Quick note: I occasionally run into arguments of the form "my research advances capabilities, but it advances alignment more than it advances capabilities, so it's good on net". I do not buy this argument, and think that in most such cases, this sort of research does more harm than good. (Cf. differential technological development.)

For a simplified version of my model as to why:

  • Suppose that aligning an AGI requires 1000 person-years of research.
    • 900 of these person-years can be done in parallelizable 5-year chunks (e.g., by 180 people over 5 years — or, more realistically, by 1800 people over 10 years, with 10% of the people doing the job correctly half the time).
    • The remaining 100 of these person-years factor into four chunks that take 25 serial years apiece (so that you can't get any of those four parts done in less than 25 years).

In this toy model, a critical resource is serial time: if AGI is only 26 years off, then shortening overall timelines by 2 years is a death sentence, even if you're getting all 900 years of the "parallelizable" research done in exchange.

My real model of the research landscape is more complex than this toy picture, but I do in fact expect that serial time is a key resource when it comes to AGI alignment.

The most blatant case of alignment work that seems parallelizable to me is that of "AI psychologizing": we can imagine having enough success building comprehensible minds, and enough success with transparency tools, that with a sufficiently large army of people studying the alien mind, we can develop a pretty good understanding of what and how it's thinking. (I currently doubt we'll get there in practice, but if we did, I could imagine most of the human-years spent on alignment-work being sunk into understanding the first artificial mind we get.)

The most blatant case of alignment work that seems serial to me is work that requires having a theoretical understanding of minds/optimization/whatever, or work that requires having just the right concepts for thinking about minds. Relative to our current state of knowledge, it seems to me that a lot of serial work is plausibly needed in order for us to understand how to safely and reliably aim AGI systems at a goal/task of our choosing.

A bunch of modern alignment work seems to me to sit in some middle-ground. As a rule of thumb, alignment work that is closer to behavioral observations of modern systems is more parallelizable (because you can have lots of people making those observations in parallel), and alignment work that requires having a good conceptual or theoretical framework is more serial (because, in the worst case, you might need a whole new generation of researchers raised with a half-baked version of the technical framework, in order to get people who both have enough technical clarity to grapple with the remaining confusions, and enough youth to invent a whole new way of seeing the problem—a pattern which seems common to me in my read of the development of things like analysis, meta-mathematics, quantum physics, etc.).

As an egregious and fictitious (but "based on a true story") example of the arguments I disagree with, consider the following dialog:


Uncharacteristically conscientious capabilities researcher: Alignment is made significantly trickier by the fact that we do not have an artificial mind in front of us to study. By doing capabilities research now (and being personally willing to pause when we get to the brink), I am making it more possible to do alignment research.

Me: Once humanity gets to the brink, I doubt we have much time left. (For a host of reasons, including: simultaneous discovery; the way the field seems to be on a trajectory to publicly share most of the critical AGI insights, once it has them, before wisening up and instituting closure policies after it's too late; Earth's generally terrible track-record in cybersecurity; and a sense that excited people will convince themselves it's fine to plow ahead directly over the cliff-edge.)

Uncharacteristically conscientious capabilities researcher: Well, we might not have many sidereal years left after we get to the brink, but we'll have many, many more researcher years left. The top minds of the day will predictably be much more interested in alignment work when there's an actual misaligned artificial mind in front of them to study. And people will take these problems much more seriously once they're near-term. And the monetary incentives for solving alignment will be much more visibly present. And so on and so forth.

Me: Setting aside how I believe that the world is derpier than that: even if you were right, I still think we'd be screwed in that scenario. In particular, that scenario seems to me to assume that there is not much serial research labor needed to do alignment research.

Like, I think it's quite hard to get something akin to Einstein's theory of general relativity, or Grothendieck's simplification of algebraic geometry, without having some researcher retreat to a mountain lair for a handful of years to build/refactor/distill/reimagine a bunch of the relevant concepts.

