During your PhD: learning to do research

A PhD is an apprenticeship in research. At the beginning, somebody else may give you a fairly concrete question and point you towards the relevant literature. By the end, you should increasingly be able to decide which questions are interesting, how to attack them, what you need to learn, when an argument is convincing, when to ask for help, and when to abandon an approach.

That is a lot to learn. It is also quite different from learning mathematics or statistics in courses. There is no syllabus for becoming a researcher.

This page grew partly out of advice pages that I found very useful when I was starting in research. In particular, Csaba Szepesvári had a page called Prepared for Research? (General Advice), which is no longer online. It collected advice by Terence Tao, Fan Chung, Gian-Carlo Rota, Michael Nielsen, J. Michael Steele and others, with Csaba's own comments. I have kept here the ideas that I still find useful, rewritten them in my own words, and credited the original sources where possible. Aaditya Ramdas's checklists for Stat-ML PhD students are another excellent source. I do not agree with every recommendation in all of these pages; advice is always shaped by the person, field and time in which it was written.

1. The main thing you are learning is how to do research

Aaditya makes a point that I think is easy to underestimate: by the end of a PhD we expect people to be able to write papers, give talks, review work, navigate conferences, develop a coherent research direction, and make many small professional judgements that they were rarely taught explicitly. His checklists are an attempt to make some of that hidden curriculum visible.

I would add one skill above all the others: research judgement. Which question is worth another week? Which assumption is doing the real work? Is a technical difficulty fundamental or an artefact of your formulation? Is a negative result telling you to stop, or telling you something interesting? Is a theorem stronger because it is more general, or weaker because nobody can see what it says?

You develop this judgement by doing research, seeing many examples, making mistakes, talking to people, and paying attention to why some projects work well and others do not. It develops gradually. You are not supposed to arrive with it.

2. Protect time in which you actually do research

Steele's old Advice for Graduate Students in Statistics stresses regular, concentrated research and reading. Csaba singled this out on his advice page. Steele gives a very specific prescription in hours; I see those numbers as his personal recipe. The underlying idea is excellent.

A day can be completely full without containing much research. Email, meetings, teaching, seminars, administration, fixing LaTeX, checking simulations and reading messages are all real work. Deep mathematical thinking needs stretches of time in which your attention is on one difficult thing.

Learn what this looks like for you. For some people it is two quiet hours first thing in the morning. For others it is a long afternoon with paper and pencil. Put those blocks in your week and protect them. A PhD gives you more control over your time than many later academic jobs will. Use some of that freedom to learn how you think best.

Regular contact with a problem matters too. A difficult proof often becomes much harder when you leave it untouched for ten days and have to reconstruct your own thoughts each time you return.

3. Learn how to find and shape questions

Early in a PhD, it is perfectly normal for your supervisor to supply much of the research direction. Independence grows in smaller steps. You start noticing an assumption that might be removable, asking what happens in a special case, spotting a connection with another paper, finding an example that does not fit the story, or suggesting a cleaner formulation.

One of the best parts of Steele's advice is his description of how he looks for problems. First learn the key results and examples. Reproduce calculations or proofs when that helps. Strip away machinery and try to understand the phenomenon underneath. Then ask simple questions about that phenomenon. Work on them long enough to discover what is wrong with the question, refine it, and repeat.

I find that a useful way to think about research. A good question often starts in a slightly clumsy form. You do not have to wait for a beautiful problem to arrive fully formed.

Tao's graduate-level career advice contains a related warning against becoming fixated too early on one grand problem or theory. There is a lot to learn from smaller questions: they teach you techniques, expose you to the literature, produce examples, and give you a sense of which obstacles are real. Over time you can take on larger and riskier questions.

When you are stuck, also change the question before assuming you need a more powerful theorem. Try the smallest nontrivial case. Remove one complication. Strengthen an assumption temporarily. Compute an example. Search for a counterexample. Prove a weaker statement. Ask what would be enough for the application you actually care about. Many useful research questions are discovered this way.

4. Read papers actively

Reading research papers is a skill of its own. You usually do not need to read every paper from the first word to the last.

