A Copernican Moment and Research Taste

When we talk about what AI can do, we are really reopening a deeper question: what, exactly, is uniquely human in research?

Lately, a line you hear more and more in academia is this: once AI becomes a research assistant, research taste will matter even more. But I have always felt there is something oddly self-contradictory about that phrase.

• On the one hand, “research taste” is too vague. It runs against the basic demand that research should make things clear, concrete, and intelligible.
• On the other hand, that vagueness can provide a kind of flexible practical wisdom, but it can just as easily curdle into survivor bias or the smugness of identity politics.

If we insist on talking about taste, then we need to say what we mean. Otherwise it becomes little more than a new religious term dressed up for academia.

Recently, Terence Tao gave me a new angle on this in his interview with the YouTube creator Dwarkesh Patel. Maybe what we usually call “research taste” really is a pseudo-problem. Different layers are getting mixed together, and those layers do different work.

• At the macro level: how is truth actually discovered?
• At the micro level: which theories get selected first, circulated first, and funded first?

At the macro level, research taste is not the source of truth. At the micro level, it certainly exists, but mostly as a bit of club language inside research communities.

• Original YouTube video: Terence Tao – How the world’s top mathematician uses AI
• Chinese text reposts include QbitAI, NetEase, and 51CTO.

Looking back at the “Copernican moment”

Strictly speaking, the so-called “Copernican moment” here is closer to the moment when Kepler actually corrected the laws of planetary motion.

Copernicus proposed heliocentrism, but he still insisted that planets moved in perfect circles.

Kepler, for a time, believed planetary orbits ought to fit some highly harmonious geometric structure, perhaps even something related to the Platonic solids. But he lacked a high-quality dataset of observations, so he turned to Tycho Brahe for one.

The planets do not move according to circles or regular polyhedra. Kepler spent years trying different fixes, shifting circles around, adjusting them here and there, and still nothing quite worked. In the end, it was a data-driven process that led him to suspect the ellipse might be the right answer.

In more modern empirical language, the process looks something like this:

1. High-quality data: Tycho’s long-run observational records;
2. Model assumptions: circular orbits, geometric harmony, and other priors;
3. Residual analysis: the model could not account for the key deviations in the orbit of Mars;
4. Repeated revision: move the circle, change the parameters, try a different structure;
5. Abandon the old assumption: admit that the “circle” itself may simply have been wrong;
6. Abstract a new law: elliptical orbits, and eventually a more general law of planetary motion.

The history of science tends to magnify the dramatic instant of discovery while downplaying the long stretch of failure, trial and error, and data accumulation that came before it. In that sense, the macro-level search for truth has never been just a matter of someone with refined taste seeing the essence at a glance. It is usually the people with better data, more time to fail, and more willingness to delete old assumptions who get closer to the truth.

Taste and the cost of trial and error?

In academia, when people talk about research taste or research intuition, what they usually mean in practice is simple enough: reduce the cost of trial and error.

Scientists face an unlimited supply of theoretical conjectures and a limited amount of time and energy to test them. That is one reason peer review exists: to filter the pile down to theories that seem more reliable. But in an environment shaped by data-driven work and AI, the cost of verification is drifting closer and closer to zero. So the real research advantage now starts to look more like this:

• who has better data;
• who can expose the weaknesses of old models faster;
• who is willing to admit that a cherished assumption is actually wrong;
• who can preserve one rough but correct idea amid a mountain of failed ones.

That line of thought naturally brings to mind one of the classic questions in social science: why didn’t the Industrial Revolution happen in China, or in Asia more broadly? Different fields and periods have given that question different names: the Needham question, the Weber question, the Great Divergence, the Qian Xuesen question, and so on.

Justin Yifu Lin’s classic answer is that the essence of science is raising productivity. China had abundant labor and scarce capital; Europe had the reverse. Europe therefore had stronger incentives to invest in science, while China developed the examination system. China’s earlier development rested on accumulated practical knowledge under high population density. The Industrial Revolution, by contrast, required institutions that would push elites into scientific work.

A crucial follow-up question is this: who really drives an Industrial Revolution, ordinary people or elites? In time, it is tempting to tell a dialectical-materialist story about historical tides. But the inequalities we see across space suggest that things are not that simple. If we assume that scientific development has bottleneck periods, is this where the analogy between AI and the Industrial Revolution begins to make sense? There may be an inverted-U relationship between the cost of trial and error and the quality of the population:

When the cost of trial and error is low, scale and broad experimentation matter more. When the cost of trial and error is high, elite filtering and intensive training matter more. And when AI begins to cut part of the cognitive cost of trial and error in a noticeable way, the filtering structure once held together by the “taste” of a small number of people may start to loosen. What changes at the macro level is not that truth suddenly begins to depend on taste. It is that the way we organize trial and error in order to approach truth is changing.

Taste and selection mechanisms

Unfortunately, scientists do not live inside macro-history. They live in the present, before the submission deadline, inside grant applications and peer review.¹

Liu Cixin gives a beautiful metaphor for this in his short story Poetry Cloud: an advanced civilization can exhaust every possible combination of Chinese characters and still not know which poem will one day truly surpass Li Bai. The question is not just “can it be generated” but “which one should we trust”.

The world of theory works the same way. We often cannot know, in the present, which theory will become important later. The value of a theory never depends only on whether it looks elegant, mature, or complete right now. It also depends on whether time will later show it to be more powerful in explanation.

