On Divergent Thinking and Creativity
There is a certain kind of person history loves to produce—brilliant, slightly unhinged, animated by a goal that posterity would find embarrassing—who ends up mattering enormously anyway. Not despite the embarrassing goal, but in some strange way because of it.
We don’t tend to tell those stories first. The version of scientific progress you get in school is clean: someone has a hypothesis, tests it, confirms it, and the textbook gets a new chapter. The eureka moment arrives on schedule. The genius sees what others couldn’t and walks a straight line toward it.
That version is mostly a lie, but it’s a comforting one, because it implies that breakthroughs come from being right. From having the correct idea at the correct time and doing the correct work to prove it. And some of them do. But the interesting ones—the ones worth actually talking about—tend to come from somewhere else entirely.
We’re talking about the kind of breakthrough that reimagines classical physics because a patent clerk couldn’t stop daydreaming about riding a beam of light. Or the kind that turns the concept of death in a video game into an experience unto itself because a designer decided the punishment loop was more interesting than the reward loop. These aren’t stories about people who saw the destination and walked toward it; these are stories about people who either happened to find their footing halfway through their walk or decided a different walk is what they should have been on in the first place.
And as much as this whole thing was inspired simply from a desire to talk about interesting weirdos, this isn’t just romantic storytelling. Charlie Munger—who spent his career building what he called a “latticework of mental models” borrowed from every discipline he could get his hands on—put it bluntly:
I couldn’t stand reaching for a small idea in my own discipline when there was a big idea right over the fence in somebody else’s discipline.
He built a multi-billion dollar track record on the premise that the best thinking crosses borders.
The academic literature agrees, if less quotably (at least, not as quotably as most of Munger’s sentences). A Harvard study by Karim Lakhani analyzed 166 unsolved R&D problems that major pharma and chemical companies had given up on internally and posted to an open platform where over 12,000 scientists could take a crack at them. The key finding: the further a solver’s own expertise was from the problem’s field, the more likely they were to solve it. Outsiders weren’t just competitive: they were statistically favored. And when researchers looked at long-term citation impact across scientific papers, work that crossed conceptually distant disciplinary boundaries was three times more likely to land in the top 10% of citations— though it took an average of seven years to get there, compared to three for specialized work. The breakthroughs weren’t just different in kind. They were slower to be recognized, which, if you think about it, is exactly what you’d expect from an idea that nobody in the room had the framework to evaluate.
The common thread—across the data and across the historical cases we’re about to walk through—is that these people weren’t operating inside the rules of the field they ended up transforming. They brought a different frame entirely—a mystic’s obsession with divine geometry, a Hollywood actress’s weekend engineering habit, a rhetoric teacher’s unanswerable question about why some sentences are better than others—and the collision between that frame and the existing discipline is what produced the spark. The outsider’s toolkit, applied with enough rigor, turns out to be unreasonably effective at finding things the insiders had stopped looking for.
This is, we think, the most underexplored category of how progress actually works. Not the clean hypothesis-to-proof pipeline. Something weirder: directed effort along a wrong vector that generates real results as a byproduct of the process.
We came at this from two directions. One of us is interested in how these people’s cross-domain thinking—the very fact that they were applying a foreign framework to an established field—is what made their contributions possible. The outsider’s lens as a creative instrument. The other is interested in something slightly different: the strange alchemy of wrong goals and right methods, where the destination was a fantasy but the journey was so scrupulously honest that the universe handed them something real anyway.
So here it is: different angles to scratching that same itch of chasing weirdos.
Aditya’s Thoughts
Two good examples I could think of are Richard Hamming and Stanislaw Ulam. They are famous in the way I mean: canonical in the right circles, under-discussed outside them, and remembered not just for discoveries but for a style of mind. I recently revisited Hamming’s excellent lecture, so I will quote him liberally. Unless mentioned otherwise, all quotes below are from that lecture.
You can trace a specific, load-bearing line from their border-crossing habits to the forma mentis they are actually remembered for. Unsurprisingly, Hamming states this in the introduction to his famous lecture series, The Art of Science and Engineering:
Style of thinking is the center of the course. I am concerned with educating and not training you.
Hamming is usually introduced as the Bell Labs mathematician behind error-correcting codes and the winner of the 1968 Turing Award. But the more interesting story is that he seems to have built an entire personal operating system for making cross-domain ideas more likely.
In the transcript of his famous Bellcore talk, ”You and Your Research,” Hamming describes eating first with physicists and then with chemists at Bell Labs because he had already learned most of the mathematics available at his own table. He deliberately placed himself where problems from other fields could leak into his head. He would ask people over lunch what the important problems in their field were. Then he would ask the much ruder follow-up: if you are not working on one of them, why are you here?
Hamming believed that great scientists carried around a live inventory of important, attackable problems, and that this inventory changed what they noticed.
I notice that if you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don’t quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, “The closed door is symbolic of a closed mind.” I don’t know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing not much, but enough that they miss fame.
