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.
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.