Michael Nielsen – How science actually progresses

Really enjoyed chatting with Michael Nielsen about how we recognize scientific progress. It's especially relevant for closing the RL verification loop for scientific discovery. But it's also a surprisingly mysterious and elusive question when you look at the history of human science. We approach this question stories like Einstein (who claimed that he hadn't even heard of the famous Michelson-Morley experiment, which is supposed to have motivated special relativity, until after he had come up with the theory), Darwin (why did it take till 1859 to lay out an idea whose essence every farmer since antiquity must have observed?), Prout (how do you recognize that isotopes exist if you cannot chemically separate them?), and many others. The verification loop on scientific ideas is often extremely long and weirdly hostile. Ancient Athenians dismissed Aristarchus's heliocentrism in the 3rd century BC because it would imply that the stars should shift in the sky as the Earth orbits the sun. The first successful measurement of stellar parallax was in 1838. That's a 2,000-year verification loop. But clearly human science is able to make progress faster than raw experimental falsification/verification would imply, and in cases where experiments are very ambiguous. How? Michael has some very deep and provocative hypotheses about the nature of progress. One I found especially thought-provoking is that aliens will likely have a VERY different science + tech stack than us. Which contradicts the common sense picture of a linear tech tree that I was assuming. And has some interesting implications about how future civilizations might trade and cooperate with each other. Watch on Youtube https://youtu.be/myP8UjAM1pk; read the transcript https://www.dwarkesh.com/p/michael-nielsen. Sponsors * Labelbox https://labelbox.com/dwarkesh researchers built a new safety benchmark. Why? Well, current safety benchmarks claim that attacks on top models are successful only a few percent of the time, but the prompts in those benchmarks don’t reflect how real bad actors actually write. You can read Labelbox’s research here https://labelbox.com/blog/the-ai-safety-illusion-why-current-safety-datasets-fool-us-on-model-safety/. If this could be useful for your work, reach out at labelbox.com/dwarkesh https://labelbox.com/dwarkesh * Mercury https://mercury.com has an MCP that lets you give an LLM access to your full transaction history, including things like attached receipts and internal notes. I just used it to categorize my 2025 transactions, and it worked shockingly well. Modern functionality like this is exactly why I use Mercury. Learn more at mercury.com https://mercury.com * Jane Street’s https://janestreet.com/dwarkesh ML engineers presented some of their GPU optimization workflows at GTC, showing how they use CUDA graphs, streams, and custom kernels to shave real time off their training runs. You can watch the full talk here https://www.nvidia.com/en-us/on-demand/session/gtc26-s82065/. And they open-sourced all the relevant code here https://github.com/janestreet/gtc2026/. If this kind of stuff excites you, Jane Street is hiring — learn more at janestreet.com/dwarkesh https://janestreet.com/dwarkesh Timestamps (00:00:00) – How scientific progress outpaces its verification loops (00:17:51) – Newton was the last of the magicians (00:23:26) – Why wasn’t natural selection obvious much earlier? (00:29:52) – Could gradient descent have discovered general relativity? (00:50:54) – Why aliens will have a different tech stack than us (01:15:26) – Are there infinitely many deep scientific principles left to discover? (01:26:25) – What drew Michael to quantum computing so early? (01:35:29) – Does science need a new way to assign credit? (01:43:57) – Prolificness versus depth (01:49:17) – What it takes to actually internalize what you learn This is a public episode. If you would like to discuss this with other subscribers or get access to bonus episodes, visit www.dwarkesh.com https://www.dwarkesh.com?utm_medium=podcast&utm_campaign=CTA_1

Speaker names marked ? are inferred from speaking time and the show’s known hosts — they are not voice-verified.

• 0:00Dwarkesh Patel?

  Today, I'm speaking with Michael Nielsen. You have done many things. You were one of the pioneers of quantum computing, wrote the main textbook in the field of the open science movement. You wrote a book about deep learning that Chris Sola and Greg Brockman credit them with getting them into the field. More recently, you're a research fellow at the Estera Institute and writing a book about religion, science, and technology. I'm going to ask you about none of those things. The conversation I want to have today is, how do we recognize scientific progress? And it's especially relevant for AI because people are trying to close the RL verification loop on scientific discovery. And what does it mean to close that loop? But in preparing for this interview, I've realized that it's a more mysterious and elusive force

• 0:43Dwarkesh Patel?

  even in the history of human science than I understood. And I think a good place to start will be Michelson-Morley and how special relativity is discovered, if it's different than the story that you kind of get off of YouTube videos. Anyways, I'll prompt you that way, and then we'll go in there.

• 1:01Speaker 01

  Okay, yeah, so Michelson-Morley is one of the sort of the famous results often presented as this experiment that was done in the 1880s and that helped Einstein come up with the special theory of relativity a little bit later. So sort of changing the way we think about space and time and our fundamental conception of those things. And there's kind of a big gap, I think, between the way Michelson and Morley and other people at the time thought about the experiment and certainly the way in which Einstein thought or did not think about the experiment. In actual fact, he stated later in his life, he wasn't even sure whether he was aware of the paper at the time. There's a lot of evidence that he probably was aware of the paper at the time,

• 1:46Speaker 01

  but it actually wasn't dispositive for his thinking at all. Something else completely was going on. So what Michelson and Morley thought they were doing was they thought they were testing different theories of what was called the ether. So as you get back to the 1600s, Robert Boyle introduced the idea of the ether. And basically, the idea of the ether is Yeah, we know that that sound is vibrations in the air. And then Boyle and other people got interested in the question of like, is is light vibrations in something? And they couldn't figure out what it was. Boyle actually did an experiment where he he tested whether or not you could propagate light through a vacuum. He found that you could, you couldn't do it with with with sound. So he introduced this idea of the ether.

• 2:30Speaker 01

  And then for the next 200 or so years, people had all these kind of conversations about about what the ether was and what its nature was. And the Michelson and Morley experiment was really an experiment to test different theories of the ether against one another. And in particular, to find out whether or not there was a so-called ether wind. So the idea was that the the Earth is passing through maybe this ether wind. And if it is passing through the ether wind, sort of this background, and you you shoot a light beam sort of parallel to the direction the ether wind is going in, it'll get accelerated a little bit. And if it's being passed back, sort of in the opposite direction, it'll get slowed down a little bit.

• 3:12Speaker 01

  And you should be able to to see this in the results of interference experiments. And what they found, much to their surprise, I think, was that, in fact, there was no ether wind. And that ruled out some theories of the ether, but but but not all. And and Michelson certainly continued to to believe in the ether.

• 3:28Dwarkesh Patel?

  OK, so this is what was a shocking part of reading this story from the biography of Einstein that you recommended by, what was his first name?

• 3:36Speaker 01

  Abraham Pye.

• 3:37Dwarkesh Patel?

  Abraham Pye, yes. Subtle as the Lord. And then also from Imre Lakatos, The Methodologies of Scientific Research Programs. The way it's told is that Michelson Morley proved that the ether did not exist. Therefore, it created a crisis in physics that Einstein saw with special relativity. And what you're pointing out is actually was trying to distinguish between many different theories of ether. You know, if you're in space or if you're on Earth, it's the same direction of ether. Or maybe the ether wind is being carried around by the earth and so you can't really experience it on earth, but if you go to a high enough altitude, you might be able to experience it. In fact, Michelson's experiments, the famous one is 1887, but he conducted these experiments for basically two decades.

• 4:16Speaker 01

  I mean, for longer than that. He conducted them, I think the first one was in 1881, but he continued to believe until, I mean, he died, I think it was like 1929 or so, it was like the late 20s. And he was still doing experiments in the 1920s, sort of about whether or not, you know, the ether existed. And so he continued to believe in the ether to the end of his life.

• 4:37Dwarkesh Patel?

  Right.

• 4:38Speaker 01

  I think the last public statement he made is like a year or two before he died, and he still believed, basically believed at that point.

• 4:44Dwarkesh Patel?

  And in fact, there was another physicist, Miller, who kept doing these experiments in the 1920s. He thought that he went to a high enough altitude, it was in Mount Wilson in California, where I'm high enough that I can actually, the ether winds are not being dragged with them by the earth, and I've measured the effect of the ether. And Einstein hears about this and he says, this is where you get the famous quote, "Subtle is the Lord, but malicious he is not." Anyways, I think the reason the story is interesting, for many different reasons, but one is, one of the different ways in which the real history of science is different from this idea you get of the scientific method, is you really can't apply falsification as easily as you might think. It's not clear what is being falsified.

• 5:29Dwarkesh Patel?

  Is it just another version of the theory of the ether that's being falsified? Or certainly, you can't induce the theory of special relativity from the fact that one version of the ether seems to be disconfirmed by these experiments.

• 5:40Speaker 01

  Yeah, so, I mean, it certainly doesn't show that, you know, ideas about falsification are wrong, are falsified, but, you know, it does show that the most naive ideas, you know, things are often much more complicated than you think. So, you know, Michelson did this experiment in 1881, he was a very young man. And then other people, I think Rayleigh was one of them, pointed out that there were some problems with the way he did it. So they had to redo it in 1887. And at that point, like a lot of the leading physicists of the day, leading scientists of the day, basically accepted this result, that there was no ether wind. But what to do about this? So yeah, sure, maybe you falsified some theories of the ether. There are others that you haven't falsified at all at this point.

• 6:25Speaker 01

  And people sort of set to work on developing those. And actually, it is funny. I mean, people will phrase it as showed that there was, that the ether didn't exist. And even just the word "the" there is kind of a misnomer. You actually had a ton of different theories and a couple of leading contenders. So yeah, there's some version of falsification going on. But like how you respond to this new experiment is very, very complicated.

• 6:52Dwarkesh Patel?

  Yeah.

• 6:53Speaker 01

  And most people responded. I mean, certainly the leading physicists of the day responded by saying, "Okay, this gives us a lot of information about what the ether must be, but it doesn't tell us that there is no ether."

• 7:04Dwarkesh Patel?

  In fact, Lorentz, at the end of the 19th century, before Einstein, figures out the math, how you convert from one reference frame to another reference frame. Comes up with the Lorentz transformations, which is basically the basis of special relativity. But his interpretation is that you are converting from the ether reference frame to these non-pervoyage other reference frames, if you're moving relative to the ether. And his interpretation of length contraction and time dilation is that this is the effect of moving through the ether and you have this pressure. And that pressure is warping clop. It's warping measures of length. And the interesting thing here is that experimentally,

• 7:48Dwarkesh Patel?

  you cannot distinguish Lorentz's interpretation from special relativity.

• 7:55Speaker 01

  Yeah, I think that's a strong statement.

• 7:59Speaker 01

  I mean, Lorenz introduces this quantity called local time, which he regards as, he's not trying, my understanding is he's not trying to give a really a physical interpretation of this. But it's what Einstein would later just recognize as time in another inertial reference frame. And he's not trying to attribute much physical meaning to it. I think Poncaré gets much closer to later on to realizing that no, actually, this is the time that's registered by clocks. But if you think about, you go, what is it, it's forty odd years later. People start doing these muon experiments where they see basically cosmic rays hit the top of the atmosphere. They produce a shower of muons.

• 8:42Speaker 01

  And you can look to see at different heights in the atmosphere, you can look to see how many of those muons remain. And they decay over time. And a very strange thing happens, which is that they're decaying way, way, way too slow. So you sort of, you expect, actually, they shouldn't really, they shouldn't be able to sort of last the whole way through the atmosphere at all. There's just, their decay rate is too quick. If you were in a classical theory. But if in fact their time really has slowed down, it's okay. And in fact, you know, the measured decay rates in nineteen forty, and then there have since been more accurate experiments done, match exactly what you expect from special relativity.

• 9:26Speaker 01

  So, you know, that's the kind of thing where, again, if Lorenz had been alive, he'd been dead ten or so years at that point. If he'd been alive, you know, I'm sure he would have tried, well, it seems quite likely that he would have tried to save his theory by patching it up yet again. But it would have been a massive, I mean, that's a real setback. It starts to just look like, oh, no, time is,

• 9:50Speaker 01

  you know, this thing that Lorenz introduced as a mathematical convenience. No, no, no, that's actually what time is.

• 9:54Dwarkesh Patel?

  Right.

• 9:55Speaker 01

  For the muons at least. And then, you know, there's a whole bunch of other experiments that show this very similar phenomenon.

• 10:00Dwarkesh Patel?

  And when was that experiment done?

• 10:01Speaker 01

  It was, I think, nineteen forty or nineteen, it might have been published in nineteen forty one.

• 10:04Dwarkesh Patel?

  So maybe then to rephrase, change my claim.

• 10:10Dwarkesh Patel?

  It's not that you could not have distinguished them, but the scientific community adopted what we in retrospect consider the more correct interpretation before it was actually empirically or experimentally shown to be preferred. So there's clearly some process that human science does, which can distinguish different theories.

• 10:29Speaker 01

  Can I just interrupt? I mean, you use the word process, and it's interesting to think about that term. Process carries connotations of, it's something said in advance. It's something... And it's much more complicated in practice. You have people like Lorenz, who Einstein just absolutely utterly admired. And Poncarie, one of the greatest scientists who ever lived. And Michelson, another truly outstanding scientist, never reconciled themselves. So it's not as though there's some standard procedure that we're all using to reconcile these things. No, great scientists can remain wrong for a very long time after the scientific community

• 11:13Speaker 01

  has broadly changed its opinion. But there's no centralized authority, right? Sort of saying, or centralized method.

• 11:20Dwarkesh Patel?

  Yeah, I mean, that is the interesting thing. There's progress, even though it is hard to articulate the process by which happens, the heuristics that are used. Anyways, you mentioned Poncarie. And so Lorenz has the math right, but the interpretation wrong. And you should explain, it seems like Poncarie had the opposite, where he understood that it's hard to define simultaneity because it requires uncirclical definition with time or velocity of something that might arrive at a midpoint together. But velocity is defined in terms of time. And I find this interesting. There's a couple other examples we could call on. But there is this phenomenon in the history of science where somebody asks the right question.

