Very sound advice from systems biologist Uri Alon:

A common mistake made in choosing problems is taking the first problem that comes to mind. Since a typical project takes years even it if seems doable in months, rapid choice leads to much frustration and bitterness in our profession. It takes time to find a good problem, and every week spent in choosing one can save months or years later on.

In my lab, we have a rule for new students and postdocs: Do not commit to a problem before 3 months have elapsed. In these 3 months the new student or postdoc reads, discusses, and plans. The state of mind is focused on being rather than doing. The temptation to start working arises, but a rule is a rule. After 3 months (or more), a celebration marks the beginning of the research phase—with a well-planned project.

Taking time is not always easy. One must be supported to resist the urge: “Oh, we must produce—let's not waste time, and start working.” I am under no illusion that everyone is free to choose their own problems, or has the time needed for an extended search. Taking time can be especially difficult when funding is insufficient and grant deadlines approach. In such difficult situations, nurturing is not enough, and you need to find support and do all you can to get into a better situation. Even so, for many of us dealing with the difficulties of running a lab, taking time to choose problems can make a huge difference.

Unfortunately this is something I learned late. It didn't help that one of my first advisors in grad school would get upset if I wasn't in the lab constantly (even during my class periods). My subsequent advisors were very supportive, but still, it was hard, in the larger environment, to escape the widely-held feeling that if you weren't doing something at the bench all the time, then you weren't being productive. This can lead to short-term thinking, and projects that don't resonate well with your interests. For a long time my habit was to always do the most immediately obvious experiment the day after I finished the last one, because the most obvious experiment (but not necessarily the best) was something I could set up quickly and thus stay at the lab bench.

Grad students and postdocs can think about this another way: you're not getting paid enough to simply produce a lot of data at the bench. You can sit back and take some time to think - your time belongs to you. Your goal is to be a good scientist, and not, for the time being, to produce a product. (And in fact this outlook is enshrined in tax law: postdocs on a fellowship aren't considered wage-earners. The money is essentially considered by the IRS to be a stipend allowing you to pursue further education and training, and "does not represent compensation or payment for services..." That also means that you lose out on certain tax credits available to wage-earners.)

So take your time to think. This can be hard in some environments, since there are a lot of unimaginative scientists pursuing very mundane research. As Alon noted, they've spent their whole careers pursuing the "easy-but-not-too-interesting variety" of research. They know how to work, and, unlike me I suppose, they don't get bored easily by research that just fills in the details.

How do you pick a good scientific project then? Alon tells us to use "the Pareto front principle of optimization theory." Go read the paper if you want to know what that is. I'm going to skip on to his next piece of good advice: taking the time to listen to "your inner voice."

The inner voice can be strengthened and guided if one is lucky enough to have caring mentors. A scientist often needs a supportive environment to begin to listen to this voice. One way to help listening to the inner voice is to ask: ‘‘If I was the only person on earth, which of these problems would I work on?’’ An honest answer can help minimize compromises.

Another good sign of the inner voice are ideas and questions that come back again and again to your mind for months or years. These are likely to be the basis of good projects, more so than ideas that have occurred to you in recent days. Another good test: When asked to describe our research to an acquaintance, how does it feel to describe each project?

It is remarkable that listening to our own idiosyncratic voice leads to better science. It makes research self-motivated and the routine of research more rewarding. In science, the more you interest yourself, the larger the probability that you will interest your audience.

Physicist John Baez calls this keeping your soul as you go through the process of training and developing an independent career:

The great thing about tenure is that it means your research can be driven by your actual interests instead of the ever-changing winds of fashion. The problem is, by the time many people get tenure, they've become such slaves of fashion that they no longer know what it means to follow their own interests. They've spent the best years of their life trying to keep up with the Joneses instead of developing their own personal style! So, bear in mind that getting tenure is only half the battle: getting tenure while keeping your soul is the really hard part.

You may be reading this, nodding your head, thinking that this all sounds like good but obvious advice. Dont' underestimate how hard it is to follow. The science profession is intensely competitive, and you can be successful in this competition without "keeping your soul" or making your research a means of expressing "your way of perceiving the world" (as Alon suggests). There are decent scientists who work hard, do solid research as scientific craftsmen, but they aren't very ambitious; there are also scientists who are extremely driven, drawn by the challenge of the field, but who would have been equally happy being highly driven corporate lawyers, investment bankers, political operatives, or McKinsey consultants. (Don't read me wrong. I'm not slamming these alternate careers, nor am I putting down people who practice science like this - there are excellent scientists who fit both types. And really, few people can be pigeonholed into just a single type.)

Those who do want to practice science as a way of pursuing an inner voice, who maybe at some point considered (however unrealistically) being writers or musicians, face a challenge trying to navigate this career path while staying satisfied with the choices made. There is strong pressure to compete by doing what everyone else is doing, and the path of least resistance is often to just wait for your advisor to tell you what to do.

You may have been inspired to go into science by the example some great figure like Einstein or Feynman who obviously was doing very original, creative science. It's almost certainly true that you're never going to be the next Einstein, but you can certainly learn to practice science like Einstein. You don't have to be a genius to stake out some room for independence and map out a research plan that fits your interests.

My apologies for the light posting recently - I'm swamped in an effort wrap up a recent project and get the paper out the door.

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