Astro Teller: The $1B Bet No CEO Will Back, Moonshots 3x Cheaper in 16 yrs, and Clean Water at 1¢/L
At X, a moonshot is a testable conjunction of a huge problem, a science-fiction-sounding solution, and a breakthrough technology that offers at least “a tiny chance” of connecting the two. The necessary temperament is equal parts audacity and humility: pursue the unlikely, but begin by admitting, “It probably won’t work,” then test the hardest assumption as cheaply as possible.
X operates less like a conventional R&D lab than a tightly filtered venture portfolio. Teller says up to 200 ideas a year make it far enough to receive code names, yet only two graduate five or six years later—a stated 2% hit rate. Across 16 years, approximately 2,000 code-named projects produced 35–50 graduates, with Google Brain illustrating how an approximately 18-person team at graduation can underpin an enormous outcome.
A central corporate obstacle is governance, because executives routinely reject bets whose expected value they readily understand. Teller contrasts $1 million guaranteed with a 1% chance at $1 billion—the latter has 10 times the expected utility, yet support disappears when employees ask whether their CEO or board would actually tolerate it. His verdict: “You don’t need a lecture on innovation. You need a new manager.” He endorses keeping the core accountable for roughly 10% profit while placing 10X bets in an edge organization reporting directly to the CEO.
X says the cost of producing a graduate has fallen roughly threefold over 16 years, or, in Teller’s uncertain estimate, perhaps 10–20% annually, through better practice, earlier graduation, and AI. Alex challenged whether this merely reflects a richer economy; Teller rejected the comparison as confusing “the cost to paint a house with the value of the house.” The return can still be extraordinary because a Waymo-sized winner covers both itself and the discarded experiments.
AI is already a teammate across X, but Teller regards “we use AI” as an implementation detail equivalent to saying “we use electricity.” On the current clean-water project, salaries still exceed the AI bill, though Teller could not say by how much. He hopes AI will shorten the path from crazy idea to evidence-based de-risking and permit even greater audacity. He does not expect 100% automation within a decade: choosing socially worthwhile problems, winning community acceptance, and building distribution will require humans for “at least the next decade or two.”
X’s kill discipline is built around solving the monkey before constructing the pedestal. Teams must attack the assumption that could invalidate the project, because the easy pedestal creates visible progress while concealing that the monkey may never recite Shakespeare. Teller calls himself the “crown prince of failure” because moonshots are learning processes: “You learn nothing when you’re right. You only learn things when you’re wrong.”
Scientific discovery is not the investable endpoint; industrialization is the remaining 95% of the work. A single flake of room-temperature superconductor might win a Nobel Prize, Teller argues, but commercial value requires thousands of tons per day, suitable ductility, and manufacturability. The same techno-economic threshold governs clean water: 10 cents per liter is insufficient when the world-changing target is approximately one cent.
1. A moonshot begins as a falsifiable story, not an ambitious slogan
Teller’s three-part definition starts with a named, consequential problem; without one, the work is “arguably an academic exercise.” It then requires a science-fiction-sounding product that would resolve that problem and a breakthrough technology offering at least “a prayer” of making the product real.
X calls that conjunction a “moonshot story hypothesis”—testable, but emphatically not a promise of success. The explorer needs audacity to “suspend your disbelief for non-stupid reasons” and equal humility to acknowledge from day one that the journey is unlikely to work.
Early rejection often comes from first-principles techno-economics: enumerate the bill of materials, raw weight, achievable price, and customer willingness to pay. Teller’s conclusion is commercial as well as moral: “Purpose and profit can support each other,” while something structurally loss-making probably will not change the world at scale.
The funnel makes that skepticism concrete. Teller says up to 200 ideas annually make it far enough to receive code names and that X graduates about two after five or six years; over 16 years, approximately 2,000 code-named projects yielded somewhere between 35 and 50 graduates.
2. Google Brain shows why apparent overnight successes require long incubation
Google Brain began at X roughly 15½ years ago, when neural networks were “absolutely dead” and academics including Andrew Ng and Yann LeCun argued that scale might revive them. Ng and Jeff Dean asked whether industrializing neural networks—making them tens of thousands of times larger—could produce the missing breakthrough.
Teller identifies TPUs and the transformer—the “T in ChatGPT”—as coming from Google Brain. X’s role is to create “seed crystals” that can later reshape the world; his broader framing is that an apparent overnight success is typically 15–20 years in the making.
The unsolved portfolio remains grounded in hard thresholds. Nearly three billion people are water-stressed and lack clean drinking water, but X stopped approaches projected at 10 cents per liter because transformative clean water requires roughly one cent all-in; it also keeps revisiting education and the broader challenge of shifting energy across both time and location.
New materials excite Teller, but discovery is “the first 5% of a business.” One flake of room-temperature superconductor could earn a Nobel Prize; the moonshot is manufacturing thousands of tons daily, with properties such as sufficient ductility for winding wires.
