(This post was factored out of a larger post that I (Nate Soares) wrote, with help from Rob Bensinger, who also rearranged some pieces and added some text to smooth things out. I'm not terribly happy with it, but am posting it anyway (or, well, having Rob post it on my behalf while I travel) on the theory that it's better than nothing.)
I expect navigating the acute risk period to be tricky for our civilization, for a number of reasons. Success looks to me to require clearing a variety of technical, sociopolitical, and moral hurdles, and while in principle sufficient mastery of solutions to the technical problems might substitute for solutions to the sociopolitical and other problems, it nevertheless looks to me like we need a lot of things to go right.
Some sub-problems look harder to me than others. For instance, people are still regularly surprised when I tell them that I think the hard bits are much more technical than moral: it looks to me like figuring out how to aim an AGI at all is harder than figuring out where to aim it.
Within the list of technical obstacles, there are some that strike me as more central than others, like "figure out how to aim optimization". And a big reason why I'm currently fairly pessimistic about humanity's odds is that it seems to me like almost nobody is focusing on the technical challenges that seem most central and unavoidable to me.
Many people wrongly believe that I'm pessimistic because I think the alignment problem is extraordinarily difficult on a purely technical level. That's flatly false, and is pretty high up there on my list of least favorite misconceptions of my views.
I think the problem is a normal problem of mastering some scientific field, as humanity has done many times before. Maybe it's somewhat trickier, on account of (e.g.) intelligence being more complicated than, say, physics; maybe it's somewhat easier on account of how we have more introspective access to a working mind than we have to the low-level physical fields; but on the whole, I doubt it's all that qualitatively different than the sorts of summits humanity has surmounted before.
It's made trickier by the fact that we probably have to attain mastery of general intelligence before we spend a bunch of time working with general intelligences (on account of how we seem likely to kill ourselves by accident within a few years, once we have AGIs on hand, if no pivotal act occurs), but that alone is not enough to undermine my hope.
What undermines my hope is that nobody seems to be working on the hard bits, and I don't currently expect most people to become convinced that they need to solve those hard bits until it's too late.
Below, I'll attempt to sketch out what I mean by "the hard bits" of the alignment problem. Although these look hard, I’m a believer in the capacity of humanity to solve technical problems at this level of difficulty when we put our minds to it. My concern is that I currently don’t think the field is trying to solve this problem. My hope in writing this post is to better point at the problem, with a follow-on hope that this causes new researchers entering the field to attack what seem to me to be the central challenges head-on.
Discussion of a problem
On my model, one of the most central technical challenges of alignment—and one that every viable alignment plan will probably need to grapple with—is the issue that capabilities generalize better than alignment.
My guess for how AI progress goes is that at some point, some team gets an AI that starts generalizing sufficiently well, sufficiently far outside of its training distribution, that it can gain mastery of fields like physics, bioengineering, and psychology, to a high enough degree that it more-or-less singlehandedly threatens the entire world. Probably without needing explicit training for its most skilled feats, any more than humans needed many generations of killing off the least-successful rocket engineers to refine our brains towards rocket-engineering before humanity managed to achieve a moon landing.
And in the same stroke that its capabilities leap forward, its alignment properties are revealed to be shallow, and to fail to generalize. The central analogy here is that optimizing apes for inclusive genetic fitness (IGF) doesn't make the resulting humans optimize mentally for IGF. Like, sure, the apes are eating because they have a hunger instinct and having sex because it feels good—but it's not like they could be eating/fornicating due to explicit reasoning about how those activities lead to more IGF. They can't yet perform the sort of abstract reasoning that would correctly justify those actions in terms of IGF. And then, when they start to generalize well in the way of humans, they predictably don't suddenly start eating/fornicating because of abstract reasoning about IGF, even though they now could. Instead, they invent condoms, and fight you if you try to remove their enjoyment of good food (telling them to just calculate IGF manually). The alignment properties you lauded before the capabilities started to generalize, predictably fail to generalize with the capabilities.
Some people I say this to respond with arguments like: "Surely, before a smaller team could get an AGI that can master subjects like biotech and engineering well enough to kill all humans, some other, larger entity such as a state actor will have a somewhat worse AI that can handle biotech and engineering somewhat less well, but in a way that prevents any one AGI from running away with the whole future?"
