Building X With Astro Teller: Monkeys, Card Counting, And The Power Of Failure

23:57And report to the market quarterly how they're doing. That is a world-class skill and Google is world-class at those things. So massive respect for that. But that is a very different way of being in the world than being an explorer. And so that's why you have to create a culturally separate place.

24:17Tomer Cohen:Now, another thing you said, which I thought was super interesting, and I'm curious always about, is this a Google X thing? Or can I extrapolate it to a broader takeaway for builders and any company? People should push on that. I think getting vested in the process and not the outcome is true, no matter where we work. You mentioned the 10 % versus the 10X. And I think you said that it's easier to make something 10 times better than to make it 10 % better. And people hearing that sound very counterintuitive. Is the point that 10 % thinking keeps you locked into the current assumptions? If I ask you to do something, to make a phone that runs on the same battery, the same number of milliamp hours for 10 % longer, at some unconscious level, you will start with the phone that already exists.

25:12I'll optimize. You are now in a smartness contest with everyone else in the world. Good luck with that. But if I tell you it has to be 10 times better, you might well not succeed. But what's for sure, what you will know, not just in your head, but your heart and your gut immediately, is you have to start over. Now you're in a creativity contest. You have to change the game or you have no chance of winning. And being in a creativity contest with the rest of the world is still hard, but it sounds a lot less impossible to me than being in a smartness contest with the rest of the world.

25:47Tomer Cohen:Now I go back to the story with your butter. See, exactly, exactly. So how do I apply this? Because this is where people would listen and they say, yeah, I want to work 10x. But I also know that there are some very successful companies that just do 10%, 10 % and they compound over time. Amazon, Meta. Yeah, I mean, to be fair, some very successful companies have done a few fairly standout things. Amazon is famous for having had Jeff Bezos' early list of things when he was only shipping books of all these other things that he wanted to do. Maybe some of them weren't right, but they have taken some sizable risks, to be fair to Amazon.

26:32But I want to come back to the very basic level. I want you to play a game with me. I've done this the world over with CXOs from large and small companies the world over, and I get the same result from everybody. Choice A, choice B. Choice A, you can give a million dollars of value to your business this year, guaranteed. Choice B, you can give a billion dollars of value to your business this year, but it's not guaranteed. It's one chance in a hundred. A, million guaranteed. B, billion, one chance in a hundred. Who's choosing choice A? Nobody in the room raises their hand. Who's choosing choice B?

27:13Everybody in the room raised their hand, big smile on their face because they've all passed the math test. Choice B has 10 times the expected utility of choice A. And they've all come to me hoping for a lecture on innovation. And then I say, now leave your hand up. If on their best days, in your most generous understanding of them, your manager, your CEO, your board of directors supports you taking choice B bets. And every hand in the room goes down. And then I say, you don't need a lecture on innovation. You need a new manager. The problem is not that people don't understand innovation. It's that organizations are not actually seriously setting themselves up in an organized and efficient way to take those choice B bets.

28:00That's the problem.

28:01Tomer Cohen:Yeah, I was thinking for this checklist within a, let's call it a regular tech company and, you know, at best, it can get two out of the four. I think maybe it's the factory part that actually gets the underscoring. It's not the moonshot. Can I, since you're a product guy, can I pick product as an issue for a moment about, because this is a real tension that comes up all the time in what we're doing. I would describe it this way. There's like a spectrum. On one end of the spectrum is industrialize and sell the bleep out of the first thing you can find that people want and are willing to pay for.

28:39The other end of the spectrum is experiment, you know, semi-randomly forever. I would consider both of those complete failure modes at X. This one's more obvious. This one, this spectrum, this side of the spectrum, the industrialize and sell a lot of the first thing you can find that people want. People have been entrained in Silicon Valley in particular to do this because of the live to fight another day, go prove that you have something. And that ends up with a very greedy local optimization kind of thing. What we're trying to do is spend the time pressure testing your idea, working on the riskiest parts of the problem first.

29:28But when it becomes the biggest remaining risks, does anyone want this? Why do they want this? What would they do with this if you gave it to them? How much will it cost to get it to them? How much will they give you in exchange And is that the subtraction of those two numbers a positive number? These are fundamentally product questions and go-to-market questions. When that becomes the biggest risk, you have to run experiments and get the answer to, do we understand how to make a once-in-a-generation business here? And ultimately, you have to do things that look more and more like building a product in order to ask and answer those questions.

