That still seems dangerous to me, since I see no reason to believe it wouldn’t end up optimizing for something we didn’t want. I guess you would have a theory of optimization and agents so good you could know that it wouldn’t optimize in ways you didn’t want it to
In my head, the theory + implementation ensures that all of the optimization is pointed toward the goal “try to help the human”. If you could then legitimately say “it could still end up optimizing for something else”, then we don’t have the right theory + implementation as I’m imagining it.
but I think this also begs the question by hiding details in “want” that would ultimately require a sufficient theory of human preferences.
I think it’s hiding details in “optimization”, “try” and “help” (and to a lesser extent, “human”). I don’t think it’s hiding details in “want”. You could maybe argue that any operationalization of “help” would necessarily have “want” as a prerequisite, but this doesn’t seem obvious to me.
You could also argue that any beneficial future requires us to figure out our preferences, but that wouldn’t explain why it had to happen before building superintelligent AI.
As I often say, the reason I think we need to prioritize a theory of human preferences is not because I have a slam dunk proof that we need it, but because I believe we fail to adequately work to mitigate known risks of superintelligent AI if we don’t because we don’t, on the other side, have a slam dunk argument for why we wouldn’t end up needing it, and I’d rather live in a world where we worked it out and didn’t need it than one where we didn’t work it out and do need it.
I agree with this, but it’s not an argument on the margin. There are many aspects of AI safety I could work on. Why a theory of human preferences in particular, as opposed to e.g. detecting optimization?
I agree with this, but it’s not an argument on the margin. There are many aspects of AI safety I could work on. Why a theory of human preferences in particular, as opposed to e.g. detecting optimization?
How we think of whether to work on one thing versus another seems a matter of both how important the project is overall and how likely it is that any individual can do something about it relative to their ability to do something about something else. That is, I don’t think of human researchers as a commodity, thus much of the answer to this question is about what can any one of us do not just what could we do if we were all equally capable of working on anything.
I think of this as a function of impact, neglectedness, tractability, skill, and interest. The first three hold constant across all people, but the last two vary. So when I choose what to work on given that I am willed to work on AI safety, I decide also based on what I am most skilled to do relative to others (my comparative advantage) and what I am most interested or excited about working on (to what extent am I excited to work on something for its own sake, irrelevant of the amount it advances AI safety).
Weighing the first three together suggests whether or not it is worth anyone working on a problem, and including the last two point to whether it’s worth you working on a problem. So when you ask about what “I could work on” all those factors are playing a role.
But if we go back to just the question of why I think a theory of human preferences is impactful, neglected, and tractable, we can take these in turn.
First, I think it’s pretty clear that developing a theory of human preferences precise enough to be useful in AI alignment is neglected. Stuart aside, everyone else I can think of thinking about this is still in the proto-formal stage, trying to figuring out what the formalisms would even look like to begin making precise statements to allow forming the theory. Yes, we have some theories about human preferences already, but they seem inadequate for AI safety purposes.
Second, I think we have reason to believe it’s tractable in that no one has previously needed a theory of human preferences accurate enough to address the needs presented by AI alignment, so we haven’t spent much time really trying to solve the problem of “precise theory of human values that doesn’t fall apart under heavy optimization”. The closest we have is the theory of preferences from behavioral economics, which I view Stuart’s work as an evolution of, and that was able to be worked out over a few decades once markets became a powerful enough optimization force that it was valuable to have it so that we could get more of what we wanted from markets and other modern transactional means of interaction. Yes, this time is different, since we are working ahead of the optimization force being present in our lives, and we are doing that for reasons relevant to the last point, impact.
I also have an intuition that thinking that we can get away without having an adequate theory of human preferences is just the same mistake we made 20 years ago when folks argued that we didn’t have to worry about safety at all because a sufficiently intelligent AI would be smart enough to be nice to us, i.e. that sufficient intelligence would result in sufficient ethics. Now of course we know this as the orthogonality thesis that the two are not correlated, and I think of trying to build powerful optimizers without adequate understanding of what we want them to optimize for (in this case human preferences) as making the same mistake we made early on, thinking we will easily solve one very different problem by solving another.
