Time in the Chaos

The decisions we make depend on where we stand

Consider these two probabilities:

They are very different conditional probabilities.

The company is different. The industry is different. But perhaps most importantly, the person making the decision is different.

We tend to evaluate past decisions using information we have today. We look at someone who joined OpenAI in 2018 and think how fortunate they were. We look at someone who declined and wonder how they could have missed such an obvious opportunity.

But nothing was obvious in 2018.

And nothing is nearly as obvious today as it will appear in retrospect ten years from now.

This is what makes career decisions so difficult.

You are not optimizing against a fixed objective function with a known reward. Your objectives change as you grow. Your constraints change. Your understanding of what constitutes a good life changes.

Even your definition of success changes.

So, do not judge the quality of your decisions solely by their eventual outcomes.

A good decision can lead to an unfavorable outcome. A poor decision can lead to an extraordinary outcome.

What matters is whether you made a thoughtful decision given the information, values, and circumstances available to you at the time.

And whether you learned something from it.

The happiest years of my academic life

The period from 2020 through the end of 2022 was probably the happiest time of my academic career so far.

The world had slowed down during the pandemic. There was less traveling, less noise, and fewer distractions. We could spend long stretches of time thinking about research problems, reading papers, developing ideas, and following our curiosity.

There was still competition, of course. Academia has always been competitive.

But I remember feeling that we had the freedom to work on questions we believed were important, without constantly wondering whether we were missing the next big thing.

We were thinking about out-of-distribution detection and how machine learning systems behave when the world deviates from their training assumptions.

These problems were not always fashionable.

But they mattered to us.

Some of the work we started during that period became among the most meaningful contributions of my career.

I learned something important from those years:

Intellectual progress often requires a kind of patience that the surrounding environment does not reward.

You need time to understand a problem deeply enough to ask a better question.

You need time to be wrong.

You need time to explore ideas that may not lead to a paper next month, or even next year.

And you need the courage to keep working on something before the rest of the world recognizes its importance.

Then came the wave of LLMs

The release of ChatGPT in late 2022 changed everything.

Or at least, it felt that way.

Suddenly, the entire research community was moving toward language models. Research agendas shifted. Funding priorities shifted. Companies began hiring aggressively. New startups appeared almost every day.

And the pace kept accelerating.

Unlike previous waves of AI, this one began to challenge something much more fundamental: the nature of intellectual work itself.

AI systems can now write code, formulate hypotheses, solve mathematical problems, run experiments, and draft scientific papers.

Of course, there are still significant limitations. But the trajectory is impossible to ignore.

For the first time, many of us are seriously contemplating a future in which AI systems can perform substantial portions of the work that researchers have traditionally done.

This is not simply another shift from computer vision to NLP, or from supervised learning to reinforcement learning.

It challenges the role of the human scientist.

I know that many of you are experiencing some form of existential uncertainty.

And perhaps the most difficult question:

I don’t think these are irrational concerns.

I think they are reasonable questions to ask during a period of profound technological change.

And I don’t have definitive answers to all of them.

But I want to share how I have been thinking about this uncertainty.

We are living through a period of chaos

I have recently been thinking about chaos theory as a metaphor for the period we are entering.

In a chaotic dynamical system, small differences in initial conditions can lead to dramatically different outcomes over time.

Importantly, chaos does not mean the absence of structure. A system can follow deterministic rules and still be extraordinarily difficult to predict over long horizons.

The AI ecosystem has some similar characteristics.

Advances in model capabilities change the economics of research. Those changes influence where talent goes. Talent concentration changes the pace of innovation. New capabilities reshape demand, investment, and public expectations. These, in turn, change what researchers choose to work on.

The system contains multiple feedback loops.

A breakthrough in one area can rapidly change the value of work in another.

An idea that seems marginal today may become central tomorrow. An expertise that commands enormous value today may become partially automated within a few years.

The further into the future we try to predict, the less reliable our forecasts become.

Think about how difficult it would have been in 2016 to predict the research landscape of 2026.

Or in 2018 to predict which AI companies would become dominant.

Or even in 2022 to predict how much the nature of AI research would change in just four years.

And yet, we constantly try to make five-year career plans as though the future were reasonably predictable.

