推文的结构很简单。先替你说出一句不屑：好吧，那又怎样，不就是数学嘛。接着摆出十行，每行一个数学名词、一个箭头、一个现实里的好处。最后收一句：加快数学发现，也许能把几个世纪的科学进步压进几年，活在这个时代真是疯了。

这十个名词不是随手编的。我对了一下 OpenAI 10 月 6 日放出的那个仓库（之前写过它），十个都在，编号是 104、107、110、120、121、267、362、365、366、372。推文挑的，正是 372 个结果里名字听起来最“有用”的那几个。

我喜欢这条推文的热情，也同意它一半的结论：数学是科学的地基。可“地基”这个比喻本身就露了馅，地基不会自己长成房子。从一条定理到一张病床，中间的箭头有多长、朝哪边、里面装着什么，推文一个字没说。

这篇只干一件事：把箭头拆开看。先说清边界，十个结果是真是假，我不判断，它们现在都还只是 OpenAI 的声明。下文说“如果它对”，是为了看箭头，不是替谁背书。

先问每个问题是从哪儿来的。答案出奇地一致：大多是先有了现实里的麻烦，数学家再把麻烦提炼成一道题。

Calderón 1980 年那篇短文开头就写明，问题来自电法勘探。据 Uhlmann 转述他晚年的回忆，1940 年代他在阿根廷国家石油公司当工程师，琢磨怎样从地表的电测量推断地下有什么。这个念头他揣了三十多年才写下来：只在物体表面测电压和电流，能不能唯一确定内部的电导率。

Mumford–Shah 来自计算机视觉。1989 年，两位作者想用一个泛函把图像切成几块光滑的区域，切口越短越好。k-server 来自操作系统里的缓存：内存页换进换出，抽象成 k 辆车在一个空间里接单。编辑距离是 Levenshtein 1965 年研究纠错码时定义的。Vlasov 方程是 1938 年为等离子体写的。

矩阵乘法的故事最好玩。1969 年，Strassen 本想证明高斯消元那套 n³ 已经最优，结果反手找到了更快的办法。

所以推文画的是“定理 → 应用”，历史上更常见的却是“应用 → 问题 → 定理”，然后才轮到“也许，更好的应用”。箭头的起点，往往就在推文说的终点附近。

还有一件事更扎心：推文说“最终可能实现”的那些应用，大半已经存在了。重症监护室里有监测肺通气的电阻抗成像，肝病门诊有测组织硬度的弹性成像，肾脏配对交换跑了二十年，玻色–爱因斯坦凝聚 1995 年就在实验室里做出来了，测序比对每天都在跑，GPU 每秒都在乘矩阵。

真正该问的不是“这个应用会不会出现”，而是“这条新定理，会不会让这个应用变好”。我把十条逐个放到这个问题下面：

十行看下来，没有一行是“定理一出，机器就来”。有几条，比如 Vlasov–Maxwell 和玻色–爱因斯坦凝聚，如果成立，会是数学物理里几十年一遇的大事。可它们回答的是“方程在数学上站不站得住”，工程师那边，方程早就在用了。

这不是说数学没用。恰恰相反，下面拿一个问题，看看数学真正“有用”的时候长什么样。

就拿推文里最像医疗广告的那条：Calderón 问题通往便携人体扫描。

设定很朴素。物体内部的电导率是 γ(x)。在表面加一个电压分布 f，内部的电势 u 满足 ∇·(γ∇ u)=0，然后在表面测流出的电流。把所有“加什么电压、测到什么电流”的对应打包，叫 Dirichlet-to-Neumann 映射，记作 Λ_γ。Calderón 问的是：Λ_γ 能不能唯一定出 γ？

先补一个直觉。在表面加电压 f，物体里消耗的电功率是 Q_γ(f)=∫γ|∇ u|²，它就等于你在表面测到的那个量。电流总会挑最省能量的走法（Dirichlet 原理），所以把 γ 轻轻改动一个 h，功率的一阶变化只有 ∫ h|∇ u|²，u 自己的变化在一阶上不起作用。

这一招的妙处在 ζ：实部让函数指数增长，虚部让它振荡，两个凑在一起，乘积刚好是一个纯粹的平面波。后来人管这类解叫“复几何光学解”，1987 年 Sylvester 和 Uhlmann 靠它的加强版，证明了三维以上光滑电导率的完整唯一性。

