In the recent article Some promising career ideas beyond 80,000 Hours' priority paths, Arden Koehler (on behalf of the 80,000 Hours team) highlights the pathway “Become a historian focusing on large societal trends, inflection points, progress, or collapse”. I share the view that historical research is plausibly highly impactful, and I’d be excited to see more people explore that area.
I commented on that article to list some history topics I’d be excited to see people investigate, as well as to provide some general thoughts on the intersection of history research and effective altruism. Arden suggested I adapt that comment into a top-level post, which led me to write this.
Note that:
- As zdgroff points out, you don’t actually have to be a historian to do this sort of historical research. (I’d add that you don’t even necessarily have to be in academia at all.)
- I’m sure there’s at least some relevant existing work on each of these topics. What I’m suggesting is that it seems likely there’s room for more work, work better targeted towards informing decisions in areas EAs care about, and/or summaries and syntheses of existing work (for EAs unfamiliar with that work).
- I have basically no background in academic history myself, am only ~6 months into my EA-aligned research career, and wrote this post fairly quickly.
- I lean towards longtermism, which influenced which history topics came to mind for me.
- Thus, this post should be seen merely as a starting point. I expect I’ve failed to include some topics it could be valuable to investigate.
- I’d therefore be really keen to see people comment on this post to mention additional topics, their thoughts or criticisms regarding anything I say here, or additional general thoughts on the intersection of history research and EA.
10 history topics it might be very valuable to investigate
(Note: The article Some promising career ideas beyond 80,000 Hours' priority paths also mentions something similar to the 1st and 3rd of these topics.)
1. The history of various types of growth and progress (economic, intellectual, technological, moral, political, etc.)
Investigations into this topic could give us evidence about:
- What developments are likely in the future
- How tractable influencing the speed or direction of various forms of growth and progress might be, and what the best interventions for doing that might be
- How severe and lasting the consequences of civilizational collapse and global (but non-existential) catastrophes might be, and thus how much we should prioritise work on those issues
I'd include as part of this topic research into trends in various forms of violence over time. See e.g. The Better Angels of Our Nature and What are the implications of the offence-defence balance for trajectories of violence?
2. The history of societal collapse and recovery
Investigations into this topic could provide evidence about things like how high existential and global catastrophic risks are, how likely humanity is to recover from a collapse, how civilization might be changed by the process of collapse and recovery, and what we can do to reduce chances of collapse and/or increases chances of a positive recovery.
Some relevant sources can be found here.
3. The history of the growth, influence, collapse, etc. of various social and intellectual movements
Investigations into this topic could provide evidence relevant to what might happen to the EA movement or related movements (e.g., the rationality, animal advocacy, and AI safety communities). That could in turn help us assess how valuable an intervention that relies on the continued presence of a particular movement is, how much we should prioritise activities that would be robust to some degree of movement collapse, how valuable movement-building activities are, and what our philanthropic discount rate should be.
In addition to informing our predictions of how certain movements might grow, have influence, collapse, etc., investigations of this topic could inform our efforts to positively influence those processes. For example, if we learn more about what factors seem to have often made the collapse of movements somewhat similar to EA more likely, we can try to avoid or counteract such factors.
Some relevant sources can be found here.
4. The history of efforts to regulate technology (or otherwise influence the direction or applications of technological development)
See Grace and Grace. (I haven’t properly read those works, but they seem relevant to this topic, as well as the next topic topic.)
See here for sources related to differential progress, differential intellectual progress, and/or differential technological development.
5. The history of proliferation and nonproliferation efforts in the case of nuclear weapons or other weapons/technologies
This is of course related to the previous topic.
6. The history of predictions (especially long-range predictions and predictions of things like extinction), millenarianism, and how often people have been right vs wrong about these and other things
Investigations into this topic could give us evidence relevant to how much to trust predictions of various kinds, which is relevant to things like whether we're at the Hinge of History and how high existential risk is. We currently seem to know very little about this. See e.g. Muehlhauser, Aird, and Aird (draft; relevant section begins "How often have").
