From browsing my publications, you might notice that my research area changed after my PhD. My thesis was on orbital integrals (Langlands-related), but now I'm working on more classical topics in associative ring theory like separable algebras and Grothendieck groups. In this short article I will explain why I switched areas, in the hope that it will help other young researchers make good decisions.

Let's go way back to my PhD, in which I solved a problem in the Langlands program. For readers that may not know about Langlands, let's just vaguely say that it studies generalisations of modular forms through representations of matrix groups and it is motivated by number theory and reciprocity laws. As a graduate student this sounded great because I like number theory and algebra. Writing a thesis was not overly difficult either and I think I did a good job with it.

So, I was excited to get a postdoc in Australia. Besides Australia being an awesome country with cool parrots, it would be a great place to further my research. I even came up with new problems connected to my thesis on which to work. But despite being well set up, I didn't make much progress. Although I had one paper from my thesis published, when I tried to publish the second part of my thesis, it was rejected multiple times on the grounds that it was not significant enough. From a career perspective, I wasn't worried because I already had a few other papers (in different areas) either sent out or in progress. But as a young researcher trying to interact with a forbiddingly technical area, it was undeniably discouraging.

Nevertheless, I continued working on more problems in Langlands. In the end however, my interest in the subject began to wane quickly. It mostly wasn't because of the paper rejection; I've actually had one other paper rejected in associative rings and I still happily work on associative rings. It was the fact that although Langlands field is rooted in number theory going back to Gauss, to me it felt completely disconnected from its origins when I was actually 'doing' the math. It probably also didn't help that tremendous amounts of 'advanced' algebraic geometry would be necessary for some of the problems I was thinking about, and after giving it a good try, perverse sheaves, stacks, ind-schemes and gerbes were really not to my liking. Hey, I'm happy that some people can enjoy it for what it is, but it turns out it's not my style.

So I moved onto something else. Actually, one of my many current projects *is* dimly related to my thesis, but it is far more computational (in fact, it involves writing an actual algorithm in Python) and it is not at all in the style of the traditional Langlands literature. After this project is done however, I don't plan on continuing in this field. With my new research areas, I am much more satisfied with my work. The only downside is that I now have to find a new community and in particular, new people who are willing to write me letters of recommendation, which has turned out to be much harder than I thought. Still, the switch was absolutely worth it, just because I believe in the math I do again.

There is a lesson in this story, and that is as a young researcher, you should not use a few chosen problems as representative of the general flavour of a research area. Such problems may be interesting on their own, but they are inevitably woven into a highly specialised research microcosm. And the whole research microcosm is something you should consider as well, which includes the general direction of the field and the community and attitude surrounding it. This applies especially to the highly abstract fields that seem to be in vogue these days such as geometric representation theory, Langlands, and higher category theory. In these fields, while a senior researcher can select and distill certain easier problems that would be suitable for many students, only a small fraction of those students will actually have the interest and personality to be successful in progressing to the serious problems of that field on their own. In this regard I'd like to emphasise that it absolutely does take more than just pure brains to succeed. Personality and style is at least as important, and these are things that you may not be fully aware of as a grad student.

So my advice to the young researcher is: know the field you are getting into. Look at some papers in the field and ask yourself if you want to write similar ones. Don't just be captivated by the ultimate, overarching motivation and instead look at the actual nitty-gritty details of the math and culture. *For it is the details you will be spending time with, not the motivation.*