[Off the top of my head. I don’t feel like my thoughts on this are very developed, so I’d probably say different things after thinking about it for 1-10 more hours.]
[ETA: On a second reading, I think some of the claims below are unhelpfully flippant and, depending on how one reads them, uncharitable. I don’t want to spend the significant time required for editing, but want to flag that I think my dispassionate views are not super well represented below.]
Do you have any thoughts on how to set up a better system for EA research, and how it should be more like academia?
Things that immediately come to mind, not necessarily the most important levers:
Identify skills or bodies of knowledge that seem relevant for longtermist research, and where necessary design curricula for deliberate practice of these. In addition to having other downsides, I think our norms of single-dimensional evaluations of people (I feel like I hear much more often that someone is “promising” or “impressive” than that they’re “good at <ability or skill>”) are evidence of a harmful laziness that helps entrench the status quo.
Possibly something like a double-blind within-EA peer review system for some publications could be good.
More publicly accessible and easily searchable content, ideally collected or indexed by central hubs. This does not necessarily mean more standard academic publications. I think that e.g. some content that currently only exists in nonpublic Google docs isn’t published solely because of (i) exaggerated worries about info hazards or (ii) exaggerated worries that non-polished content might reflect badly on the author. (Though in other cases I think there are valid reasons not to publish.) If there was a place where it was culturally OK to publish rough drafts, this could help.
This is more fuzzy, but I think it would be valuable to have a more output-oriented culture. (At the margin—I definitely agree that too much emphasis on producing output can be harmful in some situations or if taken too far.)
Culturally, but also when making e.g. concrete hiring decisions, we should put less emphasis on “does this person seem smart?” and more on “does this person have a track record of achievements?”. (Again, this is at the margin, and there are exceptions.) Cf. how this changes over the progression of a career in academia—to get into a good university as undergraduate you need to have good grades, which is closer to “does this person seem smart?”, but to get tenure you need to have publications, which is closer to “does this person have a track record of achievements?” [I say this as someone with a conspicuous dearth of achievements but ability to project and evidence of smartness, i.e. someone who has benefitted from the status quo.]
We should evaluate research less by asking “how immediately action-relevant or impactful is this?” and more by asking “has this isolated a plausibly relevant question, and does it a good job at answering it?”.
What kinds of specialisation do you think we’d want—subject knowledge? Along different subject lines to academia?
Subject knowledge
Methods (e.g. it regularly happens to me that someone I’m mentoring has a question that is essentially just about statistics but I can’t answer it nor do I know anyone easily available in my network who can; it seems like a bit of a travesty to be in a situation where a lot of people worship Bayes’s Rule but very few have the knowledge of even a 1-semester long course in applied statistics)
I expect that some of the resulting specialists would have a natural home in existing academic disciplines and others wouldn’t, but I can’t immediately think of examples.
Do you think EA should primarily use existing academia for training new researchers, or should there be lots of RSP-type things?
I think in principle it’d be great if there were more RSP-type things, but I’m not sure if I think they’re good to expand at the margin given opportunity costs.
However, I expect that for most people the best training setup would not be RSP-type things but a combination of:
Full-time work/study in academia or at some “elite organization” with good mentoring and short feedback loops.
EA-focused “enrichment interventions” that essentially don’t substitute for conventional full-time work/study (e.g. weekend seminars, fellowship in term breaks or work sabbaticals). Participants would be selected for EA motivation, there would be opportunity for interaction with EA researchers and other people working at EA orgs, the content would be focused on core EA issues, etc.
This is because I do agree there are important components of “EA/rationalist mindware and knowledge” without which I expect even super smart and extremely skilled people to have little impact. But I’m really skeptical that the best way to transmit these is to have people hang out for years in insular low-stimulation environments. I think we can transmit them in much less time, and in a way that doesn’t compete as much with robustly useful skill acquisition, and if not then we can figure out how to do this.
I expect RSP-type things to be targeted at people in more exceptional circumstances, e.g. they have good plans that don’t fit into existing institutions or they need time to “switch fields”.
We should evaluate research less by asking “how immediately action-relevant or impactful is this?” and more by asking “has this isolated a plausibly relevant question, and does it a good job at answering it?”.
Could you say more about why you think that that shift at the margin would be good?
In many cases, doing thorough work on a narrow question and providing immediately impactful findings is simply too hard. This used to work well in the early days of EA when more low-hanging fruit was available, but rarely works any more.
Instead of having 10 shallow takes on immediately actionable question X, I’d rather have 10 thorough takes on different subquestions Y_1, …, Y_10, even if it’s not immediately obvious how exactly they help with answering X (there should be some plausible relation, however). Maybe I expect 8 of these 10 takes to be useless, but unlike adding more shallow takes on X the thorough takes on the 2 remaining subquestions enable incremental and distributed intellectual progress:
It may allow us to identify new subquestions we weren’t able to find through doing shallow takes on X.
Someone else can build on the work, and e.g. do a thorough take on another subquestions that helps illuminate how it relates to X, what else we need to know to use the thorough findings to make progress on Y etc.