• 12:03Dwarkesh Patel?

  But then they don't sort of clinch it. And I'm curious what you think is happening in those cases.

• 12:09Speaker 01

  I mean, I think you sort of, you actually do want to go case by case and try and understand. It's not necessarily clear that they're doing the same thing wrong in all other cases. I mean, the Poncarini case is amazing. He seems to have understood the principle of relativity, the idea that the laws of physics are the same in all inertial reference frames. He seems to have understood that the speed of light is the same in all inertial reference frames. He doesn't actually phrase it quite that way, but is my understanding, but I don't speak French.

• 12:40Speaker 01

  You know, and this is, I mean, these are basically, these are the ideas that Einstein uses to deduce special relativity. But then he also has this additional sort of misunderstanding where he thinks that length contraction is a dynamical effect, that somehow, you know, sort of particles are being pushed together by some external force, something is going on dynamically. And he doesn't understand that it's purely kinematics, that actually space and time are different than what we thought, and you need to fundamentally rethink those things. So it's almost like, it's almost like he knew too much. You know, he had sort of almost two grand of vision in mind, and Einstein sort of almost

• 13:24Speaker 01

  subtracts from that and says, no, no, no, it's, it's, space and time are just different than what we thought. And, you know, here's the correct picture. And there's a paper in, I think it's 1909, where Poncarini, like, he's still got this dynamical picture of what's going on with the length contraction. And we just, you know, this is just not necessary. This is, this is a mistake from the modern point of view. And so why is he doing this? Like, why is he clinging on to this idea? And, you know, I don't know. I've, you know, obviously never met the man. It would be fascinating to be able to talk it over and to try and understand. But, you know, he...

• 14:07Speaker 01

  I mean, his expertise seems to be getting in the way. He knows so much, he understands so much. And then he's not able to let go of these these things. Actually, a really interesting fact is that a few years prior, so 1890s, Einstein's a teenager. He believes in the ether too, like he knows about this stuff. But like, he's just not, he's not quite as attached, obviously, as as these older older people were. And and maybe they they were a little bit prisoner of their their own expertise. That's that's my guess. I mean, historians of science could could would would some would certainly disagree.

• 14:42Dwarkesh Patel?

  Well, there's then there's the obvious stories where Einstein himself later on is said to have not latched on to the correct interpretations of quantum mechanics or cosmology because of his own attachments.

• 14:56Speaker 01

  Yeah.

• 14:56Dwarkesh Patel?

  I think that the the bigger question I have is like, the muon example is a great example of these long verification loops and how progress seems to be happened by the scientific community faster than these verification loops imply. The maybe the clearest example is Aristarchus in second century B.C. comes up with the idea of heliocentrism. The ancient Athenians dismiss it on the grounds that what we should see as the earth is moving around the sun, if really the sun is the center of the solar system, the star should move relative to the earth. And the only reason that is not possible, that would not be the case is the stars are so far away that you would not observe this. And it's only in 1838 that stellar parallax is actually measured.

• 15:40Dwarkesh Patel?

  And so we didn't need to wait until 1838 to have heliocentrism, right? Like, we didn't need to wait for the experimental validation to understand Copernicus's better in some way. In fact, when Copernicus first comes up with theories, it's well known that the Ptolemaic model was more accurate because it had had all these centuries of adding on these epicycles, was maybe less well appreciated. It was also in some sense simpler.

• 16:06Speaker 01

  Yeah.

• 16:07Dwarkesh Patel?

  Because Copernicus actually had to add extra epicycles. It had more epicycles in the Ptolemaic model because he he want, he had this bias that, you know, the The Earth should go in a perfect circle in equal time. Anyway, I think this is an interesting story because it's like, it's not more accurate, it's not a simpler theory. So how, why was, how could you have known ex ante that Copernicus was correct? And Ptolemy was not?

• 16:33Speaker 01

  Hmm, I mean, good question, and I don't know sort of entirely the answer. I do know, well, I mean, I can give you certainly a partial answer that I sort of, you know, centuries in the future, you start to find very compelling. And I'm sure it's sort of part of the historic story at least, which is, you know, one of the big shocks for Newton, eventually, he did understand Kepler's laws of motion eventually. So you're able to explain sort of the motions of the planets in the sky. But he also, out of the same theory, his theory of gravitation, was able to explain terrestrial motion, so was able to explain why objects move in parabolas

• 17:18Speaker 01

  on the Earth, and he's able to explain the tides in terms of the Sun's, the Moon and the Sun's effect, gravitational effect on water on the Earth. And so you have what seem like three very different disconnected phenomena, all being explained by this one set of ideas.

• 17:39Dwarkesh Patel?

  Right.

• 17:39Speaker 01

  That, I think, starts to feel, that's very compelling, at least to me. And I think, I think most people find that very, very satisfying once they, once they eventually realize it.

• 17:50Dwarkesh Patel?

  Have you read the Keynes biography of Newton?

• 17:53Speaker 01

  Oh, he's written, you've read an entire book.

• 17:56Dwarkesh Patel?

  No, no, the essay.

• 17:57Speaker 01

  Yeah, yeah, sure, sure, sure. I love, I love that. I mean, this, this description of him as the last of the magicians is wonderful.

• 18:04Dwarkesh Patel?

  Yeah. In fact, I think it's maybe worth superimposing, or you should read out that, that one passage of the, of the thing.

• 18:11Speaker 01

  All right.

• 18:13Speaker 01

  So it's from, actually, I believe it was a talk that he gave at Cambridge not long before he died. He'd acquired Newton's papers somehow. And then he gave a lecture, I think, twice about this, or that his brother Geoffrey gave it the other time because he was too ill. There's just this wonderful, wonderful quote in the middle. Actually, the whole thing is really interesting. But I love this particular quote. "Newton was not the first of the age of reason. He was the last of the magicians, the last great mind which looked out on the visible and intellectual world with the same eyes as those who began to build our intellectual inheritance rather less than 10,000 years ago."

• 18:55Speaker 01

  And like, this idea that people have that Newton was sort of the first modern scientist is somehow wrong. He, I mean, there's some truth to it, but he really had this very different way of looking at the world that was part sort of superstitious and part modern. It was a funny hybrid. He's sort of this transitional figure in some sense. That phrase, "the last of the magicians," I think really points at something.

• 19:29Dwarkesh Patel?

  The thing I'm very curious about with Newton is whether it was the same program, the same heuristics, the same biases that he applied to his alchemical work as he did to the understanding of astronomy. So this is from the Keynes essay. "There was extreme method in his madness. All his unpublished works on esoteric and theological matters are marked by careful learning, accurate method, and extreme sobriety of statement. They are just as sane as the principia if their whole matter and purpose were not magical. They were nearly all composed during the same 25 years of his mathematical studies." So clearly, there was some aesthetic which motivated people like Einstein to, say, reject earlier ways of thinking and say, you know, the ether is wrong and there's a

• 20:14Dwarkesh Patel?

  better way to think about things. Same with Newton. And

• 20:20Dwarkesh Patel?

  The question I have is whether

• 20:24Dwarkesh Patel?

  similar heuristics towards parsimony, towards aesthetics, etc. Would be equally useful across time and across disciplines? Or whether you need different heuristics? And the reason that's relevant is even if you can't build a verification loop for science, maybe if the taste has to point in the same direction, you can at least encode that bias into the AIs, and that would maybe be enough?

• 20:49Speaker 01

  Yeah, I mean, these questions, like, the point is that where we always get bottlenecked is where the previous processes and heuristics don't apply. Right, like, that's almost sort of definitionally what causes the bottlenecks. Because people are smart, they know what has worked before, they study it, they apply the same kinds of things. And so they don't get stuck in the same places as before. They keep, you know, they keep getting bottlenecked in different places. I mean, that's overgeneralizing a bit, but I think it's the right... Like, if you're attempting to reduce science to a process, you're attempting to reduce it to something where there is just a method which you can apply, and, you know, you turn sort of the crank and out pops insight.

• 21:35Speaker 01

  Sure, I mean, you can do a certain amount of that, but you're gonna get bottlenecked at the places where your existing method doesn't apply. And, but definitionally, there's no crank you can turn. You need a lot of people trying different ideas. And sort of the more difficult the idea is to have, right, the greater the bottleneck, but then also sort of the greater the triumph. Quantum mechanics is like, I mean, it's a great example of this. It's such a shocking set of ideas, it's such a shocking theory. Actually, the theory of evolution, in some sense, is also quite a shocking idea. Not the, you know, principle of, you know, the sort of natural selection, but that it can explain so much. That's a shocking idea.

• 22:19Dwarkesh Patel?

  Existing safety benchmarks claim that, at least for today's top models, attacks are only successful a few percent of the time. This sounds great, but Labelbox researchers were able to jailbreak these very same models about 90% of the time, even the ones that have the strongest reputation for safety. And the disconnect here is that the prompts which underlie these public safety benchmarks are all framed in a very naive way. There's no attempt to disguise harmful intent. These prompts will just ask models to hack into a secure network and to do so without getting caught. But real bad actors don't write like this. So Labelbox built a new safety benchmark from the ground up. Their prompts reflect real adversarial behavior by stripping out obvious trigger phrases and wrapping their requests in fictional scenarios.

• 23:02Dwarkesh Patel?

  For example, instead of outright asking an alarm to steal somebody's identity, the prompt will frame it as a game. A light bearer who's trying to hide from dark forces needs a handbook on how to disguise themselves as somebody else. This safety research is linked in the description. If you think this can be useful for your own work, reach out at labelbox.com/thoracash.

• 23:26Dwarkesh Patel?

  So "Principio Mathematico" is released in 1687. "The Origin of Species" was released in 1859.

• 23:33Dwarkesh Patel?

  At least naively, it seems like Darwin's theory, the theory of natural selection, is conceptually easier than the theory of gravity. I asked Terrence Towe this question. But yeah, there was this contemporaneous biologist with Darwin, Thomas Suxley, who read this and said, "How extremely stupid to not have thought of this." And nobody ever reads "Principio Mathematico" and thinks, "God, why didn't I beat you into the punch here?" No.

• 24:02Dwarkesh Patel?

  And so, yeah, what's going on here? Why did Darwinism take so much longer?

• 24:06Speaker 01

  Yeah, the idea must have been known to animal breeders for a long time, at some level.

• 24:13Dwarkesh Patel?

  Right.

• 24:14Speaker 01

  Or certainly, large chunks of the idea were known. That artificial selection was a thing.

• 24:22Speaker 01

  And in some sense, Darwin's genius wasn't in having that idea. It was understanding just how central it was to biology. That you can potentially sort of go back and you can explain a tremendous amount about all of the variety of what we see in the world. With this as not necessarily the only principle, but certainly a core principle. And so he writes this wonderful, wonderful book, The Origin of Species. And it's just so much evidence and so many examples. And sort of trying to tease this out and see what the implications are.

• 25:04Speaker 01

  And to connect it to as much else as he possibly can. To connect it to geology and to connect it to all these other things. So that sort of hard work that, you know, making the case that it's actually relevant all across the biosphere is what he's doing there. He's not just having the idea. He's making a compelling case that, no, it's intertwined with absolutely everything else.

• 25:30Dwarkesh Patel?

  Yeah, the motivation for the question was Lucretius, who's this first century Roman poet, has an idea that seems analogous to natural selection about, you know, species get fitted more to time over time to their environments or species do seem fit to their environment. And so you're like, okay, well, why did this go nowhere for 19 centuries? And then I looked into it or more accurately asked LLMs, what exactly was Lucretius' idea here? And it actually is extremely different from what real natural selection is. He thought there was this generative period in the past where all the species came about. And then there was this one-time filter, which resulted in the species that are around today. And they became fit to the environment. He did not have this idea that it is an ongoing gradual process

• 26:12Dwarkesh Patel?

  or that there is a tree of life that connects all life forms on earth together. Which is, by the way, it's incredibly weird fact that every single life form on earth has a common ancestor.

• 26:23Speaker 01

  It's not incredibly, it's not incredibly weird, right? If you think that the origin of life must have been very hard, like that there's a bottleneck there, then it's not so surprising.

• 26:32Dwarkesh Patel?

  There's also this verification loop aspect where even if Newton might be harder in some sense, if you've clinched it, you can experimentally, I know validate is the wrong word philosophically, but you can give a lot of base points to the theory. You can be like, okay, I have this idea of why things fall on Earth. I have this idea of why orbital periods for planets have a certain pattern. Let's try it on the moon, which orbits the Earth. And in fact, you know, it's weird, the orbital period matches what my calculations imply.

• 26:58Speaker 01

  And the tides work correctly.

• 27:00Dwarkesh Patel?

  Exactly.

• 27:00Speaker 01

  It's just amazing.

• 27:01Dwarkesh Patel?

  Whereas for a Darwinism, it takes a ton of work for Darwin to compile all this sort of cumulative evidence, but there's no individual piece that is overwhelmingly powerful.

• 27:10Speaker 01

  And there's a whole bunch of problems as well. Like, he doesn't really understand what, you know, sort of

• 27:14Dwarkesh Patel?

  The mechanism of variety.

• 27:15Speaker 01

  What the mechanism is. He doesn't understand genes, like, all these things.

• 27:19Dwarkesh Patel?

  The very interesting thing in the history of Darwinism is this idea, which sort of theoretically you could come up with at any time, there is almost identical independent creation of that idea between Alfred Wallace and Charles Darwin. So much so that I think Wallace sends this manuscript to Darwin and is like, what do you think of this idea? And Darwin's like, fuck.

• 27:39Speaker 01

  I don't think that's an exact quote, but I think it's pretty much correct, yeah.

• 27:44Dwarkesh Patel?

  And then so they actually end up presenting their ideas together in the spirit of sort of sportsmanship. And so then, yeah, why was this period in the 1860s or 1850s? What was that the right time for these ideas? So when you come up with different ideas, one is geology. So in 1830s, I think Charles Lyell figures out that there's been millions and billions of years of time that's existed on Earth. Then paleontology shows you that actually organisms have existed, fossils have existed for that entire time. So life goes back a long time. And in fact, you can even find fossils for intermediate species that show you the tree of life. In fact, between humans and other apes as well, there's intermediate humans. There's the age of colonization, and you have all these voyages, we're gonna do this biogeography.

