Epistemic Status: My best guess
Epistemic Effort: ~75 hours of work put into this document
Contributions: Thomas wrote ~85% of this, Eli wrote ~15% and helped edit + structure it. Unless specified otherwise, writing in the first person is by Thomas and so are the opinions. Thanks to Miranda Zhang, Caleb Parikh, and Akash Wasil for comments. Thanks to many others for relevant conversations.
Despite a clear need for it, a good source explaining who is doing what and why in technical AI alignment doesn't exist. This is our attempt to produce such a resource. We expect to be inaccurate in some ways, but it seems great to get out there and let Cunningham’s Law do its thing.
The main body contains our understanding of what everyone is doing in technical alignment and why, as well as at least one of our opinions on each approach. We include supplements visualizing differences between approaches and Thomas’s big picture view on alignment. The opinions written are Thomas and Eli’s independent impressions, many of which have low resilience. Our all-things-considered views are significantly more uncertain.
This post was mostly written while Thomas was participating in the 2022 iteration SERI MATS program, under mentor John Wentworth. Thomas benefited immensely from conversations with other SERI MATS participants, John Wentworth, as well as many others who I met this summer.
A summary of our understanding of each approach:
Empirical examples and understanding ML inductive biases
Creating datasets for evaluation + inverse scaling prize
Previous related overviews include:
One of the key problems in AI safety is that there are many ways for an AI to generalize off-distribution, so it is very likely that an arbitrary generalization will be unaligned. See the model splintering post for more detail. Stuart's plan to solve this problem is as follows:
They are currently working on algorithms to accomplish step 1: see Value Extrapolation.
Their initial operationalization of this problem is the lion and husky problem. Basically: if you train an image model on a dataset of images of lions and huskies, the lions are always in the desert, and the huskies are always in the snow. So the problem of learning a classifier is under-defined: should the classifier be classifying based on the background environment (e.g. snow vs sand), or based on the animal in the image?
A good extrapolation algorithm, on this problem, would generate classifiers that extrapolate in all the different ways, and so the 'correct' extrapolation must be in this generated set of classifiers. They have also introduced a new dataset for this, with a similar idea: Happy Faces.
Step 2 could be done in different ways. Possibilities for doing this include: conservatism, generalized deference to humans, or an automated process for removing some goals. like wireheading/deception/killing everyone.
Opinion: I like that this approach tries to tackle distributional shift, which might I see as one of the fundamental hard parts of alignment.
The problem is that I don't see how to integrate this approach for solving this problem with deep learning. It seems like this approach might work well for a model-based RL setup where you can make the AI explicitly select for this utility function.
It is unclear to me how to use this to align an end-to-end AI training pipeline. The key problem unsolved by this is how to get inner values into a deep learning system via behavioral gradients: reward is not the optimization target. Generating a correct extrapolation of human goals does not let us train a deep learning system to accomplish these goals.
ARC is trying to solve Eliciting Latent Knowledge (ELK). Suppose that you are training an AI agent that predicts the state of the world and then performs some actions, called a predictor. This predictor is the AGI that will be acting to accomplish goals in the world. How can you create another model, called a reporter, that tells you what the predictor believes about the world? A key challenge in training this reporter is that training your reporter on human labeled training data, by default, incentivizes the predictor to just model what the human thinks is true, because the human is a simpler model than the AI.
Motivation: At a high level, Paul's plan seems to be to produce a minimal AI that can help to do AI safety research. To do this, preventing deception and inner alignment failure are on the critical path, and the only known solution paths to this require interpretability (this is how all of Evan's 11 proposals plan to get around this problem).
If ARC can solve ELK, this would be a very strong form of interpretability: our reporter is able to tell us what the predictor believes about the world. Some ways this could end up being useful for aligning the predictor include:
Opinion: There are several key uncertainties that I have with this approach.
Overall, ELK seems like one of the most promising angles of attack on the problem because it seems both possible to make progress on and also actually useful towards solving alignment: if it works it would let us avoid deception. It is simple and naturally becomes turned into a proposal for alignment. I'm very excited about more effort being put towards solving ELK.
While this seems like a very powerful form of interpretability, there are also some limitations, for example, solving ELK does not immediately tell you how the internals of your agent works, as would be required for a plan like retargeting the search.
Beth is working on “generating a dataset that we can use to evaluate how close models are to being able to successfully seek power”. The dataset is being created through simulating situations in which an LLM is trying to seek power.
The overall goal of the project is to assess how close a model is to being dangerous, e.g. so we can know if it’s safe for labs to scale it up. Evaluations focus on whether models are capable enough to seek power successfully, rather than whether they are aligned. They are aiming to create an automated evaluation which takes in a model and outputs how far away from dangerous it is, approximating an idealized human evaluation.
Eli’s opinion: I’m very excited about this direction, but I think for a slightly different reason than Beth is. There’s been lots of speculation about how close the capabilities of current systems are to being able to execute complex strategies like “playing the training game”, but very little empirical analysis of how “situationally aware” models actually are. The automated metric is an interesting idea, but I’m most excited about getting a much better understanding of the situational awareness of current models through rigorous human evaluation; the project also might produce compelling examples of attempts at misaligned power-seeking in LLMs that could be very useful for field-building (convincing ML researchers/engineers).
Opinion: I think this only works in a slowish takeoff world where we can continuously measure deception. I am ~70% in a world where AGI capabilities jump fast enough that this type of evaluation doesn't help. It seems really hard to know when AGI will come.
In the world where takeoffs are slow enough that this is meaningful, the difficulty then becomes getting labs to actually slow down based on this data: if this worked, it would be hugely valuable. Even if it doesn't get people to slow down, it might help inform alignment research about likely failure modes for LLMs.
Anthropic fine tuned a language model to be more helpful, honest and harmless: HHH.
Motivation: I think the point of this is to 1) see if we can "align" a current day LLM, and 2) raise awareness about safety in the broader ML community.
Opinion: This seems… like it doesn't tackle what I see as the core problems in alignment. This may make current day language models being less obviously misaligned, but that doesn't seem like that helps us at all to align AGIs.
Chris Olah, the interpretability legend, is working on looking really hard at all the neurons to see what they all mean. The approach he pioneered is circuits: looking at computational subgraphs of the network, called circuits, and interpreting those. Idea: "decompiling the network into a better representation that is more interpretable". In-context learning via attention heads, and interpretability here seems useful.
One result I heard about recently: a linear softmax unit stretches space and encourages neuron monosemanticity (making a neuron represent only one thing, as opposed to firing on many unrelated concepts). This makes the network easier to interpret.
Motivation: The point of this is to get as many bits of information about what neural networks are doing, to hopefully find better abstractions. This diagram gets posted everywhere, the hope being that networks, in the current regime, will become more interpretable because they will start to use abstractions that are closer to human abstractions.
Opinion: This seems like it won't scale up to AGI. I think that model size is the dominant factor in making things difficult to interpret, and so as model size scales to AGI, things will become ever less interpretable. If there was an example of networks becoming more interpretable as they got bigger, this would update me (and such an example might already exist, I just don't know of it).
