TL;DR: A strategy aiming to elicit latent knowledge (or to make any hopefully robust, hopefully generalizable prediction) from interpreting an AGI’s fine-grained internal data may be unlikely to succeed, given that the complex system of an AGI’s agent-environment interaction dynamics will plausibly turn out to be computationally irreducible. In general, the most efficient way to predict the behavior of a complex agent in an environment is to run it in that exact environment. Mechanistic interpretability is unlikely to provide a reliable safety plan that magically improves on the default strategy of empiricism. Coarse-grained models of the complex system have a realistic chance of making robust predictions out-of-distribution, although such predictions would then necessarily be limited in scope.
The paradigm of deep learning, potentially with a small extra step, seems likely sufficient for creating AGI. This is because AI capabilities seem likely to continue increasing, given empirical scaling laws, the decreasing cost of compute, and AI corporations’ unabating desire to build increasingly powerful AI. The most recent findings from neuroscience also suggest that across different species, scale is the causal factor behind most general capabilities.
Biological systems like those of evolutionary biology and neuroscience are plausibly the best reference class for large-scale deep-learning models we have. To quote arguably the world’s leading expert in interpreting neural nets, Chris Olah:
“The elegance of ML is the elegance of biology, not the elegance of math or physics.
Simple gradient descent creates mind-boggling structure and behavior, just as evolution creates the awe inspiring complexity of nature.”
For a more detailed case, see (1) Olah’s excellent writeup "Analogies between biology and deep learning" as well as (2) the review paper by Saxe et al. about the analogy between deep learning and systems neuroscience.
Predicting the dynamics of biological systems is often computationally intractable. To quote "The limits to prediction in ecological systems" by Beckage et al.:
“An ecological system changes through time, updating its state continuously, and the process of system evolution can be thought of as computation…Our use of the term ‘system evolution' is much broader in meaning than biological evolution, and also includes changes in abundance, location and interactions between individuals irrespective of species, and the interface between the biotic and abiotic components of the system, e.g., flux of nutrients, water, etc. Predictive models, then, are able to forecast the future state of the system before the system performs the intermediate computations to reach its updated state. An astronomical model, for example, might predict the earth's position and orientation relative to the sun millions of years into the future, without the need for the solar system to perform the intervening computations. The intervening computations that the system performs can be circumvented to predict its future state. The astronomical model might, for example, be used to predict the latitudinal and seasonal distribution of insolation on earth, which describes the past orbital forcing of the climate system, for comparison with paleoclimatic data (e.g., EPICA community members 2004)."
Unlike astronomical systems, however, ecological systems often have computationally irreducible dynamics.
"Computational irreducibility refers to systems where the intervening computations cannot be bypassed using a simplified model. The dynamics of a system that is computationally irreducible cannot be predicted without allowing for the actual evolution of the system…A simplified model that can predict the future state of the system does not exist. Thus, the only way to ascertain the future state of the system is to allow the system to evolve on its own characteristic time scale. Computational irreducibility does not imply that the underlying processes are stochastic or chaotic, but that they are complex. The complexity can be manifested through high levels of contingency, interactions among system components, and nonlinearity. In fact, systems that evolve according to simple deterministic processes with exactly-known initial conditions can give rise to a complex state evolution that cannot be exactly predicted except by allowing the system to evolve in real time…Computational irreducibility, furthermore, may be a fundamental characteristic of some systems and does not merely reflect a shortcoming of proposed models or modeling techniques. This implies that the intrinsic predictability of these systems is inherently low.”
The computational irreducibility of ecological systems is due to “(1) the difficulty of pre-stating the relevant features of the niche, (2) the complexity of ecological communities, and (3) their potential to enable novel system states (e.g., niche creation).” As a result, the inherent predictability of ecological systems out-of-distribution is generally low. Some compelling examples of this phenomenon include the inherent unpredictability of how ecological systems will respond to future climate change and the inherent unpredictability of invasive species impact. An analogous argument correctly deduces that epigenetic systems (of genome-environment interactions) and neurocognitive systems (of brain-environment interactions) have computationally irreducible dynamics.
The three factors causing computational irreducibility in biological systems (comprised of biological agents and their environments) also seem likely to apply to AGI-scale deep-learning systems (comprised of AI agents and their training or deployment environments).
