“Endgame safety” for AGI
(Status: no pretense to originality, but a couple people said they found this terminology useful, so I’m sharing it more widely.)
There’s a category of AGI safety work that we might call “Endgame Safety”, where we’re trying to do all the AGI safety work that we couldn’t or didn’t do ahead of time, in the very last moments before (or even after) people are actually playing around with powerful AGI algorithms of the type that could get irreversibly out of control and cause catastrophe.
I think everyone agrees that Endgame Safety is important and unavoidable. If nothing else, for every last line of AGI source code, we can do an analysis of what happens if that line of code has a bug, or if a cosmic ray flips a bit, and how do we write good unit tests, etc. But we’re obviously not going to have AGI source code until the endgame. That was an especially straightforward example, but I imagine that there will be many other things that also fall into the Endgame Safety bucket, i.e. bigger-picture important things to know about AGI that we only realize when we’re in the thick of building it.
So I am not an “Endgame Safety denialist”; I don’t think anyone is. But I find that people are sometimes misled by thinking about Endgame Safety, in the following two ways:
Bad argument 1: “Endgame Safety is really important. So let’s try to make the endgame happen ASAP, so that we can get to work on Endgame Safety!”
This is a bad argument because, what’s the rush? There’s going to be an endgame sooner or later, and we can do Endgame Safety Research then! Bringing the endgame sooner is basically equivalent to having all the AI alignment and strategy researchers hibernate for some number N years, and then wake up and get back to work. And that, in turn, is strictly worse than having all the AI alignment and strategy researchers do what they can during the next N years, and also continue doing work after those N years have elapsed.
I claim that there are plenty of open problems in AGI safety / alignment that we can do right now, that people are in fact working on right now, that seem robustly useful, and that are not in the category of “Endgame Safety”, e.g. my list of 7 projects, these 200 interpretability projects, this list, ELK, everything on Alignment Forum, etc.
For example, sometimes I’ll have this discussion:
ME: “I don’t want to talk about (blah) aspect of how I think future AGI will be built, because all my opinions are either wrong or infohazards—the latter because (if correct) they might substantially speed the arrival of AGI, which gives us less time for safety / alignment research.”
THEM: “WTF dude, I’m an AGI safety / alignment researcher like you! That’s why I’m standing here asking you these questions! And I assure you: if you answer my questions, it will help me do good AGI safety research.”
So there’s my answer. I claim that this person is trying to do Endgame Safety right now, and I don’t want to help them. I think they should find something else to do right now instead, while they wait for some AI researcher to publish an answer to their prerequisite capabilities question. That’s bound to happen sooner or later! Or they can do contingency-planning for each of the possible answers to their capabilities question. Whatever.
Aside: More Sensible Cousin of Bad Argument 1 [but I still strongly disagree with it]: Three steps: “(A) Endgame safety is really the main thing we should be thinking about; (B) Endgame safety will be likelier to succeed if it happens sooner than if it happens later [for one of various possible reasons]; (C) Therefore let’s make the endgame happen ASAP.”
I mainly don’t like this argument because of (A), as elaborated in the next section.
But I also think (B) is problematic. First, why might someone believe (B)? The main argument I’ve seen revolves around the idea that making the endgame happen ASAP minimizes computing overhang, and thus slow takeoff will be likelier, which in turn might make the endgame less of a time-crunch.
I mostly don’t buy this argument because I think it relies on guessing what bottlenecks will hit in what order on the path to AGI—not only for capabilities but also for safety. That kind of guessing seems very difficult. For example, Kaj mentions “more neuroscience understanding” as bad because it shortens the endgame, but couldn’t Kaj have equally well said that “more neuroscience understanding” is exactly the thing we want right now to make the endgame start sooner??
As another example, this is controversial, but I don’t expect that compute will be a bottleneck to fast takeoff, and thus I don’t expect future advances in compute to meaningfully speed the Endgame. I think we already have a massive compute overhang, with current technology, once we know how to make AGI at all. The horse has already left the barn, IMO. See here.