7. The history of moral circle expansion
Investigations into this topic could inform future efforts to expand moral circles along various dimensions (e.g., to nonhuman animals, to future humans, to future digital minds). Such investigations could also perhaps inform us on questions like how good the future is likely to be “by default”, and how much we should prioritise preventing extinction vs improving humanity’s likely trajectory conditional on survival (see Crucial questions for longtermists: Overview).
See here for some relevant sources.
8. The history of legal and political efforts to represent or benefit various neglected populations (future generations, animals, slaves, etc.)
Investigations into this topic could help us assess how much we should prioritise more efforts of this kind, and how best to implement such efforts. Additionally, as with investigations of the history of moral circle expansion, investigations of this topic could also perhaps inform us on questions like how good the future is likely to be “by default”, and how much we should prioritise preventing extinction vs improving humanity’s likely trajectory conditional on survival.
I expect some related work has been done by Tyler John (who has written Longtermist Institutional Design and Policy: A Literature Review) and the UK’s All-Party Parliamentary Group for Future Generations. But I don’t actually know the details of these people’s work.
9. Counterfactual history related to what factors might’ve led various totalitarian regimes to last a long time, and how long they might’ve lasted if those factors had been present
Relevant regimes include Nazi Germany and the Soviet Union.
Investigations of this topic could inform how high the risk from dystopias/totalitarianism is, and how we can reduce that risk.
I'd guess that mainstream historians won’t have neglected the question of what factors might have led those regimes to last, but will have neglected the question of just how long those regimes could’ve lasted. But that’s purely a guess.
See here for some relevant sources.
10. The history of risks and harms from individuals with above-average levels of various psychological traits (e.g., sadism, psychopathy, narcissism, machiavellianism)
For an idea of why this topic might be important, what some key questions might be, and what decisions could be informed by research into this topic, see Reducing long-term risks from malevolent actors.
This might involve looking into:
- The risks and harms caused by individuals like Hitler, Stalin, Mao, and Genghis Khan
- Whether these individuals indeed seem to have had high levels of relevant psychological traits, and whether those high levels seem to have preceded or followed them gaining power
- What conditions or institutions seem to have been successful in limiting risks and harms from such individuals in certain times and places
- Other such things.
(I may soon start doing research somewhat related to this topic. So if this topic seems interesting to you, feel free to get in touch.)
General thoughts on the intersection of history research and EA
From what I’ve seen, it seems that a recurring theme is that:
- EAs without a background in history have done relatively brief analyses of many of the above topics.
- Some such analyses can be found via some of the above links.
- To be clear, I’m not saying these analyses were bad, and in fact I’ve quite appreciated many of them.
- Other people have found those analyses very interesting, and have possibly made big decisions based on them.
- But there’s been no deeper or more rigorous follow-up analysis.
And I think there are also some of those topics, or some subtopics, that haven’t even had a brief analysis from EAs.
I know less about how neglected these topics are within mainstream academia. But it seems likely that there’s at least room for summaries and syntheses for EAs, and/or investigations that are better targeted towards informing decisions in areas EAs care about.
I'd therefore be quite excited to see more people in EA (or at least interacting with EA; see Community vs Network) who are skilled at and interested in history research. As noted above, such people could be historians, but could also be other academics or even people outside of academia.
A potential counterexample to the above “recurring theme” is AI Impacts' research into “historic cases of discontinuously fast technological progress”. My understanding is that that research has indeed been done by EAs without a background in history, but also that it seems quite thorough and rigorous, and possibly more useful for informing key decisions on that topic than work on that topic by most academic historians would’ve been. (But I hold that view very tentatively, and haven’t looked into that work in great detail.) I'm not sure if that's evidence for or against the value of EAs becoming historians.
EDIT: Jamie Harris suggests some of the Sentience Institute's research as potentially another counterexample to that "recurring theme", which sounds right to me.
