In 2022, Richard Ngo wrote a list of 26 Conceptual Alignment Research Projects. Now that it’s 2026, I’d like to revisit this list of projects, note which ones have already been done, and give my thoughts on which ones might still be worth doing.
A paper which does for deceptive alignment what the goal misgeneralization paper does for inner alignment, i.e. describing it in ML language and setting up toy examples (for example, telling GPT-3 to take actions which minimize changes in its weights, given that it’s being trained using actor-critic RL with a certain advantage function, and seeing if it knows how to do so).
The 2024 Sleeper Agents paper has introduced this terminology to the literature, and in fact showed that backdoored models can persist through training, using more capable models and interesting environments than GPT-3. Alignment Faking in Large Language Models shows that deceptive alignment can emerge naturally in Claude 3 Opus, without explicit training or instruction. I'd count this as having been done.
A paper which does the same for gradient hacking, e.g. taking these examples and putting them into more formal ML language.
I'm not aware of any work in this area. Exploration hacking is a related problem that has received substantially more study (normally, as "sandbagging"). Note that model organisms of misalignment work (e.g. Alignment Faking in Large Language Models) does feature model organisms that try to manipulate the training process, but they do it through means that are substantially less advanced than the mechanisms proposed in gradient
A list of papers that are particularly useful for new research engineers to replicate.
This is the role played by intro curricula such as ARENA. My guess is that, while it doesn't exactly match up to reproducing papers, it's close enough that it should count. Otherwise, there are slightly older lists, such as Neel Nanda's mech interp quickstart. I think this counts as having been done. Part of the problem is that alignment now has way more content, so a single list is probably unlikely to be able to even briefly cover most of it.
A takeover scenario which covers all the key points in https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/, but not phrased as an argument, just phrased as a possible scenario (I think you can’t really make the argument rigorously in that little space).
A paper which defines the concepts of implicit planning, implicit value functions, implicit reward models, etc, in ML terms. Kinda like https://arxiv.org/abs/1901.03559 but more AGI-focused. I want to be able to ask people “does GPT-3 choose actions using an implicit value function?” and then be able to point them to this paper to rigorously define what I mean. I discuss this briefly in the phase 1 section here.
There are scattered pieces of this that exist in various papers, but not really one canonical references. Example includes the Othello-GPT and LeelaZero interprability work, some of Anthropic's work studying planning circuits in Claude 3.5 Haiku, and some mechanistic interpretability work on small RNNs. I think this is substantially less of a important novel contribution now that we have AI agents running around, but it's plausibly still worth doing. I also think this concept may be confused, and that the contribution may be to reduce confusion in this area.
A blog post which describes in as much detail as possible what our current “throw the kitchen sink at it” alignment strategy would look like. (I’ll probably put my version of this online soon but would love others too).
Many such plans exist, albeit probably too few, and none with much detail. For example, Redwood's AI Control agenda is basically trying to make this strategy work out. Part of it is that as we got sufficiently capable AIs, the System Cards for AI models (e.g. see the recent Mythos reports) started to resemble more and more what the kitchen sink strategy would look like. There's been some work on safety cases that's related as well. My guess is it's still valuable to write what a comprehensive version would look like nonetheless.
I don't think this exists as is, and given rabbithole the mechanistic interpretability has gotten itself into, it seems implausible that we're going to actually get any rigorous debates on weights. Note that there's some work on using debate as an outer alignment technique (see also Khan et al.). Plausible still worth doing just as historical documentation or as something to use AI labor on after AI research automation.
A blog post exploring how fast we should expect a forward pass to be for the first AGIs - e.g. will it actually be slower than human thinking, as discussed in this comment.
Several posts touch upon this implicitly or in passing (e.g. this comes up in AI 2027), but as far as I know no such explicit post exists. I think we have enough knowledge that we can try to answer this question more empirically, though this requires solving some tricky conceptual questions such as how to convert between units of AI thought (tokens? flops?) to units of human thought, and how to distinguish memorized heuristics from more "pure" thought.