30:13So this is very unique.

30:14Tomer Cohen:This is what I, so I want to unpack this a little bit. So an idea comes to the factory. Okay, let's put the factory aside. Now idea comes to the computer. It's the teleporter, let's say. And then somebody preaches really well. You feel like they're, you know, disassociated from that personality. They really, they found something really massive. You give them a little money and then you ask them to focus on the monkey. And I want you to expend the monkey for the audience. So that's how it starts. Yes, it is. So you take this moonshot story hypothesis, what you just described is what I would call the moonshot story hypothesis.

30:47Huge problem, science fiction sounding product or service, breakthrough technology. Once they come up with it and I say, hey, you're probably cool, high five, you're probably wrong. Go find out how fast and efficiently you could kill it. What I want you to work on is not the thing that will make you look cool, because what's cool at X is the intellectual honesty and the efficiency with which we can learn. It's the information gain per dollar spent. So we have this funny story, which is imagine if the project we were working on together was to get a monkey to stand on the top of a 10-foot pedestal and recite Shakespeare.

31:23Which should we do first? Train the monkey or build the pedestal? if we're really honest, most businesses most of the time are building the pedestal. Because you can say to your boss, look, I'm half done. And there's like a sense in which that's there's progress. I'm making progress. And like, hey, can I have a bonus? I want to be a vice president now. Can I have that? Look how good my pedestal is. But in that extreme situation, we can see since 100 % of the risk is piled up on whether or not we can train the monkey, There is absolutely no reason to build the pedestal first. The only thing you should spend your time on is training the monkey.

32:03If you can train the monkey, great, we'll get a pedestal. And if you can't, thank God we didn't spend time on the pedestal first. So people have really deeply understood this at X to the point where they just talk about, hey, in my project, this is the monkey. They'll just say, this is the monkey, which is shorthand for, this is the riskiest part of the problem. This is where the information gain is the highest. And that's why we're focusing on this. So I want you to spend your time on that. And then if it turns out that the result is, hey, the monkey's not speaking Shakespeare, but we got a sonnet out of him.

32:40Awesome. All right, let's keep going. And if it's like, nope, the monkey's mute after, you know, six months, like, you know what? Let's move on to another project. So literally, you would take the highest risk,

32:52Tomer Cohen:hardest problem to solve. It was a start here. Prove to me that this is doable. I mean, yes, absolutely on that. But also, imagine you and I were working on a project. And now a new project has come up over here, which has twice the risk, but four times the upside. Technically, that thing has twice the expected utility of the thing we're working on, even though it has double the risk. And this is where you come into play. And yeah, I would say, hey, guys, like we should seriously consider having you stop doing this and go help them on that if that actually has a higher expected utility. Can I give you an extreme version of this?

33:29Tomer Cohen:Sure. So we spent four and a half years on a fusion project at X. And most of the people in the fusion space. Nuclear fusion? Nuclear fusion. Are doing something where the physics risk is not low, but it's lower because they're doing something, many of the best ones, are doing something which is relatively well-trodden physics in the fusion space called a tokamak. Sort of surrounding a thing that you want to keep at very high temperature and pressure with a lot of magnets to sort of keep it in like a tiny little sun almost. I'm learning as if I understand, but. And so you have, call it medium risk and crazy high expense on the engineering side.

34:16Someone came to X and said, they were already at X, and they said, here is a crazy idea. There's this weird bit of physics that back in the 1980s, people had some good experience with, and then they couldn't keep it going. So it's kind of been discredited by the physics world. But if it was true, if they misunderstood in the 80s why that good news sort of couldn't be repeated, this way of doing fusion would be wildly cheaper to do afterwards. So the physics risk is much higher, but the engineering risk is much lower. And their argument was, it's, I don't know, call it a trillion dollar opportunity if it works.

35:00Maybe a 1 % chance that we actually get there. So let's call it an expected utility of$10 billion. If we have to spend$10 billion to find out if we're right or not, not a good lottery ticket. But these people said, we can ask and answer this question for like under$10 million. And I said, hell yes. If we can take that kind of risk with that kind of in the money upside on a lottery ticket, like that's the kind of thing we should be doing. They did it for about four or five years. It was a tiny number of people. We actually did almost 1 ,000 plasma shots before we shut the experiment down. They shut their own project down because it turned out that the physics risk wasn't playing out.

