I think > 95% of incoming PhD students in AI at Berkeley have bad ideas (in the way this post uses the phrase).[...](Note also that AI @ Berkeley is a very selective program.)
What % do you think this is true for, quality-weighted?
I remember an interview with Geoffrey Hinton where (paraphrased) Hinton was basically like “just trust your intuitions man. Either your intuitions are good or they’re bad. If they are good you should mostly trust your intuitions regardless of what other people say, and if they’re bad, well, you aren’t going to be a good researcher anyway.”
And I remember finding that logic really suspicious and his experiences selection-biased like heck (My understanding is that Hinton “got lucky” by calling neural nets early but his views aren’t obviously more principled than his close contemporaries).
But to steelman(steel-alien?) his view a little, I worry that EA is overinvested in outside-view/forecasting types (like myself?), rather than people with strong and true convictions/extremely high-quality initial research taste, which (quality-weighted) may be making up the majority of revolutionary progress.
And if we tell the future Geoffrey Hintons (and Eliezer Yudkowskys) of the world to be more deferential and trust their intuitions less relative to elite consensus or the literature, we’re doing the world/our movement a disservice, even if the advice is likely to be individually useful/good for most researchers in terms of expected correctness of beliefs or career advancement.
What % do you think this is true for, quality-weighted?
Weighted by quality after graduating? Still > 50%, probably > 80%, but it’s really just a lot harder to tell (I don’t have enough data). I’d guess that the best people still had “bad ideas” when they were starting out.
(I think a lot of what makes an junior researcher’s idea “bad” is that the researcher doesn’t know about existing work, or has misinterpreted the goal of the field, or lacks intuitions gained from hands-on experience, etc. It is really hard to compensate for a lack of knowledge with good intuition or strong armchair reasoning, and I think junior researchers should make it a priority to learn this sort of stuff.)
Re: the rest of your comment, I think you’re reading more into my comment than I said or meant. I do not think researchers should generally be deferential; I think they should have strong beliefs, that may in fact go against expert consensus. I just don’t think this is the right attitude while you are junior. Some quotes from my FAQ:
When selecting research projects, when you’re junior you should generally defer to your advisor. As time passes you should have more conviction. I very rarely see a first year’s research intuitions beat a professor’s; I have seen this happen more often for fourth years and above.
[...]
There’s a longstandingdebate about whether one should defer to some aggregation of experts (an “outside view”), or try to understand the arguments and come to your own conclusion (an “inside view”). This debate mostly focuses on which method tends to arrive at correct conclusions. I am not taking a stance on this debate; I think it’s mostly irrelevant to the problem of doing good research. Research is typically meant to advance the frontiers of human knowledge; this is not the same goal as arriving at correct conclusions. If you want to advance human knowledge, you’re going to need a detailed inside view.
[followed by a longer example in which the correct thing to do is to ignore the expert]
Thanks for the link to your FAQ, I’m excited to read it further now!
Re: the rest of your comment, I think you’re reading more into my comment than I said or meant. I do not think researchers should generally be deferential; I think they should have strong beliefs, that may in fact go against expert consensus. I just don’t think this is the right attitude while you are junior
To be clear, I think Geoffrey Hinton’s advice was targeted at very junior people. In context, the interview was conducted for Andrew Ng’s online deep learning course, which for many people would be their first exposure to deep learning. I also got the impression that he would stand by this advice for early PhDs (though I could definitely have misunderstood him), and by “future Geoffrey Hintons and Eliezer Yudkowskys” I was thinking about pretty junior people rather than established researchers.
“Defer to experts for ~3 years, then trust your intuitions”
“Always trust your intuitions”
When you said
But to steelman(steel-alien?) his view a little, I worry that EA is overinvested in outside-view/forecasting types (like myself?), rather than people with strong and true convictions/extremely high-quality initial research taste, which (quality-weighted) may be making up the majority of revolutionary progress.
And if we tell the future Geoffrey Hintons (and Eliezer Yudkowskys) of the world to be more deferential and trust their intuitions less relative to elite consensus or the literature, we’re doing the world/our movement a disservice, even if the advice is likely to be individually useful/good for most researchers in terms of expected correctness of beliefs or career advancement.
I thought you were claiming “maybe 3 > 1”, so my response was “don’t do 1 or 3, do 2″.
