Crossposted from the AI Alignment Forum. May contain more technical jargon than usual.

Alignment Newsletter is a weekly publication with recent content relevant to AI alignment around the world. Find all Alignment Newsletter resources here. In particular, you can look through this spreadsheet of all summaries that have ever been in the newsletter.

Audio version here (may not be up yet).

Please note that, while I work at DeepMind, this newsletter represents my personal views and not those of my employer.


Unsolved Problems in ML Safety (Dan Hendrycks, Nicholas Carlini, John Schulman, and Jacob Steinhardt) (summarized by Dan Hendrycks): To make the case for safety to the broader machine learning research community, this paper provides a revised and expanded collection of concrete technical safety research problems, namely:

1. Robustness: Create models that are resilient to adversaries, unusual situations, and Black Swan events.

2. Monitoring: Detect malicious use, monitor predictions, and discover unexpected model functionality.

3. Alignment: Build models that represent and safely optimize hard-to-specify human values.

4. External Safety: Use ML to address risks to how ML systems are handled, including cyberwarfare and global turbulence.

Throughout, the paper attempts to clarify the problems’ motivation and provide concrete project ideas.

Dan Hendrycks' opinion: My coauthors and I wrote this paper with the ML research community as our target audience. Here are some thoughts on this topic:

1. The document includes numerous problems that, if left unsolved, would imply that ML systems are unsafe. We need the effort of thousands of researchers to address all of them. This means that the main safety discussions cannot stay within the confines of the relatively small EA community. I think we should aim to have over one third of the ML research community work on safety problems. We need the broader community to treat AI safety at least as seriously as safety for nuclear power plants.

2. To grow the ML safety research community, we need to suggest problems that can progressively build the community and organically grow support for elevating safety standards within the existing research ecosystem. Research agendas that pertain to AGI exclusively will not scale sufficiently, and such research will simply not get enough market share in time. If we do not get the machine learning community on board with proactively mitigating risks that already exist, we will have a harder time getting them to mitigate less familiar and unprecedented risks. Rather than try to win over the community with alignment philosophy arguments, I'll try winning them over with interesting problems and try to make work towards safer systems rewarded with prestige.

3. The benefits of a larger ML safety community are numerous. They can decrease the cost of safety methods and increase the propensity to adopt them. Moreover, to ensure that ML systems have desirable properties, it is necessary to rapidly accumulate incremental improvements, but this requires substantial growth since such gains cannot be produced by just a few card-carrying x-risk researchers with the purest intentions.

4. The community will fail to grow if we ignore near-term concerns or actively exclude or sneer at people who work on problems that are useful for both near- and long-term safety (such as adversaries). The alignment community will need to stop engaging in textbook territorialism and welcome serious hypercompetent researchers who do not post on internet forums or who happen not to subscribe to effective altruism. (We include a community strategy in the Appendix.)

5. We focus on reinforcement learning but also deep learning. Most of the machine learning research community studies deep learning (e.g., text processing, vision) and does not use, say, Bellman equations or PPO. While existentially catastrophic failures will likely require competent sequential decision-making agents, the relevant problems and solutions can often be better studied outside of gridworlds and MuJoCo. There is much useful safety research to be done that does not need to be cast as a reinforcement learning problem.

6. To prevent alienating readers, we did not use phrases such as "AGI." AGI-exclusive research will not scale; for most academics and many industry researchers, it's a nonstarter. Likewise, to prevent needless dismissiveness, we kept x-risks implicit, only hinted at them, or used the phrase "permanent catastrophe."

I would have personally enjoyed discussing at length how anomaly detection is an indispensable tool for reducing x-risks from Black Balls, engineered microorganisms, and deceptive ML systems.

Here are how the problems relate to x-risk:

Adversarial Robustness: This is needed for proxy gaming. ML systems encoding proxies must become more robust to optimizers, which is to say they must become more adversarially robust. We make this connection explicit at the bottom of page 9.

Black Swans and Tail Risks: It's hard to be safe without high reliability. It's not obvious we'll achieve high reliability even by the time we have systems that are superhuman in important respects. Even though MNIST is solved for typical inputs, we still do not even have an MNIST classifier for atypical inputs that is reliable! Moreover, if optimizing agents become unreliable in the face of novel or extreme events, they could start heavily optimizing the wrong thing. Models accidentally going off the rails poses an x-risk if they are sufficiently powerful (this is related to "competent errors" and "treacherous turns"). If this problem is not solved, optimizers can use these weaknesses; this is a simpler problem on the way to adversarial robustness.

Anomaly and Malicious Use Detection: This is an indispensable tool for detecting proxy gaming, Black Balls, engineered microorganisms that present bio x-risks, malicious users who may misalign a model, deceptive ML systems, and rogue ML systems.

Representative Outputs: Making models honest is a way to avoid many treacherous turns.

