in?

    • It’s easier to describe what not to do than it is to describe what to do. 😉

      Certainly, I wouldn’t advocate avoiding knowledge gaps. And there are drawbacks to working on something we already know a lot about. There’s a good post on this over at Nothing in Biology Makes Sense!, on the advantages and drawbacks of working with a model system like Anolis or sticklebacks. A lot is already known, which gives you the ability to study things you couldn’t otherwise study. But lots of other people work in that system to, which makes it much harder for you to do work that really stands out.

      • Thanks for the reply. Those are important considerations. Hopefully some of my dissertation chapters will incorporate safer experiments in well studied areas and a couple that try to wander off in uncharted territory. There are so many interesting things to study, its difficult to choose which, and then get other people excited about it.

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