leogao's Shortform

it's surprising just how much of cutting edge research (at least in ML) is dealing with really annoying and stupid bottlenecks. pesky details that seem like they shouldn't need attention. tools that in a good and just world would simply not break all the time.

i used to assume this was merely because i was inexperienced, and that surely eventually you learn to fix all the stupid problems, and then afterwards you can just spend all your time doing actual real research without constantly needing to context switch to fix stupid things. 

however, i've started to think that as long as you're pushing yourself to do novel, cutting edge research (as opposed to carving out a niche and churning out formulaic papers), you will always spend most of your time fixing random stupid things. as you get more experienced, you get bigger things done faster, but the amount of stupidity is conserved. as they say in running- it doesn't get easier, you just get faster.

as a beginner, you might spend a large part of your research time trying to install CUDA or fighting with python threading. as an experienced researcher, you might spend that time instead diving deep into some complicated distributed training code to fix a deadlock or debugging where some numerical issue is causing a NaN halfway through training.

i think this is important to recognize because you're much more likely to resolve these issues if you approach them with the right mindset. when you think of something as a core part of your job, you're more likely to engage your problem solving skills fully to try and find a resolution. on the other hand, if something feels like a brief intrusion into your job, you're more likely to just hit it with a wrench until the problem goes away so you can actually focus on your job.

in ML research the hit it with a wrench strategy is the classic "google the error message and then run whatever command comes up" loop. to be clear, this is not a bad strategy when deployed properly - this is often the best first thing to try when something breaks, because you don't have to do a big context switch and lose focus on whatever you were doing before. but it's easy to end up trapped in this loop for too long. at some point you should switch modes to actively understanding and debugging the code, which is easier to do if you think of your job as mostly being about actively understanding and debugging code.

earlier in my research career i would feel terrible about having spent so much time doing things that were not the "actual" research, which would make me even more likely to just hit things with a wrench, which actually did make me less effective overall. i think shifting my mindset since then has helped me a lot

in research, if you settle into a particular niche you can churn out papers much faster, because you can develop a very streamlined process for that particular kind of paper. you have the advantage of already working baseline code, context on the field, and a knowledge of the easiest way to get enough results to have an acceptable paper.

while these efficiency benefits of staying in a certain niche are certainly real, I think a lot of people end up in this position because of academic incentives - if your career depends on publishing lots of papers, then a recipe to get lots of easy papers with low risk is great. it's also great for the careers of your students, because if you hand down your streamlined process, then they can get a phd faster and more reliably.

however, I claim that this also reduces scientific value, and especially the probability of a really big breakthrough. big scientific advances require people to do risky bets that might not work out, and often the work doesn't look quite like anything anyone has done before.

as you get closer to the frontier of things that have ever been done, the road gets tougher and tougher. you end up spending more time building basic infrastructure. you explore lots of dead ends and spend lots of time pivoting to new directions that seem more promising. you genuinely don't know when you'll have the result that you'll build your paper on top of.

so for people who are not beholden as strongly to academic incentives, it might make sense to think carefully about the tradeoff between efficiency and exploration.

(not sure I 100% endorse this, but it is a hypothesis worth considering)

I decided to conduct an experiment at neurips this year: I randomly surveyed people walking around in the conference hall to ask whether they had heard of AGI

I found that out of 38 respondents, only 24 could tell me what AGI stands for (63%)

we live in a bubble

(https://x.com/nabla_theta/status/1869144832595431553)

it's quite plausible (40% if I had to make up a number, but I stress this is completely made up) that someday there will be an AI winter or other slowdown, and the general vibe will snap from "AGI in 3 years" to "AGI in 50 years". when this happens it will become deeply unfashionable to continue believing that AGI is probably happening soonish (10-15 years), in the same way that suggesting that there might be a winter/slowdown is unfashionable today. however, I believe in these timelines roughly because I expect the road to AGI to involve both fast periods and slow bumpy periods. so unless there is some super surprising new evidence, I will probably only update moderately on timelines if/when this winter happens

reliability is surprisingly important. if I have a software tool that is 90% reliable, it's actually not that useful for automation, because I will spend way too much time manually fixing problems. this is especially a problem if I'm chaining multiple tools together in a script. I've been bit really hard by this because 90% feels pretty good if you run it a handful of times by hand, but then once you add it to your automated sweep or whatever it breaks and then you have to go in and manually fix things. and getting to 99% or 99.9% is really hard because things break in all sorts of weird ways.

I think this has lessons for AI - lack of reliability is one big reason I fail to get very much value out of AI tools. if my chatbot catastrophically hallucinates once every 10 queries, then I basically have to look up everything anyways to check. I think this is a major reason why cool demos often don't mean things that are practically useful - 90% reliable it's great for a demo (and also you can pick tasks that your AI is more reliable at, rather than tasks which are actually useful in practice). this is an informing factor for why my timelines are longer than some other people's

i've noticed a life hyperparameter that affects learning quite substantially. i'd summarize it as "willingness to gloss over things that you're confused about when learning something". as an example, suppose you're modifying some code and it seems to work but also you see a warning from an unrelated part of the code that you didn't expect. you could either try to understand exactly why it happened, or just sort of ignore it.

reasons to set it low:

• each time your world model is confused, that's an opportunity to get a little bit of signal to improve your world model. if you ignore these signals you increase the length of your feedback loop, and make it take longer to recover from incorrect models of the world.
• in some domains, it's very common for unexpected results to actually be a hint at a much bigger problem. for example, many bugs in ML experiments cause results that are only slightly weird, but if you tug on the thread of understanding why your results are slightly weird, this can cause lots of your experiments to unravel. and doing so earlier rather than later can save a huge amount of time
• understanding things at least one level of abstraction down often lets you do things more effectively. otherwise, you have to constantly maintain a bunch of uncertainty about what will happen when you do any particular thing, and have a harder time thinking of creative solutions

reasons to set it high:

• it's easy to waste a lot of time trying to understand relatively minor things, instead of understanding the big picture. often, it's more important to 80-20 by understanding the big picture, and you can fill in the details when it becomes important to do so (which often is only necessary in rare cases).
• in some domains, we have no fucking idea why anything happens, so you have to be able to accept that we don't know why things happen to be able to make progress
• often, if e.g you don't quite get a claim that a paper is making, you could resolve your confusion just by reading a bit ahead. if you always try to fully understand everything before digging into it, you'll find it very easy to get stuck before actually make it to the main point the paper is making

there are very different optimal configurations for different kinds of domains. maybe the right approach is to be aware that this is an important hparameter and occasionally try going down some rabbit holes and seeing how much value it provides

in some way, bureaucracy design is the exact opposite of machine learning. while the goal of machine learning is to make clusters of computers that can think like humans, the goal of bureaucracy design is to make clusters of humans that can think like a computer

learning thread for taking notes on things as i learn them (in public so hopefully other people can get value out of it)

a take I've expressed a bunch irl but haven't written up yet: feature sparsity might be fundamentally the wrong thing for disentangling superposition; circuit sparsity might be more correct to optimize for. in particular, circuit sparsity doesn't have problems with feature splitting/absorption

the most valuable part of a social event is often not the part that is ostensibly the most important, but rather the gaps between the main parts.

