Terry Tao — New Mathematical Workflows in the Age of AI

Keynote at Stanford Conference


Introduction

Jared (moderator): We're very pleased to have as our keynote speaker Terry Tao, who is professor of math at UCLA, also director of special projects at IPAM, the Institute for Pure and Applied Mathematics.

Terry told me an anecdote about how at a similar conference at IPAM a few months ago, a lot of these kinds of topics were really bubbling up, and it's really very timely to have this conference here at Stanford. Terry also said that there was an IPAM conference in 2021 where he observed that a lot of these trends were really starting to come together, and I think he was doing a great service as leadership in mathematics for trying to call an alarm to a lot of the progress we're now maybe starting to see happening.

Terry obviously won the Fields Medal in 2006 for a wide range of contributions across number theory, combinatorics, PDEs, and analysis. But today he's going to be speaking to us about maybe new mathematical workflows that we might start to have to think about in the coming years. So without further ado — Terry.


The Talk

Thanks, Jared. It's great to be here. I'm sorry I couldn't be here yesterday but I still have to teach and meet my students and I couldn't get away.

So I'll be talking about how I think math is going to change, and maybe my talk will be at a bigger scale than many of the other talks here. The current state of the art with AI-assisted mathematics is kind of at the level of solving an individual problem, or maybe an open conjecture, and possibly writing a single paper. But mathematics is not just a union of disjoint theorems and disjoint papers — there's a whole system on top of it. I think we have to start thinking about the broader system, and possibly deprioritizing the optimization at the problem level, because that is actually beginning to conflict with optimization at the system level.

Mathematics Has Not Changed Much in Centuries

Mathematics as a whole has not changed very much in centuries. If you go back 100 years, 200 years, and you go to a math conference — maybe it would be in German or French, and there wouldn't be PowerPoint or Beamer — but in many ways the way we do math hasn't changed that much, whereas other sciences have begun to transform.

There are many ways in which other sciences have transformed in recent decades, even before AI. There have been other revolutions. In science you have "big science" now where you have multiple collaborations. One thing you can see is that in the other sciences, multi-author papers where not just two or three co-authors but 10 or 50 are becoming much more common. Mathematics has stayed more or less at one or two co-authors for decades.

Another change in other sciences is the data explosion. There are many fields of science that were in an era of data scarcity where it was hard to get data, but now they've entered an era of data abundance where they're flooded with data. Genetics is one good example — gene sequencing has been completely revolutionized.

I think in math we are now entering a similar era. For millennia we've been in an era of proof scarcity, where proofs of problems were hard to find. We're entering an era of proof abundance, where not everything can be proved, but the ability to generate proofs has much outpaced the rest of mathematics. And we have to adapt to this.

Traditional Mathematical Collaboration

Traditionally, the way math works is: we have a small number of people working together, often at a blackboard. We still meet in person a lot. We can do some things by Zoom and email, but it's mostly in-person collaboration. We still use a lot of pen and paper. We need everyone to be an expert, PhD-level in math. Everyone reviews everyone else's work, and because of this we need a high level of trust between collaborators.

Particularly since proofs are only as strong as the weakest link — if you have one unreliable collaborator that screws up one key step in your proof and no one else reviews it, the entire proof collapses. Other sciences have a bit more robustness; if one data point is off by a little bit, it's not a big problem. But in math, we don't structure arguments to have that level of robustness. At least in pure math — applied math maybe has certain types of things where you can have some numerical errors.

Explicit vs. Implicit Goals

There's a distinction that we haven't needed to make before, but is now becoming extremely important: projects have goals, but there are actually two types of goals.

Explicit goals are the goals we say we want — we want to prove this theorem, solve this conjecture, answer this question.

But there are also implicit goals that attach to the explicit goal of a project, which we haven't needed to enunciate before, because humans who solve the explicit goal tend to automatically solve these implicit goals as well. But AIs are not necessarily doing this, and this is becoming an important point.

If you and your collaborator say "I want to prove this conjecture" — that's the explicit goal. But while you're doing that, you're also picking up various implicit goals:

  • How does this proof connect to past literature?
  • What are the natural follow-up questions?
  • What new techniques are being developed, and how useful will they be for other questions?
  • What are the key difficulties, and which technique deals with which difficulty?
  • What is the story? What is the narrative? Is there a high-level overview?
  • And last but not least — one of the major implicit goals in a research project is to train the authors themselves to get better at solving problems, and not just the authors, but people who read the paper.

