Starting a research project
Picking a topic to research, be it for an undergrad, MSc, or even PhD dissertation, is nothing short of daunting. Spending 6 months to 6 years on anything will feel existential. That’s normal. It’s part of the process. It’s a sign that you care, and that’s what we as advisors want to see. Below is a rough guide that I’ve developed over the past few years to help students when they are struggling to narrow down their interests.
For better and for worse, it starts with a puzzle.
When picking what to research you usually begin with the normative issues that you care about – corruption, climate change, political violence. Or a country that you want to learn more about. Either of these are important pre-requisites to come up with a viable dissertation, but thinking in those terms will leave you flailing. You need to be on the search for a puzzle. This means something quite specific in social science terms – it’s an empirical outcome that our theories fail to explain. You’ve found a puzzle when everything you know/that’s been written on a research question fails to predict what you are actually seeing in the world.
Here’s an example from my PhD Dissertation. Through the late 2000s and early 2010s a whole bunch of Russian plutocrats started suing each other in foreign courts. Russian v. Russian fighting over assets back home but dueling at the London High Courts. Yes. Very Weird. A small amount of scholarship and journalism analyzed why these disputes were occurring, with most agreeing that these were prototypical instances of “forum shopping” = claimants going to a foreign court in search of neutrality and legal precedent that would increases their chances of victory. They were shopping for the rule of law.
But that didn’t explain why the Russians only started going to London in the late 2000s. What about the ‘90s when the court system was weak and Russian commercial law was in its infancy? Moreover, most emerging markets by definition have limited rule of law. Where were all the Chinese and Saudis storming London’s Fleet Street?
Explaining this puzzle – existing theory couldn’t full uncover what was happening with the Russians (or the Chinese or Saudis) and their relationship to the London courts – became the basis of my academic life for embarrassingly long.
To find a puzzle you need to know the literature
This is going to sound like I am contradicting the first heading, but to find a puzzle you first need to know what other people have said about the phenomenon you are interested in.
Hopefully you’ve already taken a class or two on the topic you are hoping to work on, which should give you the foundations you need to figure out what other people have said. That said, research projects are often far more narrow seeming (more below) than even a week of a semester long course.
How do you know when you’ve done enough reading of the academic literature? This is really important – students spend way too much time on this task. Why? Because it’s easy to convince yourself that downloading and skimming articles is a good use of your time.
You’re done when you’ve basically created 2-3 “camps”. Groupings for arguments made by different people. When you start to read a handful of articles and you can easily place them into one of the camps you’ve identified, it’s time to move on.
But exactly are camps? They can range in specificity but let’s consider work on democratization. You can fundamentally divide them into scholars who see it as a process driven by elites, by bottom-up pressures from the masses, or international dynamics. While scholars have extremely insightful nuanced views within each of the camps, you can often place a scholarly work quickly into one of these three.
You need variation
A puzzle isn’t just something odd or unexplained — it’s something that’s puzzling because it doesn’t align with what we’d expect from theory. And that means you need variation. You want to look at cases or instances where actors faced similar conditions but chose different paths — or where similar actions produced different outcomes.
Too often, students choose cases where “everything went wrong” or where everyone behaved in similar ways. But without variation, there’s no contrast, no counterfactual, and ultimately nothing specific to analyze.
Explaining why Tunisia democratized when Egypt didn’t? That’s variation. Trying to understand why multinational companies pull out of some authoritarian states but stay in others, even when both are cracking down on dissent? That’s variation. Variation is the oxygen your puzzle needs to become a full-blown project. If you only have a single country doing a single thing, it’s going to be very hard to say anything analytically meaningful let alone new.
A good puzzle links to multiple research questions.
Puzzles worth writing on, counterintuitively, appear narrow.
The right puzzle will be precise in its empirical focus *and *opens the door to several broader debates. That’s how you get leverage. On its surface, my book seems like it is on the nichest at topics. At an empirical level it definitely is! But theoretically it’s about helping us understand how elites behave under weak rule of law, when global finance reshapes domestic institutions, and why certain groups mobilize politically while others stay quiet.
No single work can answer a Big Question like “what causes civil war?” or “what’s the future of democracy. That’s a collective field-wide effort. But the goal should be for your case – your specific, strange, under-explained thing – to help us think differently about those bigger questions.
Your empirical puzzle is the entry point. The research questions are the paths it can take you down. And ideally, some of those paths will intersect with well-trodden academic terrain — you’re not just adding to the conversation but pushing it forward.
Strategies to find a puzzle
There’s no single formula for finding a puzzle, but here are a few strategies that have worked well for students I’ve supervised:
Go deep into an unfamiliar context: Pick a country, industry, or organization that isn’t as widely studied and just start reading everything you can. Often, what looks “normal” from the inside seems bizarre from the outside. Make a list of the things that feel odd or unexpected — especially the ones that seem to go against the theories you’ve been taught.
Use the news to think across contexts/time: Skim 30–40 articles on a broad topic like AI regulation, sovereign debt, or labor markets in the gig economy. Apply theories you’ve learned. What doesn’t fit? What seems consistently under-explained or mis-explained by standard academic models? Journalists, by design are closer to the action/weirdness.
Mine the final sections. The concluding sections of journal articles and books are treasure troves. Scholars usually spell out what they think are the next big questions, what remains unresolved, and what would be a natural extension of their work. These are puzzles waiting to be picked up.
Lean on review essays: Review articles — especially those in Annual Review of Political Science or published occasionally in IO, BJPS, and World Politics — are excellent maps of the scholarly terrain. They’ll tell you where consensus exists, where debates rage, and where the gaps are. And it’s often in those gaps that you’ll find your puzzle.
If you’re feeling overwhelmed, that’s not a sign you’re doing it wrong. Good dissertation topics aren’t born fully formed; they’re built through sitting with the weirdness of the world. Start with a puzzle that genuinely bothers you, one that sticks in your head longer than it should.