到这里，好像离便携扫描仪只差工程了。并没有。

换一个能算到底的例子。单位圆盘，中心半径 ρ 以内电导率是 k，外面是 1。在边界上加电压 e^inθ，也就是绕一圈起伏 n 次，我管它叫第 n 个“频道”。

把数代进去就知道麻烦在哪。内含物占一半半径（ρ=0.5），电导率翻倍（μ=1/3）：第 1 个频道里它让读数偏 18%，第 5 个频道只剩千分之三，第 10 个频道是百万分之六。频道越高，看的细节越细，信号却按 ρ²ⁿ 指数衰减。

这不是圆盘特有的毛病。Alessandrini 1988 年证明，一般情况下电导率对边界数据的依赖至多是对数稳定的；Mandache 2001 年又证明，对数已经是最好的，不可能再好。翻成人话：想把图像的分辨率提高一截，测量精度要提高的不是一截，而是指数倍。

所以电阻抗成像的图片糊，不是工程师偷懒，是一条定理。关于这台扫描仪，最有用的数学恰恰是一句“做不到”。它告诉你别去追高清解剖图，去做别的：比如只看肺里通气随时间的变化，或者把电测量和超声、磁共振这类别的物理量绑在一起。今天进了重症监护室的肺部电阻抗成像，走的就是前一条路。

真实的组织是各向异性的，比如肌肉顺着纤维导电更好，电导率得写成一个矩阵。这时候有一个绕不过去的障碍。

所以各向异性的情形，最多只能把电导率定到“差一个这样的形变”。反过来，“只差一个形变”在三维以上对不对，从 1989 年 Lee 和 Uhlmann 做出解析情形起就悬着；2024 年还有一篇宣布解决的预印本，后来被作者自己撤回。仓库里的 365 号声称的，正是光滑情形下的这件事。

故事到这里本该结束，可 2003 年 Greenleaf、Lassas 和 Uhlmann 把这个缺陷推到了极端。他们挑了一个奇异的 F：把一个点撑成一个球，比如 F(x)=(1+|x|/2) x/|x|。推出来的电导率在球壳里极度各向异性，电流乖乖绕着走，球里放什么，边界上都测不出来。

医学成像里的一个“不唯一”，成了隐身斗篷的数学。三年后，Pendry 等人在《科学》上把同样的换元思路用到电磁波上，这一路后来叫“变换光学”，同年就有了微波段的隐身实验。

推文说，Calderón 问题通往便宜的扫描仪。历史上，它先通往了“扫描仪注定发糊”，然后通往了隐身斗篷。我不信 1980 年有谁能预言这一步。这个“不能预言”，后面还要用到。

Calderón 的故事说明箭头会拐弯。另外几条说明，箭头就算是直的，也常常不在最要紧的那一段。

一位病人需要换肾，亲属愿意捐，可配型不合。另一对也一样。如果两边的亲属刚好能给对方的病人，交换一下，两个人都得救。把每一对画成一个点，能换就连一条边，两两交换就是在图上找尽量多的不相交的边，这正是最大匹配。

在一般图里找增广路，难在奇数长的圈会把搜索绕晕。1965 年 Edmonds 想出“缩花”的办法，把奇圈缩成一个点，给出了多项式时间的算法。这篇论文顺手还提了一个主张：多项式时间才算“好算法”。今天整个计算复杂性理论，包括 P 与 NP，都站在这句话上。一道匹配题，伸出去的远比匹配多。

肾脏交换真正落地是四十年后。2004 年前后，Roth、Sönmez 和 Ünver 把它设计成一个市场：两两交换用的就是匹配的结构理论，后来又加进三方循环和由无偿捐献者起头的接力链。Roth 因为这一类市场设计，2012 年和 Shapley 分享了诺贝尔经济学奖。

有意思的是，加进三方循环以后，求最优方案变成了 NP 难问题（Abraham、Blum、Sandholm，2007）。可同一篇论文就用整数规划清空了上万对的模拟交换池，而真实的池子小得多：英国的全国交换每季度配一轮，一轮约 250 对。卡住移植的是别的东西。美国 UNOS 的平台到 2015 年底找出了 2246 个配对，最后只做成 173 例移植：配型在最后一刻失败，医院把好配的病人留在自己院里换，一个三方循环要六台手术同时开。

所以，假如 OpenAI 的 120 号是对的，这是算法理论里的一件大事：一般图上最快的精确算法，从 1980 年 Micali 和 Vazirani 的 m√n 起就没怎么动过。可它对肾脏交换几乎没有可测的影响。几百个点的图，现有算法本来就是一眨眼。

