Alignment Research = Conceptual Alignment Research + Applied Alignment Research

Instead of talking about alignment research, we should differentiate conceptual alignment research and applied alignment research.

I expect these two categories to be quite obvious to most people around here: conceptual alignment research includes deconfusion, for example work on deception, HCH, universality, abstraction, power-seeking, as well as work searching for approaches and solutions for the problems raised by this deconfusion; whereas applied alignment research focuses on experimentally testing these ideas and adapting already existing fields like RL and DL to be more relevant to alignment questions. Some work will definitely fall in the middle, but that’s not a problem, because the point isn’t to separate “good” from “bad” alignment research or “real” from “fake” alignment research, just to be able to frame these clusters and think about them meaningfully.

Isn’t that decomposition trivial though? It’s indeed obvious, just like the result of almost any deconfusion. And yet, committing to that framing clears the air about so many internal issues of the alignment research community and guards discussions of field-building against frustrating everyone involved.

Thanks to Connor Leahy, Eric Bruylant, Logan Smith and Rob Miles for feedback on a draft.

(Note that the AI tag has a distinction that sounds similar but with in my opinion far worse names (and weird classification). It might make sense to change the names following this post if the distinction makes sense to enough people.)

It’s all a Common-Payoff Game

Another obvious yet fundamental point is that neither conceptual alignment research nor applied alignment research is enough by itself—we need both. Only succeeding in conceptual alignment research would result in a very good abstract understanding of what we should do, but no means of concretely translating it in time; only succeeding in applied alignment research would result in very good ability to build and understand models that are susceptible to alignment yet no principled understanding of what to be careful of and how to steer them.

So it doesn’t make any sense to say that one is more important than the other, or that only one is “real alignment research”. Yet frustration can so easily push one to make this mistake. I personally said in multiple conversations that I was talking about “real alignment research” when talking about conceptual research, only to realize hours later, when the pressure was down, that I didn’t believe at all that the applied part was fake alignment research.

Keeping this split in mind and the complementarity of both approaches definitely helped me avoid frustration-induced lapses where I cast alignment as a zero-sum game between conceptual alignment research and applied alignment research. Instead, I remember the obvious: alignment is a common-payoff game where we all either win or lose together.

Field-Building Confusions

Keeping this distinction in mind also helps with addressing some frustrating confusions in field-building discussions.

Take my post about creating an alignment research journal/​conference: I should have made it clear that I meant conceptual alignment research, but I hadn’t internalized this distinction at the time. Objections like this comment from David Manheim or this comment from Ryan Carey saying that work can get published in ML/​CS venues and we should thus push there didn’t convince me at all, without me being able to put a finger on where my disagreement lay.

The conceptual/​applied alignment research distinction instead makes it jump out of the page: ML conferences and journals almost never publish conceptual alignment research AFAIK (some of it is published in workshops, but these don’t play the same role with regard to peer review and getting jobs and tenure). Take this quote from Ryan’s comment:

Currently, the flow of AIS papers into the likes of Neurips and AAAI (and probably soon JMLR, JAIR) is rapidly improving. New keywords have been created there at several conferences, along the lines of “AI safety and trustworthiness” (I forget the exact wording) so that you can nowadays expect, on average, to receive reviewer who average out to neutral, or even vaguely sympathetic to AIS research. Ten or so papers were published in such journals in the last year, and all these authors will become reviewers under that keyword when the conference comes around next year. Yes, things like “Logical Inductors” or “AI safety via debate” are very hard to publish. There’s some pressure to write research that’s more “normie”. All of that sucks, but it’s an acceptable cost for being in a high-prestige field. And overall, things are getting easier, fairly quickly.

Applying the conceptual/​applied distinction makes obvious that the argument only applies for applied alignment research. He literally gives two big examples of conceptual alignment research as the sort of things that can’t get published.

This matters because none of this is making it easier to peer-review/​scale/​publish conceptual alignment research. It’s not a matter of “normies” research versus “real alignment research”, but that almost all gains in field building and scaling in the last few years are for applied alignment research!

Incentives against Conceptual Alignment Research

I started thinking about all of this because I was so frustrated with having to always push/​defend conceptual alignment research in discussions. Why were so many people pushing back against it/​not seeing the problem that few people work on it? The answer seems obvious in retrospect: because years ago you actually had to push massively against the pull and influence of conceptual alignment research to do anything else.

7 years ago, when Superintelligence was published, MIRI was pretty much the whole field of alignment. And I don’t need to explain to anyone around here how MIRI is squarely in the conceptual part. As such, I’m pretty sure that many researchers who wanted a more varied field or to work on applied alignment research had to constantly deal with the fact that the big shots in town were not convinced/​interested in what they were doing. I expect that much of the applied alignment researchers positioned themselves as an alternative to MIRI’s work.

It made sense at the time, but now applied alignment research has completely dwarfed its conceptual counterpart in terms of researchers, publications, prestige. Why? Because applied alignment research is usually:

  • Within ML compared to the weird abstract positioning of conceptual alignment research

  • Experimental and sometimes formal, compared to the weird philosophical aspects of conceptual alignment research

  • Able to leverage skills that are actually taught in universities and which people are hyped about (programming, ML, data science)

Applied alignment research labs made and are making great progress by leveraging all of these advantages. On the other hand, conceptual alignment research relies entirely on a trickle of new people who bashed their heads long enough against the Alignment Forum to have an idea of what’s happening.

This is not the time for being against conceptual alignment research. Instead, we should all think together about ways of improving this part of the field. And when conceptual alignment research thrives, there will be so many more opportunities for collaborations: experiments on some conceptual alignment concepts, criticism of conceptual ideas from a more concrete perspective, conceptual failures modes for the concrete applied proposals...

Conclusion

You don’t need me to realize that there are two big clusters in alignment research: I call them conceptual alignment research and applied alignment research. But despite how obvious this distinction feels, keeping it in mind is crucial for the only thing that matters: solving the alignment problem.

Appendix: Difference with MIRI’s Philosophy → Maths → Engineering

A commenter pointed out to me that my distinction reminded them of the one argued in this MIRI blogpost. In summary, the post argues that Friendly AI (the old school name for alignment) should be tackled in the same way that causality was: starting at philosophy, then formalizing it into maths, and finally implementing these insights through engineering.

I don’t think this fits with the current state of the field, for the following reasons:

  • Nowadays, the vast majority of the field disagree that there’s any hope of formalizing all of philosophy and then just implementing that to get an aligned AGI.

  • Because of this perspective that the real problem is to formalize philosophy, the MIRI post basically reduces applied alignment research to exact implementation of the formal models from philosophy. Whereas applied alignment research contains far more insights than that.

  • Conceptual alignment research isn’t just turning philosophy into mathematics. This is a failure mode I warned against recently: what matters is deconfusion, not formalization. Some non formal deconfusion can (and so often do) help far more than formal work. This doesn’t mean that having a formalization wouldn’t be great; just that this is in no way a requirement for making progress.

So all in all, I feel that my distinction is both more accurate and more fruitful.