Comments
Thinking about insights that were particularly relevant for me / my values:
- Reducing long-term risks from malevolent actors as a potentially promising cause area
- The importance of developing (the precursors for) peaceful bargaining strategies
- Related: Anti-realism about bargaining? (I don't know if people still believed this in 2015, but early discussions on Lesswrong seemed to indicate that a prevalent belief was that there exists a proper solution to good bargaining that works best independently of the decision architecture of other agents in the environment.)
- Possible implications of correlated decision-making in large worlds
- Arguably, some people were thinking along these lines before 2015. However, so many things fall under the heading of "acausal trade" that it's hard to tell, and judging by conversations with people who think they understood the idea but actually mixed it up with something else, I assign 40% to this having been relevantly novel.
- Some insights on metaethics might qualify. For instance, the claim "Being morally uncertain and confidently a moral realist are in tension" is arguably a macrostrategically relevant insight. It suggests that more discussion of the relevance of having underdetermined moral values (Stuart Armstrong wrote about this a lot) seems warranted, and that, depending on the conclusions from how to think about underdetermined values, peer disagreement might work somewhat differently for moral questions than for empirical ones. (It's hard to categorise whether these are novel insights or not. I think it's likely that there were people who would have confidently agreed with these points in 2015 for the right reasons, but maybe lacked awareness that not everyone will agree on addressing the underdetermination issue in the same way, and so "missed" a part of the insight.)
I think there haven’t been any novel major insights since 2015, for your threshold of “novel” and “major”.
Notwithstanding that, I believe that we’ve made significant progress and that work on macrostrategy was and continues to be valuable. Most of that value is in many smaller insights, or in the refinement and diffusion of ideas that aren’t strictly speaking novel. For instance:
The ideas behind patient altruism have received substantial discussion in academia:
But this literature doesn't seem well-known among EAs. I personally didn't know about any of it until Phil Trammell cited some of it in his paper on patient philanthropy. Trammell also argued that most people use too high a discount rate, so patient philanthropists should compensate by not donating any money; as far as I know, this is a novel argument.
This has been much discussed from before the beginning of EA, Robin Hanson being a particularly devoted proponent.
Hanson has advocated for investing for future giving, and I don't doubt he had this intuition in mind. But I'm actually not aware of any source in which he says that the condition under which zero-time-preference philanthropists should invest for future giving is that the interest rate incorporates beneficiaries' pure time preference. I only know that he's said that the relevant condition is when the interest rate is (a) positive or (b) higher than the growth rate. Do you have a particular source in mind?
Also, who made the "pure time preference in the interest rate means patient philanthropists should invest" point pre-Hanson? (Not trying to get credit for being the first to come up with this really basic idea, I just want to know whom to read/cite!)
I don't know the provenance of the idea, but I recall Paul Christiano making the point about pure time preference during the debate on giving now vs later at the ?2014 GWWC weekend away.
My recollection is that back in 2008-12 discussions would often cite the Stern Review, which reduced pure time preference to 0.1% per year, and thus concluded massive climate investments would pay off, the critiques of it noting that it would by the same token call for immense savings rates (97.5% according to Dasgupta 2006), and the defenses by Stern and various philosophers that pure time preference of 0 was philosophically appropriate.
In private discussions and correspondence it was used to make the point that absent cosmically exceptional short-term impact the patient longtermist consequentialist would save. I cited it for this in this 2012 blog post. People also discussed how this would go away if sufficient investment was applied patiently (whether for altruistic or other reasons), ending the era of dreamtime finance by driving pure time preference towards zero.
Sorry--maybe I’m being blind, but I’m not seeing what citation you’d be referring to in that blog post. Where should I be looking?
The Stern discussion.
The post cites the Stern discussion to make the point that (non-discounted) utilitarian policymakers would implement more investment, but to my mind that’s quite different from the point that absent cosmically exceptional short-term impact the patient longtermist consequentialist would save. Utilitarian policymakers might implement more redistribution too. Given policymakers as they are, we’re still left with the question of how utilitarian philanthropists with their fixed budgets should prioritize between filling the redistribution gap and filling the investment gap.
In any event, if you/Owen have any more unpublished pre-2015 insights from private correspondence, please consider posting them, so those of us who weren’t there don’t have to go through the bother of rediscovering them. : )
"The post cites the Stern discussion to make the point that (non-discounted) utilitarian policymakers would implement more investment, but to my mind that’s quite different from the point that absent cosmically exceptional short-term impact the patient longtermist consequentialist would save."
That was explicitly discussed at the time. I cited the blog post as a historical reference illustrating that such considerations were in mind, not as a comprehensive publication of everything people discussed at the time, when in fact there wasn't one. That's one reason, in addition to your novel contributions, I'm so happy about your work! GPI also has a big hopper of projects adding a lot of value by further developing and explicating ideas that are not radically novel so that they have more impact and get more improvement and critical feedback.