此后半个多世纪，人们把“矩阵乘法指数” ω 一点点往下压，后来是在小数点后第四、第五位上抠。今年 8 月，DeepMind 和几位多年做这个问题的学者借助 AlphaEvolve 做了一轮优化，把纪录从 2.371339 推到 2.371177。不到两个月后，OpenAI 的 107 号声称一口气压到 9/4，也就是 2.25。

如果成立，这是代数复杂性理论里的地震。研究复杂性的 Lance Fortnow 在博客里写，这批结果要是都站得住，理论计算机过去 24 小时的进展超过此前三十年的总和；他也提醒，证明还没完全核实，模型拿到的题解出了不到一成。

可“更便宜的 AI”不会因此到来。Strassen 之后那一长串改进，构造常数大到天文数字，只在矩阵大得离谱时才占优，圈内管这叫“银河算法”。OpenAI 的论文自己也写明，它的证明没有给出任何有竞争力的有限矩阵规模。GPU 上跑的仍是三重循环的分块乘法，AI 变便宜靠的是芯片、低精度数和更聪明的数据搬运。连 Strassen 那个 2.807，在实际软件里也只偶尔用到。

编辑距离：精确计算基本没法比平方快，除非一个叫 SETH 的复杂性猜想是错的（Backurs 与 Indyk，2015）。这条下界本身就是理论家转去研究近似算法的理由，而“任意精度的近似、几乎线性时间”此前确实没人做到。可测序比对从来不靠精确的编辑距离，靠的是先找短的“种子”、串起来、再只在附近做比对的启发式。

随机博弈和 k-server 也是一样。它们给的是最坏情况下的保证，对手可以任意刁钻。自动驾驶的安全验证，难在把一辆车和一座城市写成模型；仓库机器人面对的订单有统计规律，没有一个专门跟它作对的对手。

那数学在整条路里占几成？看看 CT 的历史。

数学提前了五十多年就绪，后来还被重新发明了一次。在这条路上，数学的那一段几乎不花时间，它只是在旁边等。推文想象的“几个世纪压成几年”，需要数学占满整条路；可在多数应用里，数学是最先到、等得最久的那个。

说到这里，可能有人觉得我在泼冷水。不急，请出第一位评理的人。

9 月 28 日，Stephen Wolfram 写了一篇长文，问 AI 时代纯数学研究还有没有前途。他开头就说自己有点不耐烦：天天有人说数学可以全交给 AI 了，这里面对数学是什么、对 AI 是什么，都有根本的误解。

他有资格这么说。1988 年 Mathematica 出来的时候，也有人说数学要被机器做完了。结果它把符号积分这种活儿接了过去，数学家反而能做更高处的数学。

他的论证落在一个他用了几十年的词上：计算不可约。很多由简单规则生成的过程，没有捷径，只能一步步跑。数学的底层也是这样，从公理出发可以机械地推出无穷多条定理，但绝大多数是“外星数学”，跟人能理解的概念接不上。人做的数学，是在这片不可约的海里找出一个个“可约的口袋”，用有限的头脑装得下的叙述把它讲出来，就像流体力学不必追踪每一个分子。

他举了自己的例子。2000 年，他用自动定理证明找到了布尔代数最短的单条公理。

这是他心目中自动定理证明史上唯一一个说得上的新结果。可它就那样待着，没有长出别的东西。在他看来，数学要的是人能接得住的叙述，这一条至今是一个缺口。

接着他分了两种目标。一种是解题：题目早就定好，解出来就有一个干净的胜负，像体育比赛，AI 最擅长。另一种是造新概念、新结构，让一大片东西变简单、变统一。后者没法逐条定理地判断好坏，新概念还得像新词一样，在共同体里慢慢传开。目标从哪来？只能从系统外面来，也就是从我们这里来。他还注意到，AI 在数学上最像样的成果，多半出自最强的人类数学家之手：会问问题，活就干完了一大半。

最贴近这条推文的，是他文章快结尾的一段。常见的说法是，纯数学像在远处点灯塔，科学和技术总有一天会走到那里。他说真实的图景正好反过来：数学先给我们一种思考方式，有了这副眼镜，我们才知道去科学里找什么。不是数学和科学神秘地会合，而是科学因为那块数学存在，才被做了出来。

拿这个框架回头看隐身斗篷，严丝合缝。不是 Calderón 问题“预先点亮”了隐身技术，而是“换个坐标，介质就跟着变”这种看法先有了，变换光学的人才知道去找什么样的材料。

Wolfram 由此推出一个乐观的结论：成功做出来的纯数学不会彻底没用，它总对应着某种规律，迟早是某种科学的原料。只是那种科学，可能离我们今天关心的东西很远。

第二位评理的是 David Deutsch，牛津的物理学家，量子计算的奠基人之一。他 2011 年出了一本书，叫《无穷的开始》。书写在大模型之前，可里面有三样东西，正好拆这条推文。