Implications for predictability of agent-environment interactions
What are the implications of computational irreducibility for high-complexity systems like biological systems and future AGI systems? To again quote Beckage et al.:
“Complex systems with extremely large numbers of components can sometimes become predictable from a macro-level perspective due to the averaging of a very large number of separate interactions. In statistical physics, for example, an approximate description of the mean state of a gas is possible without an exact description of the velocities and locations of each molecule; the temperature and pressure of a gas can be described using the ideal gas law. An ecological analogy to the ideal gas law might be the species composition of a forest. Forest composition is ultimately an emergent property that results from the local interactions of many individuals and processes, i.e., seed production and dispersal, competition, growth rates, tradeoffs, etc. While it may not be possible to determine the outcome of all of these complex interactions to predict the species identity of the tree species that captures a given canopy gap, the overall composition of the forest can be predictable to some approximation…While this statistical averaging of interactions is the standard assumption in many deterministic ecological models, it may be more accurate to view most ecological systems as small-to-middle-number systems because local interactions are quite relevant in affecting system behavior. In this case, there would be a general lack of the homogeneous mixing necessary for a purely statistical mechanics view to be applicable.
We conjecture that skill in predicting the future states of ecological systems will decrease as system complexity increases up to some threshold level. Further increases in system complexity beyond this threshold, for example, through expanding interconnected components of the system or increasing potential for nonlinear interactions, will not result in further losses in predictability…Furthermore, this threshold may occur at relatively low system complexity. We note, however, that the behavior of complex ecological systems can often be readily deconstructed and explained in hindsight as the cascade of interactions and nonlinearities is examined and understood. We emphasize that this may not aid predictions of future system states due to computational irreducibility.”
A coarse-grained model—if decently correct—can make robust predictions about a computationally irreducible system, although such predictions would necessarily be informationally incomplete. This is consistent with my research background in high-complexity systems like those of biological science and social science. For such a high-complexity system, the only general hope for predictability out-of-distribution (in the absence of unrealistically large amounts of time and computational resources) is to deduce theorems from a coarse-grained model of the system based on decently correct first principles. And due to information loss, the types of predictions this method can yield are generally quite limited in scope.
In the more optimistic case where one can fully specify a computationally irreducible agent’s environment a priori, the most efficient way to predict the agent’s behavior in that environment is to run it in that exact environment. There is no shortcut, such as one based on the agent's internal data.
What does this mean for current AI safety research directions?
Given that future AGI systems will plausibly be computationally irreducible, I think the following implications of computational irreducibility deserve consideration.
1. Fine-grained interpretability of an AGI-scale model (e.g., interpreting circuits) may be intractable if researchers only have a short amount of time.
Many AI safety researchers consider fine-grained interpretability to be a promising research direction for reducing AGI x-risks. For example, Eliezer Yudkowsky—one of the founders of the AI safety field—has remarked that the interpretability agenda is "exceptional in the field," because he thinks it is one of the few research directions in the field that is "on a pathway to anything important at all."
But this may be false. Due to computational irreducibility, achieving fine-grained interpretability of AGI-scale models may be intractable in the absence of an unrealistically large amount of time and of computational resources.
A cautionary tale is provided by the Human Brain Project, which aimed to achieve a causally accurate predictive model of a brain. Why did the Human Brain Project crash and burn? Because computational irreducibility imposed a hard limit to the scientific upside of the project.
This was predictable, to the point where a year into the $1.6 billion project, almost a thousand neuroscientists—who could have gotten salaries for long periods of time by participating in the project—instead selflessly boycotted it as a waste of scarce scientific resources. That year, the Guardian reported:
“Central to the latest controversy are recent changes made by Henry Markram, head of the Human Brain Project at the Swiss Federal Institute for Technology in Lausanne. The changes sidelined cognitive scientists who study high-level brain functions, such as thought and behaviour. Without them, the brain simulation will be built from the bottom up, drawing on more fundamental science, such as studies of individual neurons. The brain, the most complex object known, has some 86bn neurons and 100tn connections.
‘The main apparent goal of building the capacity to construct a larger-scale simulation of the human brain is radically premature,’ Peter Dayan, director of the computational neuroscience unit at UCL, told the Guardian.
'We are left with a project that can't but fail from a scientific perspective. It is a waste of money, it will suck out funds from valuable neuroscience research, and would leave the public, who fund this work, justifiably upset,' he said.”
And the project did in fact crash and burn. To this day, progress on achieving a causally accurate model of the brain remains marginal at best.
Anthropic plans to rely on interpreting large-scale models at the circuit level. Given the hard bounds on predictability imposed by the phenomenon of computational irreducibility, the Human Brain Project’s waste of $1.6 billion and years of researchers’ time provides a cautionary tale for Anthropic on its strategy for how to use its $580 million funding. This is because the complexity and computational irreducibility of AGI-scale models likely imply that achieving a fine-grained causal understanding of AGI-scale models will require an extremely large amount of time and computational resources, just like for neuroscience.