The history of economic thought offers plenty of examples. Many people at the time could not accept Augustin Cournot’s use of mathematics in Researches into the Mathematical Principles of the Theory of Wealth to express the relation between price and demand. Frank Ramsey had already touched on the endogenization of the saving rate before the Solow growth model, but the importance of that move only became clear within later theoretical frameworks. Here, “taste” means something more like this:

• sensitivity to the problems of the present;
• a hazy forecast about the future explanatory power of a theory;
• the ability to tolerate the difference between “roughly right” and “beautifully wrong.”

Roughly right and beautifully wrong

Tao has a wonderful passage on this:

Science is always moving forward. When you only have a partial answer, it may look worse than a theory that is wrong but polished enough to answer every question. Newtonian theory had many mysteries, and those were not resolved until centuries later by a conceptually quite different approach. Progress often comes not from adding more theory, but from deleting some of the assumptions in your head.

That passage also helps explain why “taste” keeps coming up at the micro level.

Because real researchers are often facing two kinds of things at once:

• highly mature but wrong theories;
• highly rough but correct theories.

From the vantage point of the long run, time may eventually vindicate the correct theory. But from the standpoint of a present-day career, disciplinary division of labor, and the allocation of resources, researchers have to choose before the evidence is complete. In that setting, “taste” is not some sacred faculty. It is a practical capacity to place bets.

Taste and narrative

If all we notice is that data keeps growing and models keep getting stronger, it is easy to slip into an illusion: if machines can generate hypotheses and test patterns faster and faster, will theoretical competition eventually collapse into a pure contest of data?

Tao’s answer is no.

The art of exposition, the organization of argument, the construction of narrative — these are also important parts of science. Data helps, of course, but people still need to be persuaded. Otherwise they will not push the direction forward. They need to make an initial investment to learn your theory and actually explore it.

That gets at another micro-level fact: science is not just a process of discovery. It is also a process of organization.

Data does not persuade people on its own. A theory may be closer to the truth in some sense, but it still needs to be explained, circulated, learned, brought into courses, written into papers, and backed with new research resources. Even in empirical economics, a p-value is only one test statistic among many necessary conditions.² What we really have to persuade others of is why this particular combination of necessary conditions deserves trust. See The Rhetoric of Economics and Empirical economics: intuitive does not mean obvious.

For example, take the same topic: long-term use of AI may lead to deterioration in human cognitive ability, or perhaps skill, or attention. You can find versions of that topic in statistics, economics, the life sciences, and medicine. The theme is the same, but the methods and narrative angles differ. Even with the same topic, some people can package it for a top journal while others can only place it in lower-tier outlets. The gap there is often much larger than the supposedly tasteful question of what is worth studying in the first place.

There is also a contradiction in the macro-level idea of “research taste.” The spirit of science popularization many of us grew up with says that even the most trivial phenomenon may conceal something profound. Yet the language of taste can easily decay into a habit of treating certain directions of research as simply boring and therefore beneath notice.

At the micro level, “taste” carries a strong communal coloring. It is not just a matter of personal judgment. It is also a kind of club culture within a discipline: which questions count as worth doing, which evidence counts as decisive, which forms of expression count as serious, which assumptions feel “natural”. None of that is purely individual.

In that club setting, research taste is less about whether a topic is dull or interesting than about whether the research fits in.

Take a more pointed example. For labor economists, gender may be a basic dimension for analyzing social structure. But some sociologists working on LGBT issues may not accept that same framing of the problem. New structural economists may treat factor endowments as the primary constraint, while institutional economists may strongly reject that view. The disagreement is not entirely about who is “truer.” It is also about what each community chooses to foreground, how it organizes its questions, and where it directs attention.

So yes, at the micro level, “research taste” exists. But it looks much more like a piece of club vocabulary.³

AI and the question itself

At the macro level, taste is really a rather empty word. Wrong theories can be highly mature, and correct theories can be very rough. Taste has never had much to do with truth, because even if peer review has developed as far as it has today, that still does not guarantee that important research will necessarily rise to the top.

At the micro level, taste really does matter. Researchers cannot wait for “history’s final verdict” before deciding what to read, what to do, what to submit, or what to teach today. Limited resources force each community to build its own pre-screening rules, and “taste” is often just the everyday name for those rules.

That is why the change brought by AI is not that “research taste matters more” or that “research taste matters less.” A more precise way to put it might be this:

1. The technical cost of trial and error is falling. AI can help generate candidate ideas, search the literature, check derivations, and compress lower-level labor even further;
2. The social cost of validation has not disappeared. Data quality, theoretical interpretability, peer persuasion, training thresholds, and institutional incentives remain places AI cannot simply replace;
3. The carrier of taste is changing. In the past, it showed up more as the personal judgment of a small number of experts. Now it is increasingly embedded in datasets, citation networks, model weights, recommendation systems, and community feedback.

Research taste is not a shortcut to truth. At the macro level, truth is not determined by taste. At the micro level, taste remains a survival strategy under conditions of scarce resources. What AI changes is not truth-seeking itself, but the way truth gets discovered, selected, circulated, and funded.

Maybe that is the version of the “Copernican moment” that comes closest to where we are now.

Other recommended reading

• Teaching Econometrics in the Age of AI
• Some Thoughts on AI and Research
• The Consequences of Abundant Intelligence