书的第 5 章叫“抽象的实在性”，借了侯世达的一个思想实验（之前写过侯世达）。用一大片骨牌搭一台计算机，专门判断一个数是不是素数：输入是一排 641 块骨牌，网络在里面一路试除，如果找到因子，某一块输出骨牌就会倒。

推完以后，那块骨牌没倒。为什么？你可以一块一块追：因为推它的那块没倒，那块前面的也没倒……每句都对，可要说清楚“为什么偏偏是它不倒”，绕不开另一句：因为 641 是素数。

Deutsch 在这里比侯世达说得更细：逐块的物理叙述也是真的，也有用，它说明了素数性为什么会跟这堆骨牌扯上关系；但任何完整的解释里，都少不了“641 是素数”这一环。抽象不是物理的影子，它本身就在解释物理。顺带一提，641 也是当年欧拉拿来推翻费马猜想的那个数：2³²+1=641×6700417。

拿这个回答推文的开头那句“不就是数学嘛”，就清楚多了。推文急着替数学找用处，找的都是机器，好像数学得换成一台机器才算数。Deutsch 会说，数学用不着变成别的东西才有用，它本身就是我们解释世界的那一层。

书的第 1 章立了一个标准：好的解释“难以改动”，每个细节都在干活，动一处就整个塌掉。好解释还有一种性质，他叫“伸展”（reach）：它能解决远远超出当初为之而造的那些问题。

前面的故事全是伸展。Calderón 的复指数，伸到了一大片反问题里；形变带来的不唯一，伸到了隐身斗篷；Edmonds 为匹配写下的“好算法”，伸成了整个复杂性理论。更老的例子是 Hardy：1940 年他在《一个数学家的辩白》里颇为得意，说数论这种真数学打不了仗；三十七年后，RSA 把数论变成了公钥密码的地基。没有一项写在当初的“应用清单”里。

推文列的那张清单，恰好是伸展的反面：每个结果配一个最显眼、最近的用途。真正的伸展，你在当时根本列不出来。

第 9 章“乐观”里，Deutsch 沿着 Popper 区分了预测和预言。预测出自一个好的解释；预言是假装知道还不可能知道的事。未来要靠还没被创造出来的知识来塑造，而没有哪个解释能伸展到预先说出它的后继者是什么。他举的例子里有 1894 年的 Michelson：物理学剩下的发现，大概只在小数点后第六位了。不出十来年，量子论和相对论相继登场。

所以“把几个世纪压进几年”不是预测，是预言。Deutsch 提醒过，预言天然偏向悲观；可乐观的预言也是预言，一样没有根据。

可他绝不是悲观派。他在第 3 章把两句话说成要“刻在石头上”，第一句是：问题是不可避免的。第二句是我全文唯一想原样引用的一句：

问题都可以解决，只要有对的知识；而新知识又一定带来新问题。进步没有终点，所以我们永远站在“无穷的开始”。这是书名的意思。

按这个看法，“加速”指的是什么？不是定理的产量，而是解释和纠错的速度：提出猜想，拿批评去砸，留下砸不碎的。书的第 7 章谈人工智能，他认为卡住的是一个哲学问题：我们还不懂创造力是怎么回事。据报道，2025 年 9 月他和 Altman 在柏林对谈时又说，真正的智能得会自己挑问题。这和 Wolfram 的“目标从我们这里来”是同一个意思。

下面是我的推论，不是他们的原话：一个模型被交给四千道题、交回七百多篇手稿，它加速的是“猜想”这一步；“批评”这一步，现在还主要靠人读，而那七百多篇，大多还没人读完。

回到那句“好吧，那又怎样，不就是数学嘛”。我的回答有三层。

推文最后说，活在这个时代真是疯了。这一句我同意，只是理由不同。疯狂的不是那张时间表，是我们第一次有机会，让“纠错”也跟着变快。至于能不能做到，那是一个问题；按 Deutsch 的说法，问题是可以解决的。

“地基不会自己长成房子，
可没有它，你连该盖什么都想不到。

The tweet has a simple structure. First it voices your dismissal for you: OK, so what? It’s just math. Then it lays out ten lines, each with a mathematical term, an arrow and a real-world payoff. It closes with the thought that speeding up mathematical discovery might compress centuries of scientific progress into a few years: what a crazy time to be alive.