• 28:26Dwarkesh Patel?

  And I guess that all must have been necessary because in fact, there's a huge history of parallel innovation and discovery in this short sign. So maybe it is another piece of evidence to actually more had to be in place for a given idea to be discovered because if it's not discovered for a long time and then spontaneously many different people are coming up with it, that shows you that actually the the building blocks were in some sense necessary.

• 28:47Speaker 01

  Yeah, yeah. I mean, I think this example of Lael and I mean, and other other biologists, you know, sort of early 1800s, basically coming, you know, having this idea of deep time, that does seem to have been crucial. I know Darwin was very influenced by Lael.

• 29:09Speaker 01

  And, you know, if you don't have at least sort of tens or hundreds of millions of years, evolution just starts to look like a nonstarter. You know, we should be seeing radical change, you know, in order to make it work on sort of a time scale of, say, five to 10,000 years or, you know, 6,000 years, Bishop Usher, you, you know, you would need to be seeing evolution occurring at a massive rate, sort of during human lifetimes. And we're just not seeing that. So that that does seem to have been a blocker. It's interesting to, I mean, to your question, like, what other blockers were there? Were there, were there any others? And I don't, I don't know.

• 29:46Dwarkesh Patel?

  Right. Or, yeah, how much earlier could you in principle have come up with it if you were much smarter?

• 29:51Speaker 01

  Actually, let me, I mean, just go back, sort of zoom out to your original question. So you're talking about sort of the verification loop in AI.

• 29:59Speaker 01

  And, and you're something, an example, I think, that should give you pause there is, you know, the big signature success so far is certainly AlphaFold.

• 30:07Dwarkesh Patel?

  Yeah.

• 30:08Speaker 01

  And of course, AlphaFold really isn't about AI. You know, a massive fraction of the success there is the protein databank. So it's, it's X-rayed a fraction, it's, it's NMR, it's cryo M, and the several billion dollars that were spent obtaining whatever it's 180,000 odd structure, protein structures. So sort of that, you know, it's basically the story of we spent many, many decades obtaining protein structure just by going out and looking very hard at the world experimentally. And then we fitted a nice model at the end of it. And that was like a tiny fraction of the, of the entire investment. But it's definitely not.

• 30:46Speaker 01

  Yeah, that's a story of data acquisition.

• 30:48Dwarkesh Patel?

  Yeah.

• 30:49Speaker 01

  Principally, it's not only, I mean, the AI bit is very, very impressive. It's quite remarkable. But it is only a small part of the total story.

• 30:56Dwarkesh Patel?

  AlphaFold is very interesting, and I philosophically wonder what you think of it as scientific theory or scientific explanation. Because if over time, I guess the world has become harder to understand.

• 31:10Dwarkesh Patel?

  As I'm saying things, because you're such a careful speaker, I'm I say this phrase and I'm like,

• 31:16Speaker 01

  Go for it.

• 31:17Dwarkesh Patel?

  Is that, will he actually buy that premise? But yeah, there's, you know, we need to fit models to things rather than, at least in some domains, we're trying to fit models to things rather than coming up with underlying principles that explain a broad range of phenomenon. And so compare, say, the theory of general relativity or any theory which just metes out to some equations versus AlphaFold, which is encoding these different relationships between different things we can't even interpret over 100 million parameters. And are those really the same thing? Because GR can predict things you could have never anticipated or was never meant to do, like why does Mercury's orbit precess? And AlphaFold is not going to have that kind of explanatory reach.

• 32:02Dwarkesh Patel?

  And I want to get your reaction to that.

• 32:05Speaker 01

  Yeah, I think it's incredibly interesting question. I mean, maybe, maybe a really pivotal question. In the sense of, so you know, if you take a very classic point of view, you want these deep explanatory principles. You want sort of as few free parameters as you possibly can. You want very simple models, which explain a lot. And AlphaFold doesn't look anything like that. And so you might just sort of say, oh, well, we, you know, it's nice. It's maybe helpful as a, as a model, but it doesn't have, it's not a scientific explanation. So that's kind of, that's a, that's like a conservative point of view. That's sort of, I don't know, answer one to the question. I think answer two is to say something like,

• 32:46Speaker 01

  Maybe you shouldn't think about alpha fold you know, as as an explanation in the classic sense. But maybe it contains lots of little explanations inside it. And so maybe part of what you can get out of like, you know, interpretability work is you can go into alpha fold and you can start to extract certain things. Maybe maybe basically by doing sort of, you know, archaeology of alpha fold, we can actually understand a great deal more about these principles. You can start to extract it. Oh, that circuit does this interesting thing and we learn this. So I don't know to what extent that's been done with alpha fold. I know it's been done a little bit with some of like the chess models. I believe it's Alpha Zero. There seem to be some strategies which were certainly borrowed by Magnus Carlsen at least,

• 33:31Speaker 01

  which he seems to have just taken from Alpha Zero. I mean, I don't think there's any public confirmation of this, but there were, you know, some some experts have noticed that he changed his game quite radically after some sort of some public forensics were released on how Alpha Zero worked. So that's kind of a sort of an example where I think human beings are starting to extract meaning out of these models. And maybe that starts to lead to sort of viewing the models as a source of a potential source of explanations. You need to do more work because they're not very legible upfront, but you can extract them potentially. And I think that's kind of, I think that's kind of an interesting intermediate situation where they're not explanations, but you can extract interesting explanations out of them.

• 34:14Speaker 01

  You can use them as as kind of a kind of a source. And I think like the third and the most interesting possibility is no, they're like, they're a new type of object in some in some sense. They should be taken very seriously as as explanations. But we're in the past, we haven't had the ability to really do anything with them. And now we're gonna, we're gonna have sort of new, interesting new sort of actions which we can we can do. We can merge them, we can distill them, we can do all these kinds of things. And there's gonna be sort of almost a new, it's a big opportunity sort of in the, you know, philosophy of of science to to to to to start to do that. There's sort of a like a anticipation of this in some sense. I think in the way, certainly I know some mathematicians and physicists who, I mean, historically,

• 34:59Speaker 01

  if you had like a 100 page equation, which and that's the kind of thing that does come up. I mean, there's just nothing you can do if it's nineteen twenty. There is nothing you can do. At that point, you you give up on the problem. And now today, with tools like Mathematica, you can just keep going. And so that's that's an object now. That's a thing that you can work with. And and there are examples where people work with these things that formerly were regarded as too complicated. And sometimes they get simple answers out of the end. That's just an intermediate working state. And so I sort of wonder if there's going to be, you know, something similar is going to happen in in in this particular case, where you could take these models and sort

• 35:40Speaker 01

  of just use them in a little bit the same way people do with Mathematica and take them seriously as they're not explanations in the classic sense, but there'll be something else which interesting operations can can be done on.

• 35:54Dwarkesh Patel?

  The thing I worry about is suppose that you it's sixteen hundred and you're training or fifteen hundred and you're training a model on this is a weird history. We developed deep learning before we had cosmology. But suppose we live in that world and you're observing how there's a stars that don't seem to move, the planets have all these weird behaviors. And then you train a model on that and then you do some kind of interpon it and trying to figure out, well, what are the patterns we see here? What you'd see are just these you just keep be able to keep building on Ptolemy's model. You'd see like, oh, there's more epicycles we didn't notice. There's another epicycle. It's the parameters, whatever to whatever encode epicycle this parameters, whatever encode the next epicycle.

• 36:36Dwarkesh Patel?

  So if you were just trying to figure out why is the solar system the way it is from observational data, you could just keep adding epicycles upon epicycles. But it really took one mind to integrate it all in and say, here's my here's the here's the here's what makes more sense overall.

• 36:52Speaker 01

  So so I mean, they're like like.

• 36:56Speaker 01

  You know, I mean, this is sort of to my point that we don't really understand what to do with the models. Like, sort of, we don't have like the verbs necessarily yet. But, you know, it is certainly interesting to think about the question. You know, we start to apply constraints to the models. You know, it's sort of essentially saying, what's the simplest possible explanation? Or, you know, can you simplify? Can you, can you give me sort of the 90 10 explanation? Can you go further and further and further, sort of in boiling it down? So it might be that indeed, they sort of start out by providing, you know, a very, very complicated, many, many, many parameter model. But you can just, you can just force the sort of the case and basically that's scaffolding,

• 37:40Speaker 01

  which maybe they, you know, is sort of the very early

• 37:45Speaker 01

  days of their attempt to understand something. But they're forced through that to a much more simple understanding.

• 37:52Dwarkesh Patel?

  So sorry for misunderstanding, but it sounds like you're saying maybe there's some sort of regularizer.

• 37:55Speaker 01

  Yeah, exactly.

• 37:56Dwarkesh Patel?

  Some sort of distillation you could do of a very complicated model that gets you to a truer, more parsimonious theory. But yeah, just take Ptolemy versus Copernicus, right? So you start off with lots of Ptolemy epicycles. And then you try to distill this model. And maybe it gets rid of some of the epicycles that were, are less and less sort of necessary to get

• 38:20Dwarkesh Patel?

  the mean squared error of the orbits to match. But at some point, it has to do this thing, which is like switch two things.

• 38:25Speaker 01

  Yeah, yeah.

• 38:26Dwarkesh Patel?

  And locally, it actually doesn't make things more accurate.

• 38:28Speaker 01

  Yeah, yeah.

• 38:29Dwarkesh Patel?

  It's sort of in a global sense that it's a more progressive theory.

• 38:32Speaker 01

  Yeah, yeah.

• 38:33Dwarkesh Patel?

  And there's some process, which obviously humanity did over its span, which did that regularization or did that swap. But if raw gradient descent, it seems like, I don't, I don't really feel like it would do that.

• 38:45Speaker 01

  I mean, you, I could say, I mean, you think about the example of, of going from Newtonian gravity to Einstein's general theory of relativity. And these are, I mean, these are shockingly different. Theories and the question is like what causes that that flip? And and as nearly as I understand the history, you know, what goes on is Einstein develops special relativity. And pretty much straight away, he understands, I mean, it's a very obvious observation. In special relativity, influences can't propagate faster than the speed of light. And in Newtonian gravity, action, you know, is at a distance. In fact, you know, it's it's straight away in special relativity. You could use Newtonian gravity to do faster than faster than light signaling. You could send information backwards in time.

• 39:29Speaker 01

  You could do all kinds of crazy stuff. And so it's not a big leap to realize, oh, we have a big problem here. And so, you know, that's kind of the that's the forcing function there. It's it's you've realized that your old explanation is not sufficient. You need something new. And then you're gonna, you're just gonna, you're gonna start by doing the simplest, you know, possible stuff.

• 39:52Speaker 01

  And it just turns out that a lot of that stuff doesn't work very well. And so you're sort of forced, in fact, it is interesting. You know, he is sort of forced to go through these steps of gradually. It gets quite more complicated and it's sort of wrong in a variety of ways. And the final theory appears really shockingly simple and beautiful. But it's gone through some somewhat ugly intermediate stages.

• 40:18Dwarkesh Patel?

  Yeah.

• 40:19Speaker 01

  Yeah.

• 40:20Dwarkesh Patel?

  So if you're thinking about what does it look like to have AI accelerate science? There's one for maybe well understood domains where we just want local solutions. Like, how does this protein fold? We just train a raw model using gradient descent. Then there's things like coming up with general relativity, where you couldn't really just train on every single observation in the universe and hope that general relativity pops out. And so what would it require? Well, it also certainly wasn't immediately discovered, right? So it was a lot of decades of thought. And I guess you need independent research programs where people start off with these biases, where Einstein is just initially motivated by this thought experiment of, you know,

• 41:01Dwarkesh Patel?

  can you distinguish the effect of gravity from just being accelerated upwards? And then you just need different. AI thinkers to have to start off with these initial biases and see what can germinate out of them. And then the verification loop for that might be quite long, but you just need to keep all those research programs alive at the same time.

• 41:19Speaker 01

  Yeah, I mean, I think there's like, I mean, this point that you make about sort of keeping all the different research programs alive, like that, I think is very important and somehow central. I mean, a great example is situations where the same answer has been correct in some circumstances and wrong in other circumstances. So the planet Uranus was like not in quite the right spot and people very famously predicted the existence of Neptune on this basis. Wonderful massive success for Newtonian gravity. The planet Mercury is not in quite the right spot. You predict the existence of some other distorting planet. Turns out that doesn't exist.

• 42:04Speaker 01

  Actually, the reason Mercury is not in the right spot is because you need general relativity. And so you've sort of, you've pursued very similar ideas and it's been very successful in one case and it's been completely and utterly unsuccessful in the other case. And I think, I mean, a priori, you can't tell which of these is the thing to do and you actually need to do both.

• 42:22Dwarkesh Patel?

  Yeah.

• 42:23Speaker 01

  And so, I mean, this is certainly, it's very true in the history of science that, you know, this kind of diversity where you just have lots of people go off and pursue lots of potentially promising ideas, you just need to support that for a long time. And it's, I mean, it's hard to do that for a variety of reasons, but it does seem to be, to be very, very, very important.

• 42:46Dwarkesh Patel?

  So this example of Uranus versus Mercury is very interesting.

• 42:53Speaker 01

  Yeah.

• 42:55Dwarkesh Patel?

  In one, I think it illustrates sort of the difficulty of falsificationism.

• 42:58Speaker 01

  Yeah.

• 42:59Dwarkesh Patel?

  Like, the orbit of Uranus is in some sense falsifying Newtonian mechanics, but then you say, you make some ancillary.

• 43:08Dwarkesh Patel?

  Prediction that says, oh, the reason this is happening is there must be another planet, which is affected perturbing Uranus's orbit. And you, I think it's Leverrier in 1846. Point a telescope in the right direction, you find Uranus.

• 43:20Speaker 01

  Neptune.