If you’re instead claiming “maybe 3 > 2”, I don’t really get the argument. It doesn’t seem like advice #2 is obviously worse than advice #3 even for junior Eliezers and Geoffreys. (It’s hard to say for those two people: in Eliezer’s case, since there were no experts to defer to at the time, and I don’t know enough details about Geoffrey to evaluate which advice would be good for him.)
I think Geoffrey Hinton’s advice was targeted at very junior people.
Oh, I agree that’s probably true. I think he’s wrong to give that advice. I’m generally pretty okay with ignoring expert advice to amateurs if you have reason to believe it’s bad; experts usually don’t remember what it was like to be an amateur and so it’s not that surprising that their advice on what amateurs should do is not great. (EDIT: Here’s a new post that goes into more detail on this.)
I would guess the ‘typical young researcher fallacy’ also applies to Hinton - my impression is he is basically advising his past self, similarly to Toby. As a consequence, the advice is likely sensible for people-much-like-past-Hinton, but not a good general advice for everyone.
In ~3 years most people are able to re-train their intuitions a lot (which is part of the point!). This seems particularly dangerous in cases where expertise in the thing you are actually interested in does not exist, but expertise in something somewhat close does - instead of following your curiosity, you ‘substitute the question’ with a different question, for which a PhD program exists, or senior researchers exist, or established directions exist. If your initial taste/questions was better than the expert’s, you run a risk of overwriting your taste with something less interesting/impactful.
Anecdotal illustrative story:
Arguably, large part of what are now the foundations of quantum information theory / quantum computing could have been discovered much sooner, together with taking more sensible interpretations of quantum mechanics than Copenhagen interpretation seriously. My guess what was happening during multiple decades (!) was many early career researchers were curious what’s going on, dissatisfied with the answers, interested in thinking about the topic more… but they were given the advice along the lines ‘this is not a good topic for PhDs or even undergrads; don’t trust your intuition; problems here are distasteful mix of physics and philosophy; shut up and calculate, that’s how a real progress happens’ … and they followed it; acquired a taste telling them that solving difficult scattering amplitudes integrals using advanced calculus techniques is tasty, and thinking about deep things formulated using tools of high-school algebra is for fools. (Also if you did run a survey in year 4 of their PhDs, large fraction of quantum physicists would probably endorse the learned update from thinking about young foolish questions about QM interpretations to the serious and publishable thinking they have learned.)
I agree substituting the question would be bad, and sometimes there aren’t any relevant experts in which case you shouldn’t defer to people. (Though even then I’d consider doing research in an unrelated area for a couple of years, and then coming back to work on the question of interest.)
I admit I don’t really understand how people manage to have a “driving question” overwritten—I can’t really imagine that happening to me and I am confused about how it happens to other people.
(I think sometimes it is justified, e.g. you realize that your question was confused, and the other work you’ve done has deconfused it, but it does seem like often it’s just that they pick up the surrounding culture and just forget about the question they cared about in the first place.)
So I guess this seems like a possible risk. I’d still bet pretty strongly against any particular junior researcher’s intuition being better, so I still think this advice is good on net.
(I’m mostly not engaging with the quantum example because it sounds like a very just-so story to me and I don’t know enough about the area to evaluate the just-so story.)
I’m confused about your FAQ’s advice here. Some quotes from the longer example:
Let’s say that Alice is an expert in AI alignment, and Bob wants to get into the field, and trusts Alice’s judgment. Bob asks Alice what she thinks is most valuable to work on, and she replies, “probably robustness of neural networks”. [...] I think Bob should instead spend some time thinking about how a solution to robustness would mean that AI risk has been meaningfully reduced. [...] It’s possible that after all this reflection, Bob concludes that impact regularization is more valuable than robustness. [...] It’s probably not the case that progress in robustness is 50x more valuable than progress in impact regularization, and so Bob should go with [impact regularization].
In the example, Bob “wants to get into the field”, so this seems like an example of how junior people shouldn’t defer to experts when picking research projects.
(Specualative differences: Maybe you think there’s a huge difference between Alice giving a recommendation about an area vs a specific research project? Or maybe you think that working on impact regularization is the best Bob can do if he can’t find a senior researcher to supervise him, but if Alice could supervise his work on robustness he should go with robustness? If so, maybe it’s worth clarifying that in the FAQ.)