The ten terms weren’t made up. I checked them against the repository OpenAI released on October 6 (I wrote about it before): all ten are there, numbered 104, 107, 110, 120, 121, 267, 362, 365, 366 and 372. Out of 372 results, the tweet picked exactly the ones whose names sound most “useful.”

I like the tweet’s enthusiasm, and I agree with half of its conclusion: mathematics is the foundation of science. But the “foundation” metaphor gives the game away, because a foundation doesn’t grow into a house by itself. How long the arrow from a theorem to a hospital bed is, which way it points, what it carries inside: on all of this the tweet says not a word.

This piece does one thing only: it takes the arrows apart. First, a boundary. I won’t judge whether the ten results are right; for now they are all just OpenAI’s claims. When I say “if it’s right” below, it is to look at the arrow, not to vouch for anyone.

Start by asking where each problem came from. The answer is surprisingly consistent: mostly, a real-world headache came first, and mathematicians then distilled the headache into a problem.

Calderón’s short 1980 paper says at the very start that the problem comes from electrical prospecting. As Uhlmann recounts from Calderón’s recollections late in life, in the 1940s he was an engineer at Argentina’s state oil company, puzzling over how to infer what lies underground from electrical measurements at the surface. He carried the idea around for more than thirty years before writing it down: if you measure voltage and current only on the surface of an object, can you uniquely determine the conductivity inside?

Mumford–Shah comes from computer vision. In 1989 the two authors wanted a functional that would cut an image into a few smooth regions, with the cuts as short as possible. k-server comes from caching in operating systems: memory pages being swapped in and out, abstracted as k cars taking orders around a space. Edit distance was defined by Levenshtein in 1965 while he was studying error-correcting codes. The Vlasov equation was written down for plasmas in 1938.

Matrix multiplication has the best story. In 1969 Strassen set out to prove that the n³ of Gaussian elimination was already optimal, and instead turned up a faster method.

So the tweet draws “theorem → application,” while history more often runs “application → problem → theorem,” and only then “perhaps, a better application.” The arrow often starts close to where the tweet says it ends.

And here is the part that stings: most of the applications the tweet says “may eventually be possible” already exist. Intensive care units monitor lung ventilation with electrical impedance tomography; liver clinics measure tissue stiffness with elastography; kidney paired exchange has been running for twenty years; Bose–Einstein condensates were made in the lab back in 1995; sequence alignment runs every day; and GPUs multiply matrices every second.

The real question is not “will this application appear?” but “will this new theorem make this application better?” I put each of the ten to that question:

Read all ten rows and not one of them says “theorem out, machine in.” A few, such as Vlasov–Maxwell and Bose–Einstein condensation, would be once-in-decades events in mathematical physics if they hold. But what they answer is whether the equations stand up mathematically; on the engineering side, the equations have been in use for a long time.

None of this means math is useless. Quite the opposite: let’s take one problem and see what math looks like when it really is “useful.”

Take the line in the tweet that sounds most like a medical ad: the Calderón problem leads to portable body scanners.

The setup is plain. Let the conductivity inside an object be γ(x). Apply a voltage distribution f on the surface; the potential u inside satisfies ∇·(γ∇ u)=0, and you measure the current flowing out through the surface. Bundle up every pairing of “voltage applied, current measured” and you get the Dirichlet-to-Neumann map, written Λ_γ. Calderón asked: does Λ_γ uniquely determine γ?

First, a piece of intuition. When you apply a voltage f on the surface, the electrical power dissipated inside is Q_γ(f)=∫γ|∇ u|², and this is exactly the quantity you measure at the surface. Current always takes the path that costs the least energy (Dirichlet’s principle), so if you change γ slightly by some h, the first-order change in power is just ∫ h|∇ u|²; the change in u itself plays no part at first order.

The magic of this trick is in ζ: the real part makes each function grow exponentially, the imaginary part makes it oscillate, and together the product comes out as a pure plane wave. Solutions of this kind later came to be called “complex geometrical optics solutions,” and in 1987 Sylvester and Uhlmann used a strengthened version of them to prove full uniqueness for smooth conductivities in three or more dimensions.

At this point it may look as if only engineering stands between us and a portable scanner. It doesn’t.

Take an example we can compute all the way through. In the unit disc, let the conductivity be k inside a central disc of radius ρ and 1 outside it. Apply the voltage e^inθ on the boundary, which rises and falls n times as you go around the circle; I’ll call it channel n.

Plug in numbers and the trouble shows. Take an inclusion of half the radius (ρ=0.5) with twice the conductivity (μ=1/3): in channel 1 it shifts the reading by 18%, in channel 5 by only three parts in a thousand, in channel 10 by six parts in a million. The higher the channel, the finer the detail it sees, but the signal decays exponentially, like ρ²ⁿ.