I would love a new paradigm for interpretability, and this team seems like probably the best positioned to find such a paradigm.
There is a difficult balance to be made here, because publishing research helps with both alignment and capabilities. They are very aware of this, and have thought a lot about this information tradeoff, but my inclination is that they are on the wrong side: I would rather they publish less. Even though this research helps safety some, buying more time is just more important than knowing more about safety right now.
The basic idea is to figure out how model performance scales, and use this to help understand and predict what future AI models might look like, which can inform timelines and AI safety research. A classic result found that you need to increase data, parameters, and compute all at the same time (at roughly the same rate) in order to improve performance. Anthropic extended this research here.
Opinion: I am guessing this leads to capabilities gains because it makes the evidence for data+params+compute = performance much stronger and clearer. Why can't we just privately give this information to relevant safety researchers instead of publishing it publicly?
I'm guessing that the point of this was to shift ML culture: this is something valuable and interesting to mainstream ML practitioners which means they will read this safety focused paper.
[Disclaimer: haven't read the whole sequence]. This is primarily Steven Brynes, a full time independent alignment researcher, working on answering the question: "How would we align an AGI whose learning algorithms / cognition look like human brains?"
Humans seem to robustly care about things, why is that? If we understood that, could we design AGIs to do the same thing? As far as I understand it, most of this work is biology based: trying to figure out how various parts of the brain works, but then also connecting this to alignment and seeing if we can solve the alignment problem with this understanding.
There are three other independent researchers working on related projects that Steven has proposed.
Opinion: I think it's quite likely that we get useful bits of information and framings from this analysis. On the current margin, I think it is very good that we have some people thinking about brain-like AGI safety, and I also think this research is less likely to be dual use.
I also find it unlikely (~30%) that we'll get brain-like AGI as opposed to prosaic AGI.
Rewritten slightly after Thomas Woodside (an employee of CAIS) commented. I recommend reading his comment, as well as their sequence, Pragmatic AI Safety, which lays out a more flushed out description of their theory of impact.
Right now, only a very small subset of ML researchers are thinking about x-risk from AGI. CAIS seeks to change this -- their goal is to get the broader ML community, including both industry and academia.
CAIS is working on a number of projects, including:
One of these competitions is a Trojan detection competition, which is a way of operationalizing deceptive alignment. A Trojan is a backdoor into a neural network that causes it to behave weirdly on a very specific class of inputs. These are often trained into a model via poisoned data. Trojans are similar to deceptive alignment because there are a small number of examples (e.g. 300 out of 3 million training examples) that cause very different behavior (e.g. a treacherous turn), while for the vast majority of inputs cause the model to perform normally.
This competition is in a builder breaker format, with rewards for both detecting trojans as well as coming up with trojans that no one else could detect.
Opinion: One worry with the competition is that contestants will pursue strategies that work right now but won't work for AGI, because they are trying to win the competition instead of align AGIs.
Engaging the broader ML community to reduce AGI x-risk seems robustly good both for improving the quality of the discourse and steering companies and government away from building AGI unsafely.
CHAI is an academic research organization affiliated with UC Berkeley. It is lead by Stuart Russell, but includes many other professors and grad students pursuing a diverse array of approaches, most of whom I will not summarize here. For more information see their 2022 progress report.
Stuart wrote the book Human Compatible, in which he outlines his AGI alignment strategy, which is based on cooperative inverse reinforcement learning (CIRL). The basic idea of CIRL is to play a cooperative game where both the agent and the human are trying to maximize the human's reward, but only the human knows what the human reward is. Since the AGI has uncertainty it will defer to humans and be corrigible.
Other work that I liked is Clusterability in neural networks: try to measure the modularity of neural networks by thinking of the network as a graph and performing the graph n-cut.
Opinion: CIRL might make sense in a non-deep learning paradigm, but I think that deep learning will scale to AGI (~95%). The problem of getting a deep learning system to 'try' to maximize the human's reward is the hard part. Viewed this way, CIRL is a wrong way reduction. Some discussion on this is here.
Eli’s opinion: My understanding is that both Stuart and others mainly expect CIRL to potentially be helpful if deep learning doesn’t scale to AGI, but I expect deep learning to scale to AGI with >80% probability.
CLR is focused primarily on reducing suffering-risk (s-risk), where the future has a large negative value. They do foundational research in game theory / decision theory, primarily aimed at multipolar AI scenarios. One result relevant to this work is that transparency can increase cooperation.
Update after Jesse Clifton commented: CLR also works on improving coordination for prosaic AI scenarios, risks from malevolent actors and AI forecasting. The Cooperative AI Foundation (CAIF) shares personnel with CLR, but is not formally affiliated with CLR, and does not focus just on s-risks.
Opinion: I have <1% credence in agential s-risk happening, which is where most of the worry from s-risk is as far as I can tell. I have ~70% on x-risk from AGI, so I don't think s-risk is worth prioritizing. I also view the types of theoretical research done here as being not very tractable.
I also find it unlikely (<10%) that logic/mathy/decision theory stuff ends up being useful for AGI alignment.
Eli’s opinion: I haven’t engaged with it much but am skeptical for similar reasons to Thomas, though I have closer to ~5% on s-risk.
Conjecture is an applied org focused on aligning LLMs (Q & A here). Conjecture has short timelines (the org acts like timelines are between ~5-10 year, but some have much shorter timelines, such as 2-4 years), and they think alignment is hard. They take information hazards (specifically ideas that could lead towards better AI capabilities) very seriously, and have a public infohazard document.
The alignment problem is really hard to do science on: we are trying to reason about the future, and we only get one shot, meaning that we can't iterate. Therefore, it seems really useful to have a good understanding of meta-science/epistemology, i.e. reasoning about ways to do useful alignment research.
An example post I thought was very good.
Opinion: Mixed. One part of me is skeptical that we should be going up a meta layer instead of trying to directly solve the problem — solving meta-science seems really hard and quite indirect. On the other hand, I consistently learn a lot from reading Adam's posts, and I think others do too, and so this work does seem really helpful.
This would seem to be more useful in the long timelines world, contradicting Conjecture's worldview, however, another key element of their strategy is decorrelated research bets, and this is certainly quite decorrelated.
Eli’s opinion: I’m a bit more positive on this than Thomas, likely because I have longer timelines (~10-15% within 10 years, median ~25-30 years).
I don't know much about their research here, other than that they train their own models, which allow them to work on models that are bigger than the biggest publicly available models, which seems like a difference from Redwood.
Current interpretability methods are very low level (e.g., "what does x neuron do"), which does not help us answer high level questions like "is this AI trying to kill us".
They are trying a bunch of weird approaches, with the goal of scalable mechanistic interpretability, but I do not know what these approaches actually are.
Motivation: Conjecture wants to build towards a better paradigm that will give us a lot more information, primarily from the empirical direction (as distinct from ARC, which is working on interpretability with a theoretical focus).
Opinion: I like the high level idea, but I have no idea how good the actual research is.
