# We won't solve post-alignment problems by doing research

## Introduction

Even if we solve the AI alignment problem, we still face **post-alignment problems**, which are all the other existential problems[^3] that AI may bring.

People have written research agendas on various imposing problems that we are nowhere close to solving, and that we may need to solve before developing ASI. An incomplete list of topics: [misuse](https://longtermrisk.org/overview-of-transformative-ai-misuse-risks-what-could-go-wrong-beyond-misalignment/); [animal-inclusive AI](https://forum.effectivealtruism.org/posts/2cZAzvaQefh5JxWdb/bringing-about-animal-inclusive-ai); [AI welfare](https://eleosai.org/post/research-priorities-for-ai-welfare/); [S-risks from conflict](https://longtermrisk.org/research-agenda); [gradual disempowerment](https://www.lesswrong.com/posts/GAv4DRGyDHe2orvwB/gradual-disempowerment-concrete-research-projects); [permanent mass unemployment](https://arxiv.org/html/2502.07050v1); [risks from malevolent actors](https://forum.effectivealtruism.org/posts/LpkXtFXdsRd4rG8Kb/reducing-long-term-risks-from-malevolent-actors); [moral error](https://forum.effectivealtruism.org/posts/HqmQMmKgX7nfSLaNX/moral-error-as-an-existential-risk).

The standard answer to these problems, the one that most research agendas take for granted, is "do research". Specifically, do research in the conventional way where you create a research agenda, explore some research questions, and fund other people to work on those questions.

If transformative AI arrives within the next decade, then we won't solve post-alignment problems by doing research on how to solve them.

These problems are thorny, to put it mildly. They're the sorts of problems where you have no idea how much progress you're making or how much work it will take. I can think of analogous philosophical problems that have seen depressingly little progress in 300 years. I don't expect to see meaningful progress in the next 10.

Beyond that, there are multiple post-alignment problems. The future could be catastrophic if we get even one of them wrong. Most lines of research only address one out of the many problems. We might get lucky and solve one major post-alignment problem before transformative AI arrives, but it's extremely unlikely that we solve all of them.

Instead of directly working on post-alignment problems, we should be working on how to increase the probability that post-alignment problems get solved.

This essay will consider four ways to do that:

1. Do meta-research on what research topics are most likely to help with all post-alignment problems simultaneously.
2. Pause frontier AI development until we know how to solve post-alignment problems (and the alignment problem too).
3. Develop human-level "assistant" AI first, then leverage AI to solve post-alignment problems.
4. Steer AI development such that an autonomous ASI is more likely to solve post-alignment problems.

**If you're working on post-alignment problems, and especially if you're writing a research agenda, then don't take it for granted that "do direct research" is the right solution.** If that's what you believe, then support that position with argument. At minimum, I would like to see more post-alignment researchers engage with the question of what to do if timelines are short or progress is intractable.

*Edited 2026-03-23 to rename from "non-alignment problems" to "post-alignment problems". I'm still not satisfied with this name, but I'm told that it's less confusing.*

*Cross-posted from [my website](https://mdickens.me/2025/11/20/research_wont_solve_non-alignment_problems/).*


## Approach 1: Meta-research on what approach to use

That's what this essay is. Meta-research is useful insofar as it's unclear what approach to take, but it has rapidly diminishing utility because at some point we need to pick some strategy and pursue it (especially given short timelines).

I'd like to see more meta-research on whether there are any promising approaches that this essay did not consider.

## Approach 2: Pause AI

The case for pausing to mitigate post-alignment risks is similar to the case for alignment risk: we don't know how to make ASI safe, so we shouldn't build it until we do. The counter-arguments are also the same: a global pause is hard to achieve; a partial pause may be worse than no pause; etc.

However, in the context of post-alignment problems, the case for pausing AI is **stronger** in one way, and **weaker** in another way.

It is **stronger** in that AI companies mostly don't care about post-alignment problems. They *do* care about the alignment problem and are actively working to solve it. Some people are optimistic about their chances—I'm not, but insofar as you expect companies to solve alignment without a pause, a pause looks less important. But companies are ignoring post-alignment problems and almost certainly won't solve them on the current trajectory.

(I also believe that companies will almost certainly not solve the alignment problem; but that's a harder position to argue for, whereas it's clear that AI companies are not even working on post-alignment problems. (Except for Anthropic, which is putting in a weak effort on a subset of the problems, e.g. AI welfare.))

The case for pausing is **weaker** in that it might not increase our chances of solving post-alignment problems. Human beings mostly don't care about topics like AI welfare, wild animal welfare, or AIs torturing simulations of people for weird game-theoretic reasons. An aligned ASI, even if it's not intentionally directed at solving post-alignment problems, might do a better job than humans would.

## Approach 3: Develop human-level AI first, then (maybe) pause

An alternative approach: Don't pause yet. First develop human-level AI that can help us solve the world's major problems. Don't develop superintelligence until we're on stable ground philosophically, but still take advantage of the productivity boost that AI provides.

This plan doesn't help with misalignment or misuse risks—the human-level AI must be aligned (enough), and it must refuse to perform unethical tasks and be impossible to jailbreak. But it could help with other post-alignment risks.

This plan still requires pausing AI development at some point. In this scenario, it is critically important that we succeed at pausing AI before an intelligence explosion. Therefore, if this is our strategy, then the best thing to do today is to lay the necessary groundwork for a pause.

In an alternative version of this plan, we don't ever pause AI development. Instead, we squeeze the "solve-every-problem" step into the time gap between "AI dramatically boosts productivity" and "AI has total control of the future". This only works if post-alignment problems turn out to be much easier to solve than they look.

Another concern—shared with the [plan below](#Approach_4__Research_how_to_steer_ASI_toward_solving_post_alignment_problems)—is that it seems infeasible to build AIs that are differentially good at philosophy. Philosophy might not be the *single* hardest thing to get AIs to be good at, but AI will be worse at philosophy than at AI research; therefore, by default, we get an intelligence explosion before we solve the necessary philosophical problems.

## Approach 4: Research how to steer ASI toward solving post-alignment problems

Most of the post-alignment problems listed in this essay are different flavors of "we get ethics wrong" or "we make important philosophical mistakes". What if we can get a sufficiently smart AI to solve philosophy for us?

Four concerns with this research agenda:

1. "Solve philosophy" is not the same thing as "implement the correct philosophy", and we need the AI to bridge that gap. There is a near-consensus among moral philosophers that factory farming is wrong, yet it persists. An ASI that solves ethics would need to do the ethically correct thing, rather than the thing people want it to do.[^4]
2. Philosophy is exceptionally hard to train AIs on. You can't steer training effectively because we don't know how to judge the quality of philosophical output.[^2]
3. To my knowledge, zero people are working on this full-time. Even if there's a way to do it, it won't happen without a major shift in research priorities.
4. Even if you do come up with some useful ideas, you have to get AI companies to implement your ideas. This will be difficult if a "philosophy AI" requires a significantly different training paradigm.

## Conclusion

On balance, I believe pausing AI is the best answer to post-alignment problems. I have doubts about whether a pause is achievable, and whether it would even help; but my doubts about the other answers are even stronger.


[^2]: Particularly on the upper end, which is where it matters. Experts can judge that Kant is better than a philosophy undergrad, but can they judge whether Kant is better than Hume? To solve all post-alignment problems, we will need philosophical research of *better* quality than what Kant or Hume produced.

[^3]: Existential in the classic sense of "failing to realize sentient life's potential".

[^4]: h/t Justis Mills for raising this concern.