• at ML conferences, the headline keynotes and orals are usually the least useful part to go to; the random spontaneous hallway chats and dinners and afterparties are extremely valuable
• when doing an activity with friends, the activity itself is often of secondary importance. talking on the way to the activity, or in the gaps between doing the activity, carry a lot of the value
• at work, a lot of the best conversations happen outside of scheduled 1:1s and group meetings, but rather happen in spontaneous hallway or dinner groups

random fun experiment: accuracy of GPT-4 on "Q: What is 1 + 1 + 1 + 1 + ...?\nA:"

↑ comment by leogao · 2023-04-14T02:57:52.527Z · LW(p) · GW(p)

blue: highest logprob numerical token

orange: y = x

people often say that limitations of an artistic medium breed creativity. part of this could be the fact that when it is costly to do things, the only things done will be higher effort

any time someone creates a lot of value without capturing it, a bunch of other people will end up capturing the value instead. this could be end consumers, but it could also be various middlemen. it happens not infrequently that someone decides not to capture the value they produce in the hopes that the end consumers get the benefit, but in fact the middlemen capture the value instead

saying "sorry, just to make sure I understand what you're saying, do you mean [...]" more often has been very valuable

hypothesis: intellectual progress mostly happens when bubbles of non tribalism can exist. this is hard to safeguard because tribalism is a powerful strategy, and therefore insulating these bubbles is hard. perhaps it is possible for there to exist a monopoly on tribalism to make non tribal intellectual progress happen, in the same way a monopoly on violence makes it possible to make economically valuable trade without fear of violence

a great way to get someone to dig into a position really hard (whether or not that position is correct) is to consistently misunderstand that position

it's often stated that believing that you'll succeed actually causes you to be more likely to succeed. there are immediately obvious explanations for this - survivorship bias. obviously most people who win the lottery will have believed that buying lottery tickets is a good idea, but that doesn't mean we should take that advice. so we should consider the plausible mechanisms of action.

first, it is very common for people with latent ability to underestimate their latent ability. in situations where the cost of failure is low, it seems net positive to at least take seriously the hypothesis that you can do more than you think you can. (also keeping in mind that we often overestimate the cost of failure). there are also deleterious mental health effects to believing in a high probability of failure, and then bad mental health does actually cause failure - it's really hard to give something your all if you don't really believe in it.

belief in success also plays an important role in signalling. if you're trying to make some joint venture happen, you need to make people believe that the joint venture will actually succeed (opportunity costs exist). when assessing the likelihood of success of the joint venture, people will take many pieces of information into account: your track record, the opinions of other people with a track record, object level opinions on the proposal, etc.

being confident in your own venture is an important way of putting your "skin in the game" to vouch that it will succeed. specifically, the way this is supposed to work is that you get punished socially for being overconfident, so you have an incentive to only really vouch for things that really will work. in practice, in large parts of the modern world overconfidence is penalized less than we're hardwired to expect. sometimes this is due to regions with cultural acceptance and even embrace of risky bets (SV), or because of atomization of modern society making the effects of social punishment less important.

this has both good and bad effects. it's what enables innovation, because that fundamentally requires a lot of people to play the research lottery. if you're not willing to work on something that will probably fail but also will pay out big if it succeeds, it's very hard to innovate. research consists mostly of people who are extremely invested in some research bet, to the point where it's extremely hard to convince them to pivot if it's not working out. ditto for startups, which are probably the architypical example of both innovation and also of catastrophic overconfidence.

this also creates problems - for instance, it enables grifting because you don't actually need to have to be correct if you just claim that your idea will work, and then when it inevitably fails you can just say that this is par for the course. also, being systematically overconfident can cause suboptimal decision making where calibration actually is important.

because many talented people are underequipped with confidence (there is probably some causal mechanism here - technical excellence often requires having a very mechanistic mental model of the thing you're doing, rather than just yoloing it and hoping it works), it also creates a niche for middlemen to supply confidence as a service, aka leadership. in the ideal case, this confidence is supplied by people who are calibratedly confident because of experience, but the market is inefficient enough that even people who are not calibrated can supply confidence because of the market inefficiency. another way to view this is that leaders deliver the important service of providing certainty in the face of an uncertain world.

(I'm using the term middleman here in a sense that doesn't necessarily imply that they deliver no value - in fact, causing things to happen can create lots of value, and depending on the specifics this role can be very difficult to fill. but they aren't the people who do the actual technical work. it is of course also valuable for the leader to e.g be able in theory to fill any of the technical roles if needed, because it makes them more able to spend their risk budget on the important technical questions, it creates more slack and thereby increases the probability of success, and the common knowledge of the existence of this slack itself also increases the perceived inevitability of success)

a similar story also applies at the suprahuman level, of tribes or ideologies. if you are an ideology, your job is unfortunately slightly more complicated. on the one hand, you need to project the vibe of inevitable success so that people in other tribes feel the need to get in early on your tribe, but on the other hand you need to make your tribe members feel like every decision they make is very consequential for whether the tribe succeeds. if you're merely calibrated, then only one of the two can be true. different social technologies are used by religions, nations, political movements, companies, etc to maintain this paradox.

one kind of reasoning in humans is a kind of instant intuition; you see something and something immediately and effortlessly pops into your mind. examples include recalling vocabulary in a language you're fluent in, playing a musical instrument proficiently, or having a first guess at what might be going wrong when debugging.

another kind of reasoning is the chain of thought, or explicit reasoning: you lay out your reasoning steps as words in your head, interspersed perhaps with visuals, or abstract concepts that you would have a hard time putting in words. It feels like you're consciously picking each step of the reasoning. Working through a hard math problem, or explicitly designing a codebase by listing the constraints and trying to satisfy them, are examples of this.

so far these map onto what people call system 1 and 2, but I've intentionally avoided these labels because I think there's actually a third kind of reasoning that doesn't fit well into either of these buckets.

sometimes, I need to put the relevant info into my head, and then just let it percolate slowly without consciously thinking about it. at some later time, insights into the problem will suddenly and unpredictably pop into my head. I've found this mode of reasoning to be indispensible for dealing with the hardest problems, or for generating insights, where if I just did explicit reasoning I'd just get stuck.

of course, you can't just sit around and do nothing and hope insights come to you - to make this process work you have to absorb lots of info, and also do a lot of explicit reasoning before and after to take flashes of insight and turn them into actual fleshed-out knowledge. and there are conditions that are more or less conducive to this kind of reasoning.

I'm still figuring out how to best leverage it, but I think one hypothesis this raises is the possibility that a necessary ingredient in solving really hard problems is spending a bunch of time simply not doing any explicit reasoning, and creating whatever conditions are needed for subconscious insight-generating reasoning.

Is it a very universal experience to find it easier to write up your views if it's in response to someone else's writeup? Seems like the kind of thing that could explain a lot about how research tends to happen if it were a pretty universal experience.

for people who are not very good at navigating social conventions, it is often easier to learn to be visibly weird than to learn to adapt to the social conventions.

this often works because there are some spaces where being visibly weird is tolerated, or even celebrated. in fact, from the perspective of an organization, it is good for your success if you are good at protecting weird people.

but from the perspective of an individual, leaning too hard into weirdness is possibly harmful. part of leaning into weirdness is intentional ignorance of normal conventions. this traps you in a local minimum where any progress on understanding normal conventions hurts your weirdness, but isn't enough to jump all the way to the basin of the normal mode of interaction.