I'm not aware of any systematic treatments of this issue, especially in the context of goals vs beliefs (as opposed to goals vs capabilities). I think there's been a fair amount of intuition and writing on this topic on Twitter from Janus and crew, and the Persona Selection Model (and other writeups providing conceptual models of LLMs) definitely seem relevant, but as is there hasn't been a post that makes a clean divide between model beliefs and model goals (insofar as one exists). I think you can make a strong piece in this area using current empirical results on LLMs.
A blog post explaining why the “uncertainty” part of CIRL only does useful work insofar as we have an accurate model of the human policy, and why this is basically just as hard as having an accurate model of human preferences.
His result says that, in general, you cannot infer preferences from only observations of a policy without further assumptions (in fact, you cannot infer preferences in general even given the full policy). Much more relevant when we were thinking in terms of inverse reinforcement learning, though nowadays we no longer frame human preference alignment using IRL anymore. It's probably worth a quick writeup anyways, though I don't think it's super relevant anymore, I might do this later in Inkhaven.
As many alignment exercises as possible to help people learn to think about this stuff (mine aren't great but I haven’t seen better).
Richard's exercises eventually became AGISF, and we also have seen other intro curricula like ARENA (albeit substantially less focused on alignment in general). I think we can count this as done.
A paper properly formulating instrumental convergence, generalization to large-scale goals, etc, as inductive biases in the ML sense (I do this briefly in phase 3 here).
I don't think this exists. Arguably, this is the highest value open project on this list, because the generalization properties of LLMs is very important for figuring out how to interpret the alignment evaluation results we're seeing.
A mathematical comparison between off-policy RL and imitation learning, exploring ways in which they’re similar and different, and possible algorithms in between.
This topic confuses me, because a rich academic literature of this already existed in the robotics/RL space in 2022. I'm aware of many results bridging the two, e.g. SQIL or SAC. I'm not sure why this was relevant to alignment in 2022, and insofar as this post doesn't exist in the alignment space, I don't see the value in writing it now.
A blog post explaining the core argument for why detecting adversarially-generated inputs is likely much easier than generating them, and arguments for why adversarial training might nevertheless be valuable for alignment.
In general, adversarial examples are much less prominent an issue in 2026 than they were in 2022. Part of this is that models have just gotten more capable, and more capable models are more resistant to jailbreaks (in part because they can recognize them). Part of this is the move away from image adversarial examples (which is offense dominated) to LLMs/text-based jailbreaks (where the defense is more favored). We also don't really do traditional adversarial training anymore, insofar as this exists it falls under refusal training. I don't think this post exists, but I also don't think it's worth writing today.
A blog post exploring the incentives which models might have when they’re simultaneously trained to make predictions and to take actions in an RL setting (e.g. models trained using RL via sequence modeling).
This was already explored in a 2020 paper by Stuart Armstrong et al. I think it's plausible that it's still worth thinking about in the current context, but mainly from a unintended generalization standpoint for capable LLM agents.
A blog post exploring pros and cons of making misalignment datasets for use as a metric of alignment (alignment = how much training on the misalignment dataset is needed to make it misaligned).
Owain Evan's work on empirical misalignment is probably closest, though I don't think he uses the amount of training as a measurement of alignment. Arguably, the model organisms of misalignment agenda from Evan Hubinger qualifies, but again I don't think they use the amount of optimization pressure to remove alignment as a metric of alignment per se. (In fact, in the Sleeper Agents or Alignment Faking paper, higher optimization pressure required to remove alignment is considered a bad thing). I do think there are some clever ideas to be done quantifying the amount of optimization power required to change a model to becoming mecha hitler, but I wonder how much of this is again tying into deep problems of generalization that are hard to tackle.
A paper providing an RL formalism in which reward functions can depend on weights and/or activations directly, and demonstrating a simple but non-trivial example.