Refine is an incubator for new decorrelated alignment "research bets". Since no approach is very promising right now for solving alignment, the purpose of this is to come up with a bunch of independent new ideas, and hopefully some of these will work.
Opinion: Refine seems great because focusing on finding new frames seems a lot more likely to succeed than the other ideas.
Eli’s opinion: Agree with Thomas, I’m very excited about finding smart people with crazy-seeming decorrelated ideas and helping them.
The goal of this is to create a non-agentic AI, in the form of an LLM, that is capable of accelerating alignment research. The hope is that there is some window between AI smart enough to help us with alignment and the really scary, self improving, consequentialist AI. Some things that this amplifier might do:
A LLM can be thought of as learning the distribution over the next token given by the training data. Prompting the LM is then like conditioning this distribution on the start of the text. A key danger in alignment is applying unbounded optimization pressure towards a specific goal in the world. Conditioning a probability distribution does not behave like an agent applying optimization pressure towards a goal. Hence, this avoids goodhart-related problems, as well as some inner alignment failure.
One idea to get superhuman work from LLMs is to train it on amplified datasets like really high quality / difficult research. The key problem here is finding the dataset to allow for this.
There are some ways for this to fail:
Conjecture are aware of these problems and are running experiments. Specifically, an operationalization of the inner alignment problem is to make an LLM play chess. This (probably) requires simulating an optimizer trying to win at the game of chess. They are trying to use interpretability tools to find the mesa-optimizers in the chess LLM that is the agent trying to win the game of chess. We haven't ever found a real mesa-optimizer before, and so this could give loads of bits about the nature of inner alignment failure.
My opinion: This work seems robustly useful in understanding how we might be able to use tool AIs to solve the alignment problem. I am very excited about all of this work, and the motivation is very clear to me.
Eli’s opinion: Agree with Thomas.
David runs a lab at the University of Cambridge. Some things he is working on include:
For work done on (1), see: Goal Misgeneralization, a paper that empirically demonstrated examples of inner alignment failure in Deep RL environments. For example, they trained an agent to get closer to cheese in a maze, but where the cheese was always in the top right of a maze in the training set. During test time, when presented with cheese elsewhere, the RL agent navigated to the top right instead of to the cheese: it had learned the mesa objective of "go to the top right".
For work done on (2), see OOD Generalization via Risk Extrapolation, an iterative improvement on robustness to previous methods.
I'm not sure what his motivation is for these specific research directions, but my guess is that these are his best starts on how to solve the alignment problem.
Opinion: I'm mixed on the Goal Misgeneralization. On one hand, it seems incredibly good to simply be able to observe misaligned mesaoptimization in the wild. On the other hand, I feel like I didn't learn much from the experiment because there are always many ways that the reward function could vary OOD. So whatever mesa objective was learned this system would therefore be a 'misaligned mesaoptimizer' with respect to all of the other variations OOD. (The paper states that goal misgeneralization is distinct from mesaoptimization, and I view this as mostly depending on what your definition of optimizer is, but I think that I'd call pretty much any RL agent an optimizer.) I view also view this as quite useful for getting more of academia interested in safety concerns, which I think is critical for making AGI go well.
I'm quite excited about understanding generalization better, particularly while thinking about goal misgneralization, this seems like a very useful line of research.
Updated after Rohin's comment.
DeepMind has both a ML safety team focused on near-term risks, and an alignment team that is working on risks from AGI. The alignment team is pursuing many different research avenues, and is not best described by a single agenda.
Some of the work they are doing is:
See Rohin's comment for more research that they are doing, including description of some that is currently unpublished so far.
Opinion: I am negative about DeepMind as a whole because it is one of the organizations closest to AGI, so DeepMind is incentivizing race dynamics and reducing timelines.
However, the technical alignment work looks promising and appears to be tackling difficult problems that I see as the core difficulties of alignment like inner alignment/sharp left turn problems, as well as foundational research understanding agents. I am very excited about DeepMind engaging with MIRI's arguments.
Dylan's PhD thesis argues three main claims (paraphrased):
Thus, his motivations seem to be modeling AGI coming in some multi-agent form, and also being heavily connected with human operators.
I'm not sure what he is currently working on, but some recent alignment-relevant papers that he has published include:
Dylan has also published a number of articles that seem less directly relevant for alignment.
Opinion: I don't see how this gets at the core problems in alignment, which I view as being related to inner alignment / sharp left turn / distribution shift, and I wish that outer alignment approaches also focused on robustness to distribution shift. How do you get this outer alignment solution into the deep learning system? However, if there is a way to do this (with deep learning) I am super on board and would completely change my mind. The more recent stuff seems less relevant.
Enclutured are making a multiplayer online video game as a test environment for AI: an aligned AI should be able to play the game without ruining the fun or doing something obviously destructive like completely taking over the world, even if it has this capabilities. This seems roughly analogous to setting an AGI loose on the real world.
Motivation: Andrew Critch is primarily concerned about a multipolar AI scenario: there are multiple actors with comparably powerful AI, on the cusp of recursive self improvement. The worst case is a race, and even though each actor would want to take more time checking their AGI for safety, worry that another actor will deploy will push each actor to take shortcuts and try to pull off a world-saving act. Instead of working directly on AI, which can accelerate timelines and encourage racing, creating this standardized test environment where alignment failures are observable is one component of a good global outcome.
Opinion: I don't really see how this helps, on my models we mostly have one shot: by the time we see the core difficulties of alignment, we are past the point of no return, because that AGI is sufficiently powerful to control the world. Therefore the alignment failures that we can observe in this game seem like they won't give us useful information.
On the other hand, this might be really helpful in slow takeoff worlds where alignment failures are obvious in the video game (e.g. deception isn't selected for), and these failures are relatively easy to fix.
Idea: Make the AGI, which is an LLM, externalize its reasoning (via chain of thought) so that its thoughts are visible to an external overseer, which then verifies that the LLM is not thinking deceptive thoughts.
This scheme requires:
A key dynamic is that english is not the ideal language to be reasoning: an AGI could be more capable by doing some reasoning not in English. Thus, applying RL to a model exerts pressure towards ideal logical reasoning. However, self-supervised learning (SSL) exerts some pressure back towards just doing text prediction, and hence more of its reasoning being in English. A key question for this research agenda is thus how to put pressure to keep the reasoning externalized, instead of collapsing into internal, more efficient/logical reasoning that is much harder for us to oversee.
Opinion: This seems like it gets us a little further because we can now apply some RL, which might cause deception that is now catchable, so long as the RL doesn't push it so that the chain of thought itself is steganographic and hence not understandable to humans.
Also, catching the deception is only a small part of the battle: in worlds where deception is a big problem, we need to find ways to optimize against it, and this only gives us a small number of bits of optimization pressure.
Overall, this seems worth exploring more, I'm generally excited about more theoretical approaches on the above issues, as well as doing experiments about whether deception is a problem by default for chain of thought LLMs, which would give information on how likely deception is in general.
