Research taste interview questions

What would you work on if you had complete freedom?

Name something specific, say why it matters, why it is tractable now rather than five years ago, and what your first experiment would be. A vague area name reveals that you have not thought about it concretely.

What do you think is overrated in the field right now?

Answer with a real opinion and a reason, and be fair to the other side. The question assesses independent judgement, and refusing to have a view scores worse than having a defensible one an interviewer disagrees with.

What surprised you recently?

Something specific you expected to go one way and did not, and what you concluded. Following up on your own surprises is how directions are found, and the answer shows whether you do that.

How do you find research problems?

Read for gaps rather than results, especially limitations sections, which are authors honestly saying where the work stops. Keep a running list of questions you cannot answer, follow up your own surprises, and read adjacent fields where a standard method may be unknown.

What do you do when a result surprises you?

Follow it, because a surprise is a gap in my model of the field and those are where directions come from. I write it down rather than shrugging it off, which is what most people do.

How do you decide whether to abandon a research direction?

Design the cheapest experiment that could falsify it and run that first, and write down in advance what result would make me stop. Then judge whether the next month is the best use of the next month, ignoring what has already been spent.

When is persisting after a negative result right?

When the failure is mechanical rather than conceptual and I can name exactly what went wrong, or when strong people keep independently suggesting the idea. Not when I am persisting because stopping would feel like failure.

What would you pre-register before running an experiment, and why bother?

The quantity, the comparison, the noise floor measured on the baseline first, and the threshold that makes me stop — plus an explicit list of the moves I am not allowed to make afterwards, such as changing the eval set or dropping seeds. The point is the timestamp: it is a promise made by someone not yet invested to the person who will be invested in six weeks and will find sincere reasons why the disappointing number does not count.

Pitch me a research project in two minutes.

State the question in one sentence, why it matters and to whom, why it is tractable now, the first cheap experiment and what result would make you stop, and what you would do if it works. Stop there and invite the hard question.

What gets marked up. Marked up for a falsifiable first experiment and a pre-stated kill result. Enthusiasm without a test is marked down.

Pick a paper you admire. Why was it a good research bet at the time?

Describe what was believed before, what had changed to make it tractable, why it was a natural next step others missed, and why the answer would have been informative either way. Then say what you took from it for your own choices.

What gets marked up. Marked up for naming a constraint that changed and roughly when. Marked down for an account that reduces to the authors being cleverer than everyone else, which is unfalsifiable and teaches nothing.

Name a direction a lot of people worked on that did not pay off. What signals were visible at the time?

Pick one and be fair to it, since the useful cases are the ones where the argument was good. Then name the signals: results demonstrated only at small scale, a cost that grows rather than shrinks as hardware improves, or a direction motivated by a defect in the incumbent rather than by a measured bottleneck on a task anyone cared about. The last is the one worth carrying, because it is what your own ideas will feel like from the inside.