Summary

Noam Brown sees test-time compute as a durable second scaling curve, progressing from o1-preview to o1 to o3 and eventually from minutes of thought to hours, days, or longer. The gain is not merely buying more inference: o3 can outperform o1-preview without a radically longer trace because models are becoming “better at thinking.” Cost and serial wall-clock time remain the eventual soft ceilings.
Deep Research is Brown’s existence proof that reasoning models can improve in domains without an easily verifiable reward. Users can distinguish a strong research report from a mediocre one even when no crisp answer key exists, which is enough to support an improvement loop. His sharper criterion: if people genuinely cannot tell outputs apart, further hill-climbing “doesn’t really matter.”
Much of today’s agent infrastructure may be temporary, while reinforcement-fine-tuning data should remain useful across model generations. Brown expects hand-built harnesses, scaffolds, and perhaps routers to be “washed away by scale” as unified models internalize their functions. Reinforcement fine-tuning is different: collected domain data can be reused on more capable future models instead of becoming stranded engineering.
Coding agents already deliver real leverage, but Brown describes them as “geniuses” experiencing their first day on the job. He sends nearly anything he would code to Codex first and often receives a pull request about five minutes later, while o3 has largely replaced Google Search for him. The missing capability is accumulated job context: an agent with six months of experience would be dramatically more useful than one repeatedly starting from zero.
Brown’s multi-agent thesis is that individual AIs are still “the cavemen of AI,” and civilization-scale cooperation and competition could produce the larger capability jump. Anatomically similar humans moved from cavemen to semiconductors, nuclear reactors, and the moon through billions of people accumulating knowledge over thousands of years. His team is also studying how to extend a model’s thinking from roughly 15 minutes to hours and days, but its multi-agent method remains undisclosed.
Naïve self-play is not a guaranteed final step to superintelligence because the AlphaZero recipe relies on unusually clean two-player, zero-sum objectives. Outside that setting, optimization can select difficult but worthless behavior—for example, a math model generating 30-digit multiplication merely because another model struggles with it. Diplomacy similarly taught Brown that collaboration requires modeling and adapting to other players, not simply converging to a defensive equilibrium.
Alongside continued scaling, Brown highlights data efficiency, evaluation quality, and iteration speed as major constraints. He calls human-like sample efficiency one of the most important unsolved questions: a poker expert can profile an opponent in roughly a dozen hands where older AIs needed about 10,000. Meanwhile, three-hour or three-week reasoning runs slow the research loop itself, making unavoidable serial time “the strongest case for long timelines.”

Deep dive

1. Cicero taught Brown to play—and exposed the value of steerable agents

Building Cicero forced Brown to understand Diplomacy well enough to distinguish a bug from a strategically brilliant, non-human move. Studying tournaments, tutorials, and the bot’s unconventional behavior improved his own play; after Cicero’s late-2022 release, he kept competing and won the World Diplomacy Championship in 2025 without using the system during the tournament.
Cicero’s language model was small—about 2.7B parameters—and occasionally behaved bizarrely. It might deny something visibly present earlier in the chat, insisting, “No, you’re lying.” Players usually attributed this to tiredness, drunkenness, or trolling because they were not expecting a bot; Brown thinks active suspicion would have made Cicero much easier to identify.
Brown’s present-tense claim is stronger: “GPT-4o and o3 are passing the Turing test.” Language quality has improved enough that conversational traps may no longer reliably expose a system, though Brown’s understanding is that current bots still do not perform very well at Diplomacy itself.
The safety lesson was unexpectedly positive. Cicero conditioned language generation on concrete intended actions, making its behavior interpretable and steerable rather than “a language model running loose.” Brown says safety researchers viewed that reasoning layer as a potentially useful control mechanism; he would like to see leading bots play one another in a Diplomacy benchmark.