I respond with arguments like, "In the one real example of intelligence being developed we have to look at, continuous application of natural selection in fact found Homo sapiens sapiens, and the capability-gain curves of the ecosystem for various measurables were in fact sharply kinked by this new species (e.g., using machines, we sharply outperform other animals on well-established metrics such as “airspeed”, “altitude”, and “cargo carrying capacity”)."
Their response in turn is generally some variant of "well, natural selection wasn't optimizing very intelligently" or "maybe humans weren't all that sharply above evolutionary trends" or "maybe the power that let humans beat the rest of the ecosystem was simply the invention of culture, and nothing embedded in our own already-existing culture can beat us" or suchlike.
Rather than arguing further here, I'll just say that failing to believe the hard problem exists is one surefire way to avoid tackling it.
So, flatly summarizing my point instead of arguing for it: it looks to me like there will at some point be some sort of "sharp left turn", as systems start to work really well in domains really far beyond the environments of their training—domains that allow for significant reshaping of the world, in the way that humans reshape the world and chimps don't. And that's where (according to me) things start to get crazy. In particular, I think that once AI capabilities start to generalize in this particular way, it’s predictably the case that the alignment of the system will fail to generalize with it.
This is slightly upstream of a couple other challenges I consider quite core and difficult to avoid, including:
- Directing a capable AGI towards an objective of your choosing.
- Ensuring that the AGI is low-impact, conservative, shutdownable, and otherwise corrigible.
These two problems appear in the strawberry problem, which Eliezer's been pointing at for quite some time: the problem of getting an AI to place two identical (down to the cellular but not molecular level) strawberries on a plate, and then do nothing else. The demand of cellular-level copying forces the AI to be capable; the fact that we can get it to duplicate a strawberry instead of doing some other thing demonstrates our ability to direct it; the fact that it does nothing else indicates that it's corrigible (or really well aligned to a delicate human intuitive notion of inaction).
How is the "capabilities generalize further than alignment" problem upstream of these problems? Suppose that the fictional team OpenMind is training up a variety of AI systems, before one of them takes that sharp left turn. Suppose they've put the AI in lots of different video-game and simulated environments, and they've had good luck training it to pursue an objective that the operators described in English. "I don't know what those MIRI folks were talking about; these systems are easy to direct; simple training suffices", they say. At the same time, they apply various training methods, some simple and some clever, to cause the system to allow itself to be removed from various games by certain "operator-designated" characters in those games, in the name of shutdownability. And they use various techniques to prevent it from stripmining in Minecraft, in the name of low-impact. And they train it on a variety of moral dilemmas, and find that it can be trained to give correct answers to moral questions (such as "in thus-and-such a circumstance, should you poison the operator's opponent?") just as well as it can be trained to give correct answers to any other sort of question. "Well," they say, "this alignment thing sure was easy. I guess we lucked out."
Then, the system takes that sharp left turn, and, predictably, the capabilities quickly improve outside of its training distribution, while the alignment falls apart.
The techniques OpenMind used to train it away from the error where it convinces itself that bad situations are unlikely? Those generalize fine. The techniques you used to train it to allow the operators to shut it down? Those fall apart, and the AGI starts wanting to avoid shutdown, including wanting to deceive you if it’s useful to do so.
Why does alignment fail while capabilities generalize, at least by default and in predictable practice? In large part, because good capabilities form something like an attractor well. (That's one of the reasons to expect intelligent systems to eventually make that sharp left turn if you push them far enough, and it's why natural selection managed to stumble into general intelligence with no understanding, foresight, or steering.)
Many different training scenarios are teaching your AI the same instrumental lessons, about how to think in accurate and useful ways. Furthermore, those lessons are underwritten by a simple logical structure, much like the simple laws of arithmetic that abstractly underwrite a wide variety of empirical arithmetical facts about what happens when you add four people's bags of apples together on a table and then divide the contents among two people.
But that attractor well? It's got a free parameter. And that parameter is what the AGI is optimizing for. And there's no analogously-strong attractor well pulling the AGI's objectives towards your preferred objectives.
The hard left turn? That's your system sliding into the capabilities well. (You don't need to fall all that far to do impressive stuff; humans are better at an enormous variety of relevant skills than chimps, but they aren't all that lawful in an absolute sense.)