To be clear, a fine-grained causal understanding may be theoretically achievable given enough time and computational resources. A more optimistic reference case is provided by gene-editing, where scientists—through immense trial and error—have obtained a nontrivial ability to make a priori predictions based entirely on genomic code data. But even this scientific problem is largely unsolved. Because the inherent predictability of the genome-environment system may be low, even gene-editing strategies that scientists are comparatively confident in today will almost certainly come with unforeseen side effects arising from extremely complex and unpredictable epigenetic dynamics.
A counterargument is that researchers have more ready access to internal data for neural nets than they do for neuroscience, and that this advantage can be a game-changer. However, this advantage does not seem to address the core issue of computational irreducibility, which seems likely to be an inevitable consequence of using deep learning rather than lower-complexity paradigms (like software design by a human software engineer). Given that the core issue of computational irreducibility exists, it seems plausible that easier access to internal data will only result in a moderate increase in the rate of solving neural-net interpretability compared to the rate of solving neuroscience interpretability. This would imply that the challenges of solving neuroscience, and the prematureness and resource waste of the Human Brain Project, are apt cautionary tales for a safety plan based on fine-grained interpretability of AGI-scale neural nets, even if Anthropic’s brilliant, well-meaning, and well-funded researchers are the ones carrying out this safety plan.
Computational irreducibility implies that achieving a fine-grained causal understanding of a large-scale model will realistically require patient trial-and-error, in the precise environment in which the model is set to run. Mechanistically interpreting large-scale models is unlikely to provide a reliable safety plan, since it probably cannot efficiently yield the necessary predictions.
And since it is likely easy to make a large-scale model accidentally dangerous, an unprecedented security mindset is probably needed, both from a moral perspective and from the perspective of avoiding a movement-wide credibility risk for EA. This is especially true for Anthropic, a for-profit corporation whose credibility is intertwined with that of the EA movement, and whose $580 million Series B funding was famously raised by lead investor Sam Bankman-Fried (another movement-wide credibility risk that has recently blown up, even likely rising to the point of fraud).
If Anthropic is publicly blamed (fairly or not) for causing a future AGI disaster, then this may cause a substantial credibility loss for the EA movement as a whole. Combined with the one caused by Sam Bankman-Fried, the credibility of the EA movement—on AI safety matters and in general—may not be able to recover.
2. Eliciting Latent Knowledge from fine-grained internal data may be intractable if researchers only have a short amount of time.
See Point 1.
3. Coarse-grained models of AGI systems (e.g., game theory) have a realistic chance of efficiently making robust predictions out-of-distribution, but these predictions will be limited in scope.
The theory of computational irreducibility can explain why success cases in out-of-distribution predictions of complex systems—in biology, economics, and neuroscience—have generally arisen from coarse-grained information. Of course, a necessary condition for a coarse-grained model of a system to yield robust predictions is that the model is based on decently correct first principles.
Even when coarse-grained models based on decently correct first principles can yield robust predictions, however, these predictions then necessarily turn out to be quite limited in scope. To quote Mathematical Models of Social Evolution by McElreath and Boyd:
“Simple formal models can be used to make predictions about natural phenomena. In most cases, these predictions are qualitative. We might expect more or less of some effect as we increase the real-world analogue of a particular parameter of the model. For example, a model of voter turnout might predict that turnout increases in times of national crisis. The precise amount of increase per amount of crisis is very hard to predict, as deciding how to measure “crisis” on a quantitative scale seems like a life's work in itself. Even so, the model may provide a useful prediction of the direction of change. These sorts of predictions are sometimes called comparative statics. And even very simple models can tell us whether some effect should be linear, exponential, or some other functional form. All too often, scientists construct theories which imply highly nonlinear effects, yet they analyze their data with linear regression and analysis of variance. Allowing our models of the actual phenomenon to make predictions of our data can yield much more analytic power. In a few cases, such as sex allocation, models can make very precise quantitative predictions that can be applied to data.”
The tone of the last sentence is arguably too optimistic. The cases in which coarse-grained models can correctly make precise quantitative predictions, like Fisher’s principle of sex allocation, are extremely rare. Fisher’s principle that most sexually reproducing species produce 50% male and 50% female offspring has been called “probably the most celebrated argument in evolutionary biology” because it makes such a precise quantitative prediction, which tends to be the exception in the field, not the norm. And even when such precise predictions are possible, they are likely to then necessarily be quite limited in scope: sex allocation strategy is one of countless many phenotypic dimensions that are relevant for a given biological agent. Most aspects of phenotype are probably subject to a high level of inherent unpredictability due to computational irreducibility. This is why the best we biologists and economists can do for robust prediction usually just consists of comparative-statics predictions or functional-form predictions that are subject to significant information loss.