(epistemic status: low confidence, just a hypothesis)

Since there are basically no alignment plans/directions that I think are very likely to succeed, and adding "of course, this will most likely not solve alignment and then we all die, but it's still worth trying" to every sentence is low information and also actively bad for motivation, I've basically recalibrated my enthusiasm to be centered around "does this at least try to solve a substantial part of the real problem as I see it". For me at least this is the most productive mindset for me to be in, but I'm slightly worried people might confuse this for me having a low P(doom), or being very confident in specific alignment directions, or so on, hence this post that I can point people to.

I think this may also be a useful emotional state for other people with similar P(doom) and who feel very demotivated by that, which impacts their productivity.

a common discussion pattern: person 1 claims X solves/is an angle of attack on problem P. person 2 is skeptical. there is also some subproblem Q (90% of the time not mentioned explicitly). person 1 is defending a claim like "X solves P conditional on Q already being solved (but Q is easy)", whereas person 2 thinks person 1 is defending "X solves P via solving Q", and person 2 also believes something like "subproblem Q is hard". the problem with this discussion pattern is it can lead to some very frustrating miscommunication:

• if the discussion recurses into whether Q is hard, person 1 can get frustrated because it feels like a diversion from the part they actually care about/have tried to find a solution for, which is how to find a solution to P given a solution to Q (again, usually Q is some implicit assumption that you might not even notice you have). it can feel like person 2 is nitpicking or coming up with fully general counterarguments for why X can never be solved.
• person 2 can get frustrated because it feels like the original proposed solution doesn't engage with the hard subproblem Q. person 2 believes that assuming Q were solved, then there would be many other proposals other than X that would also suffice to solve problem P, so that the core ideas of X actually aren't that important, and all the work is actually being done by assuming Q.

philosophy: while the claims "good things are good" and "bad things are bad" at first appear to be compatible with each other, actually we can construct a weird hypothetical involving exact clones that demonstrates that they are fundamentally inconsistent with each other

law: could there be ambiguity in "don't do things that are bad as determined by a reasonable person, unless the thing is actually good?" well, unfortunately, there is no way to know until it actually happens

One possible model of AI development is as follows: there exists some threshold beyond which capabilities are powerful enough to cause an x-risk, and such that we need alignment progress to be at the level needed to align that system before it comes into existence. I find it informative to think of this as a race where for capabilities the finish line is x-risk-capable AGI, and for alignment this is the ability to align x-risk-capable AGI. In this model, it is necessary but not sufficient for alignment for alignment to be ahead by the time it's at the finish line for good outcomes: if alignment doesn't make it there first, then we automatically lose, but even if it does, if alignment doesn't continue to improve proportional to capabilities, we might also fail at some later point. However, I think it's plausible we're not even on track for the necessary condition, so I'll focus on that within this post.

Given my distributions over how difficult AGI and alignment respectively are, and the amount of effort brought to bear on each of these problems, I think there's a worryingly large chance that we just won't have the alignment progress needed at the critical juncture.

I also think it's plausible that at some point before when x-risks are possible, capabilities will advance to the point that the majority of AI research will be done by AI systems. The worry is that after this point, both capabilities and alignment will be similarly benefitted by automation, and if alignment is behind at the point when this happens, then this lag will be "locked in" because an asymmetric benefit to alignment research is needed to overtake capabilities if capabilities is already ahead.

There are a number of areas where this model could be violated:

• Capabilities could turn out to be less accelerated than alignment by AI assistance. It seems like capabilities is mostly just throwing more hardware at the problem and scaling up, whereas alignment is much more conceptually oriented.
• After research is mostly/fully automated, orgs could simply allocate more auto-research time to alignment than AGI.
• Alignment(/coordination to slow down) could turn out to be easy. It could turn out that applying the same amount of effort to alignment and AGI results in alignment being solved first.

However, I don't think these violations are likely for the following reasons respective:

• It's plausible that our current reliance on scaling is a product of our theory not being good enough and that it's already possible to build AGI with current hardware if you have the textbook from the future. Even if the strong version of the claim isn't true, one big reason that the bitter lesson is true is that bespoke engineering is currently expensive, and if it became suddenly a lot cheaper we would see a lot more of it and consequently squeezing more out of the same hardware. It also seems likely that before total automation, there will be a number of years where automation is best modelled as a multiplicative factor on human researcher effectiveness. In that case, because of the sheer number of capabilities researchers compared to alignment researchers, alignment researchers would have to benefit a lot more to just break even.
• If it were the case that orgs would pivot, I would expect them to currently be allocating a lot more to alignment than they do currently. While it's still plausible that orgs haven't allocated more to alignment because they think AGI is far away, and that a world where automated research is a thing is a world where orgs would suddenly realize how close AGI is and pivot, that hypothesis hasn't been very predictive so far. Further, because I expect the tech for research automation to be developed at roughly the same time by many different orgs, it seems like not only does one org have to prioritize alignment, but actually a majority weighted by auto research capacity have to prioritize alignment. To me, this seems difficult, although more tractable than the other alignment coordination problem, because there's less of a unilateralist problem. The unilateralist problem still exists to some extent: orgs which prioritize alignment are inherently at a disadvantage compared to orgs that don't, because capabilities progress feeds recursively into faster progress whereas alignment progress is less effective at making future alignment progress faster. However, on the relevant timescales this may become less important.
• I think alignment is a very difficult problem, and that moreover by its nature it's incredibly easy to underestimate. I should probably write a full post about my take on this at some point, and I don't really have space here to really dive into it here, but a quick meta level argument for why we shouldn't lean on alignment easiness even if there is a non negligible chance of easiness is that a) given the stakes, we should exercise extreme caution and b) there are very few problems we have that are in the same reference class as alignment, and of the few that are even close, like computer security, they don't inspire a lot of confidence.

I think exploring the potential model violations further is a fruitful direction. I don't think I'm very confident about this model.

economic recession and subsequent reduction in speculative research, including towards AGI, seems very plausible

AI (by which I mean, like, big neural networks and whatever) is not that economically useful right now. furthermore, current usage figures are likely an overestimate of true economic usefulness because a very large fraction of it is likely to be bubbly spending that will itself dry up if there is a recession (legacy companies putting LLMs into things to be cool, startups that are burning money without PMF, consumers with disposable income to spend on entertainment).

it will probably still be profitable to develop AI tech, but things will be much more tethered to consumer usefulness.

this probably doesn't set AGI back that much but I think people are heavily underrating this as a possibility. it also probably heavily impacts the amount of alignment work done at labs.

one man's modus tollens is another man's modus ponens:

"making progress without empirical feedback loops is really hard, so we should get feedback loops where possible" "in some cases (i.e close to x-risk), building feedback loops is not possible, so we need to figure out how to make progress without empirical feedback loops. this is (part of) why alignment is hard"

A common cycle:

1. This model is too oversimplified! Reality is more complex than this model suggests, making it less useful in practice. We should really be taking these into account. [optional: include jabs at outgroup]
2. This model is too complex! It takes into account a bunch of unimportant things, making it much harder to use in practice. We should use this simplified model instead. [optional: include jabs at outgroup]