35:46And we've moved on to other things. I'm incredibly proud of the fact that we did that. Not because it didn't work. Of course, I'd rather it had worked. But because that's choice Bs. That's exactly choice Bs.

36:00Tomer Cohen:And is that very often? That happens more often than not? The comparative, like, hey, I'm finding a different problem with a better risk to benefit? Yes. I mean, I think it is rare that we're taking physics risk. Often the risks are much more system integration oriented, or there are issues around skating to where a puck might be. So I don't know, maybe you think you're at X, and you have a theory about some really crazy stuff we could do with carbon nanotubes. But right now, carbon nanotubes are a thousand times too expensive to do that thing. And you have a theory that other people are going to solve the cost problem.

36:42And you want to build these, like, cool new things with carbon nanotubes. That's not exactly a physics risk, but that's a risk we would have to accept in that project.

36:54Tomer Cohen:And, Astrid, how do you think about risk reduction as part of the process? So, you know, I started my career in semiconductors. And I used to say, you know, in semiconductors, you can design a chip, build it, take it out to market. And in the meantime, you can have a baby, get married. It takes a while. Yeah. So for the process, you do a lot of work to take the risk out of the design. You don't want to find out you have an issue when you go to production. That's the worst outcome possible. So there's a lot of exit points. There's like an exit point you can, you know, this could be just an incremental chip or the previous chip, not a 10x chip you were hoping for, but there's an exit point.

37:30Tomer Cohen:So they kind of built exit points along the way that basically de-risks the project. That's like one way to take something really big, high investment, and kind of de-risk it? A hundred percent. So think about the eponymous moonshot, right? It wasn't like the first thing they did was try to go to the moon, right? It started with, hey, can we have a rocket just go up and come down again? Can we have a rocket go up and get to the place where if someone was inside, they would have experienced zero-G, but there's no one inside and come down again? Can we have a rocket go up, go around the world once and come down again?

38:03Can we have the rocket go up with a dog inside, go around the world once and come down and the dog's still alive. There was this whole series of things where they were asking and answering questions and learning what it would take to take a person to the moon. That's exactly what our moonshots are like. Hopefully they're cheaper than that. But they have that same kind of structured theory, design of experiments where we're working on the riskiest parts first, but we're trying to figure out how fast to retire risk per dollar spent. and we keep going when the risks are getting retired really quickly relative to the money we're spending.

38:41Tomer Cohen:So is this like a template that somebody produces? Once you said okay to the project, then the next step is to figure out the riskiest part and then how do you do risk it? Is this so systematized to that point? Yeah, well, again, imagine that you worked at X and you're proposing the teleporter. Not for the first$50 ,000, But if in a few months, whiteboards, talking to some experts, we haven't been able to easily kill off your idea, maybe we're getting more excited about it. You and two or three people are going to actually start being full-time on the teleporter. It's really two or three people.

39:19Because you should be able to run some experiments without some huge team. It has to work that way in order for us to be efficient. What we want you to do right then is set kill criteria. We call them kill criteria. You can't even become a project that acts without kill criteria. And those should be married against the monkey. What are the things that if we can agree now, if you can't get good evidence over the next 12 months that the following is true, we should just call it a day. Now, we have definitely gotten to kill criteria and missed, or sorry, we've missed our kill criteria and still continued projects sometimes.

40:02But at least we can agree ahead of time the default is to turn it off. So there has to be something else we've learned that gives us a different reason to go forward.

40:11Tomer Cohen:I want to take three projects slash products that you guys took out. Waymo, Loon, and Google Glass. They're all very different. And then one became a major company. One, the original project died, but it seems like the learning lived on. And one, it seems like it was ahead of the market in a way. So Waymo, everybody knows right now, maybe two years ago, it was hard to know the name, but now it's the self-driving car. Actually, funny story, I took it from Palo Alto to SF this week, and I was coming off the highway and was supposed to merge into the lane, but the lane had a traffic jam. And the Waymo was trying to get in, and nobody was giving it the space to come in.

40:53Tomer Cohen:And I'm like, oh my God, I'm stuck right now. Because a human being will just kind of nudge their way in. And now this thing is going to take me to the next interchange. And I'm going to relate to my meeting. And then it nudged. And I was amazed. It kind of felt like a New York taxi driver just finding their way in. And there was like a moment of light bulb for me. This learned. We call it body language. that it's turned out to be a whole next wave of things that Waymos had to get good at over the last five years is the body language as a car and how other drivers read the body language of these movements of your car.