There's no analogous alignment well to slide into.
On the contrary, sliding down the capabilities well is liable to break a bunch of your existing alignment properties.
Why? Because things in the capabilities well have instrumental incentives that cut against your alignment patches. Just like how your previous arithmetic errors (such as the pebble sorters on the wrong side of the Great War of 1957) get steamrolled by the development of arithmetic, so too will your attempts to make the AGI low-impact and shutdownable ultimately (by default, and in the absence of technical solutions to core alignment problems) get steamrolled by a system that pits those reflexes / intuitions / much-more-alien-behavioral-patterns against the convergent instrumental incentive to survive the day.
Perhaps this is not convincing; perhaps to convince you we'd need to go deeper into the weeds of the various counterarguments, if you are to be convinced. (Like acknowledging that humans, who can foresee these difficulties and adjust their training procedures accordingly, have a better chance than natural selection did, while then discussing why current proposals do not seem to me to be hopeful.) But hopefully you can at least, in reading this document, develop a basic understanding of my position.
Stating it again, in summary: my position is that capabilities generalize further than alignment (once capabilities start to generalize real well (which is a thing I predict will happen)). And this, by default, ruins your ability to direct the AGI (that has slipped down the capabilities well), and breaks whatever constraints you were hoping would keep it corrigible. And addressing the problem looks like finding some way to either keep your system aligned through that sharp left turn, or render it aligned afterwards.
In an upcoming post (edit: here), I’ll say more about how it looks to me like ~nobody is working on this particular hard problem, by briefly reviewing a variety of current alignment research proposals. In short, I think that the field’s current range of approaches nearly all assume this problem away, or direct their attention elsewhere.
Furthermore, figuring where to aim it looks to me like more of a technical problem than a moral problem. Attempting to manually specify the nature of goodness is a doomed endeavor, of course, but that's fine, because we can instead specify processes for figuring out (the coherent extrapolation of) what humans value. Which still looks prohibitively difficult as a goal to give humanity's first AGI (which I expect to be deployed under significant time pressure), mind you, and I further recommend aiming humanity's first AGI systems at simple limited goals that end the acute risk period and then cede stewardship of the future to some process that can reliably do the "aim minds towards the right thing" thing. So today's alignment problems are a few steps removed from tricky moral questions, on my models.
While we're at it: I think trying to get provable safety guarantees about our AGI systems is silly, and I'm pretty happy to follow Eliezer in calling an AGI "safe" if it has a <50% chance of killing >1B people. Also, I think there's a very large chance of AGI killing us, and I thoroughly disclaim the argument that even if the probability is tiny then we should work on it anyway because the stakes are high.
Note that this is consistent with findings like “large language models perform just as well on moral dilemmas as they perform on non-moral ones”; to find this reassuring is to misunderstand the problem. Chimps have an easier time than squirrels following and learning from human cues. Yet this fact doesn't particularly mean that enhanced chimps are more likely than enhanced squirrels to remove their hunger drives, once they understand inclusive genetic fitness and are able to eat purely for reasons of fitness maximization. Pre-left-turn AIs will get better at various 'alignment' metrics, in ways that I expect to build a false sense of security, without addressing the lurking difficulties.
"What do you mean ‘it takes a sharp left turn’? Are you talking about recursive self-improvement? I thought you said somewhere else that you don't think recursive self-improvement is necessarily going to play a central role before the extinction of humanity?" I'm not talking about recursive self-improvement. That's one way to take a sharp left turn, and it could happen, but note that humans have neither the understanding nor control over their own minds to recursively self-improve, and we outstrip the rest of the animals pretty handily. I'm talking about something more like “intelligence that is general enough to be dangerous”, the sort of thing that humans have and chimps don't.
"Hold on, isn't this unfalsifiable? Aren't you saying that you're going to continue believing that alignment is hard, even as we get evidence that it's easy?" Well, I contend that "GPT can learn to answer moral questions just as well as it can learn to answer other questions" is not much evidence either way about the difficulty of alignment. I'm not saying we'll get evidence that I'll ignore; I'm naming in advance some things that I wouldn't consider negative evidence (partially in hopes that I can refer back to this post when people crow later and request an update). But, yes, my model does have the inconvenient property that people who are skeptical now, are liable to remain skeptical until it's too late, because most of the evidence I expect to give us advance warning about the nature of the problem is evidence that we've already seen. I assure you that I do not consider this property to be convenient.
