It seems you’d largely agree with that characterization?
Yes. My only hesitation is about how real-life-important it’s for AIs to be able to do math for which very-little-to-no training data exists. The internet and the mathematical literature is so vast that, unless you are doing something truly novel, there’s some relevant subfield there—in which case FrontierMath-style benchmarks would be informative of capability to do real math research.
Also, re-reading Wentworth’s original comment, I note that o1 is weak according to FM. Maybe the things Wentworth is doing are just too hard for o1, rather than (just) overfitting-on-benchmarks style issues? In any case his frustration with o1′s math skills doesn’t mean that FM isn’t measuring real math research capability.
The internet and the mathematical literature is so vast that, unless you are doing something truly novel, there’s some relevant subfield there
Previously, I’d intuitively assumed the same as well: that it doesn’t matter if LLMs can’t “genuinely research/innovate”, because there is enough potential for innovative-yet-trivial combination of existing ideas that they’d still massively speed up R&D by finding those combinations. (“Innovation overhang”, as @Nathan Helm-Burger puts it here.)
Back in early 2023, I’d considered it fairly plausible that the world would start heating up in 1-2 years due to such synthetically-generated innovations.
Except this… just doesn’t seem to be happening? I’m yet to hear of a single useful scientific paper or other meaningful innovation that was spearheaded by a LLM.[1] And they’re already adept at comprehending such innovative-yet-trivial combinations if a human prompts them with those combinations. So it’s not the matter of not yet being able to understand or appreciate the importance of such synergies. (If Sonnet 3.5.1 or o1 pro didn’t do it, I doubt o3 would.)
Yet this is still not happening. My guess is that “innovative-yet-trivial combinations of existing ideas” are not actually “trivial”, and LLMs can’t do that for the same reasons they can’t do “genuine research” (whatever those reasons are).
Admittedly it’s possible that this is totally happening all over the place and people are just covering it up in order to have all of the glory/status for themselves. But I doubt it: there are enough remarkably selfless LLM enthusiasts that if this were happening, I’d expect it would’ve gone viral already.
It’s only now that LLMs are reasonably competent in at least some hard problems, and at any rate, I expect RL to basically solve the domain, because of verifiability properties combined with quite a bit of training data.
We should wait a few years, as we have another scale-up that’s coming up, and it will probably be quite a jump from current AI due to more compute:
It’s only now that LLMs are reasonably competent in at least some hard problems
I don’t think that’s the limiter here. Reports in the style of “my unpublished PhD thesis was about doing X using Y methodology, I asked an LLM to do that and it one-shot a year of my work! the equations it derived are correct!” have been around for quite a while. I recall it at least in relation to Claude 3, and more recently, o1-preview.
If LLMs are prompted to combine two ideas, they’ve been perfectly capable of “innovating” for ages now, including at fairly high levels of expertise. I’m sure there’s some sort of cross-disciplinary GPQA-like benchmark that they’ve saturated a while ago, so this is even legible.
The trick is picking which ideas to combine/in what direction to dig. This doesn’t appear to be something LLMs are capable of doing well on their own, nor do they seem to speed up human performance on this task. (All cases of them succeeding at it so far have been, by definition, “searching under the streetlight”: checking whether they can appreciate a new idea that a human already found on their own and evaluated as useful.)
I suppose it’s possible that o3 or its successors change that (the previous benchmarks weren’t measuring that, but surely FrontierMath does...). We’ll see.
I expect RL to basically solve the domain
Mm, I think it’s still up in the air whether even the o-series efficiently scales (as in, without requiring a Dyson Swarm’s worth of compute) to beating the Millennium Prize Eval (or some less legendary yet still major problems).
I expect such problems don’t pass the “can this problem be solved by plugging the extant crystallized-intelligence skills of a number of people into each other in a non-contrived[1] way?” test. Does RL training allow to sidestep this, letting the model generate new crystallized-intelligence skills?
I’m not confident one way or another.
we have another scale-up that’s coming up
I’m bearish on that. I expect GPT-4 to GPT-5 to be palatably less of a jump than GPT-3 to GPT-4, same way GPT-3 to GPT-4 was less of a jump than GPT-2 to GPT-3. I’m sure it’d show lower loss, and saturate some more benchmarks, and perhaps an o-series model based on it clears FrontierMath, and perhaps programmers and mathematicians would be able to use it in an ever-so-bigger number of cases...