3. Efficient moonshots require protected governance and unusual culture
Teller partly accepts the great-stagnation framing: after the 1960s and NASA, society “lost the explorer spirit.” His economic diagnosis is that during World War II and the Cold War, people cared less about return on investment; when return mattered more, audacious projects became harder to justify.
His “dirty little secret” is that moonshots are easy if efficiency is irrelevant: assemble “delusionally optimistic” people and pour money on them. X’s real project is systematizing radical innovation so its expected return makes sustained funding rational.
Teller’s choice experiment exposes the governance gap: $1 million guaranteed versus a 1% chance at $1 billion. Almost everyone chooses the mathematically superior second option, but hands fall when he asks whether their manager, CEO, or board would genuinely support it; the “choice Bs” therefore need a sequestered organization where their mess is tolerated.
His organizational prescription is to keep the core accountable for roughly 10% profit year after year while placing 10X—1,000%—bets in a protected edge organization reporting directly to the CEO. Peter compares this structure with Lockheed’s Skunk Works and Steve Jobs moving the Mac team off campus.
An audience question asked why X does not produce 100 baby moonshot companies a year. Teller said the limiting factor is culture engineering—intellectual honesty, humility, teamwork, and long-term thinking can be made adaptive among a few hundred people, but he does not know how to preserve that microcosm among thousands.
4. AI lowers experimentation costs without replacing the human mandate
Teller resists making AI the headline: pitching “we use AI” is like pitching “we use electricity.” Every moonshot, he says, combines people and agents, but the obsession remains the actual problem—clean water, grid storage, education, the electric grid, or preventing trillions of dollars a year from reaching landfills.
Teller hopes AI will shorten the time from a crazy idea to evidence that it is no longer crazy, while allowing X to raise its audacity and accomplish more in less time. The basic moonshot-factory structure, he says, should remain the same.
On X’s current clean-water effort, the salary bill remains larger than the AI bill, though Teller admitted he did not know the ratio. Automation will expand wherever it produces real benefit, but “spinning up an agent” is not synonymous with creating value.
Nor does he expect a fully automated moonshot factory within the next decade. Humans still choose problems and ensure solutions are socially acceptable, distributable, and welcomed by communities; those functions will require humans for “at least the next decade or two.”
X constrains ambition with a commercial clock: move from crazy to demonstrably not crazy in less than a decade, then reach an enduring business in less than another decade. Teller would hear a Mars proposal, but his test would remain: how does it become a durable business in less than two decades for Alphabet, X’s investor?
5. Killing projects early is the factory’s central compounding advantage
Teller’s monkey-and-pedestal analogy targets performative progress. If the mission is teaching a monkey atop a 10-foot pedestal to recite Shakespeare, teams instinctively build the easy pedestal; X insists they train the monkey first, because the pedestal can always be built afterward.
The point is learning speed, not failure for its own sake. Teller wants teams optimizing X’s portfolio, not protecting a beloved teleporter for five years after it becomes a zombie: “You learn nothing when you’re right. You only learn things when you’re wrong.”
One current experiment has produced a result that “would be a problem for physics” if correct. Five months in, the team is working “ferociously hard” to discover how it is fooling itself—a confidential, cold-fusion-like anomaly that leaves Teller both “deeply uncomfortable and deeply excited.”
His asymmetric rule is deliberately severe: a false positive can consume many years and many tens of millions of dollars, while rejecting a genuine moonshot costs X zero if problems and possible solutions are effectively inexhaustible. Hence the counterintuitive conclusion: X probably still does not say no quickly enough.
Full transcript
Good to see you, Ganesh.
Thanks for having me.
It's a pleasure, pal. We've known each other for God knows how long—a couple of decades now. I think most people don't know something about you, and it's worth mentioning.
Just for fun, since we're talking about genetics, his maternal grandfather was a Nobel laureate in economics, and his paternal grandfather was Edward Teller, the creator of the hydrogen bomb. It's a pretty interesting fact.
No pressure.
No pressure.
It was a high-pressure childhood, yes.
Yeah, I guess so. Let me kick off the first question. You've been in the moonshot business for over 20 years. Walk us through your advice on what it actually takes to come up with a moonshot and launch one. How do you make this real?
We've got a lot of individuals here who are here because they believe in optimism and moonshots. In 10 seconds—no, just kidding—what's your advice? I mean, you've learned so much.
1. The Moonshot Formula
Let me give you two quick things. The first one is, let's just define moonshot, at least how we think of a moonshot.
Which is how I think of it as well.
Excellent. So—
I learned from you.
So, 3 basic components. First, there has to be a huge problem with the world that you can name and you want to solve. If you can't name the huge problem, then it's arguably an academic exercise.
Second, there has to be some kind of science-fiction-sounding product or service that, no matter how unlikely it is that you could make it, we could pre-agree that if you made that science-fiction-sounding product or service, it would resolve that huge problem with the world.