We haven't needed to state these goals because naturally, if humans try to solve a problem, they will record the pain points, cite past literature, and learn from both the successes and failures of their project.

The Danger of Decoupled Goals

There is now this danger — and I think it's already beginning to happen — that AI tools might decouple these goals from each other. We are just beginning to see AI solutions which are technically solving an explicit goal, but they are not hitting the implicit goals which we were expecting a human-generated solution to create.

Maybe they will generate a proof of a conjecture and it will even be verified in Lean, but:

  • They don't cite where their influences come from — they take ideas from papers but don't cite the paper.
  • The proofs, while technically correct, spend a lot of time on routine steps, and the parts that are new and interesting are just tucked away in one subsection.
  • They don't suggest insight as to what was the key new idea or what new questions can be studied.
  • They don't train any human to become better at solving this task.

Now, some of these defects can be rectified by prompting the AI better. But this is not something we've had to focus on. Many solution attempts are just happy to get the solution and then maybe a Lean-verified check mark as a bonus, and then they quit.

We're going to enter an era where there'll be a problem people care about, and there'll be an AI-generated solution, and nobody can give a talk on it. There'll be no human that understands the proof well enough to give a talk and take questions. You may have a very unsatisfactory situation where a problem has been solved but the field as a whole does not progress, because we cannot use the proof.

Peer Review Under Pressure

Traditionally we have peer review. Human authors also sometimes miss the implicit goals — there are human-written papers in the literature which solve a problem but do not necessarily do the best job of explaining key ideas or training the next generation. But we send them to referees, and the referees can, to some extent, point out these issues and partially correct them. Over time there are follow-up papers, books, and other exposition, and there's a process which I call proof digestion, where after the proof is first made, it is simplified and the main ideas are extracted to the point where eventually you can teach it in some graduate class.

But the volume of AI-joint papers is such that human referees cannot handle all this task anymore, except for maybe the most important results. The vast majority of this output cannot be refereed this way.

So we have to turn to automated methods. Formal proof verification will at least weed out incorrect proofs. But just being correct is only one of the implicit goals that we want. We also want the proof to be understandable, to suggest further directions. Formal verification would at least relieve some of the duty of a referee — line-by-line checking of correctness, maybe we can outsource to Lean or whatever. But referees also assess importance and connection to literature, and still the volume is such that this is not enough.

You can say, "Let's use other AI graders," but reward hacking in particular is a major problem. You cannot have this as your primary line of defense — it can best be an additional filter.

The Automobile Analogy

The analogy I've been giving recently is that the AI technology is like the invention of the automobile. We have now much faster means of transportation, but our infrastructure — our journals, our classes, our textbooks, where we train students, our referee system — is from the 19th century. It's from the streets before the automobile.

You can build faster cars, more energy efficient, carry more people, and somehow traffic does not get better. In fact, it gets worse. The total capacity of your transmission network may actually decrease if you just keep making the car technology better.

Optimizing the atomic transportation problem — a single person trying to get from A to B — does not optimize the global problem of how to have a population solve their transportation needs as efficiently as possible.

What we need is new infrastructure. We need ways to design a mathematical system as a whole that can accommodate these new technologies. You still also need pedestrian walkways — cars are wonderful but you don't want them everywhere. There are no cars in this room, and for good reason. You want a clear subdivision of what parts of mathematics will have unrestricted AI input, which parts will have some AI input, and which parts are pedestrian only. Until we do that, having better and faster AIs and producing more doesn't help after a certain point.

Polymath Projects: A Precedent

We do have the Polymath projects, which come from the ancient era of the early 21st century — pre-AI, or pre-modern AI. We were able to solve some types of problems by massive (by mathematical standards, meaning 12 or 20 people) online collaboration.

There were about 15 of these projects. They were run mostly through blogs and wikis — 2000s-era internet. They could solve a couple of open problems, but more typically they could take an existing proof and optimize it somehow — get a better proof, maybe improve some bounds, and enrich it by highlighting more connections to other fields.

They didn't excel at depth — really uncovering incredibly new insights, the type of thing where someone works in an attic for seven years. But they excelled at breadth. Being open, you could have dozens of experts from different areas come in and make a comment. When you collaborate with just three people, you have access to the expertise of those three people, but with these projects, at some point someone would realize "I need some lemma from optimization theory" and there's a good chance somebody would say "I recognize this — there's a connection."

