We should evaluate research less by asking âhow immediately action-relevant or impactful is this?â and more by asking âhas this isolated a plausibly relevant question, and does it a good job at answering it?â.
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, Iâd rather have 10 thorough takes on different subquestions Y_1, âŠ, Y_10, even if itâs 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 werenât 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 didnât 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 useâthere probably are other examples where the delayed use/âbenefit is more surprising.)
Itâs 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.
Itâs also important because non-EA actors often have different criteria for when theyâre willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like âthis seems 30% likely to me, even if I canât fully defend this or even say why exactly I believe thisâ (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act theyâll need more legible arguments.
One recent examples thatâs salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrennerâs paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question âHow much should this paper update our all-things-considered view on whether itâs net good to accelerate economic growth?â. It strikes me that this is very different from the questions Iâd 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 didnât even occur to me to update my all-things-considered take on whether itâd be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect thatâs relevant to this question. Once we have 10 to 100 papers like it, I think Iâll 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 âI spent 40 hours researching whether accelerating economic growth is net good, and here is what I thinkâ simply is not.
Interesting, thanks. Iâm 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, Iâd rather have 10 thorough takes on different subquestions Y_1, âŠ, Y_10
My first thought was âBut wait, wouldnât 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?â But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be âshallowâ in relation to the larger topicâi.e., the âshallow takesâ involve the same amount of total analysis as the âthorough takesâ, but theyâre analysing such a big topic that they can only provide a shallow look at each component. Is that right?
the âshallow takesâ involve the same amount of total analysis as the âthorough takesâ, but theyâre analysing such a big topic that they can only provide a shallow look at each component
Yes, thatâs what I had in mind. Thanks for clarifying!
Thanks, thatâs helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because Iâm thinking about getting economics training, which seems useful for answering specific sub-questions in detail (âExistential Risk and Economic Growthâ being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
I think youâre very likely doing this anyway, but Iâd recommend to get a range of perspectives on these questions. As I said, my own views here donât feel that resilient, and I also know that several epistemic peers disagree with me on some of the above.
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, Iâd rather have 10 thorough takes on different subquestions Y_1, âŠ, Y_10, even if itâs 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 werenât 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 didnât 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 useâthere probably are other examples where the delayed use/âbenefit is more surprising.)
Itâs 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.
Itâs also important because non-EA actors often have different criteria for when theyâre willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like âthis seems 30% likely to me, even if I canât fully defend this or even say why exactly I believe thisâ (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act theyâll need more legible arguments.
One recent examples thatâs salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrennerâs paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question âHow much should this paper update our all-things-considered view on whether itâs net good to accelerate economic growth?â. It strikes me that this is very different from the questions Iâd 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 didnât even occur to me to update my all-things-considered take on whether itâd be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect thatâs relevant to this question. Once we have 10 to 100 papers like it, I think Iâll 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 âI spent 40 hours researching whether accelerating economic growth is net good, and here is what I thinkâ simply is not.
Interesting, thanks. Iâm 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 âBut wait, wouldnât 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?â But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be âshallowâ in relation to the larger topicâi.e., the âshallow takesâ involve the same amount of total analysis as the âthorough takesâ, but theyâre analysing such a big topic that they can only provide a shallow look at each component. Is that right?
Yes, thatâs what I had in mind. Thanks for clarifying!
Iâm confusedâdid 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, thatâs helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because Iâm thinking about getting economics training, which seems useful for answering specific sub-questions in detail (âExistential Risk and Economic Growthâ being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
Glad itâs helpful!
I think youâre very likely doing this anyway, but Iâd recommend to get a range of perspectives on these questions. As I said, my own views here donât feel that resilient, and I also know that several epistemic peers disagree with me on some of the above.