41:34Tomer Cohen:Incredible. I used to think about how do you solve the left turn, which in the U.S. you can do as well for the traffic coming from the other side in a jammed junction. That sounds like a really tough problem. But then you could see that aspect coming through. Why was the monkey in the Waymo project? Because there's so many decisions. I'm sure maybe the monkey changes shape all the time. It did. I mean, in the early days, it was how too early are we? Can you get this to work even sometimes? So we said, here are 10 different 100-mile routes around the Bay Area that were picked to be very different from each other and all very hard.

42:16in order for this project to continue the the kill criteria we hadn't named them kill criteria was for you to do each of these routes at least once without a human touching the wheel or the brake of the gas pedal these were Priuses that had been sort of fly by wire and you can try as many times as you want but you have to do each of them at least once with nobody driving the car. And that was a question that had nothing to do with feasibility or like nine's reliability or anything. It was just like, is it even possible? Later, there were very different questions. We're like three different epochs for Waymo.

42:56We thought we were making a car. We thought we were going to sell it to people. And about 2015, it was so good on the highways and city streets, but including the highways, that we said, okay, we're going to let Googlers commute with them. And we gave, I don't know, 10, 20 Googlers these cars and said, you can commute to work with these, but you have to promise to keep your hands right by the steering wheel. We're going to have cameras watching you. And these Googlers all said, oh, yeah, I promise. They were like putting on their makeup, falling asleep in the backseat, eating their lunch. It was horrible.

43:30And we had to call after a week or something. We just called off the experiment. It was dangerous. Humans are not a good backup for machines. They're just terrible at it. And so there was this - We trust too quickly. Yeah. And there was this crisis moment where we said, do we have to kill the project? And what came out of that crisis was a decision. It was a big pivot. Oh, our job is not to sell a car. Our job is to sell mobility. We're transforming mobility. That's what we're doing. And for at least five years afterwards, that was the rally in Cryowemo. We're transforming mobility. And even that turned out to be wrong.

44:07because transforming mobility includes charging the car and the app for calling the car and all these things that Waymo's happy to work on, but that's not their job. So now if you ask Waymo, what are you doing? What's your job? They say, we're making the world's safest driver. That's what they're doing. And that architecture for understanding what you're really up to as a team is part of what comes out of really deeply asking, like, what are we great at? what's important about this and what's sort of secondary?

44:41Tomer Cohen:It's interesting. My experience as a user of Waymo is that it's transforming time for me. Because I was debating this week they could take an Uber or Waymo. Granted, Uber is quicker. Waymo can take the other route a little bit. But in a Waymo, I can do whatever I want. The firm is like, okay, this is my meeting area. It's where I practice. I was giving a talk. It's where I practice my talk. And an Uber, I wouldn't feel as comfortable. so it's from time for me are you surprised sometimes how trusting human beings are like it's remember like my first ride I had to convince my wife to go on a way on a ride with me and she was you know looking out the whole time and freaking out and saying this is the last time I'm doing it and then literally the next ride she was on her phone yeah she wasn't even paying attention and then I'm thinking about everybody's like that but for me it was mind-blowing because then I'm like hey robots robots in my home doing chores I'm like, oh, this is going to be creepy.

45:37Tomer Cohen:But then my sense is it's going to be creepy for an hour. And then you're like, you're going to get upset that the robot is not doing more for you. So people are at least as much like that with Wing, the drones for package delivery. It seriously is like Harry Potter owl post. The experience of just asking for something, like imagine anything you could get at Walmart that fits in a bread box. and it just literally comes out of the sky, like drops into your hands a couple minutes later, it's kind of magical the first couple of times. And then you're like, hey, where's my, you know, I need a monkey wrench.

46:14It's been, you know, 90 seconds. Where's my monkey wrench?

46:17Tomer Cohen:It's amazing how quickly we move from like no way to, I don't know if there's a, I don't know if there is a scientific term for it, but that. At least a version of it is called hedonic adaptation. Oh, not good for me. I'm just going for it. You mentioned Loon and glass. Loon is an interesting story for us. It's a particularly good example of what we call moonshot compost. Did Loon become Tara? Yes. Okay. So Loon was our first big moonshot in connectivity. And there were two problems. One is, could you make this ad hoc mesh network of balloons in the stratosphere that somehow magically all talk to each other, move the data around, beam it onto the ground, and solve like rural connectivity.