Edit: TBC, I interpret Toby Shevlane as saying ~you should probably work on whatever senior people find interesting; while Jan Kulveit says that “some young researchers actually have great ideas, should work on them, and avoid generally updating on research taste of most of the ‘senior researchers’”. The quoted FAQ example is consistent with going against Jan’s strong claim, but I’m not sure it’s consistent with agreeing with Toby’s initial advice, and I interpret you as agreeing with that advice when writing e.g. “Defer to experts for ~3 years, then trust your intuitions”.
In that example, Alice has ~5 min of time to give feedback to Bob; in Toby’s case the senior researchers are (in aggregate) spending at least multiple hours providing feedback (where “Bob spent 15 min talking to Alice and seeing what she got excited about” counts as 15 min of feedback from Alice). That’s the major difference.
I guess one way you could interpret Toby’s advice is to simply get a project idea from a senior person, and then go work on it yourself without feedback from that senior person—I would disagree with that particular advice. I think it’s important to have iterative / continual feedback from senior people.
What % do you think this is true for, quality-weighted?
I remember an interview with Geoffrey Hinton where (paraphrased) Hinton was basically like “just trust your intuitions man. Either your intuitions are good or they’re bad. If they are good you should mostly trust your intuitions regardless of what other people say, and if they’re bad, well, you aren’t going to be a good researcher anyway.”
And I remember finding that logic really suspicious and his experiences selection-biased like heck (My understanding is that Hinton “got lucky” by calling neural nets early but his views aren’t obviously more principled than his close contemporaries).
But to steelman(steel-alien?) his view a little, I worry that EA is overinvested in outside-view/forecasting types (like myself?), rather than people with strong and true convictions/extremely high-quality initial research taste, which (quality-weighted) may be making up the majority of revolutionary progress.
And if we tell the future Geoffrey Hintons (and Eliezer Yudkowskys) of the world to be more deferential and trust their intuitions less relative to elite consensus or the literature, we’re doing the world/our movement a disservice, even if the advice is likely to be individually useful/good for most researchers in terms of expected correctness of beliefs or career advancement.
Weighted by quality after graduating? Still > 50%, probably > 80%, but it’s really just a lot harder to tell (I don’t have enough data). I’d guess that the best people still had “bad ideas” when they were starting out.
(I think a lot of what makes an junior researcher’s idea “bad” is that the researcher doesn’t know about existing work, or has misinterpreted the goal of the field, or lacks intuitions gained from hands-on experience, etc. It is really hard to compensate for a lack of knowledge with good intuition or strong armchair reasoning, and I think junior researchers should make it a priority to learn this sort of stuff.)
Re: the rest of your comment, I think you’re reading more into my comment than I said or meant. I do not think researchers should generally be deferential; I think they should have strong beliefs, that may in fact go against expert consensus. I just don’t think this is the right attitude while you are junior. Some quotes from my FAQ:
Thanks for the link to your FAQ, I’m excited to read it further now!
To be clear, I think Geoffrey Hinton’s advice was targeted at very junior people. In context, the interview was conducted for Andrew Ng’s online deep learning course, which for many people would be their first exposure to deep learning. I also got the impression that he would stand by this advice for early PhDs (though I could definitely have misunderstood him), and by “future Geoffrey Hintons and Eliezer Yudkowskys” I was thinking about pretty junior people rather than established researchers.
I’m considering three types of advice:
“Always defer to experts”
“Defer to experts for ~3 years, then trust your intuitions”
“Always trust your intuitions”
When you said
I thought you were claiming “maybe 3 > 1”, so my response was “don’t do 1 or 3, do 2″.
If you’re instead claiming “maybe 3 > 2”, I don’t really get the argument. It doesn’t seem like advice #2 is obviously worse than advice #3 even for junior Eliezers and Geoffreys. (It’s hard to say for those two people: in Eliezer’s case, since there were no experts to defer to at the time, and I don’t know enough details about Geoffrey to evaluate which advice would be good for him.)
