Do We Have an Erdos Problem?

can AI do for social science what it's doing for math?

The math world has been in minor upheaval over OpenAI disproving something called the “planar unit distance conjecture”, a problem posed by Erdos in 1946. “I find this existentially upsetting,” one alleged mathematician wrote. “I see myself shriveling into nothing.”

So naturally that got me thinking: do we have anything resembling Erdos Problems in social science? As I understand, Erdos problems have two things in common. One, they’re precisely formulated, in a way that precludes ambiguity. Everyone agrees what the problem is asking. And two, they have unambiguous resolution conditions: you know when you’ve solved them. The solution is not subject to interpretation and does not depend on your ontological commitments or analytical framework.

Do we have anything that comes close? Maybe the paradox of voting, in the sense that it’s precisely formulated. But does it have a solution that, once somehow discovered, will seem correct to everyone? I very, very much doubt it.

Or take democratic peace theory, what Jack Levy called the closest thing we have to an empirical law in social science. “Why don’t democracies fight each other?” might seem like an Erdos puzzle at first glance. But what counts as a democracy? What counts as a war? The Correlates of War threshold of 1,000 battle deaths is an arbitrary coding decision. The “puzzle” is inseparable from the way we constitute it.

The biggest problem is reflexivity. Erdos problems exist in a world where the objects you study don’t care about being studied. Prime numbers don’t change their behavior when you develop new theorems about them. But the democratic peace transformed from a statistical finding to a foreign policy doctrine. Clinton cited it to justify NATO expansion and Bush invoked it while invading Iraq. Once policymakers believe democracies don’t fight each other, they act in ways that change the incentive structure of both democratic and non-democratic states.

Same with deterrence theory. Rational choice models of nuclear strategy not only described the logic of deterrence but also constituted it. Policymakers internalized the models and acted on them, which made the models partly self-fulfilling in ways that made them impossible to test.

Anthony Giddens called this the double hermeneutic, which is an ugly phrase for an important point: social scientists interpret a world that is already interpreting itself. The physicist, on the other hand, interprets a world that does no interpreting at all.

Good for us. But if social science has no Erdos problems, it also has no Erdos solutions. The same reflexivity that protects us from obsolescence also means we’ll never get the clean framework-independent answers that mathematics gets. We are not early physicists waiting for our Newton, doing pre-paradigmatic work until the right genius or an AI breakthrough arrives to formalize us.

One thing people forget about Kuhn is he specifically said his framework should not be applied to the social sciences. Our best theories are beautiful lies. The world is complex so we have to simplify, the way maps do. This is the only way to do theory in social science, but it comes with real limitations that non-reflexive disciplines avoid.

Even without access to Erdos problems, could AI help resolve fundamental puzzles in social science, or move our priors in big ways? We know it can write empirical papers, but can it make theoretical breakthroughs? And if so, how and in what fields?

I can think of three ways AI could make a difference here, in decreasing order of likelihood.

First are new empirical discoveries that force theoretical revision. This is the most plausible path, since AI is very good at detecting patterns across massive datasets. It could find correlations, anomalies, and structural breaks that humans would miss or wouldn’t know to look for. Finding a new robust empirical regularity that existing theory can’t explain is the kind of thing that moves priors and generates new theoretical work.

After all, democratic peace theory started as a strong empirical regularity, not a theory. David J. Singer started off trying to disprove it as a statistical anomaly in the 1970s. The theories only came later, in the 1980s. Could AI help find other regularities hiding in the vast amounts of data? And then have humans step in to explain them?

This is what AI seems to do well: mass-scaling the anomaly detection step of the scientific process. This already works in genomics and materials science so there’s no principled reason it can’t work in, say, conflict studies or comparative politics.

The big obstacle is that pattern-trawling inherits all the problems I already discussed above. Looking through the Correlates of War for novel regularities is looking at a world where “war” means 1,000 battle deaths, and all empirical regularities are conditional on that assumption. That’s not even a data quality problem but a data constitution problem, since coding decisions are ontological commitments.

So when I say AI might find new empirical regularities, what that means is it will find regularities within the tendentious and artificial worlds we’ve already built for it. Which is still useful once in a while, but again, very different from the kind of discovery governing the solutions to Erdos problems.

