TL;DR: Projects are not entirely good or bad on their own. They have to match the person doing them: you! Be honest with yourself about what your strengths and passions are. Choose a project that is fundamentally aligned with those strengths. Do NOT choose a project that relies heavily on things you are not intrinsically motivated to do. You may be tempted to pick a project to shore up on weaknesses, but don’t. Any project will have aspects that will require you to work on your weaknesses, but a project that is fundamentally aligned with your weaknesses is going to be an exercise in misery.
One of the most common questions I get from new students is how to choose a scientific project. Clearly a super important part of the scientific process, but one that has had a somewhat magical quality to it, as though there is some magic wand that one waves over a set of eppendorf tubes to turn them into a preprint that everyone wants to read. Of course, many scientists have some introspection and insight into their thought processes, and while that has largely been passed on by word of mouth, there have been some wonderful recent efforts to describe project ideation (creativity), selection, and execution (see work from Itai Yanai/Martin Lorsch, Uri Alon, Michael Fischbach, and probably several others I’m missing with apologies).
But I feel like a lot of this discussion has missed one critical feature: you. As in you, the one actually doing the project. Everyone has different strengths and weaknesses as a scientist, or more relevantly, passions and aversions. In my experience, which I’m sure many have shared, it’s the match between the project and the scientist that matters far more than the project on its own.
Why does it matter so much? Here’s my theory. Academic research is a highly unstructured work environment. It is hard to quantify, on a daily, weekly, or even monthly basis, exactly what constitutes “progress”. As such, it relies very strongly on intrinsic motivation. As in, you really have to want to do something in order to put in the sustained effort required to actually do it, because it is very difficult to quantify progress from the outside to help force you to do things you don’t want to do. It is possible to force yourself to do things you don’t want in the short term, but if you are not fundamentally excited to do something, it is very hard to keep yourself motivated to do it in the medium-to-long term.
What does this mean in practice? I think it’s easier to see how it plays out by looking at common failure modes in person-project matching. One common thing I’ve seen is sometimes people feel like they need to build experimental skills even though they are fundamentally more interested in computational work, so they want to work on a project that has a significant experimental component. Then what happens is some version of the following: “I could do this experiment today, but it’s Thursday at 4pm. I’ll do it tomorrow. Oh wait, it’s Friday, now I should probably wait until Monday” and next thing you know a month goes by and the experiment still hasn’t gotten done. Sometimes, if you take the same person and give them a dataset, they’re like “I just need this analysis to finish running by 4pm, then I can run the next step, oh wouldn’t it be cool if XYZ were true, hold on let me try this…”. It’s hard to ascribe these delays or accelerations to any one particular decision, but in aggregate, they have an enormous compounding effect. Same sort of thing the other way around.
By the way, this doesn’t mean that you shouldn’t try things, especially early on. I worked in a lab for a summer after my first year of math grad school basically as an exercise in getting some exposure to experimental work, even though I thought I’d never EVER do it for my actual thesis work. Turns out I had a true passion for experiments. Been trying to lean into that ever since! But you have to continuously evaluate and be brutally honest with yourself about whether you’re doing what you’re doing because you really like it or because you think you should like it. I’ve found graduate students often get caught in the trap of working on what they think they should like instead of what they actually like.
This same reasoning affects choice of advisor, both graduate and postdoctoral, especially the latter. Pick an advisor who can help you build on your strengths, and not someone who specializes in your weaknesses. This is not to say that you can’t have complementary skills—especially for postdocs, it is often very fruitful to combine your skills from your PhD with a set of techniques in the postdoc lab. But if you join a lab where the advisor is a skilled computationalist but you want to do some cutting edge experiments, it must be done with a lot of care. You want to be sure the rest of the environment is strong, because it will be difficult for your advisor to guide you to innovate at the edge of the field given their own strengths and weaknesses. Not to say it can’t be done, but just that it should be done very carefully.
Anyway, all that to say, when choosing a project, make sure it matches your intrinsic strengths and motivations. Research is already hard enough, work on things you like to do!