The above lesson has the following implication. When developing safety plans for AGI-scale models, complexity is likely to be the enemy of security. Assuming a realistic amount of time and computational resources, simple plans for AI safety based on coarse-grained models (e.g., limiting the action space of the AGI, based on game theory/mechanism design) are the ones that have a realistic chance of working in a robust, generalizable manner. And the fact that simple safety plans are insufficient to quickly provide for-profit AGI corporations with everything they want—an AGI that is simultaneously safe and economically useful—should not be used as a source of motivated reasoning that these plans can be magically improved on by a strategy of interpreting fine-grained internal data.
Acknowledgements: I am grateful to Spencer Becker-Kahn, Michael Chen, Johannes Gasteiger, Harrison Gietz, Gwern, Adam Jermyn, Arun Jose, Jonathan Mann, Xavier Roberts-Gaal, and Luke Stebbing for providing very valuable feedback on this draft.
My model for why interpretability research might be useful, translated into how I understand this post's ontology, is mainly that it might let us make coarse-grained predictions using fine-grained insights into the model.
I think it's obviously true that we won't be able to make detailed predictions about what an AGI will do without running it (this is especially clear for a superintelligent AI: since it's smarter than us, we can't predict exactly what actions it will take). I'm not sure if you are claiming something stronger about what we won't be able to predict?
In any case, this does not rule out that there might be computationally cheap to extract facts about the AI that let us make important coarse-grained predictions (such as "Is it going to kill us all?"). For example, we might figure out that the AI is running some computations that look like they're checking whether the AI is still in a training sandbox. The output of those computations seems to influence a bunch of other stuff going on in the AI. If we intervene on this output, the AI behaves very differently (e.g. trying to scam people we're simulating for money). I think this is an unrealistically optimistic picture, but I don't see how it's ruled out specifically by the arguments in this post.
As an analogy: while we can't predict which moves AlphaZero is going to make without running it, we can still make very important coarse-grained predictions, such as "it's going to win", if we roughly know how AlphaZero works internally. You could imagine an analogous chess playing AI that's just one big neural net with learned search. If interpretability can tell us "this thing is basically running MCTS, its value function assigns very high value to board states where it's clearly winning, ...", we could make an educated guess that it's a good chess player without ever running it.
One thing that might be productive would be to apply your arguments to specific examples of how people might want to use interpretability (something like the deception case I outlined above). I currently don't know how to do that, so for now the argument doesn't seem that forceful to me (it sounds more like one of these impossibility results that sometimes don't matter in practice, like no free lunch theorems).
Thank you so much, Erik, for your detailed and honest feedback! I really appreciate it.
I agree with you that it is obviously true that we won't be able to make detailed predictions about what an AGI will do without running it. In other words, the most efficient source of information will be empiricism in the precise deployment environment. The AI safety plans that are likely to robustly help alignment research will be those that make empiricism less dangerous for AGI-scale models. Think BSL-4 labs for dangerous virology experiments, which would be analogous to airgapping, sandboxing, and other AI control methods.
I am not completely pessimistic about interpretability of coarse-grained information, although still somewhat pessimistic. Even in systems neuroscience, interpretability of coarse-grained information has seen some successes (in contrast to interpretability of fine-grained information, which has seen very little success).
I agree that if the interpretability researcher is extremely lucky, they can extract facts about the AI that lets them make important coarse-grained predictions with only a short amount of time and computational resources.
But as you said, this is an unrealistically optimistic picture. More realistically, the interpretability researcher will not be magically lucky, which means we should expect the rate at which prediction-enhancing information is obtained to be inefficient.
And given that information channels are dual-use (in that the AGI can also use them for sandbox escape), we should prioritize efficient information channels like empiricism, rather than inefficient ones like fine-grained interpretability. Inefficient information channels can be net-negative, because they may be more useful for the AGI's sandbox escape compared to their usefulness to alignment researchers.
Perhaps to demonstrate that this is a practical concern rather than just a theoretical concern, let me ask the following. In your model, why did the Human Brain Project crash and burn? Should we expect interpreting AGI-scale neural nets to succeed where interpreting biological brains failed?
I only agree with the first sentence here, and I don't think the rest of the paragraph follows from it. I agree being able to safely experiment on AGIs would be useful, but it's not a replacement for what interpretability is trying to do. Deception is a good example here: how do you empirically tell whether a model is deceptive without giving it a chance to actually execute a treacherous turn? You'd have to fool the model, and there are big obstacles to that. Maybe relaxed adversarial training could help, but that's also more of a research direction than a concrete method for now---I think for any specific alignment approach, it's easy to find challenges. If there is a specific problem that people are currently planning to solve with interpretability, and that you think could be better solved using some other method based on safely experimenting with the model, I'd be interested to hear that example, that seems more fruitful than abstract arguments. (Alternatively, you'd have to argue that interpretability is just entirely doomed and we should stop pursuing it even lacking better alternatives for now---I don't think your arguments are strong enough for that.)
