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:

• Kelly Anthis, "Social Movement Lessons From the British Antislavery Movement: Focused on Applications to the Movement Against Animal Farming" (December 1, 2017)
• Me, "Social Movement Lessons From the US Anti-Abortion Movement" (November 26, 2019)
• Me, "Social Movement Lessons from the US Anti-Death Penalty Movement" (May 22, 2020)
• Me, "Social Movement Lessons from the US Prisoners' Rights Movement" (should be out before the end of the month)

Not conducted by SI, but highly relevant:

• Włodzimierz Gogłoza, “Abolitionist outrage: what the vegan movement can learn from anti-slavery abolitionism in the 19th century” (January 20, 2020)
• Animal Charity Evaluators, "Children's Rights" (February 2018)
• Animal Charity Evaluators, "Environmentalism" (February 2018)

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:

• J. Mohorčich, "What can nuclear power teach us about the institutional adoption of clean meat?" (November 28, 2017)
• J. Mohorčich, "What can the adoption of GM foods teach us about the adoption of other food technologies?" (June 20, 2018)
• J. Mohorčich, "What can biofuel commercialization teach us about scale, failure, and success in biotechnology?" (August 21, 2019)

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:

• Gustav Arrhenius of Institute of Future Studies suggested to me that there was more rigorous discussion of grand historical theories than I was implying in that post. He recommended reading works by Pontus Strimling of the Institute of Future Studies, plus work by Jerry Cohen on Marxism plus by Marvin Harris on cultural materialism.)
• Christian Tarsney (GPI) suggested that a greater case for tractability is in shaping the aftermath of big historical events (e.g. world wars) rather than in causing the those major events to occur.
• William MacAskill (GPI) suggested that rather than seeking out any/all types of trajectory shifts, it might be more useful to look specifically for times where individuals knew what they wanted to change and then investigating whether they were able to do that or not. e.g. what's the "EA" ask for people at the time of the French Revolution? It's hard to know what would have been useful. There might be cases to study where people had a clearer ideas about how to shape the world for the better, e.g. in contributing to the writing of the bible.

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:

• 5. To what extent have past societies prioritised the reduction of risks of high amounts of suffering and how successful have these efforts been?
• 6. Historical studies of "polarisation and divergence of values."
• 7. "Case studies of cooperation failures" and other factors affecting the "likelihood and nature of conflict" (some overlap with your category 5. This was suggested by CLR. I had a conversation with Ashwin Acharya who also seemed interested in this avenue of research)
• 8. Study how other instances of formal research have influenced (or failed to influence) critical real-world decisions (suggested by CLR.)

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:

• Hopefully SI's work offers a second example of an exception to the "recurring theme" you note in that 1) SI's case studies are effectively a "deeper or more rigorous follow-up analysis" after ACE's social movement case study project -- if anything, 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, and 2) I at least had an undergraduate degree in history :D
• On the "background in history" thing, my guess is that social scientists will usually actually be better placed to do this sort of work, rather than historians. (Some relevant considerations here)
• Any of these topics could probably be covered briefly, with low rigour, in ~one month's worth of work (roughly the timeframe of my tractability post, for example), or could literally use up several lifetime's worth of work. It's a tough call to decide how much time is worth spending on each case study. Some sort of time capping approach could be useful.
• Relatedly, at some point, you face the decision of how to aggregate findings and analyse across different movements. I think we're close to this with the first two research avenues I mention that we've been pursuing at SI. So if anyone reading this has ideas about how to pursue this further, I'd be interested in having a chat!
• Many of the topics discussed here are relevant to Sentience Institute's research interests. If you share those interests, you could apply for our researcher opening at the moment.
• To write this post I've essentially just looked back through various notes I have, rather than trying to start from scratch and think up any and all topics that could be useful. So there's probably lots we're both missing, and I echo the call for people to think about areas where historical research could be useful.
• It's long been on my to-do list to go through GPI and CLR's research agendas more thoroughly to work out if there are other suggestions for historical research on there. I haven't done that to make this post so I may have missed things.
• I was told that the Centre for the Governance of AI's research agenda has lots of suggestions of historical case studies that could be useful, though I haven't looked through this yet.
• These topics probably vary widely in terms of the cost-effectiveness of time spent researching them. Of course, this will depend on your views on cause prioritisation.
• Once I've looked into the above lists and thought about this more, I might improve this comment and make my own top-level post at some point. I was planning to do that at some point anyway but you forced my hand (in a good way) by making your own post.
• I'm definitely interested in your interest in research for topic 10 on your list, so please keep me in the loop!