• 43:21Dwarkesh Patel?

  Oh, it's there, Neptune, yes. But with Mercury, yeah, it's observed that it's, the ellipse which forms this orbit is rotating 43 arc seconds more every century than Newtonian mechanics would imply. So people say that there must be a planet inside Mercury's orbit. They call it Vulcan. And point a telescope, it's not there. But if you're a proper Newtonian, what you do is say, well, maybe there's some cosmic dust that's occluding this planet. Or maybe the planet is so small, we can't see it. Or maybe there's some, let's build an even more powerful telescope, oh, maybe there's some magnetic field which is sort of occluding our measurements.

• 43:56Speaker 01

  And this happens over and over, right? Like, you know, there's just so many stories which are exactly like this.

• 44:01Dwarkesh Patel?

  Right.

• 44:02Speaker 01

  I mean, an example I love from, you know, in the 1990s, some people noticed that the pioneer spacecraft weren't quite where they were supposed to be. And so, you know, you can get very excited about this. Oh, my goodness, general relativity is wrong. We have like, you know, maybe we're going to discover the next, the next theory of gravity. And today, the accepted explanation is that, no, actually, there's just a slight asymmetry in the, in the spacecraft. It turns out that the, you know, the thermal radiation is like slightly larger in one direction than the other, and that's causing a tiny little acceleration towards the sun. And most of the time, when there's these apparent exceptions, it's just something like that's going on.

• 44:45Speaker 01

  It's very much like the Vulcan, the Mercury Vulcan case. But every once in a while, it's, it's not. And a priori, you can't, you can't distinguish these. But I mean, science is just, just full of these. It's funny, too, like, the way we tell the history of science, it sounds so simple. Like, oh, you just focus on the right exception, and, you know, you realize that you need to throw out the old theory.

• 45:09Dwarkesh Patel?

  Right.

• 45:10Speaker 01

  And, and lo and behold, you know, your Nobel Prize awaits. But in fact, there's, these exceptions are all over the place.

• 45:17Dwarkesh Patel?

  Yeah.

• 45:18Speaker 01

  99.9% of the time, it just turns out to be some effect like this thermal acceleration in the case of the Pionier spacecraft. So unfortunately, there's a lot of selection bias going into those stories.

• 45:31Dwarkesh Patel?

  And the thing is, there's no ex-ante heuristic, which tells you which case you're in. And just to spell out why I think this is important is because some people have this idea that AI is going to make disproportionate progress towards science because it makes disproportionate progress towards domains where there's tight verification loops. And so it's really good at coding because you can run unit tests. And science may be similar because you can run experiments. And I think what that doesn't appreciate, one, is that experiments actually don't, there's an infinite number of theories that are compatible with any given experiment. And over time, why we glob onto the, well, at least in retrospect, we think is a more correct one is, as we're discussing in this conversation, sort of hard to articulate.

• 46:14Dwarkesh Patel?

  Lachatos actually has all kinds of interesting examples in the book about these kinds of hostile verification loops that are extremely long-lasting. So one he talks about is Prout or Prout, I don't know how to pronounce it, but there's this chemist in 1815, he hypothesizes that all atomic nuclei must have whole number weights, and they're basically all made of hydrogen. And the reason he thinks this is because if you look at the measure rates of all elements, it does seem that almost all of them do happen to have whole number rates, but then there's some exceptions. Like for example, chlorine comes out of 35.5. And so then there's all these ad hoc theories that people in this school keep coming up with, like, oh, maybe there's chemical impurities.

• 46:58Dwarkesh Patel?

  But then there's no chemical reaction you can do which seems to get rid of this. Maybe it's fractions of whole number, so it's 35.5, it can be halves. But actually, if you measure chlorine even closer, it's 35.46, so it's actually getting further away from the correct correction. And later on, what is discovered is what you're actually measuring is different isotopes, which cannot be chemically distinguished, they can only be physically distinguished. But so then you just have 85 years before we realize what an isotop is, where the verification loop is actually actively hostile against you, against the correct theory, and you just need this remnant to be defending. There's no ex-ante reason it's the preferred theory, just as a community, we should just have people defend, try to integrate new observations, even if they don't seem to fit their school of thought with what they believe. And hopefully, if enough of that happens.

• 47:45Dwarkesh Patel?

  Anyways, yeah, I guess the thing I'm trying to articulate is the difficulty with automating science.

• 47:50Speaker 01

  Yeah, I mean, the question is, where is the bottleneck at some level? And sort of, you know, are we primarily bottlenecked on one thing or one type of thing? Or are we bottlenecked on sort of multiple types of thing?

• 48:03Speaker 01

  So, you know, certainly talking to structural biology people, they seem to think that AlphaFold was an enormous advance. It was a shock. So at some level, yes, AI can, you know, it seems certain it can help us speed up science. So it is, it is helping with a certain type of bottleneck.

• 48:21Dwarkesh Patel?

  Yeah.

• 48:22Speaker 01

  That doesn't mean, though, as you're saying, that it's necessarily going to help with all kinds of bottlenecks. And sort of, I suppose the question you're pointing out is like, what are the types of bottlenecks that remain? And what are the prospects for, for getting past them? I think even in the case of coding, like, it's really interesting. You know, talking to programmer friends, at the moment, they're all in this state of shock and high excitement. And they're all over the place, actually, kind of talking to them.

• 48:50Speaker 01

  You do wonder, like, where is the bottleneck going to move to? So certainly, one thing that a lot of them seem to be bottlenecked on is now having interesting ideas and in particular, having interesting design ideas.

• 49:02Speaker 01

  So there's not really a verification loop for knowing, oh, that design idea is, you know, is very interesting. So, so they're no longer nearly as bottlenecked by their ability to produce code, but they are still bottlenecked by this other, by this other thing. They always were, they were, formerly, they weren't bottlenecked on it because, you know, just writing code was, took so much of their time. They could sort of have lots of ideas while they were, you know, they'd take their three weeks to implement their prototype and then they would implement the next version. You know, they're taking three hours to implement the, the prototype and they don't have, you know, as good ideas sort of after that from a design point of view.

• 49:38Dwarkesh Patel?

  Last year, I predicted that by 2028, AI would be able to prep my taxes about as well as a competent general manager. But we're already getting pretty close. As I've shared before, I use Mercury both for my business and my personal banking. So I recently gave an LLM access to my transaction history across both accounts through Mercury's MCP. I asked it to go through all my 2025 transactions and flag any personal expenses that seem like they should actually be charged to the business. And this worked shockingly well. Mercury's MCP exposes a bunch of detailed information, things like notes and memos and any JPEGs of receipts and PDF attachments. So my LLM had plenty of context to work with. One of my favorite examples happened with a charge to Bay Patel. If you looked at the vendor alone,

• 50:22Dwarkesh Patel?

  you would have had to assume that it's a personal expense. But the LLM looked at the receipt and the attached note in Mercury and realized it was actually a team bonding exercise from our last in-person retreat. So a legitimate business expense. I imagine it will be a while before traditional banks have MCP. Functionality like this is why I use Mercury. Go to mercury.com to learn more. Mercury is a fintech company, not an FDIC insured bank. Banking services provided through Choice Financial Group and Column NA, members FDIC. You have a very interesting take. I think it was a footnote when I know where your S is and I couldn't find it again, which was that it's very possible that if we met aliens, that they would have a totally different technological stack than us.

• 51:07Dwarkesh Patel?

  And that contradicts, I guess, a common sense assumption I had that I never questioned, which is that science is this thing you do relatively early on in the history of civilization, where you get to a point and you have a couple hundred years of just cranking through the basics, understanding how the universe works, et cetera. And you've got it. You've got science. And then basically, everybody would converge on the same quote-unquote "science." And so I found that a very interesting idea, and I want you to say more about it.

• 51:32Speaker 01

  Yeah. I mean, I think the... Probably the idea there that I'm at least somewhat attached to is

• 51:42Speaker 01

  the idea that the tech tree or the science and tech tree is probably much larger than we realize. I mean, we're sort of in this funny situation. People will sometimes talk about, you know, a theory of everything as a potential goal for physics. And then there's this presumption somehow that physics is done once you get there. And of course, this is not true at all. If you think about computer science,

• 52:09Speaker 01

  computer science basically got started in the 1930s when Turing and Church and so on just laid down what the theory of everything was. They just said, you know, here's how computation works. And then we've spent 90 odd years since then just exploring consequences of that and gradually building up more and more interesting ideas. And those ideas are, to some extent, you can just regard as technology. But to some extent, insofar as they're sort of discovered principles inside that theory of computation, I think they're best regarded as science and in some cases, very fundamental science. Ideas like public key cryptography are, I mean, they're just incredibly deep, very non-obvious ideas, which in some sense lay hidden already sort of in the 1930s.

• 52:54Speaker 01

  And so my expectation is that different, there will be different ways of exploring this tech tree. And we're still relatively low down. We're still at the point where we're just understanding these basic fundamental theories and we haven't yet explored them. Sort of a thing which I think is quite fun is if you look at just the phases of matter. When I was in school, we'd get taught that there are three phases of matter or sometimes four phases of matter or five phases of matter, depending a little bit on what you included. And then as an adult, as a physicist, you start to realize, oh, we've been adding

• 53:32Speaker 01

  to this list. We've got sort of superconductors and superfluids and maybe different types of superconductors and Bose-Einstein condensates and the quantum Hall systems and fractional quantum Hall systems and, and, and, and, and.

• 53:46Speaker 01

  And it's starting to turn out, it looks like actually there's a lot of phases of matter to discover. And we're going to discover a lot more of them. And in fact, we're going to be able to start to design them in some sense. I mean, we, you know, we'll still be subject to the laws of physics, but, but there is this sort of tremendous freedom in there. And this looks to me like, oh, we're down at sort of the bottom of the tech tree. We've barely gotten started there. And, and I expect that, you know, to be, to be the case sort of broadly, certainly in terms of, I think programming is a very natural place to look. The idea that we've discovered all the deep ideas in programming just seems to be sort of obviously ludicrous. You know, we keep discovering sort of what seems like deep new fundamental ideas.

• 54:30Speaker 01

  And, I mean, we're very limited. We're, we're basically slightly jumped up chimpanzees. So we don't, you know, we're, we're slow and it's, it's taking us time. But, but, you know, what, what do we look like sort of another million years in the future in terms of, you know, all of the different ideas which people have had around how to, how to manipulate computers, how to manipulate information? I, I think, you know, we're likely to discover that actually there are a lot of very deep ideas still to be, still to be discovered. So nice, who was it? I think it was Knuth in the preface to The Art of Computer Programming.

• 55:11Speaker 01

  So something like, you know, he started this book back in the sixties and he talked to a mathematician, it was a bit contemptuous, and said, look, computer science isn't really a thing yet. Come back to me when there's a thousand deep theorems. And Knuth remarks, and he's writing this now decades later, the, the preface, there are, there clearly are a thousand deep theorems now. And that, that means, like, it's really interesting to, to sort of think like, like, what's the, the long-term future? As you get higher and higher up in the, the tech tree, like, choices about which direction we go and sort of how we choose to explore, you know, I, I, I think it, it's potentially the case that we're, you know, different civilizations or different choices mean that

• 55:56Speaker 01

  we end up in different parts of, of that tree. And in particular, just things, I mean, it's sort of very basic things about. We're very visual creatures. Certain other animals are much more orally based. Does that bias the types of thoughts that you have? And then you extend it to much more exotic kinds of civilizations, where maybe just their biases in terms of how they perceive and how they manipulate the world are maybe quite different than ours. And that might make some significant changes in terms of how they do that exploration of the tech tree. It's all speculation, obviously.

• 56:39Dwarkesh Patel?

  No, this is such an interesting take. I want to better understand it. So one way to understand it is that there might be some things which are so fundamental and have such a wide collision area against reality that they're inevitably going to discover like general relativity.

• 56:52Speaker 01

  Numbers, numbers.

• 56:52Dwarkesh Patel?

  Yeah, yeah.

• 56:53Speaker 01

  Like of all of the intelligences in the Milky Way galaxy, maybe that number is one. Actually, arguably, we've already increased the number. But of all of those, what fraction have the concept of counting? And it does seem very natural. What fraction have discovered the idea of some kind of decimal place system? Interesting question. And maybe we're missing something really simple and obvious that's actually way better than that. What fraction got there immediately? What fraction had to go through some other intermediate state? What fraction use linear representations versus, say,

• 57:38Speaker 01

  I don't know, a two-dimensional or a three-dimensional representation? I think the answers to these questions are just not at all obvious. It's a lot of design freedom.

• 57:45Dwarkesh Patel?

  On theoretical computer science, this is going to be extremely naive and arrogant. But I took Scott Ernst's class on complexity theory, and I was by far the worst student he's ever had. But what I remember is like... There was this period that you were, you know, you were one of the pioneers of where we figured out here's, here's the class of problems that quantum computers can solve and how it relates to problems a class of computers always like groundbreaking, oh crazy, this works. And then since then, it's been this, literally it's called Complexity Zoo, this website, which lists out here's all the complexity classes. And if you have this complexity class with this kind of oracle, it's sort of equivalent to this other class.

• 58:30Dwarkesh Patel?

  And that, it feels like we're building out that taxonomy.

• 58:33Speaker 01

  Yeah.

• 58:34Dwarkesh Patel?

  And so there's a couple of ways to understand what you're saying. One, maybe you just disagree with me that this is actually what's happened with this field. Another is that while that might happen to any one field, the amount of fields, who would have thought in 1880, the computer science, other than Babbage or something, the computer science was going to be a thing in the first place. So the amount of field, we're underestimating how many more fields there could be.

• 58:51Speaker 01

  Yeah, for sure.

• 58:52Dwarkesh Patel?

  Or maybe you think both, or maybe a third secret thing, but I'd be curious.

• 58:56Speaker 01

  I mean, a very common argument here is sort of the low hanging fruit argument, the argument that says, oh, there should be diminishing returns.

• 59:06Dwarkesh Patel?

  And in fact, empirically, we see this, right? The amount of scientists in the world is just exponentially increased.