I want to clarify that any story for solving deception (or similarly big obstacles) that's as detailed as what I described seems unrealistically optimistic to me. Out of all stories this concrete that I can tell, the interpretability one actually looks like one of the more plausible ones to me.
This is actually something I'd be interested to read more about (e.g. I think a post looking at what lessons we can learn for interpretability from neuroscience and attempts to understand the brain could be great). I don't know much about this myself, but some off-the-cuff thoughts:
Your post briefly mentions these advantages but then dismisses them because they do "not seem to address the core issue of computational irreducibility"---as I said in my first comment, I don't think computational irreducibility rules out the things people realistically want to get out of interpretability methods, which is why for now I'm not convinced we can draw extremely strong conclusions from neuroscience about the difficulty of interpretability.
ETA: so to answer you actual question about what I think happened with the HBP: in part they didn't have those advantages (and without those, I do think mechanistic interpretability would be insanely difficult). Based on the Guardian post you linked, it also seems they may have been more ambitious than interpretability researchers? (i.e. actually making very fine-grained predictions)
This conclusion has the appearance of being reasonable, while skipping over crucial reasoning steps. I'm going to be honest here.
The fact that mechanistic interpretability can possibly be used to detect a few straightforwardly detectable misalignment of the kinds you are able to imagine right now does not mean that the method can be extended to detecting/simulating most or all human-lethal dynamics manifested in/by AGI over the long term.
If AGI behaviour converges on outcomes that result in our deaths through less direct routes, it really does not matter much whether the AI researcher humans did an okay job at detecting "intentional direct lethality" and "explicitly rendered deception".
There is an equivocation here. The conclusion presumes that applying Peter's arguments to interpretability of misalignment cases that people like you currently have in mind is a sound and complete test of whether Peter's arguments matter in practice – for understanding the detection possibility limits of interpretability over all human-lethal misalignments that would be manifested in/by self-learning/modifying AGI over the long term.
Worse, this test is biased toward best-case misalignment detection scenarios.
Particularly, it presumes that misalignments can be read out from just the hardware internals of the AGI, rather than requiring the simulation of the larger "complex system of an AGI’s agent-environment interaction dynamics" (quoting the TD;LR).
That larger complex system is beyond the memory capacity of the AGI's hardware, and uncomputable.
My understanding is that chaotic dynamics often give rise to emergent order. For biological systems, the copied/reproduced components inside can get naturally selected for causing dynamics that move between chaotic and orderly effects (chaotic enough to be adaptively creative across varying environmental contexts encountered over the system's operational lifecycle; orderly enough that effects are reproduced when similar contexts reappear). But I'm not a biology researcher – would be curious in Peter's thoughts!
See further comments here.
Thanks for writing this! It’s always good to get critical feedback about a potential alignment direction to make sure we aren’t doing anything obviously stupid. I agree with you that finegrained prediction of what an AGI is going to do in any situation is likely computationally irreducible even with ideal interpretability tools.
I think there are three main arguments for interpretability which might well be cruxes.
There are quite a lot of reasons why we should expect interpretability to be much easier than neuroscience
Secondly, the blue brain project is just one example of a high profile failure in neuroscience and we shouldn’t generalize too much based on it. I have had no experience with the blue brain project, but it seems plausible to me that this could just be a standard case of garden-variety mismanagement and overoptimistic goals and hype. From my perspective, as someone who has worked in neuroscience is that the field just keeps chugging along accumulating knowledge and is advancing at a reasonable pace – i.e. our understanding of the brain has improved vastly since 20 years ago. Not at the pace probably required for alignment on short timelines but at a decent level for a scientific field.
Given this, it is not clear to me that interpretability is doomed to failure and it seems a reasonably high EV bet to me.
If by ‘empiricism’ as a channel you mean ‘just run the model and see what it does’, then while some amount of empiricism is necessary, it is also a highly dangerous channel to observe and so we should be trying to get as many bits as possible without requiring empiricism. Pre-deployment interpretability is one way to potentially get a lot of bits of information (although I agree not all the bits) without having to expose yourself to this danger. Hopefully interpretability, even if using only fairly coarse grained information can already eliminate a lot of ‘obviously dangerous AGIs’ before you have to run them.
Some empiricism will likely be necessary though and I agree that designing highly secure test-harnesses for the AGI akin to BSL-4 labs will be another necessary component to safety. However, high-powered interpretability will be a vital safety measure to be applied inside such a safe test harness. Ideally, while the AGI is running in some simulation, with interpretability tools we can be constantly scanning it for deception, for realization that it is in a simulation, for any kind of other malicious intent, and then abort or intervene to fix it if this is the case. I think just relying on airgapping and other physical measures is a bad idea vs a superintelligence and in practice we should be trying to build up as many uncorrelated lines of defense as possible in the test-harness.