There are parallels to how modern AI excels at breadth — they're trained on the entire internet, and that is one of their superpowers.

These Polymath projects sometimes evolved: they would start with a chaotic phase with hundreds of people commenting and trying all kinds of directions. Most directions get pruned out, there'd be some one path that looks promising, and of the hundreds of people, maybe only five or six were interested in pursuing it. Often these projects collapsed — like a quantum wave function collapse — to a traditional collaboration involving just three or four people. But the value of the Polymath project was identifying the right approach and then collecting the correct set of co-authors.

Also, these were one of the few projects open enough that graduate students could actually get insight into what the actual problem-solving process was. When you see a talk on a mathematical achievement, often it's a very polished success story — they don't show you the dead ends. But because everything was done openly, we actually saw that, and that was another value of these projects.

However, there's a reason why these projects petered out — they don't scale. Someone has to handle the hundreds of comments, moderate them, gently persuade people with incorrect answers, and check all the contributions. This is all done by hand. Someone basically has a full-time job running these things. Also, the technology of the early 2000s — blogs and wikis without GitHub, without Lean, without basic version control — everything was done by text comments passed back and forth.

Polymath 8: A Case Study

The most famous example is Polymath 8. Zhang famously proved that there are bounded gaps between primes — you can find infinitely many primes that differ by a bounded amount. The bound he got was 70 million. But it was obvious, and Zhang remarked, that there was nothing special about 70 million — this was just what his proof gave, and he didn't bother to optimize it. But it was a very tempting target to optimize.

Initially individual authors would say "I can get 60 million, I can get 50 million," but then it was crowdsourced together, and after about a year, the bound is now 246.

This was successful because:

  • There was an obvious goal and a clear metric — appealing to people who work in AI.
  • It was modular — you could break it into pieces, and people didn't have to understand the whole project.
  • Partial progress was okay — improving 70 million to 3 million but not to 2 million still counts.
  • It was suitable for crowdsourcing because there were just too many things to try.

Modern Formalization Projects

Polymath projects have become obsolete, but there are modern versions. Formalization projects have a very similar modular scheme — you want to formalize a big theorem, break it into small pieces, people can claim individual pieces and formalize them. Now we have GitHub, Lean, and continuous integration. The verification part can be automated, and we can decentralize it.

We now use modern project management — we actually have tasks that we can assign. It's much more organized than blog comments and someone manually keeping track of who's doing what.

We're beginning to use AI for small components of these projects. If you break up a big theorem into a lot of lemmas, people can take a single lemma and formalize it by hand or give it to an AI. Sometimes the AI will report the result can't be proven because of a counterexample, and it's because the statement was formalized incorrectly, and then you have to discuss with the community how to fix it. It can't be fully automated because sometimes there are issues that require human attention.

Where we're struggling is that the technology has outpaced the infrastructure. We now have the capability to take an entire paper and feed it to an autonomous agent that will try to break it up and formalize things. But when they do that, even if they succeed technically, it is a challenge to integrate that with an existing formalization project. The agent may break things up differently, the style might be different, they may prove the same statement over and over instead of having a single unified abstract lemma. Current auto-formalization technologies do not adhere to best formalization practices — they're trained mostly on getting the code to compile, which is the base condition, but these other implicit goals we have not trained these AIs on properly.

And the infrastructure — chat forums, GitHubs — is optimized for human use. If an AI runs into an issue, it doesn't post a question on the Zulip, wait for humans to respond, and then go fix it. Right now, the collaborative human workflow and the autonomous AI workflow are almost disjoint. They can only be glued together at micro-scale levels where one person claims one subtask, works privately with an AI, and then comes back to talk to the group.

"Merely True" vs. Multi-Objective Formalization

We may have to distinguish two types of formalization tasks:

"Merely true" formalization — where the only goal is to verify a theorem and not care about how ugly the proof is, how reusable the code is, how elegant or understandable. The only thing is verification and nothing else. If there are no other implicit goals and we just have the explicit goal, then current AI tools are suitable. You can dump these things into any AI because you just want that one check mark.

Multi-objective formalization — where in addition to formalizing something, you want the code to be elegant, readable, reusable, integrated with other code, and lots of other implicit goals. There, we can't use AI beyond a certain point at this stage. We have to keep the AIs limited to solving extremely well-scoped subtasks and humans have to do the orchestration. Maybe in the future that will change, but at this point we have to make this distinction.