Hidden Model Functionality: This also helps avoid treacherous turns. Backdoors is a potentially useful related problem, as it is about detecting latent but potential sharp changes in behavior.

Value Learning: Understanding utilities is difficult even for humans. Powerful optimizers will need to achieve a certain, as-of-yet unclear level of superhuman performance at learning our values.

Translating Values to Action: Successfully prodding models to optimize our values is necessary for safe outcomes.

Proxy Gaming: Obvious.

Value Clarification: This is the philosophy bot section. We will need to decide what values to pursue. If we decide poorly, we may lock in or destroy what is of value. It is also possible that there is an ongoing moral catastrophe, which we would not want to replicate across the cosmos.

Unintended Consequences: This should help models not accidentally work against our values.

ML for Cybersecurity: If you believe that AI governance is valuable and that global turbulence risks can increase risks of terrible outcomes, this section is also relevant. Even if some of the components of ML systems are safe, they can become unsafe when traditional software vulnerabilities enable others to control their behavior. Moreover, traditional software vulnerabilities may lead to the proliferation of powerful advanced models, and this may be worse than proliferating nuclear weapons.

Informed Decision Making: We want to avoid decision making based on unreliable gut reactions during a time of crisis. This reduces risks of poor governance of advanced systems.

Here are some other notes:

1. We use systems theory to motivate inner optimization as we expect this motivation will be more convincing to others.

2. Rather than having a broad call for "interpretability," we focus on specific transparency-related problems that are more tractable and neglected. (See the Appendix for a table assessing importance, tractability, and neglectedness.) For example, we include sections on making models honest and detecting emergent functionality.

3. The "External Safety" section can also be thought of as technical research for reducing "Governance" risks. For readers mostly concerned about AI risks from global turbulence, there still is technical research that can be done.

Here are some observations while writing the document:

1. Some approaches that were previously very popular are currently neglected, such as inverse reinforcement learning. This may be due to currently low tractability.

2. Five years ago, I started explicitly brainstorming the content for this document. I think it took the whole time for this document to take shape. Moreover, if this were written last fall, the document would be far more confused, since it took around a year after GPT-3 to become reoriented; writing these types of documents shortly after a paradigm shift may be too hasty.

3. When collecting feedback, it was not uncommon for "in-the-know" researchers to make opposite suggestions. Some people thought some of the problems in the Alignment section were unimportant, while others thought they were the most critical. We attempted to include most research directions.

[MLSN #1]: ICLR Safety Paper Roundup (Dan Hendrycks) (summarized by Rohin): This is the first issue of the ML Safety Newsletter, which is "a monthly safety newsletter which is designed to cover empirical safety research and be palatable to the broader machine learning research community".

Rohin's opinion: I'm very excited to see this newsletter: this is a category of papers that I want to know about and that are relevant to safety, but I don't have the time to read all of these papers given all the other alignment work I read, especially since I don't personally work in these areas and so often find it hard to summarize them or place them in the appropriate context. Dan on the other hand has written many such papers himself and generally knows the area, and so will likely do a much better job than I would. I recommend you subscribe, especially since I'm not going to send a link to each MLSN in this newsletter.



Selection Theorems: A Program For Understanding Agents (John Wentworth) (summarized by Rohin): This post proposes a research area for understanding agents: selection theorems. A selection theorem is a theorem that tells us something about agents that will be selected for in a broad class of environments. Selection theorems are helpful because (1) they can provide additional assumptions that can help with learning human values, and (2) they can tell us likely properties of the agents we build by accident (think inner alignment concerns).

As an example, coherence arguments demonstrate that when an environment presents an agent with “bets” or “lotteries”, where the agent cares only about the outcomes of the bets, then any “good” agent can be represented as maximizing expected utility. (What does it mean to be “good”? This can vary, but one example would be that the agent is not subject to Dutch books, i.e. situations in which it is guaranteed to lose resources.) This can then be turned into a selection argument by combining it with something that selects for “good” agents. For example, evolution will select for agents that don’t lose resources for no gain, so humans are likely to be represented as maximizing expected utility. Unfortunately, many coherence arguments implicitly assume that the agent has no internal state, which is not true for humans, so this argument does not clearly work. As another example, our ML training procedures will likely also select for agents that don’t waste resources, which could allow us to conclude that the resulting agents can be represented as maximizing expected utility, if the agents don't have internal states.

Coherence arguments aren’t the only kind of selection theorem. The good(er) regulator theorem (AN #138) provides a set of scenarios under which agents learn an internal “world model”. The Kelly criterion tells us about scenarios in which the best (most selected) agents will make bets as though they are maximizing expected log money. These and other examples are described in this followup post.

The rest of this post elaborates on the various parts of a selection theorem and provides advice on how to make original research contributions in the area of selection theorems. Another followup post describes some useful properties for which the author expects there are useful selections theorems to prove.

