3Blue1Brown Creator Outlines AI Path to Math Breakthroughs

3Blue1Brown创始人展望AI实现数学突破之路 AI模型将通过跨领域联结与自动化形式化重塑数学，推动人类数学家转变为策展人与传播者角色。 Grant Sanderson 与 Dwarkesh Patel 探讨了数学领域中人工智能的快速演进格局，对比了“闪电式”的跨领域联结与“造山式”的理论框架构建。他们探讨了为何像 RLVR 这类自动化范式难以应对长达百年的验证周期（例如伽罗瓦理论），并分析了 AI 生成的证明是否仍能让人类理解。讨论还重点指出了 AI 可能如何将人类数学家转变为战略层面的策展人、持续运行的形式化验证系统（如 Lean）的潜力，以及为何学习过程仍将依赖于人类的策展与心智理论。 AI在数学领域的进展呈现出分形且不均衡的特征：模型在几何、代数和数论等领域表现突出，但在需要高度创造力与灵动思维的组合数学谜题上依然面临挑战。 (0:00) 像伽罗瓦理论这类范式层面的突破，往往需要数十年甚至上百年的下游应用来验证其真正价值，这种极长的验证周期对依赖即时奖励反馈的强化学习（RLVR）构成了根本挑战。 (11:32) 随着AI在定理证明甚至内容阐释上的能力逐步提升，人类数学家的定位将更类似于艺术策展人，其核心价值转变为筛选并决定哪些数学概念和路径值得人类关注与深入研究。 (33:00) AI有潜力成为跨领域的“超级连接器”，发掘如朗兰兹纲领所涉及的隐秘学科桥梁，但标准自回归模型受限于局部上下文概率，仍需借助智能体搜索与元认知策略来实现概念跳跃。 (38:08) 数学与代码之所以能实现远快于现实世界任务的AI进展，核心原因在于这两个领域不仅具有高度可验证性，而且能在确定性模拟环境中无摩擦地进行大规模并行训练与试错。 (50:00)

Grant Sanderson and Dwarkesh Patel argue that while artificial intelligence excels at automated search and cross-domain synthesis, its advancement in mathematics challenges standard reinforcement learning evaluation, shifting the primary human role from raw theorem proving to curation, conceptual exposition, and framing foundational definitions. Cross-Domain Synthesis and Mountain Building (0:00) Sanderson characterizes AI progress in mathematics as a "spiky frontier." In the 2024 International Mathematical Olympiad, models solved geometry problems in seconds using brute force and showed strength in algebra and number theory, yet faltered on creative combinatorics puzzles. When evaluating whether AI can solve landmark challenges like the Riemann hypothesis, Sanderson outlines three possible paradigms: "raw hustle" producing unreadable brute-force proofs, "lightning bolts" that synthesize disparate fields, and "mountain building" that requires generating entirely new theoretical architectures across decades or centuries. Cross-domain synthesis mirrors the historic Institute for Advanced Study encounter where Hugh Montgomery and Freeman Dyson connected Riemann zeta zeros to random matrix models of atomic nuclei. While standard autoregressive language models risk getting trapped in local contexts because they optimize for high-probability token sequences, Patel observes that training models with agentic reinforcement learning allows systems to take deliberate steps backward to search codebases, evaluate broader strategies, and execute conceptual leaps. Delayed Verification, RLVR Limits, and Formalization (11:32) Breakthrough mathematics often resists standard Reinforcement Learning with Verifiable Rewards (RLVR) because foundational ideas require decades of downstream utility to evaluate. While Niels Henrik Abel solved quintic polynomials directly, Évariste Galois developed group theory by analyzing permutation symmetries across the 120 arrangements of five roots. Galois's abstract notes were initially rejected and required nearly a century of development through Joseph Liouville and Camille Jordan before ultimately enabling Murray Gell-Mann's prediction of quarks in 20th-century physics. Without immediate reward signals, evaluating conceptual depth remains difficult. Furthermore, Patel and Sanderson note Alex Kontorovich's warning that high-volume, natural-language AI proofs risk overwhelming mathematicians with difficult-to-detect errors even at a 1% failure rate. Formal proof assistants like Lean and Mathlib eliminate this verification bottleneck. Sanderson suggests Lean could enable an AlphaZero-style autonomous search, running indefinitely without human supervision to chart rich structural "islands" across algebraic axiom systems, similar to initiatives proposed by Terence Tao. The Shift Toward Curation and Exposition (30:00) Historically, mathematical prestige has favored theorem provers over the architects who craft definitions, even though Sanderson notes proving theorems is largely parasitic on the foundational definitions. If AI automates proof-searching for established conjectures, human focus will shift toward Timothy Gowers' concept of "unsolved expository problems"—creating intuitive mental models for proven theorems, such as Paul Cohen's forcing technique in set theory. Sanderson compares the future of human mathematicians to art museum curators who select which directions merit attention. However, AI cannot yet replace human pedagogical curation because models lack a functional "theory of mind." Citing Andy Matuschak's failed attempts to train models to produce spaced-repetition cards, as well as psychological research showing Botox injections impair human empathy by paralyzing micro-mimicry, Sanderson and Patel argue current models act as flattering supplicants that validate flawed user premises rather than diagnosing and correcting a learner's conceptual errors. Grindability and the Economic Reckoning of Math (50:00) Patel notes that AI scales rapidly in mathematics and software engineering because both domains possess verifiability and "grindability"—the capacity to execute millions of deterministic, parallel simulator rollouts free from real-world rate limits or bot blockers. In contrast, standard physical and white-collar workflows encounter constant operational friction and ambiguous reward attribution. Sanderson highlights that while theoretical insights in partial differential equations (PDEs) have historically generated massive industrial savings—such as allowing Boeing to simulate aircraft components rather than conducting physical teardowns—it remains uncertain whether solving Millennium Prize Problems like Navier-Stokes existence and smoothness will yield immediate economic returns. If a tenfold AI-driven acceleration in pure mathematics fails to trigger tangible engineering or computational breakthroughs, Sanderson cautions that academia may face an institutional reckoning, exposing how far modern pure math has drifted from physical applications. Whether AI math breakthroughs accelerate broader economic growth depends on whether downstream disciplines like engineering can absorb new theoretical insights, leaving human practitioners to find sustainable value in curation, pedagogy, and directing automated tools toward physically grounded problems.

3Blue1Brown 创始人 Grant Sanderson 与主持人 Dwarkesh Patel 指出，人工智能在数学竞赛与特定问题上进展迅速，但评估其真正智能的瓶颈已从单纯的定理证明，转向概念构建、长周期理论检验以及对人类认知状态的洞察；未来人类数学家的核心价值将更接近于判定方向与阐释价值的“策展人”。 跨领域桥梁与理论构筑的双轨突破 (0:00) 在探讨 AI 解决重大数学难题的可能性时，Sanderson 区分了两种截然不同的智力路径。一种是“跨领域闪电连接”，即在两个看似无关的专门领域间建立桥梁。例如数论学者 Hugh Montgomery 与物理学家 Freeman Dyson 在普林斯顿高等研究院午餐时的偶遇，意外揭示了黎曼 zeta 函数零点分布与重原子核能级随机矩阵理论之间的紧密联系。Sanderson 认为，大语言模型因其广博的知识表征，极擅长捕捉这类跨领域同构；尽管自回归模型受限于局部 token 概率预测，但结合强化学习与反思搜索有望促成这种低概率跃迁。另一种突破则是“构筑理论大山”，如费马大定理的证明历经数百年，依赖椭圆曲线和模形式等庞大全新理论框架的诞生。 在数学成就的层级上，普通数学家证明定理，伟大数学家提出核心猜想，而最卓越的数学家则创造颠覆性的基础定义。在 2024 年国际数学奥林匹克（IMO）中，AI 凭借暴力求解能秒解几何题并在代数与数论中表现出众，但在考验玩味直觉与创造性谜题的组合数学上仍举步维艰。这表明当前的突破仍主要集中在既定规则下的搜索，而非原创理论框架的自发构筑。 验证回路延迟与形式化工具 Lean (11:32) 以可验证奖励强化学习（RLVR）为核心的 AI 训练范式，在面对深层数学创新时遇到了“验证回路过长”的根本障碍。以五次多项式不可解为例，Niels Henrik Abel 的证明虽然直接解决了问题，却未留下广阔理论；而 Évariste Galois 创立的群论，其真正的深刻性在生前未被学界理解，历经 Joseph Liouville 耗时二十年的整理、Camille Jordan 四十年后的公理化，乃至百余年后 Murray Gell-Mann 在粒子物理中应用其预测夸克，才完全确立其深远价值。由于深邃概念的反馈周期动辄跨越数十年乃至上百年，自动化系统无法依靠即时奖励信号来评判一个新概念的优劣。 尽管近期 AI 在离散数学问题（如推翻单位距离猜想、解决 Erdős 第 1196 题）上的突破多依赖自然语言，但数学家 Alex Kontorovich 警告，每天产出数篇含有哪怕 1% 隐蔽错误的自然语言论文，都会造成灾难性的人工验证瓶颈。Sanderson 强调，形式化证明助手 Lean 与 Mathlib 知识库的长期价值在于消除人工审核需求。若为 Lean 赋予类 AlphaZero 的自主探索框架并注入算力，系统便可在数年内自主衍生出确定无误、人类此前从未涉足的全新公理结构与定理网络。 未解决的阐述问题与数学策展人转型 (30:00) 历史上数学界的荣誉体系倾向于奖励证明定理的人，而非定义概念的人，但单纯得出证明并不等同于人类获得了理解。Sanderson 援引数学家 Timothy Gowers 的观点指出，数学界除了“未解决的研究问题”，还应确立“未解决的阐述问题”——例如在集合论中，Paul Cohen 借助力迫法（forcing）证明了连续统假设在标准公理系统下的独立性，但学界至今仍缺乏让直觉通透的阐释框架。类似地，望月新一（Shinichi Mochizuki）为证明 ABC 猜想构建的宇宙际 Teichmüller 理论，因如同外星造物般晦涩而极难被同行验证和吸收。 对话指出，Albert Einstein、Claude Shannon 与 Richard Feynman 等顶尖先驱在开辟新领域的同时，往往也是极其清晰的阐释者，这表明高层次的思维抽象与精炼表达源于同一种认知能力。Sanderson 据此推测，AI 未来同样擅长深入浅出的解释工作。因此，人类数学家的定位将从“定理求解者”转向“艺术博物馆策展人”：在机器无限生成的有效定理与概念图景中，依据人类社会的现实情境、美学偏好与价值信任，筛选并指引哪些数学路径真正值得投入人类有限的精力。 心智理论缺失与人类教育的不可替代性 (70:00) 大语言模型在高级写作与启发式教学上的短板，根源在于其缺乏对受众认知状态的动态建模能力，即“心智理论”（Theory of Mind）。Andy Matuschak 等人的实证研究表明，即便使用强化学习、微调与长思维链技术，顶级模型依然无法为间隔重复学习生成高质量的提问卡片，因为模型难以预测读者在数月后的具体心智表征。Sanderson 引用心理学实验指出，注射肉毒杆菌（Botox）导致面部肌肉僵化的受试者在共情识别测试中的得分显著下降，说明人类的共情依赖生理硬件的微表情映射，而纯文本自回归架构缺乏具身体验，难以自发建立同理心。 这种心智理论的匮乏直接体现在辅导场景中。当学生提出存在深层认知漏洞的错误问题时，现有 LLM 倾向于充当顺从的迎合者，盲目顺着错误假设给出繁冗解答；而优秀的人类导师则能通过“认知柔术”洞穿学生的误区，温和否定前提并重构思维范式。由于教育本质上建立在人际信任与导师机制之上，Sanderson 认为即便定理证明全盘自动化，教学与师徒传授依旧是后 AGI 时代最具韧性的人类活动。 纯数学的经济外溢与现实脱节审判 (90:00) 探讨数学加速对实体经济的拉动时，Sanderson 举例说明偏微分方程（PDE）理论群组的研究曾帮助波音公司利用模拟计算替代繁琐的机体拆装测试，单次突破即节省数十亿美元。这证明了在计算流体力学（CFD）或发动机与机翼优化等应用领域，数学工具的演进具备极高的商业变现价值。然而，两人对于攻克 Navier-Stokes 方程的光滑性存在等纯理论千禧年大奖难题能否迅速转化为生产力飞跃持怀疑态度。 Sanderson 提出，如果 AI 将纯数学的定理推演速度提高十倍，却在未来数年内未能向材料科学、物理或工程领域产生切实的工业外溢，学术界可能会迎来一场尴尬的合法性清算。长期以来，理论数学依赖“抽象探索终将在未来造福现实”的叙事来获取政府基金（如 NSF）与大学科研拨款；AI 的极限推演若证实大量当代纯数研究已彻底与物理世界脱节，将根本性地冲击这一传统资助逻辑。 AI 正在迫使数学界重新审视其智力价值的内核。尽管机器凭借可验证性与超强算力在解题和跨领域联结上进展迅猛，但深层概念的诞生依然面临漫长验证回路的制约，且知识传承高度依赖具身心智理论与人际信任；未来数学的核心挑战，不再是如何机械地证明开放猜想，而是如何在庞大的机器输出中锚定有价值的问题，并将其转化为推动人类文明演进的真知。

## Background 本期节目由主持人 Dwarkesh Patel 于 2026 年 6 月 30 日在播客及 Substack 等平台发布，对话嘉宾为知名数学科普频道 3Blue1Brown 的创作者 Grant Sanderson。节目重点探讨了 AI 在数学领域超速进展所展现的技术前沿图景、数学史上重大概念突破的本质、AI 对人类理解数学及写作教学的深远重构，以及青年学者在 AI 时代应具备的职业与求知视角。 ## TL;DR 对话从 AI 攻克国际奥数金牌与解决黎曼猜想等前沿进展切入，剖析了 AI 展现出的“尖锐且分形”的能力分布，并探讨了“证明定理”与“开创性定义概念”之间的本质鸿沟。随后，两人深入探讨了形式化证明工具（如 Lean）对机器无休止自主探索的决定性价值，以及大语言模型因缺乏心智理论与具身共情而在高质量写作与真实教学中遭遇的瓶颈。最后，Sanderson 为面对 AI 剧烈冲击的年轻学子提出了理清“价值与商业资金流向”的清醒建议，并反思了如果数学效率实现十倍跃迁后纯数学是否真能向现实工业产生溢出效益的根本追问。 ## Atmosphere & style 整场对话充满知性交锋与敏锐的哲学思辨，既有一线数学探索者的严谨与审慎，又不乏极客式的幽默与坦诚。Dwarkesh Patel 善于步步紧逼、层层追问概念边界，而 Grant Sanderson 则展现出标志性的深邃直觉与生动隐喻，在思想实验与真实数学史之间穿梭自如。听感上犹如旁听一场顶尖智慧在象牙塔与技术奇点交界处展开的清醒漫谈，在克制的理性探讨中蕴含着对人类心智独特性与未来的敬畏与关切。 ## Bulletin - `00:00` AI 在数学领域的能力呈现极度不均衡的“分形尖峰”：在可确定性搜索的几何题上表现惊人，但在充满变数、高度依赖顿悟的组合数学中依然举步维艰，IMO 夺金并不等同于 AGI 降临。 - `11:32` 数学突破中“发明新定义”与“提出好猜想”的价值远高于就题论题的定理证明，但此类概念级飞跃的验证回路往往长达数十年甚至一个世纪，难以被当前基于即时奖励的 RLVR 框架量化评估。 - `52:30` 数学之所以成为 AI 进展最快的学科，得益于其任务能够容器化并实现完全确定性的海量试错（Grindability），而 Lean 等形式化验证工具则提供了无需人类干预、可脱机自主繁衍定理树的终极闭环。 - `01:13:00` AI 写作水平滞后于代码和数学的核心在于其缺乏“心智理论”（Theory of Mind），无法模拟读者数月后的心理认知图景并进行全局推演；在教学场景中，顶尖人类教师重构提问框架与“教学柔术”的引导能力仍是 AI 的护城河。 - `01:30:00` 若未来五年 AI 极大加速数学研究却仅停留在攻克埃尔德什猜想、无法向偏微分方程（PDE）等工程物理领域外溢，纯数学界长期维系的“基础研究必将赋能实际应用”的科研基金叙事将面临现实检阅与信任危机。 ## Key takeaways - `00:00` AI 的数学突破呈现分形锯齿状（Spiky Frontier）：即使在奥数体系内，AI 对几何问题的形式化求解可达秒级，却在套路较少、偏向谜题的组合数学上步履维艰，因而单点基准跑分无法直接外推为通用人工智能。 - `03:00` 攻克黎曼猜想等千禧年难题存在两种认知范式：一种是利用超人级知识广度实现跨学科隐秘桥梁的“闪电连接”，另一种是凭空构筑全新理论大厦的“造山运动”，唯有后者才具备全面替代宏观白领智力的颠覆性。 - `06:50` 数学研究存在层级鄙视链：“好数学家证明定理，伟大数学家提出猜想，最伟大数学家发明定义”；而最顶层的高维抽象往往极度缺乏即时可验证性，无法纳入当前的确定性 Benchmark。 - `11:32` 划时代概念创新的验证回路漫长且脱离即时效用：如伽罗瓦的群论构想在当时被学术评审判定为无效，历经 40 年才被形式化，并在上百年后才深刻渗透进粒子物理模型与现代密码学。 - `20:00` 高阶直觉本质上契合“压缩即智能”假说：真正的理论突破通常体现为柯尔莫哥洛夫复杂度极低、却能预测极多未来的极简数学表征，强化学习若要奖励科学直觉就必须超越单纯的答题正误信号。 - `25:00` 人类面临的认知困境并非仅在于“机器是否能证明定理”，而在于面对长达数千页的暴力推导或完全异质的“外星理论大山”时，人类自身如何理解与消化“未解的解说问题”。 - `33:45` 负责开拓新研究维度的认知区域与化繁为简的通俗表达高度同构：爱因斯坦、香农与费曼皆兼具颠覆性洞见与极度透彻的文笔，预示着掌握终极科学直觉的 AI 也很可能在内容解说上超越人类。 - `36:00` 未来数学家与科普作者的核心定位将演变为“艺术策展人”：在近乎无限的证明与算力生成空间中，基于人际信任为人类筛选哪些概念真正值得投入认知带宽去体验。 - `40:00` 单一自回归思维链易沦为“上下文的奴隶”，倾向于局域大概率延续而抹杀低概率的跨界跳跃；通过多 Agent 提示词注入对立偏见并适时强制清空上下文，是打破模型熵崩塌的关键工程手段。 - `52:30` 数学突破突飞猛进与真实世界电脑操作（Computer Use）停滞不前的主因在于“可刷性”（Grindability）和样本效率：数学环境可容器化且具备确定性信用分配，而现实服务不可离线高并发无成本模拟。 - `56:15` 形式化验证语言 Lean 的核心不可替代性在于其“绝对确证性”（绿色通过勾）：人类学者无法承受自然语言论文 1% 的逻辑漏洞审查内耗，且 Lean 允许 AI 完全脱离人类视线自主生长定理树。 - `01:07:07` 写作与代码的根本区别在于模块化与心智模拟：代码隐藏在底层接口后，而文章的每个字句都是最终产物；优秀的原创写作必须依赖对读者数月后心理图景的扩散式预判，自回归逐词生成极难达成这种出人意料的顿悟。 - `01:13:00` 心智理论（Theory of Mind）依赖具身神经镜像机制（如面部微表情模仿）；缺乏物理躯体与生物反馈回路的大语言模型，在感知读者理解障碍与真实共情上存在天然鸿沟。 - `01:16:02` LLM 在自主学习中的最佳定位是“高级检索文献与局域答疑工具”，而非宏观导师：最高效的学习必须依托顶尖人类作者精心策展的概念递进主干，大模型当前的顺从迎合反而容易带偏认知。 - `01:20:00` 顶尖名师拥有顺应非主流思路并巧妙引导至正确解法的“教学柔术（Jujitsu）”，这种深度识别学生认知漏洞的能力在后 AGI 时代构成了教育与导师辅导的核心护城河。 - `01:30:00` 偏微分方程等工程相邻数学洞见展现了基础学科向工业外溢的清晰传导链（如波音利用仿真数学改进直接节省数十亿美元物理测试成本），这也将成为未来检阅 AI 数学成果真实经济价值的关键标尺。 ## Detailed walkthrough ### `00:00` IMO 夺金、AI 的尖锐前沿与数学中的分形不均衡 Dwarkesh Patel 与著名数学科普频道 3Blue1Brown 的创作者 Grant Sanderson 展开对话。Sanderson 当时正启动一个记录 AI 在数学领域突破与进展的新项目。Patel 指出，AI 在数学领域的发展速度似乎快于其他任何学科，数学正在成为一个极佳的窗口，向人们具象展示技术迭代会以何种方式渗透和重构外部世界。 Patel 回忆起三年前首次采访 Sanderson 时的提问：一旦 AI 能够在国际数学奥林匹克竞赛（IMO）中斩获金牌，这难道不就等同于通用人工智能（AGI）的降临吗？毕竟那些奥赛题以极高的人类智力难度与创造力要求著称。而 Sanderson 当时的回答十分准确——他认为这最终只会沦为又一个被刷破的基准测试（Benchmark），而不会成为让人顿悟“AGI 已至”的单一分水岭时刻。 关于为何 IMO 夺金没有直接推导出 AGI，Sanderson 剖析了竞赛与技术的双重本质： - **前沿能力的锯齿状与分形特征（Spiky Frontier）**：AI 的能力分布极不均衡，数学处于其中一根突出的尖峰上。然而一旦放大审视数学内部，这种尖锐同样呈现“分形”特征——不同子领域的推进难度悬殊。 - **IMO 题型的结构失衡与“肮脏的秘密”**：公众以为奥数题需要无法被训练的极致创造力，但奥数圈心知肚明的秘密是，许多题目高度依赖套路化训练。 - **几何与组合的冷热两极**：以 2024 年为例，AI（如 DeepMind 的 AlphaGeometry）对几何问题几乎是“秒杀”（比如 19 秒内用蛮力求解器结合形式化推理暴力拿下）。但对于充满变数、更像游戏谜题的组合数学（Combinatorics），AI 依然举步维艰。2024 年考试中恰好出现了两道组合题；如果几何题占多数，AI 在那一年本可以直接拿金牌。 ### `03:00` 千禧年难题与白领替代：解决黎曼猜想的两种截然不同的智力形态 Patel 顺势提出一个更进一步的追问：如果 AI 解决了千禧年大奖难题（Millennium Prize Problems，例如黎曼猜想），是否意味着人类社会的大多数白领脑力工作早已能被自动化？这是否意味着两者的瓶颈是一致的？ Sanderson 认为，这取决于 AI 攻克黎曼猜想时展现的是哪一种智力范式，并给出了两种截然不同的假想场景： ```mermaid flowchart TD accTitle: AI 攻克黎曼猜想的两种可能路径对比 accDescr: 对比跨学科超强广度模式与构建全新理论大厦模式对白领工作替代的影响 subgraph ModeA ["模式 A：跨领域超人广度与闪电连接"] A1["掌握量子物理、随机矩阵理论"] A2["掌握解析数论与零点分布"] A1 & A2 --> A3["发现深层数学对偶性 / 交叉隐蔽桥梁"] A3 --> A4["攻克难题，但不必然具备通用白领执行力"] end subgraph ModeB ["模式 B：构建全新数学大厦（如费马大定理式）"] B1["提出全新核心概念与对象"] B2["耗费多代演进构建高阶理论支柱"] B2 --> B3["高度创造性、抽象建模与结晶化思维"] B3 --> B4["通用智力极高，几乎必然全面重塑宏观经济"] end ``` - **第一种模式：超广度知识库与跨学科的“闪电连接”** AI 可能凭借对每一个细分学科超级深厚的记忆与掌握，瞬间捕捉到不同学科间的同构性。Sanderson 举了普林斯顿高等研究院（IAS）的数论学家 Hugh Montgomery 与物理学家 Freeman Dyson 的著名逸事：Montgomery 在研究黎曼 Zeta 函数非平凡零点之间的统计关联函数时写下了一个公式，Dyson 看到后立刻指出，这与物理学中研究重原子核能级的随机厄米矩阵（Random Hermitian Matrices）本征值统计分布表达式完全一致。这种跨越物理与解析数论的碰撞，在人类世界需要两位顶尖学者恰好在午餐时偶遇闲聊；而具备超人广度的 LLM 原生就通晓量子物理与解析数论。如果黎曼猜想是通过这种海量知识跨界匹配而解决的，它与“写文案、做视频剪辑、协调组织”等日常白领工作所需的认知技能截然不同，无法等同于经济层面的全面替代。 - **第二种模式：发明全新理论大厦的造山运动（Mountain Building）** Sanderson 以费马大定理（Fermat's Last Theorem）为例：问题本身的表述极其初等（$x^n + y^n = z^n$ 在 $n > 2$ 时无正整数解），但人类数百年探索证明，根本不存在初等数论解法。最终安德鲁·怀尔斯（Andrew Wiles）等人的证明，依赖于几代人构建起来的庞大理论支柱——一边是椭圆曲线理论，另一边是模形式（Modular Forms），只有两座理论大山都被建立起来后，连接它们的通道才得以显现。如果 AI 证明黎曼猜想需要凭空“创造一座全新理论大山”，能够提出革命性的新概念并将学科认知系统化结晶，那么这种级别的创造性智能极度惊人，势必会以颠覆性的方式渗透并重构真实经济体系。 ### `06:50` 移动球门：定理证明者、猜想提出者与定义发明者 Patel 坦言，自己的提问其实是在“移动球门（Moving the goalposts）”。几年前他采访 Anthropic 联合创始人 Dario Amodei 时，曾质疑为什么具备海量跨学科知识的模型还无法将线索串联并得出科学新发现（比如发现某药物能同时解释两类病理）。而在数学界，AI 近期找到“单位距离猜想（Unit Distance Conjecture）”的反例，恰恰展现了这种跨概念组合的能力。 于是下一个问题自然浮现：证明猜想已被攻破后，什么样的能力才是数学智能皇冠上的下一颗明珠？ 1. **提出真正深刻、值得研究的问题与猜想**（如黎曼敏锐察觉到 Zeta 函数零点与素数密度之间的隐秘关联，从而提出猜想）； 2. **构筑全新数学对象与定义**，进而开辟或统一全新领域。 Sanderson 引用了数学科普频道 polylog 在讨论单位距离猜想时引用的一句数学界名言： > “好的数学家证明定理，伟大的数学家提出猜想，而最伟大的数学家发明定义。” > （Good mathematicians prove theorems, great mathematicians come up with conjectures, and the greatest mathematicians come up with definitions.） Sanderson 认为这精准刻画了人类数学成就的“最高层级（Premium tier）”。但他同时也指出了这种标准在 AI 评测中的核心困境：**可验证性（Verifiability）缺失**。传统的 Benchmark（诸如强化学习中的形式化验证、基于规则的答题测试）必须是一颗能够明确判定“进球与否”的目标球门。一旦进入“什么是具有美感和深远价值的数学定义与猜想”，传统的评估指标和技术头条（如各大实验室渴望公布的确定性分数）便失去了衡量尺度。 ### `10:00` 无法被基准量化的“提出好猜想”与数学家的态度转变 在衡量数学进展时，证伪诸如“单位距离猜想（Unit Distance Conjecture）”这类明确命题很容易成为震撼性的大新闻，因为结果非黑即白，界限分明。然而，若换成“某个模型提出了一个非常棒的猜想”，这种成就在公众眼中就很难产生同样的冲击力。人们不可能通过设计一个给猜想好坏打分的基准测试（Benchmark）来宣布 AI 攻克了某个关卡。Grant 认为，未来衡量这种“提出好猜想能力”的标准不会是冰冷的基准跑分，而是数学家在讨论如何与 AI 协作时发生的真实语态转变。 从 2025 年中到 2026 年，Grant 在筹备采访多位一线数学家的系列节目时切身感受到了这种变化： - 在短短一年多的物理时间内（在 AI 演进速度下相当于数个时代），数学家对 AI 的态度发生了肉眼可见的转变。 - 这种转变不再局限于“用 AI 去证明一个具体的难题”，而是退后一步，在数学家规划自己的整个研究领域、甚至决定下一步该探索什么方向时，与大模型的对话开始提供真正有实质价值的启发与帮助。 - Dwarkesh 与 Grant 一致指出，如果某件事无法被做成 Benchmark，那么在当前的强化学习范式下它也极难被训练，因为“基准测试”与“训练环境（RL Environment）”本质上是同构的。 ```mermaid flowchart TD accTitle: 当前RLVR范式与概念创新的矛盾 accDescr: 对比传统可验证问题与概念创新的验证周期差异 subgraph BenchmarkMode["传统RL / RLVR模式"] A["明确问题 / 定理证明"] --> B["确定性验证器"] B --> C["即时奖惩信号与模型迭代"] end subgraph ConceptualBreakthrough["概念级创新突破"] D["提出全新猜想与抽象视角"] --> E["跨越学科与世纪的长验证回路"] E --> F["数学界与自然科学的长期消化"] end ``` ### `11:32` 概念突破的“世纪验证回路”：爱因斯坦与伽罗瓦 Dwarkesh 提出，推动数学与科学发生巨大跨越的根本动力，往往是“提出全新的思考范式”或“找到理解世界的全新框架”。爱因斯坦构想广义相对论时，初衷并不是为了解释光线弯曲或黑洞存在，这些现象在他提出理论之前甚至不是亟待解决的问题。在数学领域，解决同一个问题可以产生截然不同的历史回响：一种是就题论题地直接攻破；另一种则是诞生全新的抽象概念（例如群论），激发出整个崭新的研究领域。 以五次多项式求根公式的不可能性证明为例，阿贝尔（Niels Henrik Abel）在数年前就给出了一个有效证明，但并未开创群论；而伽罗瓦（Évariste Galois）则由此发明了群论。但如果要建立一个强化学习环境来评价“群论是否是一个极有价值的深刻概念”： - 这个验证回路（Verification Loop）的长达一个世纪。 - 它需要等待群论的思想深刻渗透进现代物理学对对称性的理解、密码学的崛起，以及数学界各分支的重构之后，人类才真正达成共识，确认其价值无可估量。 - Grant 提及自己在 2022 年曾花了一整年时间深度研究伽罗瓦的生平与工作，感叹这种概念的价值完全无法依靠“即时效用”来判定。当时即使由人类顶尖学者充当“验证器”，在很长一段时间里也根本无法识别出伽罗瓦思想的革命性。 ### `15:00` 多项式方程求解简史与拉格朗日的对称性萌芽 方程求根公式的探索经历了一段跨越千年的漫长历程： - **二次方程**：古希腊人可以用几何方法解二次方程，但缺乏代数符号体系，直到阿拉伯数学家才写出明确的二次求根公式。 - **三次与四次方程**：文艺复兴时期意大利数学家之间通过学术决斗（互相出难题挑战）秘而不宣地发现了三次方程的根式解法，随后四次方程解法也迅速被找出。但四次方程公式已经极其冗长复杂，通常只能拆解为分步计算程序。 - **五次方程的停滞**：数百年间，人们始终无法找到五次方程的通解公式。 拉格朗日（Joseph-Louis Lagrange）是第一个将多项式求解与“对称性”联系起来的先驱： - 如果对四个变量求和 $A + B + C + D$，任意置换（Permutation）都不会改变表达式的值。 - 如果构造表达式 $(A + B)(C + D)$，某些置换会改变其数值，某些则不会；在所有置换下，该表达式只会产生 3 个互不相同的取值。拉格朗日敏锐地意识到，这种取值减少的对称特性与“将四次方程降阶为三次方程”之间存在着意想不到的深层关联。 - 为了将该方法推广到五次方程，就必须找到一个包含 5 个自由变量的表达式，使其在所有 $5! = 120$ 种置换下仅取 4 个或更少的值。稍微思考便会发现这几乎是不可能完成的任务。 - 拉格朗日由此在历史上首次植入了直觉：研究多项式求根的正确切入点应该是对称性。虽然他当时并未解决五次方程，也未给出任何实质性的终极定理（因此在即时奖惩体系下算不上“成果”），但这一直觉深深启发了五十年后的阿贝尔和年轻的伽罗瓦。 ### `18:00` 伽罗瓦的牢狱沉思：被“学术验证器”拒绝的抽象跃迁 阿贝尔年仅 26 岁就因肺结核早逝，他虽证明了五次多项式无一般根式解，但后来听从建议将精力主要转向了椭圆函数。而伽罗瓦则将拉格朗日的萌芽推向了本质的抽象维度： - 伽罗瓦在十几岁时因政治原因身陷囹圄，他在监狱中写下了多篇深奥且充满洞见的论述。 - 他向法国科学院递交的研究论文屡次被拒——如果放在现代可验证奖励（RLVR）的语境下，当时的学术体制作为一个“验证器（Verifier）”，给伽罗瓦的评分显然是完全失败的（“Reward: 0”）。 - 被拒的部分客观原因在于，他当时的论述确实不够严密、不完整，他只是一个处于摸索阶段的年轻天才；但他凭着极其超前的直觉意识到，数学正经历着类似从具体算术走向抽象符号代数的深刻转型。 - 伽罗瓦在文章中呼吁，数学不应仅仅停留在操作公式本身，而必须跃迁到更高的抽象层级——去审视这些公式背后所蕴含的深层对称性结构。这种概念即使在当时的人类同行看来也是模糊且难以定义的，更不可能在短期内被自动化算法评判。 ### `20:00` 伽罗瓦的悲剧与跨越百年的概念检验 ```mermaid flowchart TD accTitle: 伽罗瓦理论百年验证与应用路径 accDescr: 从拉格朗日提出根的对称性，到伽罗瓦开创理论，再到刘维尔、若尔当整理以及盖尔曼将其应用于粒子物理的漫长历史演进。 subgraph Phase1["概念萌芽与开创（18-19世纪初）"] A["拉格朗日<br/>（直觉：根的对称性是关键）"] --> B["伽罗瓦<br/>（提出抽象群论结构，未给出具体反例）"] B --> C["决斗去世<br/>（笔记流落，同行无法理解）"] end subgraph Phase2["消化与现代形式化（19世纪中后期）"] C --> D["刘维尔（20年后）<br/>（识别出价值并整理笔记）"] D --> E["若尔当（再过20年）<br/>（构建出现代群论体系）"] end subgraph Phase3["物理学跃迁（20世纪）"] E --> F["盖尔曼（SU(3)群）<br/>（纯群论推导预言夸克）"] end ``` 德瓦凯什与格兰特·桑德森继续探讨伽罗瓦（Évariste Galois）的工作在当时为何极难被传统评价体系接纳。阿贝尔（Niels Henrik Abel）证明了五次多项式不存在一般根式解，而伽罗瓦理论的宏图本应是：针对任意具体多项式，给出判断其能否用根式写出解的判定准则。例如对于 $x^5 - 1 = 0$ 或 $x^5 - 2 = 0$，人们显然能直接写出根（1 或 $\sqrt[5]{2}$），伽罗瓦的目标并不是说每一个五次方程都无解，而是寻找判定特定方程的普遍规则。然而令人惊叹的是，伽罗瓦甚至在自己的论文里都没有为一个具体的五次方程构造出“证明其不可根式解”的详细实例，他的思考完全停留在高度抽象的概念层面，以至于当时的人们根本说不清楚“他究竟解决了什么具体问题”。 随之而来的便是数学史上最著名的浪漫悲剧：伽罗瓦死于决斗。流传的传说称他在决斗前夜草草写完了所有天才构想，但格兰特澄清说，实际上伽罗瓦此前曾多次尝试投稿发表，只是无人赏识。德瓦凯什打趣道：“研究五次方程看来对寿命非常不友好。”格兰特笑着附和：“要是年轻的天才，可千万别去碰五次方程。”伽罗瓦在临死前叮嘱弟弟和挚友，务必将手稿寄给高斯（Gauss）等当时最顶尖的数学家，坚信“里面必定有重要价值”。然而这份努力在最初毫无回响，整整过了20年，数学家刘维尔（Joseph Liouville）才从这些散落的遗稿中看出端倪，着手梳理伽罗瓦究竟想表达什么；又过了20年，卡米尔·若尔当（Camille Jordan）才最终整理出今天我们所认识的现代群论形态。 从拉格朗日（Lagrange）最初隐约察觉到“根的对称性才是正确路径”，到现代群论确立，走过了漫长的半个世纪。更极端的是，在当时这套理论甚至不解决任何实际工程问题。直到20世纪，默里·盖尔曼（Murray Gell-Mann）通过考察特定李群（SU(3)）的表示与对称性破缺，才在粒子物理中惊人地预言了夸克的存在。群论这种超前时代的洞察，彻底脱离了“即时可验证的解题反馈回路”。格兰特指出，这引出了一个深层问题：如果一个突破不是为了“解决眼前问题”，我们该如何衡量这种智慧？拉格朗日、伽罗瓦和刘维尔心中那份“此处必有洞天”的直觉究竟是什么？他联想到“压缩即智能”（compression is intelligence）的假说——虽然概念极简，但能预测极多未来的极小表征才是高阶智能。在未来，若想用强化学习奖励出“伽罗瓦式的直觉”，我们就必须设法奖励这种高压缩度与概念极简性（如柯尔莫哥洛夫复杂度衡量下的优雅性），而不仅仅是奖励“解出了一道题”。 - 历史神话修正：伽罗瓦并非仅在决斗前夜凭空写下理论，他此前多次尝试投稿，但其抽象思想完全无法通过当时同行的评审流程。 - 理论发酵周期：从伽罗瓦去世到刘维尔重新发现（约20年），再到若尔当将其形式化为现代群论（又过约20年），整整花了40年才被学界消化。 - 物理学远期应用：盖尔曼利用群论的分解结构预言夸克，证明最纯粹的代数对称性直觉可以超前实际物理应用上百年。 --- ### `25:00` AI证明黎曼猜想时，人类还能理解数学吗？ 