And then, 3, there has to be some kind of breakthrough technology that gives us a prayer—at least a tiny chance, at minimum—of being able to make that science-fiction-sounding product or service and resolving that huge problem with the world.
When you have that, we would call that a moonshot story hypothesis. That does not mean you're going to win, but at least it means it's testable.
The second thing I would say is, one of the fundamental issues that we found at X is that you have to have 2 things in equal amounts in order to be a moonshot explorer, to be a moonshot team. The first one is, you have to have very high audacity. You have to be willing to suspend your disbelief for non-stupid reasons and go on unlikely journeys that might actually profoundly help the world.
But the second thing you have to have, in equal measure, is humility. You have to know from the first moment you set out on that unlikely journey that it's unlikely. Because if you don't, you will go ruinously far down that path before you find out that that is one of the 99% that just isn't going to work out.
So being able to say right at the beginning, "I'm proud that I'm trying this, but it probably won't work. Let me learn as fast and as cheaply as I can whether this is even possible," allows you to get onto the next moonshot when that moonshot's not the right one to do.
Hmm.
Hmm.
So your advice for folks—I mean, the challenge of picking a moonshot, given the speed at which you can test and create things, right? But what about the beginning, choosing the idea? Any advice there?
Put it this way: What do you do to shut down an idea quickly?
2. The Technoeconomics Test
Sometimes the idea is just not big enough. Sometimes the idea is too reasonable or too likely to succeed. Sometimes it's just not good for the world, or the potential for too many secondary problems associated with it is just too high.
Often, it's techno-economics. I cannot tell you the number of moonshots that feel so good to people in the early days. Often these are very technical people, and it's not until you say, "Really? Let's go step by step. What is the best-case scenario for the bill of materials that you would make this from? What is just the raw cost and weight of the stuff that would go into that? What are people really going to pay? Could this even plausibly—"
Zero, zero. You know, what does Elon call it? First-principles thinking in that regard.
Right. First-principles thinking about the techno-economics. You can often kill moonshots in the very early days because it's just not going to turn into an enduring business, and at least what I believe is that purpose and profit can support each other, and that if you're doing something that's going to lose money, it's probably not going to change the world.
Yeah.
Hmm.
Dave?
Yeah, I'm really curious about—Alex and Peter have this solve-everything book, which is phenomenal—but the rate at which physics, materials science, and chemistry are going to change is just astronomically accelerating.
So when you joined Google—what, 25, 23 years ago? How long ago?
16 and a half years ago—
16.
I co-founded X 16 and a half years ago.
16 and a half years ago, okay. And at the time, it was about a $30 billion company?
Ish, yes. It was very sweet. It was very small back then.
Very tiny, little $30 billion company. Now, just about a half-trillion-dollar company. So the scale of R&D in a corporate environment like that has grown miraculously, just absolutely tremendously.
And I think you were saying backstage that the ideal target for a new idea is 100 ideas a year, with 2 of them succeeding?
That's right.
Okay.
We start 1 to 200 ideas a year that make it far enough that they end up with a code name. Who knows how many we actually look at? But 1 to 200 ideas a year that make it far enough would get a code name. Of those, about 5 to 6 years later, we graduate 2 moonshots out of X.
Wow.
Got it.
So, a 2% hit rate.
And so then, if AGI is imminent—
And the idea rate—
No, it's here.
Astronomically. Right. Does that grow on that same exponential curve? Does the number of things at the front of the funnel go from 100 to 1,000 to 10,000 to—
3. AI Reshapes the Moonshot Funnel
Oh, for sure. There's no shortage of problems with the world. There's no shortage of creative ideas for running at those problems. I think AI is going to somewhat shrink that time from a crazy idea to us having de-risked it to the point where we can say definitively, "Here's evidence it's not a crazy idea anymore," so that's getting shorter.
Yeah.
I hope that AI is going to let us raise our audacity even higher, so we'll be shooting higher, and so we'll be able to do more in a shorter amount of time. But fundamentally, I think the structure will be the same.
But I think, if you asked me 3 years ago what the big things were that came out of X, Waymo would be at the top of the list. But now—
Google Brain.
But yeah, now—so I was going to ask about it. Google Brain was probably, like, "Yeah, this is cool," up until some point a couple of years ago, when it became, "No, this is the entire future—
Yeah.
—of Google now."
You guys just spent 80% of the last 3 hours talking about the stuff that arguably Google Brain sort of birthed into the world.
What is Google Brain? Define it, because we—
Yeah.
—we know DeepMind, but we don't know Google Brain.
So Google Brain, which started at X about 15 and a half years ago, was one of the earliest things that we started.
Yeah.
At the time, there was a set of academics who were kind of out of vogue. This was Andrew Ng, Yann LeCun, and a few others, who were saying, "I think scale might matter."
Neural nets were absolutely dead in the field at the time, and they were saying, "I think scale might matter, and it might actually bring neural networks back." And everyone else in the field said, "Nope, you're crazy."
