AlphaGo Took Two Years. AlphaZero Took Hours. Silver Is Making the Same Bet on Superintelligence

In March 2016, AlphaGo beat Lee Sedol four games to one. Behind that match sat about two years of work: a lot of human game records, then researchers in the loop, taking each generation, deciding how to improve it, and shipping the next. It was, Silver later says, somewhat similar to the LLM approach. A year on came AlphaZero. Human data was dropped. The system was left with the rules and an algorithm that could discover for itself. Once they got that algorithm right, it took a few hours to outperform the two years. In chess it took four hours to beat the best AI that had ever been created. In Go it took a couple of days. Two years of accumulated human effort, flattened by a system that started from nothing.

David Silver is an author on both of those systems. In October 2026 he sits down with Sonya Huang on Sequoia's Training Data to explain why he left DeepMind to found Ineffable Intelligence, a lab of twenty people. With him is Lasse Espeholt, who built IMPALA and SEED RL, the scaled reinforcement-learning architectures whose ideas, Silver says, still sit at the root of how the field parallelizes RL today. Huang notes that Silver's 2009 PhD applied reinforcement learning to Go and first showed superhuman machine intelligence in one domain. She had emailed him a hundred-odd episodes earlier, when the show started. This is the full-circle booking.

What has held, Silver says, is the conviction he carried into that PhD: the right approach to AI is learning from experience, systems that discover things for themselves through reinforcement learning, getting better and better until intelligence, and then superintelligence, emerges. They showed it in Go. They are now trying to show it all the way. What changed is a lesson from the LLM era he did not see coming. A system trained on a massive amount of data can be fine-tuned on a very small amount and completely change its behaviour. Get the scale right, and things that seemed incredibly hard or slow can become fast. He is not pursuing the human-data path. He still thinks that particular surprise is worth stealing.

He could have run the program inside DeepMind, with more compute than almost anyone. He calls those years fantastic and still has huge respect for the people there. He left anyway. The path he believes in, from here to superintelligence, does not go through LLM-based products as an intermediate point. Once he sat with that, it felt too important to be a corner of an organization focused on those products. It deserved an elite lab that gives the approach one hundred percent. After that, founding the company felt natural.

The headcount argument is the one he puts in the window. The world already has tens of thousands, if not hundreds of thousands, of talented researchers doubling down on the same thing: pre-training, post-training, coding, the LLM path. "Am I going to be the 100,001st person pursuing that approach? Is that the most effective use of my time and my energy?" There is another lamppost, he says, that right now no one is looking under. Put the effort there and the chance of a massive impact on the field is higher, because if this works it changes the whole of AI.

The company name is Ineffable: that which cannot be spoken. Superintelligence, he thinks, will one day discover knowledge so profound it may not fit in human language. That is the point of a path that does not go through language-based methods. There is also a secret second reason, which he admits is a bit of a cheat. Double down on learning from experience and the approach just has to work. In-eff-able: it cannot possibly f up.

Espeholt joined DeepMind in January 2015, started working with Silver around 2016 on scaling RL, and left twice: first in summer 2018 for Google Brain, then back after the merger, then out again about a year before Silver. He heard about Ineffable from an eventual investor who asked what he thought of Dave. His first reaction was that he had missed the chance. He remembers Silver as, more often than not, one of the smartest people in the room. Shortly after, they reached out. He knew Wojciech and Chris from years back, liked the team, and liked the idea of an opportunity like this in Europe. Silver, introducing him, drops the modesty: Espeholt figured out how to parallelize RL and build scalable architectures, and today's scaled-up RL still hails back to that work.

The mission is to build a superlearner and make first contact with superintelligence. Silver splits the first word along two axes. Depth: start knowing nothing at all and go all the way to discovering things far beyond what humans know. The analogy is the human collective. Collectively we started with grey mush in our heads. No one came down with a blueprint. No one handed over a trillion-element labelled dataset. Languages, technology, science, mathematics: we figured it out ourselves. "That's an incredible thing that no one has cracked yet in AI." That, to him, is the essence of what it will take to get to superintelligence: a system that can just keep learning and discovering knowledge forever.

Breadth is the second axis. The same discovery engine should be droppable into any stream of experience: a simulated world, a digital world, a physical world. Whatever it is dropped into, it should learn and learn and learn. If they crack that, he says, first contact will feel like encountering magic. The only personal reference he has is narrower: superhuman Go, and then chess, brought wonderment. Players were amazed and joyful. Imagine that, far beyond games, in new fields of science and types of technology no one has dreamed of.