Start by finding out what problem the paper is solving and what the main claim is. Look at the definitions and theorem statements. Ask why the result is interesting, what assumptions it needs, and what would fail without them. Then decide which parts deserve a slow read.

For an important proof, close the paper occasionally and try to reconstruct the next step yourself. For an empirical paper, ask what comparison would convince you and then see whether the paper makes it. If there is a simulation, try reproducing a small part. If an argument feels obscure, write down exactly where you stopped understanding it.

Also form an opinion. What is the strongest part of the paper? What is weak? What remains open? Which idea could be useful somewhere else? Csaba used questions like these when asking prospective students to discuss papers, and they remain good questions throughout a PhD.

Aaditya's checklist collection includes a short guide on reading papers. Tao also has a nice piece on getting stuck while reading technical mathematics and how to diagnose where understanding has broken down.

5. Write much earlier than feels natural

This is advice on which Csaba, Steele and I all agree: start writing before the work feels finished.

Writing is part of the research process. A proof that felt obvious in your head can acquire a hole when you try to write the quantifiers correctly. A definition that seemed harmless can become impossible to use. Two lemmas may turn out to need incompatible assumptions. A simulation result can look much less convincing once you have to state precisely what it shows.

So write down small things. Write a clean statement of the lemma you think you proved. Write the simplest example. Write why the current approach fails. Keep a research log with dates, questions, attempts and next steps. If you write code, keep it organised and under version control. Your future self is a collaborator who deserves readable notes.

I would also keep failed approaches. Six months later you may rediscover exactly the same tempting argument. A short note saying “this fails because...” can save a surprising amount of time.

Once a project starts becoming a paper, write the story early as well. What is the question? What is new? Why should somebody care? Which result carries the paper? You do not have to know the final answer to all of these questions yet. Trying to answer them often tells you what the research still needs.

6. Talk about work before it is polished

Research gets better through conversation. Steele recommends talking to other people about work in progress because explaining an idea exposes missing pieces and creates connections. I have found the same thing.

Do not save all your questions for a perfectly prepared supervision meeting. If you have been stuck on the same technical point for days, tell someone exactly what you tried. Ask another PhD student. Put the problem on a board. Explain it to somebody who works on something adjacent. A short conversation can save a week, and explaining the problem often helps even when the other person has no solution.

Learn to say “I don't understand this.” Research puts everyone at the boundary of what they know, so feeling confused is a recurring part of the job. The useful next step is to make the confusion precise. Which definition do you not understand? Which implication seems unjustified? Which calculation gives the wrong answer?

Your supervisor should help you learn this process. Over time, try to bring more than a status report to meetings: bring a question, a failed proof, a conjecture, an example, a decision you are unsure about. That makes supervision increasingly into a research conversation between colleagues.

7. Build breadth and develop your own taste

Your thesis topic will necessarily be narrow. Your intellectual life does not have to be.

Go to seminars, including some where you understand only part of the talk. Attend conferences and workshops when you can. Read outside the exact problem you are working on. Talk to visitors. Learn enough about neighbouring areas to recognise when one of their ideas could help you.

Tao repeatedly recommends this kind of breadth in his career advice. It is also one way in which you gradually develop research taste: you see many styles of argument, many choices of problem, and many ways of explaining why a result matters.

Do not try to become a copy of your supervisor. Pay attention to what you enjoy and what you are good at. Some researchers are wonderful problem solvers; some are especially good at finding the right formulation; some build theory, some connect fields, some notice examples everybody else ignored. A PhD is long enough to start discovering your own combination.

8. Learn the rest of the craft

Papers are only one way research moves through a community. During a PhD you will probably also learn to:

These are learned skills. Aaditya's PhD checklists have concise guides on many of them. Steele's advice also contains good basic points about talks: have a clear structure, decide what the audience should remember, and finish on time.

Practice helps enormously. Give the internal seminar talk. Volunteer to explain a paper. Ask a senior researcher if you can compare referee reports after you have written your first one. Ask for feedback that is concrete enough to use on the next attempt.