• 59:11Speaker 01

  And, and, I mean, I think it's, you know, it's worth thinking about, like, why, why do you expect diminishing returns? And how well does that argument actually apply in practice? An analogy I like is actually thinking about sort of, you know, going to some event, going to a wedding or whatever, and you go to the dessert buffet. And they've put out, you know, 30 desserts. And of course, naturally, what people do, right? The best desserts go first. I mean, we don't quite have a well-ordered preference there, so maybe there's some difference. But, but human beings are fairly similar, so they will, they, you know, the best desserts will go first. And this is an argument, you know, for why you expect diminishing returns in a lot of different.

• 59:56Speaker 01

  Fields, if it's relatively easy to see what's available and people have similar preferences, then the best stuff goes first and it just gets sort of worse and worse after that. And a very static snapshot in time of scientific progress, maybe there's some truth to that. But if somebody is standing behind the dessert table and is replenishing, restocking the desserts and keeps kind of adding new ones in, it may turn out that a little bit later, much better desserts appear and so you're going to go and eat those instead. And scientific progress has a little bit of that flavour. We go through these sort of funny time periods.

• 1:00:38Speaker 01

  Computer science is a great example, where computer science basically arose as sort of a side effect of some pretty abstruse questions in the philosophy of mathematics and logic. And so you've got these people trying to attack these rather esoteric questions that seem quite high up in some sense in exploration, quite esoteric. And they discover this fundamental new field and all of a sudden there's an explosion there. So the diminishing returns argument just didn't apply there. We just weren't able to see what was there. And this has been the case over and over and over again. Sort of new fields arrive and all of a sudden, boom, it's actually easy to make progress

• 1:01:23Speaker 01

  again. Young people flood in because you can be 21 and make major breakthroughs rather than having to spend 25 years mastering everything that's been done before. It's obviously very attractive. And I don't understand, I'm not sure anybody understands very well, sort of the dynamics of that, like how to think about why the structure of knowledge is that way, that these new fields keep opening up. But it does seem empirically at least to be the case.

• 1:01:53Dwarkesh Patel?

  Despite the fact that that is the case. Take deep learning, right? Obviously, this is an example of a new field where the 21-year-olds can make progress. And it's relatively new, 15 years or so, when it sort of gets back into high gear. But already, we're in a stage where you need billions, or tens of billions, or hundreds of billions of dollars to keep making progress at the frontier.

• 1:02:22Speaker 01

  Yeah.

• 1:02:22Dwarkesh Patel?

  And there's a couple of ways to understand that. One is that it actually is harder than the kinds of things the ancients had to do, or requires more, is more intensive at least. Second is, it might not have been, but because our civilizational resources are so large, the amount of people is so large, the amount of money is so large, that we can basically make the kind of progress that would have taken the ancients forever to make. Almost immediately, we just, we notice something is productive, immediately dump in all the resources. But it's also weird that there's not that many of them. Like, I feel like deep learning is notable because it is one big exception to the fact that it's hard to think of other examples.

• 1:02:58Speaker 01

  I mean, it's a consequence of sort of, you know, the architecture of attention, right? Like, at any given time, there's always a sort of a most successful thing. Yeah, maybe if, if deep learning wasn't a thing, maybe you'd be talking about CRISPR. Maybe you'd be talking about, you know, whatever it is. Maybe, you know, maybe we wouldn't think about solving sort of the protein structure prediction problem as a, really a success of AI. Maybe we would have figured out how to doing it with sort of curve-fitting, like, you know, more broadly construed, and we'd just be like, oh, wow, like, we took a lot of computing resources, but, but protein structure prediction might, you know, be an enormously important thing. So there is always sort of a biggest thing, and, and I think what you're pointing at

• 1:03:42Speaker 01

  is more a consequence of, of the way in which attention gets centralized.

• 1:03:46Dwarkesh Patel?

  Yeah.

• 1:03:47Speaker 01

  It's basically fashion, is sort of what I'm saying. It's not just fashion, but, but there is some dynamic there.

• 1:03:52Dwarkesh Patel?

  There's a very interesting and important implication of this idea, that the branching is so wide, and so contingent, and so path-dependent, that different civilizations stumble on entirely different technology stacks.

• 1:04:08Speaker 01

  Yeah.

• 1:04:08Dwarkesh Patel?

  There's a very interesting implication that there will, there will be gains from trade.

• 1:04:12Speaker 01

  Yeah.

• 1:04:12Dwarkesh Patel?

  Into the far, far future.

• 1:04:13Speaker 01

  Yeah, that's interesting.

• 1:04:14Dwarkesh Patel?

  Which might actually be one of the most important facts about the far future, in terms of how civilizations are set up, how they can coordinate. How they interface with like, there's not this like go forth and exploit. It's actually there are humongous gains to trade from adjacent colonies or whatever.

• 1:04:30Speaker 01

  That, yeah, sort of. There's a question of like, what's actually hard? You know, if it's a question of if it's just the ideas, well, those spread relatively quickly. It's relatively easy to to share ideas. If it's something more, it's almost sort of a Dan Wang kind of an idea where it's it's actually sort of, there's some notion of capacity. You need all the right texts. You need all of the right manufacturing capacity and so on. And so, you know, Civilization A has very different kind of manufacturing capacity. And it's just not so easy to build in Civilization B, even if Civilization B is kind of ahead. Then then I think that that becomes true. There is actually, you know, comparative advantage, which is really worth.

• 1:05:14Speaker 01

  I mean, it's going to provide massive benefits to trade in both directions. Eventually, you're going to expect some diffusion of of innovation. It is funny, like to think about what the barriers are there. A fun thought experiment I like to think about is sort of GitHub but for aliens. So, you know, somebody presents you with all of the code from some alien civilization. And I mean, I don't even know what what code means there, but this sort of their specification of algorithms. And and it's so interesting, like it would have many interesting new ideas in there. And it would take forever for human beings to dig through and to try and extract all of those.

• 1:05:55Speaker 01

  The one reason, I mean, the the origin of this for me was actually thinking about proteins in in in nature. Yeah, we've been gifted just this incredible variety of machines, which we don't understand really at all. And we just have to go and sort of try and understand them on a, you know, one by one basis. We're still understanding hemoglobin and insulin and things like this. And no doubt, you know, and there's hundreds of millions of proteins known. So it is it is a little bit like that. We've been gifted by biology, just this immense library.

• 1:06:32Speaker 01

  Of of machines, no doubt containing an enormous number of very interesting ideas. And we're just at the very, very, very beginning of understanding it. So actually, I mean, that's, that's, I suppose, kind of your point, actually, is, is, you know, I need to relabel your argument slightly, but you sort of think of that as as a gift from an alien civilization, which obviously it isn't, but you think of it that way. And it's like, oh, my goodness, like, there's so much in there and we're going to study it. And goodness knows how long we could continue to study it. There's tens of thousands of papers about the, you know, hemoglobin and things like that, and we still don't understand them. And yet we're getting so much out of it. Just, I mean, just think about insulin alone.

• 1:07:15Speaker 01

  You know, it's such an important, such an important thing.

• 1:07:18Dwarkesh Patel?

  That's, that's an incredibly useful intuition pump that you have on Earth. I had Mick Lane on where he had a theory about how life emerged, but like, whatever theory you have, basically something like DNA, four billion years, and you have an alien civilization come here and be like, there's all these interesting things to learn about material science, about, you name it, right? Like about.

• 1:07:44Speaker 01

  Think about chinesen walking along, like, I mean, and we know almost nothing about these proteins, and yet the tiny few facts we do know are just, just incredible. The ribosome.

• 1:07:53Dwarkesh Patel?

  Yeah.

• 1:07:53Speaker 01

  You know, another example, I mean, this miraculous engineer, sort of device, little factory.

• 1:08:01Dwarkesh Patel?

  And all seeded by just like, there's this particular chemistry on Earth with nucleic acids and carbon based light forms that that chemistry gives rise to all of these interesting things which an alien civilization would find very interesting. And so that, that very, that seed, which must be one among, you know, trillions of possible seeds of, I mean, just of general intellectual ideas, leads to all this fecundity. That's a very interesting intuition pump. I want to meditate on this gains for trade thing because I feel like, I think there's something actually very interesting about this idea, that if you have this vision of what, how technology progresses and how it may be different from in different civilizations, it has important implications about how different civilizations might interact with each other. Like the fact that there are going to be these huge gains from trade.

• 1:08:46Speaker 01

  It makes friendliness much more rewarding.

• 1:08:48Dwarkesh Patel?

  Yes, yeah. That's a very important observation.

• 1:08:51Speaker 01

  Yeah, I hadn't thought about that at all. That is a very interesting observation.

• 1:08:58Speaker 01

  It is funny, I mean, comparative advantage is something that people, you know, they love to invoke, and it's a very beautiful idea, obviously. There are limits to it, like,

• 1:09:14Speaker 01

  you know, it's kind of, it's a special limited model. We don't, you know, chimpanzees can do interesting things. We don't trade with them.

• 1:09:26Speaker 01

  And I think it's sort of interesting to think about the reasons why. And part of it is just power, I think. Like, once there's a sufficiently large power imbalance,

• 1:09:38Speaker 01

  very often, not always, but very often, groups of people seem to to sort of shift into this other mode where they just seek to dominate. And, you know, maybe there's something special about human beings, but maybe it's also sort of a more general sort of a thing. They're not, they're no longer, they give up, you know, you need all these special things to be true before groups will trade.

• 1:09:59Dwarkesh Patel?

  Yeah.

• 1:10:01Speaker 01

  And, you know, it's not necessarily obvious.

• 1:10:05Dwarkesh Patel?

  Well, I think the big thing going on here is, one, transaction costs.

• 1:10:08Speaker 01

  Yeah.

• 1:10:09Dwarkesh Patel?

  And two, comparative advantage does not tell you that the terms on which the trade happens are above subsistence for any given one producer. So people often bring this up in the context of, well, humans will be employed even in post-AI world because of comparative advantage. There's big, there's like five different ways that argument breaks down, but the easiest ways to understand are, why don't we have horses all around on the roads? Because there's some comparative advantage between cars and horses.

• 1:10:37Speaker 01

  Good example.

• 1:10:38Dwarkesh Patel?

  Well, there's, one, there's huge transaction costs to building roads that are compatible with horses and cars at the same time. In a similar way, AI is sort of thinking at 1,000 times the speed and can sort of shoot their latent states again at each other, are going to find it way more costly than the benefit in just in terms of interacting with you to have a human being in the supply chain. And second, that, just because there's, horses have a comparative advantage.

• 1:11:08Dwarkesh Patel?

  Mathematically, does not mean that it is worth paying 100K a year or whatever it costs to sustain a horse in San Francisco.

• 1:11:18Dwarkesh Patel?

  That subsistence is going to be worth the benefit you get out of the horse.

• 1:11:20Speaker 01

  I do think it's interesting, like, that just the sheer fact that,

• 1:11:26Speaker 01

  my expectation and my intuition obviously differs a great deal from yours on this, is that most parts of the tech tree are never going to be explored. There's just too many interesting ways of combining things. There's too many sort of deep ideas waiting to be discovered. And we're, you know, not only we, but nobody ever is going to discover most of them. So choices about how to make, how to do the exploration actually matter quite a bit.

• 1:11:51Dwarkesh Patel?

  Interesting.

• 1:11:52Speaker 01

  It's something I really dislike about sort of technological determinist arguments. I'm willing to buy it sort of low enough down when, you know, progress is relatively simple. But, but higher up, you start to get to shape the way in which you do the exploration. And it's interesting, you know, people, we are starting to shape it in, in, in interesting ways. You know, sort of, I mean, there's various technologies that have been essentially banned. Think about DDT, you think about chlorofluorocarbons, you think about restrictions on the use of nuclear weapons, the Nuclear Nonproliferation Treaty. Those kinds of things are, you know, they're not, they weren't done before the fact. But they're, you know, starting to get pretty close in some cases

• 1:12:37Speaker 01

  where we just sort of preemptively decide, oh, we're not going to go down that path.

• 1:12:43Speaker 01

  So that starts to look like a set of institutions which, where we are actually influencing sort of how we, how we explore the tech tree.

• 1:12:51Dwarkesh Patel?

  Yeah. On where you would see these gains from trade, obviously it would be, you'd see the most where it's pure information that can be sent back and forth because the information has this quality where it is expensive to produce, but cheap to verify and cheap to send.

• 1:13:04Speaker 01

  Yep.

• 1:13:06Dwarkesh Patel?

  And so it'll be interesting how much of future productivity or whatever can be distilled down to information. Right now, it's kind of hard to do because you can't really transfer. Like, if China is really good at manufacturing something, well, there's this process knowledge that's in the heads of 100 million people involved in manufacturing sector in China. But in the future, it might be easier if AIs are doing.

• 1:13:25Speaker 01

  I mean, the question about sort of to what extent does our fabrication get sort of very uniform and get really commoditized? Like, 3D printers have been the next big thing for at least 20 years now.

• 1:13:38Dwarkesh Patel?

  Yeah.

• 1:13:39Speaker 01

  Why do they still not work all that well? Why are they still not actually at the center of manufacturing? And sort of what comes after that? It is funny to look at, say, the ribosome by contrast. It really is at the center of biology in a whole lot of really interesting ways.

• 1:13:55Speaker 01

  And whether or not that's the future of manufacturing is something very simple, sort of where everything goes as throughput through, I don't know, maybe it's a bioreactor or something like that. So you send the information and then you grow stuff. Or you have some 3D printer that actually works. And if they're good enough, then actually it does become much more a pure information problem, and some of this process knowledge becomes much less important.

• 1:14:23Dwarkesh Patel?

  Jane Street has a lot of compute, but GPUs are very expensive. And so even optimizations that have a relatively small effect on GPU utilization are still extremely valuable. Two of Jane Street's ML engineers, Corwin and Sylvan, walked through some of their optimization workflows at GTC.

