Professor Gershman’s Advice for Young Researchers
This post is a translation of Harvard psychology professor Samuel Gershman’s presentation titled “Advice for Young Investigators.” It provides thoughtful guidance to help new graduate students navigate the process of choosing and starting a research project.
1. Choosing a Problem
Many students struggle to find a suitable research project when they start graduate school. Undergraduate students often learn science as a body of knowledge, not as a set of intellectual activities. As a result, they graduate with interests in specific topics but little understanding of what to do with those interests. But science is fundamentally a problem-solving activity. A researcher needs to either (1) identify phenomena that are not well-explained by existing theories, or (2) propose new phenomena that challenge current theories. A good research problem for new graduate students is one that others consider important but is also feasible within the time frame of a Ph.D. program.
2. Strong Problems
In an influential paper, Platt (1964) suggested that some fields advance faster than others because they make use of ‘strong inference‘—a method of designing experiments that can distinguish between alternative hypotheses. Although this approach seems intuitive, many scientists operate without theories that generate clear, testable predictions. Some adopt a “measure first, theorize later” attitude, which often leads to a random walk through experimental space. A ‘strong problem’ is one that lends itself to strong inference, meaning that a young researcher should seek out unexplained phenomena that could differentiate between competing theories.
3. Little Problems and Big Problems
Most of us naturally want to tackle big problems, but holding on to an ambitious problem with uncertain prospects for years can be harmful to your well-being. Spending years on a daunting project with uncertain outcomes can be a recipe for demoralization. Therefore, Gershman suggests that students work on two different time scales: focus on small, short-term problems (months) while gradually making progress on larger, long-term problems (years). No matter how small the intellectual output may seem, its psychological benefits should not be underestimated. Working on problems of varying scales can also help alleviate feelings of boredom and frustration.
4. Embracing Uncertainty
Science often canonizes ideas prematurely. Certain theories may seem solid and well-established until you examine them closely. However, an important issue is that we sometimes overlook how the measurement process impacts our theoretical ideas.
For example, why does the brain have so many topographic maps? Two possible explanations emerge. First, maps may serve as an organizational principle, minimizing neural wiring for efficient signal transmission. Alternatively, we may find maps simply because we know how to look for them. In other words, the use of maps as an organizing principle and the bias in our measurement techniques could both play a role.
The Drunkard’s Search is a metaphor for irrational and biased behavior in problem-solving. The term originates from the tale of a drunk man searching for his keys under a streetlight, even though he lost them in a dark area. This story illustrates how people often prefer easy, accessible methods over more difficult but important ones, a tendency known as availability bias. This concept is relevant in scientific research when we risk missing crucial information by relying on easily accessible data or familiar methods.
5. Don’t Try to Be Cool
Everyone wants to work on “cool” topics with “cool” methods, but this often leads to a crowded field. Competition can make people less generous, and you may worry about being scooped. Finding problems that people care about but aren’t yet working on can be challenging. One approach is to look for areas where theoretical ideas are underdeveloped, making strong inference difficult to apply. A well-formulated theory can be worth a million experiments. Avoiding the temptation to be cool requires courage and creativity. Read outside your specialty—explore poetry, novels, philosophy, history. Take long walks and talk to people with unique perspectives.
6. Pursue Interesting but Wrong Theories
Theories are often criticized for being wrong, but being correct is not the sole purpose of theorizing. Science is an epistemic practice, not a fixed body of knowledge. The role of theorizing is to formalize perspectives that add clarity to complex problems. Even incorrect theories can help by “carving nature at its joints,” defining the contours of a puzzle. When first presenting a theory, aim for simplicity and clarity—even if it’s wrong. The goal is not to provide the right answer but to give your audience a unique way of looking at a phenomenon. Theories are tools for thinking.
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