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.
- 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
- See also We Need a New Science of Progress.
- 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
- For example, let’s say humanity is currently experiencing various positive trends, but we discover these trends aren’t very common across different times and societies and appear to depend on many conditions being just right. We might then have additional reason to see that trend as “fragile” and worth protecting from various types of disruptions.
- See The long-term significance of reducing global catastrophic risks and Civilization Re-Emerging After a Catastrophic Collapse.
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 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.
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 also On the longtermist case for working on farmed animals [Uncertainties & research ideas]. And 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.
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.
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.