The Incentive Gap

Even making this distinction creates a problem — an incentive gap. Suppose there's a major result you want proven, like the classification of finite simple groups. Suppose an auto-formalized effort just digests all the papers and spits out a massive one-million-line repository which proves the classification in Lean, but with completely spaghetti code — no explanation, nothing. The only thing you learn is that the classification is true.

Fine, that's in some sense better than not having it. But if you also want a canonical formalized proof — where things are very structured, you're identifying key steps, making it modular, providing simplified proofs — suddenly the incentive goes away. Our whole math social system rewards being the first to do something. Now you're no longer the first to formalize this project. You get far fewer volunteers because "why bother — it's already been done."

There's actually this paradox that getting better at solving an explicit goal may actually be detrimental to the broader goals. People may not want to do the remaining work because the explicit goal was what generated the incentive, and if that's gone, there's no longer as much incentive to do everything else.

Or even if people do start working on formalizing things properly, there's a big temptation to just grab pieces of code from the messy formalization and not take the effort to polish as much as you would if you had handcrafted all the code yourself. So there's this trade-off between speed and quality which will become increasingly urgent to address.

Proof Generation, Verification, and Digestion

We're seeing this in problem solving as well. When you solve a problem in mathematics, there are really three stages:

  1. Proof generation — finding a complete proof.
  2. Proof verification — making sure the proof has no errors.
  3. Proof digestion — understanding the main ideas, how it connects to past literature, the narrative, how you would have come up with the proof yourself, and what future questions can now be answered.

Until about a year ago, all three steps were hard and humans did the bulk of all three. Because they had roughly equal difficulty, it was okay to mostly focus on proof generation. If you invest several months generating the proof, you have probably also generated enough effort to verify and digest it.

But what's happening now is that the first two components are becoming more automated and much faster, while the third component has not budged. We are now experiencing for the first time "proof indigestion" — we are generating a lot of proofs and even verifying them, but the solution is not finished because no one understands the proof well enough to give talks about it, explain to others, or learn from it. These are only two-thirds of a proof.

The correct metric is not so much whether the proof has been generated or verified, but whether someone can give a talk about it and take questions from the audience. Current AI-generated solutions only do two-thirds of this task.

The Erdős Problems: A Case Study in Real Time

A laboratory where this is playing out in real time is the Erdős problems website — a database of problems in fields amenable to AI methods, with various degrees of difficulty, where you can see progress improve quite visibly over time.

One reason you're seeing a lot more progress on Erdős problems than other open problems is that the website has a forum where humans discuss the problems, and the forum has an AI policy that welcomes certain types of AI contributions. Other problem forums, like MathOverflow, have much more restrictive AI policies — more "pedestrian only" zones with very limited AI use. Because of that, you're not seeing much AI contribution to those sites. On the other hand, they're also not experiencing the traffic congestion problems that the Erdős site is now experiencing. There's a trade-off.

There are about a thousand Erdős problems. Back in September, about 380 were solved. There was a chaotic period in early 2026 where there was a flood of both human and AI solutions — about 50 problems got solved by various means. Then it plateaued — all the easy problems had now been looked at by multiple AIs and multiple humans. Just in the last month or so it has picked up again — GPT-5.5 being released was a big factor. But there's still a purple line of 600–700 unsolved questions, which vary widely in difficulty.

AI has become useful in many ways: literature search, verifying or formalizing existing proofs, refactoring and condensing proofs, optimizing constants, generating variants of existing papers, numerical exploration, and now more frequently generating semi-autonomous or fully autonomous partial or full solutions.

But we're getting this impedance mismatch. We're getting comments like this (a very typical one currently):

"After using GPT-5 many many times I've solved this problem and I'm getting this bound. This draft has passed several AI-based checks but I do not have time to verify every detail of the proof carefully; therefore I'm posting it here and would be very grateful for any comments and checks."

There's the incentive gap — this person plus GPT has claimed the incentive for the problem. The follow-up work of cleaning up and verifying is "someone else's problem." Until very recently the frequency was low enough that volunteers would donate an hour of their time. But currently there's a backlog of about 20 of these, all saying "I have no time to check or explain this."

We have proof indigestion.