As for things that could convince me otherwise: technical understanding of intelligence could undermine my "sharp left turn" model. I could also imagine observing some ephemeral hopefully-I'll-know-it-when-I-see-it capabilities thresholds, without any sharp left turns, that might update me. (Short of "full superintelligence without a sharp left turn", which would obviously convince me but comes too late in the game to shift my attention.)
To use my overly-detailed evocative example from earlier: Humans aren't tempted to rewire our own brains so that we stop liking good meals for the sake of good meals, and start eating only insofar as we know we have to eat to reproduce (or, rather, maximize inclusive genetic fitness) (after upgrading the rest of our minds such that that sort of calculation doesn't drag down the rest of the fitness maximization). The cleverer humans are chomping at the bit to have their beliefs be more accurate, but they're not chomping at the bit to replace all these mere-shallow-correlates of inclusive genetic fitness with explicit maximization. So too with other minds, at least by default: that which makes them generally intelligent, does not make them motivated by your objectives.
Thanks for the post, I think it's a useful framing. Two things I'd be interested in understanding better:
As I said in a reply to Eliezer's AGI ruin post:
So I'd be curious to know what you think the biggest disanalogies are between the example of human evolution and building AGI. Relatedly, would you consider raising a child to be a "real example of intelligence being developed"; why or why not?
Granting that there's a bunch of logical structure around how to think in accurate ways (e.g. solving scientific problems), and there's a bunch of logical structure around how to pursue goals coherently (e.g. avoiding shutdown) what's the strongest reason to believe that agents won't learn something closely approximating the former before they learn something closely approximating the latter? My impression of Eliezer's position is that it's because they're basically the same structure - if you agree with this, I'd be curious what sort of intuitions or theorems are most responsible for this belief.
(Another way of phrasing this question: suppose I made an analogous argument before the industrial revolution, saying something like "matter and energy are fundamentally the same thing at a deep level, we'll soon be able to harness superhuman amounts of energy, therefore we're soon going to be able to create superhuman amounts of matter". Yet in fact, while the premise of mass-energy equivalence is true, the constants are such that it takes stupendously more energy than humans can generate, in order to produce human-sized piles of matter. What's the main thing that makes you think that the constants in the intelligence case are such that AIs will converge to goal-coherence before, or around the same time as, superhuman scientific capabilities?)
I want to outline how my research programme attempts to address this core difficulty.
First, like I noted before, evolution is not a perfect analogy for AI. This is because evolution is directly selecting the policy, whereas a (model-based) AI system is separately selecting (i) a world-model (ii) a reward function and (iii) a plan (policy) based on i+ii. This inherently produces better generalization-of-alignment (but not nearly enough to solve the problem).
With iii, we have the least generalization problems, because we are not limited by training data: the AI can use the world-model to test the plan in any scenario, limited only by computing resources.
With ii, we have ample generalization problems because (a) the true reward function we are trying to convey to the AI is complex and (b) the data-points we do have might contain systematic errors. The MIRI approach to addressing this is (1) focusing on a relatively narrow task (like the strawberry problem) and (2) somehow add corrigibility. This approach is difficult because "corrigibility" is not a terribly natural property, and AFAICT it's ill-defined even pretheoretically. Instead, I propose to address this by directly learning the user's preferences, a path that MIRI believes to be harder (but I believe to be easier).
Since the user is an "arbitrary" system from the AI's perspective, in order to learn the user's preferences we need to understand how to assign agentic interpretations to arbitrary systems (the "intentional stance"), with the understanding that these interpretations are only meaningful to the extent the system is actually an agent (a rock has no sensible agentic interpretation). This seems to me as a natural problem, and indeed there is a line of attack using algorithmic information theory: 1 2.