This is not a quirk of the disc. Alessandrini proved in 1988 that, in general, the conductivity depends on the boundary data only with logarithmic stability; in 2001 Mandache proved that logarithmic is the best there is and cannot be improved. In plain terms: to sharpen the image by one notch, you must improve the measurement precision not by one notch but exponentially.

So the blur in impedance images isn’t the engineers slacking off; it is a theorem. The most useful mathematics about this scanner turns out to be a “can’t be done.” It tells you not to chase high-definition anatomical images and to do something else: for example, look only at how ventilation in the lungs changes over time, or tie electrical measurements to other physical quantities, as in ultrasound or MRI. The lung impedance imaging that has made it into today’s ICUs took the first of these roads.

Real tissue is anisotropic. Muscle, for instance, conducts better along its fibers, so the conductivity has to be written as a matrix. And here there is an obstacle you cannot get around.

So in the anisotropic case, the conductivity can at best be determined “up to such a deformation.” Conversely, whether “up to a deformation” is the only ambiguity in three or more dimensions has been open ever since Lee and Uhlmann settled the analytic case in 1989; a preprint announcing a solution appeared as recently as 2024, and was later withdrawn by its own authors. Entry 365 in the repository claims precisely this, in the smooth case.

The story could have ended there, but in 2003 Greenleaf, Lassas and Uhlmann pushed this defect to the extreme. They chose a singular F that blows a point up into a ball, for instance F(x)=(1+|x|/2) x/|x|. The pushed-forward conductivity is extremely anisotropic in the shell, the current obediently flows around, and whatever you put inside the ball cannot be detected from the boundary.

A “non-uniqueness” in medical imaging became the mathematics of the invisibility cloak. Three years later, Pendry and colleagues applied the same change-of-variables idea to electromagnetic waves in Science; this line of work came to be called “transformation optics,” and a cloaking experiment at microwave frequencies followed the same year.

The tweet says the Calderón problem leads to cheap scanners. Historically, it led first to “scanners are doomed to be blurry,” and then to the invisibility cloak. I don’t believe anyone in 1980 could have predicted that step. That “could not have predicted” will come back later.

Calderón’s story shows that arrows can bend. Several of the others show that even when an arrow runs straight, the math is often not the stretch that matters most.

A patient needs a new kidney, and a relative is willing to donate, but the two are incompatible. Another pair is in the same situation. If each relative happens to be able to give to the other pair’s patient, they swap, and both patients are saved. Draw each pair as a vertex and join two vertices by an edge when they can swap; two-way swaps then mean finding as many disjoint edges in the graph as possible, which is exactly maximum matching.

In a general graph, the difficulty in finding augmenting paths is that odd cycles send the search in circles. In 1965 Edmonds came up with “blossom shrinking,” contracting an odd cycle to a single vertex, and obtained a polynomial-time algorithm. In passing, the same paper put forward a thesis: only polynomial-time algorithms count as “good algorithms.” All of today’s computational complexity theory, P versus NP included, stands on that sentence. A matching problem reached far beyond matching.

Kidney exchange really got off the ground forty years later. Around 2004, Roth, Sönmez and Ünver designed it as a market. Two-way swaps used the structure theory of matchings; later came three-way cycles and chains started by altruistic donors. For this kind of market design, Roth shared the 2012 Nobel Prize in Economics with Shapley.

Interestingly, once three-way cycles are allowed, finding the optimal plan becomes NP-hard (Abraham, Blum and Sandholm, 2007). Yet the same paper used integer programming to clear simulated pools of ten thousand pairs, and real pools are much smaller: the UK’s national scheme runs a matching round each quarter, with about 250 pairs per round. What holds transplants back is something else. By the end of 2015 the US UNOS platform had identified 2,246 matches, which led to only 173 transplants: crossmatches failed at the last minute, hospitals kept their easy-to-match patients for swaps within their own walls, and a three-way cycle needs six operations to run at the same time.

So if OpenAI’s entry 120 is right, it is big news in algorithm theory: the fastest exact algorithm for general graphs has barely moved since Micali and Vazirani’s m√n in 1980. But it would have almost no measurable effect on kidney exchange. On a graph with a few hundred vertices, existing algorithms already finish in the blink of an eye.

For more than half a century since, people have pushed the “matrix multiplication exponent” ω down bit by bit, until they were scraping at the fourth and fifth decimal places. This August, DeepMind and a few researchers who have worked on the problem for years ran a round of optimization with AlphaEvolve and moved the record from 2.371339 to 2.371177. Less than two months later, OpenAI’s entry 107 claimed to have pushed it in one go down to 9/4, that is, 2.25.