47:03That part worked amazingly. Hats off to the team. You also have to make it into a business. And we were doing it, but it was going too slow. Our ability to get there with the telcos, it wasn't what we wanted it to be. So we shut it down. But in the process of that ending, we had been having these balloons talk to each other and the ground using lasers. And a few of the laser people said, I know this isn't supposed to work on the ground, but will you just like let us take these lasers and start a new project at X, just seeing if we could solve the world's connectivity problems using lasers on the ground.

47:39And eight years later, the Tara team, which has now graduated from Exxon as an independent company, is moving more data every like two or three minutes in 20 countries around the world than Loon did in its entire nine-year history. and so it's really upsetting when something ends but as long as you're in love with the problem and not in love with the current solution you know again if you worked at x i would say i know this is upsetting but your people don't have to leave x the patents don't have to leave the code doesn't have to leave the hardware doesn't have to leave even the partnerships that you've built We can repurpose those.

48:26If you're passionate about solving the problem, it all goes back into the dirt. And you'd be surprised. It comes back.

48:33Tomer Cohen:That's amazing. And Google Glass, because in many ways, I remember we talked about, you know, LinkedIn used to be in Sterling Court. It was like, you know, doing the round around the campuses and seeing, this is like a decade ago now, people walking around with Google Glass and like, you know, using it and like saying, this is cool, but, you know, it's actually painful a little bit more than it's cool. And then now you see it's becoming more and more mainstream. I think increasingly it's obvious we were right and we were way too early. That would be my summary of the situation as Glass is coming.

49:04So what did you underappreciate about that moment? So I think we got something incredibly right about pre-product and then something incredibly wrong about product. And here it is. We called the early versions of Glass the Explorer Edition. And at first, we saw it for ourselves, and we were telling you, did you have an early version of Glass? Yeah. Yeah. So then you remember, you are an explorer. And if you buy this, we need you to think of yourself as an explorer. It's literally what we called you when you bought it. And so we were trying to train you that this is not a product. This is a learning platform.

49:47And in the early days of Glass, people were kind of crazy about it. Yeah, you saw it. You saw it. Everyone loved it. And there were so people were flooding back to us. Filmmakers and doctors, people who were chefs. They wanted to love it. Remember, like, I wanted to love it. And as a learning platform, I think it was pretty exceptional. So that's what we got right, really right. Then somewhere along the way, we lost the thread. And we started to believe people's excitement and started to think of it as a product when it was not a product yet. and partly because we were charging as much for it as we were.

50:23I think that encouraged people to think of it as a product. It ended up on some runway models in New York. There were a few things like that that coincided to leave people feeling like we were promising them an exceptional product experience.

50:38Tomer Cohen:They were buying the future in a way. Right. And then once their expectation had risen up to here, and it was still a great learning platform, but it was not a product, but they were now expecting a great product, then we were deeply disappointing a lot of people. And then I think that's what caused Glass to regress in terms of people's experience. So what would you have done differently in that respect? I think we should have started with professionals and prosumer experiences and spent longer with doctors, people on oil rigs. So narrowed the use cases. Narrowed the use cases. And for longer said, we're listening to you, but this is not a product.

51:19We're glad that you find some use in it, but you have to keep telling us what you wish this did. Where do you find this useful? We're going to keep trying to improve this, but do not expect this to be a polished, clear value proposition, you know, solve for something in your life because it isn't yet. Even though doctors like, oh, I could use this as a checklist for the things I have to go through every day. The mechanics for airplanes were like, oh, I could look at a million pages of manuals while I'm like fixing. Yes, conceivably, kind of today, but it wasn't optimized for any of those things.

51:57And you know what it takes to make a product. The difference between proof of concept and a really thoughtful, like capital P product is like often years. Do you see augmented reality in the same category? You see it different? Oh yeah, there was a decent amount of augmented reality in what Les was doing.

52:14Tomer Cohen:kind of the whole augmented reality glasses for doctors to try and pull it out. This was a big project with Microsoft, and then it was not. Oh, do I think that they suffered some of the same problems? Yeah, absolutely. I think they might have been even less successful at flagging it as a learning experience, but they fundamentally suffered from the same problem, which is it wasn't a product. They were kind of making it sound like it was. Developers don't develop, at least in large amounts, for a learning platform. They'll experiment with the learning platform, but developers go crazy once it's actually stable enough.