All of this suggests to me that we should be making space for some people to work on a theory of human preferences, just like we make space for some people to work on agent foundations and some people to work on alignment in the context of current ML systems. There’s no one overseeing AI safety as a Manhattan-style project, so the natural way to organize ourselves is not around driving towards a single objective, but of driving towards a goal that we might approach by many means and, lacking clear consensus, it is worth pursuing these many means as a hedge against the likelihood that we are wrong, and we are not resourced to the frontier such that we must make tradeoffs against different directions so much as we can just expand the frontier by bringing in more people to work on AI safety.
I agree with basically all of this; maybe I’m more pessimistic about tractability, but not enough to matter for any actual decision.
It sounds to me that given these beliefs the thing you would want to advocate is “let those who want to figure out a theory of human preferences do so and don’t shun them from AI safety”. Perhaps also “let’s have some introductory articles for such a theory so that new entrants to the field know that it is a problem that could use more work and can make an informed decision about what to work on”. Both of these I would certainly agree with.
In your original comment it sounded to me like you were advocating something stronger: that a theory of human preferences was necessary for AI safety, and (by implication) at least some of us who don’t work on it should switch to working on it. In addition, we should differentially encourage newer entrants to the field to work on a theory of human preferences, rather than some other problem of AI safety, so as to build a community around (4). I would disagree with these stronger claims.
Do you perhaps only endorse the first paragraph and not the second?
I endorse what you propose in the first paragraph. I do think a theory of human preferences is necessary and that at least someone should work on it (and if I didn’t think this I probably wouldn’t be doing it myself), although not necessarily that someone should switch to it all else equal, and I wouldn’t say we should encourage folks to work on it more than other problems as a general policy since there’s a lot to be done and I remain uncertain about prioritization so can’t make a strong recommendation there beyond “let’s make sure we don’t fail to work on as much as seems relevant as possible”.
So it sounds like we only disagree on the necessity aspect, and that seems to be the result of an inferential gap I’m not sure how to bridge yet, i.e. why it is I believe it to be necessary hinges in part on deeper beliefs we may not share and haven’t figured out to make explicit. That’s good to know, because it points towards something worth thinking about and addressing so that existing and new entrants to AI safety work may more accept it as important and useful work.
In my head, the theory + implementation ensures that all of the optimization is pointed toward the goal “try to help the human”. If you could then legitimately say “it could still end up optimizing for something else”, then we don’t have the right theory + implementation as I’m imagining it.
I think it’s hiding details in “optimization”, “try” and “help” (and to a lesser extent, “human”). I don’t think it’s hiding details in “want”. You could maybe argue that any operationalization of “help” would necessarily have “want” as a prerequisite, but this doesn’t seem obvious to me.
You could also argue that any beneficial future requires us to figure out our preferences, but that wouldn’t explain why it had to happen before building superintelligent AI.
I agree with this, but it’s not an argument on the margin. There are many aspects of AI safety I could work on. Why a theory of human preferences in particular, as opposed to e.g. detecting optimization?
How we think of whether to work on one thing versus another seems a matter of both how important the project is overall and how likely it is that any individual can do something about it relative to their ability to do something about something else. That is, I don’t think of human researchers as a commodity, thus much of the answer to this question is about what can any one of us do not just what could we do if we were all equally capable of working on anything.
I think of this as a function of impact, neglectedness, tractability, skill, and interest. The first three hold constant across all people, but the last two vary. So when I choose what to work on given that I am willed to work on AI safety, I decide also based on what I am most skilled to do relative to others (my comparative advantage) and what I am most interested or excited about working on (to what extent am I excited to work on something for its own sake, irrelevant of the amount it advances AI safety).
Weighing the first three together suggests whether or not it is worth anyone working on a problem, and including the last two point to whether it’s worth you working on a problem. So when you ask about what “I could work on” all those factors are playing a role.
