“the thing where it keeps being literally him doing this stuff is quite a bad sign”
I’m a bit confused by this part. Some thoughts on why it seems odd for him (or others) to express that sentiment...
1. I parse the original as, “a collection of EY’s thoughts on why safe AI is hard”. It’s EY’s thoughts, why would someone else (other than @robbensinger) write a collection of EY’s thoughts?
(And if we generalize to asking why no-one else would write about why safe AI is hard, then what about Superintelligence, or the AI stuff in cold-takes, or …?)
2. Was there anything new in this doc? It’s prob useful to collect all in one place, but we don’t ask, “why did no one else write this” for every bit of useful writing out there, right?
Why was it so overwhelmingly important that someone write this summary at this time, that we’re at all scratching our heads about why no one else did it?
My shoulder Eliezer (who I agree with on alignment, and who speaks more bluntly and with less hedging than I normally would) says:
The list is true, to the best of my knowledge, and the details actually matter.
Many civilizations try to make a canonical list like this in 1980 and end up dying where they would have lived just because they left off one item, or under-weighted the importance of the last three sentences of another item, or included ten distracting less-important items.
There are probably not many civilizations that wait until 2022 to make this list, and yet survive.
It’s true that many of the points in the list have been made before. But it’s very doomy that they were made by me.
Nearly all of the field’s active alignment research is predicated on a false assumption that’s contradicted by one of the items in sections A or B. If the field had recognized everything in A and B sooner, we could have put our recent years of effort into work that might actually help on the mainline, as opposed to work that just hopes a core difficulty won’t manifest and has no Plan B for what to do when reality says “no, we’re on the mainline”.
So the answer to ‘Why would someone else write EY’s thoughts?’ is ‘It has nothing to do with an individual’s thoughts; it’s about civilizations needing a very solid and detailed understanding of what’s true on these fronts, or they die’.
Re “(And if we generalize to asking why no-one else would write about why safe AI is hard, then what about Superintelligence, or the AI stuff in cold-takes, or …?)”:
The point is not ‘humanity needs to write a convincing-sounding essay for the thesis Safe AI Is Hard, so we can convince people’. The point is ‘humanity needs to actually have a full and detailed understanding of the problem so we can do the engineering work of solving it’.
If it helps, imagine that humanity invents AGI tomorrow and has to actually go align it now. In that situation, you need to actually be able to do all the requisite work, not just be able to write essays that would make a debate judge go ‘ah yes, well argued.’
When you imagine having water cooler arguments about the importance of AI alignment work, then sure, it’s no big deal if you got a few of the details wrong.
When you imagine actually trying to build aligned AGI the day after tomorrow, I think it comes much more into relief why it matters to get those details right, when the “details” are as core and general as this.
I think that this is a really good exercise that more people should try. Imagine that you’re running a project yourself that’s developing AGI first, in real life. Imagine that you are personally responsible for figuring out how to make the thing go well. Yes, maybe you’re not the perfect person for the job; that’s a sunk cost. Just think about what specific things you would actually do to make things go well, what things you’d want to do to prepare 2 years or 6 years in advance, etc.
Try to think your way into near-mode with regard to AGI development, without thereby assuming (without justification) that it must all be very normal just because it’s near. Be able to visualize it near-mode and weird/novel. If it helps, start by trying to adopt a near-mode, pragmatic, gearsy mindset toward the weirdest realistic/plausible hypothesis first, then progress to the less-weird possibilities.
I think there’s a tendency for EAs and rationalists to instead fall into one of these two mindsets with regard to AGI development, pivotal acts, etc.:
Fun Thought Experiment Mindset. On this mindset, pivotal acts, alignment, etc. are mentally categorized as a sort of game, a cute intellectual puzzle or a neat thing to chat about.
This is mostly a good mindset, IMO, because it makes it easy to freely explore ideas, attend to the logical structure of arguments, brainstorm, focus on gears, etc.
Its main defect is a lack of rigor and a more general lack of drive: because on some level you’re not taking the question seriously, you’re easily distracted by fun, cute, or elegant lines of thought, and you won’t necessarily push yourself to red-team proposals, spontaneously take into account other pragmatic facts/constraints you’re aware of from outside the current conversational locus, etc. The whole exercise sort of floats in a fantasy bubble, rather than being a thing people bring their full knowledge, mental firepower, and lucidity/rationality to bear on.