He even formalized part of this into what he called “Great Thoughts Time”: Friday lunches reserved for questions like what computers would do to science, or which major shifts were arriving early enough to matter. He was unusually good at tracing where the tendrils of an idea might reach and clearing space for them to take root. He knew how to give his brainchildren room to grow.
For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. nine out of ten experiments would be done on the computer and one in ten in the lab. They knew I was a crazy mathematician and had no sense of reality. I knew they were wrong and they’ve been proved wrong while I have been proved right.
That is the Hamming pattern in miniature: he kept moving upstream. For him, the machine was downstream of a better question.
Ulam, by contrast, seems to have moved laterally, weaving through domains with extraordinary ease.
Ulam taught himself calculus at sixteen, emerged from the extraordinary Lvov mathematical scene, fled Europe just before the war closed over it, and ended up at Los Alamos. He contributed to thermonuclear weapons design, helped originate the Monte Carlo method, later appeared in the Fermi-Pasta-Ulam-Tsingou problem that helped open nonlinear science, and even co-proposed Orion, the nuclear-pulse spaceship idea. He refused to be intellectually boxed.
The Monte Carlo story gets closest to what I am after. In Roger Eckhardt’s Alamos account, Ulam recalls recovering from illness in 1946, playing solitaire, wondering about the odds of a successful game, and then asking whether it might be easier to simply play many times and count outcomes than to force the whole problem through combinatorics. From there he jumped almost immediately to neutron diffusion and mathematical physics.
And Ulam seems to have been built for that kind of leap. In a biographical sketch preserved through Los Alamos’s Center for Nonlinear Studies, his wife Francoise describes him as someone who carried everything in his head, whose mind outran his fingers, and who often produced written work mainly by talking it through. The same page quotes Gian-Carlo Rota describing Ulam after his 1946 illness as someone whose ideas came at odd intervals and were more fascinating than anything he had witnessed before.
That is why these two feel newly relevant in an AI moment. Call it the “judgment gap”, that the most important decisions are usually the ones with the least data, because once something is legible enough to spreadsheet cleanly, it is already closer to core business than frontier bet. Hamming and Ulam were particularly good at transforming the incomprehensible to the arbitrary.
It feels like a reminder that the first scaffold for any serious new world is still internal. Before a machine can search a possibility space, someone has to decide what counts as a possibility, which analogy is secretly doing the work, which problem is important enough to deserve obsession, and which toy model is worth inflating into a universe. The map is not the territory.
The great scientists, when an opportunity opens up, get after it and they pursue it. They drop all other things. They get rid of other things and they get after an idea because they had already thought the thing through. Their minds are prepared; they see the opportunity and they go after it. Now of course lots of times it doesn’t work out, but you don’t have to hit many of them to do some great science. It’s kind of easy. One of the chief tricks is to live a long time!
Saksham’s Thoughts
Weirdos With Wrong Routes to Real Places
Johannes Kepler wanted to prove that God had arranged the planets at distances corresponding to the five Platonic solids nested inside each other. He also believed the planets produced a celestial harmony that only God could hear, and he spent years trying to transcribe it. This is, to be clear, completely insane. But Kepler’s mystical obsession demanded precision — you can’t fit orbital data to a geometric cosmology without very good orbital data — and that demand for precision is what produced three of the most consequential laws in the history of science. The main quest was a fever dream. The side quest was the foundation of modern astronomy. I’m sure you’ve noticed already, by the way, but this is the Kepler — laws of planetary motion, elliptical orbits, the whole thing. The mystic chasing God’s geometry is the same man whose name your high school physics teacher wrote on the board.
Isaac Newton is somehow even better. The man who gave us calculus, classical mechanics, and the universal law of gravitation spent more of his total working hours on alchemy and biblical prophecy than on physics. He genuinely believed the Book of Daniel contained a secret chronological code for human history, and that he—uniquely among men—had been chosen to decode it. He pursued this with the same monastic rigor he brought to the Principia. The prophet’s quest led nowhere. But the habit of mind it forged— the obsessive, almost punishing focus, the willingness to sit alone with a hard problem for years—is probably inseparable from the physicist who pulled it off.
I’m going to indulge myself a little bit and frame this whole thing in the context of competitive gaming, so feel free to skip this next line if you wish: this whole thing resembles the actions of someone who decided to one-trick a niche pick in an off-meta role, and instead got so good he ended up not just creating a new meta, he ended up joining the dev team.
Paul Ehrlich had a concept he called the “magic bullet”—the idea that a specific chemical could be made to bind only to a pathogen and kill it without touching the host. His contemporaries found this fanciful, more theology than science. Ehrlich pursued it anyway with systematic, almost fanatical rigor: he tested compound after compound: 605 of them before he found something that worked against syphilis. The magic bullet metaphor was, arguably, more mystical intuition than hard science. But the process he designed to chase it was impeccably empirical, and that process gave us the conceptual and methodological foundation of all targeted drug therapy. In a just world, there’d be a biopic—somewhere with a mix of the procedural patience of Tinker Tailor Solider Spy and the mad obsessive energy of The Imitation Game—about a man who tested six hundred wrong answers before finding the right one.