But I predict, with low-moderate confidence, that it still won’t kick off a deluge of synthetically derived innovations. It’d have even more breadth and eye for nuance, but somehow, perplexingly, still no ability to use those capabilities autonomously.
“Non-contrived” because technically, any cognitive skill is just a combination of e. g. NAND gates, since those are Turing-complete. But obviously that doesn’t mean any such skill is accessible if you’ve learned the NAND gate. Intuitively, a combination of crystallized-intelligence skills is only accessible if the idea of combining them is itself a crystallized-intelligence skill (e. g., in the math case, a known ansatz).
Which perhaps sheds some light on why LLMs can’t innovate even via trivial ideas combinations. If a given idea-combination “template” weren’t present in the training data, the LLM can’t reliably independently conceive of it except by brute-force enumeration...? This doesn’t seem quite right, but maybe in the right direction.
I think my key crux is that in domains where there is a way to verify that the solution actually works, RL can scale to superhuman performance, and mathematics/programming are domains that are unusually easy to verify/gather training data for RL performance, so with caveats it can become rather good at those specific domains/benchmarks like millennium prize evals, but the important caveat is I don’t believe this transfers very well to domains where verifying isn’t easy, like creative writing.
I’m bearish on that. I expect GPT-4 to GPT-5 to be palatably less of a jump than GPT-3 to GPT-4, same way GPT-3 to GPT-4 was less of a jump than GPT-2 to GPT-3. I’m sure it’d show lower loss, and saturate some more benchmarks, and perhaps an o-series model based on it clears FrontierMath, and perhaps programmers and mathematicians would be able to use it in an ever-so-bigger number of cases...
I was talking about the 1 GW systems that would be developed in late 2026-early 2027, not GPT-5.
in domains where there is a way to verify that the solution actually works, RL can scale to superhuman performance
Sure, the theory on that is solid. But how efficiently does it scale off-distribution, in practice?
The inference-time scaling laws, much like the pretraining scaling laws, are ultimately based on test sets whose entries are “shallow” (in the previously discussed sense). It doesn’t tell us much regarding how well the technique scales with the “conceptual depth” of a problem.
o3 took a million dollars in inference-time compute and unknown amounts in training-time compute just to solve the “easy” part of the FrontierMath benchmark (which likely take human experts single-digit hours, maybe <1 hour for particularly skilled humans). How much would be needed for beating the “hard” subset of FrontierMath? How much more still would be needed for problems that take individual researchers days; or problems that take entire math departments months; or problems that take entire fields decades?
It’s possible that the “synthetic data flywheel” works so well that the amount of human-researcher-hour-equivalents per unit of compute scales, say, exponentially with some aspect of o-series’ training, and so o6 in 2027 solves the Riemann Hypothesis.
Or it scales not that well, and o6 can barely clear real-life equivalents of hard FrontierMath problems. Perhaps instead the training costs (generating all the CoT trees on which RL training is then done) scale exponentially, while researcher-hour-equivalents per compute units scale linearly.
It doesn’t seem to me that we know which one it is yet. Do we?
I think a different phenomenon is occuring. My guess, updating on my own experience, is that ideas aren’t the current bottleneck. 1% inspiration, 99% perspiration.
As someone who has been reading 3-20 papers per month for many years now, in neuroscience and machine learning, I feel overwhelmed with ideas. I average about 0.75 per paper. I write them down, and the lists grow faster than they shrink by two orders of magnitude.
When I was on my favorite industry team, what I most valued about my technical manager was his ability to help me sort through and prioritize them. It was like I created a bunch of LEGO pieces, he picked one to be next, I put it in place by coding it up, he checked the placement by reviewing my PR. If someone has offered me a source of ideas ranging in quality between worse than my worst ideas, and almost as good as my best ideas, and skewed towards bad… I’d have laughed and turned them down without a second thought.
For something like a paper instead of a minor tech idea for 1 week PR… The situation is far more intense. The grunt work of running the experiments and preparing the paper is enormous compared to the time and effort of coming up with the idea in the first place. More like 0.1% to 99.9%.
Current LLMs can speed up creating a paper if given the results and experiment description to write about. That’s probably also not the primary bottleneck (although still more than idea generation).
So the current bottleneck, in my estimation, for ml experiments, is the experiments. Coding up the experiments accurately and efficiently, running them (and handling the compute costs), analyzing the results.
