If LLMs Are a Dead End, Could They Still Accelerate AGI?

François Chollet has made one of the sharper criticisms of the current artificial-intelligence boom. In a 2024 interview with Dwarkesh Patel, the creator of Keras and ARC-AGI, and co-founder of the ARC Prize, argued that OpenAI had effectively set progress toward artificial general intelligence back by five to ten years.

Chollet gave two reasons. First, he argued that frontier AI research had become much less open, with leading laboratories publishing fewer of the technical details that previously allowed ideas to spread across the research community. Second, he believed that the success of large language models had caused them to “suck the oxygen out of the room”: money, compute and researchers were flowing toward an approach he regarded as an off-ramp rather than a route to AGI.

The first criticism is mainly institutional. The second creates a stranger counterfactual. Suppose Chollet is right that scaling transformers never produces artificial general intelligence. It still does not follow that the enormous investment in LLMs delayed AGI. That conclusion treats LLMs only as candidate AGI architectures, when they may also become research infrastructure capable of helping to discover whatever replaces them.

The real question is therefore whether that research acceleration outweighs the opportunity cost and intellectual monoculture created by concentrating so much effort on one paradigm. A technological dead end can still help build the road beyond itself.

Editorial image generated by the author.

Suppose LLMs Really Are an Off-Ramp

It is useful to grant the strongest version of Chollet’s technical case rather than arguing against a weaker one. Perhaps an LLM can acquire an enormous collection of skills through training while remaining fundamentally poor at learning genuinely new skills from sparse experience. It may lack persistent world models, robust causal reasoning or the ability to restructure its own concepts when confronted with something far outside its training distribution. Such a system could become extraordinarily competent without acquiring the flexible intelligence humans display when entering an unfamiliar environment.

This distinction lies behind Chollet’s work on ARC-AGI. The benchmark was designed to resist memorization and reward systems able to infer unfamiliar rules from very little information. The ARC Prize’s account of ARC-AGI-2 notes that a roughly 50,000-fold increase in base-LLM scale produced little progress on the original benchmark until test-time adaptation methods began appearing in late 2024. ARC-AGI-2 is explicitly designed around the proposition that scale alone is insufficient.

That comparison describes the benchmark’s earlier history, not its present ceiling. By November 2026, ARC Prize’s verified results included scores above 90 per cent on ARC-AGI-2, while ARC-AGI-3 had extended the evaluation to interactive environments requiring adaptation over time. Those advances make it harder to treat the early failures as permanent limitations, but they do not by themselves establish that scaling pretrained language models is a sufficient route to AGI.

None of this proves that transformers can never produce AGI. It does explain why the question remains open despite the remarkable capabilities of current systems. General intelligence may eventually require persistent memory, continual learning, better world models, program induction, embodied interaction, new forms of search or mechanisms nobody has yet invented. Even under that assumption, however, it does not follow that building LLMs delayed their discovery.

The Missing Arrow in the AGI Counterfactual

The argument that LLMs delayed AGI usually follows an intuitive chain:

resources spent on LLMs → fewer resources spent on alternative approaches → slower discovery of AGI

Some version of that effect must exist. Researchers, capital and computing resources are finite. Once transformers began producing commercially useful systems, enormous parts of the AI ecosystem reorganised around them. A researcher exploring an unusual architecture now competes for funding and compute with technologies that already generate working products.

But the counterfactual has another branch:

resources spent on LLMs → increasingly capable research tools → faster exploration of alternative approaches → faster discovery of AGI

Chollet’s argument counts the human researchers drawn into the LLM paradigm. It does not necessarily count the artificial researchers that the LLM paradigm may create. That omission could matter because scientific progress is limited not only by the number of good ideas humans have, but by the cost of finding out which ideas are good.

The romantic picture of scientific discovery emphasises the breakthrough insight. Real research contains much more friction. Someone has to search the literature, understand old work well enough to reproduce it, write and debug code, choose parameters, run experiments, analyse failures and decide whether an unexpected result is interesting or merely an implementation error. Many conceivable research directions never receive serious attention because skilled researcher time is scarce.

An advanced AI system does not therefore need superhuman scientific intuition to change research substantially. It only needs to reduce the cost of exploring possibilities. Ten researchers who can each investigate a few difficult ideas per year face a different constraint from ten researchers able to delegate literature searches, implementation, replication, debugging and preliminary analysis to AI systems. Most of the additional experiments might fail, but scientific progress depends as much on cheaply killing bad hypotheses as on generating good ones.

Early versions of this model already exist. Google’s Co-Scientist system, described in Nature, uses multiple Gemini-based agents to generate, criticise and iteratively refine scientific hypotheses. Its proposals were subjected to end-to-end laboratory validation across three biomedical problems, including drug repurposing, liver-fibrosis targets and antimicrobial resistance.

AlphaEvolve provides an even cleaner example because candidate solutions can be evaluated automatically. DeepMind’s AlphaEvolve uses Gemini models to generate candidate programs, automated evaluators to test them, and an evolutionary process to retain and modify promising solutions. Algorithms discovered through that process have been deployed in Google’s computing infrastructure as well as used for mathematical and algorithmic problems.

More direct, though still qualified, evidence arrived in November 2026. In a high-access assessment, the independent research organisation METR estimated that Anthropic’s rate of progress on well-specified model-capability benchmarks since October 2025 was about 1.9 times its earlier rate. METR judged that AI assistance probably accounted for much of this acceleration, while stressing substantial uncertainty, redacted evidence and the continued importance of human-directed research. That supports the claim that AI can accelerate AI development, but it does not tell us whether the route to AGI has become shorter.

The significant development is not simply that an LLM can suggest an idea. It is that the model can become one component inside a machine for conducting search.