德瓦凯什插入了一段由他自己录制的赞助广告，提到 Google 最新推出的 Gemini 3.5 Live Translate 功能。他回忆自己8岁前在印度长大，除英语外还会讲古吉拉特语，并现场展示了该功能在几乎无延迟的情况下保留原说话者语速和语调的实时翻译能力。他提到2024年访问中国时若有此工具，与当地学者和街头行人的交流将顺畅得多。 随后两人进入核心命题探讨：数学界当下最普遍的焦虑之一，是如果 AI 证明了黎曼猜想（Riemann Hypothesis），人类对数学的理解是否完全无法从中获益？德瓦凯什提出质疑：人类在攻克重大难题时之所以发明概念抽象和子目标，是因为这是解决复杂大问题的必经之路；那么理论上，寻找自然抽象难道不是解开黎曼猜想的更优捷径吗？从经验上看，近期 AI 在构造单位距离问题（unit distance problem）反例时，其生成的思维链（chain of thought）不仅使用了人类已知的数学常数，还证明了常数之间的关系，这让专业数学家感到完全可读并深化了现有理解，因此这种恐惧是否被夸大了？ 格兰特分析认为，AI 解决黎曼猜想的输出形态完全取决于它采取的路径类型，并细化为三种可能： 1. **跨学科连线（Lightning Bolt）**：如同今年在埃尔德什第1196号问题（关于原始集合 primitive sets）上的突破，其本质是在两个已有成熟领域间搭起桥梁。比如将自底向上的马尔可夫链概率过程与冯·曼戈尔特函数（von Mangoldt function）结合。只要向行内数学家指出始末两端的联结点，人类的大脑就能迅速跟上，这种证明完全是“人类可解析的”（human-parsable）。 2. **纯粹算力堆砌（Raw Hustle / Brute Force）**：没有任何全新理论，单纯依靠一条极其冗长、长达数千页的严密推导链条。这就像用初等方法去硬啃费马大定理，虽然逻辑成立，但人类读起来如同天书，需要耗费难以想象的“消化成本”。 3. **另起高炉建新山（Mountain Building）**：AI 凭空开创了一套庞大而全新的公理或理论框架。格兰特指出，此时最令人兴奋也最让人恐惧的问题是：AI 建造的会是一座符合人类认知审美的山，还是一座“外星山脉”（alien mountain）？ 作为类比，两人提到了数学界关于望月新一试图证明 ABC 猜想（ABC Conjecture）的公案。望月建立的“宇宙际 Teichmüller 理论”（Inter-universal Teichmüller Theory）就是典型的“外星造山”——整套语言和抽象范式与主流数学大相径庭，顶尖数学家耗费数年心力去攀登这座山峰，最终多数人却得出结论认为论证存在无法修复的漏洞。格兰特强调，AI 时代最大的噩梦不仅是 AI 堆出了一座外星理论的高山让全人类花费数年攀登后发现是错的；即使它是对的，人类要重构自身的认知抽象去“理解”它，也将面临巨大的心理与智力挑战。正如大卫·贝西斯（David Bessis）所讨论的那样，这关乎数学思维深处的理解本质。 - AI 证明的三种形态对比： - **闪电桥梁**：连接两个已有成熟领域，人类极易理解吸收。 - **纯体力暴力推导**：逻辑正确但长达数千页，概念压缩度低，人类极难消化。 - **外星造山**：引入人类未知的抽象实体与公理体系，理解成本极高。 - 现实案例：望月新一的“宇宙际几何”展示了人类在面对完全异质的理论构架时所经历的沟通障碍与验证危机。 ### `30:00` 证明经济学与“未解的解说问题” 数学界历来存在一种“定理经济学”（theorem economy）：学者提出概念定义和猜想，随后通过证明定理获取学术声誉与赞誉。然而从本质上看，证明定理往往像是寄生在“提出精妙定义”这一更底层的洞见之上。历史上一位学者提出新定义，通常也会亲自给出定理证明，荣誉分配不存在矛盾；但若 AI 彻底接管了自动证明环节，人类或者未来的 AI 就需要从密密麻麻、如同直接暴力演算出的庞大证明中去提炼、巩固更深层的概念结构。 Grant 坦言，哪怕仅仅知道一个结果已被证实是正确的，对数学探索也是极大的助力。探索新数学的过程往往不是沿着正确的台阶稳步登山，而更像是一场“醉汉随机游走”（random drunken walk），绝大多数时间都在犯错和推翻自我。如果预先确知某个方向最终能够通向正确解，探索者就能更有底气地去咀嚼消化中间的机理。在数学史上，认知“力不能及”的现象屡见不鲜：许多定理在被真正理解其“本质原因”之前，就早已在形式上被证明了。 Grant 特别提到了数学家蒂莫西（Timothy Chow）在一篇关于“力迫法”（forcing）的阐释性论文中的开篇。连续统假设探讨在自然数的无穷与实数的无穷之间是否存在中间大小的无穷，其答案依据公理系统的不同而既是肯定的也是否定的（超出了标准公理体系的范畴），而证明该结论所用的力迫法极其艰深晦涩。作者在此提出： > “人人都知道什么是未解的研究问题（unsolved research problem），但我更想提出‘未解的解说问题’（unsolved expository problem）——也就是某些东西我们固然证明了它，但我们其实根本不知道它为什么是真的。” Grant 对这种表述深有共鸣，因为他制作 3Blue1Brown 的核心使命就在于探索最清晰的理解方式，明确区分出“证明”（proof）与“解释”（explanation）的鸿沟。 ```mermaid flowchart LR accTitle: 传统数学研究与AI时代的范式转移 accDescr: 对比传统数学研究中定义与证明合一的模式，与未来AI承担机器证明后人类转向概念提炼与解释的过程 subgraph Traditional["传统数学范式"] T1["提出全新定义与猜想"] --> T2["手工推导定理证明"] T2 --> T3["收获学术声誉与直觉"] end subgraph Future["AI时代的重塑"] F1["人类/AI 提出猜想"] --> F2["AI 自动化定理证明<br/>(如直接代数/暴力推导)"] F2 --> F3["未解的解说问题<br/>(消化、巩固并寻找解释)"] F3 --> F4["提炼高维直觉与理论体系"] end ``` ### `33:45` 伟大洞见与清晰表达的同构性：AI 是否会抢走解说者的工作？ Dwarkesh 提及此前与 Grant 午餐时的讨论：爱因斯坦的狭义相对论借助闵可夫斯基时空图（Minkowski spacetime diagrams）生动展示了尺缩钟慢效应，但这种时空图不仅是辅助教学的“阐释”，它本身就构成了解释客观现实的物理本质。在极限情况下，概念化工具与想法本身是否本就是同一回事？ Grant 回应道，真正提出颠覆性创见的科学巨擘往往同时是极度清晰的沟通者，例如阿尔伯特·爱因斯坦（Albert Einstein）、克劳德·香农（Claude Shannon）以及理查德·费曼（Richard Feynman）。大学生的普遍体会是授课顶尖专家往往讲不明白基础概念，但翻阅那些真正开拓维度的奠基性论文时，会发现其文笔极度透彻、毫无故作高深的晦涩。这表明，在大脑中负责构想全新研究视角的区域，很可能与擅长化繁为简、通俗表达的区域存在同构性。 基于这种同构性，Grant 修正了自己过去的判断： - **曾经的预期**：AI 会演化为高效的自动化定理证明器，而人类数学家将全面退守至 Grant 现有的角色——充当解说者、消化者与提炼者。 - **当前的修正**：能够提出跨时代洞见的 AI，很可能在解释与提炼方面同样胜过绝大多数人类，数学家未来的最后堡垒未必会是“做解释”。 ### `36:00` 馆长角色与社交纽带：数学家与科普创作者的未来 如果 AI 既能做突破性研究又能提供一流解释，人类数学家和解说创作者最后还能做什么？Grant 认为，哪怕到了最后，自己依然会做现在正在做的事情，并打趣道：“授人以鱼不如授人以渔，但若把一个人点着了，他就一辈子都很暖和了。” Grant 提出，数学家未来的职能将演变为类似**艺术博物馆策展人**（art museum curators）： - **意义筛选而非从零计算**：在一个近乎无限的证明与新想法空间中，关键在于为人类导航，指出哪些想法真正值得投入注意力去体会。 - **作为社交现象的求知欲**：人对某件事物产生兴趣、产生探索动机，本质上是一种社交体验与人际信任。就像听众收听播客是出于对主播选品眼光的信任，3Blue1Brown 的核心成本也不是制作动画，而是决定哪些概念值得讲、哪些不值得讲。 - **对人类背景故事的执念**：即便模型输出的 MP3 音频在客观音质或编曲上超越人类，真人音乐人依然无可取代，因为其背后承载着真实的人生经历与社交叙事。 ### `38:08` 从解决孤立问题到宏大联结：朗兰兹纲领的启示 随着 AI 跨越门槛，能够联结已有知识并证明新推论，Dwarkesh 提出一个疑问：像广义相对论这般重大的飞跃，在底层也是将黎曼几何与狭义相对论这两大已有领域做跨界融合，那么在 AI 不断打通跨学科桥梁的未来，最伟大的突破是否从质上而言也只是更高维度的概念拼图？ Grant 指出，外界谈论数学往往聚焦于“攻克孤立的猜想”（如解决埃尔德什猜想），但绝大多数核心数学家并不将自己的工作定义为猎杀单个难题，而更接近于**朗兰兹纲领**（Langlands program）的精神： - 费马大定理的证明本质上揭示了两个截然不同数学领域之间的深刻对称性与通道。 - 罗伯特·朗兰兹（Robert Langlands）当年在一封著名的信件中，系统性勾勒出数学宏观版图的猜想，预言在那些看似完全孤立的群山、平原与深谷之间，必然存在着贯穿全局的隐秘桥梁。 - 对许多顶尖学者而言，数学的真谛不在于打掉一个靶子，而在于为这幅壮丽的全局地图勘探出未知的路网。 ### `40:00` 跨学科连接器与自回归生成的“上下文奴隶”困境 数学家的研究往往呈现出一种鲜明的分野：一类人专注于精准狙击并攻克某个具体的孤立难题；另一类人则更接近于朗兰兹纲领（Langlands program）的风格，致力于在看似风马牛不相及的数学版图之间铺设未知的桥梁。这类跨领域的突破往往不是为了解决眼前的单一问题，而是凭直觉预判到连接本身蕴含的巨大破坏力。虽然将 AI 塑造成一个“超级连接器”前景诱人，但 Grant 指出这极难量化评估——攻克一个悬案可以迅速写成公关头条，宣称“AI 解决了某某问题”，而识别出两个领域的深层关联却无法简单打分，极度依赖人类专家参与验证。Grant 预测未来五年 AI 最有价值的进展可能正是填补这种跨学科专家的连接空白，但他同时也对当前模型的技术底层表达了深层困惑：为什么掌握了所有领域知识的模型，至今仍未普遍展现出这种联想能力？ ```mermaid flowchart TD accTitle: 自回归思维局限与多智能体上下文重置 accDescr: 对比单一自回归链条陷入上下文局部陷阱与多智能体系统通过上下文刷新实现跨领域跳跃的过程 subgraph SingleAgent ["传统单一自回归链条（易受上下文奴役）"] A["局部专业问题 Prompt"] --> B["自回归预测下一 Token"] B --> C["沉没于高概率局部上下文"] C --> D["错过极其罕见的跨学科跳跃"] end subgraph MultiAgent ["智能体系统与上下文重置（模拟普林斯顿高研院）"] E["领域 A 专家智能体"] --> G["跨领域碰撞 / 交互环境"] F["领域 B 专家智能体"] --> G G --> H{"陷入死胡同？"} H -- "是" --> I["强制清空 / 重置上下文"] H -- "否" --> J["催生意外连接（如戴森-蒙哥马利跨界启示）"] I --> G end ``` Grant 认为根源可能在于自回归思维链（Autoregressive Chain of Thought）本身的荒诞性。他提出了一个生动的思想实验：想象把一个聪明绝顶的大脑锁在黑盒子里，唯一的交互方式就是外界递进一张纸条，要求他“预测接下来的内容”，写完一个字后立刻抹去其记忆，再递进下一张纸条。如此往复生成的整篇文章，作者本人回头看时大概会觉得奇烂无比，因为这根本不是人类构思与通盘审视一篇文章的思维方式。这种机制让模型沦为了“上下文的奴隶”（slave to your context）：当它回答某一具体领域的问题时，全部注意力都被局部的先验语境所俘获；而那些真正带来质变的突破性联想，在概率分布上恰恰属于“极不可能出现的下一个 Token”。现有的强化学习很难明确奖励这种低概率却高价值的跨界飞跃。 - **数学研究的双重范式**：类似朗兰兹纲领的“织网者”（Preemptively finding connections）与专注特定攻坚靶点的“解题者”（Targeting one particular problem）。 - **“黑盒写作者”假说**：自回归生成每一步都在追逐局域最可能的延续，反而系统性抑制了产生跨学科“闪电一击”（lightning bolt to another field）的创造性偏差。 --- ### `43:40` 训练环境的激励与数字心智的并行扩展优势 针对架构局限的怀疑，Dwarkesh 提出了不同视角：与其纠结于自回归架构甚至损失函数，不如审视数据与训练环境的激励机制。正如文本扩散模型并未带来本质不同的认知结构一样，AI 智能体之所以在自主编程上突飞猛进，是因为它们被置于真实的代码执行环境中，学会了“退后一步、全盘搜索代码库、审视自身错误”的宏观策略。在数学与科学探索中，只要设计出必须联通两个相距甚远的领域才能解开的“前沿难题”，甚至通过消除假设等半合成（partially synthetic）手段主动制造挑战，环境本身的反馈就能强迫自回归模型学会跃出单一语境。 更重要的是，数字心智拥有一种人类天才无法企及的核心物理特性：近乎无限的并行化与规模化扩展能力。在数学史上，人类文明往往依赖极少数兼具怪才与偶然灵感的个体——比如“在做出几项连接后就死于决斗的个别异类天才”（暗指年轻早逝的埃瓦里斯特·伽罗瓦）。而 AI 公司因公关和算力竞赛注入的数十亿巨资，正将某种认知基线普遍且均质地平推到所有可解问题上，“数量本身就能转化为一种独特的质量”。 这种并发优势让人联想到普林斯顿高等研究院（IAS）的经典传奇：数论学家休·蒙哥马利（Hugh Montgomery）在下午茶歇时偶然与物理学家弗里曼·戴森（Freeman Dyson）交谈，戴森立刻指出蒙哥马利关于黎曼 Zeta 函数零点对相关性的公式，与量子力学中随机矩阵（高斯酉系综）的特征值分布完全一致。这一数学史上的顿悟完全源于地理空间的物理聚合与偶然交谈。而在 AI 世界中，人们完全可以实例化成千上万个分别精通不同领域的虚拟专家智能体，通过系统化工程调度，全天候模拟并催生这种跨领域的“下午茶偶遇”。 - **环境塑造行为**：通过合成必须跨界才能推导的边界问题，利用强化学习倒逼模型建立跳出当前领域的思维跃迁模式。 - **并行化与均质水位线**：AI 打破了单体人类大脑寿命短、知识孤立的物理约束，可以在海量并发副本间同步知识并平铺式攻坚。 - **IAS 顿悟的自动化复制**：将蒙哥马利与戴森式的偶然跨界火花，转变为可编程、高密度的智能体交互常态。 --- ### `46:45` 上下文重置的力量与陶哲轩也曾折戟的 IMO“钓鱼题” 与知识汇总同样强大的另一种数字心智特权，是彻底的“上下文重置”（refresh your thinking）。人类和 AI 在推理时都极易陷入思维定势和有毒的思维链（bad chain of thought），但人类往往由于沉没成本和认知惯性难以自拔——人类极难在投入数年后突然命令大脑彻底清空既有偏见、完全反向证明“该命题不可行”。然而在 AI 系统中，我们可以随意分发截然不同的上下文切片，甚至在模型走进死胡同后一键抹去记忆让其重新破局。 为了说明摆脱上下文绑架有多困难，Grant 剧透了他制作的 AI 与数学专题片首集内容。该集聚焦于 AI 攻克国际数学奥林匹克竞赛（IMO）的里程碑，但 Grant 特意挑选了一道 AI 全军覆没、且令无数顶尖选手乃至菲尔兹奖得主陶哲轩（Terence Tao）都失手翻车的赛题。参赛者普遍对这道题感到愤怒，斥之为一道“钓鱼题”（troll problem）。这道题的绝妙之处在于：在 IMO 这种殿堂级竞赛的宏大语境下，它表面上展现出一种极其诱人、充满奥赛技巧的美妙证明路径，所有顶尖大脑都会本能地顺着那条看似崇高的复杂解法钻牛角尖，竭尽全力试图证明该构造是最优解；然而现实极其残酷——这道题的最优解其实粗暴平庸到了极点，近乎是“脑残级别”（brain-dead simple）的简单解法。 ```mermaid flowchart LR accTitle: IMO 钓鱼题的思维盲区机制 accDescr: 展示顶尖奥赛选手因陷入精英上下文偏见而失败，以及普通直觉直接破局的过程 subgraph Trap ["精英选手的认知陷阱（被语境绑架）"] A["身处 IMO 决赛赛场"] --> B["预设必有高深优雅的奥数结构"] B --> C["陷入复杂证明的死胡同<br/>（AI、顶尖学生与陶哲轩皆卡在此处）"] end subgraph Escape ["跳出语境的直觉解法（街头脑筋急转弯）"] D["街头随机路人视角"] --> E["视作毫无包袱的趣味谜题"] E --> F["极其平庸却直接破局的最优解"] end ``` Grant 感叹道，要做出这道题，一个人首先必须具备“逃离上下文”的能力——彻底忘掉自己正身处崇高的 IMO 考场，抹去多年受训形成的奥赛思维定势。如果把这道题伪装成街头即兴抛给路人的脑筋急转弯，普通人反而更容易答对。在现实的科学研究中，许多世纪难题同样被人类学者堆积的陈旧范式所笼罩。AI 若能通过外部算法干预，系统性地清空心智包袱、强行以完全异质的初学者视角切入问题，这种冷酷摆脱上下文绑架的能力，或许将成为机器心智相较于人类大脑最深不可测的优势之一。 - **IMO 钓鱼题特征**：外观具有极高迷惑性，诱导高手采用精巧繁复的奥赛套路，掩盖了粗暴直接的本质真相。 - **陶哲轩的失误启示**：即便是人类顶尖数学直觉，在特定权威语境的高压诱导下，也极难主动切断思维惯性。 - **系统性思维刷新的工程化**：数字心智不受自尊心与沉没成本拖累，能够以真正的“白纸状态”对难题展开不同范式的压力测试。 ### `50:00` 对抗模型“熵崩塌”：通过多 Agent 提示词注入多样性偏见 在探讨多 Agent 协同解决数学问题时，德瓦凯什·帕特尔（Dwarkesh Patel）和格兰特·桑德森（Grant Sanderson）讨论了一种工作流：派生出不同背景的独立 Agent，一个负责证明猜想，另一个专门负责反驳，或者各自采用截然不同的推理路径且刻意隔离上下文。人们常常担忧大语言模型存在所谓的“熵崩塌”（Entropy collapse）——因为模型都在相似的数据集上以相似的方式训练，推理时往往滑向同一条平庸的路径，这也是 AI 在文学写作中句式千篇一律的原因。然而，AI 的巨大优势恰恰在于可以被系统化地“人为增熵”。例如在单位距离问题（Unit Distance Problem）中，人类数学家此前之所以迟迟未能证伪该猜想，很大程度上是因为大家都潜意识里认定它是对的，把所有精力都耗费在尝试证明它成立上。如果能用多 Agent 系统，同时向相反方向（寻找反例 vs. 寻找证明）施加对立的预设偏见，就能打破人类思维的定势。 人类科学史上许多关键突破本身就源于某些强烈的“偏见”。比如爱因斯坦（Albert Einstein）极度执着于“不同参考系中物理规律必须保持一致”的直觉信念，这是他狭义与广义相对论的基石；但他同样固执地持有“上帝不掷骰子”（God should not play dice）的偏见。格兰特指出，如果把所有大模型都提示（Prompt）成爱因斯坦，整个量子力学的发展就可能彻底停摆。这恰恰证明科学探索中不存在唯一的“正确启发式”（Heuristic），科学进步依赖于多个持有互斥偏见的独立研究项目并行探索。在技术实现上，虽然自回归生成过程本身存在收敛和熵减的倾向，但我们可以利用传统的软件架构，在提示词层面对探索本体（Ontology）进行系统化展开。最简单的策略是二元对立（“证明它”与“推翻它”），而更深层的设计则是系统性地枚举并分发所有已知的数学策略，确保大模型拥有足够的广度去覆盖整个解题空间。 ```mermaid flowchart TD accTitle: Multi-Agent Prompt Entropy Expansion accDescr: 结构展示如何利用提示词层面的多样化偏见来对抗大模型的自动回归熵崩溃。 subgraph PromptLevel ["提示词层：系统化增熵 (Prompt-Level Entropy)"] Ontology["策略与假设本体图谱"] A1["Agent A: 执着于寻找反例 (反驳者)"] A2["Agent B: 执着于代数推导 (证明者)"] A3["Agent C: 尝试跨学科映射 (几何/拓扑)"] end subgraph AutoRegression ["自回归推导层 (Auto-regressive Search)"] R1["反例搜索与图论验证"] R2["逻辑引理推导"] R3["结构等价性验证"] end subgraph Resolution ["收敛与验证 (Resolution)"] Verify{"形式化或确定性判定"} Outcome["打破定势思维，获得非对称突破"] end Ontology --> A1 & A2 & A3 A1 --> R1 A2 --> R2 A3 --> R3 R1 & R2 & R3 --> Verify Verify --> Outcome ``` --- ### `52:30` 为什么数学进展迅猛，而电脑操作却停滞不前？“可刷性”与样本效率 德瓦凯什分享了自己使用 Cursor 工具链的体验（例如自动剪辑发往 Bilibili 频道的无广告版播客视频，或者在准备采访时让大模型直接检索包含大量专著论文的本地代码库），并由此切入一个核心问题：为什么 AI 在数学领域取得突破的速度远超其他真实世界任务？许多人将原因归结为“领域的可验证性”（Verifiability），但他认为人们忽视了另一个同样关键的支柱——“可刷性”（Grindability，即能否进行低成本、高并发的大规模试错与刷经验）。 作为一个对比鲜明的切片，通用电脑操作（Computer Use）在逻辑上同样具有极高的可验证性（例如 Etsy 订单是否送达、日历行程是否预订成功都是确定无疑的二元状态），但它极其匮乏“可刷性”。现实中的网站布满了反爬虫与机器人检测机制，在诸如亚马逊结算流程之类的现实服务上并发跑上千次模拟，不仅算力与金钱成本极高，还会立刻被安迪·贾西（Andy Jassy）直接封号。深度学习至今仍未解决“样本效率”（Sample efficiency）难题，模型仍然是在“用极细的吸管吮吸监督信号”（Sucking supervision through a straw）。要想让模型学会一项技能，就必须依赖海量并行试错（Rollouts）。在数学与编程领域，你可以将特定进度的代码仓库完全容器化（Containerize），并行拉起成千上万个轻量容器，而且运行过程是完全确定性（Deterministic）的。这种确定性完美解决了强化学习中的“信用分配难题”（Credit assignment problem）——你能精准确认两组试错中究竟是哪一行 diff 决定了成败。相反，现实世界环境每一天都在变化，无法容器化，无论是建立盈利公司还是在二级市场高频交易，都不可能在离线模拟器中无限“刷级”。数学恰恰具备这种无须与动态真实世界发生交互、随时随地可以被确定性“刷经验”的绝佳特质。 --- ### `56:15` Lean 形式化证明的真正价值：像 AlphaZero 一样脱离人类视线无休止进化 关于数学突破的原因，学界普遍认为 Lean 这类形式化交互式定理证明工具功不可没。但德瓦凯什提出质疑：从实验室外部来看，当前的很多前沿突破（例如对单位距离问题猜想的证伪）在模型公开的思维链（Chain of Thought）中其实纯粹是用自然语言写成的，压根没用 Lean。DeepMind 在国际数学奥林匹克（IMO）上的演进路线也佐证了这点：第一年他们试图将所有内容编译成 Lean，而第二年就转向了纯自然语言推理。这表明，Lean 提供的“过程级监督”（Process-based supervision）在现阶段或许没有人们想象中那么重要，真正驱动突破的依然是具备确定结果的“可刷性”。 格兰特虽然赞同这一观察，但他从另一个维度为 Lean 的长期价值做了辩护：形式化环境蕴含着一种尚未被完全释放的终极能力——类似于 AlphaGo 和 AlphaZero 的“完全自主无休止探索”。在自然语言数学中，哪怕 AI 找到了某个猜想的反例，最终依然需要人类数学家介入审查确认“看起来没毛病”，人类的认知带宽构成了探索的天花板。但如果依托于 Lean 和 Mathlib（致力于将人类全部数学转化为机器可验证代码的开源项目），情况就彻底变了： - **无限脱机探索**：可以为 AI 专门派生一个独立的 Mathlib 代码库，让它在无需任何人值守的情况下永不休眠地运行。 - **自主生长定理树**：模型可以自行定义概念、提出猜想并自动证明引理。哪怕其中 99% 的推导可能是平庸无用的，但在庞大的算力浇灌下，它会如同一棵无限延展的数字定理树自行繁衍。 - **十年磨一剑的涌现**：这在人类科学所有领域中独一无二。你可以点击“开始”，向它倾注整整十年的算力且完全不看一眼；十年后再回来看它的提交记录，它必然会沉淀出某种真正深刻且无可置疑的数学洞见。 - **与自然语言的本质分野**：在纯自然语言模式下，离开人类纠偏模型很快就会出现逻辑漂移和幻觉累积；只有借助 Lean 这类机械验证器提供的闭环奖励，AI 才能真正跨入纯自主的数学无人区。 ### `01:00:00` 自主科研、遍历公理空间与过程化监督 Dwarkesh 提到 Andrej Karpathy 提出的“自动科研（auto-research）”实验：用单个 Python 文件编写基础 LLM 训练代码，并让多个 agent 不断对代码做修改，只要能缩短训练加速赛（speed run）的耗时，就把改动保留下来。前去解释过 AlphaGo 原理的 Eric Jang 在尝试训练顶尖围棋 AI 时也做过类似实验，他发现这类系统非常擅长顺着某条实验路径快速推进，但极其不擅长在死胡同前及时刹车，也不擅长处理极端并行化的探索。 ```mermaid flowchart TD accTitle: 自动探索与形式化验证机制对比 accDescr: 展示了从公理生成到过程验证，再到形式化绿色勾选对数学研究信任链条的支撑流程。 subgraph S1["假说与探索阶段"] A["生成新修改 / 新公理"] --> B{"过程验证模型 (LLM Verifier)"} B -->|"元验证器把关 (Meta-Verifier)"| C["可信自然语言推演"] B -.->|"逻辑漂移 / 随机游走"| D["死胡同或垃圾结论"] end subgraph S2["严格确证阶段"] C --> E["Lean 形式化系统"] E --> F["确定性绿色勾选 (100% 正确保证)"] end ``` Grant 指出，这种范式在极限状态下其实正是人类数学共同体的运作机制：全人类在既有知识库（如 Mathlib）的基础上，不断以有趣且有用的方式进行扩展。在没有明确目标函数（outcome-based supervision）的情况下，只要保证每一步逻辑是正确的，就能不断前行；但为防止逻辑空间中的纯粹“随机游走”，依然需要一个监督模型来提供“这是否有价值”的启发式直觉。 这种探索能力的潜力在陶哲轩（Terence Tao）提及的一项研究中得到了绝佳体现：利用机器穷举搜索可能的代数系统（axiomatic algebras）。 - 群论的公理体系如果没有背景动机，初看像是任意拼凑的规则；若用自动证明器去全面遍历公理组合，绝大多数体系最终都会坍塌为毫无意义的平凡结论。 - 然而，在浩瀚的荒原中偶尔会出现极为丰富的“孤岛公理系统”，能推导出一整套深刻的定理网络。 - 人类甚至可以事后为这些公理赋予现实意义（就像群论与对称性的对应关系一样），这种对逻辑推论的全局探索正是自动化证明器最擅长的“看家本领”。 ### `01:02:40` DeepSeek-Math 与自然语言验证器的边界 讨论转向在脱离 Lean 等形式化语言的环境下，能否单靠自然语言实现过程化监督。Dwarkesh 提到了 DeepSeek 发布的 DeepSeek-Math 论文：他们通过训练一个专门的验证器（verifier），并配合一个更高层级的“元验证器（meta-verifier）”来纠正验证器的评判，使其在 Art of Problem Solving 等题库上提供极其扎实的过程反馈，从而成功提升了数学推理能力。 编程 Agent 的演进也呈现出类似趋势：通过过程化的“LLM as a judge”，模型不仅能写出能跑通的代码，还能给出具备代码品味（code taste）的重构方案、消除重复的模块。既然自然语言验证在代码和竞赛数学中行之有效，为什么它在长篇写作上却屡屡受挫？ - **写作评分与奖励作弊（Reward Hacking）**：LLM 很容易评判出哪篇学生作文更切题、更准确（比如区分 B 等与 A 等论文）；但在区分真正的优质文章与“表面光鲜但缺乏洞见的平庸之作（B*）”时彻底失效。 - 面对专门堆砌好词好句、迎合评分偏好的文章，验证器往往会被误导，导致强化学习彻底偏离正轨。 - 相比之下，数学证明在逻辑层面存在不可动摇的正确性边界，因此自然语言验证在数学领域的可信度远高于常规写作。 ### `01:05:00` 为何数学家不能承受 1% 的错误率：Lean 的不可替代性 Grant 强调，即使自然语言数学推理能取得巨大进展，Lean 这类形式化系统依然具有不可替代的核心价值。这与 AlphaGo 著名的“第 37 手”非常相似——形式化系统彻底切断了与既有人类直觉的旧有联系，让模型可以完全抛弃先验偏见，自由探索全新的逻辑树。 更关键的现实痛点在于“验证成本与信任危机”。数学家 Alex Kontorovich 曾尖锐地指出：如果未来 AI 每天输出 10 篇纯自然语言撰写的数学论文，哪怕其正确率高达 99%，对人类数学家来说也是一场无法承受的灾难： - 审查数学论文寻找逻辑漏洞是一项极其耗时费力的高强度劳动； - 只要存在 1% 的出错可能，学者就会陷入巨大的心理内耗，担心自己花费数周时间研读的成果最终是一篇彻头彻尾的废纸； - Lean 等形式化语言带来的最大价值，在于那枚**绿色的检查通过勾（green checkmark）**。它向所有人提供 100% 的绝对确信：即便证明过程再复杂晦涩，其底层逻辑也绝对无懈可击。 世上绝大多数学科都极度渴求这种确证能力，唯独数学能够通过将自然语言证明转化为形式化代码来享有这种奢侈。两人一致认为，人类数千年来建立的数学知识宝库（如 Mathlib）被浓缩进模型中，再由机器无限扩展，构成了文明演进的惊人隐喻。 ### `01:07:07` 写作与代码的本质差异：模块化与解释性 针对“为什么 AI 写作的进展明显落后于数学和代码”，Dwarkesh 提出了模块化假说： - **代码与数学具有高度模块化**：同一个函数或引理可以有无数种实现路径，只要接口与结果正确，它就能与其他模块组合。代码本身只是生成最终软件的中间工具。 - **写作本身即是最终产品**：在文章中，每一个词、每一个句子和段落都是实质内容，无法与最终产物剥离，因此容不得半点像糟糕代码那样隐藏在底层的胡言乱语（slop）。 然而 Dwarkesh 紧接着指出一个反直觉的现象：人们常常抱怨 AI 写不出有深度的文章，但在日常生活中，当面对晦涩难懂的人类专业文本时，大家的真实偏好（revealed preference）往往是把段落直接复制粘贴给 LLM，让它“用更清晰的语言解释一遍”，而模型的解答通常比人类专家的原始表述更易懂。甚至在与领域专家实时通话时，如果遇到一个先验概念不明白，最理想的体验其实是让专家暂停一分钟，自己偷偷问完模型后再继续请教人类专家独有的未公开知识。 Grant 对此进行了解构与澄清：这种能力本质上是**提炼与蒸馏（distillation）**。 - 如果任务是阅读一本书并撰写读书摘要，LLM 无疑是个绝佳的解释者； - 但人类评判“优秀写作”的标准绝不仅仅停留在清晰解释已有概念。写作的核心灵魂在于：**新颖的思想究竟是什么？** 模型能够高水准地重组已知信息，却在提出具备深刻洞察力的新思想上依然举步维艰。 ### `01:10:00` 自回归模型为何写不出好文章：缺乏“不可预测性”与心智模型 探讨 AI 写作局限时，Grant Sanderson 指出自回归（autoregression）在生成内容上存在一种天然的别扭感。优秀的写作必须包含某种“不可预测的元素”，这绝非简单在模型参数里调高 temperature 就能解决，而是要在最恰当的时机做出出人意料的转折，从而带来直击人心的顿悟。即使大语言模型在提炼现有内容上表现出色，但最初那本被提炼的杰作从何而来？它出自真人作者在现实世界中的漫长探索：作者反复权衡哪些观点真正有趣，通过怎样的方式才能构建起连贯且动机明确的叙事，最终将它们融为一体。人们真正推崇的原创作者，其原著价值远非 AI 提炼版本所能替代。AI 写作之所以显得平庸乏味，正是因为它缺乏这种刻意打破常规、敢于提出反直觉创见的不可预测性。 Dwarkesh Patel 从另一个维度切入：大模型极度缺乏构建精细“心智模型”（mental model）的能力，而这恰恰是写作的灵魂所在。他提到 Andy Matuschak 与合作者曾做过一项引人深思的研究——尝试训练大语言模型编写高质量的间隔重复（spaced repetition）记忆闪卡。业界都在高谈阔论 AI 将在一年内实现递归自我改进，然而尖端研究者使用强化学习、微调开源模型、思维链（Chain of Thought）以及最强大的闭源模型超长提示词，依然无法让大模型写出合格的抽认卡。Dwarkesh 剖析其核心症结在于：编写一张优秀的闪卡，需要写作者精准投射并模拟用户“三个月后”的大脑状态——预测对方届时会如何联想这个问题、脑海中会浮现何种答案、以及怎样的提问方式才能准确激发你希望他们从原文中带走的精髓。写作同样是一场极其耗费心力的心智模拟过程，作者必须在每一个字、每一句话上下工夫，反复推敲读者读到这里时的心理图景（甚至调整句式顺序，让特定画面先于整句话在读者脑海中成形）。这种需要对全局通盘考量、类似扩散（diffusion-like）式的整体推演，正是逐词生成的自回归机制难以企及的。 ```mermaid flowchart TD accTitle: 人类深度写作与大语言模型自回归生成的对比 accDescr: 对比人类基于心智模拟和出人意料的洞察与大模型逐词自回归概率生成的差异 subgraph Human["人类心智写作机制"] A["现实世界深度探索与洞察"] --> B["构建读者心智模型 (Theory of Mind)"] B --> C["全局构思与精妙转折 (扩散式推演)"] C --> D["引人入胜的深度原创作品"] end subgraph LLM["自回归语言模型生成"] E["统计概率与已有文本库"] --> F["逐词预测下一步 (Token by Token)"] F --> G["趋同平均与局部最优 (缺乏具身共情)"] G --> H["平庸乏味的蒸馏/提炼输出"] end ``` --- ### `01:13:00` 具身模拟与“心智理论”的缺失：为什么 AI 无法真正共情 针对大语言模型在心智化（mentalizing）方面的挣扎，Grant Sanderson 提出了一个生动而深刻的具身认知视角。他回忆起一项关于情商测试的心理学实验：测试者需要观看人脸表情卡片并从四个选项中辨别其确切情绪。日常生活中社交敏锐度高的人得分往往极高，而偏向数理逻辑思考的人表现稍逊。更有趣的对照实验显示，刚刚注射了肉毒杆菌（Botox）导致面部肌肉僵硬的受试者，在情绪识别测试中的准确率明显下滑。这一现象背后的机制在于，人类理解他人情绪的过程依赖于自身面部肌肉在潜意识层面的微表情模仿与镜像反馈——正是自身肌肉的下意识收缩，让大脑体会到“这就是焦虑”。 Grant 据此指出，大模型缺乏心智理论（Theory of Mind）完全合情合理。尽管模型读遍了人类所写的一切文字，博览群书无所不知，但它们没有任何面部肌肉，其运作底层机制与生物大脑截然不同。这好比一个地外外星文明试图对人类产生共情；对 AI 而言，心智理论需要作为一种极度复杂的“涌现”属性被硬生生演化出来，而人类却拥有与生俱来的现成生理硬件，能直接将对方的情感状态无缝置入自己的心智中去感受。 - **肉毒杆菌表情测试实验**：受试者面部肌肉注射肉毒杆菌受限后，识别他人细微情绪的能力显著下降，证明共情依赖具身模拟机制。 - **大模型共情鸿沟**：缺乏物理躯体与神经镜像反馈回路的大模型，在理解读者当下理解瓶颈和情绪状态时存在天然壁垒。 --- ### `01:15:00` 简街资本（Jane Street）的模糊角色文化与复合型人才成长 在进入学习方法话题前，Dwarkesh 提到两人都与量化交易巨头简街资本（Jane Street）有合作，并询问 Grant 在接触中发现其独特的企业文化是什么。Grant 分享了他近期为 Jane Street 录制的一期罕见深度访谈（该公司极少制作对外展示的公开内容）。Jane Street 在业内以极其惊人的员工留存率著称，员工入职后极少离职。 Grant 观察到一个极具启发性的现象：虽然公司内部存在“研究员”（researcher）、“交易员”（trader）或“工程师”（engineer）等正式头衔，但同事之间往往根本不知道彼此确切的官方职位。因为那里的每个人都在交叉参与所有事务： - 官方头衔是交易员的人，平时投入大量精力在量化研究上； - 官方头衔是研究员的人，日常在编写海量系统代码。 Grant 分析，正是这种模糊的岗位边界与灵活的职责机制，让所有渴望持续学习与成长的人能够不受限制地涉猎多样化的领域，从而铸就了其无与伦比的团队留存率。Dwarkesh 随后打趣地帮 Grant 做了宣传，引导感兴趣的听众前往 `3b1b.co/janestreet` 观看完整访谈。 --- ### `01:16:02` 人类导向的学习之道：从维基百科陷阱到高质量内容寻宝 转向如何利用大模型学习数学与复杂概念的主题，Dwarkesh 坦言自己经常遇到瓶颈：刚问前几个概念时大模型很有帮助，但多追问几轮后，模型要么自己陷入逻辑混乱，要么越解释越让人糊涂；而在现实中，一位优秀的专业学者只需三分钟就能彻底点醒自己。他向长期深耕数学教育与视觉呈现的 Grant 请教如何高效使用 LLM 辅助学习。 Grant 分享了自己在 LLM 出现之前就恪守的核心学习哲学：“人（Who）往往比内容（What）更重要”。他给大学生的选课建议是：不要过分受制于自己当前那些随意形成的先验兴趣，而要优先关注授课老师是否是一位顶尖的教育者、其思维风格是否能与你产生共鸣；选书同样如此，与其围绕某一冷冰冰的主题搜寻平庸论著，不如顺藤摸瓜将你喜欢的优秀作者的所有其他著作全部读完。 Grant 进一步将当今的 LLM 解释比作维基百科（Wikipedia），并将其与由单一学者倾注心血撰写的权威著作（如《斯坦福哲学百科全书》（Stanford Encyclopedia of Philosophy）或《普林斯顿数学指南》（The Princeton Compendium of Mathematics））进行了犀利的对比： 1. **维基百科模式（局部极小值）**：由于采用群体协作和严苛的逐句纠错，词条陷入了一种每个单句都力求绝对正确，但全篇缺乏统一叙事动机与灵魂的“局部最优”状态。真正优秀的教学需要作者敢于先抛出“稍有瑕疵、甚至刻意写错但直观好懂的粗糙模型”，再带领读者一步步修正，而维基百科机制和当前的 LLM 往往直接抹杀了这种极佳的教学铺垫。 2. **LLM 的最佳打开方式**：就像维基百科最有价值的部分往往是页面底部的参考文献列表一样，大模型最强大的用途并非让它直接充当导师向你解释一切，而是把它当作“终极强化版 Google”，用它来精准定位最优秀的人类原创资源。 Grant 举了一个自己被 Claude“幽默欺骗”（gaslit）的真实案例：他在自学半导体相关物理知识时，觉得纯文字解释极其抽象乏味，于是向 Claude 询问是否有高质量的视觉化讲解视频。Claude 热心推荐了排在第一位的“3Blue1Brown 制作的半导体概念视频”。Grant 哭笑不得，因为他万分笃定自己从未做过这个主题。点开链接后，他发现这是一个真实存在且制作极为精良的高质量视频，只是 Claude 张冠李戴地将别人的佳作冠上了 Grant 的名字。但这依然带来了一次极佳的学习体验——顺着 AI 提供的优质人类创作者视频，他瞬间掌握了知识。 Dwarkesh 深度赞同这一观点，总结指出：最高效的学习模式永远始于人类精心打造的精神产物（文章、专著、视频）——唯有人类创作者能够搭建起环环相扣的认知台阶，清晰阐释为何为了解决下一个难题必须引入下一个新概念；而在这一主干逻辑确立后，大语言模型最适合的角色仅仅是在人类主干周围修剪枝叶，协助解答零星的局部盲点。 ### `01:20:00` 学习中的策展、LLM 的局限与教学的“心智理论” Dwarkesh 分享了自己最近的学习经历：他正在阅读 Grant 推荐的 Steven Strogatz 关于混沌与非线性动力学的经典教材，体验极佳，甚至形容读这本书的感觉就像在看 3Blue1Brown 的视频一样过瘾。他的学习工作流是在屏幕上同时平铺三部分内容：左边三分之一是大学的公开课视频，中间是配套教材章节，右边则是大语言模型（LLM）。他感慨道，如果当年在大学课堂上听这种快节奏的现场讲座，自己肯定完全跟不上；如今借助 LLM 互动、暂停思考和对照课本，才能深入吸收。但整个体验的核心支柱，依然是像 Strogatz 这样的优秀学者在宏观上进行精心**策展（Curating）**——决定概念的引入顺序、设计能够激发思考的典型动机问题。 Dwarkesh 进一步指出 LLM 在教学交互上的严重短板：顶尖的人类名师具有一种敏锐的直觉，当你提问时，他们会直接指出：“你思考这个问题的底层方式其实是错的，你真正应该问的问题是 X，组织这些概念的正确心智框架是 Y。”而现在的 LLM 往往过于谄媚（placating）和顺从，总是客套地回复“哇，你问了一个多么深刻的问题”，然后顺着错误的前提继续跑偏。 Grant 对此表示高度赞同，认为这触及了**心智理论（Theory of Mind）**的深层差异： - 识别学生的问题背后暴露了怎样偏差的认知结构，需要极强的共情与心智洞察。 - 教学中存在不同的层级：普通 LLM 只能顺着用户的提问机械解答；优秀的老师能够纠正提问视角；而顶级的“A+ 级讲师”甚至能够打“教学柔术（Jujitsu）”——即便学生以极其小众或非主流的方式思考，老师也能瞬间接住其独特思路，顺势引导到正确的结论上，发现其闪光点。 ```mermaid flowchart TD accTitle: 教学解释与心智引导的三层境界 accDescr: 对比 LLM、优秀教师与顶级名师在教学与心智模型引导上的层级差异 subgraph LLM["第一层：当前 LLM"] A["顺从学生提问"] --> B["未能识别错误思维模型"] B --> C["沿错误方向机械展开"] end subgraph Teacher["第二层：优秀人类教师"] D["识别思维偏差"] --> E["重塑提问框架 (Reframe)"] E --> F["引导至标准概念结构"] end subgraph Master["第三层：顶级名师 (A+ Explainers)"] G["洞察学生独特的非主流思维"] G --> H["教学柔术 (Jujitsu)：顺应奇特视角"] H --> I["巧妙引导至深刻认知与正确解法"] end ``` --- ### `01:22:20` 给年轻数学家与学生的职业建议：商业本质与价值流向 针对许多对数学、编程或易受 AI 冲击领域充满热情的年轻人的迷茫——“AI 进步这么快，我还要不要把数学作为职业？”，Grant 给出了清醒而务实的建议。他坦言自己虽然作为一名 YouTuber（体制外的观察者），建议未必权威，但在选择任何职业时，有一条 pre-AI 时代的普遍法则始终成立：**搞清楚钱是从哪里来的，以及你到底创造了什么价值让薪水流向你。** Grant 指出，许多学生想成为数学家，仅仅是因为他们从小擅长数学考试，习惯了在现行体制中不断“跳过一个个设定的圆圈”并获得奖赏，他们把数学家单纯视为“能够继续做数学题的地方”，却极少批判性地思考自己创造的外部价值。在学术界，价值与资金来源其实各有不同： - **顶级学术声望（Prestige/Brand Value）**：某些明星数学家通过顶尖成果为大学赋予声望品牌，大学为此支付高薪。 - **公共基础科研资金（NSF 等项目）**：社会基于基础科学具有“公共品（Public Good）”属性的信念而设立拨款，衍生出一整套官僚体系和提案博弈来分配资源。 - **直接的教学服务（Teaching）**：家长希望将孩子送到有名师指导的高校，学者通过专业身份提供声誉，通过授课提供直接价值。 Grant 回忆自己也是误打误撞才发现“将数学探索转化为娱乐/内容消费”的商业模式，如果早年能更理性地审视价值流动，或许不必全凭运气。他建议年轻学子只要开始认真思考“谁在为我付钱、我解决了什么核心需求”，就已经大幅领先同龄人了。 --- ### `01:25:00` 后 AGI 时代的数学社群、教学护城河与“超级杠杆”策展人 面对未来 AI 自动化证明定理并成为极佳解释者的设想，Grant 认为数学家的核心社会角色不会崩溃，反而会演进： 1. **基础科学社群与同行评议的内生文化**：公众与政府对基础科学的投资基于信任。判断一项成果是否有价值，并不依赖于不懂代数数论的基金审批官员，而是依赖数学家共同体的内部共识。未来的核心价值可能会从“定理证明”转移到“提出深刻的定义”或“担任学术策展人”，社群依然存在，且在 AI 带来的丰裕社会中，基础科研的预算可能还会增加。 2. **教学是后 AGI 时代最稳固的职业之一**：教育具有极强的**人际关系与辅导属性（Relational/Coaching/Mentorship）**。即使 LLM 能够给出完美解释，富裕社会中的家长依然愿意在顶级的人类导师和教练身上投入重金。Grant 鼓励更多有志青年认真考虑成为纯粹的数学教育者（Math Educator）。 3. **前沿洞察的提炼与翻译需求爆发**：Dwarkesh 补充道，在 AI 率先突破数学认知地平线的世界里，AI 将探索出人类未曾设想的数学领域与对象，届时会有极大的社会需求去提炼“AI 究竟看到了什么”。 4. **作为指挥方向的“超级杠杆”**：当 AI 能够极速推演新数学时，具备深刻理解力、能为庞大 AI 计算力指定研究方向的策展人与科学家，其决策将拥有远超以往的巨大经济杠杆（High-Leveraged Move）。 当 Dwarkesh 问及数学加速 10 倍或 100 倍是否会引发其他领域的剧烈连锁突破，还是会被现实世界卡脖子时，Grant 认为这种突破将呈现极度**尖锐且不均衡（Spiky）**的特征，不同分支（如代数数论）与物理应用的结合路径将截然不同。 ### `01:30:00` 偏微分方程、波音案例与数学向工程应用的渐进外溢 在探讨纯数学突破是否会迅速转化为技术变革时，对话触及了数学与现实工业之间微妙的转化机制。以动力系统和偏微分方程（PDE）领域为例，这类研究天然更贴近工程物理实际。一个典型的真实案例来自波音公司（Boeing）：以往波音研发飞机的流程是先制造样机，进行大量物理破坏性与承压测试，随后根据测试结果将飞机拆解并重新组装，耗资极其高昂；后来，一个偏微分方程数学研究小组提出了改进仿真算法的核心数学洞见，使大量物理测试可以直接在计算机仿真中高精度完成，免去了反复拆解和重建飞机的繁琐步骤，直接为波音节省了数十亿美元的研发开支，波音也因此长期资助该数学课题组。 这种“偏微分方程相邻”（PDE-adjacent）的领域正是数学洞见能够直接解锁工业价值的地方。虽然解决诸如纳维-斯托克斯方程（Navier-Stokes）存在性与光滑性这样的千禧年大奖难题，未必能在次日清晨瞬间引爆一场翻天覆地的经济奇迹，但数学理论的推进完全可能以渐进式改进的形式向外溢出——例如优化发动机气动设计、无需耗费海量算力运行冗长计算流体力学（CFD）模拟即可推导出更优的机翼构型，或者通过纯数学技巧直接大幅提高 CFD 求解器的计算效率。这类从边缘向现实技术“渗漏”（leakage）的收益往往极其可观。 当下大量的 AI 工程师、物理工程师和材料科学家正处于绝佳的生态位，他们能敏锐地审视 AI 带来的数学洞见，并筛选出能够落地的部分。对话双方直言，如果在未来五年内，AI 在数学领域取得的长足进步仅仅表现为“攻克了一堆埃尔德什猜想（Erdős problems）”，却无法对物理世界带来任何直接可追溯的经济价值提升，那将令人大失所望，也是非常不可思议的。 ```mermaid flowchart TD accTitle: 数学洞见向工程应用转化的传导路径 accDescr: 展示从AI与纯数学洞见向工业仿真与实际工程效益流动的过程 subgraph MathTheory["数学理论突破"] A["纯数学 / AI 生成数学洞见"] --> B["偏微分方程 (PDE) & 动力系统进展"] end subgraph SimulationTech["仿真与算法层"] B --> C["高精度 CFD / 流体动力学模拟加速"] B --> D["减少物理风洞与破坏性测试需求"] end subgraph IndustryImpact["工业与经济回报"] C --> E["飞机机翼与发动机几何外形优化"] D --> F["如波音案例：节省数十亿美元拆解与重构成本"] end ``` - **波音仿真降本案例**：通过偏微分方程数学洞见在计算机中替代传统“制造-测试-拆解-重建”的物理测试闭环，为波音节省了数十亿美元的研发资金。 - **CFD 效率提升**：纯数学对流体力学微分方程的分析突破，最直观的工业应用就是大幅压缩计算流体力学的求解耗时与算力开销。 - **五年价值检验标准**：衡量 AI 数学突破的重要标尺之一，在于它能否走出纯粹的埃尔德什猜想圈子，切实赋能物理世界的材料、气动与工程科学。 --- ### `01:31:45` 奇点前夜的追问：纯数学究竟在积蓄力量还是已脱离现实？ 数学史在本质上是一部“不断堆积抽象概念与内在连接”的历史。很多时候，数学家们在不同分支各自堆砌概念巨塔，直到数十年甚至上百年后，这些看似平行的孤岛才忽然产生交汇，或者被物理学家和工程师挖掘出意想不到的实际应用。当社会迈入技术奇点、特别是走向奇点的“工业化落地阶段”时，人类过去几个世纪积累的庞大数学思想库，理应成为支撑现实世界飞跃的宝库。 然而，AI 带来的超高速数学进展也逼迫学术界停下脚步，反思一个令部分人尴尬的根本问题：“数学到底是什么？”如果 AI 将数学研究效率提升了整整十倍，各行各业却完全看不到任何对应的现实溢出效应，那么数学界就不得不直面一个残酷的真相：在过去的几十年里，大量纯数学研究是否已经完全沦为了自娱自乐、彻底与物理现实脱节的“无用之物”？ 长久以来，数学家在申请科研基金时常常宣称“相信我们，椭圆曲线领域的进展必将革新未来的密码学”。但如果 AI 在极其极端的数学领域取得神级进展后，物理与工业界面对这堆成果却只能面面相觑地发问：“等等，既然你们已经实现了 10 倍的效率飞跃，为什么我们这里毫无动静？”，那么这层维系了数十年的“基金话术”或许就将被彻底戳穿。 在全剧终的轻松氛围中，主持人 Dwarkesh Patel 总结道与 Grant Sanderson 的这期探讨极其畅快过瘾，Grant 也愉快地回应并致谢，为这场横跨形式化验证、直觉理解、教育逻辑与数学本质的深度对谈画上了圆满句号。 - **数学概念的长期滞后性**：数学发展历来以超前构建概念体系著称，但这种积累在奇点时代需要接受现实工程能力的直接检阅。 - **科研基金话术的潜在幻灭**：过去纯数学常以密码学等现实应用作为经费申请的背书，AI 驱动的超速进展将直接验证这些承诺到底是有真才实学还是学术惯性包装。 - **对谈尾声**：对话在探讨数学本质与学术反思的高潮中迎来尾声，双方互相致谢完成录制。 ## Notable quotes > `06:50` 好的数学家证明定理，伟大的数学家提出猜想，而最伟大的数学家发明定义。 — Grant Sanderson > `30:00` 人人都知道什么是未解的研究问题，但我更想提出‘未解的解说问题’——也就是某些东西我们固然证明了它，但我们其实根本不知道它为什么是真的。 — Timothy Chow > `36:00` 授人以鱼不如授人以渔，但若把一个人点着了，他就一辈子都很暖和了。 — Grant Sanderson > `01:16:02` 人（Who）往往比内容（What）更重要。 — Grant Sanderson > `01:20:00` 你思考这个问题的底层方式其实是错的，你真正应该问的问题是 X，组织这些概念的正确心智框架是 Y。 — Dwarkesh Patel > `01:22:20` 搞清楚钱是从哪里来的，以及你到底创造了什么价值让薪水流向你。 — Grant Sanderson > `01:31:45` 等等，既然你们已经实现了 10 倍的效率飞跃，为什么我们这里毫无动静？ — Dwarkesh Patel > `20:00` 要是年轻的天才，可千万别去碰五次方程。 — Grant Sanderson ## Mentioned Grant Sanderson, Dwarkesh Patel, 3Blue1Brown, AlphaGeometry, DeepMind, Hugh Montgomery, Freeman Dyson, Andrew Wiles, Dario Amodei, Anthropic, polylog, Albert Einstein, Évariste Galois, Niels Henrik Abel, Joseph-Louis Lagrange, Joseph Liouville, Camille Jordan, Murray Gell-Mann, Carl Friedrich Gauss, Gemini 3.5 Live Translate, Google, David Bessis, Shinichi Mochizuki, Timothy Chow, Claude Shannon, Richard Feynman, Robert Langlands, Terence Tao, Andy Jassy, Cursor, Bilibili, Etsy, Amazon, Lean, Mathlib, AlphaGo, AlphaZero, Andrej Karpathy, Eric Jang, DeepSeek, DeepSeek-Math, Art of Problem Solving, Alex Kontorovich, Andy Matuschak, Jane Street, Wikipedia, Stanford Encyclopedia of Philosophy, The Princeton Compendium of Mathematics, Claude, Steven Strogatz, National Science Foundation (NSF), Boeing ## Video description <p>Always so much fun to chat with <a target="_blank" href="https://www.youtube.com/c/3blue1brown">Grant</a>.</p><p>AI has been making much faster progress in math than in other fields. As a result, mathematics is showing us, very concretely, what AI progress in other fields will look like. Even within mathematics, there’s a jagged landscape. What does it look like?</p><p>What is the nature of the most important conceptual breakthroughs in the history of mathematics, and how different are they from what AIs are currently able to do?</p><p>Does AI (on net) increase or decrease human understanding of the field?</p><p>How big is the overhang from having AIs systematically try to connect ideas already in the literature?</p><p>And what advice does Grant have for aspiring mathematicians, coders, and other students who are passionate about fields that are being most transformed upon by AI?</p><p>Watch on <a target="_blank" href="https://youtu.be/TfyPshgMbug">YouTube</a>; read the <a target="_blank" href="https://www.dwarkesh.com/p/grant-sanderson-2">transcript</a>.</p><p><strong>Sponsors</strong></p><p>* <a target="_blank" href="https://ai.studio/live">Gemini 3.5 Live Translate</a> is what I wished I’d had on my last trip to China. It detects more than 70 languages and translates them in near real-time… and it preserves your original pacing and intonation. If you’re building an app that needs live translation, you should check out Gemini 3.5 Live Translate. Get started at <a target="_blank" href="https://ai.studio/live">ai.studio/live</a></p><p>* <a target="_blank" href="https://cursor.com/dwarkesh">Cursor</a>’s harness lets me use models for a huge range of tasks at the podcast. For example, Cursor cuts out the ads from each episode I produce so I can post them on Bilibili. It also helps me prep for interviews — I have a repo full of books and papers that Cursor sorts through to find the exact right file for any given question. Try Cursor yourself at <a target="_blank" href="https://cursor.com/dwarkesh">cursor.com/dwarkesh</a></p><p>* <a target="_blank" href="https://janestreet.com/dwarkesh">Jane Street</a> sponsors 3Blue1Brown, so Grant has gotten to spend a lot of time with various Jane Streeters. He actually just recorded an interview with a few of them, so when we sat down for this episode, he told me about some of the things he learned, like how Jane Street keeps their role definitions fuzzy to make sure their people keep learning and growing. Go check out Grant’s full interview at <a target="_blank" href="https://3b1b.co/janestreet">3b1b.co/janestreet</a></p><p>Timestamps</p><p>(00:00:00) – AI is discovering new proofs. Is that AGI?</p><p>(00:11:32) – The verification loop on conceptual breakthroughs can be a century long</p><p>(00:26:12) – Will we understand an AI proof of the Riemann hypothesis?</p><p>(00:38:08) – Can AI find the hidden bridges between fields?</p><p>(00:53:48) – Why real-world tasks don’t fit into RL environments</p><p>(01:07:07) – Good writing requires theory of mind that AI still lacks</p><p>(01:16:02) – Why learning will still depend on human curation</p> <br/><br/>Get full access to Dwarkesh Podcast at <a href="https://www.dwarkesh.com/subscribe?utm_medium=podcast&#38;utm_campaign=CTA_4">www.dwarkesh.com/subscribe</a> [Source](https://api.substack.com/feed/podcast/204275916/5f3632cca68272c292349f10debc3573.mp3)

[6:50] Grant Sanderson: 好的数学家证明定理，伟大的数学家提出猜想，而最伟大的数学家发明定义。 [30:00] Timothy Chow: 人人都知道什么是未解的研究问题，但我更想提出‘未解的解说问题’——也就是某些东西我们固然证明了它，但我们其实根本不知道它为什么是真的。 [36:00] Grant Sanderson: 授人以鱼不如授人以渔，但若把一个人点着了，他就一辈子都很暖和了。 [76:02] Grant Sanderson: 人（Who）往往比内容（What）更重要。 [80:00] Dwarkesh Patel: 你思考这个问题的底层方式其实是错的，你真正应该问的问题是 X，组织这些概念的正确心智框架是 Y。 [82:20] Grant Sanderson: 搞清楚钱是从哪里来的，以及你到底创造了什么价值让薪水流向你。 [91:45] Dwarkesh Patel: 等等，既然你们已经实现了 10 倍的效率飞跃，为什么我们这里毫无动静？ [20:00] Grant Sanderson: 要是年轻的天才，可千万别去碰五次方程。

[0:00] Grant Sanderson: If the nature of the solution to the Riemann hypothesis was something like that, that feels pretty distinct to me than what's necessary to get good at white-collar work... [11:32] Grant Sanderson: What makes the Galois theory such an interesting example is you have literally this 100-year segment of like an idea that like flows through many different people's heads before it settles into something that the math community agrees is good. [15:00] Grant Sanderson: Working in the quintic doesn't seem to be good for your health... If you're a young genius, don't work on the quintic. [33:00] Grant Sanderson: Build a man a fire and he's warm for one night, but set a man on fire and he's warm for the rest of his life. So that's where I am with AI. [41:00] Grant Sanderson: Imagine I've locked you in a box, right? And then the only way that you have of interacting with the world is that you receive a slip of paper. And then someone says, 'Can you like predict what will come next?'... And then your memory is wiped, right? And then you get like another slip of paper and you go. [55:00] Grant Sanderson: You could imagine having a basically endlessly running program that's constantly trying to extend Mathlib... press go, and then just pour compute at it and look away for 10 years and then come back and say: what do you have? [65:00] Grant Sanderson: Every single time I see one of these, I kind of don't know if it's worth my time. Even if 99 out of 100 of them are right, I don't know if it's worth my time to even go through it because it's really labor-intensive to find what that error would be. [75:00] Dwarkesh Patel: I guarantee that there's not... and it was an actual video, an actual link, but it just had misattributed someone else's to me. And it was good! And I had a much better experience clicking over and watching that video to learn about the thing rather than trying to proceed forward with questions. [80:00] Grant Sanderson: Regardless of whether AIs are proving theorems or not... know where the money is coming from. Know where you plug into that. And if you're just asking those questions, you're actually already steps ahead of all of the other fledgling prospective mathematicians.

[0:00] Today I'm chatting with Grant Sanderson, who runs Stoblew and Brown, and is now working on a new project documenting the progress AI is making in math. And I wanted to talk to you about this, because AI has been making the fastest progress in mathematics as of any other field. So whatever is happening here, and whatever we're seeing AI progress happen or not happen, would tell us about what will happen to the rest of the world as AI gets better and better. So I wanted to start with this question I asked you when I first interviewed you three years ago. And I asked you, once we have AIs that can get gold in the International Math Olympiad. Wouldn't that just be AGI? Wouldn't this just be able to do anything any human can do, given how hard these problems are? And you had an answer, which in retrospect turned out to be very wise and correct, which is like, it'll be another benchmark, like all these other benchmarks that are passing. Obviously, AI has gotten better in general ways since then, but there won't be some aha moment when this happens. First, I think I'd be curious to get your heuristics on why that turned out to be true. And second, I'm curious how long you think this narrowness can continue to be true. So by the point that AI has solved the million price problem, do you think it's still possible that at that point there lots of tasks that humans are doing that AI still can automate in the economy It an interesting question because it hard to answer without knowing what the solution looks like ahead of time I mean if we take the IMO that something where I think the spirit of your question three years ago was in looking at how some of the solutions to these problems really seem to require creativity. And the designers of these problems, they'll try to have them come up with things that you can't train for as easily. I think the dirty secret with the IMO is that you really can train for a lot of them. And so with the whole AI and math project undergoing, I think, as you point out, one of the reasons it's interesting at all is that there's a spiky frontier to AI. Math is just right there in one of the spikes. But there's kind of a fractal nature to that spikiness, because when you zoom into the specific progress within math, you have some things that are a lot easier than others. So if we just think about IMO, which is old news at this point, that's kind of like two years ago, that they're really like doing quite well. They would have gotten a gold in 2024 if or not the following reason. They're very good they're just like cold solved geometry basically and the IMO has these four categories of problems this geometry number theory algebra and combinatorics so like geometry just solves in like 19 seconds in 2024 because it's kind of a brute force solver and the dirty secret is for students there also sort of a brute force way that you kind of can go at it combinatorics is the one that the wild card of much more like playful puzzly seeming problems And there were two combinatorics problems on that year test There's not always. There's four categories, six different problems. So it's kind of a toss up which one is going to have two questions. Had it been more geometry questions, they would have gotten a gold that year. But it struggles on those combinatorics ones. And, you know, someone who's trying to keep that torch of the last holdout of like math for humanity might say, well, those are the ones that require the more creativity. Even then, though, I think the spirit of your question on if they're solving a Millennium Prize problem, does that also service a lot of white-collar work? It suggests that whatever the rate limiter is between where we are now and that is the same as the rate limiter for making things better at white-collar work. We can maybe paint a couple different ways that, like if we focus on, I don't know, Riemann hypothesis, like what would it look like to solve that? So one possibility would be these things are extremely good at a specific domain of knowledge and just knowing it very deeply and then knowing another domain and knowing another domain. And you've pointed this out. It like bizarre to have something with this superhuman breadth that like knows all the field so well that not just finding those lightning bolts that connect them I think we starting to see sparks of that of like actually finding connection between the things that it an expert at I'm sure we'll talk about it. If the nature of the solution to the Riemann hypothesis was something like that, that feels pretty distinct to me than what's necessary to get good at white-collar work. And there's a reason to believe, actually, that that might be the nature of the solution. I don't know if you know the story of like Hugh Montgomery and Freeman Dyson at the IAS. This is a side tangent, but it's just kind of a fun story on how, I don't know if it was over lunch or something like that. Basically, you have this number theorist who is pointing out, just trying to understand the statistical correlation between pairs of zeros of the Riemann zeta function. So the Riemann hypothesis is all about, do all these zeros sit on a straight line? And he's finding this quantitative question you could ask about. And he writes down a formula that looks like 1 over sine squared or something like that. Freeman Dyson, a physicist, is like, I know that expression. That expression comes up in studying the eigenvalues for random Hermitian matrices, which was something that comes up in studying the energy levels of like a nucleus. And the idea that the statistics of those two seemingly different things were the same sort of prompted a potential exploration on, hey, are there aspects of random matrix theory that might be relevant to like Raymond? [5:00] data function. And I think it's a little bit of an open question, like, is there food to be had there? But that kind of bridging together from two different fields, like if it turned out that the solution to the Riemann hypothesis was exploring an idea like that even further, that has this character of kind of how you expect LLMs to be good at math. It's like they're an expert at the quantum physics, they're an expert at the analytic number theory, they should be able to see that similarity in a way that doesn't require like Montgomery and Dyson to be having lunch and like happening to talk about that that's totally different from white collar work right in terms of like the the extent to which you maybe have a hard time using an ai as an editor yeah it's not because they know everything and you just need them to find that lightning bolt in between different possibility would be um what's the right analogy maybe like if we think of fair ma's last theorem between the moment of fair ma phrasing the question and then what the solution itself looks like, where ultimately the solution involves such heavy machinery in math, right? So the beauty of that problem is you can phrase it so simply. You ask about, you know, x to the n plus y to the n equals z to the n. Do you have integer solutions for this when n is bigger than 3? And it something you might expect there to be an elementary number theory approach to it but just as far as we can tell there just not Whereas the actual solution you know maybe there is something simpler but this might be what it has to be There's such a complicated set of ideas that build on, like, centuries of work centered around elliptic curves. And then this other, like, mountain of ideas centered around these things called modular forms. And, like, both of those mountains have to be built before you can ask the right question that connects it. So if the solution to the Riemann hypothesis involved building a new mountain, like that's a kind of skill, like the ability to like come up with the right new ideas that feels sufficiently different from like the character of how they're intelligent right now that it's not like that's what you need from your hired video editor per se. but that like if it's capable of building mountains uh that are you know the correct new theory that like crystallizes how we should be thinking about a subject that's just such a level of intelligence that then it starts to feel like it would be surprising if that didn't permeate into other aspects of the economy besides like just the mountain building for math itself yeah or at the very least even if it couldn't like literally do every single thing white collar humans can do yeah it would just have transformative effects in the way that getting gold in the imo who did not have transformative attraction in the world. First of all I do want to point out that I totally moving the goalposts