Value generalisation Theory of Change: putting it into practice

By Stuart Armstrong @ 2026-08-31T12:58 (+4)

Cross posted at the alignment forum.

In the previous post, I presented my theory of change for why value generalisation is vital for AI alignment. Here I'll add the practical part of the argument: given those facts, why explicitly try to do value generalisation, what are the dangers of the approach, how should it be done, and how do we mitigate the risks?

The formal theory of change is down below, but I'll put a collapsible version here, to make references easier:

Explicit targeting of value generalisation

• Claim J: explicit value generalisation is much more useful than implicit value generalisation.

Fundamentally, there's a difference between an AI that knows what course humans would consider the best one, and one that actually follows that course. Having the AI capable of value generalisation inside its own mind is not useful, unless we can incorporate that generalisation into its goals. And explicit generalisation allows that.

This leads to the crucial and unfortunate claim:

• Claim K: value generalisation will aid in empirical generalisation. But empirical generalisation will likely not aid value generalisation.

Empirical generalisation is the ability to update features usefully across model splinterings, in ways that preserve or improve the ability of the modeller to effectively influence the world.

Claim K derives in part from claim J: since useful value generalisation is the explicit kind, implicit empirical generalisation is not likely to usefully help. It also derives from the fact that empirical generalisation can afford to discard its features if necessary: we refined concepts like heat while discarding vitalism. But we can't just discard the "suffering" feature in "avoid human suffering"; it has to be redefined and extended. So value generalisation is strictly harder.

Somewhat connected to that is the fact that "in the limit" of infinite computation and infinite observation, empirical generalisation is doable, but value generalisation involves moral choices that don't come free from mere observations.

This asymmetry leads to the unfortunate result that:

• Claim L: a value generalisation project will increase AI capabilities.

How to achieve value generalisation

I've previously made the claim that:

• Claim M: strong generalisation is a uniquely human ability, that current LLMs don't have and will likely not develop; nor will any similar model develop strong generalisation either.

However, this claim is not crucial to the approach. If M is wrong, claim L becomes less worrying (AIs will develop the ability anyway) but the research becomes more urgent: we need to get a decent start on explicit value generalisation before AIs get good at empirical generalisation.

The weaker claim is:

• Claim M1: studying how humans do strong generalisation is a fruitful way of analysing the skill, at least initially.

The arguments in the second value generalisation post apply also for claim M1. Even if one is of the claim that "LLMs will always fail at strong generalisation", there is certainly evidence that humans are doing something very different (and much more data-efficient) when we generalise.

The question of timing

Given that value generalisation is essential to alignment, but also could lead to capability increase, the question is: should we research it now (early) or later (late)?

I believe:

• Claim N: value generalisation should be researched early.

The arguments for this are that it's better to have a capability increase while the models are weaker and more controllable, and early value generalisation can more easily be integrated into models from the get-go rather than retro-fitting at a later date. We want a minimal capability overhang that empirical generalisation can unleash. And, of course, we want to avoid the scenarios where the research arrives too late.

The corporate argument

Given the above, I propose creating either a research program or a commercial entity to find useable solutions to value generalisation. But I will claim:

• Claim ): if value generalisation is indeed revolutionary but does lead to dangerous capability increases, then the commercial route weakly dominates the research route.

The main argument for claim O comes from the question: assume that value generalisation is solved or partially solved, then what? We have a powerful alignment technology that is essential for alignment, but also a powerful capability technology, in a way that can't be separated. What do we do with it?

Well, we'd probably want to hand it over to some trustworthy entity (some have suggested a "CERN for AI") to implement the alignment part at some point.

But that is easier to achieve for a corporation than for a research program. A corporation is much better placed to keep its research private or patent-protected and concealed from the world. It can sell or license the research to a trustworthy entity, or sell it to a semi-trustworthy entity with conditions. And it can also choose to be the trustworthy entity and start implementing alignment itself. Indeed:

• Claim P: if the capability boost from generalisation is inevitable, a corporation can mix the capability increase with the alignment increase (such as prealigned AIs) so that the first generalising AIs are aligned, and the initial income from generalising AIs flows to value aligned entities.

I've mentioned the advantages of the corporate route, but what of the advantages of the academic or research route - such as openness allowing more scrutiny and feedback, getting more trust from the safety community? Well, the research is potentially dangerous, so we can't expect to have it publicly or semi-publicly available. Thus:

• Claim O1: the potential need for secrecy reduces the standard advantages from the academic or research institution route.

Armouring the corporate weak points

Of course, the corporate path has its weaknesses, mainly revolving around the profit motive. Investors, the legal system, management, and employees will all want a company to cash in on legal innovative ideas, even if the ideas are potentially dangerous. So a first step would be:

• Design I: the corporation should have an independent AI ethics board, with the power to block the use of IP it deems dangerous. To facilitate this, the AI ethics board should be the owner of the IP.

That solves the problem in the formal sense, which means that it doesn't really solve it. Additional measures would be:

• Design II0: the employees and management should be value aligned with AI safety.
• Design II1: the investors should be value-aligned with AI safety.

That also helps; also not enough. The situation will never be "do I kill everyone with certainty to make $10,000 more this year"? The situation will be more like "when I feel the ethics board is being fussy and unreasonable and overly cautious, do I nevertheless bow down to their irrational decrees that will cost me a lot of my expected income that I have worked so hard on and so earned, and also give up my possibility of improving the world for the better"? And value-aligned investors remain investors: they expect to make a profit (a not-unreasonable demand, which the legal system backs up).

