How to Choose a Research Topic

I have now provided a lot of advice to research students: how to start, how to finish, how to survive a viva, how to get a job, and so on. In all of these I have sort of skirted round the big issue: how to find a research topic. I can avoid it no longer, and in any event, it seems like the right time, the start of the academic year, to tackle it.

First, and most important is 'authenticity'. I am not sure this is the best word but I cannot think of a better for the moment. The topic must reflect what you care about, what really matters to you. It is not enough simply to be interested. The topic must engage you, directly, personally and, yes, emotionally. If it does none of these things you will be unable to 'own' the topic or to engage the best of your creativity. All the practicalities have necessarily to take a second place to this.

You should focus on a problem. Seems obvious, yes.  A real problem, one that needs to be addressed. You should avoid confusing 'tools' or 'methods' with problems. It is too easy to be sidetracked by the ways in which a problem might be tackled rather than focussing on the problem itself. There is no such thing as a 'methodological thesis', or rather there is no such thing as a good 'methodological thesis'. Effective methods are only derived in the context of meaningful problems. Besides, as I have argued before, in engineering at least, problems tend to persist, while methods are more ephemeral.

I enjoy reading scientific biographies and, though scientific 'heroes' do not always make for the best models, they display a fairly consistent pattern. Early in their career the best scientists and engineers turn their attention to a big problem. A large question at the very centre of their disciplines. Often a question that others have shied away from, or answered in a partial or inadequate manner. They have tackled this problem and, mostly, success has not come immediately. They have made numerous attempts and have persisted in the face of failure. Despite the failures they have not weakened their ambition nor, and this is critical, loosened their focus. There is a lesson here, to think big, to be ambitious, and to maintain that ambition.

You are encouraged to eschew fashions, but you still need a community. Science and engineering are a collective undertaking. It is important that other people care enough to read what you write and criticise it. This is a tricky issue to determine in the early stages of work. You should rely upon colleagues and your supervisor to navigate you here. It will be important to have a sensitive understanding of the 'state-of-the-art' in the broadest sense. Taking into account all I have said earlier it is critical too that your supervisor is committed, really committed, to the topic, you will need that relationship. The research is in some sense a shared undertaking.

It is true that there is not much time and that, no sooner have you started research, the tyranny of deadlines and  the progress hoops that you are required to jump through, will bear down upon you. Despite this you should take the time to think about your research topic and to mull it over rather than leap at the first challenge you are presented with. Think about the intellectual skills you have at your personal disposal and think too about the ways in which you are going to test your ideas, through proof, case study, experiment, observation, and so on. The early stage of research, when you are sill looking for your topic, is precisely the time when you can, and should, challenge received ideas.

You will find a lot of people encouraging you to narrow your sights. Listen to them, they have your best interests at heart and they may have a good understanding of the practicalities. Just because you listen to them however, and absorb the lessons about what they feel can and cannot be done, does not mean you should do what they say. This is research after all. It should not be safe.