Rohin's opinion: People sometimes expect me to be against this sort of work, because I wrote Coherence arguments do not imply goal-directed behavior (AN #35). This is not true. My point in that post is that coherence arguments alone are not enough, you need to combine them with some other assumption (for example, that there exists some “resource” over which the agent has no terminal preferences). I do think it is plausible that this research agenda gives us a better picture of agency that tells us something about how AI systems will behave, or something about how to better infer human values. While I am personally more excited about studying particular development paths to AGI rather than more abstract agent models, I do think this research would be more useful than other types of alignment research I have seen proposed.



State of AI Report 2021 (Nathan Benaich and Ian Hogarth) (summarized by Rohin): As with past (AN #15) reports (AN #120), I’m not going to summarize the entire thing; instead you get the high-level themes that the authors identified:

1. AI is stepping up in more concrete ways, including in mission critical infrastructure.

2. AI-first approaches have taken biology by storm (and we aren’t just talking about AlphaFold).

3. Transformers have emerged as a general purpose architecture for machine learning in many domains, not just NLP.

4. Investors have taken notice, with record funding this year into AI startups, and two first ever IPOs for AI-first drug discovery companies, as well as blockbuster IPOs for data infrastructure and cybersecurity companies that help enterprises retool for the AI-first era.

5. The under-resourced AI-alignment efforts from key organisations who are advancing the overall field of AI, as well as concerns about datasets used to train AI models and bias in model evaluation benchmarks, raise important questions about how best to chart the progress of AI systems with rapidly advancing capabilities.

6. AI is now an actual arms race rather than a figurative one, with reports of recent use of autonomous weapons by various militaries.

7. Within the US-China rivalry, China's ascension in research quality and talent training is notable, with Chinese institutions now beating the most prominent Western ones.

8. There is an emergence and nationalisation of large language models.

Rohin's opinion: In last year’s report (AN #120), I said that their 8 predictions seemed to be going out on a limb, and that even 67% accuracy woud be pretty impressive. This year, they scored their predictions as 5 “Yes”, 1 “Sort of”, and 2 “No”. That being said, they graded “The first 10 trillion parameter dense model” as “Yes”, I believe on the basis that Microsoft had run a couple of steps of training on a 32 trillion parameter dense model. I definitely interpreted the prediction as saying that a 10 trillion parameter model would be trained to completion, which I do not think happened publicly, so I’m inclined to give it a “No”. Still, this does seem like a decent track record for what seemed to me to be non-trivial predictions. This year's predictions seem similarly "out on a limb" as last year's.

This year’s report included one-slide summaries of many papers I’ve summarized before. I only found one major issue -- the slide on TruthfulQA (AN #165) implies that larger language models are less honest in general, rather than being more likely to imitate human falsehoods. This is actually a pretty good track record, given the number of things they summarized where I would have noticed if there were major issues.


CHAI Internships 2022 (summarized by Rohin): CHAI internships are open once again! Typically, an intern will execute on an AI safety research project proposed by their mentor, resulting in a first-author publication at a workshop. The early deadline is November 23rd and the regular deadline is December 13th.


I'm always happy to hear feedback; you can send it to me, Rohin Shah.


An audio podcast version of the Alignment Newsletter is available. This podcast is an audio version of the newsletter, recorded by Robert Miles.

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My point in that post is that coherence arguments alone are not enough, you need to combine them with some other assumption (for example, that there exists some “resource” over which the agent has no terminal preferences).

Coherence arguments sometimes are enough, depending on what the agent is coherent over.

depending on what the agent is coherent over.

That's an assumption :P (And it's also not one that's obviously true, at least according to me.)

What is the extra assumption? If you're making a coherence argument, that already specifies the domain of coherence, no? And so I'm not making any more assumptions than the original coherence argument did (whatever that argument was). I agree that the original coherence argument can fail, though.

I think we're just debating semantics of the word "assumption".

Consider the argument:

A superintelligent AI will be VNM-rational, and therefore it will pursue convergent instrumental subgoals

I think we both agree this is not a valid argument, or is at least missing some details about what the AI is VNM-rational over before it becomes a valid argument. That's all I'm trying to say.

Unimportant aside on terminology: I think in colloquial English it is reasonable to say that this is "missing an assumption". I assume that you want to think of this as math. My best guess at how to turn the argument above into math would be something that looks like:

This still seems like "missing assumption", since the thing filling the ? seems like an "assumption".

Maybe you're like "Well, if you start with the setup of an agent that satisfies the VNM axioms over state-based outcomes, then you really do just need VNM to conclude 'convergent instrumental subgoals', so there's no extra assumptions needed". I just don't start with such a setup; I'm always looking for arguments with the conclusion "in the real world, we have a non-trivial chance of building an agent that causes an existential catastrophe". (Maybe readers don't have the same inclination? That would surprise me, but is possible.)