Sometimes this even results in better models over time.

for something to be a good way of learning, the following criteria have to be met:

• tight feedback loops
• transfer of knowledge to your ultimate goal
• sufficiently interesting that it doesn't feel like a grind

trying to do the thing you care about directly hits 2 but can fail 1 and 3. many things that you can study hit 1 but fail 2 and 3. and of course, many fun games hit 3 (and sometimes 1) but fail to hit 2.

lifehack: buying 3 cheap pocket sized battery packs costs like $60 and basically eliminates the problem of running out of phone charge on the go. it's much easier to remember to charge them because you can instantaneously exchange your empty battery pack for a full one when you realize you need one, plugging the empty battery pack happens exactly when you swap for a fresh one, and even if you forget once or lose one you have some slack

often the easiest way to gain status within some system is to achieve things outside that system

the project of rationality is the project of becoming slightly more mesaoptimizery

Corollary to Others are wrong != I am right (https://www.lesswrong.com/posts/4QemtxDFaGXyGSrGD/other-people-are-wrong-vs-i-am-right [LW · GW]): It is far easier to convince me that I'm wrong than to convince me that you're right.

current understanding of optimization

• high curvature directions (hessian eigenvectors with high eigenvalue) want small lrs. low curvature directions want big lrs
• if the lr in a direction is too small, it takes forever to converge. if the lr is too big, it diverges by oscillating with increasing amplitude
• momentum helps because if your lr is too small, it makes you move a bit faster. if your lr is too big, it causes the oscillations to cancel out with themselves. this makes high curvature directions more ok with larger lrs and low curvature directions more ok with smaller lrs, improving conditioning
• high curvature directions also have bigger gradients. this is the opposite of what we want because in a perfect world higher curvature directions would have smaller gradients (natural gradient does this but it's usually too expensive). adam second moment / rmsprop helps because it makes gradients stay exactly the same size when the direction gets bigger, which is sorta halfway right
  • applied per param rather than per eigenvector
• in real NNs edge of stability means it's actually even more fine to have a too-high lr: the max curvature increases throughout training until it gets to the critical point where it would diverge, but then instead of diverging all the way the oscillations along the top eigenvector somehow cause the model to move into a slightly lower curvature region again, so that it stabilizes right at the edge of stability. 
  • for Adam, these oscillations also cause second moment increases, which decreases preconditioned max curvature without affecting the original curvature. so this means the original max curvature can just keep increasing for Adam whereas it doesn't for SGD (though apparently there's some region where it jumps into a region with low original max curvature too)

papers

• https://distill.pub/2017/momentum/ really cool momentum explainer
• https://arxiv.org/abs/2103.00065 - edge of stability
• https://arxiv.org/abs/2207.14484 - edge of stability for adam

adhd is a mechanism for seeking domains with tight feedback loops

Some aspirational personal epistemic rules for keeping discussions as truth seeking as possible (not at all novel whatsoever, I'm sure there exist 5 posts on every single one of these points that are more eloquent)

• If I am arguing for a position, I must be open to the possibility that my interlocutor may turn out to be correct. (This does not mean that I should expect to be correct exactly 50% of the time, but it does mean that if I feel like I'm never wrong in discussions then that's a warning sign: I'm either being epistemically unhealthy or I'm talking to the wrong crowd.)
• If I become confident that I was previously incorrect about a belief, I should not be attached to my previous beliefs. I should not incorporate my beliefs into my identity. I should not be averse to evidence that may prove me wrong. I should always entertain the possibility that even things that feel obviously true to me may be wrong.
• If I convince someone to change their mind, I should avoid say things like "I told you so", or otherwise try to score status points out of it.

I think in practice I adhere closer to these principles than most people, but I definitely don't think I'm perfect at it.

(Sidenote: it seems I tend to voice my disagreement on factual things far more often (though not maximally) compared to most people. I'm slightly worried that people will interpret this as me disliking them or being passive aggressive or something - this is typically not the case! I have big disagreements about the-way-the-world-is with a bunch of my closest friends and I think that's a good thing! If anything I gravitate towards people I can have interesting disagreements with.)

hypothesis: the kind of reasoning that causes ML people to say "we have made no progress towards AGI whatsoever" is closely analogous to the kind of reasoning that makes alignment people say "we have made no progress towards hard alignment whatsoever"

ML people see stuff like GPT4 and correctly notice that it's in fact kind of dumb and bad at generalization in the same ways that ML always has been. they make an incorrect extrapolation, which is that AGI must therefore be 100 years away, rather than 10 years away

high p(doom) alignment people see current model alignment techniques and correctly notice that they fail to tackle the AGI alignment problem in the same way that alignment techniques always have. they make an incorrect extrapolation and conclude that p(doom) = 0.99, rather than 0.5

(there is an asymmetry which is that overconfidence that alignment will be solved is much more dangerous than overconfidence that AGI will be solved)

Understanding how an abstraction works under the hood is useful because it gives you intuitions for when it's likely to leak and what to do in those cases.

takes on takeoff (or: Why Aren't The Models Mesaoptimizer-y Yet)

here are some reasons we might care about discontinuities:

• alignment techniques that apply before the discontinuity may stop applying after / become much less effective
  • makes it harder to do alignment research before the discontinuity that transfers to after the discontinuity (because there is something qualitatively different after the jump)
  • second order effect: may result in false sense of security
• there may be less/negative time between a warning shot and the End
  • harder to coordinate and slow down
  • harder to know when the End Times are coming
• alignment techniques that rely on systems supervising slightly smarter systems (i.e RRM) depend on there not being a big jump in capabilities

I think these capture 90% of what I care about when talking about fast/slow takeoff, with the first point taking up a majority

(it comes up a lot in discussions that it seems like I can't quite pin down exactly what my interlocutor's beliefs on fastness/slowness imply. if we can fully list out all the things we care about, we can screen off any disagreement about definitions of the word "discontinuity")

some things that seem probably true to me and which are probably not really cruxes:

• there will probably be a pretty big amount of AI-caused economic value and even more investment into AI, and AGI in particular (not really a bold prediction, given the already pretty big amount of these things! but a decade ago it may have been plausible nobody would care about AGI until the End Times, and this appears not to be the case)
• continuous changes of inputs like compute or investment or loss (not technically an input, but whatever) can result in discontinuous jumps in some downstream metric (accuracy on some task, number of worlds paperclipped)
• almost every idea is in some sense built on some previous idea, but this is not very useful because there exist many ideas [citation needed] and it's hard to tell which ones will be built on to create the idea that actually works (something something hindsight bias). this means you can't reason about how they will change alignment properties, or use them as a warning shot

possible sources of discontinuity:

• breakthroughs: at some point, some group discovers a brand new technique that nobody had ever thought of before / nobody had made work before because they were doing it wrong in some way / "3 hackers in a basement invent AGI"
  • depends on how efficient you think the research market is. I feel very uncertain about this
  • importantly I think cruxes here may result in other predictions about how efficient the world is generally, in ways unrelated to AI, and which may make predictions before the End Times
  • seems like a subcrux of this is whether the new technique immediately works very well or if it takes a nontrivial amount of time to scale it up to working at SOTA scale
• overdetermined "breakthroughs": some technique that didn't work (and couldn't have been made to work) at smaller scales starts working at larger scales. lots of people independently would have tried the thing
  • importantly, under this scenario it's possible for something to simultaneously (a) be very overdetermined (b) have very different alignment properties
  • very hard to know which of the many ideas that don't work might be the one that suddenly starts working with a few more OOMs of compute
• at some scale, there is just some kind of grokking without any change in techniques, and the internal structure and generalization properties of the networks changes a lot. trends break because of some deep change in the structure of the network
  • mostly isomorphic to the previous scenario actually
  • for example, in worlds where deceptive alignment happens because at x params suddenly it groks to mesaoptimizer-y structure and the generalization properties completely change
• at some scale, there is "enough" to hit some criticality threshold of some kind of thing the model already has. the downstream behavior changes a lot but the internal structure doesn't change much beyond the threshold. importantly while obviously some alignment strategies would break, there are potentially invariants that we can hold onto
  • for example, in worlds where deceptive alignment happens because of ontology mismatch and ontologies get slowly more mismatched with scale, and then past some threshold it snaps over to the deceptive generalization

I think these can be boiled down to 3 more succinct scenario descriptions:

• breakthroughs that totally change the game unexpectedly
• mechanistically different cognition suddenly working at scale
• more of the same cognition is different

The following things are not the same:

• Schemes for taking multiple unaligned AIs and trying to build an aligned system out of the whole
  • I think this is just not possible.
• Schemes for taking aligned but less powerful AIs and leveraging them to align a more powerful AI (possibly with amplification involved)
  • This breaks if there are cases where supervising is harder than generating, or if there is a discontinuity. I think it's plausible something like this could work but I'm not super convinced.

In the spirit of https://www.lesswrong.com/posts/fFY2HeC9i2Tx8FEnK/my-resentful-story-of-becoming-a-medical-miracle [LW · GW] , some anecdotes about things I have tried, in the hopes that I can be someone else's "one guy on a message board. None of this is medical advice, etc.

• No noticeable effects from vitamin D (both with and without K2), even though I used to live somewhere where the sun barely shines and also I never went outside, so I was almost certainly deficient.
• I tried Selenium (200mg) twice and both times I felt like utter shit the next day.
• Glycine (2g) for some odd reason makes me energetic, which makes it really bad as a sleep aid. 1g taken a few hours before bedtime is substantially less disruptive to sleep, but I haven't noticed substantial improvements.
• Unlike oral phenylephrine, intranasal phenylephrine does things, albeit very temporarily, and is undeniably the most effective thing I've tried, though apparently you're not supposed to use it too often, so I only use it when it gets really bad.

for a sufficiently competent policy, the fact that BoN doesn't update the policy doesn't mean it leaks any fewer bits of info to the policy than normal RL

aiming directly for achieving some goal is not always the most effective way of achieving that goal.

people love to find patterns in things. sometimes this manifests as mysticism- trying to find patterns where they don't exist, insisting that things are not coincidences when they totally just are. i think a weaker version of this kind of thinking shows up a lot in e.g literature too- events occur not because of the bubbling randomness of reality, but rather carry symbolic significance for the plot. things don't just randomly happen without deeper meaning.

some people are much more likely to think in this way than others. rationalists are very far along the spectrum in the "things just kinda happen randomly a lot, they don't have to be meaningful" direction.

there are some obvious cognitive bias explanations for why people would see meaning/patterns in things. most notably, it's comforting to feel like we understand things. the idea of the world being deeply random and things just happening for no good reason is scary.

but i claim that there is something else going on here. I think an inclination towards finding latent meaning is actually quite applicable when thinking about people. people's actions are often driven by unconscious drives to be quite strongly correlated with those drives. in fact, unconscious thoughts are often the true drivers, and the conscious thoughts are just the rationalization. but from the inside, it doesn't feel that way; from the inside it feels like having free will, and everything that is not a result of conscious thought is random or coincidental. this is a property that is not nearly as true of technical pursuits, so it's very reasonable to expect a different kind of reasoning to be ideal.

not only is this useful for modelling other people, but it's even more useful for modelling yourself. things only come to your attention if your unconscious brain decides to bring them to your attention. so even though something happening to you may be a coincidence, whether you focus on it or forget about it tells you a lot about what your unconscious brain is thinking. from the inside, this feels like things that should obviously be coincidence nonetheless having some meaning behind them. even the noticing of a hypothesis for the coincidence is itself a signal from your unconscious brain.

I don't quite know what the right balance is. on the one hand, it's easy to become completely untethered from reality by taking this kind of thing too seriously and becoming superstitious. on the other hand, this also seems like an important way of thinking about the world that is easy for people like me (and probably lots of people on LW) to underappreciate.

One of the greatest tragedies of truth-seeking as a human is that the things we instinctively do when someone else is wrong are often the exact opposite of the thing that would actually convince the other person.

it is often claimed that merely passively absorbing information is not sufficient for learning, but rather some amount of intentional learning is needed. I think this is true in general. however, one interesting benefit of passively absorbing information is that you notice some concepts/terms/areas come up more often than others. this is useful because there's simply too much stuff out there to learn, and some knowledge is a lot more useful than other knowledge. noticing which kinds of things come up often is therefore useful for prioritization. I often notice that my motivational system really likes to use this heuristic for deciding how motivated to be while learning something.

a claim I've been saying irl for a while but have never gotten around to writing up: current LLMs are benign not because of the language modelling objective, but because of the generalization properties of current NNs (or to be more precise, the lack thereof). with better generalization LLMs are dangerous too. we can also notice that RL policies are benign in the same ways, which should not be the case if the objective was the core reason. one thing that can go wrong with this assumption is thinking about LLMs that are both extremely good at generalizing (especially to superhuman capabilities) and simultaneously assuming they continue to have the same safety properties. afaict something like CPM avoids this failure mode of reasoning, but lots of arguments don't

Schmidhubering the agentic LLM stuff pretty hard https://leogao.dev/2020/08/17/Building-AGI-Using-Language-Models/

in a highly competitive domain, it is often better and easier to be sui generis, rather than a top 10 percentile member of a large reference class

tourist traps are the lubricant between the expectations and realities of travel

an interesting fact that I notice is that in domains where there are are a lot of objects in consideration, those objects have some structure so that they can be classified, and how often those objects occur follows a power law or something, there are two very different frames that get used to think about that domain:

• a bucket of atomic, structureless objects with unique properties where facts about one object don't really generalize at all to any other object
• a systematized, hierarchy or composition of properties or "periodic table" or full grid or objects defined by the properties they have in some framework

and a lot of interesting things happen when these collide or cooccur, or when shifting from one to the other

I know my description above is really abstract, so here are a bunch of concrete examples that all gesture at the same vibe:

basically all languages have systematic rules in general but special cases around the words that people use very often. this happens too often in unrelated languages to be a coincidence, and as a native/fluent speaker it always feels very natural but as a language learner it's very confusing. for example, for languages with conjugations, a few of the most common verbs are almost always irregular. e.g [to be, am, is, are, was, were] (english), [sein, bin, ist, war, sind] (german), [être, suis, est, était, sont] (french); small counting numbers are often irregular [first, second, third], [两个], [premier], [ひとつ、ふたつ、みっつ]. my theory for why this makes sense to natives but not to language learners is that language learners learn things systematically from the beginning, and in particular don't deal with the true distribution of language usage but rather an artificially flat one designed to capture all the language features roughly equally.