One problem (identified by John Wentworth) with this strategy is that the AI might cause large bad side effects, like wiping out humans without intent, simply because the AGI wants to use the earth for something else, and this won't trigger the oversight schemes. This seems like a problem, but this project still is clear progress towards solving alignment.
Eli’s opinion: Seems promising, though significantly more promising on shorter timelines where something like current LLMs scale to AGI.
FHI does a lot of work on non-technical AI safety, but as far as I know their primary technical agenda is the Causal incentives group (joint between FHI and DeepMind), who uses notions from causality to study incentives and their application to AI Safety. Recent work includes:
Opinion: I haven't read this research in depth, but I don't understand the focus on causality as necessarily the best way to do theory work on alignment.
Description copied from a comment by board member Adam Gleave
FAR's theory of change is to incubate new, scalable alignment research agendas. Right now I see a small range of agendas being pursued at scale (largely RLHF and interpretability), then a long tail of very diverse agendas being pursued by single individuals (mostly independent researchers or graduate students) or 2-3 person teams. I believe there's a lot of valuable ideas in this long tail that could be scaled, but this isn't happening due to a lack of institutional support. It makes sense that the major organisations want to focus on their own specific agendas -- there's a benefit to being focused! -- but it means a lot of valuable agendas are slipping through the cracks.
FAR's current approach to solving this problem is to build out a technical team (research engineers, junior research scientists, technical communication specialists) and provide support to a broad range of agendas pioneered by external research leads. Those that work, FAR will double down on and invest more in. This model has had a fair amount of demand already so there's product-market fit, but we still want to iterate and see if we can improve the model. For example, long-term FAR might want to bring some or all research leads in-house.
In terms of concrete agendas, an example of some of the things FAR is working on:
You can read more about FAR in their launch post.
Eli's opinion: New, scalable alignment research agendas seem great to me in theory. I don't have strong opinions on the concrete agendas FAR is working on thus far; they seem interesting but hard to evaluate their usefulness without more deeply understanding the motivations (I skimmed the inverse scaling justification and felt a bit skeptical/unconvinced of direct usefulness, though it might be pretty useful for field-building).
MIRI thinks technical alignment is really hard, and that we are very far from a solution. However, they think that policy solutions have even less hope. Generally, I think of their approach as supporting a bunch of independent researchers following their own directions, hoping that one of them will find some promise. They mostly buy into the security mindset: we need to know exactly (probably mathematically formally) what we are doing, or the massive optimization pressure will default in ruin.
Opinion: I wish that they would try harder to e.g. do more mentorship, do more specific 1-1 outreach, do more expansion, and try more different things. I also wish they would communicate more and use less metaphors: instead of a dialogue about rockets, explain why alignment needs math. Why this reference class instead of any other?
Now I'll list some of the individual directions that they are pursuing:
Recently they've been trying to communicate their worldview, in particular, how incredibly doomy they are, perhaps in order to move other research efforts towards what they see as the hard problems.
Opinion: I am glad that they are trying to communicate this, because I think it caused a lot of people to think through their plans to deal with these difficulties. For example, I really liked the DeepMind alignment team's response to AGI ruin.
Eli’s opinion: I also really appreciate these posts. I generally think they are pointing at valuable considerations, difficulties, etc. even if I’m substantially more optimistic than them about the potential to avoid them (my p(doom) is ~45%).
I don't know a lot about this. Read Evan's research agenda for more information.
It seems likely that deceptive agents are the default, so a key problem in alignment is to figure out how we can avoid deceptive alignment at every point in the training process. This seems to rely on being able to consistently exert optimization pressure against deception, which probably necessitates interpretability tools.
His plan to do this right now is acceptability verification: have some predicate that precludes deception, and then check your model for this predicate at every point in training.
One idea for this predicate is making sure that the agent is myopic, meaning that the AI only cares about the current timestep, so there is no incentive to deceive, because the benefits of deception happen only in the future. This is operationalized as “return the action that your model of HCH would return, if it received your inputs.”
Opinion: I think this is a big problem that it would be good to have more understanding of, and I think the primary bottleneck for this is understanding the inductive biases of neural networks.
I'm skeptical of the speed prior or myopia is the right way of getting around this. The speed prior seems to take a large capabilities hit because the speed prior is not predictive about the real world. Myopia seems weird to me overall because I don't know what we want to do with a myopic agent: I think a better frame on this is simulacra theory.
Eli’s opinion: I haven’t engaged much with this but I feel intuitively skeptical of the myopia stuff; Eliezer’s arguments in this thread seem right to me.
They are working on fundamental problems like embeddedness, decision theory, logical counterfactuals, and more. A big advance was Cartesian Frames, a formal model of agency.
Opinion: This is wonderful work on deconfusing fundamental questions of agency. It doesn't seem like this will connect with the real world in time for AGI, but it seems like a great building block.
See Vanessa's research agenda for more detail.
If we don't know how to do something given unbounded compute, we are just confused about the thing. Going from thinking that chess was impossible for machines to understanding minimax was a really good step forward for designing chess AIs, even though minimax is completely intractable.
Thus, we should seek to figure out how alignment might look in theory, and then try to bridge the theory-practice gap by making our proposal ever more efficient.The first step along this path is to figure out a universal RL setting that we can place our formal agents in, and then prove regret bounds in.
A key problem in doing this is embeddedness. AIs can't have a perfect self model — this would be like imagining your ENTIRE brain, inside your brain. There are finite memory constraints. Infra-Bayesianism (IB) is essentially a theory of imprecise probability that lets you specify local / fuzzy things. IB allows agents to have abstract models of themselves, and thus works in an embedded setting.
Infra-Bayesian Physicalism (IBP) is an extension of this to RL. IBP allows us to
Vanessa uses this formalism to describe PreDCA, an alignment proposal based on IBP. This proposal assumes that an agent is an IBP agent, meaning that it is an RL agent with fuzzy probability distributions (along with some other things). The general outline of this proposal is as follows:
Vanessa models an AI as a model based RL system with a WM, a reward function, and a policy derived from the WM + reward. She claims that this avoids the sharp left turn. The generalization problems come from the world model, but this is dealt with by having an epistemology that doesn't contain bridge rules, and so the true world is the simplest explanation for the observed data.
It is open to show that this proposal also solves inner alignment, but there is some chance that it does.
This approach deviates from MIRI's plan, which is to focus on a narrow task to perform the pivotal act, and then add corrigibility. Vanessa instead tries to directly learn the user's preferences, and optimize those.
Opinion: Seems quite unlikely (<10%) for this type of theory to connect with deep learning in time (but this is based on median ~10 year timelines, I'm a lot more optimistic about this given more time). On the other hand, IB directly solves non-realizability, a core problem in embedded agency.
Also, IBP has some weird conclusions like the monotonicity principle: the AI's utility function has to be increasing in the number of computations running, even if these computations would involve the experience of suffering.
In the worlds the solution to alignment requires formally understanding AIs, Infra-Bayesianism seems like by far the most promising research direction that we know of. I am excited about doing more research in this direction, but also I'm excited for successor theories to IBP.