52:46Tomer Cohen:I don't recall any of the learning platform narrative when I was using it. Because I think, actually, even if it was out there, maybe people didn't want to listen to it. Or didn't want to, I don't recall that narrative coming out. But you remember being called an explorer? Yeah, to an extent, yeah. Yeah, so that was... I thought it was cool. Okay, but I think this disconnect where we were seeing it that way, we were calling an explorer, but then you even, and you're like much more thoughtful and sensitive than probably most of our customers were, we're still experiencing it like we were making a product promise to you.

53:20This is exactly what we got wrong.

53:22Tomer Cohen:So you gave some pretty amazing principles, which I think people can take away. I think people are, they kind of want to get all the use cases out. So like, what's a good way to get all the use cases out from this amazing, you know, years of learnings you have? So we started a podcast a little over a year ago. We did a first season, which is audio only, though we have some deep dives, which are video. Those are more like an hour. The audio ones are also an hour, but they're more of a smorgasbord. And the hour-long deep dives are individual conversations like this about a specific project. We have a second season, which is a little more than half out now.

54:00It's still coming out every Wednesday. and each of these episodes is an introduction to usually two of our different projects that have something in common. So this is me as the host and interviewer. So this is not me saying how it is. It's me asking people who've gone through X, how did we find you? What was it like to start a moonshot? Where did you get lost? What was hard about it? What was the breakthrough? what happened after you graduated. And we are having these conversations with the people who started Google Brain, with the people who started Waymo, with the people who started Wing and Loon and Tara and others.

54:40I think there's a ton to learn from. I think it's really fun for people to listen to. Love it. And the name? Is called the Moonshot Podcast. If you just search for Moonshot Factory, Moonshot Podcast, you'll find it.

54:52Tomer Cohen:So we talked a lot about what you're doing, your team is doing. It's just unbelievable. Now, just like, if you zoom out, I think that would be just getting to know you through this time. It would be actually easier for you than most people. If you look at the next decade, you zoom out of Google, of Google X and Google in general, and you think about the next generation of builders. What do you want them to be brave enough to try and build? And in a way, also wise enough to not touch. one of the things I would like builders, especially people, you know, in their teens and twenties to hear every generation feels like all the good ideas have been used up.

55:33They have absolutely not. We are at the beginning of a Cambrian explosion of innovation. I really believe that. And I can, I can feel, and I've heard many times people, especially younger people's fear that they sort of somehow showed up on the scene at the wrong time that they sort of like musical chairs ended just before they got to this, you know, the next open chair, everyone sat down and they're sort of left hanging. I don't think that's true. I'm not saying it's, it's easy. It's all, you know, rainbows and unicorns. But I really do think that innovation is going to ramp up. We're going to see more positive change in what's possible for humanity in the next 20 years than we did in the last 50.

56:25And I hope builders can feel that opportunity. There is so much temptation to just vibe code your way to something that's mildly better, that people already kind of understand that's like a super comfort feature, but won't fundamentally make things different than they are today. I just would encourage people to go get their boots a little bit dirty and be open to the idea of trying things that sound uncomfortably exciting. You know, one of my mantras or maybe metrics is if you ask a hundred experts and even 10 of them tell you what you're talking about sounds exciting or reasonable, you're too late.

57:10If zero of a hundred tell you that what you're talking about sounds interesting or exciting or reasonable, you're too early or it's just not possible. You want like three or four, maybe, of a hundred. I just would encourage people to take a little bit more risk. Anything you want them to not try to build? I mean, I have a bias, which is, I think, the pursuit of knowledge, understanding how the universe works and how to engineer things, almost nothing is off limits there. But there are things that are not the right product to build, not the right service to build. And unfortunately, I think we live in a time where we have overlauded people for going extremely fast and not caring very much about the damage that's done on the way to making your first billion.

58:08I'm not saying that money isn't important, but I would love to see people have a little bit more of a principled approach. That doesn't necessarily mean go slower or take less risk, but think of your bank account as not just the number of dollars that you have, but the pride in yourself that you can have and the legacy that you're creating. If we could reconceive of what we're building in those broader terms, I think people would build somewhat different things. You know, we have not said the word AI, I think, once in this session. I'm so proud about that. Every single thing we do at X, essentially, has AI in it.