Andrew Ng came to Google X at the time, and we set up what was called Google Brain with Jeff Dean. So the 2 of them paired together to say, "What if we industrialized neural networks? What if we made them tens of thousands of times bigger than anyone had ever done before? Could that actually be the breakthrough that everyone's been waiting for?"
So we were the first ones who really made what—
Fast-forward—
—got called—
Yes.
—deep learning. TPUs ultimately came from Google Brain. The transformer, which underpins everything—it's literally the T in ChatGPT—came from Google Brain.
So, our job is to make the seed crystals that ultimately go on to change the world, and I think Google Brain counts as one of those.
But there must have been a long period of time there where that was kind of quaint and promising, and then a period of time just recently where it's like, "Holy crap, that was a lot more than quaint and promising."
Of course, but I think the reality of any innovation is it takes a super long time. Every single innovation is like an overnight success that was 15 to 20 years in the making.
Right.
An overnight success after 11 years of hard work.
Yeah.
For sure.
Yeah.
So, Astro, you've watched hundreds of moonshots and evaluated hundreds. What are a couple of examples of moonshots that you would have loved to see come to fruition but that didn't quite make it, didn't cut the mustard, or whatever?
I have a very long list. I'll give you 2 examples, but—
Sure.
4. The Moonshots That Keep Failing
We've been working on clean water over and over again. If you can make clean water—if you could pull it from the atmosphere, if you could desalinate for a tenth the price—you have to be able to get to about a penny a liter in all-in cost for it to really change the world. But we have almost 3 billion people in the world who are water-stressed—
Yeah.
—who don't have clean water to drink. That's going to get worse as climate change picks up. We're going to have hundreds of millions of climate refugees around the world, and it's often going to start because they don't have enough clean water. This is one of the biggest problems to solve.
Hmm.
But technoeconomics—we've done some great work in this space, but it's going to be 10 cents a liter. Nope. We'll stop doing that. Try it again. So that's an example of something we keep coming back to.
Got it.
And 2 more.
Two more.
Okay. Being able to time-shift and location-shift energy—and I say it that way on purpose—
Hmm.
—because if you say transmission lines and batteries, people tend to narrow their focus in. But being able to time-shift and location-shift energy is absolutely going to change the world. We've taken a bunch of runs at those. So far, we haven't been super excited with what we've found.
Education is another one. Education is not working. It's not working in the developed world. It's not working in the developing world.
Standing ovation.
We're going to keep coming back to that one until we find something, because that has got to be one of the most fundamental moonshots that you could do.
Got it. Love it. Alex, please.
5. The Great Moonshot Stagnation
Yeah. I'd love to talk a bit about the history of moonshots. One of your grandfathers invented the hydrogen bomb, and if you look at history—and I should add, maybe humanity was in the process, once upon a time, of landing humans on the Moon in actual moonshots, and then that stopped.
Sometime—you can quibble over the chronology, but arguably, depending on which version of the great stagnation thesis one subscribes to, there was maybe up to a 50-year period, call it 1970 to 2020 or so. Again, one can quibble at the margins. It would seem that there was a reduced launch velocity of moonshots from humanity as a whole. We stopped landing humans on the Moon. We stopped inventing arguably applied physical innovations, regardless of their warfare potential or not, like hydrogen bombs.
Then, again arguably, sometime around 2020 or so, plus or minus a few years, moonshots started again. We got superintelligence that actually works. We're getting robots that actually work. Physical intelligence, so-called, is seeming to work. We got arguably medical nanotechnology in the form of lipid nanoparticles that helped to treat a pandemic.
So, a few related subquestions. One: Do you believe—do you subscribe to any variant of a great stagnation hypothesis, that there was a half-century pause in moonshots? And to the extent you do—
Another question: How do we prevent that from happening again?
Well, the first thing is, I know you didn't intend it that way, maybe, but I'm going to take that as an enormous compliment and an 11-year-in-the-making joke that we just made. Since we started in 2010, and you said 2020 several times, exactly my point is that we started literally a moonshot factory in 2010—
I see. So your answer is you brought moonshots back.
Yes, to some extent. I would like to think that we did.
Woo!
And so that's the first half of the answer. Yes, I do think that—I don't know. I don't think anyone was planning on it being a stagnation, but I think functionally we had lost our way a little bit.
Somewhere between the 1960s, NASA, and the inspiration that created, there was a period where we sort of lost the explorer spirit.
Yes.
Somewhere between—you had your Star Trek stuff up here a little bit.
Well, what do you think—
What do you have—an ideology, a diagnosis? What do you think went wrong?
I don't know, but here is a partial answer to that, and then I want to get to the future.
Yeah.
Can I tell you all a dirty little secret?
It'll be our little secret.
Taking moonshots is really, really easy.
Huh.
It's laughably easy if you don't care about efficiency. You just find some super-energetic people who are delusionally optimistic, pour a bunch of money on them, and you will absolutely get some moonshots. It's just not a very good return on investment.