As far as I know this does not exist as Richard envisioned it even today. There's progress toward it in terms of process feedback on CoT and (arguably) white-box techniques like activation steering and activation oracles. Michael Dennis's work features some exploration of rewards that can depend on the entire policy, but not the weights in particular. Maybe the Latent Adversarial Training work also counts? That being said, I don't think this is particularly worth doing, and I struggle to see the relevance to alignment today.
A blog post evaluating reasons to think that situational awareness will be a gradual development in models, versus a sharp transition.
We have models that are substantially situationally aware today. In the past (e.g. in 2022) the models did not seem so situationally aware. We also have datasets that try to quantify situational awareness (sometimes under the guise of "quantifying hallucinations"). I don't think the post as envisioned by Richard exists. Probably, it's worth revisiting this from a historical lens using the empirical evidence we have today; though it's no longer as important given the models today are substantially situationally aware.
A blog post explaining reasons to expect capabilities to be correlated with alignment while models lack situational awareness, and then less correlated afterwards, rather than the correlation continuing.
Given this blog post topic, I now suspect that Richard imagines a substantially deeper level of situational awareness than we see in present models. This post seems worth doing nonetheless, given the models are situationally aware and there's an open question as to how to interpret the alignment results.
A blog post estimating how many bits of optimization towards real-world goals could arise from various aspects of a supervised training program (especially ones which slightly break the cartesian formalisms) - e.g. hyperparameter tuning, many random seeds, training on data generated by other AIs, etc.
Doesn't exist as far as I know. Probably irrelevant/only of academic interest now, given we directly optimize models to be agents (i.e. act in real-world settings).
A sketch of what a model-free version of AIXI would look like (according to one person I talked to, it’s a lot like decision transformers).
I think there's been a small amount of discussion on LessWrong linking decision transformers to AIXI, but as far as I know the model-free version has not been formalized. (I also confess I don't know how to construct the model-free version of AIXI!) As with previous topic, I suspect this isn't worth doing except as academic interest.
A blog post evaluating whether shard theory makes sense/makes novel predictions compared with Steve Byrnes’ model of the brain (he partly explains this in a comment on the post, but I’m still a bit confused).
Later in 2022, I wrote a post explaining and critiquing Shard Theory, and contrast it to alternative models, including Steve Byrnes. Alex Turner and Steve Byrnes have both written more about their respective models as well. This counts as being done, in my opinion.
A blog post or paper reviewing what types of feedback humans perform best and worst at (e.g. reward vs value feedback) and then designing a realistic setup for optimal-quality human feedback.
There's been some work on this in academia, but arguably the key problem was never the modality of human feedback, but problems like ELK or partial observability. It's probably pretty easy to just synthesize the academic literature to answer the first half, the second half seems both very challenging and probably not worth.
A blog post compiling examples of surprising emergent capabilities (especially in large language models).
Basically every new model generation's release blog post has a bunch of examples. We've also seen lists of this compiled by e.g. Sage research. People are less surprised and more boil-frogged at this point.
An investigation of the extent to which human concept representations are localized to individual neurons, versus being spread out across different neurons.
There's been a lot of mechanistic interpretability work (and other theory work) concluding pretty conclusively that most concept representations are distributed across many neurons (and arguably across many layers as well). Done, though maybe it's worth writing a brief synopsis for posterity.
My main takeaway from reading this list is that, Richard's list in 2022 seemed pretty reasonable. While some of the projects were arguably already completed when he wrote the list in 2022, most of them seem to be to be relevant at the time, and a slight majority seem pretty relevant even today. As you might expect given the direction of the field, of said 26 topics, most of the empirical projects have been done, while the conceptual ones are still mostly open or unresolved.
Written very quickly for the InkHaven Residency.
In 2022, Richard Ngo wrote a list of 26 Conceptual Alignment Research Projects. Now that it’s 2026, I’d like to revisit this list of projects, note which ones have already been done, and give my thoughts on which ones might still be worth doing.
