The summer before my final undergraduate year, I was in Tallinn. I wasn’t there for research. Tallinn was one of the stops on my hitchhiking trip from Helsinki back to Prague. During that stop I learned that public transport in the city was fare-free for its residents. “Cool,” I thought at the time, and left the city behind without thinking much more of it.

Months later, I found myself staring at an empty screen, wondering what to write my bachelor’s thesis on. That is when I remembered Tallinn and its fare-free public transport. A quick search told me two things. First, there were no bachelor’s or master’s theses on fare-free public transport written in Czech. Second, the academic debate in Czechia had barely touched it either. It was a marginal topic, and that was exactly what drew me in. There was room to stake out ground rather than crowd into someone else’s.

That topic carried me through a bachelor’s thesis, a master’s thesis, and eventually a publication-based PhD. Along the way I learned something that sounds obvious but matters greatly: I set realistic goals and mostly kept them. Luckily, the research never seriously fell apart. The one thing I couldn’t control was peer review. With a PhD built from published papers, a long review or a rejection wasn’t just a pain. It threatened to stretch the whole degree out by months or even years.

The Harder Choice Came Second

What nobody warns you about is that the second topic is harder to choose than the first.

When I finished my PhD, I expected relief and satisfaction. To my surprise, I also felt a kind of drift. I knew I couldn’t be the fare-free transport person forever and that I needed something new. But nothing pulled at me the way Tallinn once had. Part of it was plain fatigue. Part of it was something I didn’t want to admit. The obvious move was to grab a safe, publishable topic, something that would keep the papers coming and the CV growing. I had the skills to do it. I just couldn’t make myself care about research chosen only for safety.

So I did something that looks irresponsible on paper. I didn’t force it and took my time. I finished the papers I still had in progress, kept the lights on, and waited, hoping I’d collide with a topic and a question that would grab me the way the first one had.

What the Research Says About Choosing Research

I later understood that my reluctance wasn’t laziness. I was resisting something the whole system quietly rewards.

Uri Alon (2009), in a short essay in Molecular Cell, points out that scientists almost never discuss openly how they choose problems. That silence, he writes, “leaves a vacuum that can lead to approaches such as choosing problems that can give results that merit publication in valued journals, resulting in a job and tenure.” In other words, the default is to let publishability choose for you.

There’s data behind the instinct too. Foster, Rzhetsky and Evans (2015), studying millions of biomedical papers, found that most research plays it safe, building incrementally on established questions rather than pursuing risky new links. Safe work is more likely to be published. Risky, innovative work is more likely to be ignored, but also more likely, if it lands, to earn high impact and recognition. And what do they conclude? On average, the extra reward from risk doesn’t justify it. In their reading, the institutions of science end up favouring tradition over innovation.

In Central Europe the pressure wears a local uniform. Polish academia runs on a points system, where each journal on the ministerial list carries a point value, and those points feed the national evaluation that judges the quality of universities, disciplines and individual researchers. They function almost like currency. And this is where the collision becomes concrete. Every time I decide where to send a paper, my instinct is the professionally sound one: aim for a journal with real standing in my field, respected internationally or at least across Europe. Yet some of those respected journals carry remarkably few ministerial points, while others, with far weaker reputations, carry many. This isn’t just my impression. In 2022 the Polish Political Science Association publicly warned that the ministerial list includes titles overlapping with lists of predatory journals. Judged by points alone, a serious journal from a respected publisher can look no better than a venue few would trust. The metric meant to measure the worth of my work can pull against my own judgement of where that work belongs. And the deeper problem is that the Polish system sits partly apart from what the wider academic world counts as good. This leaves you with an uncomfortable choice. You can collect points at home, or build a record that looks credible to colleagues abroad who don’t know the system and simply see where you published. Optimise for one and you can quietly undermine the other.

Interest Is Grown, Not Found

There’s a tempting myth here, that somewhere out there is the one topic you’re destined for, and your job is simply to find it and live happily ever after. My own experience fits a different picture. The fare-free public transport idea didn’t arrive as a passion. It started as something I happened to learn on a stopover in Tallinn and then chose to grow into something more. Psychologists O’Keefe, Dweck and Walton (2018) tested exactly this. People who believed interests are fixed, something you discover rather than develop, expected a true passion to supply endless motivation, and their interest dropped faster once the material got difficult. A topic doesn’t have to thrill you on day one. It has to be something you can imagine still caring about in five years, when the novelty is gone, the reviews are slow and the house is burning.

I should be honest about one limit, which Alon himself admits: not everyone is free to choose. Time, funding and looming grant deadlines don’t always allow a long, unhurried search. The luxury of waiting for the right topic is exactly that. Unfortunately, it is a luxury that is not evenly shared.

The Second Choice

When the new topic finally came, it didn’t feel like a bolt from the blue. It felt like something resurfacing. As a teenager, around fifteen or sixteen, I read Zoo Station: The Story of Christiane F. (Wir Kinder vom Bahnhof Zoo), the late-1970s book in which two journalists, Kai Hermann and Horst Rieck, reconstructed from interviews a Berlin teenager’s slide into heroin addiction. I still remember reading it cover to cover and, as soon as I finished, asking the librarian to recommend other books from that world. Years later I realised the pull I’d felt back then was still there. I ran a small search of the literature and found that geography, my own discipline, had barely engaged with the topic. And there it was again! An “empty” field with room to stake out ground, the same pattern that had drawn me to fare-free public transport, and to shared e-scooters before I set them aside for the PhD.

So I wrote a project proposal to find out whether that gap was real and to build something useful. Research that fills a blind spot on the map and speaks to practice and society, not just to my publication count. That became Geographies of Recovery, which only properly began this October. The hard days will come. Every project has them. But this time I’ve chosen a topic with a purpose I can point to, one that matters beyond my CV. I’m counting on that purpose to be the anchor when progress slows to a crawl and I feel like I’m standing still.

Before You Commit

If there’s a lesson in all this, it isn’t “follow your passion.” It’s something more modest and, I think, more useful. Before you commit to a research topic, a decision that will quietly shape years of your life, it’s worth asking yourself three questions.

Is there a gap? Not whether the topic is fashionable, but whether there’s genuine room to stake out ground of your own.

Can I set realistic goals and hold them? The grand question means little if you can’t break it into steps you can actually reach.

Will I still care in five years? When the novelty fades, the reviews drag, and the points system pulls you somewhere you’d rather not go, will the topic still feel worth it to you, and ideally to someone beyond you?

A research project is a long-distance run. The topic doesn’t have to dazzle you at the starting line. But it does need to be something you can keep caring about long after the excitement wears off, because that caring, more than any metric, is what carries you to the finish.

References

Alon, U. (2009). How to choose a good scientific problem. Molecular Cell, 35(6), 726–728. https://doi.org/10.1016/j.molcel.2009.09.013

Foster, J. G., Rzhetsky, A., & Evans, J. A. (2015). Tradition and innovation in scientists’ research strategies. American Sociological Review, 80(5), 875–908. https://doi.org/10.1177/0003122415601618

O’Keefe, P. A., Dweck, C. S., & Walton, G. M. (2018). Implicit theories of interest: Finding your passion or developing it? Psychological Science, 29(10), 1653–1664. https://doi.org/10.1177/0956797618780643

Polish Political Science Association. (2022, February 21). The Polish Political Science Association position on the so-called “predatory journals”. Council of Scientific Societies, Polish Academy of Sciences. https://rtn.pan.pl/en/news/174-ppsa-position-predatory-journals