often, when there is a systematic way of naming things, the things that are most common will have special names/nicknames (eg IUPAC names vs common names). sometimes this happens because those things were discovered first before the systematization happened, and the once the systematization happens everyone is still used to the old names for some things. but also even if you start with the systematized thing, often people will create nicknames after the fact.

it often happens that we write software tools for a specific problem, and then later realize that that problem is a special case of a more general problem. often going more general is good because it means we can use the same code to do a wider range of things (which means less bugs, more code reuse, more elegant code). however, the more general/abstract code is often slightly clunkier to use for the common case, so often it makes sense to drop down a level of abstraction if the goal is to quickly hack something together.

when compressing some distribution of strings, the vast majority of the possible but unlikely strings can be stored basically verbatim with a flag and it is very easy to tell properties of the string by looking at the compressed representation; whereas for the most common strings they have to map to short strings that destroy all structure of the data without the decompressor. though note that not all the examples can be described as instances of compression exactly

sometimes, there's friction between people who are using the systematizing and people who are doing the atomic concepts thing. the systematizer comes off as nitpicky, pedantic, and removed from reality to the atomic concepts person, and the atomic concepts person comes off as unrigorous, uncosmopolitan, and missing the big picture to the systematizer.

I think the concept of zero only being invented long after the other numbers is also an instance of this - in some sense for basic everyday usage in counting things, the existence of zero is a weird technicality, and I could imagine someone saying "well sure yes there is a number that comes before zero, but it's not useful for anything, so it's not worth considering". I think a lot of math (eg abstract algebra) is the result of applying truly enormous amounts of this kind of systematizing

I think this also sort of has some handwavy analogies to superposition vs composition.

if there is an existing name for the thing I'm pointing at, I would be interested in knowing.

retargetability might be the distinguishing factor between controllers and optimizers

House rules for definitional disputes:

• If it ever becomes a point of dispute in an object level discussion what a word means, you should either use a commonly accepted definition, or taboo the term if the participants think those definitions are bad for the context of the current discussion. (If the conversation participants are comfortable with it, the new term can occupy the same namespace as the old tabooed term (i.e going forward, we all agree that the definition of X is Y for the purposes of this conversation, and all other definitions no longer apply))
• If any of the conversation participants want to switch to the separate discussion of "which definition of X is the best/most useful/etc", this is fine if all the other participants are fine as well. However, this has to be explicitly announced as a change in topic from the original object level discussion.

A few axes along which to classify optimizers:

• Competence: An optimizer is more competent if it achieves the objective more frequently on distribution
• Capabilities Robustness: An optimizer is more capabilities robust if it can handle a broader range of OOD world states (and thus possible pertubations) competently.
• Generality: An optimizer is more general if it can represent and achieve a broader range of different objectives
• Real-world objectives: whether the optimizer is capable of having objectives about things in the real world.

Some observations: it feels like capabilities robustness is one of the big things that makes deception dangerous, because it means that the model can figure out plans that you never intended for it to learn (something not very capabilities robust would just never learn how to deceive if you don't show it). This feels like the critical controller/search-process difference: controller generalization across states is dependent on the generalization abilities of the model architecture, whereas search processes let you think about the particular state you find yourself in. The actions that lead to deception are extremely OOD, and a controller would have a hard time executing the strategy reliably without first having seen it, unless NN generalization is wildly better than I'm anticipating. 

Real world objectives is definitely another big chunk of deception danger; caring about the real world leads to nonmyopic behavior (though maybe we're worried about other causes of nonmyopia too? not sure tbh), I'm actually not sure how I feel about generality: on the one hand, it feels intuitive that systems that are only able to represent one objective have got to be in some sense less able to become more powerful just by thinking more; on the other hand I don't know what a rigorous argument for this would look like. I think the intuition relates to the idea of general reasoning machinery being the same across lots of tasks, and this machinery being necessary to do better by thinking harder, and so any model without this machinery must be weaker in some sense. I think this feeds into capabilities robustness (or lack thereof) too.

Examples of where things fall on these axes:

• A rock would be none of the properties.
• A pure controller (i.e a thermostat, "pile of heuristics") can be competent, but not as capabilities robust, not general at all, and have objectives over the real world. 
• An analytic equation solver would be perfectly competent and capablilities robust (if it always works), not very general (it can only solve equations), and not be capable of having real world objectives. 
• A search based process can be competent, would be more capabilities robust and general, and may have objectives over the real world.
• A deceptive optimizer is competent, capabilities robust, and definitely has real world objectives

A thought pattern that I've noticed myself and others falling into sometimes: Sometimes I will make arguments about things from first principles that look something like "I don't see any way X can be true, it clearly follows from [premises] that X is definitely false", even though there are people who believe X is true. When this happens, it's almost always unproductive to continue to argue on first principles, but rather I should do one of: a) try to better understand the argument and find a more specific crux to disagree on or b) decide that this topic isn't worth investing more time in, register it as "not sure if X is true" in my mind, and move on.

there are policies which are successful because they describe a particular strategy to follow (non-mesaoptimizers), and policies that contain some strategy for discovering more strategies (mesaoptimizers). a way to view the relation this has to speed/complexity priors that doesn't depend on search in particular is that policies that work by discovering strategies tend to be simpler and more generic (they bake in very little domain knowledge/metis, and are applicable to a broader set of situations because they work by coming up with a strategy for the task at hand on the fly). in contrast, policies that work by knowing a specific strategy tend to be more complex because they have to bake in a ton of domain knowledge, are less generally useful because they specifically know what to do in that situation, and thereby are also less retargetable)

random brainstorming about optimizeryness vs controller/lookuptableyness:

let's think of optimizers as things that reliably steer a broad set of initial states to some specific terminal state seems like there are two things we care about (at least):

• retargetability: it should be possible to change the policy to achieve different terminal states (but this is an insufficiently strong condition, because LUTs also trivially meet this condition, because we can always just completely rewrite the LUT. maybe the actual condition we want is that the complexity of the map is less than the complexity of just the diff or something?) (in other words, in some sense it should be "easy" to rewrite a small subset or otherwise make a simple diff to the policy to change what final goal is achieved) (maybe related idea: instrumental convergence means most goals reuse lots of strategies/circuitry between each other)
• robustness: it should reliably achieve its goal across a wide range of initial states.

a LUT trained with a little bit of RL will be neither retargetable nor robust. a LUT trained with galactic amounts of RL to do every possible initial state optimally is robust but not retargetable (this is reasonable: robustness is only a property of the functional behavior so whether it's a LUT internally shouldn't matter; retargetability is a property of the actual implementation so it does matter). a big search loop (the most extreme of which is AIXI, which is 100% search) is very retargetable, and depending on how hard it searches is varying degrees of robustness.

(however, in practice with normal amounts of compute a LUT is never robust, this thought experiment only highlights differences that remain in the limit)

what do we care about these properties for?

