Jascha Sohl-Dickstein: What Is Still Worth Doing as AI Gets Better?

A graduate student expected AGI to arrive within 3 years. When the conversation turned to career plans, the student still intended to finish a doctorate, take a postdoc and then apply for faculty positions.

Jascha Sohl-Dickstein remembered the mismatch. The student's expectations about the future had not reached the decisions shaping everyday life.

He acknowledges that nobody can describe academic work, or other jobs, 10 or 20 years from now with confidence. But anyone expecting substantial disruption from AI has reason to question the stability of a conventional career path.

Beliefs about the future should affect how time is spent, problems are chosen and tools are used today. That argument runs through his talk. Its premise needs to remain visible: near-term AGI is his forecast, with no established countdown attached.

Why he takes rapid progress toward AGI seriously

Sohl-Dickstein begins with training scale. According to the chart he presents, the compute used to train the largest models increased roughly 10,000,000-fold over the preceding decade.

He also makes a rough comparison with the computation performed by a human brain over a lifetime. He explicitly qualifies the analogy: comparable compute is neither sufficient evidence of comparable intelligence nor necessarily a prerequisite for reaching it. The comparison supplies intuition, not a demonstration of capability.

A more practical measure comes from METR's task-completion time horizons. These estimate the difficulty of software tasks an agent can complete with 50% success, using the time a human expert would need as the yardstick. The horizon is not the duration an AI runs autonomously, and it does not cover every kind of work that occupies the same human time.

In the talk, he reports an approximately 10-fold increase in this horizon since presenting an earlier version less than a year before. He also estimates that requiring 80% or 90% success would push equivalent capability milestones back by about 1 or 2 years. That latter statement is an extrapolation, rather than a promise of reliable delivery.

His other example is AI contributing to solutions of Erdős problems. The research record documents several kinds of contribution, distinguishing standalone results, human collaboration, partial progress, errors and unverified claims. Describing all of them as independent AI breakthroughs would erase meaningful differences.

These developments leave him expecting substantial further progress from existing approaches. He acknowledges finite physical resources and serious inefficiencies in current training methods. A criticism of efficiency and a claim about an ultimate capability ceiling are separate arguments.

His professional circle's optimism about AGI timelines is not a consensus across research. Continued benchmark improvement cannot, by itself, establish a year in which AGI will arrive.

Compare a project with the models that will exist when it finishes

He describes a concrete failure mode: a researcher spends 2 years advancing a problem, only to find that a newer foundation model produces a better result when asked.

The work may have been careful and demanding. Its baseline has nevertheless moved.

A project has to survive a question about its completion date: how much value will remain then? Selecting a topic entirely around today's model weaknesses can commit years of effort to a temporary gap.

He draws on Richard Sutton's 2019 essay, The Bitter Lesson, to explain the distinction. General methods can keep improving as more computation becomes available. Research can benefit from that process, while other problems may be resolved by scaling itself.

He favors projects whose usefulness increases as models improve and computation becomes cheaper, particularly work that helps that process. A project valuable only because a model currently fails at something needs repeated scrutiny of that premise.

This pushes him toward focused collaboration and research that can be tested relatively quickly. He does not welcome every consequence. Slow, wandering exploration is precisely the kind of science he loves; faster capability changes increase the cost of taking that time.

Delegate execution while retaining an understanding of the result

Sohl-Dickstein describes working with Claude every day. At the time of the talk, it felt like an extraordinarily capable graduate student at execution, with weaker judgment about which research questions deserved attention.

He presents that division of labor as temporary. Models could not collaborate this way a year earlier, and he expects them to change again over the following year.

In his own work, models already produce code, analysis and plots. He says he almost never writes code by hand, instead requesting custom dashboards and examining the results through successive iterations.

The audience supplies a necessary qualification. If Claude can write the code, a student asks, is practicing it personally still worthwhile? His answer is that understanding what the code does remains necessary, and some experience writing it is part of acquiring that understanding.

What can change is the level of abstraction. A researcher can request plots, ask why they conflict with expectations and investigate the assumptions or computation. As programming languages reduced the need to handle lower-level details, AI may remove another layer of manual work. The researcher still has to interrogate and think.

He compares the collaboration to leading a research group: scope, expectations and communication need to be clear. Delegating execution does not resolve an ambiguous question. Producing more work does not repair a mistaken research direction.

Why writing the first draft can still matter

He encourages researchers to brainstorm with AI and request criticism of their writing, while advising them to write the first draft themselves.