2. Deep Research breaks the verifiable-reward objection

Brown is surprised that established researchers still assume reasoning models can only excel in math, coding, and other easily graded domains. Deep Research directly contradicts that view: “What is the best research report that you can generate?” has no simple answer key, yet the product is popular and the models perform extremely well in this domain.
The hosts pressed on whether a broad quality spectrum makes progress hard to recognize. Brown’s answer was that people can distinguish a good report from a mediocre or bad one, even though the system is “not 100%” and will improve. That comparative signal is enough to feed the feedback loop for refining the product and model.
His boundary condition is pragmatic rather than philosophical: models can improve wherever some measure of success exists, including subjective or difficult-to-define measures. If users cannot perceive any difference between two outputs, then optimization is irrelevant; otherwise, easy mechanical verification is helpful but not necessary.

3. System 2 only works once System 1 crosses a capability threshold

Brown’s qualification to the Thinking, Fast and Slow analogy is that extra thought cannot rescue an incapable base model. Chain-of-thought brought little benefit to very small models such as GPT-2, whereas larger pretrained models showed a lift. His analogy: asking a pigeon to contemplate chess for 1,000 years still will not produce strong play.
The benefit depends on whether the task contains information that reasoning can transform. GeoGuessr and spatial problems can reward deliberation; image recognition may benefit less. Without web access, a birth-date question is largely retrieval—“you either know it or you don’t”—although reasoning might narrow the historical period and produce an educated estimate.
Tic-tac-toe captures the current division. Brown says GPT-4.5 can draw the board and make legal moves but occasionally errs, while System 2 can enable perfect play. He leaves open whether a hypothetical GPT-6 might solve it instantly through System 1 alone: larger base models can absorb capabilities that currently require explicit reasoning.
Prior knowledge still accelerates deliberation. A brilliant person given three weeks could potentially reason through a novel game against an expert, but learned intuition makes the process vastly faster. System 1 and System 2 are therefore coupled scaling paradigms, not independent substitutes.

4. The ideal harness disappears, but reality cannot be rolled back

Brown’s position on agent scaffolding is blunt: “The ideal harness is no harness.” When Pokémon became an evaluation target, he preferred letting o3 fail unaided rather than engineering a structure that manufactured a higher score. A model doing badly is useful evidence; the research goal should be broader capability that eventually lifts Pokémon performance as a side effect.
Environmental tools are still legitimate. A chess model could be offered a tool to check whether a contemplated move is legal. Brown distinguishes that advance check from committing an illegal move, receiving feedback, then declaring, “Just kidding,” and selecting another action.
That distinction becomes non-negotiable in robotics. A model may simulate a movement, discover that it breaks something, and reject it; once a physical robot has acted, however, “the thing is broken.” Brown warns against relying on a test-time-compute paradigm that freely undoes consequential real-world actions.
Routers face the same long-term pressure as harnesses. A cheap model can recognize some hard requests, but it can also be fooled or overconfident; OpenAI’s stated destination is a single unifying model, with routing eventually built into the model itself. Brown hedges that provider routing may retain value, and he concedes that today’s routers can be commercially worthwhile.

5. Domain data should outlast short-lived agent scaffolding

Brown’s warning to developers is temporal: capabilities may change radically in three months, “let alone six months.” A product team should avoid spending six months perfecting infrastructure that a stronger base model could erase upon arrival, even when temporary scaffolding is rational for shipping now.
Reinforcement fine-tuning sits on the complementary side of that divide. It specializes a model around data the provider is unlikely to bake into a general release, and the same collected examples can fine-tune future, stronger models. That makes domain datasets more durable assets than elaborate workarounds for a particular model’s limitations.
The hosts translated this into a build-versus-wait question: rush to fine-tune today, or first construct the environment and reward signal? Brown did not prescribe one universal sequence, but emphasized the durable component—collecting data that remains useful as model capability scales.