So anyway, I see this whole (B) argument as quite fragile, even leaving aside the (A) issues. And speaking of (A), that brings us to the next item:
Bad argument 2: “Endgame Safety researchers will obviously be in a much better position to do safety / alignment research than we are today, because they’ll know more about how AGI works, and probably have proto-AGI test results, etc. So other things equal, we should move resources from current less-productive safety research to future more-productive Endgame Safety research.”
The biggest problem here is that, while Endgame Safety researchers will be in a better position to make progress in some ways, they’ll be in a much worse position than us in other ways. In particular:
Endgame Safety researchers will be in a severe time crunch thanks to the fact that if they don’t deploy AGI soon, someone less careful probably will.
…And for pretty much anything that you want to do in life, you can’t just make it happen 10× or 100× faster by hiring 10× or 100× more people! (“You can’t produce a baby in one month by getting nine women pregnant.”) In particular:
Conceptual (“deconfusion”) research seems especially likely to require years of wall-clock time (further discussion by Nate Soares).
And even if the conceptual research is going well, spreading those concepts to reach broad consensus might take further years of wall-clock time, especially when the ideas are counterintuitive.
It takes wall-clock time for arguments to be refined, and for evidence to be marshaled, and for pedagogy to be created, etc. It certainly takes a lot of wall-clock time for the stubborn holdouts to die and be replaced by the next generation! And the latter seems to have been necessary in many cases in the past—think of the gradual acceptance of evolution or plate tectonics. In the case of AGI safety, consider that, for example, some AI thought-leaders like Yann LeCun and Jeff Hawkins have continued to say very stupid things about very basic AGI safety concepts for years, despite being smart people who have definitely been exposed to good counterarguments. Clearly we still have work to do!
If it turns out that the path to safety entails building complex supporting tools and infrastructure (e.g. this or this or this), then that likewise takes a certain amount of wall-clock time to spin up, architect, build, test, debug, iterate, etc.
Even leaving aside issues with unwieldy bureaucracies etc., you just can’t hire an unlimited number of people fast without scraping the bottom of the hiring pool, i.e. getting people with less relevant knowledge and competence, and/or who need time-consuming training. (In this sense, spending resources on AGI safety research & pedagogy right now helps enable spending resources on endgame safety, by increasing the number of future people who already have some knowledge about AGI safety, both directly and via outreach / pedagogy efforts.)
Early hints about safety can inform early R&D decisions—including via “Differential Technological Development”. By contrast, once a concrete development path to AGI is widely known and nearing completion, it would be very difficult for any other approach to AGI to catch up to it in a race.
Delaying the deployment of AGI by some number of years is by no means easy right now, but I bet it will be even harder in the endgame, when probably many powerful actors around the world will see a sprint-to-AGI as feasible.
Even if a future Endgame Safety researcher is aware of a failure mode (e.g. deception), and has proto-AGI code right in front of them that reproducibly exhibits that failure mode, that doesn’t mean that they will know how to solve that problem. Or maybe they’ll think they know how to solve it, but actually their plan amounts to building a band-aid that hides the problem while making it worse (e.g. making the deceptive proto-AGI better at not getting caught). And even if they do think of a way to solve the problem, maybe the solution looks like “our whole approach to AGI is wrong; throw it out and rebuild from scratch”, and there won’t be time to do so.
Also, maybe we’re already in the endgame! Maybe there are no important new insights standing between us and AGI. I don’t think that this is the case, but it’s difficult to be super confident about that kind of thing. So we should have people contingency-planning for that.
Aside: More Sensible Cousin of Bad Argument 2: “There are some safety things that we can and should do now, and other safety things that need to get done in the Endgame. We should be planning for both.”
As mentioned at the top, I think this is obviously true.
I’m talking as if there’s a sharp line where things either are or aren’t “Endgame Safety”. More realistically, I’m sure there will be a continuum. I don’t think that matters for anything I’m saying in this post.
I guess I could share information in secret, but let’s assume for the sake of argument that I don’t want to. For example, maybe I don’t know them very well. Or maybe they’re planning to publish their research. (A very reasonable thing to do!) Or maybe secrets are a giant awful mess with tons of negative consequences that I don’t want to burden them with.