We should evaluate research less by asking āhow immediately action-relevant or impactful is this?ā and more by asking āhas this isolated a plausibly relevant question, and does it a good job at answering it?ā.
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, Iād rather have 10 thorough takes on different subquestions Y_1, ā¦, Y_10, even if itās 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 werenāt 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 didnāt 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 useāthere probably are other examples where the delayed use/ābenefit is more surprising.)
Itās 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.
Itās also important because non-EA actors often have different criteria for when theyāre willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like āthis seems 30% likely to me, even if I canāt fully defend this or even say why exactly I believe thisā (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act theyāll need more legible arguments.
One recent examples thatās salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrennerās paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question āHow much should this paper update our all-things-considered view on whether itās net good to accelerate economic growth?ā. It strikes me that this is very different from the questions Iād 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 didnāt even occur to me to update my all-things-considered take on whether itād be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect thatās relevant to this question. Once we have 10 to 100 papers like it, I think Iāll 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 āI spent 40 hours researching whether accelerating economic growth is net good, and here is what I thinkā simply is not.
Interesting, thanks. Iām 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, Iād rather have 10 thorough takes on different subquestions Y_1, ā¦, Y_10
My first thought was āBut wait, wouldnāt 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?ā But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be āshallowā in relation to the larger topicāi.e., the āshallow takesā involve the same amount of total analysis as the āthorough takesā, but theyāre analysing such a big topic that they can only provide a shallow look at each component. Is that right?
the āshallow takesā involve the same amount of total analysis as the āthorough takesā, but theyāre analysing such a big topic that they can only provide a shallow look at each component
Yes, thatās what I had in mind. Thanks for clarifying!
Thanks, thatās helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because Iām thinking about getting economics training, which seems useful for answering specific sub-questions in detail (āExistential Risk and Economic Growthā being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
I think youāre very likely doing this anyway, but Iād recommend to get a range of perspectives on these questions. As I said, my own views here donāt 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, Iād rather have 10 thorough takes on different subquestions Y_1, ā¦, Y_10, even if itās 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 werenāt 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 didnāt 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 useāthere probably are other examples where the delayed use/ābenefit is more surprising.)
Itās 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.
Itās also important because non-EA actors often have different criteria for when theyāre willing to act on research findings. I think EAs tend to be unusually willing to act on epistemic states like āthis seems 30% likely to me, even if I canāt fully defend this or even say why exactly I believe thisā (I think this is good), but if they wanted to convince some other actor (e.g. a government or big firm) to act theyāll need more legible arguments.
One recent examples thatās salient to me and illustrates what strikes me as a bit off here is the discussion on Leopold Aschenbrennerās paper on x-risk and growth in the comments to this post. A lot of the discussion seemed to be motivated by the question āHow much should this paper update our all-things-considered view on whether itās net good to accelerate economic growth?ā. It strikes me that this is very different from the questions Iād 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 didnāt even occur to me to update my all-things-considered take on whether itād be good to accelerate growth much, I think the paper does a really thorough job at modeling one aspect thatās relevant to this question. Once we have 10 to 100 papers like it, I think Iāll 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 āI spent 40 hours researching whether accelerating economic growth is net good, and here is what I thinkā simply is not.
Interesting, thanks. Iām 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 āBut wait, wouldnāt 10 thorough takes take more time than 10 shallow takes, making this comparison unfair?ā But now I think maybe you meant both sets of investigations to take a similar amount of time, but the former to be āshallowā in relation to the larger topicāi.e., the āshallow takesā involve the same amount of total analysis as the āthorough takesā, but theyāre analysing such a big topic that they can only provide a shallow look at each component. Is that right?
Yes, thatās what I had in mind. Thanks for clarifying!
Iām confusedādid 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, thatās helpful for thinking about my career (and thanks for asking that question Michael!)
Edit: helpful for thinking about my career because Iām thinking about getting economics training, which seems useful for answering specific sub-questions in detail (āExistential Risk and Economic Growthā being the perfect example of this), but one economic model alone is very unlikely to resolve a big question.
Glad itās helpful!
I think youāre very likely doing this anyway, but Iād recommend to get a range of perspectives on these questions. As I said, my own views here donāt feel that resilient, and I also know that several epistemic peers disagree with me on some of the above.