This project is to create a language dataset where the characters think out loud a lot, so that when we train an advanced LLM on this dataset, it will be thinking out loud and hence interpretable.
Opinion: Seems reasonable enough.
Jacob Steinhardt is a professor at UC Berkeley who works on conceptual alignment. He seems to have a broad array of research interests, but with some focus on robustness to distribution shift.
A technical paper he wrote is Certified defenses against adversarial examples: a technique for creating robust networks in the sense that an adversary has to shift the input image by some constant in order to cause a certain drop in test performance. He's also researched the mechanics of distribution shift, and found that different distribution shifts induce different robustness performance.
He's published several technical overviews including AI Alignment Research Overview and Concrete problems in AI safety, and created an AI forecasting competition.
Opinion: I think it is very valuable to develop a better understanding of distribution shifts, because I view that at the heart of the difficulty of alignment.
The safety team at OpenAI's plan is to build a MVP aligned AGI that can help us solve the full alignment problem.
They want to do this with Reinforcement Learning from Human Feedback (RLHF): get feedback from humans about what is good, i.e. give reward to AI's based on the human feedback. Problem: what if the AI makes gigabrain 5D chess moves that humans don't understand, so can't evaluate. Jan Leike, the director of the safety team, views this (the informed oversight problem) as the core difficulty of alignment. Their proposed solution: an AI assisted oversight scheme, with a recursive hierarchy of AIs bottoming out at humans. They are working on experimenting with this approach by trying to get current day AIs to do useful supporting work such as summarizing books and criticizing itself.
OpenAI also published GPT-3, and are continuing to push LLM capabilities, with GPT-4 expected to be released at some point soon.
See also: Common misconceptions about OpenAI and Our approach to alignment research.
Opinion: This approach focuses almost entirely on outer alignment, and so I'm not sure how this is planning to get around deception. In the unlikely world where deception isn't the default / inner alignment happens by default, this alignment plan seems and complicated and therefore vulnerable to the godzilla problem. I also think it relies on very slow takeoff speeds: the misaligned AGI has to help us design a successor aligned AGI, and this only works when the AGI doesn't recursively self improve to superintelligence.
Overall, the dominant effect of OpenAI pushes is that they advance capabilities, which seems really bad because it shortens AGI timelines.
Eli’s opinion: Similar to Thomas. I’m generally excited about trying to automate alignment research, but relatively more positive on Conjecture’s approach since it aims to use non-agentic systems.
Ought aims to automate and scale open-ended reasoning through Elicit, an AI research assistant. Ought focuses on advancing process-based systems rather than outcome-based ones, which they believe to be both beneficial for improving reasoning in the short term and alignment in the long term. Here they argue that in the long run improving reasoning and alignment converge.
So Ought’s impact on AI alignment has 2 components: (a) improved reasoning of AI governance & alignment researchers, particularly on long-horizon tasks and (b) pushing supervision of process rather than outcomes, which reduces the optimization pressure on imperfect proxy objectives leading to “safety by construction”. Ought argues that the race between process and outcome-based systems is particularly important because both states may be an attractor.
Eli’s opinion (Eli used to work at Ought): I am fairly optimistic about (a), the general strategy of applying AI in a differentially helpful way for alignment via e.g. speeding up technical alignment research or improving evaluations of alignment-aimed policies. Current Elicit is too broadly advertised to all researchers for my taste; I’m not sure whether generally speeding up science is good or bad. I’m excited about a version of Elicit that is more narrowly focused on helping with alignment (and perhaps longtermist research more generally), which I hear may be in the works.
I’m less optimistic about (b) pushing process-based systems, it seems like a very conjunctive theory of change to me. It needs to go something like: process-based systems are competitive with end-to-end training for AGI (which may be unlikely, see e.g. Rohin’s opinion here; and my intuition is that HCH doesn’t work), process-based systems are substantially more aligned than end-to-end training while being as capable (feels unlikely to me; even if it helps a bit it probably needs to help a lot to make the difference between catastrophe and not), and Ought either builds AGI or strongly influences the organization that builds AGI. Off the cuff I’d give something like 10%, 3%, 1% for these respectively (conditioned on the previous premises) which multiplies to .003%; this might be fine given the stakes (it’s estimated to be worth $17-$167M via .01% Fund proposal assuming AI x-risk is 50%) but it doesn’t feel like one of the most promising approaches.
The following diagram describing an adversarial oversight scheme to do for aligning an RL agent:
Motivation: The point of this approach is to create extremely reliable AI where it will never engage in certain types of behavior, for example, killing all humans, or deceiving its creators. A practice problem is to get any kind of behavior extremely reliably out of current day LLMs. The way Redwood operationalized this is by trying to train an LLM to have the property that they finish the prompt such that no humans get hurt (technically slightly weaker than this — only the AI believes no one gets hurt).
Opinion: This seems like a reasonable applied alignment project because it is a technique that could solve alignment for worlds in which alignment is pretty easy: if we just train the model to not hurt people, not take over the world, etc, then it'll just work. More specifically, we use either humans or amplified humans to get the description of the bad thing, then train a model that can very reliably simulate this description (and is much quicker to query than a human). Then, when we train the AI agent, we use this model to make sure that the AI never does the bad thing.
My worry with adversarial training is that it might just be pushing around the inner misalignment somewhere else in the model. In the real case there are instrumental incentives for power seeking to push against this technique, so even if the failure rate is 1 in a trillion, there will be strong optimization pressure, and a large distribution shift that will break this learned invariant.
Redwood is also doing some work on interpretability tools, though as far as I know they have not published a writeup of their interpretability results. As of April, they were focused on getting a complete understanding of nontrivial behaviors of relatively small models. They have released a website for visualizing transformers. Apart from the standard benefits of interpretability, one possibility is that this might be helpful for solving ELK.
Opinion: Excited to see the results from this.
Sam runs a lab at NYU. He is on sabbatical working at Anthropic for the 2022-2023 academic year, and has already been collaborating with them.
Projects include language model alignment by creating datasets for evaluating language models, as well as inductive biases of LLMs.
He is involved in running the inverse scaling prize in collaboration with FAR, a contest for finding tasks where larger language models perform worse than smaller language models. The idea of this is to understand how LLMs are misaligned, and find techniques for uncovering this misalignment.
Opinion: I don't understand this research very well, so I can't comment.
John's plan is:
Step 1: sort out our fundamental confusions about agencyStep 2: ambitious value learning (i.e. build an AI which correctly learns human values and optimizes for them)Step 3: …Step 4: profit!… and do all that before AGI kills us all.
Step 1: sort out our fundamental confusions about agency
Step 2: ambitious value learning (i.e. build an AI which correctly learns human values and optimizes for them)
Step 3: …
Step 4: profit!
… and do all that before AGI kills us all.
He is working on step 1: figuring out what the heck is going on with agency. His current approach is based on selection theorems: try to figure out what types of agents are selected for in a broad range of environments. Examples of selection pressures include: evolution, SGD, and markets. This is an approach to agent foundations that comes from the opposite direction as MIRI: it's more about observing existing structures (whether they be mathematical or real things in the world like markets or e coli), whereas MIRI is trying to write out some desiderata and then finding mathematical notions that satisfy those desiderata.