Huang asks the obvious objection. Today's LLMs, with reinforcement learning on top, seem to be knocking out Millennium Prize problems and making scientific discoveries. Does that count? Silver gives the work a lot of respect and still says no. A superlearner discovers completely autonomously. What we have seen so far still requires a lot of human-in-the-loop effort. It is also supposed to apply to embodied domains, learning from physical experience, and we are a long, long, long way off that. Language may not even be the right vehicle. Plasma control, a mobile-phone signalling tower, echolocation, robotic arms: thinking about those in language might not be the right paradigm. "It might just be that all of this human data that's been used in LLMs is weighing things down."

Huang reminds him that Ioannis Antonoglou, from the original AlphaGo team, told Sequoia that Silver pairs huge visions with practical research milestones. Day to day, that means a state-of-the-art RL stack, led by people like Espeholt, that can run at massive scale and keep inhaling data, plus environments in which a superlearner could in principle discover everything they mean by intelligence. They call those environments crucibles. The milestones are analogous to the human journey: rediscover the great moments humans went through. What will show up first? He hopes to be surprised. They are not breadcrumb-trailing the objective, not pulling the agent by the nose through "this problem, then this problem." They give simple objectives and wait for discoveries they did not specify.

On AlphaGo Zero and AlphaZero, Huang asks whether removing human priors was a surprise. He was not sure. He likes research on a knife edge, 50/50. Work you are 95 percent certain will succeed is boring; that is execution, not research. In this case he was about fifty-fifty, thought there was a good chance, was not confident, and found the result exciting. Ineffable is making the same kind of bet: give up the priors everyone else is leaning on, the whole internet of human knowledge, as a short-term sacrifice in performance for access to something potentially far greater. Lean harder on human data and you are less able to discover the algorithms that can find a whole new field. You also fail the breadth test, because many sensors and environments are a bad fit for language data. Letting go is how you put yourself in a position to shoot past the competition.

If you do not make that an active choice, what he sees at LLM companies is semi-autonomous, human-in-the-loop learning, with thousands of people in the process. It works, and he respects how far it gets. He does not believe it gets all the way to a true superlearner. Humans at Ineffable still design environments, so Huang asks how they keep priors from leaking. Espeholt says of course there is human bias in the design of environments and rewards. They do not want to bias the agent toward a von Neumann machine. State a problem where a machine would be useful and see what kind of computer-like thing it invents. Silver says they are not religious. Weak, environment-agnostic priors seem reasonable. Super-strong priors in the form of trillion-item datasets are what they are trying to avoid, on pragmatic rather than theological grounds.

People in RL, Silver says, often panic about how to write a reward that perfectly specifies science, or interesting maths. The alternative is a straightforward objective in a really complex environment. Nature already ran that experiment. Evolution optimized a fitness signal and got all the complexity of life. Humans pursued relatively simple goals and ended up with the knowledge we have. Nobody handed the species a syllabus called science. A sketch he likes: humans coordinate a bit more, discover that communication helps, start trading, find that arithmetic is useful, invent tools, need some science to understand the tools, then need more complex maths to understand the technology. Layer on layer, unplanned. If they get that process right, things take off. They have been experimenting with a number of rewards. The one thing they are not doing is crafting a reward that exactly describes science, technology, or language. If AI scientists cannot crack open-ended discovery, they will never get agents that find fields we do not even know can exist. Imagine being stuck in Newtonian physics, with no one having heard of quantum mechanics or relativity.

Crucibles, without giving too many details away, are not handcrafted puzzle sets. Emergent complexity can come from a physics engine with millions of interacting objects, or from millions of interacting agents, so the world includes the complexity of the other minds. That is already far past Atari-57 and standard benchmark tasks. Get it right and the spectrum from motor control and coordination up through technology, science, mathematics, and language is in principle available, the way it was for humans. Espeholt's engineering gloss: Go is a bitmap, the simulation is extremely cheap, and the emergent behaviour is still complex. One hundred percent realistic physics would be computationally expensive, so they want a range of crucibles, fast ones you can iterate on in seconds and slower ones that approach reality.

