A Product Market Fit Show | Startup Podcast for Founders
00:23:12 · Astro Teller
[00:23:12] S0: Often things will not make it to that sort of, the ones that get a code name. Because nobody believes in it strongly enough to spend at least fifty percent of their time on it. People can't describe it crisply in terms of those three things I just described. Huge problem with the world, radical proposed solution, breakthrough technology. Where it feels like now there's something there. But sometimes people, for example, will say what it is, but they haven't figured out how to make it a testable hypothesis and you saying, hey, the world might be like this in the future, is like, yeah, you might be right. But that's not what we do. We do not fund things for five years so you can go try it. We're going to fund this for like five weeks, maybe five months. Which is easy for us because you're part of X, right? We don't have to incorporate anything and you're almost certainly wrong. So spend the next month or two trying to get one piece of information that tells us whether you're a little bit more wrong than we think or a little bit less wrong than we think. But if you don't have a testable hypothesis, we can't even get onto that flywheel. So that's another reason. Sometimes someone will have a really interesting proposal, but we just don't have the right labs for it, and we can't find someone who does, or sometimes something will go dormant because we're like, hey, that's a really cool idea. We need this physical lab. Hey, Caltech has that lab, and then we end up spending a year in slow motion just working with some university to have them let us use their lab. So then we're spending almost no time on that, just sort of waiting for the contract to come through and then it comes back to life. So very different reasons. But ultimately, the question is never, I have to prove, as the captain of Moonshots, that your idea is physically impossible. Almost nothing is physically impossible. It's actually more like you have to prove that your idea has a better reward risk ratio than the other things that we're currently looking at, and I would actually say it's reward divided by risk. Which includes all the costs and time, relative to how cheap or expensive it is to answer each question about, hey, what did we learn this week? Hey, what did we learn this week?
00:25:24 · Astro Teller, Pablo Srugo
If the reward risk ratio is okay, and it's going to take us a million dollars to find out the first piece of information about whether we're on the right track, not worth it. Reward is ginormous, risk is pretty big but we can find out for $100,000 whether this is a little bit less crazy than we thought. Yeah, I'll play that game all day long. [00:25:44] S2: I'm going to ask you for a small favor, a tiny little favor. In fact, now that I think about it. It's not even really a favor for me. I'm actually trying to help you do a favor for you. Just hit the follow button. You won't miss out on the next episode. You'll see everything that we release. If you don't want to listen to an episode, you just skip it. But at least you don't miss out. Tell me a bit about that next step, maybe give me an example of this testable hypothesis. Because I think that's a huge learning for founders. A lot of founders are not like me, by the way, and they have many ideas. A lot of ideas, and what they're not good at is, how do I kill it? How do I, as quickly as possible, in a week, two weeks, four weeks max. Kill it, move on to the next one, and go all in on the thing that actually shows the most promise. A subset of what you're doing.
00:26:28 · Astro Teller, Pablo Srugo
[00:26:28] S0: I'll give you an example, but first, bear with me for a very short story. Because this is how we talk about it here at X. So for a long time, I would say to Xers, obviously, we should work on the riskiest part of the problem first and pretty much everybody at X said, I'm pretty sure that's wrong, Astro. And I said, no, that's what we should do. And we just were not connecting on this. And then, I was at a Wall Street Journal live conference about eleven years ago on stage, and I said, we obviously should work on the riskiest part of the problem first. And the interviewer said, I'm pretty sure that's right. I don't think that's right. What do you mean? So in a moment of hyperbole, I said, look, let's say that our collective project was to get a monkey to stand on the top of a 10-foot pedestal and recite Shakespeare. Which should we do first in this somewhat extreme situation? Build the pedestal or train the monkey? In this extreme situation, we can see that if you built the pedestal, you're half done but you're really zero percent done at burning down the risk. [00:27:28] S2: That's right.
00:27:28 · Pablo Srugo, Astro Teller
[00:27:28] S2: That's right. [00:27:29] S0: The point of a testable hypothesis, especially at X. Everyone at X will just say as shorthand to each other, what's the monkey? What they mean by that is not just, do you have a testable hypothesis but how is the thing that you're doing now attempting to burn down the risk on the riskiest part of the problem? Because if you can't train the monkey, you do not need to build the pedestal, obviously, and in a much more subtle way for every moonshot we have here. How scary is making this thing physically? Oh yeah, if we're really honest, we're going to be able to do it. How cheaply can we make it? Oh yeah, that actually could be the scary part. Okay, if the scary part is the techno economics. Let's not wait. Let's get really crisp about what has to be true. Maybe you can just do a bunch of spreadsheet math and kill the project on the basis of, okay, almost no matter how good we make each of these ten pieces. We're going to have to jam them all together. Yeah, the numbers are just not going to pencil out. This is not going to be competitive. Great, kill the project, move on. Sometimes it's actually how people will use something. Sometimes it's a safety issue and sometimes the solutions. In the very early days of Wing, we spent so much time trying to think about safety and make it safe with a very small number of propellers. [00:28:55] S2: And Wing, for those who don't know, that's the drone delivery.
00:28:55 · Pablo Srugo, Astro Teller
[00:28:55] S2: And Wing, for those who don't know, that's the drone delivery. [00:28:58] S0: Drones for package delivery. Until we got to the place where we said, what are we doing? These are literally hobbyist motors. They don't cost us that much. What if we just had a bunch extra? Then if a blade falls off, some motor stops working in the middle of a flight, we won't even notice. So safety was still really important. But all of a sudden, safety moved from being this complex control problem to something where for a very small incremental cost. We were just over actuated and then we had this defense in depth. And so safety then dropped as a risk. And then there were all kinds of other risks that we had to work on. [00:29:37] S2: So you find the biggest risk and you try and de-risk that. And if I understood you correctly earlier, if the biggest risk is going to take too much time, too much money to de-risk. That alone is a reason for moving on to the next one.
00:29:48 · Astro Teller
[00:29:48] S0: Yeah, but if you have a crazy idea about nuclear fusion. Okay, first, let's see if we can kill it on the whiteboard. If we can't kill it on the whiteboard, I guarantee you the next thing we're doing is not building something the size of a house to start doing plasma shots. We're going to build a simulator or find someone who has a simulator and see if we can kill it using the simulator. If it survives that process, maybe we have to build something the size of a house, but maybe we can even find someone in a university who can do a little bit of the de-risking with us even if it's only bits and pieces. And then when we get to the place, which we did. We closed this down about a year and a half ago. We had a fusion project. We ran it. We did build something the size of a house. We did almost a thousand plasma shots. We convinced ourself it was not going to change the world, and we closed the project down. But it was money well spent because we had removed all the cheaper ways to try that first. Speaking of which, we have a Moonshot podcast. If your audience wants to hear more about some of these stories. Really hear what it was like building Waymo or building Wing. Building this Fusion project. We now have two seasons out. If people just search for Moonshot Factory Moonshot podcast, it'll come up and I think people really enjoy this sort of deep dives. It's not just what it was like for us, but it's exploring with the entrepreneurs that have gone through X. What it felt like for them and what other people can learn about taking their own shots.