58:49I'm sure. But it drives me crazy when people talk about AI.

58:52Tomer Cohen:Well, you know, now it's kind of hard because there's like AI since 2022. and there's AI before. Why do people get wrong about AI in your mind when they talk about AI? So I have a PhD in artificial intelligence from almost 30 years ago. So, I mean, first, it's a 70-year-old field. It did not start five years ago. Two, it's not actually a monolithic domain. There's a lot of different things happening in AI. And mostly when people say AI, they mean LLMs. But AI is a much more complex world of learnings and experiences than that. I guess here's maybe what I would encourage people to take away. We say that hot air balloons fly, that dragonflies fly, that 747s fly.

59:39We use the word fly for all of them. And yet at some level, we understand that they fly in incredibly different ways. Intelligence is similarly multidimensional in its characteristics. And are we smarter than machines? Like, that's just not helpful. That's just not what I think of as an interesting topic. It's like saying, do dragonflies fly less well than 747s? I mean, kind of yes, kind of no, kind of who cares. I would just encourage people to think of intelligence as a much wrinklier and more high dimensional subject than intelligence.

1:00:25Tomer Cohen:If you could snap your fingers and solve a product issue or a tech issue like right now, what would that be for you? I mean, I have some particular fondness for room temperature superconductors and a number of other things. But I guess if I was trying to, I'm going to turn your question into what one underlying technology change would unlock the most new moonshots. I'll tell you that way, because that's what's on my mind. I think having energy density 10 to 100 times higher than what we currently have in lithium-ion would change the world in a lot of different spaces. I can't tell you the number of dreams we've had at X that we've just had to put in the freezer because we need a battery that's, you know, 20 times the energy density of what we are right now.

1:01:20Tomer Cohen:What's a product that you did not think would be successful but surprised you? One of the really mature projects at X is a synthetic genomics effort. It is being able to simulate small cell biology so well in the computer that you can reprogram the biology to ask it to manufacture new things for you. And that involves a level of being able to understand, have the computer understand biology well enough that you can simulate it. When we started that nine years ago, I was incredibly sure that was not going to work. And I was wrong, and I'm really excited that I was wrong. What's your favorite non-digital product?

1:02:05I mean, I'm constantly grateful for my glasses. I think glasses are one of the best user interfaces that humanity has come up with. You forget that they're there. You use them in actually quite dynamic ways. These are progressive lenses. So I can see up close. I can see far away. They never run out of batteries. They actually change. These are progressives. So they turn into sunglasses when I go outside. Like that's a bit of a miracle. But can I give you a second one? Yeah. I think we should be trying to get technology to be like glasses sometimes, but also like anti-lock brakes on your car. When you are about, like something bad happens and you smash your brake, that's great.

1:02:50Like there's a very kinesthetic experience to smash the brake. But when you smash the brake, that does not actually break, like put the pads against the brake part of the car. You're talking to a robot. and the robot is like, I hear you and I will now try to stop as fast as I can subject to not putting us into a skid. What an incredible user interface where you don't have to think about that at all. You can just be like, stop! And then all this complexity happens behind the scene and it's a very kinesthetic thing. There's no button pushing. I wish more of technology was like that.

1:03:32Tomer Cohen:For young aspiring builders who are seeing you, they're inspired by you, they want to be you. What do you think they should learn or go do? Like, what would you advise somebody who is now 17, 18? I mean, I definitely would say you can always get a soulless job later. Find something you're passionate about and go do it. I think people are playing it safe way too early in life. One. Two, surround yourself with good human beings who you can learn a ton from, it doesn't matter what they're doing. Who cares what your degree was in? Who cares what they're currently doing? If they will hire you, if you can find fantastic human beings to be around and a great manager to learn from, that's what to optimize for, not the subject they're working on.

1:04:24And if they want to get into X, what's the recipe for that? I mean, we're looking for people. We are looking for people. We are hiring, but we're looking for people who are weirdos, who have never quite fit in other places. We hire a lot of people with no job description, even quite senior people. And if that sounds crazy, like, hey, I'd like to hire you. I'm probably going to pay you half of what you're worth for right now, and then we'll ratchet it up when we figure out what your actual job is. I want you to spend the next six months here just wandering around X and figuring out what your job should be.