There are also other considerations that push in favour of or against taking up projects or career pathways that haven’t yet been taken up by many EAs (including but not limited to history research). For example, doing that could provide more information value, but conversely could be harder because there’s less impact-focused advice or mentorship available for that pathway. For more on that matter, see Some promising career ideas beyond 80,000 Hours' priority paths and Thoughts on doing good through non-standard EA career pathways.
People who are considering doing EA-aligned research might find it useful to watch the EAG 2018 talk From the Neolithic Revolution to the Far Future: How to do EA History.
Finally, as mentioned earlier, this post should be seen merely as a starting point, and I’d encourage people to comment to mention additional topics, their thoughts or criticisms regarding anything I say here, or additional general thoughts on the intersection of history research and EA.
For a wider range of potentially valuable research projects one could do, see A central directory for open research questions.
I'm excited to see this post! Thanks for the suggestions. A few I hadn't considered. In general though, this is an area I've thought about in various ways, at various points, so here's my list of an additional "9 history topics it might be very valuable to investigate" (with some overlap with your list)!
I'll start with some examples of categories of historical projects we've worked on at Sentience Institute.
1. The history of past social movements
Some overlap with your categories 3 and 8. This is to inform social movement strategy. At Sentience Institute, we've been focusing on movements that are 1) relatively recent, and 2) driven by allies, rather than the intended beneficiaries of the movement. This is because we are focusing on strategic lessons for the farmed animal movement, although I've recently been thinking about how it is applicable to other forms of moral circle expansion work, e.g. for artificial sentience (I have a literature review of writings on this coming out soonish).
Conducted by SI:
Not conducted by SI, but highly relevant:
I've written a fuller post about "What Can the Farmed Animal Movement Learn from History" which discusses some methodological considerations; some of the discussion could be relevant to almost any "What can we learn about X from history" questions of interest to the EA movement. (As a talk here)
2. The history of new technologies, the industries around them, and efforts to regulate them.
This overlaps with your category 4. Sentience Institute's interest has been in learning strategic lessons for the field of cellular agriculture, cultured meat, and highly meat-like plant-based foods, to increase the likelihood that these technologies are successfully brought to market and to maximise the effects that these technologies have on displacing animal products.
Conducted by SI:
3. Assessing the tractability of changing the course of human history by looking at historical trajectory shifts (or attempts at them).
Covered briefly in this post I wrote on "How tractable is changing the course of history?" (March 12, 2019). I didn't do it very systematically. I was trying to establish the extent to which the major historical trajectory shifts that I examined were influenced by 1) thoughtful actors, 2) hard-to-influence indirect or long-term factors, 3) contingency, i.e. luck plus hard-to-influence snap decisions by other actors.
One approach could be to create (crowdsource?) a large list of possible historical trajectory shifts to investigate. Then pick them based on: 1) a balance of types of shift, covering each of military, technological, and social trajectory shifts, aiming for representativeness 2) a balance of magnitudes of the shifts, 3) time since the shift, 4) availability of evidence.
Some useful feedback and suggestions I had when I presented this work to a workshop by the Global Priorities Institute:
Some other topics I've thought about much more briefly:
4. The history of the growth, influence, collapse, etc. of various intellectual and academic movements.
Overlaps with your category 3. I think of this as quite different to the history of social movements. Separately from direct advocacy efforts, EA is full of ideas of research fields that could be built or developed. The ones I'm most familiar with are "global priorities research," "welfare biology," and "AI welfare science" but I'm sure there are either more now, or there will be soon, as EAs explore new areas. For example, there were new suggestions in David Althaus and Tobias Baumann, "Reducing long-term risks from malevolent actors" (April 29, 2020). So working out how to most effectively encourage the growth and success of research fields seems likely to be helpful
Various historical research to help to clarify particular risk factors for s-risks will materialise in the future
These could each be categories on their own. Examples include:
9. Perhaps lower priority, but broader studies of the history of various institutions
The focus here would be on building an understanding of the factors that influence their durability. E.g. at a talk at a GPI workshop I attended, someone (Phillip Trammel? Anders Sandberg?) noted a bunch of types of institutions that have had some examples endure for centuries: churches, religions, royalty, militaries, banks, and corporations. Why have these institution types been able to last where others have not? Within those categories, why have some lasted where others have not.