I think we had a period, mostly because of World War II and the Cold War, where people didn't care about the return on investment.
Yeah.
Then there was a period where people probably still wanted moonshots, but they cared about the return on investment.
Mm.
And so there was less of it. What X has been trying to practice is making a moonshot factory, being able to get at that audacity efficiently enough to systematize the process—not just to do it a lot, but to do it efficiently so it is rational for people to put a lot more money in.
And to your point about the future, good news: I think we get approached now on a weekly basis by some large company or some country saying they want to set up their own moonshot factory. I'm not sure exactly how we can help them with that, but there is a hunger to do more of this. So, good news, I expect you'll see a lot more of it in the future, not just from us.
But Astro, take a second. There are a number of people here in the audience who are running companies that do want to set up a moonshot factory. We have discussed a little bit about this, right? Let me paraphrase what I've learned from you. You're my moonshot mentor here.
Your core organization is responsible for delivering 10% profit year after year. Salim and I have written about this: Your moonshot factory, if you will, needs to be on the edge of the organization, where your crazy thinkers exist, right? And, again quoting you, you know, “If you work on anything at 10%, you're fired. Focus on 10X—1,000%,” and then have that side moonshot organization report directly to the CEO. Is that still a formulation?
Absolutely. I've run the following experiment. I apologize to Peter, who's heard this a bunch. Salim's probably heard it a few times too, but just bear with me for 45–50 seconds.
Choice A, choice B. Choice A: You can give 1 million dollars of value to your business this year, and it's guaranteed. Choice B: You can give 1 billion dollars of value to your business this year, but it's not guaranteed. It's 1 chance in 100. So, A: 1 million guaranteed. B: 1 billion, 1 chance in 100.
Who's choosing choice A?
All right. Almost nobody here—almost nobody in the world—raises their hand. Who's choosing choice B?
Woo!
All right, so you all pass the math test, because it has 10 times the expected utility. I've done this with CXOs the world over, and I've said, “Okay, now keep your hand up if, on their best days, in your wildest dreams, your manager, your CEO, your board of directors—
Right.
—actually supports you doing choice B.”
Yeah.
And every hand in the room goes down.
Goes down. Yeah.
And I say, “You don't need a lecture on innovation. You need a new manager.”
Yeah.
So the formulation—
That can do math.
The formulation you just described is exactly right, and it's—
Yeah.
—because of this thing: You have to sequester the choice Bs to a place where they're actually wanted, and where the mess that comes with them is tolerated.
This is Lockheed's Skunk Works off on the edge. This is Steve Jobs taking the Mac team off campus to build it.
Yeah. Yeah. Exactly.
Yeah.
The capability of the human mind to do this is very hard. There's something I've been observing over the last few years, and I'd love for you to comment on this.
Peter wrote about this in one of his original books, The Demonetization of the World, right? Throughout human history, it's always been true that advanced technologies cost a lot. And today, for the first time in human history, advanced technologies are cheap. So solar energy: cheap. Sensors are cheap. Blockchains: open source and free, et cetera, et cetera.
This should enable a CFO or a big company—when you want to do something very disruptive, you used to have to make a big bet, put a lot of resources in, and the CFO hated you. They would defund it as fast as they could. Today, you can take a portfolio of very disruptive experiments at the edge, so now it just comes down to mindset and whether you're willing to go for it.
Do you agree with that? And how much are you seeing companies do that?
I do agree.
I hear a lot, “Oh, well, Alphabet has lots of money, and so that’s why this is happening.” I guarantee you that is not why. We have tiny teams. The teams that graduate from us—Google Brain had about 18 people when it graduated—and that’s pretty normal. We keep our teams tiny.
Interesting.
I say to them all the time, “I want you to find a cheat in the video game of life, a Gordian-knot-chopping moment. If you can’t find that, I don’t want you solving things the normal way.”
Mm.
“I’d rather you stop and we go find a different moonshot,” because that’s what moonshots mean.
Mm.
So I believe it is mostly a mindset issue. And for those of you out there who are interested in learning more, we did a master class certificate course. It's about 20 hours if you do all the work. It's about three and a half hours if you just watch the videos. I encourage people to go watch. It's on breakthrough innovation, and it will step people through. It's ... Our secret sauce is not secret. We're telling people exactly how to do it.
And tonight, Astro, there's an evening program by your team—doing a 50-minute condensed version of that, you know, you know, 10-hour course.
Exactly. 7:00 tonight, Joe Sargeant. It's gonna be a lot of fun. It's on rapid prototyping.
Amazing.
I’d also love to better understand and develop the record on the economics of moonshots. On the one hand, I could make an argument that the real cost of moonshots increases over time because expectations go up, and we see weird-ish problems solved left and right by people sitting on the toilet, casually solving hard problems. I could make the argument in the opposite direction—that the real cost of achieving a moonshot is hyper-deflating because we have superintelligence now, and we can solve lots of hard problems. I could probably make some sort of mediocre, middle-of-the-road argument as well. What would be your position on the long-term economics of the real costs of moonshots: hyperinflating, hyper-deflating, or staying the same?