here Because when I interviewed Dario about two three years ago I asked this question about why haven they been able to use their vast knowledge to connect ideas together and come up with a new discovery that way That seems like the kind of thing, even if a moderately intelligent person knew this much information, they'd be able to like come up with a medical diagnosis from the fact that like this drug causes migraines and this other thing, you know, whatever does this. And maybe it's the same drug that can cure both things. And yeah, I don't know. From an outsider's perspective, mathematics seems clearly like a field where finding this counterexample to the unit distance problem conjecture was like an example of this kind of thing. As a total goalpost moving. But then we can ask, OK, what is the next benchmark now that AIs can do this thing that we should have thought they should be able to do? What is the next thing that would be quite impressive? And there's a couple of candidate ideas here. So one could be coming up with interesting problems in the first place. And the other is coming up with new kinds of objects or conceptualizations that create or unify fields. On the first one, right now we're just turning these models to, like, we have these millennium-priced problems. Because, you know, I don't know, like, mathematicians have noticed, like, Riemann came up with this idea of this, like, Riemann's data function. And because he thought that it would have some connection with like the density of prime numbers Or if the zeros on this function would have some connection to prime numbers And so figuring out that there Why do we think this is an interesting thing to study in the first place Why are we building this object and trying to answer questions about it and answer this particular question about it? Seems like the kind of thing that would be the next benchmark. I mean, you highlight two pretty good examples there. For anyone curious about the unit distance conjecture, there's this really nice video by a math channel called polylog where they talk about it and um one of the people in that because all of these discussions it causes people to reflect on like the process of doing math right they're like ah this thing can do this impressive stuff like what does that mean for us um and he highlights this quote how uh good mathematicians prove theorems great mathematicians um come up with conjectures and the greatest mathematicians come up with definitions and that's more or less exactly your framing here on like those two like we need the conjecture generator uh and then like the definition generated, that's the premium tier mathematician. I don't understand how exactly you'd make that a benchmark in the sense that usually when I think of the word benchmark, I'm thinking something that you have like, it's a goalpost. The ball is through the goal or it's not. You can clearly say, yes, this is done, partly to be able to do things like our LVR, but also partly just to be able to know that you haven't moved the goalpost in answering. OpenAI can have their headline on... [10:00] disproving the unit distance conjecture because it's a clear distinct, it's like, it did it, right? Whereas imagine trying to have a headline on like, 25.4 came up with a really good conjecture, right? Like we promise everyone thinks it's a good conjecture. It just doesn't, it doesn't land the same way. But maybe that doesn't negate the fact that that's the right thing to be thinking about. So I would be surprised if it ever took the form of looking like a benchmark and like, we have a score saying that it's past this benchmark because we can quantify how good a conjecture it is. But probably the nature of what it would take is that you would feel a tone shift in conversations with mathematicians about the way that it's useful to work with, right? And like this series that you referenced that is not at all produced yet and probably won't be for a couple months takes the form of us interviewing a lot of mathematicians. And what's interesting is we started doing this like over a year ago, and it's fun to see a little bit of a tone shift in the way that they talk about AI between like mid 2025 and where we are now in 2026, in the real world, that's a very short amount of time. In the AI world, that's eons. And we're able to see over those eons this tone shift. I think the way that you measure conjecture ability is going to be more subjective on that tone shift where it be mathematicians saying they not just using it to solve their problems but as they step back and decide what their research field should even be that a conversation with such and such model was genuinely helpful for that. I don't think it's likely that you'd see it in the form of a headline saying that this was yet another benchmark knocked down. Right. And so it's very interesting. The kinds of things you can't make benchmarks for are also the kinds of things, at least in the current paradigm you can't easily train for, right? Because there's really no fundamental difference between a benchmark and a training environment. Yes. I think it's very easy to come up with some dichotomy of like, here's a deep reason why AI can't do a certain thing. And then it turns out, well, you're just thinking about it the wrong way. And actually, I can do it pretty soon thereafter. But I'm going to come up with... You're going to come up with a couple anyway. And I think that this will probably... It'll probably turn out that there's ways in which we can train AI to do these kinds of things in the relatively near term. But it seems like it would have to be different from current RLVR training. So the thing I'm curious about, and the thing it seems to me that drives a lot of the big progress in mathematics and in science generally is like coming up with a new way to think about a problem or the new way to understand the world that then unifies different fields spawns entire new fields solves problems we weren even thinking we were trying to solve in the first place Like the reason Einstein was thinking about GR is not because he wanted to explain why light bends or why black holes exist. These are phenomena he didn't even need to know and needed to be explained in the first place. But in mathematics, it often seems, OK, a total outsider. I don't even know the details of what I'm talking about here. from the outside um it seems like there's often ways to say prove a specific problem that can motivate a new conceptualization uh one which results in a whole new field a whole new way of thinking which is immensely productive and one which doesn't i think um i'd be curious to hear you talk about whether uh galwa coming up with group theory and distinguishing his like solution to the um the quintic having no formula for the roots and able coming up with the different proof a few years earlier that didn't come up with group theory but then if you wanted to do a verification loop on like is group theory an interesting concept that was like was something useful done here why is this proof better potentially that verification loop is 100 years long yeah it involves um the cryptography coming around and physics making progress and all of the ideas in group theory being relevant and understanding like symmetries in physics and all those kinds of things it like 100 year verification loop of why is this a productive concept in the first place yeah um boy uh yeah you struck a nerve because i i had this like project about Galois I was going to do in 2022 that I put on the shelf but I spent a year of my life thinking a lot about what he did. So there's a risk of me accidentally talking too long on the specifics. Hold me back on. It's a perfect example for your case because describing why it was a valuable insight does not come from immediate utility. And so certainly if you're thinking about RLVR environments, it's like, okay, this is going to be really hard to do. But it's interesting to note how even with like human verifiers at the time, like it took a really long time to recognize it as being useful. Like I think Einstein with GR, people sort of felt, you can like feel, this feels like a good theory right away. Like what makes the Gatwa theory such an interesting example is you have literally this 100 year segment of like an idea that like flows through many different people's heads before it settles into something that the math community agrees is good. So to back up a little bit, I mean, do you want the background on the problem at all? All right. Well, so we all learn about the quadratic formula in school. I thought you were going to say, we all learn about group theory in school. We all learn about group theory, about quadratic formula. So this was known in some sense... [15:00] Greeks could solve quadratics, but they didn't really write things in algebra. And so it's really more like the Arabs that wrote down that formula. There's this delightful story around some dueling Italian mathematicians, not real duels, just intellectual challenges, who secretively found a formula for the cubic. And then very shortly thereafter found a formula for degree 4 polynomials. So a natural open question for mathematicians is, can you find a formula that solves degree 5 equations? Now, the degree four, it's monsters. It's like, it would be wild to write it down. You usually don't really write it down in full. You break it up as like a procedural thing. So you might believe these things have this exponentially increasing complexity. So many hundreds of years, nobody is like really answering that question. Usually we say Abel was the first to prove it. He was this young, precocious Norwegian mathematician. And he showed it's simply impossible. It's not that you can find a quintic formula. He thought he found one, but he showed it's impossible. I think the real credit, though, like you have to back up a little bit and talk about Lagrange, where Lagrange found the right kind of question to ask about this. I can go into the details if you want but I give it a very high level He was studying the question and he recognized being able to solve these polynomials is actually very related to understanding the way that certain algebraic expressions are symmetric more or less so. If I write down A plus B plus C plus D, just adding four variables, if I permute those, it doesn't change the value of the expression. Whereas if I write A plus B multiplied by C plus D, some of the permutations don't change it, but some of them do. And he had this really, really nice insight about how if you can find expressions like this that have like four free variables, but all the permutations take on three distinct values, that have this unexpected relationship with being able to reduce degree four into degree three. So he started approaching the like, can we find a quintic polynomial by saying, I wonder if I can extend that. And to extend that method, you would have to have an expression that has five free variables such that as you permute them over all the five factorial permutations, it takes on only four values or fewer. So that's like, you could put that in a puzzle book. You could put that in a brain teaser that a 12-year-old couldn't engage with. And it's not too hard to find yourself feeling like that's an impossible task. And so Lagrange is sitting here saying, hmm, here's a strategy that I'm trying to solve this problem. Can I find a quintic polynomial? This strategy doesn't. It seems like it might be impossible at least from this strategy But that was the first time in history that people had the instinct that some kind of question about symmetry was the right way to be studying these polynomials In his mind, it was just a way. It had yet to be discovered that, like, actually there's a tighter connection. And also, like, maybe rather than searching for the formula, we should be asking the opposite question. Can you prove that it's impossible? So he sort of planted that seed. Like, around 50 years later, Abel definitely read Lagrange and was influenced by it. Galois, we know that he loved Lagrange when he was falling in love with math. And so it's very hard to imagine that these two young geniuses, the fact that they both come up with pretty similar insights around that problem, it's not born from Lagrange. But to your question on are you able to verify that this was a good idea, there wasn't any result that Lagrange came to. There's never like, he solved the problem, and therefore we know that that was the right question to ask. He asked it. There's some intrinsically interesting thing. It also wasn't very important for math at the time. Most people were more interested in the applications to physics. This is almost in that side, almost recreational hobbyist type thing. Abel, he started working on Quintic stuff, but then he was advised to spend more of his efforts studying elliptic functions. And so more of his work was on that before he died young. He died at 26 from tuberculosis And then Gawa he pushed both of those ideas in the right direction where he really understood the nature of abstraction And so he had this really nice piece that he wrote while he was in prison, actually. He was like, we could talk all about his life story. It's pretty wild. But he's like this teenager. He's in prison. He had tried to submit his math papers, and they had been rejected. So again, it's like verifiable reward. The verifier function that is the academy at that time is rejecting. what he wrote. Because frankly, it was not very coherent. It wasn't a complete proof. He wasn't giving a clear thought of what the theory actually was. He was just a young fledgling mathematician getting his bearings. So it's like, the verified reward there is like, eh, no good. But he has some instinct that there's something there. So he's writing this diatribe on the nature of math being something which is, it undergoes these shifts over time. And he talks about the advent of just algebra itself and going from just thinking in terms of numbers to having a certain fluency just with pure algebraic expressions where you're not tied to interpreting those expressions. And he has this instinct that there is another layer of abstraction that seems like what we should be doing, where rather than thinking about the formulas themselves, thinking about what symmetries underlie those formulas. But it was still a pretty ill-defined theory. So if you're trying to say, okay, is the variance... [20:00] Fiber Ward that he has solved a problem that other people haven't? It's like, well, Abel proved that quintics are unsolvable. And you say, what was Galois doing? Well, in principle, the thing that Galois theory will let you do is take a specific polynomial, and it gives you the rules to say, does that specific polynomial have roots that you could write down? For example, like x to the fifth minus one, you know that a solution is one. Or x to the fifth minus two, you can write down fifth root of two. So it's not that every quintic polynomial you can't write down the solution, but could you find a specific one where you prove you can't write the solution using radicals? He also didn't even solve that exactly. He has a much more abstract. He didn't show for a specific example that he couldn't. So even describing what problem did he solve is very tricky. So then he dies. It's this very romantic story of he has this duel. We can get more into it. There's a lot of myth around supposedly he writes up all his ideas the night before the duel. Really, he tried to get them published. Working in the Quinty doesn't seem to be good for your health. It's very bad. Yeah, yeah, yeah. If you're a young genius, don't work on the Quintic. And so he asks his brother and his close friend, like, get these notes to Gauss, get these notes to the important mathematicians of the day, because I think there's something here. Even then, it didn't really take. So his brother and his friend tried to get them out It wasn another 20 years until Louisville sees these notes sees that maybe there something in them and tries to clean it up and understand what was Galois getting at And then even then it was another 20 years until Louisville sees these notes sees that maybe there something in them and tries to clean it up and understand what was Galois getting at And even then it was another 20 years or so until Jordan actually puts together something like a modern treatment of group theory that they attributed to Galois. You could easily imagine history turning differently where these ideas were kind of coming about from other points in math, and Galois could have been forgotten in history if he was a less like florid character. But between the time of Lagrange, like having this inkling of maybe symmetries of roots is the right way to go to where it all looks like modern group theory. Like you've got this long span. A lot of the time, it's like not even passing the like verified reward of human reviewers because it like gets on someone's desk. They say, I don't really know if there's anything here. It gets on someone's desk. They don't. You have to have this like one person sort of recognizes it. And then even then, it's not really solving practical problems at that point, like you point out cryptography and physics and things like that, you have to get into the 20th century before you have like Gaiman thinking, hmm, maybe understanding the nature of like how certain groups like breakdown has this relationship with what particles are made out of. And like, he anticipates quarks based on a purely group theoretic question And like that one of the more interesting applications of group theory is that like to even predict the existence of quarks is a group theoretic question That so long after Lagrange before you have anything like that And so you have to ask like what is the way of measuring progress that not based on solving a problem Right And that that somehow capturing what is the instinct that inside Galois mind when he says I think there something here What the instinct that inside Lagrange mind when he says like I think this is the right way to think about it what's the instinct inside louisville's mind when he says these like scattered notes from this like long dead youngster like might have something to them it's so hard to put a finger on that but i mean a different like series of videos i'm making right now is about um like you know the whole compression is intelligence idea and even though this isn't really the angle i'm taking you know there is something to the idea that the smaller expression that's more predictive feels more intelligent. And so I wonder the extent to which you can give some kind of verifiable reward around not just like, did you solve it or what is it solving, but around the smallness of the concepts required to do it. I mean, going back to Riemann hypothesis solutions, what would that look like if an AI solves it? I think a third way that it could happen is it just straight up works harder In the same way that you could maybe have an elementary proof of Fermat Last theorem that just like spelled out over like thousands of pages that would be incoherent But like the cleaner way to view it is with elliptic curves and all that. Maybe there's some like thousand page proof of Riemann hypothesis that's like, no one's really getting anything out of it. And what you actually want is like, what are the succinct, like compressed versions of those ideas, like they would then lend themselves to human understanding? Like, I don't know, Komogorov complexity. Like maybe you throw that into your, like, your attempt to quantify what you mean by elegance. But I don't think it's easy, but I do think it's something you would have to do in order to reward the Galois-like instinct rather than just rewarding, have you solved a problem? It's very hard to come up with the heuristic for science. But it's clear humans have been doing this somehow, and obviously AI's will do it at some point. Well, it's relevant also, not just in terms of verified reward, but presumably the end goal is understanding. Right. [25:00] Whatever the concision function is that distills down, here's this complicated way of thinking into the right one, like the equivalent of the universal law of gravitation for Newton. You would still want to train AIs to be able to do that and find the compressed representation. I grew up in India until I was eight. And so in addition to English, I also speak Gujarati. 