Serious Respectable Person Mindset. Alternatively, when EAs and rationalists do start taking this stuff seriously, I think they tend to sort of turn off the natural flexibility, freeness, and object-levelness of their thinking, and let their mind go to a very fearful or far-mode place. The world’s gears become a lot less salient, and “Is it OK to say/think that?” becomes a more dominant driver of thought.
Example: In Fun Thought Experiment Mindset, IME, it’s easier to think about governments in a reductionist and unsentimental way, as specific messy groups of people with specific institutional dysfunctions, psychological hang-ups, etc. In Serious Respectable Person Mindset, there’s more of a temptation to go far-mode, glom on to happy-sounding narratives and scenarios, or even just resist the push to concretely visualize the future at all—thinking instead in terms of abstract labels and normal-sounding platitudes.
The entire fact that EA and rationalism mostly managed to avert their gaze from the concept of “pivotal acts” for years, is in my opinion an example of how these two mindsets often fail.
“In the endgame, AGI will probably be pretty competitive, and if a bunch of people deploy AGI then at least one will destroy the world” is a thing I think most LWers and many longtermist EAs would have considered obvious. As a community, however, we mostly managed to just-not-think the obvious next thought, “In order to prevent the world’s destruction in this scenario, one of the first AGI groups needs to find some fast way to prevent the proliferation of AGI.”
Fun Thought Experiment Mindset, I think, encouraged this mental avoidance because it thought of AGI alignment (to some extent) as a fun game in the genre of “math puzzle” or “science fiction scenario”, not as a pragmatic, real-world dilemma we actually have to solve, taking into account all of our real-world knowledge and specific facts on the ground. The ‘rules of the game’, many people apparently felt, were to think about certain specific parts of the action chain leading up to an awesome future lightcone, rather than taking ownership of the entire problem and trying to figure out what humanity should in-real-life do, start to finish.
(What primarily makes this weird is that many alignment questions crucially hinge on ‘what task are we aligning the AGI on?’. These are not remotely orthogonal topics.)
Serious Respectable Person Mindset, I think, encouraged this mental avoidance more actively, because pivotal acts are a weird and scary-sounding idea once you leave ‘these are just fun thought experiments’ land.
What I’d like to see instead is something like Weirdness-Tolerant Project Leader Mindset, or Thought Experiments Plus Actual Rigor And Pragmatism And Drive Mindset, or something.
I think a lot of the confusion around EY’s post comes from the difference between thinking of these posts (on some level) as fun debate fodder or persuasion/outreach tools, versus attending to the fact that humanity has to actually align AGI systems if we’re going to make it out of this problem, and this is an attempt by humanity to distill where we’re currently at, so we can actually proceed to go solve alignment right now and save the world.
Imagine that this is v0 of a series of documents that need to evolve into humanity’s (/ some specific group’s) actual business plan for saving the world. The details really, really matter. Understanding the shape of the problem really matters, because we need to engineer a solution, not just ‘persuade people to care about AI risk’.
If you disagree with the OP… that’s pretty important! Share your thoughts. If you agree, that’s important to know too, so we can prioritize some disagreements over others and zero in on critical next actions. There’s a mindset here that I think is important, that isn’t about “agree with Eliezer on arbitrary topics” or “stop thinking laterally”; it’s about approaching the problem seriously, neither falling into despair nor wishful thinking, neither far-mode nor forced normality, neither impracticality nor propriety.
“In the endgame, AGI will probably be pretty competitive, and if a bunch of people deploy AGI then at least one will destroy the world” is a thing I think most LWers and many longtermist EAs would have considered obvious.
I think that many AI alignment researchers just have a different development model than this, where world-destroying AGIs don’t emerge suddenly from harmless low-impact AIs, no one project gets a vast lead over competitors, there’s lots of early evidence of misalignment and (if alignment is harder) many smaller scale disasters in the lead up to any AI that is capable of destroying the world outright. See e.g. Paul’s What failure looks like.
On this view, the idea that there’ll be a lead project with a very short time window to execute a single pivotal act is wrong, and instead the ‘pivotal act’ is spread out and about making sure the aligned projects have a lead over the rest, and that failures from unaligned projects are caught early enough for long enough (by AIs or human overseers), for the leading projects to become powerful and for best practices on alignment to be spread universally.
Basically, if you find yourself in the early stages of WFLL2 and want to avert doom, what you need to do is get better at overseeing your pre-AGI AIs, not build an AGI to execute a pivotal act. This was pretty much what Richard Ngo was arguing for in most of the MIRI debates with Eliezer, and also I think it’s what Paul was arguing for. And obviously, Eliezer thought this was insufficient, because he expects alignment to be much harder and takeoff to be much faster.
