Recently, I spoke at the CCF 2026 Outstanding Doctoral Forum about research in the age of AI. As AI capabilities advance, more researchers, especially those early in their careers, have shared their anxiety about what these changes mean for their future. Their concerns are understandable, and I feel a responsibility to contribute to this conversation at such an important moment. I want to offer a perspective that addresses those concerns seriously by looking toward the opportunities ahead.
In recent years, AI has advanced rapidly. It now feels as though we may be approaching an inflection point.
OpenAI and Anthropic have both announced results at the research frontier of mathematics. OpenAI has released hundreds of mathematical manuscripts produced by an internal model. Anthropic has reported an improved bound concerning the zeros of the Riemann zeta function. Solving a frontier research problem of this kind can define a researcher’s career.
If the results are proved correct, the implications are hard to ignore. For a young mathematician investing years in a problem, the possibility that a model might resolve it changes more than a research schedule. It can unsettle a thesis, a route to recognition, or a picture of an entire career.
Mathematics is sometimes described as the canary in the coal mine for research. Other disciplines may feel the same pressure soon, especially those in which problems can be formulated precisely and results verified efficiently. Elsewhere, researchers whose work depends on costly physical experiments may feel safer.
I understand both the anxiety and the sense of protection. People who have devoted themselves to scientific progress deserve more than advice to adapt. They need time, training, access to tools, and fair recognition.
Yet I believe that, with abundant intelligence, researchers, including those facing the most immediate disruption, can find greater opportunities ahead.
As I look toward that horizon, my starting point is simple:
Taste. Ambition. Rigor.
Increasingly capable AI makes all three more important. It is not because they must remain exclusively human, but because they determine whether greater capability becomes worthwhile progress.
Taste: Choosing Better Problems
With abundant intelligence, it is easy to ask, “How can AI help me finish this project faster?” or think, “We can now turn more ideas into papers!” But a much more important question is “What should I be working on?”
Research agendas often reflect the constraints under which they were formed. We choose questions partly because we believe we have a chance to make meaningful progress within the time and resources available. When those constraints change, simply accelerating the old agenda leaves much of the opportunity unexplored.
This is why I put taste first. A tenfold increase in speed is valuable, but its value depends on the direction.
Some opportunities will be famous problems that have resisted generations of effort. Others will not resemble the old frontier at all.
In 1900, Hilbert articulated 23 problems that helped shape twentieth-century mathematics. A century later, the Clay Mathematics Institute selected seven Millennium Prize Problems. As intelligence becomes more abundant, we have another opportunity to ask not only how to solve the inherited problems, but what agenda should guide the next era of discovery.
In systems research, we may ask how AI can improve today’s important workloads, such as faster GPU kernels. We can also ask what a computer should look like when its main users are AI agents: how reasoning, execution, memory, permissions, and recovery should work together. The second question is not merely a harder version of the first. It opens a different research agenda.
To develop research taste, it is useful to ask whether a project addresses an enduring need or a temporary inconvenience; whether it creates an isolated improvement or an abstraction others can build on; whether we are trying to be slightly better within an existing design, or have reason to try something different. These questions are not new; they have always been central to first-class research. But we often set them aside because they are difficult to answer. With abundant intelligence, we have more resources, and fewer reasons, to leave them unexplored.
Note that none of this makes incremental effort unworthy. Careful measurements, small improvements, and patient refinement are how large ideas become real. Nor must every worthy problem promise an immediate application. Understanding, elegance, and beauty are reasons to do research in their own right. The point is to choose deliberately, rather than let the ease of producing a publishable result choose for us.
Ambition: Aiming Higher
Once we choose a worthwhile direction, we should reconsider what we can attempt. We can make easy things easier. We can make difficult things less difficult. Or we can make previously impossible things possible.
All three have value. Automating routine work can free time for thinking. Making a difficult experiment affordable can let more people participate. But if the main outcome is simply more papers produced at lower cost, we will have captured only a small part of the opportunity.
What excites me most is the third possibility.
For example, some researchers may see costly physical experiments as a key bottleneck limiting AI’s impact in their fields. Semiconductor research and drug discovery are two examples. But could better AI help choose more informative experiments, reduce wasted trials, design instruments, or coordinate automated laboratories? Some constraints will yield; others will remain. We should investigate which is which. I do believe radical AI-assisted approaches could transform entire industries.
Rigor: Verifying Carefully
Greater ambition requires stronger evidence.
We can delegate execution, but not responsibility. “The model said so” is not an adequate account of why we should believe a claim.
Mathematics makes this especially clear. A proof checker can establish that a formal conclusion follows from specified definitions and assumptions. We must also establish that those definitions and assumptions faithfully express the claim we intended. Formal verification is powerful precisely when we are careful about what has been formalized.
We also need to know which parts have been checked. OpenAI’s collection contains results at different stages of verification, and its public revision history records corrections and withdrawals. The Association for Human Mathematics has rejected OpenAI’s claim that the release advances mathematics. I believe the useful response is neither unquestioning acceptance nor blanket dismissal. It is to make the evidence, dependencies, and remaining uncertainty legible, so that others can build on solid ground.
In experimental work, the corresponding questions concern measurements, controls, and reproducibility. Can an independent implementation recover the result? Does it survive evaluation on data or workloads held out from the search? Do the reported gains remain when we change the assumptions that made the original setup convenient? Can we trace a figure back to the data, code, and decisions that produced it?
These questions should shape a project from the beginning. If we search enough possibilities and report only the best-looking outcome, we (or AI) can fool ourselves very efficiently. Designing the decisive test before searching, and preserving failed attempts as well as successes, helps distinguish true discovery from selection effects.
But rigorous verification cannot mean sending an ever-growing mountain of AI output to an unchanged queue of human reviewers. We need to scale our ability to check alongside our ability to generate. AI can help search for counterexamples, reproduce experiments, inspect dependencies, and construct formal proofs. Reusable test environments and independently developed checks can make confidence less dependent on any one person or model.
We need a process that earns trust by making clear what has been checked, under which assumptions, and what remains uncertain.
Build the future we want to research in
These choices also belong to institutions. We cannot tell young researchers to pursue ambitious, long-term questions while only rewarding immediate, short-term results. We should create room for transitions and recognize contributions for the insights and lessons they provide.
I do not know how quickly AI will change each discipline. I do believe that treating researchers only as people at risk of being overtaken misses something essential. We are also people who can help decide what becomes possible.
The most hopeful question is not “What will be left for us?” It is “What can we now set out to understand, build, and make better?”
Choose better with taste. Aim higher with ambition. Verify carefully with rigor.
That is how I want to approach the opportunities ahead.