And the proofs are often kind of frustrating to read. For example, there's a very nice solution by Liam Price and GPT of problem 11196 — a GPT-generated proof about 10 pages long. It's correct, but one of the key lemmas is in fact exactly Mertens's theorem — but it never mentions this, it just says "here's a theorem, here's a proof." In a human-written paper it says "by Mertens's theorem this is true" and just moves on. The way it's presented, you get the impression this is a core component of the proof, when it's just one tiny ingredient. Basic human exposition traits — emphasis on the most important parts, deemphasis on the less important parts — you often don't see in first-generation AI-generated proofs.

You can feed these proofs into other AIs and say "please improve the exposition" — that helps a little. But because of the incentive gap, the incentive is often just to rush out the first proof and not do this cleaning.

There's now for the first time a traffic jam on the Erdős problem website. There's a wiki page tracking AI contributions to these problems, and the "pending assessment" section used to have one or two entries — it currently has 20.

You can put some filters in — require a Lean certificate before we look at an AI-generated solution. That would help, but even that is only a partial solution. Eventually we'll have a flood of formalized AI-generated proofs that still need to be digested.

Redefining What a Solution Is

Until recently we've only focused on proof generation and verification as our two main steps. We now have to realize that even when a proof is verified, that is not the final stage. Proof digestion is the important third stage. It used to happen organically when the first two stages were produced by humans. Now we have to make it explicit, value it, and really redefine what a solution is — and change the incentive structure.

As Bill Thurston wrote:

"We are not trying to meet some abstract production quota of definitions and proofs. The measure of success is whether what we do enables people to think and understand more clearly and effectively about mathematics."

Building Freeways: New Kinds of Mathematics

Maybe we just accept that traditional mathematics is rate-limited and there's only so much AI assistance it can absorb. But there are other ways to do mathematics that were not possible before, which can scale, and maybe we should be experimenting with these.

The Equational Theories Project

This is a project I started two years ago, wondering whether you could automatically prove millions of micro-theorems by a crowdsourcing project. I picked a very basic topic and tried to make it fit the same criteria that make a good Polymath project — modular, good benchmark, and so on.

I generated a list of 22 million questions in universal algebra. I generated laws of algebra — the commutative law, the associative law, and 4,000 other laws — and asked which ones imply which other ones. For example: does every binary operation which is commutative automatically become associative? (No — you can write down a law that is one but not the other.) But you ask 22 million questions like this.

Any given one, a grad student in algebra could sit and for most of them, working for an hour with pen and paper, could decide whether it's true or false. But I don't have 22 million grad students.

Within three months we settled all these questions. About 95% could be done automatically using traditional automated theorem provers (not modern AI). Then 99% by various methods. But there was a holdout set of about 100 really hard problems which needed humans. It all got formalized in Lean.

It was a very good crowdsourceable project — there was a dashboard where you could see how many implications were still open, going down over time. People could claim one cluster and work on it, very decentralized. Someone would have a human proof, someone else would convert it to Lean, someone else would automate it and scan the other 22 million implications.

Now, if you plug any of these questions into GPT, frontier models can solve 99.9% of them and even give Lean proofs — but they think for 30 minutes for each question, and you have 22 million questions. In principle a large tech company could replicate the entire project, but at incredible expense. You should not use frontier models as your first line of defense. Use the cheapest tools first — automated theorem provers from the 1990s — to clear out the low-hanging fruit, then move up the tier, and save your most expensive resources (human experts and frontier AI) for the most filtered, curated set of hard problems.

The Distillation Challenge

Once I had this dataset of 22 million algebra questions, it became a great problem set for other purposes. If you take an open-source model like DeepSeek-Qwen and give it one of these problems — never mind a proof, just ask "is it true or false?" — the success rate is 55%, barely better than random chance.

Currently I'm running (with Dick Davis, sponsored by the Simons Foundation) a challenge to see whether you can improve the performance of open-source models to become closer to frontier-level performance, just by better prompting. We call it a "distillation challenge" or "cheat sheet challenge." It's like giving a one-page cheat sheet to weak students taking an algebra midterm — can they improve their percentage above 50%?

The competition has been running for about three months. The best cheat sheets so far can get 80–90% performance on these algebra questions. We just finished the first stage.

We're now running the second stage, where people supply Python code which can call LLMs (with a limited budget, open-source models only), and the objective is to not just answer yes or no but to supply a Lean proof or disproof. It will be interesting to see how well they perform.