9. Treat research integrity and reproducibility as part of the research

Good research practice starts long before a paper is submitted.

Keep enough of a record that you can reconstruct what you did. Use version control for code. Store data and derived data sensibly. Record random seeds and simulation settings when they matter. Cite ideas and software properly. Discuss authorship early enough that nobody has to guess what the expectations are. If you find a mistake, investigate it and correct it.

For researchers in the Netherlands, the KNAW research-integrity page is a good entry point to the Netherlands Code of Conduct for Research Integrity and the Dutch system around it. Your university will also have local rules and confidential advisers.

Tools change too. Code assistants and generative AI can be useful, but you remain responsible for what goes into your work: the mathematics, the code, the references, the confidentiality of data, and the final text. Learn the rules that apply in your field, journal and institution.

10. Take care of the brain that has to do the thinking

This is one of my own hobbyhorses. Deep mathematical thinking requires a well-rested brain. I think about taking care of the brain in much the same way that an athlete takes care of their body: if you expect it to perform difficult work, you also have to give it what it needs to be in good shape.

For me, the basics are enough, good and regular sleep, healthy food, and plenty of rest. Rest can mean hobbies, leisure, family and friends, and the details will be completely different for different people. For some it is sport; for others music, church, board games, cooking, reading novels, being outdoors, spending time with children or friends, or something else entirely. Usually it is some combination. For me, it includes almost everything on that list, some of it for many hours a week.

There is no universal recipe. The aim is simple: to arrive at work on Monday morning with a fresh brain, ready to take in complicated things and to do complicated things itself.

I see this as an essential part of doing good research. A tired brain can spend six hours circling a problem that a rested brain sees through in one. Rest also gives ideas time to settle. Some connections appear precisely when you have stopped actively pushing on them. I don't think it is a coincidence that people so often get good ideas in the shower: for a little while, the brain is forced to disconnect. No screen, no audio input, no responsibility for a baby or a pan on the stove. There is simply some room for thoughts to wander.

Michael Nielsen's Principles of Effective Research makes a closely related point: health, relationships and life outside research support good research over the long run. Aaditya also puts work-life balance among the first topics in his PhD checklist collection.

Use your holidays. Have evenings and weekends that are, most of the time, completely unrelated to your thesis. Serious research does not require being mentally at work every waking hour. In my experience, the opposite is closer to the truth. Think of the training schedule of an endurance athlete: recovery is part of the training.

It is also worth remembering that not all academic work requires the same kind of concentration. Teaching, email, administration and organisation take time too, and it is perfectly normal to spend several hours a day on them. A few hours of genuinely deep thinking is already a lot. For most of us, trying to do that all day is simply impossible, and trying to do it day after day is not sustainable.

11. Your PhD and your career belong to you

Steele makes an observation that I still think is important: academics tend to advise PhD students from the perspective of the career they themselves know. That can quietly turn “What would be good for you?” into “What would prepare you for an academic career?”

Tell your supervisors what you want, as far as you know it. If you are interested in an academic career, say so. If you are curious about industry, government, a research institute, teaching, entrepreneurship or something else, say that too. You are allowed to change your mind.

This also affects what you choose to learn. A student aiming for a theoretical postdoc may make different choices from somebody who wants to move into clinical research or a technology company. Both can have excellent PhDs.

12. Gradually take the initiative

By the later part of the PhD, start noticing which parts of the research process you can initiate yourself.

Find a paper without being sent it. Suggest the next lemma. Contact somebody whose work is relevant. Propose a small side project. Organise a reading group. Decide that an approach has had enough time. Draft the email to a collaborator. Sketch the paper before your supervisor asks for it.

Tao has a useful short piece called Take the initiative. The transition is gradual: supervision should still be there, but the centre of gravity moves. By the end of the PhD, the research should increasingly feel like something you are driving.

If I had to condense this page

A PhD does not have to turn you into a finished researcher. I am not sure anybody ever becomes one. It should leave you much better at finding your way through a problem that nobody has solved for you.

Further reading and sources

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