Seventeen Questions to Keep Asking During a PhD

Friday. August 21, 2026 - 6 mins

I keep a short file of questions that aren’t about the technical content of any one project, but about the shape of the PhD as a whole — where I am, why the problem matters, who else is chasing it, who needs to hear about it once it’s done. This post is an attempt to turn that into an actual guide: grouped by what each question is really asking, tagged with when it’s worth asking, and linked to whatever’s actually helped me answer it.

How to use this

Four rough priorities, attached to each group below:

Gate: answer before sinking real time into a new sub-project. If the answer is vague, get digging (don’t code)!
Orient: revisit every few months and/or before major events (advisor check-ins etc). Computer vision moves fast so this can’t hurt.
Close: answer near submission (per contribution) and/or once a project arc is wrapping up. These are also, not coincidentally, the questions a paper’s introduction and discussion sections have to answer.
Ongoing: no fixed ‘periodic’ rhythm, but important to deliberately revisit to avoid drifting.

1. Problem selection: Gate

The two questions that should show up every single time before starting something new.

What are current methodologies for this problem, and specifically where are they lacking? Jason Eisner’s How to Find Research Problems makes the useful case that a large share of tractable contributions come from spotting one arbitrary or harmful simplification baked into existing work. Naming that simplification concretely is what turns “the field is lacking X” into a project.

Why is the problem, or my work on it, interesting? Remember that underexplored and important aren’t the same thing. Richard Hamming’s You and Your Research argues that important problems are usually sitting in plain sight, avoided because they look too large or too risky, and that picking one is a question of courage as much as taste. Worth also asking the meaner companion question: what’s the fastest experiment or literature check that could kill this direction outright, and have I actually run it, or just assumed it would work out?

2. Mapping the field: Orient

These take real work to answer honestly, and the honest answer changes all the time.

Which overlapping fields or principles does the work touch, and why? Worth writing down explicitly rather than leaving implicit: it’s the thing that lets you talk to people outside your own subfield without losing them halfway through.

Who is working on similar topics? This one is a task, not just a question. There are plenty of resources out there which build a co-citation map in a blink, a much better source of truth than a vague sense of “I think there’s a group doing something similar.”

In which direction is the field or problem currently going? Best answered by actually tracking a handful of venues and a handful of people over time (this is why someone comes along and clusters CVPR papers by keyword every year: it’s a real question people want answered).

What paradigm shifts has the field been through in the past few years? Thomas Kuhn’s The Structure of Scientific Revolutions is the actual source of the term “paradigm shift,” and it’s worth reading the concept in its original, more specific form.

(Lit study) What foundations does the problem or the work lie on, and have any been under-examined? Pairs naturally with a deliberate novelty check before committing serious time to a direction, better to do this at the start than to discover at the review stage that a “headline” result was already published.

3. Positioning yourself in time: Ongoing

Where am I currently? Where did I start? Mostly narrative, but these come in handy for a talk: they give perspective and help you spot your own patterns of doing research (how exactly did I drift? why?).

4. Contribution and reach: Close

To be answered during project wrap-up and/or paper-writing prep.

What form can the contribution take, and for which publications or venues? In How to Write a Great Research Paper Simon Jones makes the case that you should be able to state the contribution as one crisp sentence before writing the paper. If that sentence doesn’t come easily, the contribution isn’t settled yet.

How can the work, or its contributions, aid others on similar or on different problems? Worth answering concretely: it’s usually a clue for the next paper, or the next collaborator.

How generalizable is the approach? Does it relate to other fields or methodologies? This is the territory PLOS’s Ten simple rules for surviving an interdisciplinary PhD covers, including the failure mode of overclaiming an approach’s reach into a field you don’t yet understand well enough.

What are the implications of improving this specific problem? Who is affected, and how? The natural follow-up to the “why is this interesting” question. If the honest answer to “who’s affected” turns out to be thin, better to find that out before putting more time in, not after.

5. People and dissemination: Ongoing

(Dissemination) Who needs to know about this work, and what’s the clearest way to communicate it? Simon Jones’s talk How to Give a Great Research Talk, is built around exactly this question. Start from what the audience already cares about rather than from the chronology of the work (nobody cares which side of the canvas Picasso started painting from).

What or who are my research role models? Who’s a great scientist in my book, and what do they actually do differently?

Who do I want to work with, and why? Eisner’s How to Evaluate an Advisor turns this into a checklist of concrete traits: does this person hand you problems or their own agenda, do they publish with their students, and/or how do they actually handle a student’s direction failing.

What would I like to teach others about this work, and how could I get others involved? Imagine building a university course around it. This is a decent test for whether the problem is understood from first principles, or just from habit, and is worth sketching out even if the course never happens.

Conclusion

Grouped this way, the seventeen questions turn into four different rhythms: two gating questions before every new sub-project, five field-mapping questions on a rough biannual clock, four closing questions that double as paper-writing prep, and the rest as ongoing background maintenance. Worth keeping this open at the key checkpoints of the PhD: the Exposé, the thesis document, and everywhere in between.