So I’ve been expecting to see an acceleration dependent on that aspect. That’s hard to measure though. Are LLMs currently speeding this work up a little? Probably. I’ve had my work sped up some by the recent Sonnet 3.5.1. Currently though it’s a trade-off, there’s overhead in checking for misinterpretations and correcting bugs. We still seem a long way in “capability space” from me being able to give a background paper and rough experiment description, and then having the model do the rest. Only once that’s the case will idea generation become my bottleneck.
That’s the opposite of my experience. Nearly all the papers I read vary between “trash, I got nothing useful out besides an idea for a post explaining the relevant failure modes” and “high quality but not relevant to anything important”. Setting up our experiments is historically much faster than the work of figuring out what experiments would actually be useful.
There are exceptions to this, large projects which seem useful and would require lots of experimental work, but they’re usually much lower-expected-value-per-unit-time than going back to the whiteboard, understanding things better, and doing a simpler experiment once we know what to test.
Ah, well, for most papers that spark an idea in me, the idea isn’t simply an extension of the paper. It’s a question tangentially related which probes at my own frontier of understanding.
I’ve always found that a boring lecture is a great opportunity to brainstorm because my mind squirms away from the boredom into invention and extrapolation of related ideas. A boring paper does some of the same for me, except that I’m less socially pressured to keep reading it, and thus less able to squeeze my mind with the boredom of it.
As for coming up with ideas… It is a weakness of mind that I am far better at generating ideas than at critiquing them (my own or others). Which is why I worked so well in a team where I had someone I trusted to sort through my ideas and pick out the valuable ones. It sounds to me like you have a better filter on idea quality.
That’s mostly my experience as well: experiments are near-trivial to set up, and setting up any experiment that isn’t near-trivial to set up is a poor use of the time that can instead be spent thinking on the topic a bit more and realizing what the experimental outcome would be or why this would be entirely the wrong experiment to run.
But the friction costs of setting up an experiment aren’t zero. If it were possible to sort of ramble an idea at an AI and then have it competently execute the corresponding experiment (or set up a toy formal model and prove things about it), I think this would be able to speed up even deeply confused/non-paradigmatic research.
… That said, I think the sorts of experiments we do aren’t the sorts of experiments ML researchers do. I expect they’re often things like “do a pass over this lattice of hyperparameters and output the values that produce the best loss” (and more abstract equivalents of this that can’t be as easily automated using mundane code). And which, due to the atheoretic nature of ML, can’t be “solved in the abstract”.
So ML research perhaps could be dramatically sped up by menial-software-labor AIs. (Though I think even now the compute needed for running all of those experiments would be the more pressing bottleneck.)
This looks reasonable to me.
Yes. My only hesitation is about how real-life-important it’s for AIs to be able to do math for which very-little-to-no training data exists. The internet and the mathematical literature is so vast that, unless you are doing something truly novel, there’s some relevant subfield there—in which case FrontierMath-style benchmarks would be informative of capability to do real math research.
Also, re-reading Wentworth’s original comment, I note that o1 is weak according to FM. Maybe the things Wentworth is doing are just too hard for o1, rather than (just) overfitting-on-benchmarks style issues? In any case his frustration with o1′s math skills doesn’t mean that FM isn’t measuring real math research capability.
Previously, I’d intuitively assumed the same as well: that it doesn’t matter if LLMs can’t “genuinely research/innovate”, because there is enough potential for innovative-yet-trivial combination of existing ideas that they’d still massively speed up R&D by finding those combinations. (“Innovation overhang”, as @Nathan Helm-Burger puts it here.)
Back in early 2023, I’d considered it fairly plausible that the world would start heating up in 1-2 years due to such synthetically-generated innovations.
Except this… just doesn’t seem to be happening? I’m yet to hear of a single useful scientific paper or other meaningful innovation that was spearheaded by a LLM.[1] And they’re already adept at comprehending such innovative-yet-trivial combinations if a human prompts them with those combinations. So it’s not the matter of not yet being able to understand or appreciate the importance of such synergies. (If Sonnet 3.5.1 or o1 pro didn’t do it, I doubt o3 would.)
Yet this is still not happening. My guess is that “innovative-yet-trivial combinations of existing ideas” are not actually “trivial”, and LLMs can’t do that for the same reasons they can’t do “genuine research” (whatever those reasons are).
Admittedly it’s possible that this is totally happening all over the place and people are just covering it up in order to have all of the glory/status for themselves. But I doubt it: there are enough remarkably selfless LLM enthusiasts that if this were happening, I’d expect it would’ve gone viral already.
There are 2 things to keep in mind:
It’s only now that LLMs are reasonably competent in at least some hard problems, and at any rate, I expect RL to basically solve the domain, because of verifiability properties combined with quite a bit of training data.
