From my notebook to the next generation

Last Sunday I was on a panel at the Young Professional and Student Day, part of the IAEE 2026 conference in Chile, a full day built around graduate students and early-career researchers, with a handful of us there to talk about building a research career in energy economics. 

One of the first questions the facilitator put to us was simple and impossible at the same time: how do you know if your research question is actually good (original, novel, publishable..)?

I have asked myself that more times than I'd like to admit — as a young researcher staring at a blank page, and later, as an editor staring at someone else's blank-page attempt. That day, I found myself trying to say out loud all the things I usually only know by instinct. I took notes through the whole session, half for whoever was in the room, half for myself. Some things you only really learn when you are forced to explain them to someone earlier in the journey than you.

The first thing that came out of my mouth was: original doesn't mean untouched. Early researchers often freeze up chasing a question no one has ever asked before, as if research is a race and someone else might beat them to it. But a well-worn question can still be yours — a new context, a new dataset, a genuinely different mechanism. It isn't about whether the question is new. It is about whether you have a good reason for asking it again, from exactly where you're standing. And underneath all of it sits a smaller, quieter question that never makes it onto anyone's slides: so what? If you can't answer that in a sentence, the question isn't ready. It won't matter how elegant the model looks.

I kept circling back to the fact that relevance and publishable are not the same word, even though we throw them around like they are. Relevance is about mattering to a conversation people are already having: it tracks the debates, the disagreements, the things people in the room actually argue about at 11pm after the wine runs out. Publishable is narrower, less romantic: can you actually answer this, systematically, with evidence someone else could check? I have read so many proposals that describe a problem beautifully and then just... stop. Never narrow it down to something testable. It's the most common failure I see as an editor, and I think it happens because narrowing feels like losing something. It isn't. A narrow, answerable question is a gift you give your future self, the one who will be up at midnight trying to finish the paper.

There was a question about the literature review. I am sure I have said it before: this debate has usually been running for decades before you arrived. You are not opening the conversation. You are walking into a room where people have been talking for a very long time, and someone's just handed you the microphone. Would you take it if you had nothing to say? That is really what a lit review is for: not proving you've read everything, but showing you know exactly where you stand, and why. What disappoints me most as an editor is the exhaustive review that never takes a position, or the one that quietly ignores an entire field that's been circling the same question from another angle for years.

There is a small habit I mentioned that I think about more than I expected. Your literature section is almost always written before you know your results, before you have any idea what you are going to find. So go back. Once the results are in, reread what you wrote and ask, honestly, whether they confirm, complicate, or contradict what you cited. Such a small step. And it is always the first thing to get cut when the deadline is breathing down your neck. But it is the difference between a paper that is actually in conversation with the field, and one that is just standing politely next to it.

By the time we got to what editors actually look for, I realised I had never laid it out in order before, not even to myself. So I did, right there on the spot, counting on my fingers like a mother reciting a shopping list to a distracted toddler: purpose and contribution visible from the introduction, so the reader can see the question coming; robustness, meaning evidence the result survives reasonable alternative choices and not just the one you happened to run at 2am; honesty about limitations instead of overselling; specificity, so that "no data available" always comes with which data; a genuine match between the question you asked and the one you actually answered, which sounds obvious and is somehow the thing that goes wrong most often; and writing quality, plainly, because flow and structure matter more than we like to admit, even in economics. Six things. 

There was also a question about responding to reviewers, and I felt myself getting almost protective of the process. Go point by point. Explain, don't defend. Not every suggestion deserves to be taken, and that is fine; but where you push back, do it with evidence and reasoning, not ego. Editors are far more open to well-argued disagreement than people expect. What we are not open to is dismissiveness. And when two reviewers flatly contradict each other, which happens more often than anyone tells you, just say so. Lay out the conflict, explain your approach, move on. Tone matters more in that letter than almost anywhere else in the whole process; funny how the thing that feels most technical is often the most human.

Near the end came a bigger question: not about one paper, but a whole career. How do you build a coherent long-term publication strategy? I didn't have a tidy answer, and I said so. There is no recipe for this, no single sequence of steps that works if you just follow it in order, the way you would follow a recipe for tiropita. I know people who built careers on one long, ambitious, slow-burning project. I know others who published often and small and built momentum that way. Neither is wrong. What I could offer was only what worked for me: co-authoring early with good people in my own department, which taught me the unwritten rules of the game faster than I ever could have alone. Aiming, loosely, for one or two sole-authored papers a year, as a kind of anchor point. And, strangely, the grant applications and evaluation exercises I used to dread turned out to be some of the most useful exercises I have had: they make you sit still long enough to ask what you actually want to spend your career on, and what you still need to learn to get there.

I left that room the way I usually leave rooms full of young researchers: a little tired, a little recharged, and thinking about how much of what we call expertise is really just a long list of mistakes we made early, that we are now trying to spare someone else.

If even one of these lands for someone somewhere, and saves them a year of wondering about things, my notebook was worth carrying halfway across the world.