• efficacy of filtering bad behaviors in pretraining: sufficiently good robustness means doing things that achieve the goal even in states that it never saw during training, and then even in states that require strategies that it never saw during training. if we filter out deceptive alignment from the data, then the model has to do some generalizing to figure out that this is a strategy that can be used to better accomplish its goal (as a sanity check that robustness is the thing here: a LUT never trained on deceptive alignment will never do it, but one that is trained on it will do it, a sufficiently powerful optimizer will always do it)
• arguments about updates wrt "goal": the deceptive alignment argument hinges a lot on "gradient of the goal" making sense. for example when we argue that the gradient on the model can be decomposed into one component that updates the goal to be more correct and another component that updates the capabilities to be more deceptive, we make this assumption. even if we assume away path dependence, the complexity argument depends a lot on the complexity being roughly equal to complexity of goal + complexity of general goal seeking circuitry, independent of goal.
• arguments about difficulty of disentangling correct and incorrect behaviors: there's a dual of retargetability which is something like the extent to which you can make narrow interventions to the behaviour. (some kind of "anti naturalness" argument)

[conjecture 1: retargetability == complexity can be decomposed == gradient of goal is meaningful. conjecture 2: gradient of goal is meaningful/complexity decomposition implies deceptive alignment (maybe we can also find some necessary condition?)]

how do we formalize retargetability?

• maybe something like there exists a homeomorphism from the goal space to NNs with that goal
• problem: doesn't really feel very satisfying and doesn't work at all for discrete things
• maybe complexity: retargetable if it has a really simple map from goals to NNs with goals, conditional on another NN with that goal
• problem: the training process of just training another NN from scratch on the new goal and ignoring the given NN could potentially be quite simple
• maybe complexity+time: seems reasonable to assume retraining is expensive (and maybe for decomposability we also consider complexity+time)

random idea: the hypothesis that complexity can be approximately decomposed into a goal component and a reasoning component is maybe a good formalization of (a weak version of) orthogonality?

a tentative model of ambitious research projects

when you do a big research project, you have some amount of risk you can work with - maybe you're trying to do something incremental, so you can only tolerate a 10% chance of failure, or maybe you're trying to shoot for the moon and so you can accept a 90% chance of failure.

budgeting for risk is non negotiable because there are a lot of places where risk can creep in - and if there isn't, then you're not really doing research. most obviously, your direction might just be a dead end. but there are also other things that might go wrong: the code might end up too difficult to implement, or it might run too slowly, or you might fail to fix a solvable-in-principle problem that comes up.

I claim that one of the principal components of being a good researcher is being able to eliminate as much unnecessary risk as possible, so you can spend your entire risk budget on the important bets.

for example, if you're an extremely competent engineer, when brainstorming experiments you don't have to think much about the risk that you fail to implement it. you know that even if you don't think through all the contingencies that might pop up, you can figue it out, because you have a track record of figuring it out. you can say the words "and if that happens we'll just scale it up" without spending much risk because you know full well that you can actually execute on it. a less competent engineer would have to pay a much greater risk cost, and correspondingly have to reduce the ambitiousness of the research bets (or else, take on way more risk than intented).

not all research bets are created equal, either. the space of possible research bets is vast, and most of them are wrong. but if you have very good research taste, you can much more reliably tell whether a bet is likely to work out. even the best researchers can't just look at a direction and know for sure if it will work, if you know that you get a good direction 10% of the time you can do a lot more than if your direction is only good 0.1% of the time.

finally, if you know and trust someone to be reliable at executing on their area of expertise, you can delegate things that fall in their domain to them. in practice, this can be quite tough and introduce risk unless they have a very legible track record, or you are sufficiently competent in their domain yourself to tell if they're likely to succeed. and if you're sufficiently competent to do the job of any of your report (even if less efficiently), then you can budget less risk here knowing that even if someone drops their ball you could always pick it up yourself.

https://arxiv.org/abs/2304.08612 : interesting paper with improvement on straight through estimator

https://arxiv.org/abs/2302.07011 : sharpness doesn't seem to correlate with generalization

the phenomenon of strange bedfellows is probably caused in no small part by outgroup vs fargroup dynamics

'And what ingenious maneuvers they all propose to me! It seems to them that when they have thought of two or three contingencies' (he remembered the general plan sent him from Petersburg) 'they have foreseen everything. But the contingencies are endless.'

We spend a lot of time on trying to figure out empirical evidence to distinguish hypotheses we have that make very similar predictions, but I think a potentially underrated first step is to make sure they actually fit the data we already have.

Is the correlation between sleeping too long and bad health actually because sleeping too long is actually causally upstream of bad health effects, or only causally downstream of some common cause like illness?

GPT-2-xl unembedding matrix looks pretty close to full rank (plot is singular values)

Unsupervised learning can learn things humans can't supervise because there's structure in the world that you need deeper understanding to predict accurately. For example, to predict how characters in a story will behave, you have to have some kind of understanding in some sense of how those characters think, even if their thoughts are never explicitly visible.

Unfortunately, this understanding only has to be structured in a way that makes reading off the actual unsupervised targets (i.e next observation) easy.

An incentive structure for scalable trusted prediction market resolutions

We might want to make a trustable committee for resolving prediction markets. We might be worried that individual resolvers might build up reputation only to exit-scam, due to finite time horizons and non transferability of reputational capital. However, shareholders of a public company are more incentivized to preserve the value of the reputational capital. Based on this idea, we can set something up as follows:

• Market creators pay a fee for the services of a resolution company
• There is a pool of resolvers who give a first-pass resolution. Each resolver locks up a deposit.
• If an appeal is requested, a resolution passes up through a series of committees of more and more senior resolvers
• At the top, a vote is triggered among all shareholders

Levels of difficulty:

1. Mathematically proven to be impossible (i.e perfect compression)
2. Impossible under currently known laws of physics (i.e perpetual motion machines)
3. A lot of people have thought very hard about it and cannot prove that it's impossible, but strongly suspect it is impossible (i.e solving NP problems in P)
4. A lot of people have thought very hard about it, and have not succeeded, but we have no strong reason to expect it to be impossible (i.e AGI)
5. There is a strong incentive for success, and the markets are very efficient, so that for participants with no edge, success is basically impossible (i.e beating the stock market)
6. There is a strong incentive for a thing, but a less efficient market, and it seems nobody has done it successfully (i.e a new startup idea that seems nobody seems to be doing)

Hopefully this is a useful reference for conversations that go like this:

A: Why can't we just do X to solve Y? B: You don't realize how hard Y is, you can't just think up a solution in 5 minutes A: You're just not thinking outside the box, [insert anecdote about some historical figure who figured out how to do a thing which was once considered impossible in some sense] B: No you don't understand, it's like actually not possible, not just like really hard, because of Z A: That's what they said about [historical figure]!

(random shower thoughts written with basically no editing)

Sometimes arguments have a beat that looks like "there is extreme position X, and opposing extreme position Y. what about a moderate 'Combination' position?" (I've noticed this in both my own and others' arguments)

I think there are sometimes some problems with this.

