120. Take Heart, If You Proved A Known Result

(Epistemic status: Morally correct, in the mathematician's sense, and the sort of thing that any good doctoral advisor will tell you.)

I still remember the day I proved that successive squares of integers differ by successive odd numbers. I was maybe 6 or 7, and had noticed what looked like a strange coincidence while playing around with numbers, like I often did at the time when bored during recess. I hadn't had any training in how to prove something cleanly, so it took a lot of poking and prodding and a geometric argument based on L-shaped figures that you probably already know. But it was real, and it was mine, and so it was especially crushing when I brought it to Mr. AB (after Mrs. SB, my actual teacher, sent me to him, and to the middle schoolers' room) only to be congratulated on having proven a millennia-old result, all on my own. He must have been impressed at the time, because that was the start of my being allowed to go to the middle schooler's room to look at math books and take reading assessments whenever I liked, and also getting tracked into gifted programs, but at the time, I was crushed. I got about halfway through proving something about the difference of two successive cubes before giving up and moving on after a week or so.

I still have the paper I wrote on; it lives in a little ring-bound notebook I got when I was 10 from Mrs. LP, my math teacher at the time. I wrote down all sorts of other rediscoveries in it over the course of the 2000s: I thought up tetration and pentation and so on, and came up with an absolutely awful notation for it. I drew compass-and-straightedge constructions in it, and figured out how to draw a hexagon and how to use them to do basic arithmetic. I wrote down times tables for bases up to 20, found patterns in the ending digits under repeated squaring, and (in hindsight) got most of the way to reinventing finite group theory. I don't think I've talked about that little notebook at all in the past 20 years, between no one around me caring much towards the start and having realized that I'd long since far surpassed it by the end. 

It was bad enough to go through when I was that young, but it just kept happening all through high school and college: excited and then deflated by rediscoveries - or more often, embarassed admissions that the version we'd been taught was a deliberate oversimplification - in biology, chemistry, physics, and even linguistics and computer science, between clever sorting and searching algorithms for the latter and poking and prodding at shared-looking morphemes and comparisons between cognates for the former. At some point, I finally began to see a pattern, both in how academic subjects got taught and in the progression of those would-be research results: they were steadily advancing in chronological order, albeit obviously much faster than real time. Ancient subtopics before more recent ones, with younger fields like biology having less to get through than older ones like mathematics; the rediscoveries kept pace, too.

Fine, enough hagiography of my misspent youth. What does this have to do with you, if you're a working researcher, or training to become one? Consider that the very worst sort of day in mathematics is the realization that you got scooped by someone who died a decade before you were born. It's not the false proof: there, you can trace the error, find the gap, close it or prove you can't, and move on, a little wiser about where and how your intuition can fail you. It's not the accidental triviality, either, which shows you a short circuit you might make something of, nor time spent neck-deep in old papers hunting for obscure but relevant results. No, it's when you pose yourself what seems like an open problem, dig into it, find it startlingly tractable, pull book after book off the shelf, and in a frenzy, get the thing written up, checked twice, TeXed up, and sent off to your advisor brimming with hope, only for them to, during your weekly research meeting, hit you with a "not bad", name three researchers (only one you've heard of), and spend 30 seconds pulling up a paper from the 1980s that's evidently a classic of your subfield. It's a strange but precise feeling: a little like embarassment or humiliation; a little like deflated pride or curdled hope; a little like not being sure why you believed in yourself; maybe a dash of trauma.

I'm here to tell you: take heart, if you proved a known result. The news is far better than you fear. Sure, the result you just got may have been proven half a century ago, but it's still you who proved it, and especially in research mathematics, the late 20th century is practically recent developments. The burning you feel is a miscalibration, one borne of the math world's justified obsession with priority: when you need no physical setup for your results and all your research results are all but self-verifying, all that remains is who found the right answer first. Other people who became giants in their time found the answer first; then, an eyeblink later in historical time, so did you, assuming that you didn't forget you looked up the answer first.

And even having hit on the answer late still says something flattering about your research skills and taste. Consider how stupidly, unbelievably vast the space of all remotely interesting mathematical statements is. Even after we've pruned away everything not well-formed, everything false, everything banal or meaningless, and everything trivial, the remainder still stretches on far out of sight. But you, in your meandering and independent search, hit on a gem of a result; in fact, by construction, two independent searches through that sprawling and densely-thicketed expanse converged on it independently. An unguided random walk through the space of all true mathematical statements will basically never hit a result worth sharing, let alone anything really good; even a guided search will stumble on those same treasures only to the extent that the guide is a good one. Suppose you were barely worth your starvation-level graduate stipend, and that your sense of the value of a result weren't that good - then what's happened to you is the kind of luck that recommends playing the lottery. No, far more plausibly, your inuition led you - unassisted - to a place that the field had already marked as important, and that is not a sign that you're derivative, but rather strong evidence that you've got a good nose for mathematical quality. Can you really blame yourself for missing out on priority for a result that was celebrated when your parents were undergrads?

Here's another related take: half this blog's epistemology runs on confidence from convergence and consilience. When multiple reasonable lines of reasoning of varying strengths and rigor all converge on the same answer, that's an excellent sign that you should accept the conclusion, and furthermore should believe in the value and validity of those same lines of reasoning. Rejoice: in your rediscovery, you are one such independent line. The known result and the work that got there before you wrote your first proof cannot be seen as your competitor, but rather the corroboration that you're pulled in the right directions. Through no fault of your own, you've missed out on being first to the prize, but you've won better calibration, and should grant yourself the confidence that were you around at the time, you might well have been the fourth author on that paper.

Farkas Bolyai once wrote to his son János, who famously had just rediscovered non-Euclidean geometry in the very same decade that Lobachevsky did. He put it better than I can, and did so well enough and long enough ago that I'll borrow his image outright: there are ideas whose time has come, and so many such things have an epoch in which they are discovered independently in several places at once, just as violets appear suddenly on all sides out of nowhere at the start of springtime. I'll inflect it a little, though; violets have been known to bloom off-schedule, too; shoots carried by runner vines and seeds carried by ants, springing up whenever the weather suits them in odd corners and new lawns and unfamiliar gardens; a small second bloom scattered throughout cool autumn weather. Congrats, little autumn violet: the spring may have been and gone, and left your search and finding a bittersweet anomaly, but you have bloomed all the same where and when you could and are no less fragrant for it.

And just as the killing frost gives way to a new spring, so too is your lot: after you've taken a moment to recover, go back and read that paper your advisor ruefully handed you. There's a pretty good chance that its authors, groping in the dark, actually proved a bit less than you did, or proved it very differently, or proved it using a notation so unwieldy that no one's used it since. If you've got a really good advisor, it's entirely possible that they set you up for this on purpose, and now your work can truly begin; they've walked you through a literature review in the only way that gets you to fall in love with a research direction, got you to approach the thing from a novel direction, and now you're ready to follow an overlooked trailhead off into the wilderness. It's not every day nor every year that someone thinks to follow this particular trail, even if it's one people have seen before; you carry more or even just different tools with you than the others who've tried and failed to walk this particular trail. And who could possibly know where this trail will lead? The wilds of mathematics have a way of meandering and sprawling and branching and coming out in totally different subfields.

These days, it's not even clear for how much longer there will be meaningful mathematical progress by individual people, working late in chalk and graphite and arXiv preprints, and so there may someday soon come a final frost. But for now, for you, the ground is thawing, spring is coming, and an embarassment of appealingly juicy theorems await you. So take heart, little violet, and prepare to bloom.

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