But I think that’s the reason a lot of alignment researchers haven’t focussed on pivotal acts: because they think a sudden, fast-moving single pivotal act is unnecessary in a slow takeoff world. So you can’t conclude just from the fact that most alignment researchers don’t talk in terms of single pivotal acts that they’re not thinking in near mode about what actually needs to be done.
However, I do think that what you’re saying is true of a lot of people—many people I speak to just haven’t thought about the question of how to ensure overall success, either in the slow takeoff sense I’ve described or the Pivotal Act sense. I think people in technical research are just very unused to thinking in such terms, and AI governance is still in its early stages.
I agree that on this view it still makes sense to say, ‘if you somehow end up that far ahead of everyone else in an AI takeoff then you should do a pivotal act’, like Scott Alexander said:
That is, if you are in a position where you have the option to build an AI capable of destroying all competing AI projects, the moment you notice this you should update heavily in favor of short timelines (zero in your case, but everyone else should be close behind) and fast takeoff speeds (since your AI has these impressive capabilities). You should also update on existing AI regulation being insufficient (since it was insufficient to prevent you)
But I don’t think you learn all that much about how ‘concrete and near mode’ researchers who expect slower takeoff are being, from them not having given much thought to what to do in this (from their perspective) unlikely edge case.
But I don’t think you learn all that much about how ‘concrete and near mode’ researchers who expect slower takeoff are being, from them not having given much thought to what to do in this (from their perspective) unlikely edge case.
I’m not sure how many researchers assign little enough credence to fast takeoff that they’d describe it as an unlikely edge case, which sounds like <=10%? e.g in Paul’s blog post he writes “I’m around 30% of fast takeoff”
ETA: One proxy could be what percentage researchers assigned to “Superintelligence” in this survey
I don’t think what Paul means by fast takeoff is the same thing as the sort of discontinous jump that would enable a pivotal act. I think fast for Paul just means the negation of Paul-slow: ‘no four year economic doubling before one year economic doubling’. But whatever Paul thinks the survey respondents did give at least 10% to scenarios where a pivotal act is possible.
Even so, ‘this isn’t how I expect things to to on the mainline so I’m not going to focus on what to do here’ is far less of a mistake than ‘I have no plan for what to do on my mainline’, and I think the researchers who ignored pivotal acts are mostly doing the first one
Great comment. Perhaps it would be helpful to explicitly split the analysis by assumptions about takeoff speed? It seems that conditional on takeoff speed, there’s not much disagreement.
At least for me, I thought we should avoid talking about the pivotal act stuff through a combination of a) this is obviously an important candidate hypothesis but seems bad to talk about because then the Bad Guys will Get Ideas and b) other people who’re better at math/philosophy/alignment presumably know this and are privately considering it in detail, I have only so much to contribute here.
b) is plausibly a dereliction of duty, as is my relative weighting of the terms, but at least in my head it wasn’t (isn’t?) obvious to me that it was wrong for me not to spend a ton of time thinking about pivotal acts.
I think that makes sense as a worry, but I think EAs’ caution and reluctance to model-build and argue about this stuff has turned out to do more harm than good, so we should change tactics. (And we very probably should have done things differently from the get-go.)
If you’re worried that it’s dangerous to talk about something publicly, I’d start off by thinking about it privately and talking about it over Signal with friends, etc. Then you can progress to contacting more EAs privately, then to posting publicly, as it becomes increasingly clear “there’s real value in talking about this stuff” and “there’s not a strong-enough reason to keep quiet”.
Step one in doing that, though, has to be a willingness to think about the topic at all, even if there isn’t clear public social proof that this is a normal or “approved” direction to think in. I think a thing that helps here is to recognize how small the group of “EA leaders and elite researchers” is, how divided their attention is between hundreds of different tasks and subtasks, and how easy it is for many things to therefore fall through the cracks or just-not-happen.
On Twitter, Eric Rogstad wrote:
Copying over my reply to Eric:
I think that this is a really good exercise that more people should try. Imagine that you’re running a project yourself that’s developing AGI first, in real life. Imagine that you are personally responsible for figuring out how to make the thing go well. Yes, maybe you’re not the perfect person for the job; that’s a sunk cost. Just think about what specific things you would actually do to make things go well, what things you’d want to do to prepare 2 years or 6 years in advance, etc.