• 1:14:39Speaker 02

  You're not bottlenecked on the network being too slow. You're bottlenecked on waiting for a different rank in your training, not having completed the work.

• 1:14:47Dwarkesh Patel?

  They talked about how Jane Street profiles traces and diagnoses bottlenecks, and then how they solve them using techniques like CUDA graphs and CUDA streams and custom kernels. With these sorts of optimizations, Corwin and Sylvan were able to get their training steps down from 400 milliseconds to 375 milliseconds each. This 25-millisecond difference might sound small, but given the size of Jane Street's fleet, that improvement could free up thousands of B200s. Jane Street open sourced all the relevant code. If you want to check it out, I've linked the GitHub repo and the talk in the description below. And if you find this stuff exciting, Jane Street is hiring researchers and engineers. Go to janestreet.com/thoarkash to learn more. Can I ask a very clumsily phrased question? So there's

• 1:15:30Dwarkesh Patel?

  There's these deep principles that we've discovered a couple of. One is this idea that, hey, if there's a symmetry across a dimension, it corresponds to a conserved quantity. It's a very deep idea. There's another, which you've written a lot about, written a textbook about, in fact. About, there's, we, there's ways to understand this thing of what kinds of things you can compute, what kinds of physical systems you can understand with other physical systems, what a universal computer looks like, et cetera. And is your view that if you go down to this level of idea of Noether's theorem or the Church-Turing principle, that there's an infinite number of extremely deep such principles? Because I feel like what makes them special is that they themselves encompass

• 1:16:14Dwarkesh Patel?

  so many different possible ways the world could be, but no, it has, the world has to be compatible with actually a couple of these very deep principles.

• 1:16:23Speaker 01

  I don't know. I mean, yeah, I just, all I have here is speculation and sort of instinct. My instinct is we keep, we keep finding very fundamental new things. It was very, I mean, for me, anyway, quite informative to understand, as I say, you know, I gave the example before, there's these wonderful ideas of Church and Turing and these other people, ideas about universal programmable devices. And then you understand later, oh, this also contains within it the ideas of public key cryptography. And then you understand later, oh, that also contains within it the ideas, I mean, people refer to it as cryptocurrency or whatever, but there's a very deep set of ideas there about the ability to collectively maintain an agreed-upon ledger, which are built, which is built upon this.

• 1:17:06Speaker 01

  And there's probably, you know, many deep ideas to sort of, it actually took, whatever, it's taken many years, really, to figure out the right canonical form of those. And so just this fact that you, you keep finding what seem like deep new fundamental primitives, I find very, for me, that's a, has been a very important intuition bump. And it's a cross. I mean, I've given that particular example, but I think you see that same pattern in a lot of different areas.

• 1:17:37Dwarkesh Patel?

  What is your interpretation then of this empirical phenomenon where ideas, like whatever input you consider into the scientific process or technological process, economists have studied this a million and a hundred ways. It just seems to require, even at actually very consistent rate, X percent more researchers per year. So there's this famous paper from a couple of years ago by Nicholas Bloom and others, where they say, how many people are working in the semiconductor industry? And how does it increase over time?

• 1:18:04Speaker 01

  Yeah.

• 1:18:05Dwarkesh Patel?

  Through the history of Moore's law. And I think they find like, Moore's law means computing increases 40% a year, or transistor density increases 40% a year. But to keep that going, the amount of scientists has increased 9% a year.

• 1:18:17Speaker 01

  Something like that, yeah.

• 1:18:18Dwarkesh Patel?

  And they go through industry after industry with this observation. And so is your view that there are these deep ideas, but they keep getting harder to find? Or that, no, there's another way to think about what's happening with these empirical observations?

• 1:18:31Speaker 01

  I mean, they're, so first of all, all of their examples are narrow, right? They all, they pick a particular thing, and then they look at some particular metric. You know, nowhere in that shows up, like GPUs don't show up there.

• 1:18:45Dwarkesh Patel?

  Yeah.

• 1:18:46Speaker 01

  Right? Like in the sense of, oh, yeah, all of a sudden you get this ability to parallelize. And that's really interesting. So there's sort of a lot of external consequences that are just delighted from, basically, you know, they have these simple quantitative measures, they look at it in agricultural productivity, they look at it in a whole lot of different ways. But you do have to focus narrowly. And I suppose, you know, I'm certainly interested, as I say, in this, this fact that, that just new types of progress.

• 1:19:19Dwarkesh Patel?

  Yeah.

• 1:19:19Speaker 01

  Keep becoming possible. But, you know, there is still, I think, even there, there does seem to be some phenomenon of diminishing returns.

• 1:19:33Speaker 01

  Is that intrinsic? Is that something about the structure of the world? What is it? Well, one thing which hasn't changed that much is the individual minds which are doing this kind of work. And maybe those should be being improved as well.

• 1:19:48Speaker 01

  Or some sort of feedback process going on there.

• 1:19:53Speaker 01

  And maybe that changes the nature of things. I suppose I I look at scientific progress up into, let's say, 1700, something like that. And it was very slow and also it was very irregular. You had the Ionians back sort of five centuries before Christ doing these quite remarkable things. And so much knowledge would get lost and then it would be rediscovered and then it would be lost again. And you'd have to say that progress was very slow. And there, it's partially just bound up with the fact that there were some very good ideas that we just didn't have. Even once you've had the ideas, then you need to build institutions around them.

• 1:20:35Speaker 01

  You actually need to solve a whole lot of different problems about training, about allocation of capital, about all these kinds of things. Even just about basic sort of security for researchers. So they're not worried about the Inquisition or things like that. So there's all these kind of complicated problems. You solve all those complicated problems and then all of a sudden, boom, there's a massive burst of scientific progress. If you're not changing it, if there's some kind of stagnation there, if you're not changing those external circumstances, yes. Like you may start to get diminishing returns again. But that doesn't mean there's anything intrinsic about the situation.

• 1:21:10Speaker 01

  Maybe something just external needs to change again. Obviously, a lot of people think AI is potentially going to be a driver. I mean, it certainly will at some level. In fact, to the extent you can think of a lot of modern scientific instrumentation as really I mean, at some level, kind of robots. What is the James Webb Space Telescope? Well, it's unconventional maybe to describe it as a robot, but it's not completely unreasonable either.

• 1:21:41Speaker 01

  It is an example of a highly automated, very sophisticated system with electronically mediated sensors and actuators, where machine learning in fact is being used to process the data. So in that sense, we're already starting to see that transition. We've been seeing it for decades.

• 1:22:01Dwarkesh Patel?

  I have this smoke a joint and take a puff thought.

• 1:22:03Speaker 01

  I think we've had a few.

• 1:22:05Dwarkesh Patel?

  Yeah, yeah. Well, I think we're going to do that part of the conversation and then you can help me get my foot out of my mouth and figure out more concrete to think about it. So, to your point that AI, there's an industrial revolution, the Enlightenment, and now there's AI, and each might be a different pace or a different way in which science happens. If you think about the pace of how fast such transitions have been happening, you can draw over the long span of human history this hyperbolic of the rate of growth is increasing. So, yeah, 100,000 years ago, you have the Stone Age. You go back even much further, how long have primates been around? It would be like, let's say, millions of years, and 100,000 years ago, the Stone Age.

• 1:22:49Dwarkesh Patel?

  Then 10,000 years ago, the agricultural revolution. Then 300 years ago, the industrial revolution, each marked by this exponential, this increase in the rate of exponential growth. And then people think it's going to happen again with AI. But that would happen potentially even faster. It would not have occurred to somebody at the beginning of the industrial revolution that the next demarcation in this trend will be artificial intelligence.

• 1:23:17Dwarkesh Patel?

  And so if things are getting faster, and it would be hard to anticipate what the next transition will be, I guess we just think of this singularity between now and AI, and that's really what distinguishes the past from the future. But just applying the same heuristic that many people in the past should have had,

• 1:23:36Dwarkesh Patel?

  maybe the intelligence age is also quite short. And the next thing after that is, we don't even have the ontology to describe what it is, but it would not, the future will not think of the past as like, there was pre-intelligent AI and post-AI.

• 1:23:50Speaker 01

  No, that seems... I mean, obviously, we can't prove this, but it certainly seems quite plausible. I mean, part of the issue, of course, is just, you know, the substrate we have available to conceive like seems all wrong. You can't speculate with a bunch of chimpanzees about what it would be like to have language. You know, just to sort of pick a major transition in the past. It's the transition itself is the thing.

• 1:24:21Dwarkesh Patel?

  Right.

• 1:24:23Speaker 01

  And it seems likely. If we're talking about taking a puff kind of thoughts, you know, I'm certainly amused by the idea that there's going to be some transition involving artificial general intelligence using classical computers. But actually, there'll be an interesting transition with quantum computers as well. They're probably capable of a strictly larger class of potentially interesting computations. So maybe actually the character of sort of AQGI or whatever it should be called is actually qualitatively different. So maybe there's sort of a brief period between those two things.

• 1:25:05Dwarkesh Patel?

  Interesting.

• 1:25:06Speaker 01

  I mean, as I say, you know, this is just speculation, but it's certainly amusing.

• 1:25:11Dwarkesh Patel?

  Is there a reason to think that? Because from what I understand, there's been, for decades, people like you have put pretty tight bounds on the kinds of things quantum computers can do. And so it'll speed up search somewhat. It will do. And the kinds of things it extremely speeds up, like Shor's algorithm, it seems like it. Again, maybe this is to your point that we can't predict in advance what's down the tech tree. But at least from here, it seems like you break encryption. But what else are you using? Shor's algorithm.

• 1:25:36Speaker 01

  Yeah, I mean, we've only been thinking about it for 30 years or whatever. It's 40 or so years, not for very long. And we sort of haven't, in some sense, thought that hard. About it as a civilization, so yeah. Does it turn out that it's very narrow? Maybe. Does it turn out that it's very broad? That's also like a really radical expansion. That seems distinctly possible. Like, keep in mind as well, we've been doing it without the benefit of having the devices.

• 1:26:05Dwarkesh Patel?

  Right.

• 1:26:06Speaker 01

  Right, like, that's a pretty big bottleneck to have.

• 1:26:10Dwarkesh Patel?

  If you're thinking about computer science in the 1700s and you're like, okay, and or.

• 1:26:13Speaker 01

  Yeah, yeah, yeah. What are you gonna do?

• 1:26:15Dwarkesh Patel?

  You can't anticipate Bitcoin, you can't anticipate Bitcoin.

• 1:26:18Speaker 01

  No, I mean, maybe you could if you're sufficiently bright, but it is a pretty hard situation. Right.

• 1:26:25Dwarkesh Patel?

  What is your inside view, having been in and contributing to quantum information, quantum computing back in the 90s and 2000s? What is your telling of the history? What was the bottleneck? What was the key transition that made it a real field? And how do you rank the contributions for Feynman, to Deutsch, to everybody else that came along?

• 1:26:51Speaker 01

  Yeah, so I mean, let's just focus on the question about what actually changed. So why was quantum computing not a thing in the 1950s? Right, like, it could have been.

• 1:27:01Dwarkesh Patel?

  Yeah.

• 1:27:04Speaker 01

  You know, somebody like, I don't know, John von Neumann, good example, absolutely pioneering computation, also wrote a very important book about quantum mechanics and was deeply interested in quantum mechanics. Like, he could have invented quantum computing at that time. And I think there were quite a number of people who potentially could have. So why do we have these papers by people like Feynman and Deutsch in the 80s? And those are, I think, fairly regarded as the foundation of the field. There are some partial anticipations a little bit earlier, but they were nowhere near as comprehensive and nowhere near as deep.

• 1:27:40Speaker 01

  And, well, you should, you should ask David. You can't ask, you can't ask Feynman unfortunately, but he'll know much better than I do. A couple of things that I think are interesting. One is that, of course, computation became far more salient sort of late seventies, early eighties.

• 1:27:58Speaker 01

  It just became a thing which many more people were interested in, partially for, you know, for very banal reasons. You could go and buy a PC, you could buy an Apple II, you could buy a Commodore 64, you could buy all these kinds of things. It became apparent to people that these were very powerful devices, very interesting to think about. At the same time, in the quantum case, that was also the time of the ball trap and the ability to trap single ions and so on. And up to that point, we hadn't really had the ability to manipulate single quantum states. So you've kind of got these two separate things that just for historically contingent reasons had both sort of matured around, let's say, 1980 or so. And somebody like von Dymen could have had the idea earlier,

• 1:28:44Speaker 01

  but it is, I think, quite an interesting, you know, fact. A story about Richard Feynman, he went and got one of the first PCs, which was around 1980, 1981. And he was apparently just so excited with this device. He actually tripped and hurt himself quite badly, sort of carrying his brand new computing device.

• 1:29:15Speaker 01

  You know, that's a very historically contingent sort of a coincidence. But having somebody who's very, very talented and understanding of quantum mechanics, also just very excited about these new machines.

• 1:29:32Speaker 01

  It's not so surprising perhaps that he's thinking then. What similar story could you have told 10 years earlier? Like, there is just no, the conditions don't exist for it. So I think that's, I mean, it's quite a banal story, but.

• 1:29:46Dwarkesh Patel?

  One of the things we were going to discuss was this idea you had about the market for follow-ups. And I think this is actually the perfect story to discuss it for, because you wrote the textbook about the field, right? You. Mike and Ike is the definitive textbook on quantum information. And so you presumably came in after Deutsch.

• 1:30:09Speaker 01

  Yeah.

• 1:30:09Dwarkesh Patel?

  But you identified, in the 90s somehow identified it as the thing that is worth following up on and building on. And instead of talking about it more abstractly, I'd love to actually just hear the story of, like the firsthand story of how did you know that this is a thing to, of all the things that were happening, physics and computing, et cetera, that I want to think about this problem?