This is an interesting objection. While it is possible that the AGI could hack interpretability channels, it seems much more difficult than just communicating in the normal way by running in the world – i.e. the ‘empirical channel’. This is because it probably doesn’t know (and we should be careful to make sure that it definitely does not know) what interpretability tools we are using on it, and that interpretability tools can be applied before we actually run the AGI (i.e. directly to weights) or to individual components in isolation.
Thank you so much for your insightful and detailed response, Beren! I really appreciate your time.
The cruxes seem very important to investigate.
It probably helps to have the AGI's architecture hand-designed to be more human-interpretable. My model is that on the spectrum of high-complexity paradigms (e.g., deep learning) to low-complexity paradigms (e.g., software design by a human software engineer), having the AGI's architecture be hand-designed moves away from the former and towards the latter, which helps reduce computational irreducibility and thereby increase out-of-distribution predictability (e.g., on questions like "Is the model deceptive?").
However, my guess is that in order for out-of-distribution predictability of the system to be nontrivial, one would need to go substantially towards the low-complexity end of the spectrum. This would make it unlikely for the model to achieve AGI-like capabilities.
It would be great if we can get a statistical-mechanics-like theory. Realistically, such a theory would probably be a combination of "small-to-middle-number systems because local interactions are quite relevant in affecting system behavior. In this case, there would be a general lack of the homogeneous mixing necessary for a purely statistical mechanics view to be applicable."
I can't rule it out (gene editing is the optimistic outside view here), but I expect such interventions to be imperfect and vulnerable to unforseeable side effects. These interventions would likely require immense trial-and-error to achieve nontrivial out-of-distribution predictability.
I agree with the characterization "not at the pace probably required for alignment on short timelines but at a decent level for a scientific field." Indeed, the main point I wanted to make was my skepticism that interpretability research on AGI-scale models will progress fast enough to solve alignment in a short amount of time.
I completely agree, as long as the lines of defense are net-positive rather than net-negative. An information channel should only be opened if it helps the alignment researchers (to align the AGI) more than it helps the likely by-default misaligned AGI (to prematurely escape its sandbox).
My guess is that the reward-risk tradeoff of empirical channels—empiricism in the deployment environment or a precise replica of the deployment environment—is more likely to be favorable than that of interpretability channels. This is because the reward is high (empiricism efficiently yields predictive information) while ways to mitigate the risk are human-understandable (as opposed to "complexity is the enemy of security").
If the AGI doesn't have prior knowledge of our interpretability plans and how to exploit them (e.g., by deceiving us into a false sense of security), then I would be much more optimistic about the reward-risk tradeoff of interpretability channels! This is why we should keep our interpretability plans inacessible to the AGI as much as possible. Since there is plausibly a significant amount of secrecy value in interpretability plans, we should:
I have been campaigning for these measures, but many AI safety researchers have generally opposed adopting Measure #1. I hope this will change going forward!
It seems to me that this argument proves much too much. If I understand correctly, you're saying that various systems including advanced ML-based AI are 'computationally irreducible', by which you mean there's no simplified model of the system that makes useful predictions. I don't think humans are computationally irreducible in this way. For example, I think you can make many very useful predictions about humans by modeling them as (for example) having some set of goals, habits, tendencies, and knowledge. In particular, knowing what the human's intentions or goals are is very useful for the sort of predictions that we need to make in order to check if our AI is aligned. Of course, it's difficult to identify what a human's intentions are just by having access to their brain, but as I understand it that's not the argument you're making.
Thank you so much, Beth, for your extremely insightful comment! I really appreciate your time.
I completely agree with everything you said. I agree that "you can make many very useful predictions about humans by modeling them as (for example) having some set of goals, habits, tendencies, and knowledge," and that these insights will be very useful for alignment research.
I also agree that "it's difficult to identify what a human's intentions are just by having access to their brain." This was actually the main point I wanted to get across; I guess it wasn't clearly communicated. Sorry about the confusion!
My assertion was that in order to predict the interaction dynamics of a computationally irreducible agent with a complex deployment environment, there are two realistic options:
When researchers try to predict intent from internal data, their assumptions/first principles (based on the limited empirical data they have) will probably not be guaranteed to be "valid even in the unknown deployment enviroment." Hence, there is little robust reason to believe that the predictions based on these model assumptions will be generalizable out-of-distribution.