1:05:00Most people wouldn't take that deal, but that's actually good because the people who wouldn't take that deal would be miserable at X anyway. I just hired someone to a deal sort of like that. And she had just given most of the money that she had raised back to her VCs. Does not happen very often. That wasn't the reason we hired her, but it was like one of 10 reasons we hired her, because that's showing a kind of intellectual honesty and not just playing the system and like spend every dime that you got that signal to us, oh yeah, she needs to be with us next.

1:05:37Tomer Cohen:Astro, this was wonderful. Thank you so much. Homer, thank you for doing this with me. Thank you. I love this conversation with Astro. What struck me the most is how he took something that can easily sound very abstract, moonshots, innovation, impossible ideas, but then he made the day-to-day practice sound incredibly concrete. Here are some of my main takeaways from the conversation. First, when it comes to solving really hard problems, the best builders are not trying to be right. They're trying to become less wrong as fast as possible. Astros shared that the operating principle at X is not simply dream big.

1:06:15Tomer Cohen:It's actually to become the best in the world at the learning game. In moonshot projects, the hard part is not building the solution. The hard part is figuring out what the solution should be. Because once you know the answer, building it is much easier. That mindset completely changes how you think about progress. It's not about shipping more. It's about learning faster. And sometimes the best way to do it is by quickly proving that your current direction is wrong. That's why Astra wants his teams to try and kill their own projects early and discover as quickly and honestly as possible why their idea might not work.

1:06:55Tomer Cohen:If they cannot kill it, that is a good sign to keep going and invest more. And if they can kill it, that's also a good outcome because they'll learn quickly, they save years of wasted effort, and they can move on to the next idea. Second, don't build the pedestal before you train the monkey. I love this metaphor. If your project is to get a monkey to stand on a pedestal and recite Shakespeare, most teams start by building the pedestal. Because they know it's doable. It feels like progress, it feels good. But the real risk is not getting the monkey on the pedestal. It's getting the monkey to recite Shakespeare.

1:07:33Tomer Cohen:Can you even do that? With Moonshots, you need to attack the hardest, riskier assumptions first, because until the risk is addressed, everything else is just theater. Third, going for 10x improvement is not just about being more ambitious. It actually changes the game you're playing. Astra framed this beautifully. If you try to make something 10 % better, then you start with the existing system and you enter a smartness contest with everybody else. But if you try to make it 10 times better, you are forced into a creativity contest. Now, this thinking doesn't apply to every problem because not every problem deserves a moonshot.

1:08:13Tomer Cohen:But it does mean that sometimes incremental thinking traps you inside of the box. Fourth, innovation is not gambling. It's actually card counting. Astro wants his team to be card counters of innovation. In blackjack, card counters do not know the next card. They're not predicting the future with certainty, but they are paying super close attention to the evidence. And then when the odds improve, they increase the bet. That's how X thinks about moonshots. At the beginning, most ideas are probably wrong. So you start small and you observe them very closely. You give them some time, some capital, and a clear question to answer.

1:08:53Tomer Cohen:But then you watch the evidence. And if the odds improve, you invest more. If they get worse, you fault. The same lesson goes for builders. Let conviction guide your path at the beginning, but then let evidence tell you when to double down and when to fault. And last but not least, real innovation requires culture engineering. This might be the deepest lesson from this episode. Astro's process sounds obvious. Run experiments, follow evidence, kill what doesn't work, double down what actually improves. But most organizations are not actually built to do that. Because they say they want learning, but they reward certainty.

1:09:34Tomer Cohen:They say they want risk-taking, but then they punish failure. They say they want bold ideas, but then they ask every team to show predictable progress. And that is the part of what makes XO unique. It was built as a separate environment with operational independence, very strong founder support, and a culture designed specifically for this work. So now, think about your own company. Would it tolerate such a process? Would it actually reward it? And if the answer is no, then the bottleneck for innovation is not the lack of ideas, it's the culture. I'm Tom Erkoin, and this is Building One. I hope you enjoy this one.

1:10:18you've been watching building one our show is hosted by tomer cohen building one is produced and edited by mason cone and the team at coastal production works this episode was mixed by tim boland at linkedin our team includes rachel carp sarah storm dave pond and alicia mann with support from alex kuznetsova and mujib merdad until next time keep building Thank you.