nobody really teaches you research. you get a desk, a problem someone else picked, and a vague instruction to produce something novel. so most people reverse-engineer the job from what they can see, which is papers, threads, and announcements, and what they end up learning is how to look like a researcher rather than how to be one. the actual skill is a stack of smaller skills, and almost every one of them can be deliberately trained. pick your own problems richard hamming had a habit at bell labs that made him unpopular at lunch. he'd ask whoever sat near him what the important problems in their field were, then ask why they weren't working on them. people changed tables. the question stings because most of us have no good answer. we don't choose problems, we absorb them, from an advisor, from whatever a big lab announced last quarter, from the paper everyone is quote-tweeting this week. the trouble with an absorbed problem is that you hold the conclusion without the reasoning. you know some famous lab cares about a direction, but not why, not what they expect to find, not what would make them drop it. when they pivot, you find out a year later. and on a problem that's already fashionable, you're racing a thousand people who started earlier and have more compute than you. john schulman's guide to ml research splits the work into two modes. in one, you read the literature and hunt for things to improve. in the other, you choose an outcome you genuinely want to exist and reason backwards to the experiments. he argues for the second, and the quiet reason is that it manufactures originality. a goal you actually care about will drag you into territory no survey paper covers. taste, meanwhile, gets discussed like a gift. it behaves more like a muscle. predict the result of every experiment before you run it. cover a paper's results section and guess the numbers from the method alone. mark down which of this month's releases will matter in two years and check your hit rate later. a forecast plus a correction, repeated a few hundred times, is how every good model gets trained, including the one in your head. upgrade your inputs shared reading lists produce shared ideas. if your information diet is the trending page of arxiv plus whatever survives the group chat filter, you will reliably reach the same conclusions as everyone else, at the same time, which makes those conclusions worth approximately nothing. old material is criminally underpriced. this field reruns its own past on a delay: mixture of experts dates to 1991, lstms to 1997, backprop went mainstream in 1986. rich sutton needed about a thousand words in 2019 to write the bitter lesson, and it predicts the shape of the field better than surveys ten times its length. claude shannon gave a talk on creative thinking in 1952 where his opening move was to shrink a problem until it's nearly trivial, crack the small version, then reintroduce the difficulty one piece at a time. that single trick will carry you through more walls than any modern productivity advice. range matters as much as depth. interpretability borrows shamelessly from neuroscience. eval design is mechanism design wearing a lab coat. a working sense of how gpus actually move memory tells you which architecture papers are doomed before the benchmarks do. and honest statistics might be the rarest skill in ml, where a lot of published rigor is vibes with error bars. one more thing. read the paper itself, not the thread summarizing it. the appendix is where the bodies are buried, and the limitations section is usually the most honest paragraph in the document. write everything down paul graham points out that an idea can feel fully formed right up until you try to put it into words. the page finds gaps your head papers over: the assumption you never tested, the step that doesn't actually follow, the two claims that quietly contradict each other. feynman's rule was that the first person you must avoid fooling is yourself, because you're the easiest target. writing is the cheapest defense ever invented. darwin went further and made it procedural. any fact that cut against his theory got written down on the spot, because he'd caught his own memory deleting inconvenient evidence faster than the convenient kind. your memory does the same thing to your failed runs. keep a log: hypothesis, setup, expectation, result, updated belief. rereading last month's entries is humbling in a way no reviewer can match. then put some of it in public. olah and carter's research debt essay makes the case that fields choke on undigested ideas, and that a clear explanation is a genuine contribution rather than a service job. a lot of people working in interpretability today found the field through readable posts, not conference papers. a body of public writing also doubles as the strongest credential you can hold, because it's an unfakeable sample of how you think. tighten the loop the stories about alec radford rarely inv