This is the type of task where unrestricted AI use is fine — people create their own harnesses, refine cheat sheets using all kinds of homebrew technologies, the results are mathematically interesting, and they're not bottlenecked by the bottlenecks of traditional mathematics.

Summary

We have to make a distinction between traditional workflows that for structural reasons will remain mostly human-dominated, and new challenges where we can really leverage the full power of modern AIs.

At the same time, for existing tasks like solving problems, we have to change our incentives. Just being the first to prove something or the first to formalize a theorem — that should be decentered as the primary goal. It is part of the goal, but exposition and digestion are becoming far more important.

More generally, we should be better at enunciating goals. If you give a human a task, usually they understand not only the explicit task but can read between the lines and understand your implicit goals as well. But AIs are like these genies that grant wishes very literally — you ask it to do something and it does what you ask, but you realize there were other things you wanted that you didn't realize were part of the goal.

We need to think more about what our goals are — why do we do mathematics at all?


Q&A

Q: You mentioned the incentive gap — it made me think of the Szemerédi theorem, how there was initially a complicated and opaque proof, followed by more illuminating proofs that were celebrated even though they weren't proving something new. Is that a useful analogy?

Tao: Yes, this kind of proof digestion already happens in human mathematics. The first person to prove a theorem often is not the best placed to explain the proof. And just the psychological breakthrough of knowing that the theorem is true can indirectly inspire other proofs. It's possible that there's an incomprehensible AI proof and shortly afterwards other proofs appear, semi-inspired by the AI proof — this is already beginning to happen.

But the new thing is the impedance mismatch. Previously the number of people willing to digest proofs and their ability to do so was roughly comparable to the ability to generate proofs. But now if generation increases by one or two orders of magnitude and digestion doesn't, we get the traffic jam. If you have 10 or 100 Szemerédi-level results and only one Gowers or one Graham to digest them, that's a problem.

Q: Are there more traditional mathematical topics which are "formalization only" — not worthwhile enough to come back and look at the actual proof?

Tao: I'm working right now in number theory. There's a sub-branch of analytic number theory called explicit analytic number theory, where people carefully work out all the constants — this constant is 6.5, this bound holds once n is bigger than 10⁴⁶. People in this field are known for being very careful, doing lots of precise numerics and micro-optimizations. But it's a very tedious field.

We'd like automated ways to verify and generate new results here. Every time there's a new bound, how does it propagate? If you improve one constant, that should improve all these other constants — kind of like when you update one cell in an Excel spreadsheet and other cells should update. You're not doing any interesting new mathematics, just recalculating and verifying. This is perfect for AI. No one wants to do this. There are tasks in traditional mathematics which are very outsourceable to AI, and we should think about what these might be — and have them on separate lanes from the human mathematical lane.

Q: How would you recommend we change mathematics education to account for proof digestion?

Tao: That is a great question — we don't have the answers yet. But I think we have to deprioritize getting the correct answer as our main rubric for assessment. We're already in an era where almost any random homework or final exam question can be solved quite correctly by AI.

I think we have to move towards things like presentations, projects, discussions, conversations. There are interesting experiments — there was a math professor at Harvard who got their entire class to generate a prompt to get an AI to solve the final as accurately as possible. The students broke into teams: data generation (generating new test problems), prompt engineering (coming up with good prompts), evaluation (evaluating the outputs), and orchestration. The final prompt did about 50% of the final from two years ago — which was amazing performance — but it was very educational for all the students involved.

Old methods of assessment — unless you do them in environments where there's no AI assistance at all, like in-person exams — I think basically you can't do it anymore.

Q: Can we do reinforcement learning with human feedback on proof digestion?

Tao: My short answer is no. You can create things that look like proof digestion — rubrics for whether you've cited references correctly and highlighted the right things, AI critiquing each other. But if you have too much of that kind of metric, there's reward hacking, and you'll get things that may make the problem worse — papers that look like they're explaining things, but actually the explanations are misleading and not emphasizing the right things.

Digestion takes time. Sometimes there are papers whose impact was not realized until years later. There was no obvious metric you could point to at the time that indicated a breakthrough — but later, in context, there was a connection to some other field. There's a place for optimization, and then there are things that optimization hurts. Just because optimization works some of the time doesn't mean it's the hammer you use for everything.

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Pub: 04 May 2026 19:48 UTC

Views: 175