Try to think your way into near-mode with regard to AGI development, without thereby assuming (without justification) that it must all be very normal just because it’s near. Be able to visualize it near-mode and weird/novel. If it helps, start by trying to adopt a near-mode, pragmatic, gearsy mindset toward the weirdest realistic/plausible hypothesis first, then progress to the less-weird possibilities.
I think there’s a tendency for EAs and rationalists to instead fall into one of these two mindsets with regard to AGI development, pivotal acts, etc.:
Fun Thought Experiment Mindset. On this mindset, pivotal acts, alignment, etc. are mentally categorized as a sort of game, a cute intellectual puzzle or a neat thing to chat about.
This is mostly a good mindset, IMO, because it makes it easy to freely explore ideas, attend to the logical structure of arguments, brainstorm, focus on gears, etc.
Its main defect is a lack of rigor and a more general lack of drive: because on some level you’re not taking the question seriously, you’re easily distracted by fun, cute, or elegant lines of thought, and you won’t necessarily push yourself to red-team proposals, spontaneously take into account other pragmatic facts/constraints you’re aware of from outside the current conversational locus, etc. The whole exercise sort of floats in a fantasy bubble, rather than being a thing people bring their full knowledge, mental firepower, and lucidity/rationality to bear on.
Serious Respectable Person Mindset. Alternatively, when EAs and rationalists do start taking this stuff seriously, I think they tend to sort of turn off the natural flexibility, freeness, and object-levelness of their thinking, and let their mind go to a very fearful or far-mode place. The world’s gears become a lot less salient, and “Is it OK to say/think that?” becomes a more dominant driver of thought.
Example: In Fun Thought Experiment Mindset, IME, it’s easier to think about governments in a reductionist and unsentimental way, as specific messy groups of people with specific institutional dysfunctions, psychological hang-ups, etc. In Serious Respectable Person Mindset, there’s more of a temptation to go far-mode, glom on to happy-sounding narratives and scenarios, or even just resist the push to concretely visualize the future at all—thinking instead in terms of abstract labels and normal-sounding platitudes.
The entire fact that EA and rationalism mostly managed to avert their gaze from the concept of “pivotal acts” for years, is in my opinion an example of how these two mindsets often fail.
“In the endgame, AGI will probably be pretty competitive, and if a bunch of people deploy AGI then at least one will destroy the world” is a thing I think most LWers and many longtermist EAs would have considered obvious. As a community, however, we mostly managed to just-not-think the obvious next thought, “In order to prevent the world’s destruction in this scenario, one of the first AGI groups needs to find some fast way to prevent the proliferation of AGI.”
Fun Thought Experiment Mindset, I think, encouraged this mental avoidance because it thought of AGI alignment (to some extent) as a fun game in the genre of “math puzzle” or “science fiction scenario”, not as a pragmatic, real-world dilemma we actually have to solve, taking into account all of our real-world knowledge and specific facts on the ground. The ‘rules of the game’, many people apparently felt, were to think about certain specific parts of the action chain leading up to an awesome future lightcone, rather than taking ownership of the entire problem and trying to figure out what humanity should in-real-life do, start to finish.
(What primarily makes this weird is that many alignment questions crucially hinge on ‘what task are we aligning the AGI on?’. These are not remotely orthogonal topics.)
Serious Respectable Person Mindset, I think, encouraged this mental avoidance more actively, because pivotal acts are a weird and scary-sounding idea once you leave ‘these are just fun thought experiments’ land.
What I’d like to see instead is something like Weirdness-Tolerant Project Leader Mindset, or Thought Experiments Plus Actual Rigor And Pragmatism And Drive Mindset, or something.
I think a lot of the confusion around EY’s post comes from the difference between thinking of these posts (on some level) as fun debate fodder or persuasion/outreach tools, versus attending to the fact that humanity has to actually align AGI systems if we’re going to make it out of this problem, and this is an attempt by humanity to distill where we’re currently at, so we can actually proceed to go solve alignment right now and save the world.
Imagine that this is v0 of a series of documents that need to evolve into humanity’s (/ some specific group’s) actual business plan for saving the world. The details really, really matter. Understanding the shape of the problem really matters, because we need to engineer a solution, not just ‘persuade people to care about AI risk’.
If you disagree with the OP… that’s pretty important! Share your thoughts. If you agree, that’s important to know too, so we can prioritize some disagreements over others and zero in on critical next actions. There’s a mindset here that I think is important, that isn’t about “agree with Eliezer on arbitrary topics” or “stop thinking laterally”; it’s about approaching the problem seriously, neither falling into despair nor wishful thinking, neither far-mode nor forced normality, neither impracticality nor propriety.