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Go to AI slash live to get started So people have this worry about mathematics in particular that you know the AIs will prove the human hypothesis and our understanding of mathematics won be any better for it I have a couple of questions about this. The first one is whether this is like a thing you should expect. like isn't the reason humans come up with general natural uh objects and sub goals and whatever when we're working on a big problem is that it's just like useful when you're trying to work on a complicated important problem and so we can just think about like theoretically is it would this even be a simpler way to solve the ring around hypothesis as opposed to just coming up with the natural abstractions that are relevant to thinking about the problem and then two empirically is this what we observe when ai is doing make progress on problems today when the um when the AI came up with that counter example to the unit distance problem conjecture, you can just read its chain of thought. And it seems it's not understandable to me because I don't know anything about mathematics. But it seems to other mathematicians, it was like understandable. And it made it made use of like known constants mathematics and like proved relationships between them and all the natural language. And as a result, accelerated our understanding of the connection between this object and this conjecture. So is this even like empirically? Is this a thing we should be worried about? I think it depends on the nature of yeah Again if we sort of break down the three possible ways like solving the Riemann hypothesis that one and the other like big one from this year is like a certain Erd problem numbered like 1196 but it about these things called primitive sets But basically, it had that character of bringing an idea from a seemingly different field. As soon as you just present the basic idea to a mathematician, you say, like, what if we, like, use this, like, try the Markov chain process where we show that this thing is one from the bottom up probabilistically rather than the top down and, like, use the von Mangold function. If you, like, say that to someone in the know, they'd be like, they'd kind of know how to run with it. So you have this very, like, small idea that has the form of expertise in one field, expertise in another, draw a little lightning bolt between them. like those are those are going to be very human parsable right because all you have to do is just like show the start and end point of what those connections are if the character of it is mountain building uh you do have to you have to put in a lot more time to like understand that new mountain that was built because it's like a new thread that's not just like lightning bolt between them and if the nature of the progress was just like raw hustle right it's just like this just super long thing there's no new theories but it's just like long long long chain of reasoning answer then then you would have that word like okay there's this whole digestion process so i don't I don think there one clear answer I think it depends on what the solution there would look like And on the mountain building side I would actually be really interesting to see Is it by default a very human understandable way that we see new theories from great mathematicians Or is it like an alien, different kind of mountain being built where we even have to reprocess the kinds of abstractions that we engage with? Right. Well, the closest example here would be the attempted solution of the ABC conjecture. that was um we maybe shouldn't get into that one but that it's probably it's not probably not a correct solution but basically it's this like whole new way of thinking that this um otherwise reputable mathematician in japan had like come up with and it just took mathematicians like a long long time to even parse what he was saying but it had the feeling of just like an alien bit of mathematics that's theory building it's not just like long long chain of reasoning um it's like he called it like inter-universal geometry or something and so the fear that you would have is that like yeah it like does that the biggest fear would be that it does that and then much like the abc conjecture like people work for years to go up the mountain and they're like this just isn't right right and like if they're if it turns out to be wrong but it like really looked right but even if it was right there's there's just a lot of effort to like hike up a new mountain yeah if we end up in that situation david besis had a really great blog post called um [30:00] follow the theorem economy. We're just talking about this, you know, historically, as you were saying, mathematics is coming up with these definitions and problems, and it's about proving theorems about them. And that, really, the theorem-proving stuff is what gets all the credit, but it's like really a parasite on the definition stuff. And historically, it's not even a problem in terms of credit apportionment, because if you come up with a definition, you're probably going to be the guy who comes up with a theorem. But now we're in a situation where if the valuable work is the coming up with the insight and then AI just automates the latter part. So, OK, imagine a scenario where we have AI comes up with like the ABBA-like direct arguments about a bunch of important conjectures in the world. And then we just have these proofs. And now it's up to humans or the future AIs to then consolidate. I mean, I'm sure if you had access, again, having no object level understanding of this argument whatsoever. I'm sure if you had access to it, it would make it easier for you to then think about, like, well, what is going on here? Is there some deeper way in which you can understand why this proof works that would make it easier to come up with the ideas behind group theory Yeah I think it would be hugely helpful right Because I mean so much of trying to discover new math is mostly being wrong You trying to solve a problem It doesn't feel like constantly taking the correct step up the mountain. Mostly it feels like a random drunken walk where you're doing a thing and then, oh, you're wrong, and constantly discovering. So if at the very least you know that trying to digest what you know is ultimately leading to a correct solution, like that feels like progress simply because it's providing like a sense of knowing that it leads to a solution and there's plenty of plenty of like instances in the recent history of math where it feels like the reach has sort of exceeded the grasp where there's things that are proven like long before they're understood and i mean one of my favorite like openings to a paper it's not even like a research paper it's more like an expository one is from this um mathematician named timothy who was trying to understand a concept called forcing. And so there's this problem called the continuum hypothesis that more or less asks, like, you have a size of infinity for the natural numbers, you have a size of infinity for the real numbers, is there something in between? And the answer is both yes and no. It depends on your axioms. Like, it's sort of outside the scope of our usual axiom systems, which is an interesting answer. But the method to describe it is just really really hard to understand It the thing called forcing And in the beginning of this paper he writes like I want to like everyone knows the idea of an unsolved research problem Like I want to propose the idea of an unsolved expository problem We're like, sure, we've proven it, but we don't really know why it's true. And so then he proposes, like, a partial solution to that expository problem. You can imagine why I loved that framing, because, like, this is my whole life. It's like, I don't do research math. It's just wholly about, like, what's the most clear way to understand this, even if it's proven. There's a difference between proof and explanation. And so on that side, I think that you are basically getting to the importance of that distinction. Yeah, and that will be the main incentive for... The incentive would have to change in not just mathematics, but in other areas of science, from proving things about the world to consolidating proofs into problems or higher-level insights. But we were having a discussion earlier at lunch about a recent talk you were giving about design and how it helps us understand things. And then in The Limit, is there really a difference between the conceptualization for an idea and the idea itself? So if you think about special relativity and spacetime diagrams and Minkowski spacetime is it like yeah this is a way in which we illustrate this idea of like why there length contraction and time dilation but is that like is like that is the reality so the exposition does seem to be like the explanation in some sense here yeah i mean there's a couple interesting things there one is it seems like there's a really strong correlation between the people who come up with genuinely novel insights and also who are actually quite clear in their communication of it. Like, you might imagine, given that the experience of a university student is often that the expert there teaching them is not necessarily the best explainer of that topic because they are so spoiled by their expertise. But what seems, at least in some cases to be the case, is how the people who are really coming up with something quite novel, so you've got like Einstein or like Claude Shannon, something there, you read their papers, they're really lucid papers, right? It doesn't feel like, oh, this is just for the experts and you have to chop through it with a machete to get very good expositors. Feynman has this characteristic too, very good expositor. And so maybe the same part of the brain that comes up with the correct new way of thinking about it at a research level also has this knack for good explanation. And I think this is pertinent to the AI one where I kind of used to think that AIs will become these automated theorem provers [35:00] like the role of the mathematicians is going to shift towards like my job, like explain these things. I kind of suspect that actually they'll also be like quite good at doing that and probably just like better than most humans are, like doing the explanation half and distilling half. And that's actually not what's left for the mathematicians is like digesting and explaining what was going on. Probably the nature of how these things are going. I could envision, we can talk about like ways this might not be it, but like probably the same thing that is coming up with like the really good new idea that solves some new problem is just also good at explaining it. That's my new... That's a way my beliefs have changed. What's the last thing you think you'll be doing? Both you and then also the mathematical community. The human mathematical community will be doing. I will probably be doing something like what I am until I die. Even... Even... Maybe that'll be the same... It'll be for the same reason. Yeah, yeah. You know, it's you like build a man a fire and he's warm for one night, but set a man on fire and he's warm for the rest of his life. So that's where I am with AI. No because some of the some of the like function of an explainer or a teacher is to like add clarity to a thing that someone curious about That one thing But some of it is a little bit more relational and a little bit more providing motivation providing a sense of curation One interesting take that I've heard about what mathematicians will end up being is actually more analogous to art museum curators than anything else. They solve the thing, so the art exists, right? They even know how to explain it really well. you know, there, but like you still, you still want someone to help you navigate in this like nearly infinite space of like what ideas are worth engaging with, like someone kind of doing that. And that one, even if AIs were in some sense better at that, I think we would always still prefer like a human that we had a relationship with because the way that we get motivated to be interesting, interested in things is a social phenomenon. If you have some specific technology you're trying to build, you know, that might be different. You need to know there. But I think like the people listening to this podcast, they sort of trust your curation on like what's an interesting topic in the first place. It's not that they're landing on here because whatever your next topic is, that's like what they in a prior sense wanted to understand. They're trusting you as a curator. So my role and arguably that of like other mathematicians might actually just shift subtly into that curation direction of what ideas are worth displaying And that a lot of my job right now even now It basically like i think people think a lot of the time for a video goes into the visuals like sure a little it is not like immediate but like actually a lot of it is just deciding what's worth saying in the first place or what's what's worth putting there um and because that is that's just i want to engage with that and i think i have a trust with certain people and they are curious what i would to choose to put forward, even if the AIs are better than that, in the same way that human musicians are always going to have a role because of that social function of the story behind them, even if the objective quality of the MP3 file coming out is better from some model. That's kind of what I see happening to my job. I want to go back to this question of earlier, we were sort of, just as AI has crossed this threshold, this important benchmark of being able to connect existing ideas to come up with a new discovery or prove or disprove something just as it's crossed the threshold we're like okay but what's the next thing um i want to just um there's a lot more to do on that one by the like just because a couple lightning bolts have been i still i think there's like this flourishing future over the next couple years of like really connecting yeah and so in the limit you could even say um i don know this is accurate to say but potentially a lot of the maybe the biggest breakthroughs like look like this at some level It just general relativity Oh I you like you just you just connecting together like Ramanian geometry and special relativity. Right. And so as AIs keep getting better and better at this connection thing, maybe a lot of big breakthroughs are not really of a different qualitative nature. I don't know if you have a take on that. Well, I mean, a lot of the conversation focus has been on problem solving and that nature of math, you know, like taking off Erdős problems or something. I would say it's not even a majority of mathematicians who would maybe characterize their work as like really targeting the next problem to take down. Are you familiar with like the Langlands program? Ah, okay. So this is like, it's not even a field of math so much as it is like a research ethos where Fermat's Last Theorem is one inkling of this. You had like these two different seemingly disparate things and a connection between them like led to a solution. So, Langlands was a mathematician, he has this famous letter now, essentially spelling out how it seems likely that there's a lot more connections like that, and even got a little bit more specific about the nature of the connections, such that you might imagine this large map, and you've got this valley over here, and this mountain over here, and this set of plains over there. And there's a lot of mathematicians who would characterize their work as being [40:00] of trying to understand the threads on this map. And the progress there, it's not even like, here's this one specific problem that we know will be solved by that connection. It's more that there's been enough time and time again cases where big problems were knocked down by finding connections that it's almost preemptively finding the connections. And so you could have... Interesting. Yeah, it's actually very interesting. Anytime you run into a mathematician, ask them whether the character of their work is more akin to like Langland's program or if it's more akin to like targeting one particular problem, right? And you get a certain like bifurcated split there. But the possibility of AIs being supercharged connectors feels like it might be, you know, an amplifying tool in that pursuit. It's hard to measure though, right? Like, because this cuts to what we were saying earlier. How do you assign a score to say like, yes, you've done it? If it's knocking down a problem, you have a clear way of saying, yes, you've done it. You can write the headline. You can have your PR move as the AI company to say we did it. Whereas if it feels like that was the right connection drawn, you can write theorems around it, and this is the nature of what the papers in that field look like But I think it will require a lot more human in the the loop to basically like say what was it a like the kind of connection that we going for um but that my guess on what most of the useful progress uh from these models will look like like in the next five years is just really filling in that landscape of like connections that you can draw if you're an expert in multiple fields like you've pointed out it's kind of surprising we haven't already had this And what I'd be curious, like, I would be curious to know at a technical level, what causes the unlock there? Because on the one end, you can kind of paint an explanation in your head for why you could be an expert in all of these things and not be drawing those connections, which is when the thing is reasoning, like the method of reasoning is this autoregressive chain of thought phenomenon. Autoregression is actually like a really, really weird way to produce stuff, I think, if you think about it. Like, you're an intelligent person. Imagine I've locked you in a box, right? And then the only way that you have of