At some points in your comment you use the criterion "likely to be valid", at other points you use the criterion "guaranteed to be valid". These are very different! I think almost everyone agrees that we're unlikely to get predictions which are guaranteed to be valid out-of-distribution. But that's true of every science apart from fundamental physics: they all apply coarse-grained models, whose predictive power out-of-distribution varies very widely. There are indeed some domains in which it's very weak (like ecology), but also some domains in which it's pretty strong (like chemistry). There are some reasons to think interpretability will be more like the former (networks are very complicated!) and some reasons to think it'll be more like the latter (experiments with networks are very reproducible). I don't think this is the type of thing which can be predicted very well in advance, because it's very hard to know what types of fundamental breakthroughs may arise.
More generally, the notion of "computational irreducibility" doesn't seem very useful to me, because it takes a continuous property (some systems are easier or harder to make predictions about) and turns it into a binary property (is it computationally reducible or not), which I think obscures more than it clarifies.
Thank you for this critique! They are always helpful to hone in on the truth.
So as far as I understand your text, you argue that fine-grained interpretability loses out against "empiricism" (running the model) because of computational intractability.
I generally disagree with this. beren points out many of the same critiques of this piece as I would come forth with. Additionally, the arguments seem too undefined, like there is not in-depth argumentation enough to support the points you make. Strong upvote for writing them out, though!
You emphasize the Human Brain Project (HBP) quite a lot, even in the comments, as an example of a failed large-scale attempt to model a complex system. I think this characterization is correct but it does not seem to generalize beyond the project itself. It seems just as much like a project management and strategy problem as so much else. Benes' comment is great for more reasoning into this and why ANNs seem significantly more tractable to study than the brain.
Additionally, you argue that interpretability and ELK won't succeed simply because of the intractability of fine-grained interpretability. I have two points against this view:
1. Mechanistic interpretability have clearly already garnered quite a lot of interesting and novel insights into neural networks and causal understanding since the field's inception 7 years ago.
It seems premature to disregard the plausibility of the agenda itself, just as it is premature to disregard the project of neuroscience based on HBP. Now, arguing that it's a matter of speed seems completely fine but this is another argument and isn't emphasized in the text.
2. Mechanistic interpretability does not seem to be working on fine-grained interpretability (?).
Maybe it's just my misunderstanding of what you mean by fine-grained interpretability, but we don't need to figure out what neurons do, we literally design them. So the inspections happen at feature level, which is much more high-level than investigating individual neurons (sometimes these features seem represented in singular neurons of course). The circuits paradigm also generally looks at neural networks like systems neuroscience does, interpreting causal pathways in the models (of course with radical methodological differences because of the architectures and computation medium). The mechanistic interpretability project does not seem misguided by an idealization of neuron-level analysis and will probably adopt any new strategy that seems promising.
For example work in this paradigm that seems promising, see interpretability in the wild, ROME, the superpositions exposition, the mathematical understanding of transformers and the results from the interpretability hackathon.
For an introduction to features as the basic building blocks as compared to neurons, see Olah et al.'s work (2020).
When it comes to your characterization of the "empirical" method, this seems fine but doesn't conflict with interpretability. It seems you wish to make game theory-like understanding of the models or have them play in settings to investigate their faults? Do you want to do model distillation using circuits analyses or do you want AI to play within larger environments?
I falter to understand the specific agenda from this that isn't done by a lot of other projects already, e.g. AI psychology and building test environments for AI. I do see potential in expanding the work here but I see that for interpretability as well.
Again, thank you for the post and I always like when people cite McElreath, though I don't see his arguments apply as well to interpretability since we don't model neural networks with linear regression at all. Not even scaling laws use such simplistic modeling, e.g. see Ethan's work.
Thank you so much for your detailed and insightful response, Esben! It is extremely informative and helpful.
The main benefit of interpretability, if it can succeed, is that one can predict harmful future behavior (that would have occurred when deployed out-of-distribution) by probing internal data. This allows the researchers to preemptively prevent the harmful behavior: for example, by retraining after detecting deceptive intent. If this is scientifically possible, it would be a substantial benefit, especially since it is generally difficult to obtain out-of-distribution predictions from atheoretical empiricism.
However, I am skeptical that interpretability can achieve nontrivial success in out-of-distribution predictions, especially in the amount of time alignment researchers will realistically have. The reason is that deceptive intent is likely a fine-grained trait at the internal-data level (rather than at the behavioral level). Consequently, computational irreducibility is likely to impose a hard bound on predicting deceptive intent out-of-distribution, at least when assuming realistic amounts of time and resources.
My guess is that detecting deceptive intent solely from a neural net's internal data is probably at least as fine-grained as behavioral genetics or neuroscience. These fields have made some progress, but preemptively predicting behavioral traits from internal data remains mostly unsolved.