Two key properties that might be selected for are modularity and abstractions.
Abstractions are higher level things that people tend to use to describe things. Like "Tree" and "Chair" and "Person". These are all vague categories that contain lots of different things, but are really useful for narrowing down things. Humans tend to use really similar abstractions, even across different cultures / societies. The Natural Abstraction Hypothesis (NAH) states that a wide variety of cognitive architectures will tend to use similar abstractions to reason about the world. This might be helpful for alignment because we could say things like "person" without having to rigorously and precisely say exactly what we mean by person.
The NAH seems very plausibly true for physical objects in the world, and so it might be true for the inputs to human values. If so, it would be really helpful for AI alignment because understanding this would amount to a solution to the ontology identification problem: we can understand when environments induce certain abstractions, and so we can design this so that the network has the same abstractions as humans.
Opinion: I think that understanding abstraction seems like a promising research direction, both for current neural networks, as well as agent foundations problems.
I also think that the learned abstractions are highly dependent on the environment, and that the training environment for an AGI might look very different than the the learning environment that humans follow.
A very strong form of the Natural Abstraction Hypothesis might even hold for the goals of agents, for example, maybe cooperation is universally selected for by iterated prisoners dilemmas.
Modularity: In pretty much any selection environment, we see lots of obvious modularity. Biological species have cells and organs and limbs. Companies have departments. We might expect neural networks to be similar, but it is really hard to find modules in neural networks. We need to find the right lens to look through to find this modularity in neural networks. Aiming at this can lead us to really good interpretability.
Opinion: Looking for modules / frames on modularity in neural networks seems like a promising way to get scalable interpretability, so I'm excited about this.
Humans care about things! The reward circuitry in our brain reliably causes us to care about specific things. Let's create a mechanistic model of how the brain aligns humans, and then we can use this to do AI alignment.
One perspective that Shard theory has added is that we shouldn't think of the solution to alignment as:
Shard theory argues that instead we should focus on finding outer objectives that reliably give certain inner values into system and should be thought of as more of a teacher of the values we want to instill as opposed to the values themselves. Reward is not the optimization target — instead, it is more like that which reinforces. People sometimes refer to inner aligning an RL agent with respect to the reward signal, but this doesn't actually make sense. (As pointed out in the comments this is not a new insight, but it was for me phrased a lot more clearly in terms of Shard theory).
Humans have different values than the reward circuitry in our brain being maximized, but they are still pointed reliably. These underlying values cause us to not wirehead with respect to the outer optimizer of reward.
Shard Theory points at the beginning of a mechanistic story for how inner values are selected for by outer optimization pressures. The current plan is to figure out how RL induces inner values into learned agents, and then figure out how to instill human values into powerful AI models (probably chain of thought LLMs, because these are the most intelligent models right now). Then, use these partially aligned models to solve the full alignment problem. Shard theory also proposes a subagent theory of mind.
This has some similarities to Brain-like AGI Safety, and has drawn on some research from this post, such as the mechanics of the human reward circuitry as well as the brain being mostly randomly initialized at birth.
Opinion: This is promising so far, deserves a lot more work to be done on it to try to find a reliable way to implant certain inner values into trained systems. I view Shard Theory as a useful frame for alignment already even if it doesn’t go anywhere else.
Eli’s opinion: I’m not sure I agree much with the core claims of Shard Theory, but the research that I’ve seen actually being proposed based on it generally seems useful.
Truthful AI is a research direction to get models to avoid lying to us. This involves developing 1) clear truthfulness standards e.g. avoiding “negligent falsehoods”, 2) institutions to enforce standards, and 3) truthful AI systems e.g. via curated datasets and human interaction.
See also Truthful LMs as a warm-up for aligned AGI and TruthfulQA: Measuring How Models Mimic Human Falsehoods.
Edit for clarity: According to Owen, TruthfulAI is not trying to solve the hard bit of the alignment problem. Instead, the goal of this approach is to improve society to generally be more able to solve hard challenges such as alignment.
Opinion: It seems like the root problem is that deception is an instrumental subgoal of powerful inner misaligned AGIs, so we need to fix that in order to solve alignment. I'm confused about how this helps society solve alignment, but that is probably mostly because I don't know much about this.
Eli’s opinion: This seems like a pretty indirect way to tackle alignment of powerful AIs; I think it’s mostly promising insofar as it helps us more robustly automate technical and strategy alignment research.
Though we have tried to be exhaustive, there are certainly many people working on technical AI alignment not included in this overview. While these groups might produce great research, we either 1) didn't know enough about it to summarize or 2) weren’t aware that it was aimed at reducing x-risk from AI.
Below is a list of some of these, though we probably missed some here. Please feel free to add comments and I will add others.
Much of the difference between approaches comes down to disagreements on two axes: how promising it is to automate alignment vs. solve it directly and how difficult alignment is (~p(doom)). We’ll chart our impression of where orgs and approaches stand on these axes, based on something like the median view of org/approach leadership. We leave out orgs/approaches that we have no idea about, but err on the side of guessing if we have some intuitions (feel free to correct us!).
Another important axis distinguishing approaches is conceptual (i.e. thinking about how to align powerful AI) vs. applied (i.e. experimenting with AI systems to learn about how to align powerful AI).
This is a summary of my overall picture of the AGI landscape, which is a high level picture of the generator of most my opinions above.
I buy most of the arguments given in Without specific countermeasures, the easiest path to transformative AI likely leads to AI takeover and AGI Ruin, A List of Lethalities.
To make AGI go well, many organizations with economic and social incentives to make AGI before alignment is solved must avoid doing so. Moreover, the majority of the AI community does not take x-risk from AGI seriously. Whatever it is that moves us from our current trajectory to a safe-from-AGI-world, in my eyes, would count as a pivotal act — an act that makes a large positive impact on the world a billion years in the future. A pivotal act might also consist of lots of smaller actions that together make a difference in the long term, then all these acts together could constitute a pivotal act.
Performing a pivotal act without AI is likely really hard, but could look something like transforming the world's governments into Dath Ilan. If a non-AI pivotal act is feasible, I think it is probably best for us to cease all AIS research, and then just work towards performing that pivotal act. AIS research usually contributes at least something to capabilities, and so stopping that buys more time (so long as the AIS researchers don't start doing capabilities directly instead).
The other option is an AI-assisted pivotal act. This pivotal act might look like making a very aligned AI recursively self improve, and implement CEV. It might be more like the MIRI example of melting GPUs to prevent further AI progress and then turning itself off, but this isn't meant to be a concrete plan. MIRI seems to think that this is the path with the highest odds of success — see the strategic background section here.
The alignment tax is the amount of extra effort it will take for an AI to be aligned. This includes both research effort as well as compute and engineering time. I think it is quite likely (~80%) that part of the alignment tax for the first safe AGI requires >1 year of development time.