I think that many AI alignment researchers just have a different development model than this, where world-destroying AGIs don’t emerge suddenly from harmless low-impact AIs, no one project gets a vast lead over competitors, there’s lots of early evidence of misalignment and (if alignment is harder) many smaller scale disasters in the lead up to any AI that is capable of destroying the world outright. See e.g. Paul’s What failure looks like.
On this view, the idea that there’ll be a lead project with a very short time window to execute a single pivotal act is wrong, and instead the ‘pivotal act’ is spread out and about making sure the aligned projects have a lead over the rest, and that failures from unaligned projects are caught early enough for long enough (by AIs or human overseers), for the leading projects to become powerful and for best practices on alignment to be spread universally.
Basically, if you find yourself in the early stages of WFLL2 and want to avert doom, what you need to do is get better at overseeing your pre-AGI AIs, not build an AGI to execute a pivotal act. This was pretty much what Richard Ngo was arguing for in most of the MIRI debates with Eliezer, and also I think it’s what Paul was arguing for. And obviously, Eliezer thought this was insufficient, because he expects alignment to be much harder and takeoff to be much faster.
But I think that’s the reason a lot of alignment researchers haven’t focussed on pivotal acts: because they think a sudden, fast-moving single pivotal act is unnecessary in a slow takeoff world. So you can’t conclude just from the fact that most alignment researchers don’t talk in terms of single pivotal acts that they’re not thinking in near mode about what actually needs to be done.
However, I do think that what you’re saying is true of a lot of people—many people I speak to just haven’t thought about the question of how to ensure overall success, either in the slow takeoff sense I’ve described or the Pivotal Act sense. I think people in technical research are just very unused to thinking in such terms, and AI governance is still in its early stages.
I agree that on this view it still makes sense to say, ‘if you somehow end up that far ahead of everyone else in an AI takeoff then you should do a pivotal act’, like Scott Alexander said:
But I don’t think you learn all that much about how ‘concrete and near mode’ researchers who expect slower takeoff are being, from them not having given much thought to what to do in this (from their perspective) unlikely edge case.
I’m not sure how many researchers assign little enough credence to fast takeoff that they’d describe it as an unlikely edge case, which sounds like <=10%? e.g in Paul’s blog post he writes “I’m around 30% of fast takeoff”
ETA: One proxy could be what percentage researchers assigned to “Superintelligence” in this survey
I don’t think what Paul means by fast takeoff is the same thing as the sort of discontinous jump that would enable a pivotal act. I think fast for Paul just means the negation of Paul-slow: ‘no four year economic doubling before one year economic doubling’. But whatever Paul thinks the survey respondents did give at least 10% to scenarios where a pivotal act is possible.
Even so, ‘this isn’t how I expect things to to on the mainline so I’m not going to focus on what to do here’ is far less of a mistake than ‘I have no plan for what to do on my mainline’, and I think the researchers who ignored pivotal acts are mostly doing the first one
Great comment. Perhaps it would be helpful to explicitly split the analysis by assumptions about takeoff speed? It seems that conditional on takeoff speed, there’s not much disagreement.
At least for me, I thought we should avoid talking about the pivotal act stuff through a combination of a) this is obviously an important candidate hypothesis but seems bad to talk about because then the Bad Guys will Get Ideas and b) other people who’re better at math/philosophy/alignment presumably know this and are privately considering it in detail, I have only so much to contribute here.
b) is plausibly a dereliction of duty, as is my relative weighting of the terms, but at least in my head it wasn’t (isn’t?) obvious to me that it was wrong for me not to spend a ton of time thinking about pivotal acts.
I think that makes sense as a worry, but I think EAs’ caution and reluctance to model-build and argue about this stuff has turned out to do more harm than good, so we should change tactics. (And we very probably should have done things differently from the get-go.)
If you’re worried that it’s dangerous to talk about something publicly, I’d start off by thinking about it privately and talking about it over Signal with friends, etc. Then you can progress to contacting more EAs privately, then to posting publicly, as it becomes increasingly clear “there’s real value in talking about this stuff” and “there’s not a strong-enough reason to keep quiet”.
Step one in doing that, though, has to be a willingness to think about the topic at all, even if there isn’t clear public social proof that this is a normal or “approved” direction to think in. I think a thing that helps here is to recognize how small the group of “EA leaders and elite researchers” is, how divided their attention is between hundreds of different tasks and subtasks, and how easy it is for many things to therefore fall through the cracks or just-not-happen.