For example, consider a question analogous to that of deceptive misalignment: 'Is the given genome optimized for inclusive fitness, or is it optimized for a proxy goal that deviates from inclusive fitness in certain historically unprecedented environments?' We know that evolutionary pressures select for maximizing inclusive fitness. However, the genome is optimized not for inclusive fitness, but for a proxy goal (survive and engage in sexual intercourse) that deviates from inclusive fitness in environments that are sufficiently distinct from ancestral environments.
How did scientists find out that the genome is optimized for a proxy goal? Almost entirely from behavior. We have a coarse-grained behavioral model that is quite good and generalizable. Evolution shaped animals' behavior towards a drive for sexual intercourse, but historically unprecedented environmental changes (e.g., widespread availability of birth control) has made this proxy goal distinct from inclusive fitness. Parsimonious models based on first principles that are likely to be correct, like the above one, have a realistic chance of achieving situation-specific predictability that generalizes out-of-distribution.
In contrast, there is still very little understanding of which genes interact to cause animals' sex drive. Which genes affect sex drive? Probably a substantial proportion of them, and they probably interact in interconnected and nonlinear ways (including with the extremely complex, multidimensionally varying environment) to produce behavioral traits in an unpredictable manner. Moreover, a lot of the information needed to predict behavioral traits like sex drive will lie in the specific environment and how it interacts with the genome. Only the most coarse-grained of these interaction dynamics will be predictable via bypassing empiricism with a statistical-mechanics-like model, due to computational irreducibility. And such a coarse-grained model will likely be rooted in behavior-based abstractions.
Deep-learning neural nets do come with an advantage lacked by behavioral genetics and neuroscience: a potentially complete knowledge of the internal data, the environmental data, and the data of their interaction throughout the whole training process.
But there is a missing piece: complete knowledge of the deployment environment. Any internals-based model of deceptive intent that alignment researchers can come up with is only guaranteed to hold in the subset of environments that the researchers have empirically tested. In the subset of environments that the polycausal model has not been tested in, there is no a priori reason that the model will generalize correctly. A barrier to generalizability is posed by the nonlinear and interconnected interactions between the neural net's internals and the unprecedented environment, which can and likely will manifest differently depending on the environment. Relaxed adversarial training can help test a wider variety of environments, but this is still hampered by the blind spot of being unable to test the subset of environments that cannot be instantiated at human-level capabilities (e.g., the environment in which RSA encryption is broken). Thus, my guess is that the intrinsic out-of-distribution predictability of the AGI neural net's behavior would be low, just like that of behavioral genetics or neuroscience.
For a conceptual example, consider the fact that the dynamics of cellular automata can change drastically with just one cell’s change in the initial conditions. See Figure 1 of Beckage et al. (Code 1599 in Wolfram's A New Kind of Science), reproduced below:
In general, the only way to accurately ascertain how a computationally irreducible agent will behave in a complex environment is to run it in that environment. Even with complete knowledge of the agent's internals, incomplete knowledge of the environment is sufficient to constrain a priori predictability. I expect that many predictions yielded by interpretability tools in the pre-deployment environment will fail to generalize to the post-deployment environment, unless the two are equal.
Sorry for the miscommunication! I meant to say that the rate at which mechanistic interpretability will yield useful, generalizable information is slow, not zero.
But this is sufficient for concern because informational channels are dual-use; the AGI can use it for sandbox escape. We should only open an interpretability channel if the rate of scientific benefit exceeds the rate of cost (risk of premature sandbox escape by a misaligned AGI).
My opinion is that while mechanistic interpretability has made some progress, the rate at which this progress is happening is not fast enough to solve alignment in a short amount of time and computational resources. So far, the rate of progress in interpretability research has been substantially outpaced by that in AI capabilities research. I think this was predictable, due to what we know about computational irreducibility.
Roughly speaking, there is a spectrum between high-complexity paradigms of design (e.g., deep learning) and low-complexity, modular paradigms of design (e.g., software design by a human software engineer). My guess is that for many complex tasks, the optimal equilibrium strategy can be achieved only by the former, and attempting to meaningfully move towards the latter end of the spectum will result in sacrificing performance. For example, I expect that we won't be able to build AGI via modular software design by a human software engineer, but that we will be able to build it by deep learning.
In Ethan's scaling law, extrapolatory generalization is only guaranteed to be valid locally ("perfectly extrapolate until the next break"), and not globally. This is completely consistent with my prior. My assertion was that in order to globally extrapolate empirical findings to an unknown deployment environment, only simple models have a nontrivial chance of working (assuming realistic amounts of time and computational resources). These simple models will likely be based on parsimonious first principles that we have strong reason to be valid even in the unknown environment. And consequently, they will likely be largely based on behavioral data rather than the internal data of the agent-environment interaction dynamics.