We track what it costs for us to get to our graduates very carefully because we’re obsessed with the efficiency of getting at moonshots, and I can tell you that it’s down by about a factor of 3 over the last 16 years.
Mm.
There’s a lot of waste and complexity, and it’s a bit of a lagging indicator.
Wait, wait. That’s inflation.
No, no. It is a factor of 3 cheaper, just to be clear.
Okay. But a factor of 3 over 16 years sounds to me like 10% per year, right? Or at least market returns. It may be market returns.
Well, we’re talking about 2 different things.
Yeah.
I’m talking about the cost to get to a Waymo. I guarantee you the value of the Waymo is so huge relative to not only the cost of developing that team but also developing all of the other things that didn’t work. It is a very good return on investment, so I’m not worried about that. I’m looking at what it costs for each individual thing that makes it all the way through our process—
Right.
—and that is getting cheaper at, I don’t know, 10% to 20% year over year, something like that. Some of that is because we’re getting better at our job. Some of that is because we’re graduating things a little bit earlier. A lot of it is because of artificial intelligence, so it’s a mix of all of those things.
But it’s cheaper to get to moonshots now than it was in the past.
So maybe, just to develop this a little bit more, some would argue that to solve some of the grandest challenges in science and engineering, it’s not going to be a one-shot, spiky-capability launch. It’s going to be the result of our economy’s macro growth: We grow the capacity of our economy holistically, and that enables particular moonshots to become easier. When I hear you say 3X cost reduction, presumably in real terms, over 16 years, that to me sounds basically like just the result of markets doubling, say, every 10 years. The stock market doubles every 10 years. So the result of the reduced cost of moonshots sounds to me like basically just our economy is capable of more things, and it’s basically the same cost.
I disagree. I think you’re confusing the cost to paint a house with the value of the house. They’re like apples and oranges. They’re not the same thing.
Okay.
I’m talking about how cheap it is for us to paint our house—
Well—
—not what the world will pay for the house afterward.
Why stop at 2 moonshots a year, Astro? Why aren’t you pushing out 100 baby moonshot Alphabet companies per year? I mean, this is about 10X growth, right?
True. Again, if all I cared about was moonshots and I didn’t care about efficiency, I guess we would do that. Because I’m obsessed with efficiency, there’s a cultural rhythm and a set of habits that are really easy to describe but fiendishly hard to get people to practice.
Mm.
Things like playing the long game, being intellectually honest, showing up with humility, being a team player, and not being an egomaniac. Everyone’s like, “Yeah, yeah, duh, everyone wants that.” But just take a moment and ask yourself, super honestly: Is that how your organization really functions today? Right. I can hear the laughter because it isn’t. It’s not your fault, but someone would have to be maniacally determined to create a microcosm in which those things were actually the adaptive behaviors in order to do that. That’s what I’m maniacally focused on—
Mm.
—creating the culture engineering necessary to get people to practice the habits—
So important.
—that drive innovation efficiently. Unfortunately, I know how to do that with a few hundred people. I don’t know how to do that with a few thousand people.
Interesting.
It’s a culture problem that I just don’t know how to solve.
But Astro, aren’t you making the argument, then, that the ultimate moonshot is the meta-moonshot of solving the organizational problem of launching more moonshots?
Yes. I’m going to connect your question with the way I think about it. I would say the meta-moonshot—we often talk about the meta-moonshot—is how to systematize radical innovation.
Right.
So, to your question, there is a meta-meta-moonshot, which is how to systematize systematizing radical innovation.
There you go.
How to copy and paste moonshot factories.
Yeah. There you go.
Which brings me back to what I was saying before: The world is coming and asking us that. We would love to help. I haven’t yet figured out how to do the meta-meta-moonshot, but we’re excited to help.
Organizational singularity, Salim.
Yeah.
Yes.
I think we might have that methodology for you because we’ve been building for 10 years a societal layer. We’re now 50,000 people globally, focused on how to actually create an environment where you can spin off these things very, very quickly. So I think there’s— It’s almost like you’ve solved the inner few layers of Stewart Brand’s pace-layer thing, and we’ve solved the outer few layers.
Oh.
We should talk offline.
Well, I’d like to take your exact quote and say, “Look, dirty little secret, everybody: Doing a moonshot is really, really easy. You take fanatically focused people who care about a mission, who are really, really smart, and you pour money on them.” Great. Now, there will be a world where you swap out the people and you swap in AGIs, and you take out the money and you pour compute on them. That world isn’t here yet. There’s got to be some transition world we’re in right now where there are 3 AIs and 3 people, and you pour compute and money on them. And then there’s another ratio, and there’s— Have you started down that journey yet?
