A student from China recently asked me about how I got interested in relay selection and started obtaining (publishable) results. Since I have some free time on my hands now, I figured I’d share some thoughts on this topic.

I actually don’t think that the way I got interested in relay selection was the ideal strategy in terms of “finding a good research topic.” Instead, I’ll discuss what I think is a better way of “finding a good research topic.” Note that the following is especially relevant for graduate students researching wireless communications (for the obvious reasons).

It’s fairly common for a new graduate student to be overwhelmed by the plethora of potential research topics. When I was starting work on my masters degree, I wanted to do research involving some aspect of wireless networks, since I felt (wrongly, as it turned out) that all of the good point-to-point problems had already been solved. During the summer of 2004, I worked on beamforming for MIMO ad hoc networks, but that ended up being a major dead end. On a related note, I recently perused my research notebook and found that during January 2006, I was interested in cooperative diversity for OFDM networks (my, how things have changed).

This brings up the key question: how should a new graduate student sort through the morass of potential research topics and come up with a good one? I’ll discuss two potential answers.

One approach is to have your advisor answer this question for you, assuming that you have an advisor. In general, you can assume that your advisor has a strong grasp of the current state of research in wireless communications. This knowledge can help him/her determine a topic for you that is 1) interesting, so you won’t be bored stiff for approximately 5 years and 2) worthy of a Ph.D. dissertation, so you will have made a fundamental contribution of some sort by the time you graduate.

The second approach, which I highly recommend, is to take the initiative. To start off, you should do a significant amount of reading. Survey articles in journals such as the IEEE Communications Magazine and the IEEE Signal Processing Magazine can be valuable starting points for the interested yet relatively inexperienced grad student.

A particularly well-written survey article can provide the reader with a good grasp of “what’s been done” on a topic such as “OFDMA power allocation for relay-based networks” and suggest various open problems that are both interesting and important. When reading through these survey articles, one should also scan the list of references to learn about the key papers (and researchers, so you can bookmark their home pages) in a particular area.

It’s then important to read through these key papers to grasp the nuances of the topic that you’re learning about and ask yourself tough questions along the way. For example, do you understand the (technical) paper that you’re reading? Can you justify all of the authors’ assumptions? Can you re-derive every expression (especially the proofs of key theorems) in the paper? I should note that sometimes papers contain typos/gross errors, so you shouldn’t automatically trust everything you read.

If you want to answer these questions in the affirmative, this is a great opportunity for building your technical background. For example, let’s say that the authors are studying a MIMO wireless system and assume that a two-ring scattering model is being employed. If you don’t know what a two-ring scattering model is, you should obtain a copy of a MIMO textbook such as this one by Paulraj et al. and learn more about channel modeling.

Also, let’s say that you’re reading through this famous paper by Gupta and Kumar, and you’re having trouble deriving some (or all, as this paper is actually quite tricky to understand) of the key results. In this case, you might want to strengthen your graph theory background by taking an appropriate class, such as this one at UT-Austin. You might also want to improve your knowledge of random geometry, and you can check your university library for a helpful book such as this one by Bollobas for more coverage of this advanced topic.

As you read through the key technical papers in the area that you’re learning about, you should think of additional open problems and ask yourself more tough questions. For example, you can ponder something like, “the authors’ assumption of a zero-error feedback channel seems a bit restrictive. From my other reading it’s clear that introducing a channel estimation error at the transmitter would better model a practical system. Maybe I can’t obtain an exact expression for the sum capacity given channel estimation errors, since that seems quite complicated, but can I obtain relatively tight bounds?”

Regardless of the approach that you take in terms of finding a good research topic, it’s crucial that you interact with your advisor during this process. Your advisor, who has worked in either the general area that you’re considering or a related area, can help you determine if the open problem you’re considering is either trivial, worthy of multiple dissertations, or actually reasonable for a dissertation. Note that by adopting the second approach I discussed above, your ability to have meaningful dialogue with your advisor during this process is enhanced. In particular, you can evaluate your advisor’s suggestions and converge on a reasonable topic more quickly; this is especially important if your advisor has not worked in the general area that you’re considering.

That’s all I had to say on this subject, at least for now. I welcome comments, especially from my group-mates on this issue of “finding a good research topic.”