Other comments and caveats:
Thanks for sharing those topic ideas, links to resources, and general thoughts on the intersection of history research and EA! I think this post is made substantially more useful by now having your comment attached. And your comment has also further increased how excited I'd be to see more EA-aligned history research (with the caveats that this doesn't necessarily require having a history background, and that I'm not carefully thinking through how to prioritise this against other useful things EAs could be doing).
If you do end up making a top-level post related to your comment, please do comment about it here and on the central directory of open research questions.
Yeah, that sounds valuable. I generated my list of 10 topics basically just "off the top of my head", without looking at various research agendas for questions/topics for which history is highly relevant. So doing that would likely be a relatively simple step to make a better, fuller version of a list like this.
Yeah, that makes sense to me. I've now edited in a mention of SI after AI Impacts. I hadn't actively decided against mentioning SI, just didn't think to do so. And the reason for that is probably just that I haven't read much of that work. (Which in turn is probably because (a) I lean longtermist but don't prioritise s-risks over x-risks, so the work by SI that seems most directly intended to improve farm animal advocacy seems to me valuable but not a top priority for my own learning, and (b) I think not much of that work has been posted to the Forum?) But I read and enjoyed "How tractable is changing the course of history?", and the rest of what you describe sounds cool and relevant.
Focusing in on "I worry that they're too deep and rigorous and that this has drastically cut down the number of people who put the time into reading them" - do you think that that can't be resolved by e.g. cross-posting "executive summaries" to the EA Forum, so that people at least read those? (Genuine question; I'm working on developing my thoughts on how best to do and disseminate research.)
Also, that last point reminds me of another half-baked thought I've had but forgot to mention in this post: Perhaps the value of people who've done such history research won't entirely or primarily be in the write-ups which people can then read, but rather in EA then having "resident experts" on various historical topics and methodologies, who can be the "go-to person" for tailored recommendations and insights regarding specific decisions, other research projects, etc. Do you have thoughts on that (rather vague) hypothesis? For example, maybe even if few people read SI's work on those topics, if they at least know that SI did that research, they can come to SI when they have specific, relevant questions and thereby get a bunch of useful input in a quick, personalised way.
(This general idea could also perhaps apply to research more broadly, not just to history research for EA, but that's the context in which I've thought about it recently.)
Thanks! And, of course, I understand that our lists look different in part because of the different cause areas that we've each spent more time thinking about. Glad we could complement each others' lists.
Huh, weird, I'm not sure why I didn't do that for either of the case studies I've done so far -- I've certainly done it for other projects. At some point, I was thinking that I might write some sort of summary post (a little like this one, for our tech adoption case studies) or do some sort of analysis of common themes etc, which I think would be much more easily readable and usable. I'd definitely post that to the Forum. I don't think posting to the forum would make a lot of difference though, for us. This is mainly because my impression / intuition is that people who identify with EA and are focused on animal advocacy use the EA Forum less than people who identify with EA and are focused on extinction risk reduction, so it wouldn't increase the reach to the main intended audience much over just posting the research to the Effective Animal Advocacy - Discussion Facebook group and our newsletter. But that concern probably doesn't apply to many of the suggestions in your initial list.
I think there's some value in that. A few concerns jump to mind:
Slight tangent from the discussion here, but you might like to add "and their summary of "Foundational Questions for Effective Animal Advocacy" after where you've listed SI's research agenda on that post. This is essentially a list of the key strategic issues in animal advocacy that we think could/should be explored through further research. Once I've published my literature review on artificial sentience, I'd be keen to add that too, since that contains a large list of potential further research topics.
Thanks for those answers and thoughts!
And good idea to add the Foundational Questions link to the directory - I've now done so.