This is the paradox.

A PhD takes years. But the technological environment may change several times during that period.

So how should you plan your future?

My answer is that you should:

Stop trying to optimize your career for one particular prediction of the future. Instead, optimize for your ability to adapt across many possible futures.

This is a fundamentally different way of thinking.

What, then, is the value of a PhD?

I want to make a distinction between learning to do research and producing research outputs.

For a long time, the two were closely connected.

You learned how to do research by reading papers, designing experiments, writing code, analyzing results, and eventually publishing papers of your own.

The outputs were evidence of your growing abilities.

But as AI becomes increasingly capable of producing these outputs, we need to ask what the underlying education is really for.

I don’t think the primary value of a PhD is that you become exceptionally good at writing PyTorch code, running experiments, or producing conference papers.

Those are useful skills, but they are not the essence of scientific training.

The deeper value is that you learn to think independently about questions for which nobody knows the answer.

You learn how to recognize when an assumption is wrong.

You learn how to distinguish an interesting result from an important problem.

You learn how to develop taste: the ability to identify questions worth spending years of your life on.

You learn how to navigate uncertainty without needing someone to tell you what to do next.

You learn how to challenge conventional wisdom, including your advisor’s.

And perhaps most importantly, you learn how to teach yourself something entirely new.

These abilities have always mattered. I believe they become even more important as the cost of executing research decreases.

If AI can make it ten times easier to implement an idea, then having a good idea becomes relatively more valuable.

If AI can generate a hundred plausible hypotheses, then knowing which hypotheses are meaningful becomes more valuable.

If AI can produce convincing-looking experimental results, then understanding what constitutes trustworthy evidence becomes more important.

I don’t mean that technical depth will become irrelevant. Quite the opposite. Good scientific judgment requires deep understanding. You cannot reliably evaluate what you do not understand.

But the goal of your PhD should not be to become a faster producer of research artifacts.

It should be to become someone who can create intellectual direction, even when the tools, methods, and surrounding landscape change.

Don’t confuse the current frontier with the permanent frontier

One of the greatest risks during a period of rapid technological change is overfitting to the present.

Right now, certain research topics, skills, and organizations attract enormous attention.

It is tempting to conclude that the safest career strategy is to move as close as possible to whatever is currently at the center of the field.

Sometimes that is a perfectly reasonable choice.

There are tremendous opportunities at frontier AI labs. The concentration of talent, compute, and ambition is historically unusual. For some of you, joining these organizations may be the best possible next step.

But I want you to distinguish between two questions:

And:

These are not the same question.

When I began working on out-of-distribution detection, the prevailing emphasis was on improving predictive accuracy under standard benchmarks.

We were asking a different question: what happens when a model encounters something it has never seen before?

That question did not disappear when the field moved from convolutional networks to transformers, or from classification models to language models.

If anything, it became more consequential as AI systems acquired greater autonomy.

The methods changed. The architectures changed. The applications changed.

But the underlying scientific problem endured.

This is something I hope you will remember when choosing your research directions.

Try to identify problems with a long intellectual half-life.

Problems that arise from fundamental limitations, tensions, or unanswered questions, rather than temporary deficiencies of a particular model.

Ask yourself: if models become dramatically more capable in three years, will this question still matter?

If the answer is yes, you may have found something worth pursuing.

Think about your career as a portfolio of possibilities

Many students approach career decisions as though they must identify one optimal destination: academia, a frontier lab, a large technology company, or a startup.

And then they try to maximize the probability of reaching that destination.

But during periods of high uncertainty, committing too early to a single future can be risky.

A better strategy is to build capabilities that preserve multiple possibilities.

Scientific depth gives you the ability to create new knowledge.

Engineering ability gives you the power to turn ideas into working systems.

Communication and leadership allow you to influence people and coordinate ambitious projects.

Understanding how research connects to real-world needs helps you recognize opportunities beyond academia.

These capabilities reinforce one another.

I am not suggesting that you should try to do everything. That would be a recipe for becoming mediocre at many things.

Rather, build exceptional strength in something fundamental, while developing enough breadth to recognize and pursue new opportunities.