6. Reasoning emerged as a contested second scaling paradigm

Brown’s conviction came from poker, Hanabi, and Diplomacy, where thinking before acting produced “orders of magnitude” gains—roughly equivalent to making a model 1,000 to 100,000 times larger. Language models instead answered immediately, making him skeptical that pretraining alone could reach superintelligence before economic limits intervened.
At a late-2021 meal, Ilya Sutskever asked Brown for his AGI timeline. Brown argued that general language models still lacked a general reasoning paradigm; absent one, even several more pretraining orders of magnitude would fall short unless someone could spend “a quadrillion dollars.” Brown’s mistake was believing the missing paradigm would take a long time to discover.
Sutskever and others had already explored reinforcement learning, with partial successes that accumulated across iterations as models improved and experiments became faster. Brown dates his own conviction to around October or November 2023, when the team saw “very conclusive signs of life” and OpenAI recognized the result strongly enough to scale it.
That allocation was controversial because 2023 OpenAI had more constrained compute and every reasoning experiment displaced another bet. Some questioned whether the behavior would generalize or deserved heavy investment. Brown recalls a researcher who left OpenAI dismissing the “Strawberry” work, then revising their view after seeing coworkers at a competing lab react to o1’s release with “Oh, crap, this is a big deal” and pivot their research agenda.

7. Startup-style resource allocation made the scaling bets possible

Brown credits OpenAI not merely with discovering pretraining and reasoning curves, but with organizing around them. The lab operated more like a startup pursuing AGI than a university: teams could collaborate, pool compute, and make painful centralized choices instead of preserving many independently allocated small experiments.
The original reinforcement-learning motivation was not solely test-time compute. Researchers worried that data, rather than compute, would become the wall and explored RL for greater data efficiency. The eventual paradigm delivered both: better use of data and an enormous effective increase in inference-side compute.
Brown remains impressed by Sutskever’s early vision. He cites emails from 2016–17 arguing that one big experiment can be more valuable than 100 small ones, as well as internal documents from 2021, 2022, and earlier. The broader research lesson is that “the best research is obvious in retrospect”; at discovery time, deciding that one large experiment deserves resources taken from numerous plausible alternatives is neither obvious nor politically easy.

8. Codex already changes software work, but persistent experience is missing

Brown’s current stack is Windsurf plus Codex, with reasoning models preferred for difficult work. “Basically anything that I would normally try to code up I try to do it with Codex first”; a self-contained request can run and return roughly five minutes later as a pull request.
Brown says anybody can use Codex and “feel the AGI,” but the feeling fades as users get accustomed to the capability and notice what it lacks. The hosts illustrated the same effect with Sora: its initial magic gave way to noticing unnatural motion and inconsistencies.
o3 has “basically replaced Google Search” for Brown and can perform a compact version of Deep Research in about three minutes. Its latency is awkward for pair programming, where GPT-4.1 may preserve flow; asynchronous Codex changes the ergonomics by letting a longer task proceed while the user does other work.
The core limitation is organizational memory: “They’re geniuses but it’s their first day on the job.” Agents repeatedly spend ten minutes rediscovering similar context instead of behaving like employees with six months of experience. Brown frames that as a model-and-product problem OpenAI must solve, not merely a missing third-party harness.

9. Remote-work agents turn alignment into an economic advantage

Brown expects the agent surface to expand beyond software engineering into many remotely performed tasks. His advice is broad: anyone whose job can be done remotely should learn what current models can and cannot do, because the feasible task envelope will continue widening.
Virtual assistance illustrates the potential. Human delegation creates a principal-agent problem around effort, cost, and fidelity to the principal’s preferences. An AI genuinely aligned with its user might do “a way better job than a human would”—Brown carefully corrects himself from “could”—because it can follow that user’s preferences more closely.
Personal alignment and safety alignment diverge at the target. Aligning perfectly to a user fails when that user wants to create “a novel virus that’s going to wipe out half of humanity.” The unresolved hierarchy spans individual preferences, collective human goals, and the constraints between them.

10. Multi-agent civilizations could dwarf single-model intelligence

Brown says “multi-agent team” understates his group’s remit. One program asks how to scale a model from roughly 15 minutes of thought to hours, days, and beyond, allowing it to attack much harder problems; another studies both cooperation and competition among agents.
He rejects the idea that humans occupy an extremely narrow intelligence band. Cavemen and modern humans are anatomically similar, yet only the latter inhabit a civilization capable of semiconductors, nuclear reactors, and moon landings. The difference is thousands of years of accumulated competition, cooperation, and knowledge across billions of people.
The analogy yields Brown’s signature thesis: today’s systems are “the cavemen of AI.” Billions of AIs interacting over long periods could build an AI civilization whose products and answers lie far beyond those of any isolated current model.
Brown declined to reveal whether knowledge is stored through skill libraries, retraining, or another mechanism, promising more in the “not-too-distant future.” He did say the approach differs materially from historical multi-agent work, which he considers overly heuristic and insufficiently faithful to the Bitter Lesson of scalable general methods.