If you would like to do further recorded discussions about your research, I'm happy to do so anytime.
Thanks! No need to inflict another recording of my voice on the world for now, I think, but glad to hear you like how the project coming.
It seems you're right. I did a little searching and found Hanson making that argument here: https://www.overcomingbias.com/2013/04/more-now-means-less-later.html
That post just makes the claim that "all we really need are positive interest rates". My own point which you were referring to in the original comment is that, at least in the context of poverty alleviation (/increasing human consumption more generally), what we need is pure time preference incorporated into interest rates. This condition is neither necessary nor sufficient for positive interest rates.
Hanson's post then says something which sounds kind of like my point, namely that we can infer that it's better for us as philanthropists to invest than to spend if we see our beneficiaries doing some of both. But I could never figure out what he was saying exactly, or how it was compatible with the point he was trying to make that all we really need are positive interest rates.
Could you elaborate?
I liked this answer.
One thing I'd add: My guess is that part of why Max asked about novel insights is that he's wondering what the marginal value of longtermist macrostrategy or global priorities research has been since 2015, as one input into predictions about the marginal value of more such research. Or at least, that's a big part of why I find this question interesting.
So another interesting question is what is required for us to have "many smaller insights" and "the refinement and diffusion of ideas that aren’t strictly speaking novel"? E.g., does that require orgs like FHI and CLR? Or could we do that without paid full-time researchers, just via a bunch of people blogging in their spare time?
I don't know about generating many smaller insights or refining ideas. But I'd guess that mere "diffusion" probably doesn't require full-time researchers, just good and well-respected communicators.
But I'd also guess that there's another thing that happened: Active critique and screening of a large set of potentially important insights, to identify those that are actually important and correct (or sufficiently likely to be correct to warrant major shifts in decisions). And that process seems likely to benefit substantially from having orgs like FHI and CLR. Both because the set of potentially important insights might be very large, and because effectively screening them might be something most people can't easily do.
And I'd guess that ideas tend to diffuse more and more as they do better in the screening process.
But I only got involved in EA in 2018, and only got inside peaks into some EA orgs this year, so a lot of the above is guesswork.
I think that's a very interesting question, and one I've sometimes wondered about.
Oversimplifying a bit, my answer is: We need neither just bloggers nor just orgs like FHI and CLR. Instead, we need to move from a model where epistemic progress is achieved by individuals to one where it is achieved by a system characterized by a diversification of epistemic tasks, specialization, and division of labor. (So in many ways I think: we need to become more like academia.)
Very roughly, it seems to me that early intellectual progress in EA often happened via distinct and actionable insights found by individuals. E.g. "AI alignment is super important" or "donating to the best as opposed to typical charities is really important" or "current charity evaluators don't help with finding impactful charities" or "wow, if I donate 10% of my income I can save many lives over my lifetime" or "oh wait, there are orders of magnitudes more wild than farmed animals, so we need to consider the impact of farmed animal advocacy on wild animals".
(Of course, it's a spectrum. Discussion and collaboration were still important, my claim is just that there were significantly more "insights within individuals" than later.)
But it seems to me that most low-hanging fruits have been plucked. So it can be useful to look at other more mature epistemic endeavours. And if I reflect on those it strikes me that in some sense most of the important cognition isn't located in any single mind. E.g. for complex questions about the world, it's the system of science that delivers answers via irreducible properties like "scientific consensus". And while in hindsight it's often possible to summarize epistemic progress in a way that can be understood by individuals, and looks like it could have been achieved by them, the actual progress was distributed across many minds.
(Similarly, the political system doesn't deliver good policies because there's a superintelligent policymaker but because of checks and balances etc.; the justice system doesn't deliver good settlement of disputes because there's a super-Salomonic judge but because of the rules governing court cases that have different roles such as attorneys, the prosecution, judges, etc.)
This also explains why, I think correctly, discussions on how to improve science usually focus on systemic properties like funding, incentives, and institutions. As opposed to, say, how to improve the IQ or rationality of individual scientists.
And similarly, I think we need to focus less on how to improve individuals and more on how to set up a system that can deliver epistemic progress across larger time scales and larger numbers of people less selected by who happens to know whom.
This is really interesting and I'd like to hear more. Feel free to just answer the easiest questions:
Do you have any thoughts on how to set up a better system for EA research, and how it should be more like academia?
What kinds of specialisation do you think we'd want - subject knowledge? Along different subject lines to academia?
Do you think EA should primarily use existing academia for training new researchers, or should there be lots of RSP-type things?
What do you see as the current route into longtermist research? It seems like entry-level research roles are relatively rare, and generally need research experience. Do you think this is a good model?
[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:
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:
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:
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:
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.