Could LLMs Discover What Comes After LLMs?

If transformers themselves are insufficient, someone still has to discover the alternative. One possibility is the familiar historical model: thousands of human researchers gradually explore competing architectures, publish results and build on one another’s work. Another is that those same researchers increasingly work with systems able to read papers, reproduce experiments, implement architectural variants and test them at machine speed.

LLMs may therefore help invent the architecture that replaces LLMs. There is nothing particularly paradoxical about this. Classical computers are used to design quantum computers, and existing semiconductor technologies help develop the materials and manufacturing processes intended for later generations of chips. A technology does not have to survive into the final system to make that system possible.

The transformer could occupy a similar position in the history of artificial intelligence: capable enough to automate parts of AI research while still lacking whatever properties eventually prove necessary for general intelligence. Its historical importance would then lie partly in the search capacity it created rather than in its own eventual destination.

This also changes how developments in reasoning, search, memory and tool use should be interpreted. The relevant unit of intelligence may increasingly be not the pretrained language model in isolation but the larger system constructed around it. If a future route to AGI combines learned representations with search, experimentation, external memory, continual adaptation and feedback from the world, there is no obvious reason that language models must either solve the whole problem or be discarded entirely.

The Monoculture Problem—and the Role of Experiment

This argument does not dispose of Chollet’s deeper concern. AI-assisted research could make one part of it worse. Large language models learn from existing human knowledge, so their conceptual repertoire reflects the theories, terminology and assumptions already prominent in the literature. Ask such a model for promising directions in artificial intelligence and it is naturally likely to recombine ideas already familiar to AI researchers.

If those same models increasingly help scientists select papers, generate hypotheses and design experiments, a feedback loop becomes possible:

dominant paradigm → training data → AI-generated research ideas → more research within the dominant paradigm → future training data

Research could become dramatically faster while becoming intellectually narrower. This is closely related to a question explored previously in whether AI gives science more paths through an existing map or helps redraw the map itself. If AGI requires escaping the conceptual basin surrounding current deep learning, accelerating exploration inside that basin may accomplish less than the raw volume of papers and experiments suggests.

The problem resembles climbing the wrong mountain. Better equipment can get everyone to the summit faster without revealing that a taller mountain exists beyond the horizon. The danger is not merely that money is being wasted. A dominant technology changes which questions are easy to ask, which experiments are cheap to perform and which directions therefore look attractive to researchers, investors and institutions.

There is, however, an important difference between asking a language model what it thinks and using one inside an empirical search process. Ask an LLM what architecture should replace transformers and its answer will inevitably be shaped by patterns in its training data. Give a system the ability to generate hundreds of candidate architectures, implement them, test them against unfamiliar tasks and retain unexpected successes, and the model no longer gets the final vote. Reality does.

The loop becomes:

model → hypothesis → experiment → measurement → selection → revised hypothesis

AlphaEvolve illustrates the principle particularly clearly. The language model proposes programs, but automated evaluators determine which survive. A candidate succeeds because it performs better according to an external test, not because the model finds it persuasive. Empirical feedback can therefore pull the search away from the model’s initial preferences.

That escape route has limits. Cheap experimentation helps only when success can be recognised. Automated search is especially powerful in mathematics, programming and engineering, where candidate solutions can often be evaluated against clear objectives. In messier scientific problems, the evaluation function may itself be uncertain, expensive or misleading. If researchers optimise an inadequate proxy, automation simply allows them to optimise the wrong thing faster.

AI does not abolish the need for scientific judgement, better measurements or contact with the physical world. But where reliable feedback exists, the model can generate possibilities while experiment decides which deserve another generation. That is a much more powerful research role than merely producing plausible prose.

The Counterfactual We Cannot Observe

It would be equally premature to reverse Chollet’s argument and declare that LLMs must therefore accelerate AGI. Three forces pull in different directions: AI-assisted research lowers some costs of experimentation; concentrating talent and compute on LLMs creates an opportunity cost for competing approaches; and tools built around the dominant paradigm may reinforce that paradigm by making nearby research unusually easy and productive.

The problem is that the relevant comparison is a world that never happened. Imagine one history in which the transformer boom never occurs. AI remains smaller and more intellectually diverse, with more researchers exploring symbolic systems, world models, alternative neural architectures and other approaches, but doing so largely at human research speed. Compare that with the history we actually have: extraordinary concentration around transformers followed by systems increasingly able to assist with coding, literature search, hypothesis generation, experiment design and automated evaluation.

The first world might reach AGI sooner because somebody discovers the missing architecture before the field converges on LLMs. The second might win because years spent developing the supposedly wrong architecture produce machines capable of searching the space of alternatives far faster than humans could. There is no experiment that lets us observe both histories, which is why the claim that OpenAI delayed AGI by five or ten years is better treated as a provocative counterfactual than as a measurable conclusion.

The larger point extends beyond transformers. Technologies rarely advance along clean paths in which the successful invention turns out to have been the destination all along. They create scaffolding, tools and capabilities that make later technologies possible. The final architecture of artificial general intelligence may contain transformers everywhere, use them mainly for language, or look so different that today’s systems appear to belong to an earlier technological era. None of those outcomes would by itself tell us whether building LLMs accelerated or delayed what followed.

If artificial intelligence eventually becomes capable of substantially accelerating scientific and technological research, there must be a transitional point at which AI is not yet generally intelligent but is nevertheless useful enough to help improve AI research itself. That threshold may prove historically more consequential than many arguments over exactly when a system deserves the label AGI.

The most consequential achievement of the LLM era may therefore turn out not to be the creation of artificial general intelligence. It may be the creation of machines capable enough to help us discover how artificial general intelligence actually works.