We should wait a few years, as we have another scale-up that’s coming up, and it will probably be quite a jump from current AI due to more compute:
https://www.lesswrong.com/posts/NXTkEiaLA4JdS5vSZ/?commentId=7KSdmzK3hgcxkzmPX
I don’t think that’s the limiter here. Reports in the style of “my unpublished PhD thesis was about doing X using Y methodology, I asked an LLM to do that and it one-shot a year of my work! the equations it derived are correct!” have been around for quite a while. I recall it at least in relation to Claude 3, and more recently, o1-preview.
If LLMs are prompted to combine two ideas, they’ve been perfectly capable of “innovating” for ages now, including at fairly high levels of expertise. I’m sure there’s some sort of cross-disciplinary GPQA-like benchmark that they’ve saturated a while ago, so this is even legible.
The trick is picking which ideas to combine/in what direction to dig. This doesn’t appear to be something LLMs are capable of doing well on their own, nor do they seem to speed up human performance on this task. (All cases of them succeeding at it so far have been, by definition, “searching under the streetlight”: checking whether they can appreciate a new idea that a human already found on their own and evaluated as useful.)
I suppose it’s possible that o3 or its successors change that (the previous benchmarks weren’t measuring that, but surely FrontierMath does...). We’ll see.
Mm, I think it’s still up in the air whether even the o-series efficiently scales (as in, without requiring a Dyson Swarm’s worth of compute) to beating the Millennium Prize Eval (or some less legendary yet still major problems).
I expect such problems don’t pass the “can this problem be solved by plugging the extant crystallized-intelligence skills of a number of people into each other in a non-contrived[1] way?” test. Does RL training allow to sidestep this, letting the model generate new crystallized-intelligence skills?
I’m not confident one way or another.
I’m bearish on that. I expect GPT-4 to GPT-5 to be palatably less of a jump than GPT-3 to GPT-4, same way GPT-3 to GPT-4 was less of a jump than GPT-2 to GPT-3. I’m sure it’d show lower loss, and saturate some more benchmarks, and perhaps an o-series model based on it clears FrontierMath, and perhaps programmers and mathematicians would be able to use it in an ever-so-bigger number of cases...
But I predict, with low-moderate confidence, that it still won’t kick off a deluge of synthetically derived innovations. It’d have even more breadth and eye for nuance, but somehow, perplexingly, still no ability to use those capabilities autonomously.
“Non-contrived” because technically, any cognitive skill is just a combination of e. g. NAND gates, since those are Turing-complete. But obviously that doesn’t mean any such skill is accessible if you’ve learned the NAND gate. Intuitively, a combination of crystallized-intelligence skills is only accessible if the idea of combining them is itself a crystallized-intelligence skill (e. g., in the math case, a known ansatz).
Which perhaps sheds some light on why LLMs can’t innovate even via trivial ideas combinations. If a given idea-combination “template” weren’t present in the training data, the LLM can’t reliably independently conceive of it except by brute-force enumeration...? This doesn’t seem quite right, but maybe in the right direction.
I think my key crux is that in domains where there is a way to verify that the solution actually works, RL can scale to superhuman performance, and mathematics/programming are domains that are unusually easy to verify/gather training data for RL performance, so with caveats it can become rather good at those specific domains/benchmarks like millennium prize evals, but the important caveat is I don’t believe this transfers very well to domains where verifying isn’t easy, like creative writing.
I was talking about the 1 GW systems that would be developed in late 2026-early 2027, not GPT-5.
Sure, the theory on that is solid. But how efficiently does it scale off-distribution, in practice?
The inference-time scaling laws, much like the pretraining scaling laws, are ultimately based on test sets whose entries are “shallow” (in the previously discussed sense). It doesn’t tell us much regarding how well the technique scales with the “conceptual depth” of a problem.
o3 took a million dollars in inference-time compute and unknown amounts in training-time compute just to solve the “easy” part of the FrontierMath benchmark (which likely take human experts single-digit hours, maybe <1 hour for particularly skilled humans). How much would be needed for beating the “hard” subset of FrontierMath? How much more still would be needed for problems that take individual researchers days; or problems that take entire math departments months; or problems that take entire fields decades?
It’s possible that the “synthetic data flywheel” works so well that the amount of human-researcher-hour-equivalents per unit of compute scales, say, exponentially with some aspect of o-series’ training, and so o6 in 2027 solves the Riemann Hypothesis.