Mini meta tangent: Part of me wanted to call this “10 history topics it might be very valuable to investigate”. But I felt like maybe it’s good for EA to have a norm against that sort of listicle-style title, which promises a specific number of things, as such titles seem to be oddly enticing. It seems like maybe posts with that sort of title would grab more attention, relative to other EA Forum posts, than they really warrant. (I don't mean that any article with such a title would warrant little attention, just that they might get a "unfair boost" relative to other posts.)

I think my feeling on that was informed in part by Scott Alexander's writing on asymmetric weapons, in which he says, among other things:

Logical debate has one advantage over narrative, rhetoric, and violence: it’s an asymmetric weapon. That is, it’s a weapon which is stronger in the hands of the good guys than in the hands of the bad guys.

In this case, it's not about good guys vs bad guys, but about more useful vs less useful posts. Perhaps we should try to minimise the number of things that boost the attention an article gets other than things that closely track how useful the article is.

Meanwhile, I recently published a post I called 3 suggestions about jargon in EA. Maybe, with this in mind, I should’ve called that “Some suggestions about jargon in EA”, to avoid grabbing more attention than it warranted. (I didn't really think about this issue when I posted that, for some reason.)

Does anyone else have thoughts on whether EA should have a norm against listicle-style numbered titles, or on whether we already implicitly do have such a norm?

(By the way, I didn’t specifically aim to have 10 history topics in this post; it just happened to be that 9 initially came to mind, and then later I was thinking about the malevolence post so I added a 10th topic related to that.)

Oh, another very broad category of topics that I perhaps should've mentioned explicitly is the history of basically any specific topic EAs care about. E.g., history of concerns about animal welfare, arguments about AI risk and AI safety, the randomista movement, philanthropy ...

People interested in this post may also be interested in 80k's recent interview with Tom Moynihan "on why prior generations missed some of the biggest priorities of all". Here's a relevant excerpt:

---

Rob Wiblin: Let’s push on and talk about intellectual history as a high-impact career. So yeah, as far as I know, we’ve never had a historian on the show before, which obviously means we haven’t had an intellectual historian either. And I think you’re reasonably familiar with 80,000 Hours’ goal of trying to help people have a bigger social impact with their career. Do you think some listeners should consider intellectual history as a potentially valuable career path to go on? And if so, why?

Tom Moynihan: Yeah, so I think that insofar as longtermism, EA-aligned with longtermism is about affecting the far future, trying to shape it positively, I think that there is actually a good case for history — not necessarily intellectual history, but history broadly — to play a bigger role in this new way of approaching priorities based on long arcs of history. So I do think that it can be impactful in the sense that it can actually derive lots of information value, so you can gain these nice insights and these things that we’ve been talking about a lot of, you almost get a sense of the heuristics of background assumptions or ‘crucial considerations.’ So that’s the term that Bostrom uses to basically describe a piece of information or knowledge that changes your whole priorities. So I think the example he uses is, if you’re lost in the woods and you’re using a compass, then you realize your compass is broken, that’s a crucial consideration.

Rob Wiblin: I guess the idea being that it doesn’t just mean that you should go one degree to the right, it means that everything is thrown into doubt.

