There were no continuous language model scaling laws before the transformer architecture

https://arxiv.org/abs/1712.00409 was technically published half a year after transformers, but it shows power-law language model scaling laws for LSTMs (several years before the Kaplan et al. paper, and without citing the transformer paper). It's possible that transformer scaling laws are much better, I haven't checked (and perhaps more importantly, transformer training lets you parallelize across tokens), just mentioning this because it seems relevant for the overall discussion of continuity in research.

I also agree with Thomas Kwa's sibling comment that transformers weren't a single huge step. Fully-connected neural networks seem like a very strange comparison to make, I think the interesting question is whether transformers were a sudden single step relative to LSTMs. But I'd disagree even with that: Attention was introduced three years before transformers and was a big deal for machine translation. Self-attention was introduced somewhere between the first attention papers and transformers. And the transformer paper itself isn't atomic, it consists of multiple ideas—replacing RNNs/LSTMs with self-attention is clearly the big one, but my impression is that multi-head attention, scaled dot product attention, and the specific architecture were pretty important to actually get their impressive results.

To be clear, I agree that there are sometimes new technologies that are very different from the previous state of the art, but I think it's a very relevant question just how common this is, in particular within AI. IMO the most recent great example is neural machine translation (NMT) replacing complex hand-designed systems starting in 2014---NMT worked very differently than the previous best machine translation systems, and surpassed them very quickly (by 2014 standards for "quick"). I expect something like this to happen again eventually, but it seems important to note that this was 10 years ago, and how much progress has been driven since then by many different innovations (+ scaling).

ETA: maybe a crux is just how impressive progress over the past 10 years has been, and what it would look like to have "equivalent" progress before the next big shift. But I feel like in that case, you wouldn't count transformers as a big important step either? My main claim here is that to the extent to which there's been meaningful progress over the past 10 years, it was mostly driven by a large set of small-ish improvements, and gradual shifts of the paradigm.

Yeah. I think there's a broader phenomenon where it's way harder to learn from other people's mistakes than from your own. E.g. see my first bullet point on being too attached to a cool idea. Obviously, I knew in theory that this was a common failure mode (from the Sequences/LW and from common research advice), and someone even told me I might be making the mistake in this specific instance. But my experience up until that point had been that most of the research ideas I'd been similarly excited about ended up ~working (or at least the ones I put serious time into).

Some heuristics (not hard rules):

• ~All code should start as a hacky jupyter notebook (like your first point)
• As my codebase grows larger and messier, I usually hit a point where it becomes more aversive to work with because I don't know where things are, there's too much duplication, etc. Refactor at that point.
• When refactoring, don't add abstractions just because they might become useful in the future. (You still want to think about future plans somewhat of course, maybe the heuristic is to not write code that's much more verbose than necessary right now, in the hope that it will pay off in the future.)

These are probably geared toward people like me who tend to over-engineer; someone who's currently unhappy that their code is always a mess might need different ones.

I don't know whether functional programming is fundamentally better in this respect than object-oriented.

Research mistakes I made over the last 2 years.

Listing these in part so that I hopefully learn from them, but also because I think some of these are common among junior researchers, so maybe it's helpful for someone else.

• I had an idea I liked and stayed attached to it too heavily.
  • (The idea is using abstractions of computation for mechanistic anomaly detection. I still think there could be something there, but I wasted a lot of time on it.)
  • What I should have done was focus more on simpler baselines, and be more scared when I couldn't beat those simple baselines.
  • (By "simpler baselines," I don't just mean comparing against what other people are using, I also mean ablations where you remove some parts of the method and see if it still works.)
  • Notably, several researchers I respect told me I shouldn't be too attached to that idea and should consider using simpler methods.
• I was too focused initially on growing the field of empirical mechanistic anomaly detection; I should have just tried to get interesting results first.
• Relatedly, I spent too much time making a nice library for mechanistic anomaly detection (though in part this was for my own use, not just because of field-building).
  • Apart from being a time sink, this also had bad effects on my research prioritization. It nudged me toward doing experiments that were easy to do with the library or that would be natural additions to the library when implemented. It made it aversive to do experiments that wouldn't fit naturally into the library at all.
  • It also made fast iteration more difficult, because I'd often be tempted to quickly integrate some new method/tool into the library instead of doing a hacky version first.
  • I do still think clean research code and infrastructure are really valuable, so this is difficult to balance. Consider reversing advice especially on this point.
• I worked on purely conceptual/theoretical work without collaborators or good mentorship, and with only ~2.5 years of research experience. I expected beforehand that I'd be unusually good at this type of research (and I still think that's plausibly true), but even so, I don't think it was time well spent in expectation.
  • I'm very sympathetic to this kind of work being important. But I think it's really brutal (and won't work) without at least one (and ideally more) of (1) strong collaborators and ideally mentors, (2) good empirical feedback loops, (3) a lot of research experience. Maybe there are a small handful of junior researchers who can do useful things there on their own, but I've been growing more and more skeptical.
• I looked into related work too late several times, and didn't think about how my work was going to be different early enough.
  • Drafting a paper outline was great for making me confront that question (and is also a useful exercise for noticing other mistakes).
• I didn't work on control. I was convinced that control was great pretty quickly, and then ... assumed that everyone else would also be convinced and lots of people would switch to working on it, and it would end up being non-neglected. This sounds really silly in hindsight, and I suspect I was also doing motivated reasoning to avoid changing my research.
  • "Working on control" is a messy concept. Mechanistic anomaly detection (which I was working on) seems at least as applicable to control as to alignment. But what I mean by "working on control" includes an associated cluster of research taste aesthetics, such as pessimistic assumptions about inductive biases, meta-level adversarial evals, and thinking about the best protocols a blue team could use given clearly specified (and realistic) rules. I think I've been slowly moving closer toward that cluster, but could have gotten there sooner by making a deliberate sudden switch.
  • I didn't explicitly realize how "working on control" has this research taste cluster associated with it until more recently, otherwise the "everyone will work on it" argument would've had less force anyway.