But if we go back to just the question of why I think a theory of human preferences is impactful, neglected, and tractable, we can take these in turn.
First, I think it’s pretty clear that developing a theory of human preferences precise enough to be useful in AI alignment is neglected. Stuart aside, everyone else I can think of thinking about this is still in the proto-formal stage, trying to figuring out what the formalisms would even look like to begin making precise statements to allow forming the theory. Yes, we have some theories about human preferences already, but they seem inadequate for AI safety purposes.
Second, I think we have reason to believe it’s tractable in that no one has previously needed a theory of human preferences accurate enough to address the needs presented by AI alignment, so we haven’t spent much time really trying to solve the problem of “precise theory of human values that doesn’t fall apart under heavy optimization”. The closest we have is the theory of preferences from behavioral economics, which I view Stuart’s work as an evolution of, and that was able to be worked out over a few decades once markets became a powerful enough optimization force that it was valuable to have it so that we could get more of what we wanted from markets and other modern transactional means of interaction. Yes, this time is different, since we are working ahead of the optimization force being present in our lives, and we are doing that for reasons relevant to the last point, impact.
On the question of impact, I think Stuart addressed this question well several months ago.
I also have an intuition that thinking that we can get away without having an adequate theory of human preferences is just the same mistake we made 20 years ago when folks argued that we didn’t have to worry about safety at all because a sufficiently intelligent AI would be smart enough to be nice to us, i.e. that sufficient intelligence would result in sufficient ethics. Now of course we know this as the orthogonality thesis that the two are not correlated, and I think of trying to build powerful optimizers without adequate understanding of what we want them to optimize for (in this case human preferences) as making the same mistake we made early on, thinking we will easily solve one very different problem by solving another.
All of this suggests to me that we should be making space for some people to work on a theory of human preferences, just like we make space for some people to work on agent foundations and some people to work on alignment in the context of current ML systems. There’s no one overseeing AI safety as a Manhattan-style project, so the natural way to organize ourselves is not around driving towards a single objective, but of driving towards a goal that we might approach by many means and, lacking clear consensus, it is worth pursuing these many means as a hedge against the likelihood that we are wrong, and we are not resourced to the frontier such that we must make tradeoffs against different directions so much as we can just expand the frontier by bringing in more people to work on AI safety.
I agree with basically all of this; maybe I’m more pessimistic about tractability, but not enough to matter for any actual decision.
It sounds to me that given these beliefs the thing you would want to advocate is “let those who want to figure out a theory of human preferences do so and don’t shun them from AI safety”. Perhaps also “let’s have some introductory articles for such a theory so that new entrants to the field know that it is a problem that could use more work and can make an informed decision about what to work on”. Both of these I would certainly agree with.
In your original comment it sounded to me like you were advocating something stronger: that a theory of human preferences was necessary for AI safety, and (by implication) at least some of us who don’t work on it should switch to working on it. In addition, we should differentially encourage newer entrants to the field to work on a theory of human preferences, rather than some other problem of AI safety, so as to build a community around (4). I would disagree with these stronger claims.
Do you perhaps only endorse the first paragraph and not the second?
I endorse what you propose in the first paragraph. I do think a theory of human preferences is necessary and that at least someone should work on it (and if I didn’t think this I probably wouldn’t be doing it myself), although not necessarily that someone should switch to it all else equal, and I wouldn’t say we should encourage folks to work on it more than other problems as a general policy since there’s a lot to be done and I remain uncertain about prioritization so can’t make a strong recommendation there beyond “let’s make sure we don’t fail to work on as much as seems relevant as possible”.
So it sounds like we only disagree on the necessity aspect, and that seems to be the result of an inferential gap I’m not sure how to bridge yet, i.e. why it is I believe it to be necessary hinges in part on deeper beliefs we may not share and haven’t figured out to make explicit. That’s good to know, because it points towards something worth thinking about and addressing so that existing and new entrants to AI safety work may more accept it as important and useful work.