If it holds, it is an earthquake in algebraic complexity theory. The complexity theorist Lance Fortnow wrote on his blog that if these results all stand, theoretical computer science made more progress in the past 24 hours than in the previous thirty years combined; he also cautioned that the proofs have not been fully checked, and that the model solved fewer than one in ten of the problems it was given.

But “cheaper AI” won’t follow. The long line of improvements after Strassen all carry astronomically large constants and only pay off for absurdly large matrices; people in the field call them “galactic algorithms.” OpenAI’s paper itself states that its proof gives no competitive finite matrix size. GPUs still run triple-loop blocked multiplication, and AI gets cheaper thanks to chips, low-precision numbers and smarter data movement. Even Strassen’s 2.807 is used only occasionally in real software.

Edit distance: computing it exactly essentially cannot be done faster than quadratic time, unless a complexity conjecture called SETH is false (Backurs and Indyk, 2015). That lower bound is itself the reason theorists turned to approximation algorithms, and “approximation to any precision in almost-linear time” really had not been achieved before. But sequence alignment has never relied on exact edit distance. It relies on heuristics that first find short “seeds,” chain them together and then align only in their neighborhood.

Stochastic games and k-server are the same story. They give worst-case guarantees, against an adversary who can be as devious as it likes. The hard part of verifying a self-driving car’s safety is writing the car and a city down as a model; the orders a warehouse robot faces have statistical regularities, and there is no adversary out to get it.

So what share of the whole path does math take? Look at the history of CT.

The math was ready more than fifty years ahead of time, and was even reinvented once along the way. On this path, the math stretch took almost no time; it just waited on the side. The tweet’s vision of “centuries compressed into years” needs math to fill the whole path, but in most applications math is the first to arrive and the one that waits the longest.

By now some readers may feel I’m pouring cold water on everything. Bear with me: let me bring in the first referee.

On September 28, Stephen Wolfram published a long essay asking whether pure mathematics research has a future in the age of AI. He says right at the start that he is a little impatient: every day someone declares that math can be handed over entirely to AI, and behind this lies a fundamental misunderstanding both of what mathematics is and of what AI is.

He has earned the right to say so. When Mathematica came out in 1988, people also said machines were about to finish off mathematics. Instead it took over chores such as symbolic integration, and mathematicians were freed to do mathematics at a higher level.

His argument rests on a term he has used for decades: computational irreducibility. Many processes generated by simple rules have no shortcut; you can only run them step by step. Mathematics is like this at bottom too. From the axioms you can mechanically derive infinitely many theorems, but the vast majority of them are “alien mathematics” that connect to no concept a human can understand. Human mathematics is the business of finding “pockets of reducibility” in this irreducible sea and telling them in narratives a finite mind can hold, much as fluid dynamics need not track every molecule.

He gives an example of his own. In 2000 he used automated theorem proving to find the shortest single axiom for Boolean algebra.

He regards it as the only new result worth mentioning in the whole history of automated theorem proving. Yet there it sits, and nothing else has grown out of it. In his view, mathematics needs narratives that humans can take hold of, and for this theorem that is still a gap.

Next he separates two kinds of goals. One is solving problems: the problem is fixed in advance, and solving it gives a clean win or loss, like a sport, which is what AI is best at. The other is creating new concepts and new structures that make a whole swath of things simpler and more unified. The latter can’t be judged theorem by theorem, and a new concept, like a new word, has to spread slowly through a community. Where do the goals come from? Only from outside the system, which is to say from us. He also notes that AI’s most respectable results in mathematics have mostly come from the hands of the strongest human mathematicians: knowing what to ask is more than half the work.

The passage closest to this tweet comes near the end of his essay. The usual picture is that pure mathematics lights lighthouses in the distance, and that science and technology will one day reach them. He says the real picture is the reverse: mathematics first gives us a way of thinking, and only with those glasses on do we know what to look for in science. It is not that mathematics and science mysteriously meet; the science gets done because that piece of mathematics exists.

Look back at the invisibility cloak with this frame, and everything fits. It wasn’t that the Calderón problem “lit the way in advance” for cloaking technology. Rather, the view that “change coordinates and the medium changes with them” came first, and that is how the people in transformation optics knew what kind of material to look for.

From this Wolfram draws an optimistic conclusion: pure mathematics that has been successfully done is never entirely useless. It always corresponds to some regularity, and sooner or later it becomes raw material for some science. It’s just that the science may be far from anything we care about today.

