In part three of what has become my mini series of muses about the “Art in Science” I wanted to get back to the more general question I mentioned in Part I: “What problem should I choose to work on?”.
First, a humble disclaimer is in order given my junior position. Take everything below with a grain of salt. Obviously YMMV and my perspective if that of a computational biologist growing up in a computer science/machine learning environment. With that said, here are a few observations I made during my years in and outside Academia:
- The answer to the question really depends on the stage of your career: If you are a PhD student then you are very much in a *training* phase. Thus, I find the exact topic you work on during your PhD is less crucial. More important is getting a good base in terms of computational know-how and research approach. You want to get good papers that showcase your capabilities and you want your advisor to be respected and connected to help you with your next step, whether that’s in Academia or Industry.
- When you are a postdoc good capabilities are just not enough. As many have noted in today’s environment you simply can not get passed the initial screening of recruiting committees without that high impact paper(s). So how do you do that? Tuuli Lappalainen recently wrote a nice commentary about transitioning to tenure-track positions . Her advice is to “Try to figure out what is the next big thing within your broader field, and get into a pioneering lab that is doing it right now”. Indeed, that approach can help you get that high impact paper but moreover it can help position you as an attractive faculty candidate, an expert in a hot new field. After all, science is driven by people and hence bound to have its fashions as well. In Tuuli’s experience, the high impact field was functional population genomics. My experience involved computational modeling of RNA processing but I admit I did not think in terms of optimizing for the next big thing. There are several things I would note about this: First, to figure out what is the next best thing you should shop around, ask people whose advice you value, and keep an open mind in the process. Second, the above statement can be erroneously interpreted as finding “an” area. My experience has been that, especially as a computationally skilled person, there are actually many interesting things you can work on. Thus, finding an environment that will make you flourish is just as important if not more. In fact, if you join such an environment there are much higher chances that you will land that major paper or develop a completely new area (and “own” it) even if it’s not exactly what you originally set out to do. Science in that sense is not unlike startups. NYT reporter Randall Stross, who studied the famous startup accelerator Y Combinator (think Dropbox, Airbnb), claims that one of its distinct characteristics is its focus on people, letting them explore as in (yes..) grad school, instead of closely watching/telling them what to do. Randall claims in Y Combinator the initial ideas are considered less crucial as the original idea is frequently abandoned. Instead, it’s the people that matter and the iterative process of evaluating and refining their ideas. Getting back to scientific research – What environment would make you flourish naturally depends on your character and interest, but at least keep this in mind instead of simply focusing on finding “a” topic. Finally, there is a point to be made about serendipity, scientific curiosity, and basic research. Who could have anticipated how we would get CRISPR technology and its effect on current research? For science to progress we need to hedge our bets. If we all focus on “the next big thing” we are more likely to actually miss it. Besides, many people may actually not respond well to working on a hot topic with intense competition. Thus the optimal setting is left for each individual to figure out for themselves.
- As a young PI figuring out what you want to work on is just as important if not more. So is that nurturing environment. This is especially true in the area of computational biology which tends to be highly collaborative – tackling a cool topic/question can be so much harder without good people to work with. As a young PI, you are also likely to get into the related problem “What problem I should NOT work on?” – this happens when you have too many ideas and too many suggestions for collaborations. Even if they are all great you still have limited resources – funds, time, energy, computing power, people. So you need to prioritize and learn to say no (how to say no is probably another form of art…). Think of it as rounds in your magazine. You only have a few, so think carefully what you aim for and make those bullets count.
In summary, the above points can be seen as general guidelines but to us scientists they offer no exact, deterministic, formula that we can apply to solve the problem. That’s why choosing what work to on can be seen as part of the “Art in Science”. When transitioning to tenure track, Tuuli writes that success is “a mixture of hard work, support, luck, strategy, persistence, talent and personality.” I liked her list. Indeed, anyone who successfully deals with “What to work on?” should be humble enough to admit that there is an element of luck involved. But you do not control luck so focus instead on what you do control. I really like Pasteur’s assertion: “Luck favors the prepared mind.” And Richard Hamming (I highly recommend reading ) added: “The particular thing you do is luck, but that you do something is not. The prepared mind sooner or later finds something important and does it”. Now, all we have to do is simply implement this… 😉
 From trainee to tenure-track: ten tips, Lappalainen Tuuli, Genome Biology 2015
 You and Your Research, Richard W. Hamming, Transcription of the Bell Communications Research Colloquium Seminar, 1986