I don't expect myself to be immune to that pressure and those arguments. And it's not just a question of holding firm; as OpenAI's experience demonstrates:

• Claim Q: if the employees are ready to jump ship to a partner organisation that can continue the research with a minimum of fuss, the AI ethics board's power is theoretical rather than real.

So I've been considering ways to remove the stark tension. One design is:

• Design III: the AI ethics board will have the power to implement a "pivot to immediate profit". The long-range dangerous IP will be removed from the company, and the company will turn to making money from all the partial ideas and designs that it has made and rejected (as not being alignment relevant) along the way. The board will, of course, vet these ideas for danger, but immediate short-term profitability is less likely to overlap with truly dangerous IP.

Arguably, the pivot to immediate profit would be more profitable, in expectation, than speculative long term IP. This would relieve much of the commercial pressure. And if the long term IP was truly world-improving, the ethics board would find a way to get it carefully deployed, so world-improving impulses are preserved (if the research is merely dangerous, the ethics board would bury it, and good riddance).

Plan, milestones, and assumption checks

Let's gather all the previous together to put it all in one plan:

1. Inputs / activities: investment/grants, a small research team, small-medium compute resources.
2. Outputs:
   1. Solutions to the three components of value generalisation (see here) in academically rigorous forms, demonstrations of these solutions on toy problems, public benchmarks, and new benchmarks. If going commercial, applications of this value generalisation to saleable products.
      1. The first component is recognising that the AI is off-distribution in a value-relevant way.
      2. The second component is establishing what features should be used to reach a decision while off-distribution this way.
      3. The third component is to reach a good decision while off distribution, and to loop through the process again to critique and improve the decision, including using outside feedback.
   2. Combination of these approaches in a successful prealigned learning model.
      1. If going commercial and it is safe, sale of the model to the public.
3. Intermediate outcomes:
   1. Development of value generalisation alignment methods for AIs.
   2. Making these methods available to AI safety researchers.
   3. Prealigned models being generally available to safely empower users and keep humanity on track for a positive outcome.
   4. If the approach fails, the failed attempts and the partial successes will be made available to others.
4. Impact:
   1. If failed:
      1. A seemingly promising approach crossed off the list of possible paths to alignment.
      2. A better understanding of the issues around the "value generalisation" framing.
   2. If intermediate outcome:
      1. A tool or collection of useful tools or models that can improve some AI alignment techniques.
   3. If successful:
      1. AI alignment, or a big step forwards towards it.
      2. An increase in AI capabilities.

Ongoing and initial assessments

This theory of change has been a bit light on specific probability estimates for different assumptions, and for the overall program.

The reason is that, for this approach, the proof of the pudding is in the eating. Now, I've presented solid theoretical arguments for the necessity and usefulness of value generalisation, I can point to my own research track record and intermediate successful results and a plan for the R&D path and how it builds on human generalisation abilities.

I feel the case is compelling, but it rests ultimately on a judgement call: that it makes sense to group all these problems under the heading "value generalisation", to see it all as a single specific goal, and to aim to tackle it directly.

That judgement call may be valid (I certainly feel it is!) and is the true crux in this theory of change. And the best way of figuring out its truth or falsity is to... attempt the project and see what happens, see whether the framework gives swift success or falls apart into disparate disconnected problems.

To check on that, we'll need intermediate benchmarks and assessments. The initial phase of the program (carried out in part while the setup is happening) will include establishing key benchmarks for each subsequent step.

We'll be using public benchmarks for these purposes, though they need to be used with care^[1]. A lot of benchmarks get saturated quite easily by models that don't show the true performance the benchmark was supposed to measure. We need algorithms that solve benchmarks via value generalisation, not via any intermediate incomplete shortcuts. The benchmark design can do part of the work, but controlling the information and methods the algorithm can use is also crucial.

Conclusion: value generalisation is a useful path for AI alignment

To summarise:

1. Most AI alignment failures are value generalisation failures.
2. Non-decomposability: alignment likely can't be decomposed into smaller simpler parts.
3. Thus value generalisation is necessary for alignment, and will make alignment a lot easier.
4. Explicitly targeting value generalisation is necessary.
5. Unfortunately, value generalisation aids empirical generalisation (a capability) while the converse is not true.
6. A corporate structure weakly dominates a research structure for solving value generalisation and for using the results as safely as possible.
7. Good design and a good AI ethics board can mitigate the vulnerabilities of the corporate route.
8. There is a plan to solve value alignment step by step, focusing first on how agents identify they are out of distribution, then what features to use for deciding in those circumstances, and finally what decision to make and how to assess and improve that decision.

So, let's go and solve this little alignment problem, aye? ^_^

1. ^{^}

   Take the "wolf vs husky" image classification problem, where the wolf images were all taken on snow, causing the classifier to misclassify any light-background image as a wolf.

   We had a similar benchmark, "tanks vs forests" where the tank images were taken on a cloudy day (a recreation of an apocryphal but traditional tale in machine learning). The ACE algorithm successfully disambiguated "darkness" from "tankiness".

   But a well-trained image recognition model could likely solve both of these benchmarks, just by having enough wolf/dog/tank/forest data that it can resolve these images anyway. That's not out-of-distribution learning, that's increasing the training data until the benchmarks are in-distribution.