Tom Moynihan: Exactly. So I think that it can be high-impact in the sense that there is a lot of information value to be derived here. I’ve noticed, there’s a post on the EA Forum of potentially valuable research areas in history, I think those are all brilliant. I think there was also an 80,000 Hours post talking about non-standard careers outside of the major priority areas, and one of them was a historian with a long-term arc of history specialization. Yeah, and so I think that there’s definitely a scope for this. I think that historians tend to not be EA-aligned, so there’s value for EAs to go and become historians and figure out the useful stuff. However, it is a non-standard career, and it’s also highly competitive and risky. If you want to reliably have an impact, it’s definitely not one to be advised. But if you want to take a big risk, maybe yeah.

Rob Wiblin: I think that’s probably the case with almost all academic or research careers — that, again, it’s hits based. Most researchers don’t have a massive social impact, but some of them really make important discoveries. I guess I would encourage people to make peace with that, rather than just try to play it super safe, because that limits your options so severely.

Tom Moynihan: Yeah, so I think that that’s the basic message that I want to give, is that, I think there’s scope for a lot of valuable information to be mined here, but the problem with that is that you don’t know what information… Particularly when you’re trying to find these long-term arcs or these stories about intellectual, moral, material, economic progress, you don’t know what you’re looking for ahead of time. I know that applies to almost all search functions in a sense, but you don’t know if it’s going to pay out in the end. So yeah, I do think because of that non-standardness and riskiness, I think that’s definitely something to consider. But I do think that, to put it simply, in EA and longtermism there’s so much history, there’s so much talk of history. The hinge of history, moral circle expansion, these are all historical ideas, progress itself is a historical idea. So there’s definite scope to do valuable work here.

[...]

Rob Wiblin: Are there any particularly valuable questions within intellectual history that you’d like to see people investigate that haven’t already come up? We’ve talked about quite a few.

Tom Moynihan: So, I think the question of the history of moral circle expansion and what are the causes that shift people’s intuitions outside of the kind of baseline of prejudice. Because you can go back and find people arguing for various very forward-thinking moral positions earlier than that actually spilled out and became a wider movement or a wider cause. So, something must’ve happened to create that critical mass. I think that that could be interesting. The Needham question that I spoke about earlier, this question of why one civilization you have over here, it’s actually far more technologically advanced…how they have something like a steam engine to open doors in the palaces, but just decide not to use it elsewhere. And then you have another civilization where something happens there that means that science locks in as an institution that perpetuates itself, perpetuates knowledge in a unique way.

Tom Moynihan: What are the institutions behind that? I think that there’s interesting research to be done there. Of course, and this is one that I’ve seen in various places, is researching the dynamics of lock-in. So, instances in the past where we can see clear path dependence in culture, values, et cetera. Also, again, another obvious one is studying the rise and fall of civilizations. What creates civilizational resilience? I think that making inductions from the past is dangerous because when civilizations have risen and fallen in the past, often it wasn’t a globalized technological civilization in the same way we have today, but people who have worked in this field have already kind of made that point. Tech trees, I think, are a really important and interesting place to try and look at. In a sense recreating the evolutionary tree of life, trying to do that for technology. And then that leads me to the final one that I find really interesting.

Tom Moynihan: And this comes from an idea that I got from a researcher Karim Jebari. He has, I think it’s a preprint paper currently, but it’s called Replaying history’s tape. And he’s taking those ideas of contingency and convergence from the biological sciences and seeing if they can be meaningfully applied to civilization and cultural progress and technological progress. So, as I was saying earlier, I think we do tend to overestimate the convergence or the recurrence or repeatability of a lot of insights, ideas, technologies. And the line is of course blurred. I would really love a map of cultural progress across different cultures, civilizations, and trying to map how convergent some might be.

Tom Moynihan: And obviously the way of measuring this, and Jebari kind of puts this forward in the paper, is that if you can see a cultural practice appearing independently in lots of places, you can kind of presume that it’s convergent in the same way as evolution. It becomes interesting because then when you get a more globalized society, it can appear in one place and then spread. So, there’s lots of interesting questions there I think to be had. And then, again, that can affect our judgments of how severe certain collapse events or very destructive global catastrophic risks are. So, I think there’s lots to be done there.