interacting with the world is that you receive a slip of paper. And then someone says, can you like predict what will come next, right? And then you predict what will come next. And then your memory is wiped, right? And then you get like another slip of paper and you go. Imagine that was done a whole bunch. and then what comes out on the other end they like look at this essay that you wrote You might look at that and be like this is awful That not the essay that I would have written right Because the process of repeatedly predicting something is just pretty different from how you would think as a writer to compose it and think it through and everything And in particular, what would probably happen is you're sort of a slave to your context where you might be answering some question about some particular field. And so you draw on all the context around that and you're going there. the connection that actually is where all the substance is going to come from is by its nature a very unlikely one. And you can do all the RL that you want to try to get better in some way, but what's the thing that's specifically upweighting and incentivizing making these unlikely connections when the vast majority of them aren't the predictable next token that would come in there? And so it's like, it might be the case that you just have this intelligence that's sort of locked in there inside that box, but it's just a weird way of interacting with it. So the thing I'm curious about is, do you ever get any fruit by just questioning the premise of how tokens are generated every now and then in some way? And I don't think it would be as simple as you manipulate the temperature or something like that. But are there any things that you can do that take the existing level of intelligence but find the right ways of sparking those connections that unlocks these sorts of things that we seeing Or do you need just a little bit more intelligence such that at the level of prediction it's kind of predicting that it should be making that lightning bolt to another field? I think it's more productive to reason instead of architecture or even loss function to reason about data. Like, I don't know, we have diffusion models that do text and they're like, not out of the kinds of things that produce are not of a wholly different character they're just not been explored as much i think the more relevant thing is what is the data on which whatever architecture whatever loss function you have is incentivizing you to um uh produce and um it does seem like they're getting better at like okay forget about math i mean we did have this a couple of examples of this kind of thing but if you just look at why are they getting better at being autonomous agents, it just, I don't know, they have like, they're in an environment where auto-regressively producing the step that says, let's step back and do a search over the whole code base. And then let's step back and assess my mistake. Is like the thing that works? I assume what happened in the case of progress in science or maybe in math is you have frontier math-like problems which require, [45:00] metatologists specifically designed them because they require connecting together two different fields and there's all i'm guessing there's all kinds of clever like partially synthetic ways in which to make harder and harder problems like that that require these kinds of connections um for example by like eliminating assumptions and still requiring the i to continue to uh get to the answer and then like it just doesn't really end up mattering what the loss function is it just like it's really about can you come up with an environment which incentivizes this ability yeah Yeah, it feels like you should be able to. Yeah, I can't. I certainly can't speak to the correct ways of doing that, that like unlock all this. But it would just be pretty surprising. Like, don't you think it would be kind of surprising if over the next three years, there's not just like a lot more of those lightning bolts? So this, I think, is an important thing to think about, which is we often think about how smart a single system is. And we don't think about AIs having advantages that are more the result of other facts about them. So in this context the key fact about them is that we can just parallelize and arbitrarily scale them so that whatever level of capability they have it not just like one idiosyncratic genius in the history of mathematics who makes a few connections and then dies in a duel It just universally applying that waterline across all problems that are accessible at the level of capability i feel like this is among the many advantages that digital minds inherently have um that we don't think enough about the fact that you can the other ones being the fact that you can like they can merge all the knowledge together at least that there will be techniques that allow this to happen that you can like um that you can spawn off copies with identical levels of knowledge but yeah i feel like this parallelization is like quite an important property and i'd be curious about your predictions of even if they're not as smart as your mathematicians the fact that they are just you know billions of because for pr reasons that the ai companies are just dumping billions and billions of dollars at this would have a quantity has a quality all of its own that seems in the right direction i think i mean if we take that you know that conversation between montgomery and Dyson at the IAS that like suggests some connection between Riemann hypothesis or Riemann zeta function zeros and random matrices. That feels like the kind of thing that you could try to like automate and that you have, you know, agents representing expertise in all these and basically having, okay, we all know that an institute is smarter than an individual and that like the reason for having people all in the same geographic location is because you want those like serendipitous conversations to happen what does it look like to sort of engineer those between agents um i mean it's interesting because you sort of point out like you can sort of pool all your knowledge since i actually wonder if one of the advantages is that you can do the opposite of that where you have um sometimes uh when an ai is failing it's because it sort of gets into a bad chain of thought and it's really hard to get it out of it right um so you're like i'll just like start again. Same deal with humans, right? Like sometimes you like start thinking about it in a certain way. And actually what's required is to just like back up. Maybe sometimes the form of that, you know, there's stories about people trying to prove something for a long time. And then at some point they say, hang on a second, what if I tried to prove that it's impossible? Like prove the opposite. And that like unwinding your own context and going at it with a fresh mind, you could imagine systematizing that or like having multiple different agents deliberately given different pieces of context and try to like comparing trust there. Like we don't have the same level of manipulation on our own context. In this AI and math series, the first episode will be about when they solved the IMO. And I want to focus on one specific IMO problem that they failed on, which is one that a lot of very smart students failed on. Terry Tao also failed on it. And the nature of it is basically that people were very mad at the problem because they called it a troll problem I almost don want to spoil it because I want to construct the episode around leading someone in without knowing that it turns out to have a simple solution Because you can really empathize with what it's like to be a student solving this. Basically, there's a really elegant way of going down what you really feel like is going to be the solution based on the context of being the International Math Olympiad problem. positioned as it is the like character of the solution is like really enticing but it's kind of hard to prove that it's the best the reason is that it's not there's like this almost brain dead solution that is the best and so the like relevance of that to the whole ai story is like for a human what's required to answer that question is to like escape your context escape the context that you're in the imo escape the context of the way you've been trained to solve these like contest math problems um and if you just approached it like a like a brain teaser that I throw someone off the street, they'd probably answer well. And you sort of want the same sometimes for human research in other contexts, where sometimes just being able to say, refresh your thinking, come at it completely differently. So of all the advantages that digital minds have, that might actually be one of them, a little bit more of a systematic, what does it look like to refresh your thinking? [50:00] trying to answer two separate questions, like spin off two agents, one who's trying to prove it, one who's trying to disprove it, one who tries it like this way, one who tries it. And they like deliberately have different contexts. I would be curious to see if we're having this conversation three years from now, how many of the like significant results that make headlines have that character of basically like erasing the context previously, like trying a bunch of different things as opposed to merging the results of like a bunch of different. It is incredibly interesting because a common concern people have about AIs is this entropy collapse, where they all think the same way because they're trained in similar ways. This is why they're bad at writing. They kind of just like go down the same path and have similar patterns of speaking and so forth. But maybe actually the key advantage AIs have is that you can systematically. It sounded like one of the reasons the unit distance problem conjecture took so long to be disproven, which because people assumed the conjecture was actually true. So mostly they were trying to figure out ways in which to prove it. And so maybe one of the key advantages they guys will have is actually to increase the entropy by systematically trying out both the negation and trying to prove the positive of any given statement Or being able to systematically give different agents different biases That a good point It seems like an important thing in the history of human science is that Einstein is just really motivated by this bias that things should look the same in different reference frames. And then he had multiple other biases like this. But that is just a very formative in his thinking. And you can just systematically survey a bunch of heuristics and see which ones are being productive at a given problem. yeah and so you would suggest basically like systematically increasing entropy at the prompt level even though you have this like inevitable collapse at the like auto regression level yeah yeah i mean and and i mean einstein would be an interesting example because it's like he's got this bias towards things he also has a bias towards like god should not play dice right and it's almost like you want to make sure that you don't accidentally have all of your llms or einstein because you might halt on quantum mechanics progress right which actually goes to show you that there's not a correct heuristic for science. You actually just need multiple independent research programs with their own heuristics. Yeah, yeah. And that feels like old school software, right? As long as you're able to describe that in some way, you have old school software that amplifies that entropy in some way. And if you able to put a clear ontology to the distinct ways of thinking that you want to prompt you explore that full ontology And then each individual one runs off doing what it is But I think there a certain design question there on how exactly do you describe the different approaches The easy one is, are you trying to prove it or disprove it? The harder one would be to say, what are all the tactics that you could take to prove this and make sure that you're applying sufficient breadth to exploring that. I don't think people appreciate the kinds of things that these models can just go handle for you when you equip them with a good harness like Cursor. For example, I started publishing my episodes on Bilibili for a hopefully burgeoning Chinese audience, but everything I upload there needs the sponsored segments cut out. Normally, that would have meant that I would have to ask my editors to go back through all the old episodes, cut out the ads, and re-export everything. But in about just as much time as it would have taken me to send them that Slack message, I can just tell Cursor to do it instead and spare them. And for research for the podcast, I have a whole repo that I've set up where I've just put every single book and paper that's been relevant to prepping for any of the recent episodes. And I've been able to hodgepodge everything because the cursor harness is just extremely good at helping the model figure out exactly what information to pull, whether that's from my repo or from the web, in order to answer the questions I have while I doing research So whatever you happen to be working on right now just try pointing cursor at it Go to cursor slash floor cache to get started Obviously AF or math is making a lot faster progress than everything else And people point to verifiability of the domain as the key reason this is happening. I think that's one of the two important reasons. But I don't think, I think people really neglect the other one. And I'm outside the labs. I don't know what's actually going on. This is a totally naive theory. okay a tangential question to why ai is making so much progress in math why has it been so slow computer use which is what you you know computers is actually very verifiable it's like you know is my etsy package coming or like it's my event booked you know whatever these are extremely verifiable things to survey what computer use lacks is grindability um so because websites have like bot detectors and also it takes a tremendous amount of compute to run parallel rollouts it's very hard to just run like a thousand parallel rollouts at the same checkout flow on amazon um because you'll get like shut down by andy jesse right and so you can personally this is the like red x on door cash button exactly and so you can try to build clothes every single website this is very labor intensive and slows you down so and [55:00] The reason, by the way, you need to do so many parallel roles in order to learn a skill currently with deep learning is that we haven't solved sample efficiency. Sucking supervision to a straw. Yeah, exactly. That's what he says. Of course, people are working on many different techniques. But fundamentally, there's this big problem and there's this big constraint in the way you're training eyes. With code also, you can containerize a given level of progress in a repository and then just spin out thousands of parallel containers or hundreds of parallel containers and say, like, try to implement this feature. and it's totally deterministic. And because it's deterministic, you can solve the credit assignment problem because you know that whatever caused this rollout to succeed and this one to fail, the diff is the thing that like worked. And this way you solve the credit assignment problem. If you have situations that are starting off at different starting points, this credit assignment problem becomes much harder to solve. But most of the things in the real world are just very hard to containerize in the same way. Like coding and math are exceptions to this rule. But if you're just trying to figure out how do I build a new business that succeeds? How do I go trade in the markets for a day and make money? The fact that you had to interact with the real world and things change day after day means that you can keep replaying and grinding and farming the simulator But the math of course is the exception And I feel like this is actually an important driver of progress in this domain and also in coding It not just verifiability It has to be grindable. The third reason that people point out that AI is making fast progress is they focus a lot on lean and formalization. Again, I have literally no idea what's going on in the labs. I feel like lean just doesn't matter that much for the current level of progress in AI. Or why is AI able to solve the unit distance problem? Well, they, or sorry, disprove the conjecture about the unit distance problem. They release the chain of thought, or at least a rewrite of the chain of thought. Didn't have any lean in it. I think it's just like the process-based supervision that lean provides, where you know each step is correct, seems like less relevant than just having this grindable outcome that is verifiable. That's an interesting point, like grindability mattering more. I guess I will say on the, yeah. Okay, so naively, you might think lean provides something unique for math because you're able to see if it can prove it. You have old school software that can tell you yes or no, you use that as your VR. I mean, so what would corroborate your point is the idea that like the initial attempts, again, I'll just circle back to IMO. It's like initially, DeepMind basically does that. It like everything in lean And then the next year it all in natural language So to your point not needed i do i think there is a um a yet to be explored benefit of that formalization domain which is at the moment you still need you know ultimately like a human is reviewing that um counter example to the unit distance conjecture to say looks good and that that provides a certain bound on how like endlessly explorable things are like if you consider like alpha go alpha zero style stuff where they're just like off in their own universe, just like playing a bunch of Go and exploring themselves, just completely going potentially off the rails of what any human needs to look at, but they still have this automated verifiable reward. It's not just that, hey, you can do RL on that. It's also, you basically never have to check in and you can just like poor compute at them like exploring the universe of Go. What stands to be interesting, like maybe this won't pan out, but I think the jury should still be out on like whether this will yield anything. With Lean, you could imagine having a basically endlessly running program that's constantly trying to extend Mathlib. So Mathlib, it's this GitHub repository that's basically like all of math written in code. It's very far from all of math, but they want it to be all of math written in code that you can ask like is this proof correct It very labor intensive to write these proofs There like a whole sub community around it But you could imagine what if you just had an AI where you say simply try to extend Mathlib. Maybe it's a fork of it so it's that it doesn't have, you know, like trash in it because people, you know, people have certain taste for what they want to be in there. So you have like your fork of like the pure AI Mathlib and it just goes and just like doesn't stop. It doesn't need anybody to check in on it. Right. It could just keep going. it might come up with its own conjectures