Astro Teller has a project at X that he expects to fail. He said it is "almost certainly wrong," and that it "would be a problem for physics if it turned out to be right." It is working in the lab anyway, and he said the team does not know why. So the team is doing what X usually does with a promising result: "We're working ferociously hard to find why we're kidding ourselves so that we can kill it off."
Teller co-founded X, Alphabet's innovation lab, and holds the title Captain of Moonshots there. He told the story onstage at Moonshots Live 2026 in a conversation recorded on September 25, 2026, and released on October 5 as an episode of Moonshots with Peter Diamandis. His interviewers included Peter Diamandis, founder of XPRIZE, and Dave Blundin, founder of Link Ventures. Over the conversation Teller described X's method in some detail. It is a system for producing a few successes, and much of its work goes into ending ideas early.
What counts as a moonshot
Teller began by defining the term, at least as X uses it. He said a moonshot has three parts. First, there is "a huge problem with the world that you can name and you want to solve"; without that, he said, the effort is "arguably an academic exercise." Second, there is a "science fiction sounding product or service" that everyone agrees in advance would solve the problem if it could be built, however unlikely that is. Third, there is a breakthrough technology that gives the team "a prayer, at least a tiny chance" of building it.
Teller calls this combination a "moonshot story hypothesis." It does not mean the project will succeed, he said, "but it at least means it's testable." X's published blueprint for moonshots sets out the same three ingredients. It describes the problem as one affecting millions or billions of people and asks for a breakthrough that offers a plausible route to a solution within five to ten years.
He said the people who pursue these projects need two traits in equal amounts. One is audacity: being willing "to suspend your disbelief for non-stupid reasons." The other is humility: knowing from the start that the journey is unlikely to succeed. Without that, Teller said, a team will go "ruinously far" down a path before discovering that its project is "one of the 99%" that won't work out. His recommended attitude: "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."
How an idea gets killed
Diamandis asked what X does to shut an idea down quickly. Teller gave several reasons. Some ideas are not big enough. Some are "too reasonable or likely to succeed," which means they do not need a moonshot lab. Some would be bad for the world or carry too high a risk of secondary problems.
Often, Teller said, the reason is techno-economics: whether the technology could ever work as a business. He said many projects feel good in the early days, often to very technical people, until someone works through the questions step by step. What is the best-case bill of materials? What is the raw cost in weight of the stuff that would go into the product? What will people really pay? Diamandis compared this to what Elon Musk calls first-principles thinking, and Teller agreed: "First principles thinking about the techno-economics." Teller said he believes "purpose and profit can support each other," and that a project that will lose money is probably not going to change the world.
Teller's 2016 operating manual for X gives an example. A project called Foghorn succeeded in making fuel from seawater. However, the team could not find a way to make it cost-competitive with gasoline within five to ten years. Stopping criteria agreed in advance helped the team shelve the technically promising work and free its people and money for other projects. The manual also describes how projects pass through stages. Early evaluations take weeks and a few thousand dollars. Funding and team size grow only as the major risks are reduced.
Train the monkey first
To explain why X attacks the hardest problem first, Teller used what he called the monkey and pedestal analogy. Imagine a moonshot whose goal is to get a monkey to stand on a 10-foot pedestal and recite Shakespeare. Should you train the monkey first or build the pedestal?
Teller said building the pedestal is "so weirdly tempting." It produces visible progress: you can tell investors or your boss you are half done, raise another round of funding, ask for a promotion or a bonus. "This is what drives the world. And it drives me crazy," he said. X's rule is to forget the pedestal: "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." He set out the idea in more detail in a 2016 essay, Tackle the Monkey First, which uses Foghorn as its practical example: making fuel was less uncertain than proving it could be cost-competitive, and the team ended the project when that economic hurdle stayed unresolved.
Making failure feel acceptable
Teller called himself "the crown prince of failure," then explained that this is not because he likes losing. "You learn nothing when you're right. You only learn things when you're wrong," he said. If moonshots are almost entirely a process of learning, he argued, then the adventure is defined by how fast a team learns. People who feel bad when their model of the world turns out to be wrong will avoid that moment, consciously or not. So X tries to remove the stigma from failure.
He illustrated the point with a teleporter project. He wants the teleporter to work, he said, but he wants to find out as efficiently as possible whether it will. What he does not want is a team in denial that keeps going for five years, spends tens of millions of dollars, and ends up with a project still "going sideways": a zombie. He asked the audience how many of them had spent at least five years on a zombie project after knowing for two or three years that it was one.
X has built habits around this. An essay on X's blog by Courtney Hohne, The Monkey, the Tiger Beetle and the Language of Innovation, describes several. Teams make deliberately rough early drafts, use "monkey" labels to focus reviews on a project's central uncertainty, run pre-mortems, and keep failure résumés. They also talk openly about grief when projects end.
The funnel in numbers
Blundin recalled Teller saying backstage that the ideal is about 100 ideas a year with two succeeding. Teller confirmed the rough shape. He said X starts 100 to 200 ideas a year that get far enough to receive a code name, out of many more it looks at. About five to six years later, two of those graduate from X, a hit rate of about 2%. Later Diamandis asked whether the rate was under 1%. Teller said it is "close to 2%." He put the total at about 2,000 code-named projects over the last 16 years, with "sort of 35 to 50 graduates," depending on how you count. Those figures work out to between about 1.75% and 2.5%.
Blundin asked whether artificial general intelligence, or AGI (AI as capable as people across most tasks), would make the front of the funnel grow from 100 ideas to 1,000 to 10,000. Diamandis interjected that AGI is already here. Teller said there is "no shortage of problems with the world" and no shortage of creative ideas for tackling them. He expects AI to "somewhat shrink" the time between a crazy idea and evidence that it is no longer crazy. He hopes AI will let X raise its audacity and aim higher, doing more in less time. "But fundamentally, I think the structure will be the same," he said.
Why saying no costs nothing
An audience member asked whether there were moonshots X had turned down that Teller regretted, given how the world's problems have changed. Teller said no, but first made clear that this did not mean X had always been right: "We're wrong all the time."
His reasoning is about the unequal cost of two kinds of mistakes. A false positive is a project X believes is a moonshot and runs for many years before finding out it is not. Teller said that can cost "many tens of millions of dollars." A false negative is a real moonshot that X rejected. That, he said, costs zero, as long as you believe there is an infinite number of problems and creative solutions to draw from. "It costs us nothing to say no," he said. "So I say no and have no regrets even about the stuff we were wrong about." His one self-criticism ran the other way: "We probably don't do it fast enough."
The result X is trying to disprove
That is the background to the project Teller described when Blundin asked about X's worst failures. The team is about five months into trying to discover what Teller called "this sort of like cold fusion moment," a label he said he hates: "It's not cold and it's not fusion." X does not want to be the group that clings to a result it cannot explain, he said; "we are trying to be the opposite of that group."
Blundin pressed him to say what the project was. Teller declined. "If it works out, we'll tell you about it," he said, adding that it "makes me deeply uncomfortable and deeply excited."