Comment that came in from the EA Newsletter:

"I’m writing a PhD on alumni engagement with effective altruism as the philosophical background. I’m comparing six top 100 ranked universities in the world and their alumni engagement. The universities are Harvard, Penn State, Cambridge, Vienna, Uppsala, Helsinki. I am interested in any seminar or discussions about implementing effective altruism and historical research as I have been doing that myself for the past four years. I’m writing the PhD for the University of Helsinki for professor Laura Kolbe, I myself live on the Åland Islands." 

Pia Widén (pia.widen at aland.net)

Great write up, though I feel slight regret reading it as there are now a further 10 things in my life to be annoyed I don't know more about!

Maybe it would be valuable to try crowdsourcing research such as this?

Start a shared g-suite document where we can coordinate and collaborate. I would find it fairly fun to research one of these topics in my free time, but doubt I commit the full energy it requires to produce a thorough analysis.

I could write myself up publicly somewhere others can see, that I'm willing to work 7 hours a week, on eg. studying societal collapse. Then someone else looking to do the same, can coordinate and collaborate with me, and we could potentially produce a much better output.

Even if collaboration turns out to be unfruitful, coordination might at least prevent double work.

Good list! For next steps, I'd like to see one-pager research proposals, detailing gaps in the literature and the value-added of new work.

Great post!

I would love to see a study on the history of wellbeing and suffering. This is perhaps more challenging as our understanding of how people suffered in the past is (arguably) poorly understood (as is our understanding of exactly how/why people suffer today!). But a first order approximation could look at generic factors that we expect to correlate with wellbeing, such as the proportion of people living in slavery or servitude; the personal freedoms people had; the levels of violence; and so on. Then a more detailed study -- which would probably require expertise beyond history -- would be to look at more direct (but harder to find historically) indicators of wellbeing such as mental health, self-reported happiness, suicide rates, etc.

Ben Garfinkel writes:

I would be interested in an investigation into the history of existential risk concerns around nanotechnology and the lessons it might hold for the modern AI risk community.

The relevant section of that doc is quite interesting, and I recommend reading it. I raise this here since it's somewhat relevant to "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".

A friend of mine said, essentially, that:

• A lot of the topics in this post seem like just "the history of EA-related idea X"
• For some (but not all) of these topics, my friend doesn't really see a clear path to impact, and they think one would need to flesh out the case for why the history of X is particularly important to understand

I think those are basically fair points, but I'm fairly excited about research into these topics despite them. Here's the response I wrote to that friend of mine, which might be useful to other people who are trying to think about the value of EA-aligned history research (whether or not on these topics).

Yeah, I'd agree that my post doesn't explicitly outline paths to impact - or at least not very concrete ones - and that fleshing out and critiquing potential paths to impact would be a logical and useful early step. (The post was meant mainly as a starting point.)

But I'd be surprised if quality research into each of those topics wouldn't turn out to be at least fairly useful. (But that sentence could be said about way more things that EAs have time to research, so fleshing out the paths to impact would still be useful for prioritisation, as well as for crafting more specific research directions, making dissemination plans, etc. See also.)

The reason I'd be surprised is partly because of roughly the following generic argument:

"Understanding the history of a topic often seems to help in: 

• Predicting what will happen in future in relation to that topic
• Thinking about what one could/should do to intervene in that (including noticing common mistakes/pitfalls/downside risks)
• Thinking about what to do in relation to other topics that might be affected by this topic (e.g., maybe understanding things to do with AI, bio, and nuclear risks should influence which countries we prioritise engagement with or movement-building in or how we do that)

And it seems reasonable to assume that that'll be true for a given topic unless one has reason to believe otherwise.

So if a topic seems potentially quite relevant to efforts to improve the expected value of the long-term future, then understanding the history of it better will probably be useful."

(But there are definitely more than 10 topics that fit that description, so it could definitely be useful to create a longlist of a broader set of topics that seem to fit that description, sketch potential paths to impact for research on them, and get a rough sense of which ones should be highest priority. I'd guess that the "ideal top 10" would differ at least somewhat from what's in this post.)