The expected benefit from unknown unknowns is larger. Random examples: the economic historians who assembled data on historic GDP growth presumably didn’t anticipate that their data would feature in outside-view arguments on the plausibility of AGI takeoff this century. (Though if you had asked them, they probably would have been able to see that this is a plausible use—there probably are other examples where the delayed use/benefit is more surprising.)
It’s often more instrumentally useful because it better fulfills non-EA criteria for excellence or credibility.
I think this is especially important when trying to build bridges between EA research and academia with the vision to make more academic research helpful to EA happen.
It’s also important because non-EA actors often have different criteria for when they’re willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like “this seems 30% likely to me, even if I can’t fully defend this or even say why exactly I believe this” (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act they’ll need more legible arguments.
One recent examples that’s salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrenner’s paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question “How much should this paper update our all-things-considered view on whether it’s net good to accelerate economic growth?”. It strikes me that this is very different from the questions I’d ask about that paper, and also quite far removed from why, as I said, I think this paper was a great contribution.
These reasons are more like:
As best as I can tell (significantly because of reactions by other people with more domain expertise), the paper is quite impressive to academic economists, and so could have large instrumental benefits for building bridges.
While it didn’t even occur to me to update my all-things-considered take on whether it’d be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect that’s relevant to this question. Once we have 10 to 100 papers like it, I think I’ll have learned a lot and will be in a great position to update my all-things-considered take. But, crucially, the paper is one clear step in this direction in a way in which an EA Forum post with bottom line “I spent 40 hours researching whether accelerating economic growth is net good, and here is what I think” simply is not.
Interesting, thanks. I’m not sure whether I overall agree, but I think this glimpse of your models on this topic will be useful to me.
One clarifying question:
Instead of having 10 shallow takes on immediately actionable question X, I’d rather have 10 thorough takes on different subquestions Y_1, …, Y_10
My first thought was “But wait, wouldn’t 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?” But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be “shallow” in relation to the larger topic—i.e., the “shallow takes” involve the same amount of total analysis as the “thorough takes”, but they’re analysing such a big topic that they can only provide a shallow look at each component. Is that right?
the “shallow takes” involve the same amount of total analysis as the “thorough takes”, but they’re analysing such a big topic that they can only provide a shallow look at each component
Yes, that’s what I had in mind. Thanks for clarifying!
Thanks, that’s helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because I’m thinking about getting economics training, which seems useful for answering specific sub-questions in detail (‘Existential Risk and Economic Growth’ being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
I think you’re very likely doing this anyway, but I’d recommend to get a range of perspectives on these questions. As I said, my own views here don’t feel that resilient, and I also know that several epistemic peers disagree with me on some of the above.
[Off the top of my head. I don’t feel like my thoughts on this are very developed, so I’d probably say different things after thinking about it for 1-10 more hours.]
[ETA: On a second reading, I think some of the claims below are unhelpfully flippant and, depending on how one reads them, uncharitable. I don’t want to spend the significant time required for editing, but want to flag that I think my dispassionate views are not super well represented below.]
Things that immediately come to mind, not necessarily the most important levers:
Identify skills or bodies of knowledge that seem relevant for longtermist research, and where necessary design curricula for deliberate practice of these. In addition to having other downsides, I think our norms of single-dimensional evaluations of people (I feel like I hear much more often that someone is “promising” or “impressive” than that they’re “good at <ability or skill>”) are evidence of a harmful laziness that helps entrench the status quo.
Possibly something like a double-blind within-EA peer review system for some publications could be good.
More publicly accessible and easily searchable content, ideally collected or indexed by central hubs. This does not necessarily mean more standard academic publications. I think that e.g. some content that currently only exists in nonpublic Google docs isn’t published solely because of (i) exaggerated worries about info hazards or (ii) exaggerated worries that non-polished content might reflect badly on the author. (Though in other cases I think there are valid reasons not to publish.) If there was a place where it was culturally OK to publish rough drafts, this could help.
This is more fuzzy, but I think it would be valuable to have a more output-oriented culture. (At the margin—I definitely agree that too much emphasis on producing output can be harmful in some situations or if taken too far.)
Culturally, but also when making e.g. concrete hiring decisions, we should put less emphasis on “does this person seem smart?” and more on “does this person have a track record of achievements?”. (Again, this is at the margin, and there are exceptions.) Cf. how this changes over the progression of a career in academia—to get into a good university as undergraduate you need to have good grades, which is closer to “does this person seem smart?”, but to get tenure you need to have publications, which is closer to “does this person have a track record of achievements?” [I say this as someone with a conspicuous dearth of achievements but ability to project and evidence of smartness, i.e. someone who has benefitted from the status quo.]
We should evaluate research less by asking “how immediately action-relevant or impactful is this?” and more by asking “has this isolated a plausibly relevant question, and does it a good job at answering it?”.