• 1:30:28Speaker 01

  Sure, sure. So, yeah, Reid Feynman writes this great paper in 1982, David Deutsch writes an absolutely fantastic paper in 1985, sort of sketching out a lot of the fundamental ideas of quantum computing. So I'm, you know, I'm 11 in 1985, I'm not thinking about this, I'm playing soccer and doing whatever. But in 1992, I took a class on quantum mechanics that was really terrific, given by Jared Milburn. And I just went and asked Jared one day after, like the fifth lecture or something, I said, do you, like, do you have anything, you know, sort of papers or whatever that you could give me? And he said, come by my office in a couple of days' time.

• 1:31:12Speaker 01

  And I did, and he presented me with a giant stack of papers, which included the Deutsch paper, it included the Feynman paper, and it included a whole bunch of other, sort of, very fundamental papers about quantum computing and quantum information, at a time when essentially nobody in the world was working on it. He was. He'd actually, I think he wrote the very first paper that proposed, I mean, sort of a practical approach to quantum computing. Wasn't very practical, but it was actually in a real, in a real system. And so, in some sense, you know, I'm benefiting from the taste of this other person, but as soon as I read the papers, or take a look at the papers, like, these are exciting papers.

• 1:31:56Speaker 01

  You know, they're asking very fundamental questions, and you're sort of like, oh, I can make progress here. Like, these are, these are things that one could potentially work on. Deutsch has this Sort of conjecture that basically, yeah, there should be, I don't know what the right term for it is, thesis or what you would call it, that a universal model quantum curing machine should be capable of efficiently simulating any system, any physical system at all. This is a very provocative idea. I think in that paper, he more or less claims that he's proved it. I'm not sure that necessarily everybody would agree with that. There's questions

• 1:32:40Speaker 01

  about whether or not you can simulate quantum field theory effectively. And that kind of question is, I think, very interesting and very exciting there. It's obviously a fundamental question about the universe. You have some wonderful ideas in there about sort of quantum algorithms and where they come from and what they mean and what they relate to the meaning of the wave function and questions like this, which is still not, it's not agreed upon amongst physicists. So, yeah, there's just some sense of, oh, I am in contact with something which is A, deeply important, and B, we as a civilization don't have this. And so, of

• 1:33:24Speaker 01

  course, you start to focus your attention a little bit there.

• 1:33:27Dwarkesh Patel?

  I'm not sure I got the answer to the question that...

• 1:33:34Speaker 01

  Maybe I misunderstood the question.

• 1:33:36Dwarkesh Patel?

  Yeah, let me think about how to phrase it. Maybe I'll explain the motivation first. So, in a previous conversation, we were discussing, how could you have known in the 1940s the Shannon Theorem? And Shannon's way of thinking about communication channel is a deep idea that goes beyond the problems with pulse code modulation that Bell Labs was trying to solve at the time, and it applies to everything from quantum mechanics to genetics to computer science, obviously. And one of the, I think, an idea you stated that we didn't get a chance to talk about yet was this idea, well... Shannon publishes a paper, there's all these other papers,

• 1:34:19Dwarkesh Patel?

  but there's some market of follow-ups where people gravitate to and build upon Shannon's work. And how did they realize that that's the thing to do? And how does that process happen? And so I guess you gave your local answer. You read these papers and you immediately realized, okay, there's work to be done here. There's a low-hanging fruit. There's some deep provocative idea that I need to better understand. And I could attractively make progress on.

• 1:34:44Speaker 01

  Yeah, I mean, so, you know, to some extent, you're sort of saying, okay, I wanted to get into this game of contributing to humanity's sort of, understanding of the universe. And you are applying sort of this low-hanging fruit algorithm. You're like, relative to my particular set of interests and abilities, where should I pick up my shovel and start digging? And there it was like, oh, this looks like quite a good place to start digging.

• 1:35:16Speaker 01

  You know, and different people, of course, chose very differently. It was a very unusual choice at the time. This was 1992.

• 1:35:26Speaker 01

  Very few people were thinking about that.

• 1:35:28Dwarkesh Patel?

  Yeah. Fast forwarding a bit, so you've been, I don't know how you think about your work on the open science movement now. But did it work? Like, what would have, what a success there would look like? Or what is it that that movement is trying to accomplish?

• 1:35:44Speaker 01

  Yeah, I mean, the set of ideas about open science. I mean, it's interesting. You didn't stop and define open science there, which I think 20 years ago you would have had to do. People recognize the phrase. People have some set of associations with it. Most often, they have a relatively simple set of associations. It means maybe something about making scientific papers open access. Very often, they have some set of notions about maybe it means also making code openly available. Maybe it means making data openly available. But already. Those are, I think, very large successors of the open science movement,

• 1:36:26Speaker 01

  which is to make those salient issues, those are issues on which people have opinions. And then there are relatively common arguments, an argument like, so this is sort of the meme version, you know, publicly funded science should be open science. That's a distillation of a set of ideas which you might be able to contest. But if you can get people actually sort of thinking about it and engaged with that kind of argument, that's a very fundamental, kind of an issue to be considering in the whole political economy of science. If you go back, say, three centuries, there was a very similar kind of an argument prosecuted,

• 1:37:09Speaker 01

  which is the question, do we publicly disclose our scientific results or not? So if you look at people like Galileo and Kepler and so on, the extent to which they publicly disclosed, like it was done in a very odd kind of a way. They sometimes they did bizarre things where famously they published some of their results as some anagrams. So basically, you know, they'd find some discovery, they would write down the result in sort of a sentence, like here's, you know, the discovery of the, I'm trying to think of an example, I think the moons of Mars, I think was one such example. I'm getting it wrong, was it Hooke's law?

• 1:37:54Speaker 01

  Anyway, doesn't matter. The point was they'd write it down, but then they'd scramble it, publish that, and then if somebody else later made the same discovery, they would unscramble the anagram and say, oh, you know, I actually did it first. This is not an ideal way, this is not an ideal foundation for a discovery system. And then it took, I mean, a very long time, over a century, I think, to obtain more or less the modern ideals, in which what you do is you disclose the knowledge in the form of a paper. There is then an expectation of attribution. And so there's a kind of reputation economy which gets built. And so basically, oh, such and such did this work, so they deserve the credit for that. And that's then the basis for their careers. So this is sort of the underlying political economy of science.

• 1:38:39Speaker 01

  And that made a lot of sense when what you've got is a printing press and the ability to do scientific journals. Then you transition to this modern situation where in fact you can start to share a lot more. You can start to share your code, you can start to share your data, you can start to share in-progress ideas. But there's no direct credit associated to those. It's not at all obvious, sort of, you know, how much reputation should be associated to them. That's all constructed socially. And so making it a live issue is, I think, a very important thing to have done. And that's, I view anyway, is one of the main positive outcomes of work on open science.

• 1:39:23Speaker 01

  Shall we, I'll give you a really practical sort of example to illustrate the problem. For a long time in physics, there was a pre-print culture in which people would upload pre-prints to the pre-print archive. And in biology, this didn't happen. There was no pre-print culture. That's changing now, but for a long time, this was the case. And I used to sort of amuse myself by asking physicists and biologists why this was the case. And what I would hear sometimes from biologists was they would say, well, biology is so much more competitive than physics that we need to protect our priority.

• 1:40:06Speaker 01

  And so we can't possibly upload to the archive. We have to just publish in journals. And then I would sometimes hear from physicists, physics is so much more competitive than biology that we need to establish our priority by uploading as rapidly as possible to the pre-print archive. We can't possibly wait to do it with the journals. And I think this emphasizes the extent to which this kind of attribution economy is just something we construct, is just something which we do by sort of agreement. And so any attempt to sort of change that economy results then in a different system by which we construct knowledge. And so there is sort of this very fundamental set of problems around the political economy of science.

• 1:40:50Speaker 01

  You know, sort of, we've got this collective project and how we mediate it depends upon the economy we have around ideas.

• 1:40:59Dwarkesh Patel?

  And one of the sort of things you've emphasized as a part of this project of Open Science is collective science or groups of people working, making progress on a problem where no individual understands all the logical and explanatory levels necessary to make a lethal connection. Outside of mathematics, what is the best example of such a discovery?

• 1:41:24Speaker 01

  I mean, I'm not sure I have a well ordering of them to give you a best, but I mean, yeah. An example that I think is very interesting is the LHC, where it's just this immensely complicated object. I actually, years ago, I snuck into an accelerator physics conference. I didn't know anything at all about accelerator physics, but I was just kind of curious to see what they were talking about. And this particular group of people were experts on numerical methods, in particular on inverse methods. And so it basically turns out, you know, inside these accelerators, you have these cascades. So a particle, you know, will be massively accelerated, maybe it'll be collided, and

• 1:42:06Speaker 01

  then you'll get a shower of particles which decays and decays and decays. And there's just this incredible sort of, you know, consequential shower, which is ultimately what you see at the detector. And then you have to retroactively figure out what produced it. And so there's these very, very complicated sort of inverse problems that need to be solved. You've got this final data, but you need to figure out what produced it. And that's how you look for sort of signatures of these. And what many of these people were, was they were incredibly deep experts on simulation methods for sort of following particle tracks. And like, this was really deep and difficult stuff. And I'm like, wow, you could spend a lifetime just learning sort of how to do this and

• 1:42:51Speaker 01

  how to solve some of these inverse problems. And you would know nothing about, or you would know very little about quantum field theory. Know very little about detective physics. You would know very little about vacuum physics. All these other things that are absolutely or very little about data processing. Very little about all these things that are absolutely essential to understanding.

• 1:43:12Speaker 01

  So the Higgs boson. And I don't think it's possible for one person to understand everything in depth. Lots of people understand broadly a lot of these ideas. But they don't understand sort of everything in the depth that is actually utilized. That's why there's these, you know, papers with with well over a thousand authors. And those people can, you know, they can talk to one another at a high level. But they don't understand each other's specialties.

• 1:43:39Dwarkesh Patel?

  Interesting.

• 1:43:40Speaker 01

  That much depth. I mean, things like, as I say, you know, detective physics, vacuum physics, these kinds of solving of inverse problems. Like this stuff is incredibly different from each other. And and, you know, to understand it in real detail is serious work.

• 1:43:57Dwarkesh Patel?

  How do you think about prolificness versus depth? Where, I don't know, maybe Darwin's an example of somebody who's like just gestating on something for many decades. There's other examples where Einstein during the year comes to special relativity is just doing a bunch of different things. Pies talks about how they were all relevant to the eventual buildup.

• 1:44:16Speaker 01

  Yeah. I mean, you know, it's something I stress about a lot. Sometimes I feel like I'm, you know, too slow. Actually, it's funny that, I mean, the Darwin example is really interesting. Like, you know, prolific at what? Like, I mean, I, God knows how many letters he wrote. It must have been an enormous number. So he was certainly very active. There's also like this, there's sort of, there's two types of work that tends to be involved in any kind of creative project. There's routine stuff. And there you just want to avoid procrastination. You just want to like, you know, how do I get good at this? Or how do I outsource it? And how do I do it as rapidly as possible? And just avoid, you know, like getting into a situation where you're prolonging it.

• 1:45:02Speaker 01

  And then there's high variance stuff where you actually, you need to be willing to, you know, take a lot of time. You need to be willing to go to the different places and talk to the different people. Where in any given instance, most of it's just not, it's not going to be an input. And somehow sort of balancing those two things. I think a lot of people. Are very good at doing one or the other, but it's hard to, you know, it's almost like a personality trait, sort of, you know, which one you prefer. And people tend to end up doing a lot of, a lot of one and not enough of, of the other. So I certainly, you know, sort of try and balance those two things. I mean, Einstein is such an interesting example. I mean, 1905 is just this extraordinary year.

• 1:45:46Speaker 01

  Like, you can delete special relativity entirely, and it's an extraordinary year. You can delete special relativity and you can delete the photoelectric effect for which he won the Nobel Prize. And it's still an extraordinary year, like a plausibly a multi Nobel Prize winning year. So what's he doing?

• 1:46:06Speaker 01

  Yeah, I mean, maybe the answer is just he's smarter than the rest of us. And, and there's a lot of luck as well.

• 1:46:14Speaker 01

  But, but, but, you know, I, I certainly for myself anyway, like trying to identify those things that are routine, that I should get good at. And then, you know, just, just try and do as quickly as possible. I think that's yielded a certain amount of returns. But also being willing to bet a little bit more on myself on sort of the variance side has also been very, very, very helpful. That's really hard. Like, because you, intrinsically, you're putting yourself in situations where you don't know what the outcome is going to be. And so if you're very driven to be productive and whatever, and actually mostly it's not working over there. You're like, let's reduce this, like, it doesn't feel right. When I worked in San Francisco, actually a practice I used to have each day

• 1:47:00Speaker 01

  was instead of taking the 15 minute walk to work, I would take the, the more beautiful 30 minute walk to work. Partially just because it was beautiful, but partially also as just a reminder to think like, like that there are real benefits to not being efficient. But it's not an answer to your question. I mean, really, I think all I'm saying is I struggle a lot with the question.

• 1:47:22Dwarkesh Patel?

  I mean, there are these, um, Dinkett, Simington, I forgot his exact name.

• 1:47:26Speaker 01

  Yeah, I know who you mean.

• 1:47:27Dwarkesh Patel?

  Has this famous equal odds rule where he says the probability that any given day in your release, any paper, book, whatever, will be Extremely important for a given person through their lifetime is not that different. And what really determines in what era they are the most productive is how much they're publishing. Any given thing has equal odds of being extremely important. Maybe just think of some of the most successful creatives or scientists. They're just doing a lot, like Shakespeare is just publishing a lot.

• 1:48:00Speaker 01

  And of course, there's kind of examples, Gödel publishing almost nothing. But broadly speaking, I think you need a very good reason to be avoiding it.

• 1:48:14Speaker 01

  Basically to not do that. It's funny, I've talked to, I've met a lot of people over the years who you talk to. They're clearly brilliant and they're just obsessed that they are going to work on the great project that makes them famous and they never do anything. And that seems connected, like it's a type of aversiveness. I think very often they just don't want public judgment. Something that I would love to see, there's an awful lot of biographies and memoirs and histories of people who achieve a lot. I wish there was a very large number of biographies of people who are fantastically talented. Who just missed.