And looking at various parts of the history of math and science, it looks to me like technical fields often move forwards by building up around subtly-bad framings and concepts, so that a next generation can be raised with enough technical machinery to grasp the problem and enough youth to find a whole new angle of attack, at which point new and better framings and concepts are invented to replace the old. "A new scientific truth does not triumph by convincing its opponents and making them see the light, but rather because its opponents eventually die and a new generation grows up that is familiar with it" (Max Planck) and all that.

If you need the field to iterate in that sort of way three times before you can see clearly enough to solve alignment, you're going to be hard-pressed to do that in five years no matter how big and important your field seems once you get to the brink.

(Even the 25 years in the toy model above feels pretty fast, to me, for that kind of iteration, and signifies my great optimism in what humanity is capable of doing in a rush when the whole universe is on the line.)


It looks to me like alignment requires both a bunch of parallelizable labor and a bunch of serial labor. I expect us to have very little serial time (a handful of years if we're lucky) after we have fledgling AGI.

When I've heard the “two units of alignment progress for one unit of capabilities progress” argument, my impression is that it's been made by people who are burning serial time in order to get a bit more of the parallelizable alignment labor done.

But the parallelizable alignment labor is not the bottleneck. The serial alignment labor is the bottleneck, and it looks to me like burning time to complete that is nowhere near worth the benefits in practice.


Some nuance I'll add:

I feel relatively confident that a large percentage of people who do capabilities work at OpenAI, FAIR, DeepMind, Anthropic, etc. with justifications like "well, I'm helping with alignment some too" or "well, alignment will be easier when we get to the brink" (more often EA-adjacent than centrally "EA", I think) are currently producing costs that outweigh the benefits.

Some relatively niche and theoretical agent-foundations-ish research directions might yield capabilities advances too, and I feel much more positive about those cases. I’m guessing it won’t work, but it’s the kind of research that seems positive-EV to me and that I’d like to see a larger network of researchers tackling, provided that they avoid publishing large advances that are especially likely to shorten AGI timelines.

The main reasons I feel more positive about the agent-foundations-ish cases I know about are:

  • The alignment progress in these cases appears to me to be much more serial, compared to the vast majority of alignment work the field outputs today.
  • I’m more optimistic about the total amount of alignment progress we’d see in the worlds where agent-foundations-ish research so wildly exceeded my expectations that it ended up boosting capabilities. Better understanding optimization in this way really would seem to me to take a significant bite out of the capabilities generalization problem, unlike most alignment work I’m aware of.
  • The kind of people working on agent-foundations-y work aren’t publishing new ML results that break SotA. Thus I consider it more likely that they’d avoid publicly breaking SotA on a bunch of AGI-relevant benchmarks given the opportunity, and more likely that they’d only direct their attention to this kind of intervention if it seemed helpful for humanity’s future prospects.[1]
  • Relatedly, the energy and attention of ML is elsewhere, so if they do achieve a surprising AGI-relevant breakthrough and accidentally leak bits about it publicly, I put less probability on safety-unconscious ML researchers rushing to incorporate it.

I’m giving this example not to say “everyone should go do agent-foundations-y work exclusively now!”. I think it’s a neglected set of research directions that deserves far more effort, but I’m far too pessimistic about it to want humanity to put all its eggs in that basket.

Rather, my hope is that this example clarifies that I’m not saying “doing alignment research is bad” or even “all alignment research that poses a risk of advancing capabilities is bad”. I think that in a large majority of scenarios where humanity’s long-term future goes well, it mainly goes well because we made major alignment progress over the coming years and decades.[2] I don’t want this post to be taken as an argument against what I see as humanity’s biggest hope: figuring out AGI alignment.


 

  1. ^

    On the other hand, weirder research is more likely to shorten timelines a lot, if it shortens them at all. More mainstream research progress is less likely to have a large counterfactual impact, because it’s more likely that someone else has the same idea a few months or years later.

    “Low probability of shortening timelines a lot” and “higher probability of shortening timelines a smaller amount” both matter here, so I advocate that both niche and mainstream researchers be cautious and deliberate about publishing potentially timelines-shortening work.