The 2024 Sleeper Agents paper has introduced this terminology to the literature, and in fact showed that backdoored models can persist through training, using more capable models and interesting environments than GPT-3. Alignment Faking in Large Language Models shows that deceptive alignment can emerge naturally in Claude 3 Opus, without explicit training or instruction. I'd count this as having been done.
I'm not aware of any work in this area. Exploration hacking is a related problem that has received substantially more study (normally, as "sandbagging"). Note that model organisms of misalignment work (e.g. Alignment Faking in Large Language Models) does feature model organisms that try to manipulate the training process, but they do it through means that are substantially less advanced than the mechanisms proposed in gradient
This is the role played by intro curricula such as ARENA. My guess is that, while it doesn't exactly match up to reproducing papers, it's close enough that it should count. Otherwise, there are slightly older lists, such as Neel Nanda's mech interp quickstart. I think this counts as having been done. Part of the problem is that alignment now has way more content, so a single list is probably unlikely to be able to even briefly cover most of it.
AI 2027 exists! We've also seen many other smaller writeups like this, like Josh Clymer's AI Takeover in 2 Years blog post. This definitely counts as having been done.
There are scattered pieces of this that exist in various papers, but not really one canonical references. Example includes the Othello-GPT and LeelaZero interprability work, some of Anthropic's work studying planning circuits in Claude 3.5 Haiku, and some mechanistic interpretability work on small RNNs. I think this is substantially less of a important novel contribution now that we have AI agents running around, but it's plausibly still worth doing. I also think this concept may be confused, and that the contribution may be to reduce confusion in this area.
Many such plans exist, albeit probably too few, and none with much detail. For example, Redwood's AI Control agenda is basically trying to make this strategy work out. Part of it is that as we got sufficiently capable AIs, the System Cards for AI models (e.g. see the recent Mythos reports) started to resemble more and more what the kitchen sink strategy would look like. There's been some work on safety cases that's related as well. My guess is it's still valuable to write what a comprehensive version would look like nonetheless.
I don't think this exists as is, and given rabbithole the mechanistic interpretability has gotten itself into, it seems implausible that we're going to actually get any rigorous debates on weights. Note that there's some work on using debate as an outer alignment technique (see also Khan et al.). Plausible still worth doing just as historical documentation or as something to use AI labor on after AI research automation.
Several posts touch upon this implicitly or in passing (e.g. this comes up in AI 2027), but as far as I know no such explicit post exists. I think we have enough knowledge that we can try to answer this question more empirically, though this requires solving some tricky conceptual questions such as how to convert between units of AI thought (tokens? flops?) to units of human thought, and how to distinguish memorized heuristics from more "pure" thought.
I'm not aware of any systematic treatments of this issue, especially in the context of goals vs beliefs (as opposed to goals vs capabilities). I think there's been a fair amount of intuition and writing on this topic on Twitter from Janus and crew, and the Persona Selection Model (and other writeups providing conceptual models of LLMs) definitely seem relevant, but as is there hasn't been a post that makes a clean divide between model beliefs and model goals (insofar as one exists). I think you can make a strong piece in this area using current empirical results on LLMs.
This was covered in Rachel Freedman and Adam Gleave's 2022 blog post, "CIRL Corrigibility is Fragile". Done.
His result says that, in general, you cannot infer preferences from only observations of a policy without further assumptions (in fact, you cannot infer preferences in general even given the full policy). Much more relevant when we were thinking in terms of inverse reinforcement learning, though nowadays we no longer frame human preference alignment using IRL anymore. It's probably worth a quick writeup anyways, though I don't think it's super relevant anymore, I might do this later in Inkhaven.
Richard's exercises eventually became AGISF, and we also have seen other intro curricula like ARENA (albeit substantially less focused on alignment in general). I think we can count this as done.
I don't think this exists. Arguably, this is the highest value open project on this list, because the generalization properties of LLMs is very important for figuring out how to interpret the alignment evaluation results we're seeing.
This topic confuses me, because a rich academic literature of this already existed in the robotics/RL space in 2022. I'm aware of many results bridging the two, e.g. SQIL or SAC. I'm not sure why this was relevant to alignment in 2022, and insofar as this post doesn't exist in the alignment space, I don't see the value in writing it now.
