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Let me start somewhere most people never go. Below the waterline of a warship, in the engine room, where I spent a good part of my twenties. I was a marine engineer in the navy: fast attack craft, corvettes, submarines, the machine side. Diesel engines, gas turbines, electric propulsion, battery banks.

The thing about a gas turbine is that it is not an abstraction. It has sound, heat, vibration, fuel, routines, and consequences. You are responsible for the whole system, not one component. Four-hour sleep shifts, weeks away at sea, conditions that do not negotiate with you. And if something fails out there, you cannot call support. You cannot google it. You fix it, or you have a very serious problem.

I think about that environment a lot, because of one feature it has that almost nothing else in modern life has. Out there, being wrong is fast. It is physical. There is no dashboard sitting between you and the consequence, softening it, delaying it. If your understanding of the system is wrong, the system tells you, in seconds, in heat and noise and the wrong number on a gauge. The sea does not care how confident you were.

Years later I left the sea and did something that felt completely different. I spent five years on a PhD. And the single most valuable thing I got from those five years was not the title, and it was not the result. It was discovering that the central promise of my own thesis was wrong.

I read an essay this week, by a researcher who writes as Vivek, called how to be good at research. It put words to something I had felt for a long time without saying it cleanly. There is a gap between looking like a researcher and being one, and most people, without meaning to, train the first thing. The real skill is a stack of smaller habits, almost every one of which can be deliberately trained. And when I went through them, one by one, I noticed they all bottom out in the same place: how fast you can find out you are wrong.

I did not learn that from the essay. I learned it on a ship, and then I printed it. At the top of the methods chapter of my thesis, I put a borrowed line. You should take the approach that you are wrong. Your goal is to be less wrong.

Pick your own problems

The essay opens with a habit that made the mathematician Richard Hamming unpopular at lunch. At Bell Labs he would sit with the chemists or the physicists, and after a while he would ask them what the important problems in their field were. And then, once they answered, the question that emptied the table: then why aren’t you working on them? He tells it himself, with comic timing: “I wasn’t welcomed after that. I had to find somebody else to eat with.” One chemist later admitted the question had gotten under his skin and stuck with him all summer, and went on to do important work. Hamming’s quiet, devastating coda is that he never heard the names of any of the other men at that table mentioned in science again.

The sting is that most of us have no good answer. We don’t choose our problems; we absorb them, from an advisor, from whatever a big lab announced last quarter, from the paper everyone is quote-tweeting this week. And the trouble with an absorbed problem is that you hold the conclusion without the reasoning. When the famous lab pivots, you find out a year too late, racing a thousand people who started earlier and have more compute than you.

I started my PhD with an absorbed problem. The shipping industry hands you one the moment you walk in: burn less fuel. So I spent my first years deep in thermodynamics, waste-heat recovery, exergy analysis, squeezing a few percent out of an engine that throws most of its energy away as heat. I genuinely loved the thermodynamics, the calculating on a real process and watching the energy balance out. But the problem was not mine. It was the industry’s. And it nearly made me quit.

What kept me in was a person, not a result. A mentor of mine, Magnus Genrup, talked me into staying at the exact moment I was wrong about quitting. And in that second phase I found my own problem. It started small, almost annoying: a ship is covered in sensors, producing an enormous amount of data every minute, so why do we still not know how much fuel each part of it is burning? Could the ship just tell you, from the data it already produces, without bolting a fuel meter onto every engine? A virtual fuel meter.

That question was mine. The researcher John Schulman 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. The second mode manufactures originality almost as a side effect, because a goal you actually care about drags you into territory no survey paper covers. The fuel question dragged me out of marine engineering and into machine learning, and I never really came back. I did not switch fields. The problem moved, and I followed it.

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, you’ll reliably reach the same conclusions as everyone else, at the same time, which makes those conclusions worth approximately nothing.

So where is the edge? One place is almost embarrassingly underpriced: old material. This field reruns its own past on a delay. There’s a thousand-word essay by Rich Sutton from 2019, the bitter lesson, that predicts the shape of the whole field better than surveys ten times its length. It’s called bitter because it’s so uncomfortable: looking back at seventy years of AI, the same pattern repeats. Researchers lovingly build their human knowledge into a system by hand; it helps for a while; and then it’s beaten, decisively, by a simpler method that just throws computation at search and learning. When Deep Blue beat Kasparov in 1997, it didn’t understand chess like a grandmaster; it searched staggeringly fast. Sutton notes, with an edge, that the chess researchers who’d encoded human knowledge for years were “not good losers.” The same story repeated in Go, in speech, in vision. The bitter part is that a lot of your hard-won specialist cleverness is a dead end, and you only learn it by reading the quiet old essay, not the loud new thread.

Which is the second habit: 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. The interesting part of anyone’s work is almost never the headline. It’s the quiet place where they tell you what they couldn’t make work.

There’s an even older voice in the essay, and it’s the one I’d tattoo on a wall. Claude Shannon, the father of information theory, gave an informal talk to his Bell Labs colleagues in 1952 on how creative people actually crack hard problems. His first and most powerful move was radical simplification: cut it down to size. Strip everything from the problem except the essentials, until it barely resembles what you started with. And then, he says, very often if you can solve that simple problem you can add refinements, one at a time, until you get back to the one you started with. Shrink it, solve the toy, grow the difficulty back. That single trick has carried me through more walls than any productivity advice ever written.

But the place the edge hides that I know in my hands is different. Sometimes upgrading your inputs doesn’t mean finding new data at all. It means reading the data everyone already had and nobody bothered to look at. On the cruise ship I studied, almost a fifth of the electricity on board could have been replaced by heat that was already there, pouring out of the exhaust, doing nothing. In Swedish we have an expression for wasting heat like that: elda för kråkorna, heating the crows. The whole ship was heating the crows, and the signal that proved it had been sitting in the logging system the entire time. Nobody was w…



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