  2. ^

    "Decades" would require timelines to be longer than my median. But when I condition on success, I do expect we have more time.

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How do you think about empirical work on scalable oversight? A lot of scalable oversight methods do result in capabilities improvements if they work well. A few concrete examples where this might be the case:

  1. Learning from Human Feedback
  2. Debate
  3. Iterated Amplification
  4. Imitative Generalization

I'm curious which of the above you think it's net good/bad to get working (or working better) in practice. I'm pretty confused about how to think about work on the above methods; they're on the main line path for some alignment agendas but also advanced capabilities / reduce serial time to work on the other alignment agendas.

I tend to agree that burning up the timeline is highly costly, but more because Effective Altruism is an Idea Machine that has only recently started to really crank up. There's a lot of effort being directed towards recruiting top students from uni groups, but these projects require time to pay off.

I’m giving this example not to say “everyone should go do agent-foundations-y work exclusively now!”. I think it’s a neglected set of research directions that deserves far more effort, but I’m far too pessimistic about it to want humanity to put all its eggs in that basket.

If it is the case that more people should go into Agent Foundations research then perhaps MIRI should do more to enable it?

Suppose that aligning an AGI requires 1000 person-years of research.

  • 900 of these person-years can be done in parallelizable 5-year chunks (e.g., by 180 people over 5 years — or, more realistically, by 1800 people over 10 years, with 10% of the people doing the job correctly half the time).
  • The remaining 100 of these person-years factor into four chunks that take 25 serial years apiece (so that you can't get any of those four parts done in less than 25 years).

 

Do you have a similar model for just building (unaligned) AGI? Or is the model meaningfully different? On a similar model for just building AGI, then timelines would mostly be shortened by progressing through the serial research-person-years instead of the parallelisable research-person-years. If researchers who are progressing both capabilities and aligning are doing both in the parallelisable part, then this would be less worrying, as they're not actually shortening timelines meaningfully.

 

Unfortunately I imagine you think that building (unaligned) AGI quite probably doesn't have many more serial person-years of research required, if any. This is possibly another way of framing the prosaic AGI claim: "we expect we can get to AGI without any fundamentally new insights on intelligence, using (something like) current methods."

I like the distinction between parallelizable and serial research time, and agree that there should be a very high bar for shortening AI timelines and eating up precious serial time.

One caveat to the claim that we should prioritize serial alignment work over parallelizable work, is that this assumes an omniscient and optimal allocator of researcher-hours to problems. Insofar as this assumption doesn't hold (because our institutions fail, or because the knowledge about how to allocate researcher-hours itself depends on the outcomes of parallelizable research) the distinction between parallelizable and serial work breaks down and other considerations dominate.

One caveat to the claim that we should prioritize serial alignment work over parallelizable work, is that this assumes an omniscient and optimal allocator of researcher-hours to problems.

Why do you think it assumes that?

Also, on a re-read I notice that all the examples given in the post relate to mathematics or theoretical work, which is almost uniquely serial among human activities. By contrast, engineering disciplines are typically much more parallelizable, as evidenced by the speedup in technological progress during war-time.

This isn't a coincidence; the state of alignment knowledge is currently "we have no idea what would be involved in doing it even in principle, given realistic research paths and constraints", very far from being a well-specified engineering problem. Cf. https://intelligence.org/2013/11/04/from-philosophy-to-math-to-engineering/.

If you succeed at the framework-inventing "how does one even do this?" stage, then you can probably deploy an enormous amount of engineering talent in parallel to help with implementation, small iterative improvements, building-upon-foundations, targeting-established-metrics, etc. tasks.

FWIW, I had a mildly negative reaction to this title. I agree with you, but I feel like the term "PSA" should be reserved for things that are really very straightforward and non-controversial, and I feel like it's a bit of a bad rhetorical technique to frame your arguments as a PSA. I like the overall content of the post, but feel like a self-summarizing post title like "Most AI Alignment research is not parallelizable" would be better.