In general, adversarial examples are much less prominent an issue in 2026 than they were in 2022. Part of this is that models have just gotten more capable, and more capable models are more resistant to jailbreaks (in part because they can recognize them). Part of this is the move away from image adversarial examples (which is offense dominated) to LLMs/text-based jailbreaks (where the defense is more favored). We also don't really do traditional adversarial training anymore, insofar as this exists it falls under refusal training. I don't think this post exists, but I also don't think it's worth writing today.
This was already explored in a 2020 paper by Stuart Armstrong et al. I think it's plausible that it's still worth thinking about in the current context, but mainly from a unintended generalization standpoint for capable LLM agents.
Owain Evan's work on empirical misalignment is probably closest, though I don't think he uses the amount of training as a measurement of alignment. Arguably, the model organisms of misalignment agenda from Evan Hubinger qualifies, but again I don't think they use the amount of optimization pressure to remove alignment as a metric of alignment per se. (In fact, in the Sleeper Agents or Alignment Faking paper, higher optimization pressure required to remove alignment is considered a bad thing). I do think there are some clever ideas to be done quantifying the amount of optimization power required to change a model to becoming mecha hitler, but I wonder how much of this is again tying into deep problems of generalization that are hard to tackle.
As far as I know this does not exist as Richard envisioned it even today. There's progress toward it in terms of process feedback on CoT and (arguably) white-box techniques like activation steering and activation oracles. Michael Dennis's work features some exploration of rewards that can depend on the entire policy, but not the weights in particular. Maybe the Latent Adversarial Training work also counts? That being said, I don't think this is particularly worth doing, and I struggle to see the relevance to alignment today.
We have models that are substantially situationally aware today. In the past (e.g. in 2022) the models did not seem so situationally aware. We also have datasets that try to quantify situational awareness (sometimes under the guise of "quantifying hallucinations"). I don't think the post as envisioned by Richard exists. Probably, it's worth revisiting this from a historical lens using the empirical evidence we have today; though it's no longer as important given the models today are substantially situationally aware.
Given this blog post topic, I now suspect that Richard imagines a substantially deeper level of situational awareness than we see in present models. This post seems worth doing nonetheless, given the models are situationally aware and there's an open question as to how to interpret the alignment results.
Doesn't exist as far as I know. Probably irrelevant/only of academic interest now, given we directly optimize models to be agents (i.e. act in real-world settings).
I think there's been a small amount of discussion on LessWrong linking decision transformers to AIXI, but as far as I know the model-free version has not been formalized. (I also confess I don't know how to construct the model-free version of AIXI!) As with previous topic, I suspect this isn't worth doing except as academic interest.
Later in 2022, I wrote a post explaining and critiquing Shard Theory, and contrast it to alternative models, including Steve Byrnes. Alex Turner and Steve Byrnes have both written more about their respective models as well. This counts as being done, in my opinion.
There's been some work on this in academia, but arguably the key problem was never the modality of human feedback, but problems like ELK or partial observability. It's probably pretty easy to just synthesize the academic literature to answer the first half, the second half seems both very challenging and probably not worth.
Basically every new model generation's release blog post has a bunch of examples. We've also seen lists of this compiled by e.g. Sage research. People are less surprised and more boil-frogged at this point.
There's been a lot of mechanistic interpretability work (and other theory work) concluding pretty conclusively that most concept representations are distributed across many neurons (and arguably across many layers as well). Done, though maybe it's worth writing a brief synopsis for posterity.
My main takeaway from reading this list is that, Richard's list in 2022 seemed pretty reasonable. While some of the projects were arguably already completed when he wrote the list in 2022, most of them seem to be to be relevant at the time, and a slight majority seem pretty relevant even today. As you might expect given the direction of the field, of said 26 topics, most of the empirical projects have been done, while the conceptual ones are still mostly open or unresolved.