Or it scales not that well, and o6 can barely clear real-life equivalents of hard FrontierMath problems. Perhaps instead the training costs (generating all the CoT trees on which RL training is then done) scale exponentially, while researcher-hour-equivalents per compute units scale linearly.
It doesn’t seem to me that we know which one it is yet. Do we?
I don’t think we know yet whether it will succeed in practice, or whether it training costs make it infeasibble to do.
Consider: https://www.cognitiverevolution.ai/can-ais-generate-novel-research-ideas-with-lead-author-chenglei-si/
I think a different phenomenon is occuring. My guess, updating on my own experience, is that ideas aren’t the current bottleneck. 1% inspiration, 99% perspiration.
As someone who has been reading 3-20 papers per month for many years now, in neuroscience and machine learning, I feel overwhelmed with ideas. I average about 0.75 per paper. I write them down, and the lists grow faster than they shrink by two orders of magnitude.
When I was on my favorite industry team, what I most valued about my technical manager was his ability to help me sort through and prioritize them. It was like I created a bunch of LEGO pieces, he picked one to be next, I put it in place by coding it up, he checked the placement by reviewing my PR. If someone has offered me a source of ideas ranging in quality between worse than my worst ideas, and almost as good as my best ideas, and skewed towards bad… I’d have laughed and turned them down without a second thought.
For something like a paper instead of a minor tech idea for 1 week PR… The situation is far more intense. The grunt work of running the experiments and preparing the paper is enormous compared to the time and effort of coming up with the idea in the first place. More like 0.1% to 99.9%.
Current LLMs can speed up creating a paper if given the results and experiment description to write about. That’s probably also not the primary bottleneck (although still more than idea generation).
So the current bottleneck, in my estimation, for ml experiments, is the experiments. Coding up the experiments accurately and efficiently, running them (and handling the compute costs), analyzing the results.
So I’ve been expecting to see an acceleration dependent on that aspect. That’s hard to measure though. Are LLMs currently speeding this work up a little? Probably. I’ve had my work sped up some by the recent Sonnet 3.5.1. Currently though it’s a trade-off, there’s overhead in checking for misinterpretations and correcting bugs. We still seem a long way in “capability space” from me being able to give a background paper and rough experiment description, and then having the model do the rest. Only once that’s the case will idea generation become my bottleneck.
That’s the opposite of my experience. Nearly all the papers I read vary between “trash, I got nothing useful out besides an idea for a post explaining the relevant failure modes” and “high quality but not relevant to anything important”. Setting up our experiments is historically much faster than the work of figuring out what experiments would actually be useful.
There are exceptions to this, large projects which seem useful and would require lots of experimental work, but they’re usually much lower-expected-value-per-unit-time than going back to the whiteboard, understanding things better, and doing a simpler experiment once we know what to test.
Ah, well, for most papers that spark an idea in me, the idea isn’t simply an extension of the paper. It’s a question tangentially related which probes at my own frontier of understanding.
I’ve always found that a boring lecture is a great opportunity to brainstorm because my mind squirms away from the boredom into invention and extrapolation of related ideas. A boring paper does some of the same for me, except that I’m less socially pressured to keep reading it, and thus less able to squeeze my mind with the boredom of it.
As for coming up with ideas… It is a weakness of mind that I am far better at generating ideas than at critiquing them (my own or others). Which is why I worked so well in a team where I had someone I trusted to sort through my ideas and pick out the valuable ones. It sounds to me like you have a better filter on idea quality.
That’s mostly my experience as well: experiments are near-trivial to set up, and setting up any experiment that isn’t near-trivial to set up is a poor use of the time that can instead be spent thinking on the topic a bit more and realizing what the experimental outcome would be or why this would be entirely the wrong experiment to run.
But the friction costs of setting up an experiment aren’t zero. If it were possible to sort of ramble an idea at an AI and then have it competently execute the corresponding experiment (or set up a toy formal model and prove things about it), I think this would be able to speed up even deeply confused/non-paradigmatic research.
… That said, I think the sorts of experiments we do aren’t the sorts of experiments ML researchers do. I expect they’re often things like “do a pass over this lattice of hyperparameters and output the values that produce the best loss” (and more abstract equivalents of this that can’t be as easily automated using mundane code). And which, due to the atheoretic nature of ML, can’t be “solved in the abstract”.
So ML research perhaps could be dramatically sped up by menial-software-labor AIs. (Though I think even now the compute needed for running all of those experiments would be the more pressing bottleneck.)
Convincing.