Let’s face it. While what’s his name’s honeymoon was 10 days in Seychelles, ours seems to go on for a lot, lot longer. In slow motion though. When you take up a new job, in an academic environment at least, you are your own boss and you have a lifetime ahead to explore whatever you wish. Resources, funds, colleagues, space, technologies: They are all there for your asking, pretty much, and for ever. Who could ask for anything more? Well, maybe I exaggerate. The going can be tough, it is tough, but the point I am trying to make is that all to often, we seem to spend our discussions on how to get the very important but mundane done and neglect the very important but sublime. Finding a place to work, finding space, money, students are all relatively easy compared to the very difficult task of deciding what to work on and actually working on it. How do you choose what to work on? Before I answer, here are two classes of people who should stop reading this. If you know what you want to work on and are passionate about it, move on. You don’t need this. If you don’t particularly care what you work on and see your academic life as a steady 9AM-6PM job, you don’t need this. This blog is for the worry-ridden like me who agonize about whether what they do has some relevance to anything at all and could they do their science wiser or better.

Here, then, is unsolicited advice to young scientists. All those who are alive are young, by my definition, and I include myself as one who may want to listen to my advice on how to choose a scientific problem. So, maybe I should call this advice to live scientists.

First, think. As opposed to drift. Most of us drift. Accidents of choice build on other accidents of narrower choices shape our lives. On the scientific front, you studied physics or chemistry because of the stunning teacher you had at high school and before you knew it, this approach to decision making took you along a route that narrowed your choices, and you find yourself a crystallographer studying phospo-proteins. Damn that teacher! You could have been a scuba diver studying cardiac arrest in Manta rays in the Andamans, were it not for her. But, let’s step back a little. Once done with high school we constantly see forks: Science versus humanities, if science then what, and so on. While we drift into a direction, we rarely recognize that we can swim back or drill through to do what we really consider important. Its going to be work, not drifting, but that’s the definition of not-drifting. So, if after thinking hard, you think that Manta ray cardiac arrest is made for you, whose’s to stop you but yourself?

Second, when in a hole, stop digging. Having drifted into a scientific question, usually by accident of our postdoctoral venue, we drift into choosing the scientific directions of a lifetime. This, in itself may not be wrong. Our doctoral or postdoctoral lives can be full of buzz, addressing challenging and deep questions. To want to continue on something that you were closely a part of and something important is natural, even sensible and changing course for no other reason that discarding a trajectory may be silly. And, many important projects are those of a lifetime. However, if you are not careful, what was once a cutting-edge question can become archaic very fast. Indeed, many life science departments the world-over, no less in India, are live fossil records of the history of biology. A faculty member who has been around for 40 years can often be seen working on a 40 year problem. Again, no harm getting better and better at doing less and less, as long as what you are getting better at interests a couple of people other than just you. If we are to inspire our students to excel, rather than just train them to sequence a few genomes or examine the anatomy of the fly’s brain, we are doing more than ourselves damage by a ​‘stuck in a time-warp’ attitude to our science. Many of us do see this growing pit early in our career: Starting off with vigour, continuing our post-doctoral work, we find success in about five years. At this stage, many of us get trapped into chasing the derivative. We find we are good at publishing decent papers on our special topic and get better and better at this. We forget our original aim of doing interesting science and gradually transform this ideal into one of publishing ​‘good’ papers in ​‘good’ places. You become known as the guy who has five JBC papers a year. If you are convinced that what you are doing is addressing an important question, stay on, and JBC is not a bad place to be at all, say soml. If not, stop and do something else. Its fine to be a borer, digging deeper and deeper into solving something important. If its not a real problem you are addressing, a borer becomes a bore. Stop digging, get out. Stop!! Stop early! If you didn’t stop early, stop now.

Third, cut the excuses and the whining, get good science done. We often choose an important question or area and address it in a completely useless manner. Cancer, or TB, are important areas deserving study, I am sure. But, I am studying cancer, therefore, I am doing something important is delusional. Choosing an interesting question requires lots of thought, work and action. Yet, we often forget the work and action. A trap we fall into is to take on an important question and address it sub-optimally. For example, understanding the structure and function of an signaling pathway my require biochemistry, cell- biology and genetics. As a biochemist, you may easily fall into the trap of writing 30 papers, all suggestive rather than take an integrative approach to solve a question decisively. Its here we whine the most. Our promotion, our recognition, depends on our papers. I don’t have the resources to do any cell-biology. My students are ghastly. My institute is worse. My director is a jerk. My administration is the pits. Despite all this I have managed to teach my dog to dance and now you want it to dance well? Actually, yes. If we are to do anything other than me-too science, we need to work towards solving problems rather that nibbling at them each with our specialized kinds of teeth. We can do this by becoming complete scientists, or by collaborating, or by choosing an approach is focused but builds on diverse approaches by others. However, hearing as I did the other day that ’ I need to analyze 40 samples for my microarray approach to make sense, I have funds to analyze 4, so I thought I’d still do it as something is better than nothing’ is most depressing. Doing nothing is actually better than depressing halfhearted approaches to important questions.

So, think, stop digging when in a hole, cut the excuses and grasp your question in its entirety. All well, but what is the question that one should home in on? The luxury of support that India now affords, the flexibility to choose whether to work alone or to collaborate to bring in the best in complementarity and the fact that we can choose what we want to study is a fantastic opportunity. As long as we also engage in our work with the best intellects everyday, we are home. This last bit is a challenge working from India, where we are sub-optimal in our institutional size and quality. This is where, each of us needs to be most innovative. As for the questions themselves? They are hiding in the open: whether they are top questions that torment the best anywhere, or top questions that are relevant to our environment, they are self- evident from each of our special perspectives. Look at the top 10 papers in your area published in the last few years. If you are older than 10 years in science, were you an author? If not why not? Its not too late. Dump intellectual lethargy, search the open for what excites you. Then, go for it and get it done. All of us always have 5 – 10 years ahead of us, no matter how young or old we are. Its never too early to do something exciting and never too late.