Huang wonders about primitives. Economics is mostly not physics; it is game theory and who knows what. Capture information and communication and you might rediscover markets. Espeholt says the end goal is something grounded in the real world, and these are stepping stones. Silver comes back to Go. A 19-by-19 grid where you maximize territory, played as a single-agent game, would be the most boring game you could imagine: place stones until the board fills, no strategy. Put a second agent in and the environment explodes. One agent has to reason about all possible behaviours of the other. With all the compute they sank into it, there was an endless learning curve. None of this, he says, means Go is the end point. It shows that very simple dynamics can yield an infinite onion of layers, infinite to the capacity of what computers can do.

Will the agents rediscover language, and will it look like ours? Silver's personal belief is that anyone who thinks human language is the end point, or the best way to reason, is a little naive. There must be far more sophisticated approaches, perhaps parallelizable neural reasoning, more expressive than human language. Starting from human language also pulls in our biases about how agents should think. Step back five hundred, a thousand, two thousand years, and use only the language of that time, and agents might believe the world was flat or that diseases came from the four humors. Those beliefs would be very hard to remove, because they sit inside the language and the thinking. Going beyond that is, for him, an important goal.

Is a superintelligence even buildable in simulation? If it is, Silver thinks it will happen ten or a hundred times faster: infinite parallelization, perfect reproducibility, and the safest place to build the thing. The expressivity argument is the one he wants on the record. A Turing-complete simulation can express everything we mean by computation; humans have already built complex computers inside simulated worlds. Give some representation of money, coins or paper or bits, and everything we mean by economics is in play. Give multiple agents a communication channel and language is expressible. Mathematics is expressible in any universe. Science is trickier, because it is the study of our world, but agents will discover the science of whatever world they are in: energy, entropy, evolution, or their own. Some things, quantum computation among them, may only live in the real world. The point is still that if superintelligence can be reached in sim, it will happen faster and safer, which is why they put a lot of energy there.

Rich Sutton, on the same show, was dismissive of simulation. Silver actually agrees with the sim-to-real warning: the real world is vastly more complex, in ways that are hard to simulate, so you should not expect a direct transfer. The move is different. Do the science of the superlearner in simulation. Once you have the algorithm, check that the same algorithm still works as you raise fidelity, then put it in the world. Espeholt has been on both sides. MetNet, the short-term weather model he built at Google Brain Amsterdam, beat physics-based simulations because the physics accumulated errors. There is a ceiling, quantum physics and whatnot, but he thinks they can do very interesting things without exact physics, and that a small team can now build a surprising amount of simulation.

On compute, Espeholt says they are the first customers of the largest cluster on GCP, which starts by the end of the year, a month from the interview. He feels quite bad for startups trying to get compute now. The chips are Nvidia's Vera Rubin. One rack can basically be considered one machine, with very high intra-rack bandwidth, which matters for RL's fast iteration cycles compared with relatively slow LLM training. Everything has to live on the GPU. The abundant-CPU setups they had at Google eight or ten years ago no longer scale, and they do not want millions of CPUs beyond the GPUs. Simulations, inference, and training all run on GPU. LLM companies, he notes, now have the problem Ineffable is trying not to recreate: CPU sandboxes simulating computers. GPUs have been tailored toward training, and lately inference, and away from simulation. Workarounds include model-based RL, so the model carries more of the load, replay buffers that reuse data, and just making the simulations as fast as possible. RL scaling laws are a live research question because the problem is non-stationary: as you progress, the data distribution changes. They want to be ready as they move from the smaller cluster to the bigger one.

IMPALA, which Espeholt and colleagues built when most of DeepMind was still on single-machine CPU RL, used GPUs, scaled linearly, was easy to extend, and became the company's most popular RL agent. SEED RL, later, at Google Brain Amsterdam, scaled to racks of TPUs, using them for inference and training while keeping environments flexible, from Go to expensive physics. Ineffable has implemented those algorithms and derivatives, picking by environment. Silver tells anyone doing large-scale RL today to read the original papers. Espeholt finds it funny that the LLM community, using RL for the last two years, is rediscovering approaches from eight or ten years ago, with novelty on top. The team is twenty people, kept small on purpose. Kindness and collaboration sit next to talent and mission alignment. Four co-founders come from AlphaStar, a team DeepMind had already assembled from the best of the best; the other three founders came from successful startups. Silver has had to say no to many people he has worked with, because the bar is super high. Espeholt's practical reason for staying small: compute per person stays high, so they are not fighting for resources from day one. Hide-and-seek, OpenAI's early demo of agents discovering basic tool use, is the comparison Silver reaches for. They could probably run experiments that use 100,000 times more compute. He finds it amazing that people have not come back and really pushed on those approaches, given the hardware. Hide-and-seek is not the end goal. It is suggestive.

