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.)
Let's start with the third caveat: maybe the real crux is what we think are the best outputs; what I consider some of the best outputs by young researchers of AI alignment is easier to point at via examples - so it's e.g. the mesa-optimizers paper or multiple LW posts by John Wentworth. As far as I can tell, none of these seems to be following the proposed 'formula for successful early-career research'. My impression is PhD students in AI in Berkeley need to optimise, and actually optimise a lot for success in an established field (ML/AI), and subsequently, the advice should be more applicable to them. I would even say part of what makes a field "established" actually is something like "somewhat clear direction in the space of unknown in which people are trying to push the boundary" and "shared taste in what is good, according to the direction". (The general direction or at least the taste seems to be ~ self-perpetuating once the field is "established", sometimes beyond the point of usefulness). In contrast to your experience with AI students in Berkeley, in my experience about ~20% of ESPR students have generally good ideas even while at high school/first year in college, and I would often prefer these people to think about ways in which their teachers, professors or seniors are possibly confused, as opposed to learning that their ideas are now generally bad and they should seek someone senior to tell them what to work on. (Ok - the actual advice would be more complex and nuanced, something like "update on the idea taste of people who are better/are comparable and have spent more time thinking about something, but be sceptical and picky about your selection of people"). (ESPR is also very selective, although differently.) With hypothetical surveys, the conclusion (young researchers should mostly defer to seniors in idea taste) does not seem to follow from estimates like "over 80% of them would think their initial ideas were significantly worse than their later ideas". Relevant comparison is something like "over 80% of them would think they should have spent marginally more time thinking about ideas of more senior AI people at Berkeley, and more time on problems they were given by senior people, and smaller amount of time thinking about their own ideas, and working on projects based on their ideas". Would you guess the answer would still be 80%?
It's good to see a new enthusiastic team working on this! My impression, based on working on the problem ~2 years ago is this has good chances to provide value in global health a poverty, animal suffering, or parts of meta- cause areas; in case of x-risk focused projects, something like a 'project platform' seems almost purely bottlenecked by vetting. In the current proposal this seems to mostly depend on "Evaluation Commission"-> as a result, the most important part for x-risk projects seems judgement of members of this commission and/or it's ability to seek external vetting
In my view this text should come with multiple caveats.- Beware 'typical young researcher fallacy'. Young researchers are very diverse, and while some of them will benefit from the advice, some of them will not. I do not believe there is a general 'formula for successful early-career research'. Different people have different styles of doing research, and even different metrics for what 'successful research' means. While certainly many people would benefit from the advice 'your ideas are bad', some young researchers actually have great ideas, should work on them, and avoid generally updating on research taste of most of the"senior researchers". - Beware 'generalisation out of training distribution' problems. Compared to some other fields, AI governance as studied by Allan Dafoe is relatively well decomposed into a hierarchy of problems and you can meaningfully scale it by adding junior people and telling them what to do (work on sub-problems senior people consider interesting). This seems more typical for research fields with established paradigms than for fields which are pre-paradigmatic, or fields in need of a change of paradigm. - Large part of the described formula for success seems to be optimised for success in the direction getting attention of senior researchers, writing something well received, or similar. This is highly practical, and likely good for many people in fields like Ai governance; at the same time, it seems the best research outputs by early career researchers in eg AI safety do not follow this generative pattern, and seem to be motivated more by curiosity, reasoning from first principles, and ignoring authority opinions.
Contrary to what seems an implicit premise of this post, my impression is - most EA group organizers should have this as a side-project, and should not think about "community building" as about their "career path" where they could possibly continue to do it in a company like Salesforce- the label "community building" is unfortunate for what most of the EA group organizing work should consist of- most of the tasks in "EA community building" involve skills which are pretty universal a generally useable in most other fields, like "strategizing", "understanding people", "networking" or "running events"- for example: in my view, what can an EA group organizer on a research career path get from organizing an EA group as a side-project are skills like "organizing event", "explaining complex ideas to people" or even "thinking clearly in groups about important topics". Often the benfits of improving/practicing such skills for a research career are similar or larger than e.g. learning a new programming languageThere are exceptions to this, such as people who want to work on large groups full time, build national groups, or similar. In my view these projects are often roughly of the scope of founding or leading a startup or a NGO and should be attempted by people who, in general, have a lot of optionality in what to do both before working on an EA group and eventually after it. Vint Cerf seems actually more of a counterexample toward "community building and evangelism" as a career objective: anyone who wants to follow this path should note he wrote the TCP protocol internet is still running on first, co-founded one of the entities governing internet later, and worked for Google on community building only after all these experiences. Another reason I'm sceptical of the value of this argument is my guess is people who would be convinced by it ("previously I was hesitant about organizing an EA group because the career path seems too narrow and tied to EA, now I see career paths in for-profit world") are people who should mostly not lead or start EA groups. In most cases EA group organizing involves significant amount of talking to people about careers, and whoever has so limited understanding of the careers to benefit from this advice seems likely to have non-trivial chance of giving people harmful career advice.
1.For different take on very similar topic check this discussion between me and Ben Pace (my reasoning was based on the same Sinatra paper).
For practical purposes, in case of scientists, one of my conclusions wasTranslating into the language of digging for gold, the prospectors differ in their speed and ability to extract gold from the deposits (Q). The gold in the deposits actually is randomly distributed. To extract exceptional value, you have to have both high Q and be very lucky. What is encouraging in selecting the talent is the Q seems relatively stable in the career and can be usefully estimated after ~20 publications. I would guess you can predict even with less data, but the correct "formula" would be trying to disentangle interestingness of the problems the person is working on from the interestingness of the results.
2.For practical purposes, my impression is some EA recruitment efforts could be more often at risk of over-filtering by ex-ante proxies and being bitten by tails coming apart, rather than at risk of not being selective enough.Also, often the practical optimization question is how much effort you should spend on on how extreme tail of the ex-ante distribution. 3. Meta-observation is someone should really recommend more EAs to join the complex systems / complex networks community. Most of the findings from this research project seem to be based on research originating in complex networks community, including research directions such as "science of success", and there is more which can be readily used, "translated" or distilled.
First EuroSPARC was in 2016. Targeting 16-19 year olds, my prior would be participants should still mostly study, and not work full-time on EA, or only exceptionally.
Long feedback loops are certainly a disadvantage.
Also in the meantime ESPR underwent various changes and actually is not optimising for something like "conversion rate to an EA attractor state".
I. I did spent a considerable amount of time thinking about prioritisation (broadly understood)
My experience so far is
few examples, where in some cases I got to writing something
II. My guess is there are more people who work in a similar mode, trying to basically 'build as good world model as you can', dive into problems you run into, and at the end prioritise informally based on such a model. Typically I would expect such model to be in parts implicit / be some sort of multi-model ensemble / ...
While this may not create visible outcomes labeled as prioritisation, I think it's important part of what's happening now
I posted a short version of this, but I think people found it unhelpful, so I'm trying to post somewhat longer version.