11. GTO, adaptation, and self-play optimize different worlds

In poker, a game-theory-optimal policy is defensively unbeatable in expectation and still profits because opponents struggle to match it. Exploitative play can earn more from a weak opponent—bluffing heavily against someone who over-folds—but creates exploitable weaknesses of its own. “There’s no way to perfectly balance the two.”
Sample efficiency determines whether adaptation works. A human expert may profile someone’s strengths and weaknesses within roughly a dozen hands; Brown’s mid-2010s systems needed about 10,000. Poker bots therefore followed precomputed GTO strategies, beating experts and weak players alike but extracting less from weak players than an adaptive human could.
Diplomacy overturned Brown’s initial assumption that GTO would transfer. In a seven-player setting mixing competition with cooperation, a defensive equilibrium behaves poorly; the agent must model others and adapt to their style. His analogy is social rather than adversarial: if everyone at the table speaks French, continuing in English is not optimal.
The size of the hidden-state space also changes the technical problem. Poker search can enumerate 1,326 possible private-card states heads-up and then account for the other players; this breaks down in Omaha and especially in Stratego, with close to 40! possible states. The poker techniques would not work out of the box for Magic: The Gathering, though Brown guesses model-free RL could likely produce a superhuman bot with enough effort.
This is also where AlphaZero-style self-play stops being automatic. Two-player zero-sum self-play converges toward a useful minimax objective; open-ended math could instead reward one model for posing pointless 30-digit multiplication that another cannot solve. Brown agrees that choosing the right objective remains the unresolved problem.

12. Cost, data, evaluation, and serial time form the next walls

Test-time compute has a pretraining-like soft ceiling: three minutes can become three hours, three days, or three weeks, but each increase costs more. Efficiency is improving in parallel—o3 may not think radically longer than o1-preview on a question, yet performs far better because it has become “better at thinking.”
Wall-clock time may be the harder bottleneck. A three-week run requires at least three weeks before researchers can inspect results and choose the next experiment; parallelism cannot remove every sequential dependency. Brown calls this “the strongest case for long timelines,” with drug discovery especially constrained by slow validation and the lack of a perfect human-biology simulator.
Brown considers human-like data efficiency one of the most important unsolved research questions. The hosts added that algorithmic improvements may help and that humans learn from more than internet text. Brown’s own point was that current models are less data-efficient than humans and that the question remains unsolved.
Evaluation can distort research toward hard questions with cheap grading, such as Humanity’s Last Exam, while neglecting fuzzy tasks that are expensive to score. Brown says academic work still matters, but promising papers must be reproduced internally and tested at scale; useful inspiration and scalable evidence are separate filters.

13. Scale may make explicit world models unnecessary

Brown thinks sufficiently capable models develop an implicit world model that improves with scale, so an explicit world-model component may not be necessary. He once believed other agents had to be modeled explicitly because they have agency and motives, but now thinks capable models can develop theory of mind implicitly.
He presents this as a current view rather than a settled result: models may need explicit treatment in some multi-agent settings, but he increasingly expects general capability and scale to absorb that behavior.

14. Robotics has a slower research loop, with no clear case for humanoids

Brown’s robotics master’s was largely nominal; after briefly playing with LEGO robots, he shifted to AI for poker. His main takeaway from roboticists was that physical hardware makes experimentation much slower and more painful than software, helping explain the faster progress in language models and virtual-coworker tasks.
He has no strong view on humanoids, but weakly favors non-humanoid robotics after hearing the Physical Intelligence CEO’s case. Drones are his concrete example: they can be highly valuable without reproducing the human form.

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