Handbook for PhD Students
This PhD Handbook serves a dual purpose: it describes the research methodology of our group and gives general advice to students, and it sets out the standards and processes that all students in the group are expected to strive for.
PhD research means finding an important open problem and making significant progress towards solving the problem. Using the right methodology is key in this process, and this is one of the central learning outcomes of your PhD journey.
New students, having read many recent papers with exciting results, will often want to start right away with working on new methods to achieve similarly exciting results. There is typically a strong focus on method design and testing. What is often lost in the process is due consideration for the underlying problem that the method should address. Such work typically ends up with a vaguely defined problem and a method that lacks clear justification; it's not clear why the method is useful and what problem it actually solves. I call this approach "methods-driven tinkering".
In contrast, problem-driven research starts with identifying the actual problem before attempting to find new methods. This involves answers to the following questions:
- Problem: What specific technical problem does your research address?
- Motivation: Why is this problem important? (What can a solution to the problem enable us to do?)
- State of research: Why are current methods unable to solve the problem? (technical limitations, assumptions, etc)
- Contribution: How does your proposed method address the problem?
It is important to put significant thought into these questions, including writing it down formally, as this will frame your search for a method as well as how you evaluate it.
You can further maximise the impact of your work by exploring new problems which are significantly different from prior work. For example, if there is a widely-used but limiting assumption in the literature, your research could be the first to attempt to eliminate or relax this assumption. Exploring new problems can maximise your impact because others may follow your direction, in which case they are likely to cite your work. In contrast, it is relatively less exciting to work on iterative improvements, i.e. "doing more of the same", which may be easily overlooked (or ignored) by others in the field.