Second and more difficult would be something like AI-assisted formal model exploration and stress-testing. In the parts of political science and economics that already use formal models like game theory, AI could explore parameter spaces, find new equilibria, or identify edge cases. I certainly don’t know how to do any of those fun things, though I know many humans who do, but AI could do it on a massive scale.

This still may not rise to the level of theoretical innovation, since it’s a way to trawl for discoveries rather than conceptualize them, kind of what OpenAI was doing with Erdos problems. But I don’t want to keep moving the goalposts. It’s certainly not trivial either, and could occasionally turn up something actually surprising, like an equilibrium nobody expected or a scope condition that invalidates an old result.

And the third, most unlikely use of AI is for actual conceptual innovation. This is where I’m most skeptical. The kind of theoretical breakthroughs that reshape social science involve a specific cognitive move: they take what everyone already sees and reorganize it in a way that makes new things visible. I’m thinking of things like Hirschman’s exit/voice/loyalty, Scott’s seeing like a state, Olson on collective action, or Waltz on structural realism. They help you see the old world in a new way.

At that point, it’s not really pattern detection but something closer to metaphor creation. Maybe even art — which, to be fair, AI is getting pretty good at. The point, though, is not that it’s artistic but that it’s original. It’s a novel way of seeing the world that’s connected to but not rooted in existing ways of seeing. Current AI systems are at their core interpolative. As I understand, and I’m happy to be corrected here, they still operate solely in the space defined by their training data.

An AI creating social theory is like a two-dimensional object trying to interact with a 3D world. They can get a sense of the parts but never the whole. They can even recombine existing ideas in novel ways (which is sometimes useful), but the “seeing what’s not there” quality of a real conceptual breakthrough might require something they lack. I can’t say it’s impossible in principle, since I don’t know where the model boundaries will be in a year or five, but I would put low probability on it happening with current LLMs.

The field most ready for AI-assisted theoretical work seems to be economics, for the boring reason that it’s already the most formalized social science, and economists like playing with code. Or maybe I’m overexposed to economists talking about using Claude for their papers. And maybe things like mechanism design, auction theory, or matching markets are their discipline’s closest thing to Erdos problems. Similarly, political science might benefit most in the quantitative conflict and political economy subfields, where there are large datasets and at least some semi-formalized theoretical frameworks.

One caveat is that some important recent theoretical moves in economics, like the behavioral turn, came from importing insights from psychology and sociology. Formalization didn’t help here. And the already-formalized parts like auction theory have probably been computationally explored already. The low-hanging fruit might be picked.

I want to be fair. Theoretical innovation is the flashiest goal, so I’ve privileged it here. But AI’s comparative advantage might be in two less glamorous but also important things related to theory building.

One is acting as a cross-disciplinary translator. I could see an AI trained on identifying surprising structural isomorphisms across literatures that don’t read each other. Maybe there’s a similar formal structure in evolutionary biology and institutional economics that nobody notices because the fields don’t interact, but pointing out the similarity could help shed light on some mechanisms in one or both. Maybe fitness landscapes in evolutionary biology, where species get trapped on local peaks and can’t reach higher ones, map onto the timing of institutional lock-in.

This is where AI might have an advantage over even polymathic humans.¹ Scott Aaronson noted that OpenAI’s model solved the unit distance problem partly because human mathematicians were siloed. Discrete geometers didn’t know enough algebraic number theory, and number theorists weren’t thinking about unit distances.

Second, AI might contribute not by creating new ideas but by clearing deadwood. If it can identify which empirical findings don’t replicate, or which formal models contain hidden inconsistencies, or which literatures are talking past each other due to terminological confusion, that’s valuable even if it never produces one new idea.

Maybe I’m being optimistic on that last point. Would democratic peace theorists suddenly abandon their pet arguments if AI were somehow to demonstrate the pattern rests on a statistical artifact? I doubt it. As Waltz put it on the first page of his Theory of International Politics, in political science “nothing cumulates, not even criticism”. On the other hand, science proceeds funeral by funeral. AI doesn’t need to convert the tenured believers, only to keep bad theories from taking root in the next generation. Just as much theoretical progress can happen when people stop believing old things as when they start believing new ones.

1. That’s where the line between reshuffling old ideas and coming up with new ones gets blurry. If an AI successfully maps evolutionary biology’s fitness landscapes onto institutional lock-in to solve a political economy puzzle, I would suspect that type of cross-pollination is basically indistinguishable from real innovation.