2 years ago, you wrote:

theoretical progress has been considerably faster than expected, while crossing the theory-practice gap has been mildly slower than expected. (Note that “theory progressing faster than expected, practice slower” is a potential red flag for theory coming decoupled from reality, though in this case the difference from expectations is small enough that I’m not too worried. Yet.)

I don't know how much the difficulty of crossing the theory-practice gap has deviated from your expectations since then. But I would indeed be worried that a lot of the difficulty is going to be in getting any good results for deep learning, and that finding additional theoretical/conceptual results in other settings doesn't constitute much progress on that. (But kudos for apparently working on image generator nets again!)

As a sidenote, your update from 2 years ago also mentioned:

I tried to calculate “local” natural abstractions (in a certain sense) in a generative image net, and that worked quite well.

I assume that was some other type of experiment involving image generators? (and the notion of "working well" there isn't directly comparable to what you tried now?)

I think this was a very good summary/distillation and a good critique of work on natural abstractions; I'm less sure it has been particularly useful or impactful.

I'm quite proud of our breakdown into key claims; I think it's much clearer than any previous writing (and in particular makes it easier to notice which sub-claims are obviously true, which are daring, which are or aren't supported by theorems, ...). It also seems that John was mostly on board with it.

I still stand by our critiques. I think the gaps we point out are important and might not be obvious to readers at first. That said, I regret somewhat that we didn't focus more on communicating an overall feeling about work on natural abstractions, and our core disagreements. I had some brief back-and-forth with John in the comments, where it seemed like we didn't even disagree that much, but at the same time, I still think John's writing about the agenda was wildly more optimistic than my views, and I don't think we made that crisp enough.

My impression is that natural abstractions are discussed much less than they were when we wrote the post (and this is the main reason why I think the usefulness of our post has been limited). An important part of the reason I wanted to write this was that many junior AI safety researchers or people getting into AI safety research seemed excited about John's research on natural abstractions, but I felt that some of them had a rosy picture of how much progress there'd been/how promising the direction was. So writing a summary of the current status combined with a critique made a lot of sense, to both let others form an accurate picture of the agenda's progress while also making it easier for them to get started if they wanted to work on it. Since there's (I think) less attention on natural abstractions now, it's unsurprising that those goals are less important.

As for why there's been less focus on natural abstractions, my guess is a combination of at least:

• John has been writing somewhat less about it than during his peak-NAH-writing.
• Other directions have gotten off the ground and have captured a lot of excitement (e.g. evals, control, and model organisms).
• John isn't mentoring for MATS anymore, so junior researchers don't get exposure to his ideas through that.

It's also possible that many became more pessimistic about the agenda without public fanfare, or maybe my impression of relative popularity now vs then is just off.

I still think very high effort distillations and critiques can be a very good use of time (and writing this one still seems reasonable ex ante, though I'd focus more on nailing a few key points and less on being super comprehensive).

One more: It seems plausible to me that the alignment stress-testing team won't really challenge core beliefs that underly Anthropic's strategy.

For example, Sleeper Agents showed that standard finetuning might not suffice given a scheming model, but Anthropic had already been pretty invested in interp anyway (and I think you and probably others had been planning for methods other than standard finetuning to be needed). Simple probes can catch sleeper agents (I'm not sure whether I should think of this as work by the stress-testing team?) then showed positive results using model internals methods, which I think probably don't hold up to stress-testing in the sense of somewhat adversarial model organisms.

Examples of things that I'd count as "challenge core beliefs that underly Anthropic's strategy":

• Demonstrating serious limitations of SAEs or current mech interp (e.g., for dealing with model organisms of scheming)
• Demonstrate issues with hopes related to automated alignment research (maybe model organisms of subtle mistakes in research that seriously affect results but are systematically hard to catch)

To be clear, I think the work by the stress-testing team so far has been really great (mainly for demonstrating issues to people outside Anthropic), I definitely wouldn't want that to stop! Just highlighting a part that I'm not yet sure will be covered.