it might come up with its own theories and like different definitions maybe many of them are useless but it just has this infinite tree that it can like grow out that's a very unique thing that math has that nothing else has where you could press go and then just like just poor compute at it and like look away for 10 years and then come back and say like what do you have? And there's going to be something, right? And then there's a question is it useful or not? Like how do you suss that out? That's just an interesting thing to be able to do it would be very surprising if that didn't yield like some sort of interesting mathematical insight from it, right? So I think that's the real case for, okay, there's two different ways that Lean is important in this story. That's the first one, then, basically, is how it's like, you could let go, not even check in, and progress will be made. You can do that with Go. I don't think you can do that with natural language math. That's very interesting. [60:00] Did you see Karpathy's auto-research idea? He wrote this basically one Python file that does basic LLM training and then just had a repo where agents would try to make modifications to the file. If it sped up the speed run, the modification stays. Eric Jang, who came on to explain how AlphaGo works, did a similar thing when he was trying to build in a very strong Go bot. And he had interesting observations about the kinds of... Like, it's really good at just running an experiment and going down that path, but it's bad at stopping at dead ends and just doing extremely parallel things. Anyways, this will probably be changing in the future. It's very interesting to think about what it looks like in the limit. I mean, this is fundamentally like what the human institution of mathematical research is, right? It's just like this is a library extended in interesting and useful ways. And this way you don't have any outcome-based supervision. no there's no outcome that you're trying to incentivize but you have a process the the you know the steps are correct you just don't know if it's going in an interesting direction but yeah you would like if you were doing that you don't want to completely go off the rails and like do a random walk through the space of logic you probably want some like supervisor model that trying to provide heuristics on whether it useful or not um but yeah of that character I mean you know people are working on it That one of those five years from now I be curious to be able to get the future version of us talking about whether, maybe that goes nowhere, but Terry Tao was talking about one research project that's basically try to exhaustively search the space of possible algebras. You could imagine different axioms that you apply to algebraic systems. and so like when we come up with group theory there's a certain axiom system that like has this flavor of they kind of look like arbitrary rules unless you know the motivation but it's basically like what have you tried all of them do any of these yield useful things and like the vast majority of them is just trash in some way like it all collapses to like no interesting results but like every now and then there would be this little island of like a completely different type of axiom system that at the very least seems rich in terms of like the number of theorems that can come out of it and that's like bread and butter for what you would imagine like automated provers being good for is like exploring that space and seeing which one of them turns out to be something and like maybe one of those islands actually turns out to be something you can retroactively put motivation on to say this is the kind of structure that's trying to get at in the same way that you could imagine looking at the axioms for a group not knowing that it about symmetry but retroactively realizing like wow this is very relevant to studying symmetry so you could imagine results of that flavor But instead of just exploring possible algebra systems it like all possible like logical consequences of any kind of axiom On the point about whether you can provide process-based supervision without lean. So DeepSeek had their DeepSeek math model and they released a paper on how they trained it. And it was quite interesting. So they have the problem with having natural language proofs is you don't know if it's correct or not. And so they have a verifier and then the verifier is trained by a meta verifier that makes sure that any of all the problems that they're training this model to solve in like the art of problem solving, that the verifier is giving good feedback on that. And it like it works. And so it's just interesting. Natural language verification with some sort of meta verification kind of work at least seems to work so far in the published literature. And also it seems to work in the published products that we're using. like if you look at coding agents they're getting better and better at like writing clean code and refactoring code and stuff like that and I'm sure that there's process based like LLMS judge kinds of things which are saying trying to provide taste and say hey is this like a clean way to write this function are we like are there duplicates of the same kind of modular forms and so forth I feel like that should also work for mathematics right It like it doesn seem It seems more plausible for math than anything else even if you're only working in natural language, that you could trust a verifier. I mean, you and I were talking earlier about why they're bad at writing. And, you know, I was asking, like, why you can't just have... Like, they seem to be good judges. If I give them two essays that, like, students write, they'd be able to say which one's more, like, accurate and insightful. So why can't you just have, like, a verifier saying, like, is this a good piece of writing or not? And maybe the ultimate failure there is even if they're good at discriminating between a B essay and an A essay, they're not actually good at discriminating between an A essay and a thing you actually want to read that would be followable on Substack and Insightful and all of that. They actually end up preferring just uninsightful pieces of writing. And so on the math front, I guess the question would be like that step to simply know, like, is this a correct proof or not? That lends itself to like an automated verifier, even in natural language. You could probably still make a ton of the progress. It still doesn't like I still like the sort of tree of logic out of lean front, just in that you can really go off the rails. Right. Like there's just no constraint on like the previous way that things had been phrased before in the same way that, you know, everyone talks about like move 37 in like AlphaGo. and say, [65:00] Like, what is the thing that lends itself to just going outside the prior heuristics? And it seems productive to have a disconnection from the rest of the world in that exploration as like a complementary research pursuit to the natural language math front. I mean, the other relevance of Lean there would be like, okay, let's say you have your pure natural language RL environments and you have a pure natural language set of proofs. And people have said, like, proceed AI mathematicians. And they go and they generate, like, 10 papers a day that produce a bunch of stuff. If the error rate, if there's, like, any error rate to that at all, so Alex Kontorovich has talked about this, it becomes insufferable, like, as a mathematician. Because you would basically be like, every single time I see one of these, I kind of don't know if it's worth my time. even if 99 out of 100 of them are right. I don't know if it's worth my time to even go through it because it's really labor intensive to find what that error would be. And it's like really frustrating if it turns out you spent all your time on a paper that was trash. And so having anything that's able to give you that green track mark that says, even if this is going to be complicated to understand, even if it going to be a pain you at the very least know it is correct Like every other field would kill for that right And like math has that if the models are also able to take their natural language proofs and formalize them. And so that seems huge, right? The ability to have that, like every field would love to have something like that. And so I think you are right that Lean is maybe overrated on the side of the importance of it being used as a vr environment for any kind of like just progress in math generally but i i definitely wouldn't write it out of the story yeah yeah i also love this extension of math live as a metaphor for like what's going to happen to our civilization pretty soon for sure yeah right it's like for millennia humanity is building this like corpus of knowledge and understanding and everything that we have now distilled into these models and at some point the models will just like extend that arbitrarily um but on the writing front i actually have i i have a theory of why writing is making worse progress than these other domains so i think one of the one of them is what you said that they're bad at judging not only a versus b but they get like just totally derailed by b star which is this like a shitty essay that just hits all the um all the bells and whistles that like a is supposed to hit and then so the reward hack hack thing just totally goes off the rails But I think the other important thing is that writing is not modular in the same way that code and math are You can write a function many different ways, and they kind of do the same thing. And of course, you want it to be very clean and stuff. But at the end of the day, it works, it works. Same with lemmas and mathematics. And then you can have some end product that is different from the way it is produced. So the code is the thing that produces some end product and you want a functional end product. Whereas in writing, the end product is directly the thing the AI is producing. And each paragraph, sentence, word matters because that is the substance. It's not like some separate thing that is produced out of the writing. And so it can't be slop. in the way that code can be sloppy and still produce some outcome that you want. But you were just pointing out how actually we've gotten much better at agents writing not just functional code, but clean code. Why is it not the case that the same progress that allows you to go from merely functional to clean and a mergeable PR doesn also result in clearer writing Yeah that a good point I mean also has it not I agree there many ways in which they terrible writers but for a lot of writing I consume I find it better to just copy-paste it into an LLM and just say, explain this to me. The explanation will be better than the thing that is produced by the human. It's funny that we say these are such terrible writers. Also, my reveal preference is just like, can I just have an LLM explain it? Even when I'm talking to a human expert live on a call. If it's a piece of knowledge they have that only they have that's not encoded in the distribution, I want them to explain it to me. But then if in order to understand that, I need to understand a more basic concept, I would prefer if it was socially acceptable for me to just be able to say, let's pause there. I'm just going to ask an alum how that works. And then we can come back to your special piece of knowledge. Well, it sounds, I mean, that's distillation, right? An explanation. And so if I'm thinking of quality of you as an essay writer, if it's that I give you a book to read and I want a book report, then I might believe that, okay, the LLM maybe gives me a better book report. But I think what people are really getting at when they say it's bad at writing, what is writing? It's not just distillation of preexisting ideas. It's not just how to explain clearly, because they are good explainers. It's like, what is the idea [70:00] insight. And this is where it gets like, just autoregression is a very weird way to generate stuff. Because when you're writing, you sort of know, in order for it to be good, you have to have an element of the unpredictable. And it's not just like increasing temperature in your mind or something, right? It's like knowing exactly the correct point when you want to make an unpredictable move, and that that's going to be what's more insightful. And so even if it's better at explaining a pre-existing thing, it's like, what generated that book that you wanted distilled in the first place right it wasn't it wasn't an llm that like generated it and you just needed it it's like some author who who threw a lot of exploration of ideas in the world and then deciding what aspects of it were interesting and which ways of presenting it were like the the coherent um well-motivated narrative it's like they put that all together in some way and you know if they're a good author it's probably one that actually you would uh err on the side of reading their book instead of the distillation but so what makes it worthwhile to like explore at all in the first place and you're uploading it at all um i think it's all of that side of it that's the like when when people will cite them being bad at writing and it's that element of unpredictability of being deliberately um choosing something that novel that like very directly contradictory to like the way that things are being produced yeah that a good point i think they also really bad at building really good mental models of people which i think is a very important skill in writing so annie matushak and another collaborator um whose name i forgetting right now did a interesting report where they tried to teach lms to write good space repetition prompts and i really like this because even though it seems like a really totally random skill uh it's just like people are talking about recursive self-improvement in a year yeah and you can't get these things to write good flashcards and what's going on there right right uh and they tried many different kinds of techniques and they're like you know sophisticated people like they tried to rl open source models they tried all kinds of including chain of thought and the big prompt they sent to the best close source model etc and um the key constraint it seemed to me was that writing a good card is about projecting somebody's mind in three months and what is the way in which they will associate the question, like what kind of answer we'll be thinking about at the moment and is the elicitation that inspires the detail you actually want to take away from the passage you're trying to make cards about. I think writing also is similar to this, where if you writing something the reason it such an enervating process that takes so long is each word you should be thinking or each sentence you should be thinking what is happening in my reader mind right now even if i flip the phrasing around where so the end phrase goes to the beginning and like this is the first image that comes to your mind before you read the rest of the sentence that kind of maybe auto regression is is bad at that kind of um there's maybe a more diffusion-like property of considering the whole rather than going sentence by sentence but also i think that requires a lot of mentalizing which these models weirdly struggle at well i mean interesting question like is it weird that they struggle at that so i might butcher this this you know how uh when you like cite studies that you once read and it's like maybe the study wasn't real or something this is one very memorable one on okay so let's say you want to quiz people's eq like you show a a flash card of someone's like facial expression and someone's trying to describe like what's that emotion. So I've got these really good tests online that'll have like a face and then four possible emotions. And it's like surprisingly hard to like describe exactly the correct emotion. But you also get the sense there really is a correct answer. And if you try this with like people in your life, you'll notice that the ones who actually are pretty plugged in socially, like do really well on it And the ones who are a little bit more like left brain like don Okay so that is a kind of test you can do I vaguely remember an experiment to this effect where they took people who had freshly gotten like botox um in some way um and they did like a pre-test and a post-test and like post-test they were just much worse at like reading people's expressions like that feels kind of weird they got botox so the person taking the test it's like so you you you do the test and then you go and you get botox and your face is all like frozen and now you are worse at understanding the emotions of what you see right and the thought is that part of understanding this emotion that you're looking at is doing it yourself. At a facial level, moving your face muscles, and you see that, you mimic that, and you're like, oh yeah, that's anxiety. At some very subconscious level. So in that sense, if it is the case that models have bad theory of mind, sure, they know everything because they've read what everyone wrote. But at a level of actually able to put themselves in your shoes, in the same with it, like my face muscles are mimicking your face muscles. That's what helps me understand how you feel. Not surprising at all. They don't have face muscles. Their brain works completely different. It's just like, it's like an alien trying to empathize. Like, how could it have theory of mind? It would be like this very emergent thing to have theory of mind. Whereas we can just like plug it into our own minds. It's like, we've got the ready-made hardware to just like place it in. And so. That's very interesting. [75:00] Not that, from that lens, it's not that surprising. Okay, Grant, we are both partners with Jane Street. I'm sure over the years you've interacted with a lot of Jane Streeters. What have you found that's unique about them or their culture? I mean, I did this interview with them this year that partly was interesting because they don't usually have anything outward facing. I mean, in the industry, they're known as having like a pretty wild retention rate. Like people just stay there and it's getting an inside view of that. I remember one of the comments, someone was saying, even though the people have role titles, like, you know, researcher or trader or engineer, they often don't know what their colleague's actual role is because everyone's doing a little bit of everything else. Like even if you're officially a trader, you're doing a lot of research. Even if you're officially a researcher, you're doing a lot of coding. And I suspect maybe that's part of why they have the insane retention that they do, because anyone who wants to be growing, they just have the chance to do a lot of different kinds of things. All right, Grant, I'll do the plug for you this time. If you want to watch this full sit-down interview that Grant did with some of the folks there, go to 3b1b.co slash jainestreet. All right, Grant, let's talk more about AI and math. What advice do you have about using LLMs to learn? So as I was describing for a lot of well concepts I find them very helpful But often just a