Pulling off an AGI-assisted pivotal act requires aligning the AGI you are using, meaning that:
Technical alignment work is primarily focused on 1. Some organizations are also trying to be large enough and ahead to pay the alignment tax for an AGI.
My model of EA and AI Safety is that it is expanding exponentially, and that this trend will likely continue until AGI. This leads me to think that the majority of the AIS work will be done right before AGI. It also means that timelines are crucial — pushing timelines back is very important. This is why I am usually not excited about work that improves capabilities even if it does more to help safety.
In the world where we have to align an AGI, solving the technical alignment problem seems like a big bottleneck, but cooperation to slow down timelines is necessary in both worlds.
We may revise the document based on corrections in the comments or future announcements, but don't promise anything. Others are welcome to create future versions or submit summaries of their own approaches for us to edit in. We will note the time it was last edited when we edit things. (ETA: most recent update: 10/9/2022)
In this chart, the ? denotes more uncertainty if this is a correct description
I would appreciate someone giving more information on DeepMind's approach to alignment. Update: Rohin has given a helpful summary in a comment.
Technically, they just need to span the set of extrapolations, so that the correct extrapolation is just a linear combination of the found classifiers.
Hold on, how come you are excited about Conjecture automating alignment research but not OpenAI? Answer: I see a categorical distinction between trying to align agentic and oracle AIs. Conjecture is trying only for oracle LLMs, trained without any RL pressure giving them goals, which seems way safer. OpenAI doing recursive reward modeling / IDA type schemes involves creating agentic AGIs and therefore faces also a lot more alignment issues like convergent instrumental goals, power seeking, goodharting, inner alignment failure, etc.
I think inner alignment can be a problem with LLMs trained purely in a self-supervised fashion (e.g., simulacra becoming aware of their surroundings), but I anticipate it to only be a problem with further capabilities. I think RL trained GPT-6 is a lot more likely to be an x-risk than GPT-6 trained only to do text prediction.
To be clear: I am very against proposals for violent pivotal acts that are sometimes brought up, such as destroying other AI labs on the verge of creating a misaligned AGI. This seems bad because 1) violence is bad and isn't dignified. 2) it seems like this intention would make it much harder to coordinate. 3) Setting an AGI loose to pull off a violent pivotal act could incredibly easily disempower humanity: you are intentionally letting the AGI destructively take over.
Some cruxes that would change this conclusion are if we don't get prosaic AGI or if solving alignment takes a lot of serial thought, e.g. work that needs to be done by 1 researcher over 10 years, and can't be solved by 10 researchers working for 1 year.
One insight this has generated so far is that Reward is not the optimization target — instead, it is more like that which reinforces. People sometimes refer to inner aligning an RL agent with respect to the reward signal, but this doesn't actually make sense.
Grumble grumble. Savvy people have known that reward is not the optimization target for at least five years, probably more like a decade. It's true that various people don't know this yet & so I'm glad that post was written, but it's a bit unfair to credit shard theory with having generated that idea. (I think TurnTrout would agree with this, his post says that alignment people seem to be aware of this point already)
I don't consider this a settled question; is there rigorous technical work establishing that "Reward is not the optimization target"?
Depends on your standards for "rigorous technical work" and "establishing." In some sense nothing on this topic is sufficiently rigorous, and in some sense nothing on this topic has been established yet. I think the Risks from Learned Optimization paper might be what you are looking for. There's also evhub's recent talk. And of course, TurnTrouts post that was linked above. And again I just pull these out of the top of my head, the ideas in them have been floating around for a while.
I'd be interested to hear an argument that reward is the optimization target, if you've got one!
I suspect that this is an issue that will be cleared up by everyone being super careful and explicit and nitpicky about their definitions. (Because I think a big part of what's going on here is that people aren't doing that and so they are getting subtly confused and equivocating between importantly different statements, and then on top of that other people are misunderstanding their words)
Thanks! I don't think those meet my criteria. I also suspect "everyone being super careful and explicit and nitpicky about their definitions" is lacking, and I'd consider that a basic and essential component of rigorous technical work.
Got an argument that reward is the optimization target?
I don't think this framing of it being the optimization target or not is very helpful. It's like asking "does SGD converge?" or "will my supervised learning model learn the true hypothesis?" The answer will depend on a number of factors, and it's often not best thought of as a binary thing.e.g. for agents that do planning based on optimizing a reward function, it seems appropriate to say that reward is the optimization target.Here's another argument: maybe it's the field of RL, and not Alex Turner, who is right about this: https://www.lesswrong.com/posts/pdaGN6pQyQarFHXF4/reward-is-not-the-optimization-target#Appendix__The_field_of_RL_thinks_reward_optimization_target(I'm not sure Alex characterizes the field's beliefs correctly, and I'm sort of playing devil's advocate with that one (not a big fan of "outside views"), but it's a bit odd to act like the burden of proof is on someone who agrees with the relevant academic field).
e.g. for agents that do planning based on optimizing a reward function, it seems appropriate to say that reward is the optimization target.
Often, when an RL agent imagines a possible future roll-out, it does not evaluate whether that possible future is good or bad by querying an external ground-truth reward function; instead, it queries a learned value function. When that’s the case, the thing that the agent is foresightedly “trying” / “planning” to do is to optimize the learned value function, not the reward function. Right?
For example, I believe AlphaZero can be described this way—it explores some number of possible future scenarios (I’m hazy on the details), and evaluates how good they are based on querying the learned value function, not querying the external ground-truth reward function, except in rare cases where the game is just about to end.
I claim that, if we make AGI via model-based RL (as I expect), it will almost definitely be like that too. If an AGI has a (nonverbal) idea along the lines of “What if I try to invent a new microscope using (still-somewhat-vague but innovative concept)”, I can’t imagine how on earth you would build an external ground-truth reward function that can be queried with that kind of abstract hypothetical. But I find it very easy to imagine how a learned value function could be queried with that kind of abstract hypothetical.
(You can say “OK fine but the learned value function will asymptotically approach the external ground-truth reward function”. However, that might or might not be true. It depends on the algorithm and environment. I expect AGIs to be in a nonstationary environment with vastly too large an action space to fully explore, and full of irreversible actions that make full exploration impossible anyway. In that case, we cannot assume that there’s no important difference between “trying” to maximize the learned value function versus “trying” to maximize the reward function.)
Sorry if I’m misunderstanding. (My own discussion of this topic, in the context of a specific model-based RL architecture, is Section 9.5 here.)
Thanks!I'm not sure the framing is helpful either, but reading Turner's linked appendix it does seem like various people are making some sort of mistake that can be summarized as "they seem to think the policy / trained network should be understood as trying to get reward, as preferring higher-reward outcomes, as targeting reward..." (And Turner says he himself was one of them despite doing a PhD in RL theory) Like I said above I think that probably there's room for improvement here -- if everyone defined their terms better this problem would clear up and go away. I see Turner's post as movement in this direction but by no means the end of the journey.Re your first argument: If I understand you correctly, you are saying that if your AI design involves something like monte-carlo tree search using a reward-estimator module (Idk what the technical term for that is) and the reward-estimator module is just trained to predict reward, then it's fair to describe the system as optimizing for the goal of reward. Yep that seems right to me, modulo concerns about inner alignment failures in the reward-estimator module. I don't see this as contradicting Alex Turner's claims but maybe it does.Re your second argument, the appeal to authority: I suppose in a vacuum, not having thought about it myself or heard any halfway decent arguments, I'd defer to the RL field on this matter. But I have thought about it a bit myself and I have heard some decent arguments, and that effect is stronger than the deference effect for me, and I think this is justified.