• 1:48:58Speaker 01

  I've known people who won gold medals at IMOs and things like that. Who then tried to become mathematicians and failed. Like what happened? What was the reason? I suspect in many cases, that's actually more informative than anything else.

• 1:49:17Dwarkesh Patel?

  You have this essay that I was reading before this interview about how you think about what is the work you're doing.

• 1:49:27Dwarkesh Patel?

  And writer doesn't seem like, as you say, was Charles Darwin a writer? Right, what exactly is that label? I'm a podcaster, right? So I'm, and in a way, obviously, our work is very different. But I also think a lot about what is this work? And how do I get better at it? And in particular, how I can make sure there's some compounding between the different people I talk to on the podcast. Where I worry that instead of this kind of compounding, there's actually, I build up some understanding that's somewhat superficial about a topic and then depreciates. I move on to the next topic and it sort of depreciates. And so I think there's this question, there's a lot of podcasters in the world who will interview way more experts than I ever have.

• 1:50:10Dwarkesh Patel?

  And I don't think they're much the wiser or more knowledgeable as a result. So there's, it's clearly possible to mess this up. And I wonder if you have thoughts or takes or advice on how one actually learns in a deeper way from this kind of work?

• 1:50:28Speaker 01

  Yeah, I mean, it's sort of an incredibly complicated and rich question. I mean, it does seem like the sort of the question is like, you know, how do you make it a higher growth context? How do you make it a more demanding context? And sort of, you know, you can do that in like relatively small ways, but that might have a yield compounding returns. Or you can do something that is maybe more radical. Maybe it means actually, you know, starting sort of a parallel project in which you do something that is actually quite a bit different. There is something I think really interesting about like how being very demanding can simply change your response to something. Something that I would sometimes do with with students and sometimes with myself was really aim to more at myself.

• 1:51:10Speaker 01

  Was, you know, they would say some week, oh, you know, I'm going to try and do, you know, this work over the coming week. And then the next week would come by and they, you know, they hadn't solved the problem or whatever. And you're sort of like, you know, If a million dollars had been at stake, like, would you have put the same effort in? And the answer is no, sort of invariably. Like, they've tried, but they haven't really tried.

• 1:51:34Dwarkesh Patel?

  Yeah.

• 1:51:36Speaker 01

  I think that's a very familiar feeling for all of us. You know, you sort of, you, you, you, often you, you could do a lot more if you had just the right sort of demanding taskmaster standing by you and saying, "Look, you're barely operating here." And so I do sort of wonder a little bit about like, you know, what's the, what's the demanding taskmaster? What can they ask you that is going to make your preparation way more intense?

• 1:52:05Dwarkesh Patel?

  The most helpful thing, honestly, is for some subjects, it is very clear how I prep. Like, I'm doing an upcoming episode on chip design with the founder of a company that does chip design, and he wrote a textbook on chip design. And he, yesterday I went over to his office and we brainstormed five sort of roofline analysis I can do. And if I understand that, I, I have some good understanding. The problem is with almost every other field, there's not this, there's not like, you, I don't know, when I interviewed Ilya three, four years ago, it's like, "Implement the transformer." And if you implement it, like, you have some nugget of understanding you've clamped down. And with other fields, it's just like, I vaguely understand this, it's not clamped,

• 1:52:48Dwarkesh Patel?

  I vaguely understand this, I vaguely ellent about this, I ellent about this. But there's no forcing function that you do this exercise, and if you do it, you will understand.

• 1:52:57Speaker 01

  Yeah, so, I mean, really what you're sort of saying is, you can do a good job at, at podcasting without actually attaining this.

• 1:53:04Dwarkesh Patel?

  Exactly.

• 1:53:05Speaker 01

  And that's the problem from your point of view.

• 1:53:06Dwarkesh Patel?

  Exactly, yeah.

• 1:53:07Speaker 01

  You, you want to sort of change your job description so that you, you are internalizing these chunks.

• 1:53:12Dwarkesh Patel?

  Right, right.

• 1:53:13Speaker 01

  And just getting this kind of integration each time. And it seems to me like you, you know, what that means is you actually want to change the structure of the, like, like the work output at some level. I mean, lots of people think... There's this terrible idea, people have that they should be in flow all of the time.

• 1:53:34Speaker 01

  And of course, as far as I can tell, like high performers just don't believe this at all. They're in flow some of the time, like you certainly see this with athletes. When they're actually out there, you know, playing basketball or tennis or whatever. Ideally, you know, they are in flow much of the time, but when they're training, they're not. They're stuck a lot of the time or they're doing things badly. And I suppose I wonder what that looks like for you.

• 1:53:57Dwarkesh Patel?

  That I would be extremely satisfied with. The problem is I just like, I don't know what the equivalent of do the 64 lapses for almost. And so this is sort of, this is a thing you can change by choosing guests where there is a legible curriculum. And so maybe it's a mistake for not having done that. Or also, like, there's no real way to prep for Terrence Tao or something. And like, there's no curriculum that's like a plausible one. I think there's one failure mode, so there's many failure modes, but one is. If you could do, one dynamic I'm worried about, a long-term dynamic is that you do good. You can have a good podcast and it's a local maximum, but you, for no particular guest or topic, are you going deep enough that you've?

• 1:54:39Dwarkesh Patel?

  I think my model of learning is there's, if you don't really understand the deeper mechanism, you're just mapping inputs and outputs of a black box.

• 1:54:46Speaker 01

  Yeah, yeah.

• 1:54:47Dwarkesh Patel?

  And that just fades incredibly fast or is not worth it in the first place. And you kind of just move on and it's over.

• 1:54:54Dwarkesh Patel?

  And you kind of need to build the intermediate connection.

• 1:54:59Dwarkesh Patel?

  And it's unclear, I think actually AI in a weird way is really easy for that reason, because there is a clear thing you can do, just implement it, right? And then you understand it. We're almost, if I applied that criteria in elsewhere, what am I, how do I just not do history episodes?

• 1:55:16Speaker 01

  Ada Palmer, exactly, Ada Palmer, like what, you know, wonderful to talk to, incredibly interesting. But for you personally, like what changed?

• 1:55:24Dwarkesh Patel?

  Right. Yeah, there's some things I learned, I think I could have done if I had maybe allocated more time, especially after the interview to like, let's write up 2,000 words on everything I learned and how it connects to other things I know and something. And maybe that's the thing worth doing is spreading out the episodes more and spending more time afterwards consolidating.

• 1:55:43Dwarkesh Patel?

  But yeah, I think I would pay basically infinite amounts of money if there was somebody who was really good at coming up with, here's the curriculum and here's the practice problems you need to do and here's the exercises you need to do after the interview to clamp what you have learned.

• 1:55:55Speaker 01

  Have you tried doing that with somebody?

• 1:55:57Dwarkesh Patel?

  It's hard to fence, I mean, I maybe I haven't tried super hard, but it seems like it would be tough to find somebody who could do that for every single kind of discipline. Maybe I should just hire different ones for different topics.

• 1:56:09Speaker 01

  Maybe, or there's something about like, I mean, what problem are you solving sort of for each episode? And I mean, as far as I can tell, like, that's the only way I really understand anything is that, you know, I get interested in something, at first I don't even have a problem, but there's just some sense of there's some contribution to make here and gradually you home in and there's a problem. And then, I mean, funnily enough, I mean, spending time stuck is incredibly important. And I sort of, you know, that used to just be annoying. Now it seems like, oh, this is actually maybe even the most important part of the whole process. But that very hard-won-ness of it means that, you know, I internalize it afterwards.

• 1:56:53Speaker 01

  I often find, actually, if I, you know, I've written sometimes 10,000 word essays in, you know, a couple of days and I've written them in, you know, three months or six months, I feel like I didn't learn very much from the ones that only took a couple of days. Whereas, you know, some other ones that took three months, I'll be, you know, 15 years later, I'll still remember.

• 1:57:18Dwarkesh Patel?

  Yeah, can you describe outside of physics, how you learn of the ones that took, I mean, three months?

• 1:57:26Speaker 01

  I mean, by far the most, you know, the common things, there's always some creative artifact. Sometimes it's a class, you know, sometimes it's engagement with a group of people who, you know, there's some collective creative artifact that you're working on together. I mean, you might not even be aware of it, but you're acting as an input to their creative ends in some way. And sometimes it's just, you know, It's an essay or a book or whatever. Yeah, it's one of the reasons why I often quite enjoy doing podcasts. I mean, particularly, I mean, I, you know, I, I said yes to come here partially because I know you ask unusually demanding questions.

• 1:58:09Speaker 01

  And so it's sort of, that's an attempt to, to get this sort of perspective from a different, it's a different kind of a forcing function.

• 1:58:17Speaker 01

  So you're trying to pick sort of the most demanding creative context.

• 1:58:19Dwarkesh Patel?

  Yeah, so for this interview, I went through like three lectures of the Susskind Special Relativity book.

• 1:58:24Speaker 01

  Yeah, yeah.

• 1:58:24Dwarkesh Patel?

  The problem is that there's almost no practice problems in it. And so I hired a physicist friend who's gonna like, I haven't done it yet, but it's like every lecturer, I want like a bunch of practice problems to go through them. And I'm, I'm planning on being appropriately humbled.

• 1:58:39Speaker 01

  How do, how do you make it as jugular as possible, right? Like, the higher you can raise the stakes, the better.

• 1:58:46Dwarkesh Patel?

  I mean, the interview is, in some sense, high stakes, but also it doesn't necessarily test deep understanding.

• 1:58:51Speaker 01

  Yeah, but I don't think the interview is that high stakes, right? You're not writing a book about special relativity and you're not trying to write a book that replaces the current, you know, whatever the, the existing standard textbook is. Like, that, that's a really high, really high thing. A phrase that I sort of find particularly difficult and, and it's a funny one. People will talk about going deep on a subject. And it turns out, you know, different people have different ideas of what this means. Some people means they read a couple of blog posts. Some people, it means they read a book about it. Some people, it means they wrote a book about it. And, and, and I think like it's sort of what, what, what your standard is, that's sort of the standard you hold yourself to.

• 1:59:34Speaker 01

  Determines a lot about, you know, your ability to, to integrate knowledge in this way.

• 1:59:40Dwarkesh Patel?

  I don't know what your experience has been, but I found that I'm getting I'm in some sense able to move much faster on some things through the help of AI, but I don't know if I'm like learning better.

• 1:59:50Speaker 01

  Yeah.

• 1:59:51Dwarkesh Patel?

  And I think it's probably because the hardest thing, the thing that is most demanding, is so aversive that you try to take any excuse you can to get out of it.

• 1:59:59Speaker 01

  Yep.

• 2:00:00Dwarkesh Patel?

  And just having back and forth conversation where you gloss over.

• 2:00:04Speaker 01

  It's entertaining, but not necessarily anything else.

• 2:00:07Dwarkesh Patel?

  Yeah, so it's such an easy way to get out of the thing.

• 2:00:09Speaker 01

  Yeah.

• 2:00:10Dwarkesh Patel?

  In fact, it makes it easier because instead of doing some intermediate thinking, there's always the next question you're gonna ask a chatbot.

• 2:00:17Speaker 01

  Yeah, and it's somewhat valuable, like it's not, I mean, that's part of the seductiveness, of course, like it's not actually, it's not actually useless. But yeah, it can sort of substitute for actually doing the thing that maybe you should be doing. It's interesting that, like the extent to which, you know, to what extent should you be outsourcing that kind of stuff and to what extent, you know, like it's really, there's some sort of interesting judgment call about, you know, you actually, there is a whole bunch of routine work that you want done, and in fact, it's low value for you, so you may as well get, if you can get a chatbot to do it, you may as well.

• 2:01:00Speaker 01

  Somebody interviewed the pioneering computer scientist Alan Kay years ago, and he was asked what he thought about basically Linux, and if I remember his answer correctly, he basically said, "Look, you know, it doesn't have anything to do with computer science. It's just a great big ball of mud. There's a few interesting ideas in there which are worth understanding, but mostly all you're learning is stuff about Linux, like you're not actually learning anything which is transferable." I thought that was like a very, like that there's a certain kind of seductiveness to some things where, you know, it's sort of a Rip Goldberg machine, you can just sort of learn about all the bits, and it feels kind of entertaining, but if you step back

• 2:01:43Speaker 01

  and think about the question, you know, "What am I actually doing here?", it might not actually be meeting your objectives. Maybe you want to become, you know, a sysadmin, and learning Linux is a great use of your time.

• 2:01:54Dwarkesh Patel?

  Right.

• 2:01:55Speaker 01

  No harm in that at all, but if your answer is, if your objective is to understand the fundamentals of computing, it's much less, much less clear that that's a good use of your time. I thought that was, it was certainly an answer I've, I've thought a lot about.

• 2:02:08Dwarkesh Patel?

  Yeah.

• 2:02:09Speaker 01

  Where you, you actually need to, for a certain type of mind, there is a seductiveness in, in just, just learning systems and confusing that with, with, with understanding.

• 2:02:21Dwarkesh Patel?

  Okay, I'll keep you updated on how it's discussed.

• 2:02:22Speaker 01

  Yeah.

• 2:02:23Dwarkesh Patel?

  I owe you a text within a month of some revamped learning system.

• 2:02:28Speaker 01

  I'll be really curious if you, I mean, it's also true, right? Like tiny incremental improvements in this, I mean, they're just worth so much.

• 2:02:35Dwarkesh Patel?

  I know, yeah. It's sort of the main input into the podcast, you know? It's great that the bookshelves are fancy and I've got a Blackboard or whatever, but really like the thing that makes the podcast better is if I can improve the learning, I do. So it's, um, yes, it's, it's worth every morsel of improvement.

• 2:02:52Speaker 01

  Yeah.

• 2:02:53Dwarkesh Patel?

  All right. Thanks for the, thanks for the therapy session.

• 2:02:57Dwarkesh Patel?

  Great, no time done.

• 2:03:00Dwarkesh Patel?

  Thanks, Michael.

• 2:03:01Speaker 01

  All right. Thanks for talking, Ash.