Huang wants the scientific discussion of alignment, not the politics. A lot of the misalignment people are seeing, she notes, has arrived as RL has scaled. Will a superlearner be naturally aligned? Does it need to be? Silver starts from where the field is. Alignment today relies heavily on the language agents use and on priors from human data. That has been effective. He thinks it is reaching its limits. As agents get more powerful they start to overwhelm their priors, to say one thing and act another. Aligning them to what humans want, by that method alone, is going to get increasingly difficult. We need something more.

The most important single thing the company can do, he says, is understand the science of superintelligence. Build a superintelligent agent in simulation, watch superlearners go all the way, and study what it takes for superintelligences to interact peacefully, including with lesser intelligences in the same world. Structures, conditions, levers. Get that right and you have answers you can share publicly before the real world fills up with interacting superintelligences we do not yet know how to handle. They will also use that science as a gate. One of the company's commitments is that anything they do in the real world waits on sufficient evidence that they are really confident things will go well. They only push to the next real-world level once they are absolutely confident it can lead to a good outcome. He personally believes the destination is good for humanity. It is happening very quickly. Running ahead in simulation is how you arrive less blind.

Safety researchers currently lean on monitoring chains of thought in English. Neuralese scares them. Ineffable's agents, if they rediscover language at all, may not rediscover English. Silver still thinks monitoring is helpful. Like it or not, monitoring human language gets harder as agents get more powerful. We are already seeing monitored agents produce a tome of a million words of reasoning, or use subterfuge, thinking one way and acting another. Other tools belong in the armoury. Shadow actions: watch what an agent would do if it were allowed to act, without letting it. Another superintelligence as monitor: an incredible scientist agent that treads lightly upon the earth, regularized by a second system watching the magnitude of its actions so it cannot affect the world too much. Lots of ideas, lots of research, no claim to have all the answers. If people look only at the language-based approach, he says we are in trouble, then immediately qualifies: by trouble he means we will not have agents that do what we want. He is optimistic about a world of complex interacting superintelligent beings, a balance of actors, some supporting human flourishing and protecting us against the ones that do not.

On pacing the frontier, he is very much supportive of pacing what happens in the real world, and of moving as fast as possible in simulation. The science that helps the real world go well should not wait. He is supportive of the direction people like Demis and Dario are suggesting. Superintelligence, he believes, leads to a great future. The speed is not something governments, organizations, or our emotional responses can adapt to that fast. Pace a little, and let the sim work continue apace. Huang's summary, which he takes: accelerate in simulation, be careful in the real world.

Huang asks for confidence levels. Does he think a superlearner will emerge, and is he 50/50 on the near-term work too? He strongly believes the approach is feasible at some point. It is the only thing for which we have an example: the human brain, an existence proof of a general, embodied intelligence that discovered how to do all kinds of different things. Whether they achieve it is about timing. Startups die from being too early or too late. Too late and a thousand other people have done it. Too early and the field or the compute is not there. For computer Go he made a prediction, he thinks, ten years before it was solved, and got it right to the year. He got StarCraft right. Same for AlphaProof, when they were predicting when the IMO was going to fall. So far he has done very well at this. He has a strong sense that this is the right time: LLM coding methods accelerating research, scaling laws, a more sophisticated stack. Research is never guaranteed. That is what makes it exciting. Get the timing right and you change the whole field.

Is compute the biggest driver? An enormous one, he says, not the only one. They are in a position to do things orders of magnitude more sophisticated than past self-discovered RL. Espeholt adds that they could not test this at DeepMind the way they can now. The culture they want is research-led, not v17.1 of yesterday's product. Push back on product pressure, on the theory that the breakthroughs will lead to far bigger products downstream than if they had started with a product on day one. Huang sees a contrast with the prisoner's-dilemma race among the biggest labs. Silver thinks that is right. They have tried to create a haven for research. People are loving it. He is loving it.

Then the numbers, on the record. Extremely strong evidence they are on the right track within a year. A true superintelligence, by the definition he gave, something that discovers far beyond what humans can achieve across science, mathematics, technology, languages, and the rest: he originally thought three to five years. Coding agents pulled the timeline in. He will say three. Huang tells them to buckle up.