However, having a well-grounded method of assigning utility functions to policies or programs is, in itself, insufficient. This is because (a) we still need the AI to learn the user's policy/program and (b) we need to avoid allowing the AI to choose a convenient utility function by modifying the user or hacking the channel through which the information is received. To solve this, I propose to use certain tools provided by the infra-Bayesian physicalism (IBP) framework. Specifically, IBP allows formally specifying the notion of "which programs run in the universe". The user is then one such program, and the remaining problem is how to select it among other problems, which seems tractable by establishing a certain "handshake" protocol. Moreover, the AI only considers the past behavior of the user, so it's impossible for the AI to "cheat" as in 'b' above.
Finally, we need to deal with the generalization of i. At first glance, this should be easier since (a) the true world-model should have low description complexity, implying easy generalization and (b) any false world-model is falsifiable by reality itself, without extra offer on our part. However, from the perspective of a Cartesian agent the world is actually high complexity (because of the need for bridge rules), undermining 'a'. [EDIT: Moreover, a false world-model can be erroneous at only a few special places, s.t. there are only a few mistakes but their impact is large.] The resulting failures can take the form of malign agents inside the world-model itself.
Here again IBP comes to the rescue, giving the agent an epistemology that requires no bridge rules. [EDIT: And, since the agent holds an unprivileged position in the universe, it leaves much less room for simple-to-describe false world-models that only make different predictions for very special situations.] This doesn't solve all problems entirely, and in particular the agent can still develop malign simulation hypotheses, although (as opposed to Cartesian agents), these malign hypotheses no longer have an overwhelming advantage in probability mass. To address this, I propose designing a filtering mechanism which discards such hypotheses (roughly speaking, it makes the AI disbelieve any hypothesis that involves a powerful / unhumanlike creator, formalized using IBP tools). It is currently an open problem to demonstrate that this is a complete solution for world-model generalization / inner alignment (or augment it if it isn't), but it does not seem intractable.
I expect a lot of the details to continue to change in the future, as more layers of the math become revealed, but I'm pretty confident in the ability this style of research to guide us onto the right path, eventually.
More precisely, the part of the user's subjective timeline which is outside the AI's logical-causal future, as can be specified in IBP. ↩︎
Where by "behavior" I mean the computation producing this behavior, rather than just the result of this computation. ↩︎
Huh? Evolution did not directly select over human policy decisions. Evolution specified brains, which do within-lifetime learning and therefore learn different policies given different upbringings, and e.g. learning rate mutations indirectly leads to statistical differences in human learned policies. Evolution probably specifies some reward circuitry, the learning architecture, the broad-strokes learning processes (self-supervised predictive + RL), and some other factors, from which the policy is produced.
The IGF->human values analogy is indeed relevantly misleading IMO, but not for this reason.
When I say "policy", I mean the entire behavior including the learning algorithm, not some asymptotic behavior the system is converging to. Obviously, the policy is represented as genetic code, not as individual decisions. When I say "evolution is directly selecting the policy", I mean that genotypes are selected based on their "expected reward" (reproductive fitness) rather than e.g. by evaluating the accuracy of the world-models those minds produce. And, genotypes are not a priori constrained to be learning algorithms with particular architectures, that's something the outer loop has to learn.
Evolution is not even model-free RL, since in MFRL we train a network to estimate the value function or the Q-function of different states, we don't just GD on the expected reward. But, MFRL does have the problem of extrapolating the reward function incorrectly away from the training data. ↩︎
This analogy gets brought out a lot, but has anyone actually spelled it out explicitly? Because it's not clear to me that it holds if you try to explicitly work out the argument.
In particular, I don't quite understand what it would mean for evolution to optimize the species for fitness, given that fitness is defined as a measure of reproductive success within the species. A genotype has a high fitness, if it tends to increase in frequency relative to other genotypes in that species.
To be more precise, there is a measure of "absolute fitness" that refers to a specific genotype's success from one generation to the next: if a genotype has 100 individuals in one generation and 80 individuals in the next generation, then it has an absolute fitness of 0.8. But AFAIK evolutionary biology generally focuses on relative fitness - on how well a genotype performs relative to others in the species. If genotype A has an absolute fitness of 1.2 and genotype B has an absolute fitness of 1.5, then genotype B will tend to become more common than A, even though both have fitness > 1.
Quoting from this Nature Reviews Genetics article:
Going with our previous example, genotype A would have a fitness of 0.8 and genotype B would have a fitness of 1.