Oh, I agree that’s probably true. I think he’s wrong to give that advice. I’m generally pretty okay with ignoring expert advice to amateurs if you have reason to believe it’s bad; experts usually don’t remember what it was like to be an amateur and so it’s not that surprising that their advice on what amateurs should do is not great. (EDIT: Here’s a new post that goes into more detail on this.)
I would guess the ‘typical young researcher fallacy’ also applies to Hinton - my impression is he is basically advising his past self, similarly to Toby. As a consequence, the advice is likely sensible for people-much-like-past-Hinton, but not a good general advice for everyone.
In ~3 years most people are able to re-train their intuitions a lot (which is part of the point!). This seems particularly dangerous in cases where expertise in the thing you are actually interested in does not exist, but expertise in something somewhat close does - instead of following your curiosity, you ‘substitute the question’ with a different question, for which a PhD program exists, or senior researchers exist, or established directions exist. If your initial taste/questions was better than the expert’s, you run a risk of overwriting your taste with something less interesting/impactful.
Anecdotal illustrative story:
Arguably, large part of what are now the foundations of quantum information theory / quantum computing could have been discovered much sooner, together with taking more sensible interpretations of quantum mechanics than Copenhagen interpretation seriously. My guess what was happening during multiple decades (!) was many early career researchers were curious what’s going on, dissatisfied with the answers, interested in thinking about the topic more… but they were given the advice along the lines ‘this is not a good topic for PhDs or even undergrads; don’t trust your intuition; problems here are distasteful mix of physics and philosophy; shut up and calculate, that’s how a real progress happens’ … and they followed it; acquired a taste telling them that solving difficult scattering amplitudes integrals using advanced calculus techniques is tasty, and thinking about deep things formulated using tools of high-school algebra is for fools. (Also if you did run a survey in year 4 of their PhDs, large fraction of quantum physicists would probably endorse the learned update from thinking about young foolish questions about QM interpretations to the serious and publishable thinking they have learned.)
I agree substituting the question would be bad, and sometimes there aren’t any relevant experts in which case you shouldn’t defer to people. (Though even then I’d consider doing research in an unrelated area for a couple of years, and then coming back to work on the question of interest.)
I admit I don’t really understand how people manage to have a “driving question” overwritten—I can’t really imagine that happening to me and I am confused about how it happens to other people.
(I think sometimes it is justified, e.g. you realize that your question was confused, and the other work you’ve done has deconfused it, but it does seem like often it’s just that they pick up the surrounding culture and just forget about the question they cared about in the first place.)
So I guess this seems like a possible risk. I’d still bet pretty strongly against any particular junior researcher’s intuition being better, so I still think this advice is good on net.
(I’m mostly not engaging with the quantum example because it sounds like a very just-so story to me and I don’t know enough about the area to evaluate the just-so story.)
(As an aside, I read your FAQ and enjoyed it, so thanks for the share!)
I’m confused about your FAQ’s advice here. Some quotes from the longer example:
In the example, Bob “wants to get into the field”, so this seems like an example of how junior people shouldn’t defer to experts when picking research projects.
(Specualative differences: Maybe you think there’s a huge difference between Alice giving a recommendation about an area vs a specific research project? Or maybe you think that working on impact regularization is the best Bob can do if he can’t find a senior researcher to supervise him, but if Alice could supervise his work on robustness he should go with robustness? If so, maybe it’s worth clarifying that in the FAQ.)
Edit: TBC, I interpret Toby Shevlane as saying ~you should probably work on whatever senior people find interesting; while Jan Kulveit says that “some young researchers actually have great ideas, should work on them, and avoid generally updating on research taste of most of the ‘senior researchers’”. The quoted FAQ example is consistent with going against Jan’s strong claim, but I’m not sure it’s consistent with agreeing with Toby’s initial advice, and I interpret you as agreeing with that advice when writing e.g. “Defer to experts for ~3 years, then trust your intuitions”.
In that example, Alice has ~5 min of time to give feedback to Bob; in Toby’s case the senior researchers are (in aggregate) spending at least multiple hours providing feedback (where “Bob spent 15 min talking to Alice and seeing what she got excited about” counts as 15 min of feedback from Alice). That’s the major difference.
I guess one way you could interpret Toby’s advice is to simply get a project idea from a senior person, and then go work on it yourself without feedback from that senior person—I would disagree with that particular advice. I think it’s important to have iterative / continual feedback from senior people.