How To Be Einstein Without Being A Genius
    By Michael White | September 25th 2009 11:23 AM | 13 comments | Print | E-mail | Track Comments
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    Welcome to Adaptive Complexity, where I write about genomics, systems biology, evolution, and the connection between science and literature,


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    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.

    Read the feed:


    Andrea Kuszewski
    BRAVO!!!!!!!!!!!! *clapping*

    I, too, would write more, but I am swamped with work, training and writing. GREAT article. I'm re-posting it on my blog. :)
    Great post. This is sound advice for anyone pursuing a career in the sciences. I had to leave a Ph.D. program after 5 years without the degree because I locked myself into the first topic that came my way within the first few months of my arrival as a young, wide-eyed grad student. I tried changing course mid-stream to work on something aligned more with my "soul", but it was too late. Its haunted me ever since.

    Thank you for taking the time to write this post. It makes me feel better about where I am at in the tail end of graduate studies and provides sound advice for mapping out the next phase of life. Grateful I am for the people I work with in CEMI at University of Utah who allow plenty of room for deep breaths enabling students to find and follow his/her inner voice.

    Terrific post Mike. And sound advice for scholars in the humanities too...

    Mike, I agree with Yago. Especially now that the market has created a kind of pseudo-practical hysteria in the humanities about buckling down and preemptively murdering your dreams, it's important to keep the big picture in mind. I wish we could implement a mandatory 3-month waiting period in my graduate program!

    I agree that this is certainly true of many academic fields. Based on my own experience (maybe I was just lucky with my advisors), the problem isn't that grad students and postdocs aren't allowed to take the time to think about a project. It's that the issue is never brought up explicitly. Students tend to not ask for it, because when you start grad school there is this perception that you need to start a project right away. 

    I would bet that, in my field anyway, if students and postdocs specifically asked for time to explore, they would get it in most cases. But most brand new students aren't going to be bold enough to ask - at most other jobs, when you start your first day of work, you do what you're told. Which means that the burden is on the faculty to encourage their students to take the time to explore.

    Mark Changizi
    Mark Changizi likes this. (In Facebook style!)
    Andrea Kuszewski
    ...and don't forget that the students who DO try and follow their passions from the get-go, rather than being an apprentice to whatever research their mentor is doing, are not exactly encouraged down this path. Speaking from personal knowledge about such things, *cough, cough* many professors really don't want their grad students to pursue their own topics of interest until farther down the PhD path, or even to wait until receiving their degree. MANY factors contribute to this counter-intuitive attitude about graduate study, which I will not get into right now.

    However, I do hope that the type of student who makes it clear that they are driven to do original research from the beginning (provided they demonstrate the skill to do so) is somehow valued or at least accepted as a model of a potential grad student.

    I know... I am asking for the world and a bag of chips.
    Finding the right balance between giving a new grad student freedom, and making sure that they have a doable project that falls within the scope of a thesis is really tough. And then add the fact that, in the biomedical sciences anyway, to pay for that grad student the PI usually has an already funded grant, with goals determined by the PI. It's a difficult problem given the way funding currently works.
    I like it too!
    Science advances as much by mistakes as by plans.
    Nice article. Major points I took away:

    1. Take time to choose your research problem.
    2. If I was the only person on earth, which of these problems would I work on?
    3. You don't have to be a genius map out a research plan that fits your interests.

    It's a good plan for being happy with a research career.
    Great post! I have also found some other suggestions on choosing the research topic here, and don't forget to look at the discussion there too, it's pretty interesting on its own right.