• I think Anthropic might be "all in" on its RSP and formal affirmative safety cases too much and might do better to diversify safety approaches a bit. (I might have a wrong impression of how much you're already doing/considering these.)
  • In addition to affirmative safety cases that are critiqued by a red team, the red team should make proactive "risk cases" that the blue team can argue against (to avoid always letting the blue team set the overall framework, which might make certain considerations harder to notice).
  • A worry I have about RSPs/safety cases: we might not know how to make safety cases that bound risk to acceptable levels, but that might not be enough to get labs to stop, and labs also don't want to publicly (or even internally) say things like "5% that this specific deployment kills everyone, but we think inaction risk is even higher." If labs still want/need to make safety cases with numeric risk thresholds in that world, there'll be a lot of pressure to make bad safety cases that vastly underestimate risk. This could lead to much worse decisions than being very open about the high level of risk (at least internally) and trying to reduce it as much as possible. You could mitigate this by having an RSP that's more flexible/lax but then you also lose key advantages of an RSP (e.g., passing the LeCun test becomes harder).
  • Mitigations could subjectively reduce risk by some amount, while being hard to quantify or otherwise hard to use for meeting the requirements from an RSP (depending on the specifics of that RSP). If the RSP is the main mechanism by which decisions get made, there's no incentive to use those mitigations. It's worth trying to make a good RSP that suffers from this as little as possible, but I think it's also important to set up decision making processes such that these "fuzzy" mitigations are considered seriously, even if they don't contribute to a safety case.
  • My sense is that Anthropic's RSP is also meant to heavily shape research (i.e., do research that directly feeds into being able to satisfy the RSP). I think this tends to undervalue exploratory/speculative research (though I'm not sure whether this currently happens to an extent I'd disagree with).
  • In addition to a formal RSP, I think an informal culture inside the company that rewards things like pointing out speculative risks or issues with a safety case/mitigation, being careful, ... is very important. You can probably do things to foster that intentionally (and/or if you are doing interesting things, it might be worth writing about them publicly).
• Given Anthropic's large effects on the safety ecosystem as a whole, I think Anthropic should consider doing things to diversify safety work more (or avoid things that concentrate work into a few topics). Apart from directly absorbing a lot of the top full-time talent (and a significant chunk of MATS scholars), there are indirect effects. For example, people want to get hired at big labs, so they work on stuff labs are working on; and Anthropic has a lot of visibility, so people hear about Anthropic's research a lot and that shapes their mental picture of what the field considers important.
  • As one example, it might make sense for Anthropic to make a heavy bet on mech interp, and SAEs specifically, if they were the only ones doing so; but in practice, this ended up causing a ton of others to work on those things too. This was by no means only due to Anthropic's work, and I also realize it's tricky to take into account these systemic effects on top of normal research prioritization. But I do think the field would currently benefit from a little more diversity, and Anthropic would be well-placed to support that. (E.g. by doing more different things yourself, or funding things, or giving model access.)
• Indirectly support third-party orgs that can adjudicate safety cases or do other forms of auditing, see Ryan Greenblatt's thoughts:

I think there are things Anthropic could do that would help considerably. This could include:

• Actively encouraging prospective employees to start or join third-party organizations rather than join Anthropic in cases where the employee might be interested in this and this could be a reasonable fit.
• Better model access (either for anyone, just researchers, or just organizations with aspirations to become adjudicators)
• Higher levels of certain types of transparency (e.g. being more transparent about the exact details of safety cases, open-sourcing evals (probably you just want to provide random IID subsets of the eval or to share high-level details and then share the exact implementation on request)).

I'm not sure exactly what is good here, but I don't think Anthropic is as limited as you suggest.

Interesting, thanks! My guess is this doesn't include benefits like housing and travel costs? Some of these programs pay for those while others don't, which I think is a non-trivial difference (especially for the bay area)

I think different types of safety research have pretty different effects on concentration of power risk.

As others have mentioned, if the alternative to human concentration of power is AI takeover, that's hardly an improvement. So I think the main ways in which proliferating AI safety research could be bad are:

1. "Safety" research might be more helpful for letting humans use AIs to concentrate power than they are for preventing AI takeover.
2. Actors who want to build AIs to grab power might also be worried about AI takeover, and if good(-seeming) safety techniques are available, they might be less worried about that and are more likely to go ahead with building those AIs.

There are interesting discussions to be had on the extent to which these issues apply. But it seems clearer that they apply to pretty different extents depending on the type of safety research. For example:

• Work trying to demonstrate risks from AI doesn't seem very worrisome on either 1. or 2. (and in fact, should have the opposite effect of 2. if anything).
• AI control (as opposed to alignment) seems comparatively unproblematic IMO: it's less of an issue for 1., and while 2. could apply in principle, I expect the default to be that many actors won't be worried enough about scheming to slow down much even if there were no control techniques. (The main exception are worlds in which we get extremely obvious evidence of scheming.)

To be clear, I do agree this is a very important problem, and I thought this post had interesting perspectives on it!