On choosing what to work on, after Hamming

In 1986, the mathematician Richard Hamming gave a talk at Bell Labs called "You and Your Research." The talk is short, irritable, and uncomfortably honest. Hamming had watched brilliant scientists spend entire careers on problems they privately admitted were not important. The question he wanted them to answer was the simplest one: what is the most important problem in your field, and why are you not working on it?

Most researchers get visibly uncomfortable when asked that question. The discomfort is the data. A checklist for working with the question, drawn from Hamming, the literature on research-career growth, and observations from senior researchers who do this well.

Step 1. Name the field's most important open problems out loud

Most researchers cannot name three. The exercise is not rhetorical. Sit with a blank page and list the five most important open questions in the subfield. Write them as questions, not topic areas. "Generative models" is not a question. "Why do generative models produce coherent output without grounding in verifiable facts, and what would it take to change that?" is.

If only two come, that is a signal, not a verdict. The fix is to read more broadly in the subfield. For each question, write one sentence on why the answer would matter to someone other than the writer.

Step 2. For each important problem, ask why it is not being worked on

Hamming's actual question. Three answers are common.

"The tools are not there." Often true of the most ambitious problems. The fix is to take the problem seriously anyway and work on the tool. Many durable careers are built on the side project that turned into the instrument for approaching the field's hardest question.

"It is too risky." Fair, but the thing being protected is usually the next publication, not the career. Most researchers overweight short-term publication risk and underweight 10-year career risk from working on problems that did not matter. The ratio of safe to risky projects should probably be 70/30, not 95/5.

"I do not believe I could contribute." Usually a projection of Schwartz's stupidity problem (see On the importance of stupidity in research). One does not need to solve the whole problem. One needs to contribute a piece. Pick a sub-question that is actually within reach.

Step 3. Prefer problems where one's taste is unusual

The best work tends to sit at the intersection of three things:

1. The problem is important (Step 1).
2. Progress is actually possible (skills, access, time).
3. The author's taste, meaning what they find interesting and what frustrates them about existing work, is uncommon.

The third one is what most researchers neglect. If a paper frustrates the reader in a way most of the reader's peers do not share, that frustration is a signal. The reader is noticing something the field is papering over. Work on it.

A useful prompt: "What do I think is true about my field that most of my colleagues think is obvious, but when I try to explain why they think it, I cannot?" That gap is often a research program.

Step 4. Check the investment, not just the output

Research careers are evaluated on outputs: papers, citations, grants. Outputs are produced by investments: skill-building, networks, credibility. In one's twenties the balance leans toward investment; in one's forties it tips toward spending the accumulated capital. A project that pays well in outputs but teaches nothing new is a withdrawal from the investment account. A project that produces less but compounds capabilities is a deposit.

For each candidate project, ask:

• Skill. What new technique, tool, or domain will be learned?
• Network. Who will be met or collaborated with that would not otherwise happen?
• Credibility. Does this build credibility in the area the author wants to be known for in 10 years?
• Reach. Does it enable a bigger project later, or does it cap out here?

The best projects clear all four. The worst clear zero or one.

Step 5. Work at the rate sustainable for ten years, not one

Hamming's talk contains a now-famous line: "Great scientists have greater drive. Apparently everyone who makes it has drive." He is right, but the line is widely misread as endorsing 100-hour weeks. What he means is: show up every working day with full attention, for decades.

A 70-hour week for a year is not more productive than a 55-hour week for ten years. Consistent, focused work over a long horizon compounds in ways a sprint does not. The reliable failure mode is the reverse: a three-year sprint followed by drift. Pick a sustainable pace and protect it.

Step 6. Be promiscuous about ideas, selective about projects

Read widely. Talk to people outside the subfield. Generate ideas cheaply. Commit to projects slowly, and only after the idea has survived:

• The rivals test (what else could explain the pattern this idea is built on?).
• The one-month test (is it still interesting in a month, or was it a shiny-object moment?).
• The so-what test (if the answer arrived today, what would change?).

Most researchers do the opposite: read narrowly, commit quickly. That is how a field ends up full of people producing variations on the same paper.

Step 7. Do not be afraid to drop a project

Midway through, sometimes the problem turns out to be smaller than expected, the approach has a fatal flaw, or the author's taste has moved. Stop. Write up what was learned as a short internal note. Put it in a drawer. Move on. Sunk cost ends more research careers than lack of talent.

A practical weekly habit

Once a week, on a fixed day, spend 30 minutes on two questions:

1. Did the past week move me closer to one of my field's important problems?
2. If not, what will I change next week to course-correct?

The point is not ceremony. It is a regular bookmark. Most of the drift in a research career happens at the week-to-week level, not the year-to-year level. A small Friday correction compounds.

Hamming's talk closes with a line worth keeping: "If what you are doing is not important, and it is not going to lead to anything important, why are you doing it?" Ask it once a month, kindly. The first answer does not have to be satisfying. The point is to have started the conversation.