Think of your career as a sequence of decisions, not a single irreversible choice.

Some opportunities are valuable because of what they pay today.

Others are valuable because of what they teach you, who they expose you to, and what options they create for you tomorrow.

Both matter.

And the relative importance of each will change at different stages of your life.

Don’t let the market define your self-worth

I want to say something about money, prestige, and comparison.

It would be unrealistic to pretend these things don’t matter.

We are living through a period when the financial rewards for certain kinds of AI expertise have become extraordinary.

Some researchers have accumulated wealth that would have been almost unimaginable in academia a decade ago.

Others have built influential academic careers but may feel that they missed an economic opportunity.

It is natural to compare.

I do it too.

But I have learned that comparison is a poor foundation for making life decisions.

There will always be someone who joined the right company earlier, invested in the right technology, published the right paper, or received a more prestigious offer.

If you evaluate your life primarily against the best outcome someone else achieved, you will almost always feel behind.

This is especially dangerous during a technological boom, when a small number of highly visible outcomes distort our perception of what is normal or attainable.

Money matters because it provides security, freedom, and opportunities for the people we care about.

Prestige can matter because it opens doors and gives us a platform to pursue meaningful work.

But neither tells you what kind of work you will enjoy doing every morning.

Neither tells you whether you will feel intellectually alive.

Neither tells you whether you are becoming the person you want to become.

I am not asking you to ignore financial opportunities. You should understand them, evaluate them seriously, and negotiate for what you are worth.

But make sure you are optimizing for a life you actually want, rather than a life that looks impressive from the outside.

You don’t need to have everything figured out

Perhaps the most important thing I realized is that uncertainty does not disappear when you become more senior.

You may imagine that once you finish your PhD, get a faculty position, receive tenure, or become a research leader, you will finally know what you want to do.

That has not been my experience.

I have gone through multiple periods of questioning my own direction.

I have wondered whether I should remain in academia or return to industry.

I have questioned whether the research problems I care about will remain relevant.

I have thought about the tradeoffs between intellectual freedom, resources, financial opportunities, and personal happiness.

And I am still thinking about them.

Tenure does not eliminate uncertainty. Experience does not eliminate uncertainty.

What experience gives you, hopefully, is a better ability to live with it.

You become more comfortable making decisions without knowing how everything will turn out.

You learn that changing your mind is not necessarily a failure.

You realize that there is no single path that guarantees both success and happiness.

And you become less afraid of making a choice that looks unconventional to others.

When I walked away from OpenAI’s recruitment opportunity in 2018, I could not have predicted what the next eight years would bring.

But I also could not have predicted the research I would pursue, the students I would mentor, the collaborations I would develop, or how much I would enjoy building an academic career.

There were opportunities I gave up.

There were other opportunities that became possible only because of that decision.

Every path has its own counterfactuals.

You cannot live all of them.

A final thought

More than ten years ago, I was a PhD student writing my first ICLR paper, excited about a question that probably seemed rather narrow to most people.

I could not have imagined the field we are living in today.

I could not have predicted the rise of foundation models, the emergence of AI agents, or the possibility that machines might begin to automate parts of scientific discovery itself.

And I certainly could not have predicted my own path.

If there is one lesson I have taken from the past decade, it is this:

The future is much harder to predict than we think, but our ability to grow and adapt is much greater than we realize.

The next ten years may bring even more dramatic changes. The structures of academia, the nature of scientific work, and even the way society is organized will be reshaped in many ways.

Some of the skills you are learning today will become obsolete. Some of the problems you are working on will be solved. Some of the careers you are imagining may look very different by the time you get there.

But new questions will emerge. New opportunities will appear. And there will be a need for people who can think clearly, question assumptions, exercise good judgment, and navigate uncertainty.

That is what I hope your PhD will prepare you for.

Not a particular job.

Not a particular research trend.

Not even a particular version of the future.

But the ability to shape your own path through a world that keeps changing.

You don’t need to predict the next wave. You need to become someone who can navigate the waves without losing your own sense of direction.

And sometimes, the most important thing you can do is step away from the noise, find a little quietness, and give yourself the space to think.

That was what I needed eight years ago.

Perhaps, in different ways, it is what some of you need today.