What are the important problems in your field?

Most people choose a role and inherit its problems. Choose the problem first, then find the role that lets you work on it.

In 1986 the mathematician Richard Hamming gave a talk at Bellcore called You and Your Research. In it he described eating lunch with the chemists at Bell Labs. For a while he asked them, “What are the important problems of your field?” A week or so later he asked which important problems they were working on. Some time after that he asked why, if their work was not important and would not lead to anything important, they were at Bell Labs doing it.

He was not welcome at that table after that. But one chemist, Dave McCall, told him months later that the question had stayed with him all summer. Hamming noted that McCall was made head of his department a couple of months later, and later became a member of the National Academy of Engineering. He never heard the names of the others at that table in scientific circles.

Hamming’s point was blunt. “If you do not work on an important problem, it’s unlikely you’ll do important work.”

That does not mean every scientist should drop incremental projects for grand questions. Important research often rests on unglamorous groundwork, and curiosity-driven discoveries are hard to predict. Hamming’s question is most useful when career incentives start to choose the work for you.

Titles are not problems

Ambitious people often think about careers as roles to reach, such as professor or founder. A role tells you little about what someone will accomplish. A professor can hold a prestigious chair without making a major discovery. A founder can build a company that nobody needs. Someone working quietly on a neglected problem can matter more than both.

Pick the problem first, and let the role follow from it. The role is only the vehicle. Some problems are best attacked from a lab and others from a company.

Start where the solution would be used

A common mistake is to start with a technique and look for somewhere to use it. A new kind of model appears, and people go looking for an industry to apply it to. That sometimes works, but it tends to produce impressive answers to problems nobody urgently has.

The Epic Sepsis Model shows what happens when a score stands in for the problem. It is used at hundreds of US hospitals to warn clinicians about sepsis. When researchers at Michigan Medicine checked it against 38,455 hospital stays, it missed 67% of the patients who developed sepsis while raising alerts for 18% of all stays.

The real problem was catching sepsis early without burying clinicians in false alarms. A score was only one possible means. Stanford Biodesign’s innovation process is built around this. Before anyone invents anything, trainees spend time watching the full cycle of care and listing unmet needs. That order can save months of effort on an impressive answer to the wrong question.

Important is not enough

An important problem is not automatically a good one to work on. The career-advice organization 80,000 Hours compares problems with a simple framework, and it works as well for a PhD topic as for a startup.

Three tests for a problem

Scale is how much good solving the problem would do. Neglectedness is how few people already work on it. Solvability is how much progress more effort would buy. A problem that fails any one of these is a weak bet, however good it sounds.

Many famous problems are huge but crowded. Many neglected ones are neglected because nobody can make progress on them. The good choices pass all three tests at once. None of the three can be measured precisely, so treat them as prompts to find out what is already being done and where a new contribution could matter.

Your edge

80,000 Hours adds a fourth factor, personal fit. The best problem for you is one where your knowledge lets you see something others miss.

That edge usually comes from long exposure. A researcher who has worked with genomic data sees weaknesses in existing methods that a general software engineer would miss. A clinician knows why a promising tool will not fit a hospital’s routine. People who combine two fields, such as biomedicine and machine learning, often notice openings that neither field sees alone.

The limit of expertise

Familiarity also creates blind spots, because the way your field does things starts to look inevitable. Deep knowledge of one field works best paired with curiosity about how other fields handle similar problems.

Before anyone commits years to a problem, the attempts that already failed are worth reading. They often show which obstacle is really holding things back. Choosing well also does not mean committing for life. Problems get solved or overtaken, and the choice is worth revisiting whenever the evidence changes.

Hamming’s question is about the work already on your desk, and whether it connects to something you actually regard as important. That is worth knowing before the next few years disappear into a full calendar.