• Usually almost nobody is on the most extreme ends of the spectrum. Nearly everyone falls into the "Combination" bucket technically, so in practice you have to draw the boundary between "combination enough" vs "not combination enough to count as combination", which is sometimes fraught. (There is a dual argument beat that looks like "people too often bucket things into distinct buckets, what about thinking of things as a spectrum." I think this does the opposite mistake, because sometimes there really are relatively meaningful clusters to point to. (this seems quite reminiscent of one Scottpost that I can't remember the name of rn))
• In many cases, there is no easy 1d spectrum. Being a "combination" could refer to a whole set of mutually exclusive sets of views. This problem gets especially bad when the endpoints differ along many axes at once. (Another dual argument here that looks like "things are more nuanced than they seem" which has its own opposite problems)
• Of the times where this is meaningful, I would guess it almost always happens when the axis one has identified is interesting and captures some interesting property of the world. That is to say, if you've identified some kind of quantity that seems to be very explanatory, just noting that fact actually produces lots of value, and then arguing about how or whether to bucket that quantity up into groups has sharply diminishing value.
• In other words, introducing the frame that some particular latent in the world exists and is predictive is hugely valuable; when you say "and therefore my position is in between other people's", this is valuable due to the introduction of the frame. The actual heavy lifting happened in the frame, and the part where you point to some underexplored region of the space implied by that frame is actually not doing much work.
• I hypothesize one common thing is that if you don't draw this distinction, then it feels like the heavy lifting comes in the part where you do the pointing, and then you might want to do this within already commonly accepted frames. From the inside I think this feels like existing clusters of people being surprisingly closed minded, whereas the true reason is that the usefulness of the existing frame has been exhausted.

Subjective Individualism

TL;DR: This is basically empty individualism except identity is disentangled from cooperation (accomplished via FDT), and each agent can have its own subjective views on what would count as continuity of identity and have preferences over that. I claim that:

1. Continuity is a property of the subjective experience of each observer-moment (OM), not necessarily of any underlying causal or temporal relation. (i.e I believe at this moment that I am experiencing continuity, but this belief is a fact of my current OM only. Being a Boltzmann brain that believes I experienced all the moments leading up to that moment feels exactly the same as "actually" experiencing things.)
2. Each OM may have beliefs about the existence of past OMs, and about causal/temporal relations between those past OMs and the current OM (i.e one may believe that a memory of the past did in fact result from the faithful recording of a past OM to memory, as opposed to being spawned out of thin air as a Boltzmann brain loaded with false memories.)
3. Something like preference utilitarianism is true and it is ok to have preferences about things you cannot observe, or prefer the world to be in one of two states that you cannot in any way distinguish. As a motivating example, one can have preferences between taking atomic actions (a) enter the experience machine and erase all memories of choosing to be in an experience machine and (b) doing nothing.
4. Each OM may have preferences for its subjective experience of continuity to correspond to some particular causal structure between OMs, despite this being impossible for that OM to observe or verify. This is where the subjectivity is introduced: each OM can have its own opinion on which other OMs it considers to also be "itself"), and it can have preferences over its self-OMs causally leading to itself in a particular way. This does not have to be symmetric; for instance, your past self may consider your future self to be more self like than your future self considers past self.
5. Continuity of self as viewed by each OM is decoupled from decision theoretic cooperation. i.e they coincide in a typical individual, who considers their past/future selves to be also themself, and cooperates decision theoretically (i.e you consider past/future you getting utility to both count as "you" getting utility). However it is also possible to cooperate to the same extent with OMs with whom you do not consider yourself to be the same self (i.e twin PD), or to not coordinate with yourself (i.e myopia/ADHD).

(related: FDT and myopia being much the same thing; you can think of caring about future selves’ rewards because you consider yourself to implement a similar enough algorithm to your future self as acausal trade. This has the nice property of unifying myopia and preventing acausal trade, in that acausal trade is really just caring about OMs that would not be considered the same “self”. This is super convenient because basically every time we talk about myopia for preventing deceptive mesaoptimization we have to hedge by saying “and also we need to prevent acausal trade somehow”, and this lets us unify the two things.)

Properties of this theory:

• This theory allows one to have preferences such as “I want to have lots of subjective experiences into the future” or “I prefer to have physical continuity with my past self” despite rejecting any universal concept of identity which seems pretty useful
• This theory is fully compatible with all sorts of thought experiments by simply not providing an answer as to which OM your current OM leads to “next”. This is philosophically unsatisfying but I think the theory is still useful nonetheless
• Coordination is solved through decision theory, which completely disentangles it from identity.

Imagine if aliens showed up at your doorstep and tried to explain to you that making as many paperclips as possible was the ultimate source of value in the universe. They show pictures of things that count as paperclips and things that don't count as paperclips. They show you the long rambling definition of what counts as a paperclip from Section 23(b)(iii) of the Declaration of Paperclippian Values. They show you pages and pages of philosophers waxing poetical about how paperclips are great because of their incredible aesthetic value. You would be like, "yeah I get it, you consider this thing to be a paperclip, and you care a lot about them." You could probably pretty accurately tell whether the aliens would approve of anything you'd want to do. And then you wouldn't really care, because you value human flourishing, not paperclips. I mean, it's so silly to care about paperclips, right? 

Of course, to the aliens, who have not so subtly indicated that they would blow up the planet and look for a new, more paperclip-loving planet if they were to detect any anti-paperclip sentiments, you say that you of course totally understand and would do anything for paperclips, and that you definitely wouldn't protest being sent to the paperclip mines. 

random thoughts. no pretense that any of this is original or useful for anyone but me or even correct

• It's ok to want the world to be better and to take actions to make that happen but unproductive to be frustrated about it or to complain that a plan which should work in a better world doesn't work in this world. To make the world the way you want it to be, you have to first understand how it is. This sounds obvious when stated abstractly but is surprisingly hard to adhere to in practice.
• It would be really nice to have some evolved version of calibration training where I take some historical events and try to predict concrete questions about what happened, and give myself immediate feedback and keep track of my accuracy and calibration. Backtesting my world model so to speak. Might be a bit difficult to measure accuracy improvments due to non iid ness of the world, but worth trying the naive thing regardless. Would be interesting to try and autogen using GPT3.
• Feedback loops are important. Unfortunately, from the inside it's very easy to forget. In particular, setting up feedback loops is often high friction, because it's hard to measure the thing we care about. Fixing this general problem is probably hard but in the meantime I can try to setup feedback loops for important things like productivity, world modelling, decision making, etc

Thought pattern that I've noticed: I seem to have two sets of epistemic states at any time: one more stable set that more accurately reflects my "actual" beliefs that changes fairly slowly, and one set of "hypothesis" beliefs that changes rapidly. Usually when I think some direction is interesting, I alternate my hypothesis beliefs between assuming key claims are true or false and trying to convince myself either way, and if I succeed then I integrate it into my actual beliefs. In practice this might look like alternating between trying to prove something is impossible and trying to exhibit an example, or taking strange premises seriously and trying to figure out its consequences. I think this is probably very confusing to people because usually when talking to people who are already familiar with alignment I'm talking about implications of my hypothesis beliefs, because that's the frontier of what I'm thinking about, and from the outside it looks like I'm constantly changing my mind about things. Writing this up partially to have something to point people to and partially to push myself to communicate this more clearly.