Hedy Lamarr is the outlier in this group — the main quest wasn’t bogus so much as it was wildly misaligned with where history placed her value. She was one of the most famous film stars in the world, and she spent her private hours doing what she actually cared about: inventing things. During World War II, she co-developed a frequency-hopping spread spectrum communication system intended to make Allied torpedo guidance resistant to jamming. The US Navy didn’t use it. Hollywood certainly didn’t care. Her patent expired before anyone recognized its worth. But the principle she developed became the technical basis for WiFi, GPS, and Bluetooth. Her main quest, the one the world assigned her, was being beautiful on screen. The side quest was helping build the invisible infrastructure of the modern world. She is, in a very real sense, the architect of the network you’re using to read this — a fact that would have made a better third-act reveal than anything MGM put her in.
What unites all four of these people is something that should probably embarrass the philosophy of science a little: the fact that in esports terms, their macro was wrong, but it didn’t matter. Kepler’s nested Platonic solids were nonsense. Newton’s biblical chronology led nowhere. Ehrlich’s magic bullet was more metaphor than mechanism. Lamarr’s invention was filed and forgotten. But in every case, the rigor applied to the wrong goal produced something real, because rigorous empirical work has a way of generating true things as a byproduct even when the hypothesis driving it is false. Good process, run honestly against good evidence, tends to find something — even if it isn’t what you were looking for. It is, structurally, the same reason a speedrunner who dedicates years to routing the fastest path through a video game occasionally discovers an engine-breaking glitch that the developers never knew existed. You weren’t supposed to find that. But you were looking hard enough in the right places.
We tend to tell the history of science as a story of correct hypotheses confirmed by clean experiments. The actual history is considerably messier: a lot of it is people with weird, wrong, sometimes theologically motivated obsessions who happened to be scrupulous enough about their methods that the universe handed them something anyway.
Aditya’s Response
Saksham’s cases make a nice complement. His people — Kepler, Newton, Ehrlich, Lamarr — generated breakthroughs as a byproduct of chasing wrong or misaligned goals. Scientists I talk about — Hamming, Ulam — generated breakthroughs by deliberately importing frameworks from outside the field. These people had an aura of mythos, which is why we continue to talk about them today. And looking at their stories (n=6), it would seem like the catalyst that produced the breakthrough was not pedestrian.
Kepler needed Brahe’s decades of observational data and his own mystical geometric obsession. Lamarr needed a movie star’s resources and a self-taught engineer’s weekend compulsion. Hamming had to physically switch cafeteria tables and spend years eating awkward lunches with chemists. Ulam had to flee a continent and land, by historical accident, in a weapons lab surrounded by experimentalists.
The cost of the cross-domain move was enormous. Precisely why these times are exciting since that cost is collapsing.
If you have a laptop and an API key, you can interrogate an unfamiliar field in an afternoon with a fluency that used to require a postdoc and three years of acculturation. People are now working/vibing seven days a week not just because AI agents make it possible, but because they make work feel more fun and dramatically lower the barriers to building, testing, and shipping things. There is a growing sense that if you are not leaving an agent cluster running overnight, you are somehow falling behind.
Over the long arc of civilization, we have repeatedly transformed the incomprehensible into the arbitrary. In the process, we built digital mediums through which we increasingly interface with the world and solve problems.
Now, as AI compresses the distance between idea and implementation, creativity stands out as the limiting factor, apart from compute credits. That makes it especially worthwhile to study truly creative people in science and ask how they brought ideas to life before AI, before smartphones, before this constant layer of cognitive scaffolding. If they could do it then, equipped only with their minds and far more primitive tools, what worlds might we imagine now, armed with intelligent silicon?
Saksham’s Response
I really like the idea of how with LLMs, it is now much easier to implement, which means it’s much easier for an outsider to experiment in a field not close to their own with a fresh perspective. And this line of thought also makes me wonder: what happens when you give large amounts of data to a large language model and make them the outsider in this case?
The standard use case is to have the model solve a problem you already understand well enough to specify. But the more interesting case might be the Kepler case — pointing a system with enormous generative capacity and reasonable empirical discipline at a goal that is probably wrong, and seeing what it stumbles into on the way. LLMs are already being used in drug discovery pipelines to generate candidate molecules, most of which will fail, in the hope that a few won’t. That is, structurally, exactly what Ehrlich was doing in 1909. The magic bullet instinct, now running at scale.
The honest caveat is that LLMs also confabulate with tremendous fluency, which is the failure mode Kepler didn’t have—he couldn’t hallucinate orbital data, because the data existed and Tycho Brahe (three cheers for the madman himself) had spent decades collecting it. The model needs good empirical guardrails, or the rigor that made the historical cases work is absent and you’re left with only the wrong main quest. But with the right scaffolding—real experimental feedback loops, real data, real consequences for being wrong—there’s a reasonable argument that the most interesting thing to do with these systems isn’t to aim them at problems we know how to solve. It’s to aim them at problems we don’t, with a goal that might be completely wrong, and see what the side quests turn up.
History suggests the yield can be surprisingly good.