An audience member challenges the apparent tension: if a model cannot write a first draft, how could AGI be close?

His answer concerns the writer's understanding, not an evaluation of the model's prose. Composing an argument is part of developing the thought. Delegating the entire process can remove an opportunity to understand the problem.

That position is compatible with his willingness to delegate substantial coding. He distinguishes activities that execute an already understood idea from activities that expose what remains unclear.

AI can identify gaps, suggest counterexamples and critique an explanation. The author still needs to explain why the question matters, whether the evidence supports the conclusion and where speculation begins.

Research taste presents a related difficulty. Asked whether it can be benchmarked, he acknowledges how hard it is to devise an uncontested measure. Answering an existing question and identifying a worthwhile new one remain capabilities that need separate observation.

Reconsider how much safety a conventional career actually provides

Career decisions often trade potential reward against stability: one direction is more compelling, while another appears safer.

Sohl-Dickstein's argument is conditional. If AI causes widespread disruption, every path carries some unavoidable risk. Following a familiar route may purchase less stability than expected.

That does not answer whether every individual should pursue a doctorate, or establish that a particular occupation will disappear. It calls for examining the conditions on which a supposedly safe option depends, and whether those conditions still hold.

From there, he encourages work that someone wants to pursue and that could make a larger contribution. He particularly values projects that would improve the world even after AI capabilities have advanced substantially.

Small early choices can shape the options available later

He repeatedly rejects the idea that individuals can only wait for technological change. Research questions, model interpretability, decisions about sharing work and institutional design all affect later possibilities.

He points to Epoch AI's study of training scale to explain why he considers the transition early. Under assumptions about power, chips, data and training latency, the report estimates that a training run around 10,000 times GPT-4's scale could be feasible by 2030.

The comparison requires a correction: his spoken explanation uses 2025 as the baseline, while the report uses GPT-4. The report concerns feasible scale and retains conditions including willingness to invest. It does not guarantee that expansion will occur, or that capability would rise by the same factor.

His broader point is that rules chosen early in a technology's development can affect many later participants. Examples involving communication protocols and scientific institutions encourage attention to enduring consequences as well as immediate performance gains.

He identifies several areas worth considering:

• Applying AI to science. His examples include materials discovery, protein research, weather modeling and fusion plasma monitoring.
• Studying AI as a scientific object. Neuroscience, statistical physics, psychology and economics can each contribute different methods and questions.
• Researching safety, capability forecasts and fair access. What models can do, when they fail and who can use them all require sustained attention.
• Working on policy and governance. He argues that governments need technical expertise and that academics can contribute a perspective distinct from commercial laboratories.

He also discusses the distribution of benefits, personally favoring taxation and redistribution to share the wealth created. This is his policy preference. Better capabilities still need institutions to connect them to broadly shared gains.

Keep skepticism, and make it possible to test

The final discussion returns to experimental science. An audience member points out that progress in theory and software cannot directly replace physical experiments, and that many scientific problems lack easily verifiable answers.

Sohl-Dickstein suggests that stronger theory could reduce the experiments required, and that robots might eventually perform more laboratory work. He offers a possible horizon of 10 to 15 years while acknowledging that robotics timelines are harder to predict. These are expectations, not evidence that laboratory automation has already been solved.

For claims that AI cannot perform a particular task, he recommends specifying the task, defining a standard and tracking the result. A benchmark need not be public. A private record of capability gaps can still show whether progress is occurring.

He anticipates a possible period when humans complement large teams of AI agents, followed by further erosion of the intellectual tasks humans uniquely enable. How that process would unfold remains unknown.

What is already possible is to bring stronger tools into real work, examine whether a project remains valuable, and preserve the ability to understand, question and take responsibility for the outcome. As execution becomes more abundant, deciding what deserves to be executed requires more deliberate attention.

Original source: 2026 Conference on Physics and AI: Jascha Sohl-Dickstein, published by Stanford HAI. Speaker: Jascha Sohl-Dickstein, research scientist at Anthropic. Recorded at Stanford University on 2026-06-12; uploaded on 2026-06-30; duration: 45:14.

This article synthesizes the complete automatically generated English captions, including the audience discussion, and checks key definitions against primary research. Names and affiliations were corrected using the video metadata. AGI timelines, robotics expectations and career advice remain attributed views. The difference between the spoken compute baseline and Epoch AI's report is identified in the article. The cover is a generated conceptual illustration.