Why I Didn’t Do Research In Your Area

[Note: This is a followup to my post last week about lessons I’ve learned in graduate school. The format is inspired by Tim Challies.]


Your field of research definitely sounds interesting. I really enjoyed taking that class, listening to that seminar talk, or reading a few of your most recent papers. I actually understood most of what you were talking about! Some of the techniques are quite clever, and you and your collaborators all seem really friendly.

You’re probably wondering why I didn’t end up joining you there. And you’re right to wonder — it would have been nice to collaborate with you, and I haven’t exactly found something else revolutionary to study instead. Well, it’s mostly because…

…you offered some motivation for working in this area, but then didn’t revisit it after showing me your results. It felt like you were using practical applications as a prop to check off a box, not as a real problem that needed to be solved. Where was that urgency to get back to the motivating example? Was your technique actually useful there, or were there further complications? Without that followup, it’s almost as if…

…you didn’t offer any practical applications at all. “It’s an art,” you said, quietly eliding the fact that only a handful of people will ever read many of your papers. That seemed an awfully wasteful route to take for me, given the very real problems we face today. Besides, the things you and others had managed to prove in this area didn’t seem like they had any relationship to anything remotely realistic. Maybe it’s because…

…you seem to be studying problems you could answer, not problems that accurately modeled any aspect of reality. It’s like the classic joke of the drunk looking for his keys under the streetlight, not because he dropped them there, but because that’s the only part of the street he could see. Your field seems to get palpably excited about getting ultra-precise answers to totally irrelevant questions. You use words that make it sound like you’re studying something actually useful, but the technical definition you get is completely unrelated. Meanwhile…

…your fundamental problem seems basically impossible to solve. Any good research field needs both problems and the potential for solutions, and yours is decidedly missing the latter. Every paper seems to come up with a new idea for a way to tackle this fundamental problem, but no one is anywhere close to solving it in the level of generality we’d all want. Or maybe, to the opposite extreme…

…it sounded like you wanted to reinvent the wheel. While you were talking, I was able to find multiple Wikipedia articles addressing the problem you hoped to solve, and they even pointed to several existing solutions. By comparison, it sounded like you wanted to start over from scratch, and you didn’t even seem to be aware of this previous work. In fact…

…it seemed like all the big questions in the area were already answered. Most of the papers we heard about in that class were older than me, and the newer papers we read for our class projects seemed to just clean up some of the edge cases and side problems from previously-established work. And when I asked you…

…you actively discouraged me from joining the field. Actually, thanks, that was really helpful advice. I’d gotten the sense from one of my classes that this field was super useful and could end up making entire industries more efficient, and while I’m disappointed to hear that it’s just a curiosity that no one actually cares about, I’d rather know than now than to find out after working a year or two in this area.

Please don’t take any of this personally. I’m glad I got to learn about your field! At the very least, I had fun and some of the ideas might help me in whatever I do end up doing some day. And don’t worry; I’m not objecting to you continuing to do research in your area, as long as you still find it worthwhile. I just can’t get myself excited to work in an area without more than a glimmer of hope that I’ll be able to make a contribution that helps someone other than a fellow researcher down the road. I guess you could say I’m just not optimistic enough to make it in your field.

2 responses to “Why I Didn’t Do Research In Your Area

  1. Pingback: Stop Ignoring Impact Multipliers | The Christian Rationalist

  2. Pingback: Misconceptions of Math Grad School | The Christian Rationalist

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