I often get this question, as I’m sure many other researchers do: how do you choose which research problems you want to work on? Bassam Bamieh gave a nice answer to this question on the latest episode of the inControl podcast (which I highly recommend, by the way). He said that there are two common approaches to this: one is to be driven by a specific important problem (often one arising in an application) and keep trying various methods to solve this problem; another is to have a preferred set of tools and keep applying them to various problems (which is like having a hammer and looking for nails).

As I was listening to Bassam’s explanation, I was thinking that I belong to neither of these two camps. It’s actually a bit difficult to explain how I go about selecting research projects, and this is what this post is about. I may be somewhat closer to the second way of thinking, in the sense that I’m more likely to be motivated by a solution method than by a problem itself. But I don’t get very excited about applying the same set of techniques over and over again. When getting started on a new project, it is important for me to see novelty in it. And it’s not just about novelty; it’s also about beauty, or at least elegance. What I really enjoy is seeing a nice solution or approach to a problem, one that I haven’t seen before and that appeals to my mathematical taste.

I want to stress that for me to appreciate a mathematical concept or technique, it doesn’t necessarily need to be tied to an original research contribution that I’m trying to make. A concept or idea may not be new—it doesn’t matter, as long as it’s new to me. I derive a lot of pleasure from learning beautiful mathematical constructions and results when reading papers and books written by other people, and they don’t need to be related to my own research. Even an elegant solution to a high-school-level math problem can leave a lasting impression. (I have two teenage children, so I think about elementary math problems, puzzles, etc. quite regularly.) Occasionally, though, this feeling of excitement and delight appears when I do research, and it is those moments that help me formulate new research problems and directions.

I suppose I should give a few examples to illustrate and better explain this process. When I was starting my postdoc, I learned that switching between stable linear systems may lead to instability, but that this doesn’t happen if the individual matrices defining the switched system commute with each other. This sparked my long-lasting interest in developing stability criteria for switched systems based on commutation relations (as I explain in much more detail in this recent article, which recounts several other similar moments of inspiration). As another example, at the 2003 CDC in Maui I was presenting my work on quantized feedback systems, and after my talk Dragan Nesic came up to me and suggested that my results could be alternatively derived using small-gain theorems. This idea led to a beautiful and completely new (for me) way of analyzing control algorithms that I have been developing and studying for several years prior to that. It also motivated a general approach to stability analysis of hybrid systems based on small-gain theorems (whose development can be traced from our early and quite accessible 2005 CDC paper to a much more comprehensive 2014 TAC paper). As a much more recent example, at the 2018 CDC in Miami Beach I was presenting our work with Xiaobin Gao and Tamer Başar on stability of slowly time-varying and switched systems. At the end of the talk, someone from the audience asked me what happens when fast variation or switching is also present in the system. I hadn’t thought about this issue and wasn’t able to give a coherent answer on the spot. But later Hyungbo Shim, who also attended my talk and heard the question, told me that he had done some work on averaging for systems with slow and fast time variation, which he thought could be combined with our approach to treat systems where both slow and fast switching and time variation are present. Hyungbo and I decided to join efforts and work this out, and we now have several papers published or in preparation on this topic (one of which he presented just last week at the 2024 HSCC).

I think these examples make it clear that I don’t really have a systematic method for finding good research problems; instead, good research problems occasionally find me, usually when I talk to other people or study their work. But the process is not completely random, as I do have certain criteria that help me decide which ideas to pursue and which ones to discard. An interesting additional observation is that many of the interactions and encounters that turn out to be useful are not planned in advance—which is why it’s very important to have in-person meetings. When our conferences went online during Covid, I felt very uninspired and could not imagine that our field would survive in that mode for very long. I’m able to work quite well remotely on an already existing project using Zoom and email, but that initial spark of inspiration tends to come only during face-to-face conversations (and still only very rarely).

Of course, other people have very different approaches to finding good research problems to work on. I hope you find one that works for you and brings you joy.