Totally. I’m going to connect your question to a side rant. On the one hand, if someone came to you and said, “I want to pitch you my company. Are you ready for my pitch? We use electricity,” you would think I was nuts. On the one hand, you’d be frightened if I didn’t use electricity in my business, but you’d be like, “So what? That’s an implementation detail. What are you doing?”
Yeah.
I feel the same way about AI. I actually try to say AI as little as possible because it’s driving me crazy the way I—
We should say SI now.
Yeah.
Superintelligence.
Sorry, I got a PhD 30 years ago in artificial intelligence, so I’m a little stuck on that one.
Okay.
Me too.
But on the one hand, what you just described—every one of our moonshots, that’s it. It’s a bunch of agents and a bunch of people working together to try to solve a problem.
Yeah.
That’s an implementation detail.
What we're obsessed with is the problem, whether it's clean water, a way to make grid-scale energy storage, education, how to fix the electric grid, or how to make our world actually circular so we're not sending trillions of dollars a year to landfill. Those are the things we're obsessed about. Then, in the background, it's humans and agents making it happen. Most of our obsession is the problem and how to couple that into a business so that it gets bigger over time and doesn't cost too much.
Let me translate that into a budget question. If you said, “Clean water is a great one, a great moonshot,” what was it—a penny a liter, you were saying?
About a penny a liter to really change the world. Yeah.
Okay. So that's a great moonshot. Have you already got a team on that one?
We have had teams on it in the past. Yes, we do have a team on it right now.
Okay.
To be fair, yes.
What's bigger, their AI bill or their salary bill?
It's still their salary in that particular case. But I don't know by how much, honestly. So I don't know what fraction it is for sure, but I would say they are absolutely teammates in the process—
Yeah.
—of innovation.
So that's what I'm getting at.
And in fact, we are finding ways all the time to automate parts of the moonshot factory so we can go faster and be more efficient.
So your best guess, if you're hyper-focused on the efficiency of that innovation machine, there's a case study. Right now, their AI bill is smaller than their headcount bill. When's the day when it hits 50/50, 75% AI, and then 100%?
Well, first of all, I'm not sure that at any time in the next decade it's going to be 100%.
Okay.
Because I think figuring out which problems to solve and making sure they're being solved in societally acceptable ways is an important part of the problem. If you need distributors to help sell this, if you have to land it in communities in ways that those communities feel are acceptable to them, you need humans as part of that process for at least the next decade or two.
Okay.
But look, it'll go as fast as is efficient. We're not going to use compute just to use compute, and there are people who are spinning up agents because it feels powerful to spin up agents. But there is a difference between spinning up an agent and actually getting a benefit.
Mm-hmm.
Astro, you—go ahead, Salim.
Yeah. I think of moonshots as two classes.
Okay.
One is pain points: solve hunger, solve education, solve whatever. And then there are the aspirational moonshots: Elon, get us to Mars; solve aging, et cetera. How much of your work in moonshots focuses on one versus the other? Is it an equal balance, or do you focus only on the problem side?
I mean, if you worked at X, what I would say is, “Gee, Salim, can't I have both?”
Yeah.
I want you to find the most audacious things you can work on that we can move from crazy idea to not-crazy idea in less than a decade, and then from not-crazy idea to an enduring business in less than another decade. So if you want to go to Mars, I would start with—
Got it.
—“Okay, I'm listening. How is that in less than 2 decades—
Right.
—going to be an enduring business?”
So it's—
I'm not saying it can't, but that would be my test.
So time—you're constraining yourself just so you can give a sense of whether we can reliably work on this problem over this next decade and spin out something. That becomes the main criterion.
Because I'm getting money, our investor is Alphabet. I have to tell Alphabet, “Here's what I'm doing with your money,” and they have to feel good about the sort of flywheel that I'm creating for them that—
That makes sense.
—I have to create.
Astro, one of the things I find fascinating is the fact that you kill the vast majority of the ideas that are started. Just to give us some numbers here, total number of projects started versus graduated—is it under 1%?
I think it's close to 2%, but call it 2,000 things over the last 16 years that got code names, of which we've had, depending a little bit on how you count, 35 to 50 graduates.
So talk about this idea of the importance of killing your babies early. No, not his actual baby brother.
6. The Monkey Pedestal Test
Yes. I'm going to use the monkey-and-pedestal analogy, which I know you know well.
Please, I love it.
But imagine we were working on a moonshot together, all of us, and we're trying to get a monkey to stand on the top of a 10-foot pedestal and recite Shakespeare. Which should we do first: train the monkey or build the pedestal?
It is so weirdly tempting, if we're being honest with each other, when it's not that extreme a situation, to build the pedestal, because then you're half done, and you can get another round of funding and live to fight another day. You can go to your boss and say, “Can I have a promotion? I'm half done, man. Can I have a bonus?” This is what drives the world, and it drives me crazy.
