Although it is impossible to give a definitive set of characteristics, there are some guiding principles about what constitutes a ‘good’ research question. There are three main characteristics –it must be novel, important, and tractable. The best research questions – which often lead to the best publications – fall in the intersection of these three domains.
What are novelty, importance and tractability? ‘Novelty’ essentially relates to the notion that your work must push back the frontier of knowledge. It must create something that is new to the world, not just new to your own country. This is probably much harder to do in some domains than others: for example, older (more mature) areas of inquiry that have been studied intensively by the brightest and best for the last 50 years are likely to pose a much tougher novelty requirement than newer areas of inquiry. There are obvious risk-reward trade-offs embedded in the novelty of your topic: with the potential of higher impact comes the fact that completion rates will fall and completion duration will increase.
‘Importance’ refers to the idea that the answer to your question must be of interest (and relevance) to the profession or for the welfare of society. For the most part, economics is not an abstract, esoteric social science; it is practical and relevant. So, you need to be able to articulate the relevance of your work. Although this point about ‘importance’ is seemingly obvious, it turns out to be much harder than expected to articulate why something is important. In fact, it is something that you are likely to have to continually work at over your career. So, don’t be fooled by the apparent simplicity of this idea: it is really tough to answer the question “why should anyone care about the answer to this question?”
Finally, ‘tractability’ refers to the ability to answer the question posed. There is no point asking a profound question if it can’t be answered using available techniques or data (of course, you could create the new technique and/or data to answer the profound question, but it is probably too much to do both in one PhD thesis). All too often, PhD students fall into the trap of asking questions that just cannot be answered: it is much better to ask a small, focused question and to answer this comprehensively. The inherent conflict between novelty and tractability will need to be handled carefully. Remember that the PhD is actually just a license to do future research: it’s the ticket required to demonstrate that you are a bona fide member of the academy.
One of the most important lessons for an academic to learn is how to separate a ‘good’ research question from one that is ‘not quite as good’. If you are going to be successful, you need to be able to rank-order your ideas so that you allocate your scarce time efficiently. You must apply basic economic principles to your own research endeavours! This means that you need to learn not to over-invest in weak ideas. The question is: how do you know when to let a paper go? Unfortunately, this is hard, especially when you are just starting out: but over time, you get better at knowing when to persist with a paper (even when it has been rejected several times) and when to let a paper go.
Once you have picked your research topic (and done the research), the next big challenge is to write the paper. Suffice to say that a good research question is a necessary but not sufficient condition for a good research article. Papers typically require several re-writes before I feel confident in the logic, content and flow of the piece. Given that this can take a week (sometimes much more), it can create some anxious moments when you have to leave the desk (to eat, sleep, exercise, socialise) knowing that your paper is still in bits and pieces on the shopfloor. Without a manual to help you re-build the paper (unlike a mechanic), you have to have confidence in your ability to tackle whatever problems reveal themselves. Learning to accept that this ‘dismantling’ is part of the process of re-writing papers is an important breakthrough.
Hopefully, this overview will be enlightening for PhD students (and young researchers) embarking on a research career path. It is certainly not an easy path to choose, but it can be extremely rewarding. The key message to take home is that choosing your PhD topic carefully is important for short-term reasons, but also for long-term reasons because it will shape so much of your future.
NOTE: this is an abridged version of a paper forthcoming in the December 2013 issue of the Australian Economic Review. See here for the complete version (paywalled).