The second referee is David Deutsch, the Oxford physicist and one of the founders of quantum computing. In 2011 he published a book called “The Beginning of Infinity.” It was written before large language models, yet three things in it take this tweet apart neatly.

Chapter 5 of the book, “The Reality of Abstractions,” borrows a thought experiment from Douglas Hofstadter (I’ve written about Hofstadter before). Build a computer out of a great array of dominoes, designed to decide whether a number is prime. The input is a row of 641 dominoes; inside, the network tries one divisor after another, and if it finds a factor, a particular output domino falls.

After the push, that domino is still standing. Why? You can trace it domino by domino: because the one that would have pushed it didn’t fall, and the one before that didn’t fall either… Every sentence is true, but to explain “why this one in particular stays up,” you can’t avoid another sentence: because 641 is prime.

Here Deutsch is more careful than Hofstadter. The domino-by-domino physical account is also true and also useful: it explains how primality comes to have anything to do with this pile of dominoes. But no complete explanation can do without the link “641 is prime.” Abstractions are not shadows of the physical; they themselves explain the physical. Incidentally, 641 is also the number Euler used to refute Fermat’s conjecture: 2³²+1=641×6700417.

With this in hand, the tweet’s opening line, “it’s just math,” is much easier to answer. The tweet is in a hurry to find uses for math, and the uses it finds are all machines, as if math only counts once it has been turned into a machine. Deutsch would say that mathematics doesn’t have to become something else to be useful: it is itself the layer at which we explain the world.

Chapter 1 of the book sets a standard: good explanations are “hard to vary.” Every detail does work, and changing any one of them makes the whole thing collapse. Good explanations also have another property, which he calls “reach”: they solve problems far beyond the ones they were originally made for.

Every story so far has been about reach. Calderón’s complex exponentials reached into a whole swath of inverse problems; the non-uniqueness that comes from deformations reached all the way to invisibility cloaks; the “good algorithm” Edmonds wrote down for matching grew into the whole of complexity theory. An older example is Hardy, who in 1940, in “A Mathematician’s Apology,” noted with some satisfaction that real mathematics such as number theory could not be used to wage war; thirty-seven years later, RSA made number theory the foundation of public-key cryptography. None of these was on any “list of applications” at the time.

The list in the tweet is exactly the opposite of reach: each result paired with its most conspicuous, nearest use. Real reach is something you cannot list at the time.

In chapter 9, “Optimism,” Deutsch, following Popper, distinguishes prediction from prophecy. A prediction comes out of a good explanation; prophecy is pretending to know what cannot yet be known. The future will be shaped by knowledge that has not yet been created, and no explanation can reach far enough to say in advance what its successors will be. One of his examples is Michelson in 1894, who thought the remaining discoveries in physics would probably lie “in the sixth place of decimals.” Within a decade or so, quantum theory and relativity had arrived one after the other.

So “compressing centuries into years” is not a prediction but a prophecy. Deutsch points out that prophecy is naturally biased toward pessimism; but an optimistic prophecy is still a prophecy, and just as groundless.

Yet he is anything but a pessimist. In chapter 3 he singles out two statements that deserve to be “carved in stone.” The first is: problems are inevitable. The second is the one sentence in this whole essay I want to quote exactly as written:

Problems are soluble, given the right knowledge; and new knowledge always brings new problems. Progress has no end, so we are always at “the beginning of infinity.” That is what the title means.

On this view, what does “acceleration” even mean? Not the output of theorems, but the speed of explanation and error correction: propose conjectures, throw criticism at them, keep what doesn’t shatter. Chapter 7 of the book is about artificial intelligence, and there he argues that what holds it back is a philosophical problem: we don’t yet understand how creativity works. In a conversation with Altman in Berlin in September 2025, he reportedly said again that real intelligence has to be able to choose its own problems. This is the same point as Wolfram’s “the goals come from us.”

What follows is my own inference, not their words. A model handed four thousand problems that hands back seven hundred-odd manuscripts is speeding up the “conjecture” step. The “criticism” step still depends mainly on people reading, and most of those seven hundred-odd manuscripts have yet to be read through by anyone.

Back to that line: “OK, so what? It’s just math.” My answer comes in three parts.

The tweet ends by saying what a crazy time this is to be alive. That I agree with, though for a different reason. What is crazy is not the timeline but that, for the first time, we have a chance to make “error correction” faster too. Whether we can do it is a problem; and, as Deutsch would have it, problems are soluble.

“A foundation won’t grow into a house by itself,
but without one, you can’t even imagine what to build.