The most natural interpretation of the "fitness of the species" would be as the mean relative fitness of the species:
However, it seems to me that - given that the mean relative fitness is defined by reference to the trait with the highest fitness within the genotype, that implies that the definition of the mean relative fitness changes over time. If the highest-fitness trait changes over time - because the environment changes (due to changes in the climate, other species, etc.), or because of the emergence of a new trait - then the mean relative fitness of the species also changes. The species might also be spread across different regions, with the same trait having different fitness in different regions:
The paper does note that one can define alternative definitions of fitness under which the fundamental theorem does hold, but that the "relevant literature is forbidding". The general takeaway that I would draw from this is that fitness is not the kind of clear-cut, "carves reality at joints" kind of a measure that evolution would directly optimize in a similar kind of sense as you directly optimize, say, the amount of correct classifications that a neural net gets on MNIST.
Rather it's a theoretical fiction or an abstract measure that can be defined in different ways, and which is defined in different ways in different contexts, depending on what kind of an aim one wants to achieve. But that's a simplifying interpretation imposed on complex process for the purpose of modeling it, rather than something that the process actually has an explicit optimization target. So there are ways in which you could view evolution as if it was optimizing for something, but it's not clear to me that it can be said to actually be optimizing for anything in particular - at least not in the sense in which we talk about a machine learning system being optimized for a particular goal.
Somewhat relevant comment thread
Ronny Fernandez on Twitter:
Nate's follow-up post is now up: On how various plans miss the hard bits of the alignment challenge.
Let T be the target objective we wish to align the system towards. In this paragraph, T is duplicating the strawberry (and doing nothing else). I seriously doubt that alignment is comparably difficult for all objectives T, or even all "reasonable" objectives. I think building an AGI which solves the strawberry problem is far harder than building an AGI which makes lots of dogs in the future. I think that a diamond maximizer is also harder to train than an AGI which makes lots of dogs, but an AGI which makes lots of diamonds is probably only a little harder than an AGI which makes lots of dogs.
(I haven't explained why I hold these beliefs, but I figured it would be productive to at least note this axis of disagreement.)
When I think about the strawberry problem, it seems unnatural, and perhaps misleading of our attention, since there's no guarantee there's even a reasonable solution. We'd probably be better off thinking about how to make AGIs which care about dogs, because it's an empirical fact that there's a way to align intelligences to that objective.
Why would there not be a solution?
To clarify, I said there might not be a reasonable solution (i.e. such that solving the strawberry problem isn't significantly harder than solving pivotal-act alignment).
Not directly answering your Q, but here's why it seems unnatural and maybe misleading-of-attention. Copied from a Slack message I sent:
Corrigibility is a repeller. Human values aren't a repeller, but they're a very narrow target to hit.
In the sense of moving a system towards many possible goals? But I think in a more appropriate space (where the aiming should take place) it's again an attractor. Corrigibility is not a goal, a corrigible system doesn't necessarily have any well-defined goals, traditional goal-directed agents can't be corrigible in a robust way, and it should be possible to use it for corrigibility towards corrigibility, making this aspect stronger if that's what the operators work towards happening.
More generally, non-agentic aspects of behavior can systematically reinforce non-agentic character of each other, preventing any opposing convergent drives (including the drive towards agency) from manifesting if they've been set up to do so. Sufficient intelligence/planning advantage pushes this past exploitability hazards, repelling selection theorems, even as some of the non-agentic behaviors might be about maintaining specific forms of exploitability.
I'm starting to doubt that there are strategically important human-specific objectives in the decision theory sense, things that should be used to actually optimize everything without goodharting making it counterproductive. In this hypothesis, optimization goals are not just hard to figure out, but there is almost nothing there that's human-specific, human preference is generic. Orthogonality thesis applies to agents with goals, but maybe it doesn't apply to humans, because their goals play a different role from what orthogonality thesis needs. To solve astronomical waste, humans could run their civilization on better substrate and look for goal-shaped principles that can be propagated more efficiently than civilization itself, used for optimization, but these principles are not going to be human-specific.