So what we say at X is, “Forget the pedestal. Only focus on the monkey. If you can train the monkey, we can always build a pedestal afterwards, and if you can't train the monkey, thank God we didn't waste Alphabet's money and our time on that.” And so it's not that I want to lose. I'm like the crown prince of failure, but it's not because I like to fail. It's because you learn nothing when you're right. You only learn things when you're wrong.
I love it.
Crown prince of failure. Love it.
And so if you accept, which it sounds like you do, that that's true, and moonshots are a process almost entirely taken up with learning, then we're going to go on an adventure which is defined entirely by how fast we learn. That means if we in any way feel bad in the moment where we learn because we had a model of the world that turned out to be wrong in some way, then we will unconsciously, or maybe even consciously, avoid that moment.
So we're going to destigmatize failure. If you work at X, I need you to be on the mission with me to optimize X's portfolio. It's not that I don't want the teleporter to work, Peter, who's working on this for me, but I want to find out as efficiently as possible if it's going to work.
I don't want you in denial about the fact that you just really want the teleporter to work, and we go for 5 years, and we spend tens of millions of dollars, and it's still kind of going sideways, and it's a zombie. How many of you here have spent at least 5 years on something that was a zombie, where you knew for at least 2 or 3 years that it was a zombie?
Yeah.
What's the worst failure—the failure where you were like, “That's really crazy,” and it turns out that really was really dumb?
Oh, we've had lots of those. We have one right now which is almost certainly wrong. It would be a problem for physics if it turned out to be right. But it's working. We do not know why it's working in the lab. We're working ferociously hard to find why we're kidding ourselves so that we can kill it off.
But it's about 5 months into trying to discover this sort of cold fusion moment, which I hate. Cold fusion: it's not cold and it's not fusion.
It's okay, guys. It didn't work anyway. It's all right.
But we don't want to be that group, right? We are trying to be the opposite of that group.
But you're not going to tell us what this thing is?
Nope.
Oh, come on.
But—
Okay.
If it works out, we'll tell you about it.
Time will tell.
But we have one right now that makes me deeply uncomfortable—
Now I'm so curious.
—and deeply excited.
Okay. A couple of audience questions here. Rich asks, “Are there any moonshots that you regret denying in the past, as our world's problems have changed, that you would pursue today?”
I mean—
Oh.
We were wrong a bunch. So I'm about to say no to that question, but I do not want that to be confused with “We've never been wrong.” We're wrong all the time.
But I think the question, though—
But—
The question—
I know. Do I regret it, though?
But was it something that you rejected and never even tried?
Exactly.
Okay.
So I want to be really clear. The cost for a false positive, where we believe it's a moonshot, we run it for many years, and then it turns out not to be, is very high—many tens of millions of dollars, potentially.
Yeah.
The cost of a false negative, where it actually is a moonshot but I rejected it, is zero. As long as you believe that there's an infinite number of problems in the world and an infinite number of creative solutions, we can always just go draw again from the distribution of moonshots.
Right.
It costs us nothing to say no. So I say no and have no regrets, even about the stuff we were wrong about.
We probably don’t do it fast enough.
Paul asks, “What about moonshots in materials science? Do you see any particularly promising fields to inquire about in that area?”
Well, side rant: I’m super excited about the new materials space.
Yeah.
I think people haven’t played it out in their minds, because there’s such a fervor about the technology, and everyone’s like, “And then we’ll make a business out of it.” That’s harder than it sounds. Look how many centuries it took for us to really refine steel. Steel completely changed the world, but not until it was industrialized in a bunch of ways.
Mm.
There are a lot of new materials that, if you could make one flake of room-temperature superconductor, that would be pretty cool. Nobel Prize, yay. That is not a business. That’s like the first 5% of a business. How do you make thousands of tons a day of that material? How do you make it with very high ductility so that you could put it into winding wires and things like that?
Yeah.
All of the stuff that it takes—the other 95% of the work—for new materials or otherwise, that’s what it really takes to make a moonshot. So I’m super excited about lots of things like new materials, but I’m focused on the hill after the one that people are focused on, which is, how would we scale these up as they show up in the world, not just how do we find them in the first place?
All right. Last quick question from the audience, and a quick answer, hopefully. Other companies keep trying to replicate X and fail. What’s the single hardest piece for them to replicate that you think most outside observers still underestimate?
I really believe it’s what I said: You have to have a leadership team that is maniacally focused on engineering a culture in which people can show up in the ways that tend to drive radical innovation most efficiently.
It’s obvious. You all know what it is. It’s making that space, that protected space for those explorers. That’s the really hard part.
I would like to say something to answer that question. You’ve created a mechanism where you’ve structured it such that the mothership has left you alone for a long period of time. I’ve never seen another company do it. Every other company I’ve ever seen, over time, the immune system cannot resist, reaches out its sticky little hands and snatches it back, and then messes it up invariably.
So congratulations to you for having lasted this long, and congratulations to the Google executives who’ve left it and had the discipline to leave it on the edge, because that’s where all the magic happens.