One of the most daunting prospects for a fresh graduate student is having to develop a solid research question . In my experience, many graduate students feel like they don’t even know where to start. The literature can seem overwhelming, everything has already be done by somebody, and in any case it’s impossible to really know all the literature there is anyway. Making matters worse, almost every cohort or lab inevitably has one or two students who just seem to be fountains of good ideas, who constantly come up with new research ideas they want to pursue. As a result, students who are less inventive or less imaginative can feel like they’re not cut out for a career in research, they’re never going to have the necessary ideas to sustain a research program.
I strongly believe that having good ideas is a skill that can be learned. There are simple strategies that almost always work. In the following, I describe one strategy in particular that I’ve found useful over the years.
Define a vision for your research
Before you start doing any concrete work towards developing your specific research question, you need to know what broad topic you want to work on. I call this the research vision. It turns out that developing a research vision is not that hard, for two reasons: First, the vision doesn’t have to be that specific; it doesn’t have to come with specific ideas for projects you want to do or questions you want to pursue. It’s just a guiding idea that tells you where to start. For example, a vision could be “I want to do computational work in cancer genomics” or “I want to study experimentally how bacteria adapt to novel environments” or “I want to work in infectious disease epidemiology.” Second, choosing a particular vision over another one is generally a low-stakes decision. There is interesting and valuable research to be done in the context of nearly any reasonable research vision.
The one thing you should double-check though, in particular as graduate student or postdoc, is whether the vision you want to pursue fits broadly into the topics your lab is working on. If you’re in a molecular biology lab that studies cancer genetics but your research vision is to investigate the effects of climate change on future precipitation patterns then you have a problem. In this situation, either find a different research vision or consider switching labs .
Read the literature
Once you have decided on your research vision, you need to start reading the relevant literature. There are two ways to proceed: First, if your research vision matches well with the work that is already going on in the lab you’re in, then start by reading the lab’s papers. Also, ask your PI for suggestions on which papers to read. Use all these papers as your starting point for a careful literature search.
Second, if your research vision deviates somewhat from the current direction of the lab , or if there are other reasons why you can’t ask anybody for relevant papers, then skip right ahead to the literature search.
To start your literature search, enter some key words or phrases into Google Scholar and see what comes up. Google Scholar tends to place the most highly cited papers at the top of its search results, so you’ll almost never go wrong by looking into the top hits. Using these papers as your starting point, expand your search by reading the papers that they cite (searching backwards in time), and also look up the more recent papers that cite them (searching forward in time) . By alternating between backwards and forwards search you will develop a solid grasp of the field.
In addition to Google Scholar, the “related citations” function on PubMed is also an excellent way to deepen your knowledge of the field. Look up a paper on PubMed, and then read through the papers that PubMed flags as related to the paper you looked up.
Stop reading the literature and start doing something
It’s great to be a well-read scientist. Most students don’t read enough. There’s always something else to read. However, at some point, you have to stop reading and start doing. To give a concrete (but somewhat arbitrary) cutoff: If you’ve been reading for two months or more, or if you’re familiar with over 100 papers in your broad area, and you still feel like you don’t know enough of the literature to come up with your own project, then reading even more is likely not going to improve your situation much. At this point, it’s more important that you start doing actual research.
How do you start if you’re not sure what your project is? My recommendation is to always start by reproducing somebody else’s work. Among all the papers in your broad area that you have read, pick one or two that you liked the most, and simply try to repeat what they did . Very quickly, you will discover a few things: 1. It’s not that easy to reproduce existing work, and you can learn a lot in the process. 2. There are flaws, limitations, or pitfalls that weren’t really described in the paper. Maybe the paper’s methods work only under very specific conditions and fail the moment you try something slightly different. Or the methods are somewhat unreliable and fail at random times/under random conditions. 3. There are all sorts of things you’d like to know. Such as why the methods always fail when it’s raining outside. Or why there are certain strange trends you see in the raw data. 4. There are all sorts of things you’d like to have. Like a better way to prep your samples. Or some additional measurements no existing method can produce.
Voilà, you have your research question. In fact, you probably have more than you bargained for . You may have so many questions that you still don’t know where to start.
Keep it simple
Now it’s important to keep things simple. Of the many open questions you have, pursue the one that requires the simplest possible extension to existing work but will still provide meaningful progress.
I don’t think I’ve ever seen a student fail for trying to do something too simple. However, I’ve seen plenty of student fail for trying things that were too complicated. Most students overestimate the complexity that is required to do good science. It’s better to do something simple, write it up, and publish than to do something complicated, get stuck, and get discouraged.
You may think the whole process I propose is haphazard. I suggested you start with a random topic, do some reading, try to reproduce somebody’s work, and then pursue some extension to the work, an extension that will hopefully reveal itself to you as you work on the topic. The reason why this seems haphazard is because it is. Science doesn’t follow a simple A to B path. Albert Einstein famously said “If we knew what it was we were doing, it would not be called research.” Uri Alon calls it being stuck in the cloud. Donald Rumsfeld talked about the unknown unknowns. Even though Rumsfeld wasn’t talking about scientific research, he correctly described the world in which most scientists operate day to day. We usually don’t know what we’re doing, we don’t know where we’re going, and we don’t know what we don’t know. However, we do stuff anyway, and from time to time we stumble upon a useful and novel bit of knowledge.
 And sometimes, postdocs or even young faculty members struggle with the same issue. It mostly depends on when you were asked for the first time to come up with your own project. If your graduate project was basically handed to you by your PI, and similarly during your postdoc you were working on somebody else’s project, then you may never have independently developed a project before becoming an assistant professor.
 I would almost always recommend against switching lab while in grad school, but that is a topic for a different post.
 It may seem strange that a graduate student would have her own research vision that differs from the lab’s vision. However, this scenario is often quite productive, both for the student and for the lab. The best PhD theses can take an entire lab into a new direction. PIs are generally aware of this and want their students to bring new ideas into the lab.
 Searching forward in time used to be a complicated undertaking but it is trivial with tools such as Google Scholar. Simply click on “cited by” and see which other papers cite the paper you’re interested in.
 Of course, you have to choose a paper that uses methods and/or materials that you have access to. If your favorite paper in the field uses a mass spec and you don’t have access to one then that’s a bad paper to try to reproduce.
 That’s one of the reasons why senior scientists usually have tons of research ideas. The longer you’ve been around in science, the more you’re aware of what we don’t know.