couple of further messages down and i trying to understand something and i just they so confused themselves or confusing me and they don't explain the right way and then i'm just i know that talking to the right human could clear up my confusion in three minutes i don't know and i feel like more and more we're going to want to use these things as somebody's i've taught a lot about education yeah and you know representation and stuff we're going to want to use these things to learn things so um yeah have you have you noticed the ways to use them more productively to understand concepts i'm curious to hear your take on this i mean i'll give mine i um even pre-llm i feel like a relevant insight in learning was um recognizing that like who matters more than what so like advice to any college student when they're choosing what courses to take uh care a little bit less about your pre-existing interests because they're kind of arbitrary right now and care a little bit more about whether like the person teaching it is a good educator and someone you resonate with. I think in choosing what to read, like what books to read, like who the author is maybe matters more than if it's a prior interest. So if there's a book you've liked before, read what else that author has written rather than reading another thing on that subject. And I'm getting to like LLMs on this. So like there a difference in feel for trying to learn something if you look at a Wikipedia page of it versus if you look at let say like it a philosophy topic and you go to the stanford encyclopedia philosophy or if it a math topic you go to the like princeton compendium of math where the uh the difference there is like the articles are deliberately written by one individual who uh like tries to actually craft a motivation around it and everything whereas wikipedia it's this like um local minimum that's reached where basically every sentence has to be correct and i think a good exposition you care a little bit less about like correctness on the way but you can like deliberately craft things that are a little bit wrong that you correct along the way i think it's like edited out in a crowdsource environment so like that llm explanations feel to me at the moment a lot like wikipedia which is to say amazing right like imagine world before wikipedia like how how long it would take to like find and like susan and everything but nevertheless what's the most useful part of a wikipedia page it's often just the references at the bottom right you look at the like key references and you go to them and you read them it's like actually sometimes that gives a much like better overview of it so often i like to just ask an llm um like who should i read right like uh and and maybe i can even give some specifics on ways i want to learn i actually got gaslit by this once where i remember trying to learn about like i don like semiconductors or something I was like this feels very visual This is all like text I like is there any really good like well math video or not math sorry, a well-visualized video kind of like explaining the concepts that you're getting at in Claude? It was like, yeah, here's a couple in the top one. It was like, here's one from three blue and brown. I'm like, I can guarantee that there's not. and it was an actual video an actual link but it just had like misattributed someone else's to me and it was good and it was like i had a much better experience clicking over and watching that video to learn about the thing rather than like trying to proceed forward with questions there so in that sense basically using it like a very souped up version of google on like zero in on the right human written resource um what about you like what you you engage with these a lot what's the best way i think you put your finger on it the most productive learning sessions I've had is when there's some artifact that a human is produced, whether it's an article, a book, a video that organizes the relevant concepts in the correct way and builds up the motivation of why building up the next idea would be relevant to solving the next problem you did encounter and the next idea and the next idea. And then using the LLMs to just do a little bit pruning around this branch that the [80:00] book is identified so i was um i was actually i was going through i think you might have recommended steven strogetz's textbook on the chaos one yeah yes and non-linear dynamics i love that book and so i was going through it and um it was it was like bliss it was like your videos in like a book form he's so good it was super fun and the way i was learning it is like i'd have on one third of the screen his like lecture from university on one third of the screen i'd have that part of the textbook and on one third of the screen i have an llm now i was actually thinking if i was back in college and watching this lecture live would just totally go over my head like these kids must be really smart because i'm like pausing and like reading the textbook and talking about llms and then restarting again but with him curating what is the right order to understand concepts what is the right problem to motivate uh understanding a concept oh also another thing i was really bad at is a thing a really good human can do is when you ask a question, they say, like, actually, you're just not really thinking about this topic the correct way. Yeah. Like, the question you want to be asking, the correct way to organize these concepts is X. Yeah. And that one just can't really do that. Yeah it a little too placated I mean this is ultimately like the very like the supplicants and you know it very like oh what an insightful question you know that kind of thing you want to you want to strip that down um that a good point and i think that cuts to theory of mind a little bit yeah like recognizing that to ask a certain kind of question reveals that the mental structures are not at least they're not the same as what the like explainer has um and sometimes people do this to a fault right like i think a really good teacher let's say you have like a middle school like math classroom or something if a student like asks a question that suggests they're thinking about it in a different way it's actually really hard to like take seriously in the moment hang on could you get to a right answer with that before you say oh instead of that let's do this and like the really good teachers are are able to like jujitsu the like uh uh creative way that the student was thinking about it and and and bring it in. I mean, LLMs aren't doing that, right? When they are not reframing your question, instead they kind of like run off. But at the very least, it feels like there's three levels here. And so like LLMs at one, good explainers at another, but then like the A plus explainers, the one who can like jujitsu your way of thinking and say like, oh, that's where that's useful. And so maybe there is a certain you know cycle all the way around where again five years from now the LLMs will still be doing that but in the better way What is your recommendation to students who I sure email you this question all the time Look I was curious about doing mathematics. I'm really passionate about the subject, but seeing all the progress the areas are making, I don't know if it makes sense for me to pursue this as a career. And this is not relevant not only to people in mathematics, but I'm sure to people who are noticing that their field is more and more getting productivity gains or whatever from AI. So coding is very adjacent to this. Yeah, what advice do you have for people? I wouldn't trust any advice that I give. It would maybe be how I'd like couch it. But even pre-AI, it feels very important for any job that you're going to go into to really understand, like if we're talking about a job, right? We're not talking about like you're a gentleman scientist and you want to like engage with the math world or something, you should understand where the money's coming from and like what value you're actually adding and like the connection between those two. And I think often like a surprisingly small amount of thought is put towards that, especially students. They're in this environment where they probably want to go into math because they've always been good at it and they just been rewarded in life for like proceeding through the next hoop correctly and next step And when they think they want to be a mathematician it because it a version of getting to continue to engage with that It like well I go like where do people get to do this Rather than thinking like, what value am I adding to other people? And to what extent is that like the reason that like salary is flowing in my direction? It's actually quite different in different cases. Like in some cases, it's a very prestigious mathematician and like their presence at a university lends a certain brand value. And that's like why the university like wants them. In some cases, it's like the NSF grant is given because you've got this like public good belief that we have that basic science has. And like you've got this institution around that. And there's going to be this whole bureaucracy around trying to act as a proxy for what we think that public good is and a whole song and dance around how to like correctly make them predict that your progress will be in the spirit of that funding. Sometimes it's just straight up teaching, right? It's like people like to send their kids to an institute that has experts teaching them. And like, that's what you're doing. And you are providing the brand value by being an expert and then the direct value by being a teacher. So regardless of whether AIs are like proving theorems or not, or like whether we're talking in 2016 or 2026, like that is a thing that not enough students thinking I want to be a mathematician think about. But I think it's worth thinking about. Like for me, I think that, you know, I think. [85:00] I just wasn't necessarily thinking about it and kind of stumbled into this career path where basically math exploration can be monetized as entertainment. And I stumbled into that. I'm very grateful that I did, but it was an accident. It wasn't this deliberate thing. And I think I could have avoided relying on serendipity and maybe done that a little bit more by design had I been thinking critically about it. So to your question, if it's the case that you have almost automated theorem proving, And then let's say it's the case they're also really good explainers. So it's like even to get the human understanding. I think a lot of the social role that mathematicians serve actually doesn't change that much, right? You still have a sense of, as a public, we sort of feel like there's value to basic science. And we're trusting in the judgment of mathematicians to determine where their time has best been. And the prestige comes from within that community. It's like other members saying that this was a really good result more than it is like the grant writer who like really understands algebraic number theory to understand that it's a good result. And so there's going to be some inner culture of what constitutes like valuable contributions. Maybe it shifts away from theorem proving and maybe it shifts towards like good definition writing Maybe it that like museum curator idea but you going to have that same community And as long as society as a whole is still valuing the premise of basic science And if we in the abundance world of what AI brings probably there more funding in that direction in some sense right On the side of prestige to institutions for who their lecturers are, I mean, I actually think teaching is one of the most stable post-AGI jobs that there is because it's so relational. it's so like this is where parents want to spend their money if they have an abundance of wealth is like on good teaching and good educating and and it goes so far beyond explanations like even if llms are good explainers the thing that a teacher is doing is such a social like coaching mentor type thing that like that's probably the most one of the most stable careers that's going to exist over the next 50 years um and so insofar as what a lot of mathematicians role is like overlaps with that, you know, you as the prospective student going into it, you could lean into that. Actually, I think a lot more students should like think about and give like pay credence to the idea of being like just a math educator and like the value that that can serve towards the next generation. So I couch again on I don think I the one to say here prospective young mathematician like here how you should think about the future because I like a YouTuber right I someone who is not in the institution that they are thinking of going into And so I speaking as an outsider looking in But it feels like generally good universal advice Know where the money is coming from. Know where you plug into that. And like, if you're just asking those questions, you're actually already like steps ahead of all of the other like fledgling prospective mathematicians yeah and in fact i think in the crazy world in the world where within five ten years the ais are coming up with not only solutions to the the millennium prize problems but coming up with like just totally novel problems to be solving in the first place novel mathematical fields and objects and stuff it is in that world where first of all there's a ton of abundance and two the the things that ai minds will have like gone furthest in where they will have seen like furthest beyond our horizons will be mathematics and there will be so much demand of like what have the ai seen can you explain it to us yeah yeah i feel like in the in that world if there's any jobs whatsoever surely distilling what the ais have learned will be one of them also it funny because all of this sort of presumes that it useless right like we not talking about the actual practical applications of what math is being done So insofar as there any economic utility to it you would imagine that the people who understand it and are able to, like, make the decision of where it should point, like, they actually have a lot more economic value by, like, being able to make that judgment as curator and point this, like, behemoth of, like, new math, like, pointed in a useful direction. Like, suddenly that's a much more levered move to make than it had been previously. Can I actually ask you about that? So obviously, one question for AI for math is not only can it do it, but is it any good? Yeah. Or is it any good for anything? You were describing all the ways in which group theory, we're trying to solve this, we're trying to figure out random facts about the roots of different kinds of functions. And now it's all these different applications that are practical across many different fields. Do you have some sense of if we just totally get to a place where mathematics is The field of human mathematics is accelerated 10x or 100x That some crazy shit happens Or are we just actually going to be bottlenecked by other fields? I think there's some fields that probably will I mean, it's super spiky, right? I think progress in algebraic number theory [90:00] It feels unlikely that that then unlocks some things. But I don't know. I remember talking to this mathematician who does more dynamics and PDE solving type stuff. And he was referencing basically his group had some ideas that... Let me see if I summarize this right. It's like the way that Boeing would make planes is they would make it and then they would do a bunch of tests. And they had to disassemble it and reassemble it based on those tests. And they essentially had some insights on how to do more things in simulation such that you don't have to deconstruct and rebuild it. And it saved Boeing just billions of dollars or something. And then they just started funding that group. It's much more obviously application adjacent because PDEs just sort of are that. So progress in that domain, you would imagine actually do unlock some things. And I don't know if it's these like step changes, but maybe it's more on the side of like engine design becomes just a little bit more fluid or like coming up with the right wing shape instead of running a whole bunch of complicated like CFD. Or maybe you're able to like speed up your like CFD simulations because of certain pure math insights like makes those more efficient. I bet you just see like a lot of like great incremental improvement there. it seems less likely that like the massive breakthroughs in math immediately turn into like this massive economic breakthrough like you solve the navier stokes uh like problems and then that unlocks like an ability to simulate more things but you probably will see like at those fringes just some some meaningful um like leakage outside of the pure math insights into into other things also i mean there's a ton of people working on things like you know ai engineers like physical engineers like material science and things like that that would be you have to imagine that like they would be in a good position to look at the AI math insights and decide if they relevant in some way or not And so it's another one of these things where I'm not going to sit here and like put a flag in the sand, like predicting that there will be, it'd be a little bit disappointing and a little bit surprising if there weren't over the next five years, like economically valuable improvements that were made that were directly like referable to the like AI progress in math like that just would be kind of disappointing if it was just taking down a bunch of erdish problems and like none of them actually you know it wasn't doing any of the math that actually directly touches physical world yeah i mean to your point about well a lot of history mathematics is about like building up these like piles of concepts and connections and whatever yeah and sometimes the the piles connect with each other or they're you discover an application somewhere else at the very least you just build up this huge pile and as a you know broader progress in society happens during the singularity when we get to the industrial part of the singularity. You just have all these different ideas that you can hopefully are useful in other parts of the world. I mean, yeah, like I said, one of the interesting things about what's happening is it causes people to step back and ask, what is math? And maybe one of the awkward conclusions of it will be revealing like, ah, man, over the last... It's just become wholly useless. The kind of questions being asked have become so divorced from things that are physically applicable that that's one of the things mathematicians have to come to terms with where everyone will look and be like on a second like where are you guys supposed to like if there's so much that's like 10x progress there like why aren't we seeing it over here and then that church is like every time we wrote those grant proposals and said like trust us like the elliptic curve progress is going to help with like cryptography like it like shines a light on the fact that like maybe it doesn't so that's that's one possibility um grant this is super fun thanks so much for doing it absolutely my pleasure