Subject knowledge
Methods (e.g. it regularly happens to me that someone I’m mentoring has a question that is essentially just about statistics but I can’t answer it nor do I know anyone easily available in my network who can; it seems like a bit of a travesty to be in a situation where a lot of people worship Bayes’s Rule but very few have the knowledge of even a 1-semester long course in applied statistics)
I expect that some of the resulting specialists would have a natural home in existing academic disciplines and others wouldn’t, but I can’t immediately think of examples.
I think in principle it’d be great if there were more RSP-type things, but I’m not sure if I think they’re good to expand at the margin given opportunity costs.
However, I expect that for most people the best training setup would not be RSP-type things but a combination of:
Full-time work/study in academia or at some “elite organization” with good mentoring and short feedback loops.
EA-focused “enrichment interventions” that essentially don’t substitute for conventional full-time work/study (e.g. weekend seminars, fellowship in term breaks or work sabbaticals). Participants would be selected for EA motivation, there would be opportunity for interaction with EA researchers and other people working at EA orgs, the content would be focused on core EA issues, etc.
This is because I do agree there are important components of “EA/rationalist mindware and knowledge” without which I expect even super smart and extremely skilled people to have little impact. But I’m really skeptical that the best way to transmit these is to have people hang out for years in insular low-stimulation environments. I think we can transmit them in much less time, and in a way that doesn’t compete as much with robustly useful skill acquisition, and if not then we can figure out how to do this.
I expect RSP-type things to be targeted at people in more exceptional circumstances, e.g. they have good plans that don’t fit into existing institutions or they need time to “switch fields”.
Interesting, thanks for sharing!
Could you say more about why you think that that shift at the margin would be good?
Several reasons:
In many cases, doing thorough work on a narrow question and providing immediately impactful findings is simply too hard. This used to work well in the early days of EA when more low-hanging fruit was available, but rarely works any more.
Instead of having 10 shallow takes on immediately actionable question X, I’d rather have 10 thorough takes on different subquestions Y_1, …, Y_10, even if it’s not immediately obvious how exactly they help with answering X (there should be some plausible relation, however). Maybe I expect 8 of these 10 takes to be useless, but unlike adding more shallow takes on X the thorough takes on the 2 remaining subquestions enable incremental and distributed intellectual progress:
It may allow us to identify new subquestions we weren’t able to find through doing shallow takes on X.
Someone else can build on the work, and e.g. do a thorough take on another subquestions that helps illuminate how it relates to X, what else we need to know to use the thorough findings to make progress on Y etc.
The expected benefit from unknown unknowns is larger. Random examples: the economic historians who assembled data on historic GDP growth presumably didn’t anticipate that their data would feature in outside-view arguments on the plausibility of AGI takeoff this century. (Though if you had asked them, they probably would have been able to see that this is a plausible use—there probably are other examples where the delayed use/benefit is more surprising.)
It’s often more instrumentally useful because it better fulfills non-EA criteria for excellence or credibility.
I think this is especially important when trying to build bridges between EA research and academia with the vision to make more academic research helpful to EA happen.
It’s also important because non-EA actors often have different criteria for when they’re willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like “this seems 30% likely to me, even if I can’t fully defend this or even say why exactly I believe this” (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act they’ll need more legible arguments.
One recent examples that’s salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrenner’s paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question “How much should this paper update our all-things-considered view on whether it’s net good to accelerate economic growth?”. It strikes me that this is very different from the questions I’d ask about that paper, and also quite far removed from why, as I said, I think this paper was a great contribution.
These reasons are more like:
As best as I can tell (significantly because of reactions by other people with more domain expertise), the paper is quite impressive to academic economists, and so could have large instrumental benefits for building bridges.
While it didn’t even occur to me to update my all-things-considered take on whether it’d be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect that’s relevant to this question. Once we have 10 to 100 papers like it, I think I’ll have learned a lot and will be in a great position to update my all-things-considered take. But, crucially, the paper is one clear step in this direction in a way in which an EA Forum post with bottom line “I spent 40 hours researching whether accelerating economic growth is net good, and here is what I think” simply is not.
Interesting, thanks. I’m not sure whether I overall agree, but I think this glimpse of your models on this topic will be useful to me.
One clarifying question:
My first thought was “But wait, wouldn’t 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?” But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be “shallow” in relation to the larger topic—i.e., the “shallow takes” involve the same amount of total analysis as the “thorough takes”, but they’re analysing such a big topic that they can only provide a shallow look at each component. Is that right?
Yes, that’s what I had in mind. Thanks for clarifying!
I’m confused—did you make this comment in the wrong place?
No, but there was a copy and paste error that made the comment unintelligible. Edited now. Thanks for flagging!
Thanks, that’s helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because I’m thinking about getting economics training, which seems useful for answering specific sub-questions in detail (‘Existential Risk and Economic Growth’ being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
Glad it’s helpful!
I think you’re very likely doing this anyway, but I’d recommend to get a range of perspectives on these questions. As I said, my own views here don’t feel that resilient, and I also know that several epistemic peers disagree with me on some of the above.