If an AGI is in a similar situation (doesn't have non-goodharting goals), it's going to be in the same attractor as humans, motivated to build a generic civilization. It doesn't necessarily involve humans or human-specific things, but I'm not sure this is different from a specific human deciding that their civilization doesn't involve other humans, which a priori seems like an unjustifiably privileged aspect of civilizational design.
In other words, applicability of orthogonality thesis might fail if the kind of goal knowledge relevant to it (that overcomes goodharting) tends to get obtained in convergent ways that give results that are generic, not human-specific. The disagreement of this hypothesis with the standard position is about the distinction/interaction between non-goodharting and goodharting goals. On the generic goals hypothesis, most accidental goals, including those currently held by humans, are goodharting goals (according to their role in the minds of people, not to their content), something that shouldn't be used to strongly optimize the world in anything close to their current form. And the proper way of getting appropriate non-goodharting goals (running a civilization/long reflection/CEV) somehow doesn't importantly depend on the currently held goodharting goals (this seems to be the crux).
So in this view, the dangerous AGIs are those that hold any goals in a non-goodharting role, ready to optimize the world according to them, while by default AGIs with more vague architectures are going to face the same problem of formulating non-goodharting goals as humans, and work within the same attractor for arriving at its solution. A better but not drastically different outcome is AGIs that hold human goodharting goals in a goodharting role and no goals in a non-goodharting role, so that they are even more likely to go about formulating non-goodharting goals in the same way humans would, without being opposed to actual humans in the process. Language models might help with this part.
(We can use these terms to restate the familiar catastrophic failure of alignment where an AGI is aligned to hold human goodharting goals (what we currently care about) in a non-goodharting role (as a target for optimizing the world with) without giving civilization the opportunity to improve on those goals and without limiting their applicability to situations comprehensible to current humans. A failure of non-goodharting (optimizing too much on goodharting goals), resulting in a failure of corrigibility (preventing the non-goodharting extrapolated volition from eventually being in charge).)
In my own experience examining the foundations of things in the world, I have repeatedly found there to be less of an attractor-of-fundamentally-effective-decision-making than I had anticipated. In every way that I expected to find such an attractor within epistemology, mathematics, empiricism, ethics, I found in fact that even the very basic assumptions that I started with were unfounded, and found nothing firm to replace with them with. Probability theory: not a fundamental answer to epistemology; proof-based agents: deeply paradoxical and seemingly untrustworthy; the scientific method: not precise enough to be a final answer to anything; consequentialism: what actually is it? I have the sense that you've seen just as much of this phenomenon as I have, but you still seem to hold this conviction that there is a deep well of fundamental reasonability for an AI to fall into. Why? I'm just suggesting that the existence of this well is non-trivial feature of reality, and the more we fail to find it, the more we might question whether it exists.
Individual humans can't FOOM (at lest not yet), but humanity did.
My best guess is that humanity took a sharp left turn when we got a general enough language, and then again when we got writing, and possibly again when the skill of reading an writing spread to a majority of the population.
Before language human intelligence was basically limited to what a single brain could do. When we got language we got the ability of adding compute (more humans) to the same problem solving task. Humanity got parallel computing. This extra capabilities could be used to invent things to increase the population, i.e. recusing self improvement.
Later, writing gave us external memory. Before our computations where limited by human memory, but now we could start to fill up libraries, unlocking a new level of recursive self improvement.
Every increase in literacy and communication technology (e.g. the internet) is humanity upgrading its capability.
It sounds like you don't want to argue this point further here, but I would like to point something very simple out that I think your argument here glosses over.
Humanity is a species, not an individual. It wasn't the case that a single animal arose among all the others, and out-competed everyone else. Instead, it was a large set of entities that collectively out-competed all the other animals. And I think this distinction is quite important to make.
If you think that an analogy to human evolution is critical to understanding our epistemic situation, it appears to me that the evolutionary analogy should force you to draw the opposite conclusion from the one you have drawn here (relative to credible people who disagree).
In my understanding of our situation, the conclusion to draw from human evolution is that a single species can acquire a host of very powerful technologies, and tower above everyone else, in a relatively short period of time. That is, we should predict that, in the future, a collection of AIs could eventually out-match humanity.
But you're not arguing that thesis! (At least, as I understand your argument) You're arguing that the evolutionary analogy shows that a single individual can outcompete everyone else. And I don't know where that idea is coming from.