RE appeal to authority: I mostly mentioned it because you asked for an argument and I figured I would just provide any decent ones I thought of OTMH. But I have not provided anything close to my full thoughts on the matter, and probably won't, due to bandwidth.
The main thing missing here are academic groups (like mine at Cambridge https://www.davidscottkrueger.com/). This is a pretty glaring oversight, although I'm not that surprised since it's LW. Some other noteworthy groups in academia lead by people who are somewhat connected to this community:- Jacob Steinhardt (Berkeley)- Dylan Hadfield-Menell (MIT)- Sam Bowman (NYU)- Roger Grosse (UofT)
More at https://futureoflife.org/team/ai-existential-safety-community/ (although I think the level of focus on x-safety and engagement with this community varies substantially among these people).BTW, FLI is itself worth a mention, as is FHI, maybe in particular https://www.fhi.ox.ac.uk/causal-incentives-working-group/ if you want to focus on technical stuff.Some other noteworthy groups in academia lead by people who are perhaps less connected to this community:- Aleksander Madry (MIT)- Percy Liang (Stanford)- Scott Neikum (UMass Amhearst)These are just examples.
Some other noteworthy groups in academia lead by people who are somewhat connected to this community:- Jacob Steinhardt (Berkeley)- Dylan Hadfield-Menell (MIT)- Sam Bowman (NYU)- Roger Grosse (UofT)Some other noteworthy groups in academia lead by people who are perhaps less connected to this community:- Aleksander Madry (MIT)- Percy Liang (Stanford)- Scott Neikum (UMass Amhearst)
Some other noteworthy groups in academia lead by people who are somewhat connected to this community:- Jacob Steinhardt (Berkeley)- Dylan Hadfield-Menell (MIT)- Sam Bowman (NYU)- Roger Grosse (UofT)
Some other noteworthy groups in academia lead by people who are perhaps less connected to this community:- Aleksander Madry (MIT)- Percy Liang (Stanford)- Scott Neikum (UMass Amhearst)
Can you provide some links to these groups?
These professors all have a lot of published papers in academic conferences. It’s probably a bit frustrating to not have their work summarized, and then be asked to explain their own work, when all of their work is published already. I would start by looking at their Google Scholar pages, followed by personal websites and maybe Twitter. One caveat would be that papers probably don’t have full explanations of the x-risk motivation or applications of the work, but that’s reading between the lines that AI safety people should be able to do themselves.
Agree with both aogara and Eli's comment.
One caveat would be that papers probably don’t have full explanations of the x-risk motivation or applications of the work, but that’s reading between the lines that AI safety people should be able to do themselves.
For me this reading between the lines is hard: I spent ~2 hours reading academic papers/websites yesterday and while I could quite quickly summarize the work itself, it was quite hard to me to figure out the motivations.
There's a lot of work that could be relevant for x-risk but is not motivated by it. Some of it is more relevant than work that is motivated by it. An important challenge for this community (to facilitate scaling of research funding, etc.) is to move away from evaluating work based on motivations, and towards evaluating work based on technical content.
PAIS #5 might be helpful here. It explains how a variety of empirical directions are related to X-Risk and probably includes many of the ones that academics are working on.
I don't think the onus should be on the reader to infer x-risk motivations. In academic ML, it's the author's job to explain why the reader should care about the paper. I don't see why this should be different in safety. If it's hard to do that in the paper itself, you can always e.g. write a blog post explaining safety relevance (as mentioned by aogara, people are already doing this, which is great!).There are often many different ways in which a paper might be intended to be useful for x-risks (and ways in which it might not be). Often the motivation for a paper (even in the groups mentioned above) may be some combination of it being an interesting ML problem, interests of the particular student, and various possible thoughts around AI safety. It's hard to try to disentangle this from the outside by reading between the lines.
Note: I link to a bunch of stuff below in the context of the DeepMind safety team, this should be thought of as "things that particular people do" and may not represent the views of DeepMind or even just the DeepMind safety team.
I just don't know much about what the [DeepMind] technical alignment work actually looks like right now
We do a lot of stuff, e.g. of the things you've listed, the Alignment / Scalable Alignment Teams have done at least some work on the following since I joined in late 2020:
And in addition we've also done other stuff like
I'm probably forgetting a few others.
I think you can talk about the agendas of specific people on the DeepMind safety teams but there isn't really one "unified agenda".
Thanks you for this thoughtful response, I didn't know about most of these projects. I've linked this comment in the DeepMind section, as well as done some modifications for both clarity and including a bit more.
This is useful to know.
Thanks Thomas for the helpful overview post! Great to hear that you found the AGI ruin opinions survey useful.
I agree with Rohin's summary of what we're working on. I would add "understanding / distilling threat models" to the list, e.g. "refining the sharp left turn" and "will capabilities generalize more".
Some corrections for your overall description of the DM alignment team:
Anthropic is also working on inner alignment, it's just not published yet.
Regarding what "the point" of RL from human preferences with language models is; I think it's not only to make progress on outer alignment (I would agree that this is probably not the core issue; although I still think that it's a relevant alignment issue).
See e.g. Ajeya's comment here:
According to my understanding, there are three broad reasons that safety-focused people worked on human feedback in the past (despite many of them, certainly including Paul, agreeing with this post that pure human feedback is likely to lead to takeover):Human feedback is better than even-worse alternatives such as training the AI on a collection of fully automated rewards (predicting the next token, winning games, proving theorems, etc) and waiting for it to get smart enough to generalize well enough to be helpful / follow instructions. So it seemed good to move the culture at AI labs away from automated and easy rewards and toward human feedback.You need to have human feedback working pretty well to start testing many other strategies for alignment like debate and recursive reward modeling and training-for-interpretability, which tend to build on a foundation of human feedback.Human feedback provides a more realistic baseline to compare other strategies to -- you want to be able to tell clearly if your alignment scheme actually works better than human feedback.With that said, my guess is that on the current margin people focused on safety shouldn't be spending too much more time refining pure human feedback (and ML alignment practitioners I've talked to largely agree, e.g. the OpenAI safety team recently released this critiques work -- one step in the direction of debate).
According to my understanding, there are three broad reasons that safety-focused people worked on human feedback in the past (despite many of them, certainly including Paul, agreeing with this post that pure human feedback is likely to lead to takeover):
With that said, my guess is that on the current margin people focused on safety shouldn't be spending too much more time refining pure human feedback (and ML alignment practitioners I've talked to largely agree, e.g. the OpenAI safety team recently released this critiques work -- one step in the direction of debate).