Some history topics it might be very valuable to investigate

post by MichaelA · 2020-07-08T02:40:17.734Z · score: 72 (33 votes) · EA · GW · 23 comments

Contents

  10 history topics it might be very valuable to investigate
    1. The history of various types of growth and progress (economic, intellectual, technological, moral, political, etc.)
    2. The history of societal collapse and recovery 
    4. The history of efforts to regulate technology (or otherwise influence the direction or applications of technological development)
    5. The history of proliferation and nonproliferation efforts in the case of nuclear weapons or other weapons/technologies
    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
    7. The history of moral circle expansion
    8. The history of legal and political efforts to represent or benefit various neglected populations (future generations, animals, slaves, etc.)
    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
    10. The history of risks and harms from individuals with above-average levels of various psychological traits (e.g., sadism, psychopathy, narcissism, machiavellianism)
  General thoughts on the intersection of history research and EA
None
23 comments

In the recent article Some promising career ideas beyond 80,000 Hours' priority paths [EA · GW], 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” [EA · GW]. 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:

10 history topics it might be very valuable to investigate

(Note: The article Some promising career ideas beyond 80,000 Hours' priority paths [EA · GW] 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:

On economic growth, see here [EA · GW] and here.

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? [EA(p) · GW(p)]

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 [EA · GW], 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 [EA(p) · GW(p)].

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 [EA · GW].

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 [EA(p) · GW(p)].

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 [EA(p) · GW(p)] 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 [EA · GW] and how high existential risk is [EA · GW]. We currently seem to know very little about this. See e.g. Muehlhauser, Aird [LW · GW], and Aird [EA · GW].

7. The history of moral circle expansion [EA(p) · GW(p)]

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 [EA(p) · GW(p)] 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 [EA · GW] from dystopias/totalitarianism [EA(p) · GW(p)] 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 [EA(p) · GW(p)] 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 [EA · GW].

This might involve looking into:

(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:

  1. 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.
  2. Other people have found those analyses very interesting, and have possibly made big decisions based on them.
  3. 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 [EA · GW]) 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 [EA(p) · GW(p)] 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 [LW · GW], 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 [EA · GW] and Thoughts on doing good through non-standard EA career pathways [EA · GW].

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 [EA · GW].

23 comments

Comments sorted by top scores.

comment by Jamie_Harris · 2020-07-11T13:06:31.465Z · score: 27 (9 votes) · EA(p) · GW(p)

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:

  • 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 [EA · GW]" (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!
comment by MichaelA · 2020-07-12T02:46:08.492Z · score: 3 (2 votes) · EA(p) · GW(p)

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 [EA · GW].

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.

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.

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

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.)

comment by Jamie_Harris · 2020-07-12T09:54:02.453Z · score: 3 (2 votes) · EA(p) · GW(p)

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.

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.)

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.

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.

I think there's some value in that. A few concerns jump to mind:

  • Historical case studies tend to provide weak evidence for a bunch of different strategic questions. So while they might not single-handedly "resolve" some important debate or tradeoff, they should alter views on a number of different questions. So a lot of this value will just be missed if people don't actually read the case studies themselves (or at least read a summary).
  • While I think I'm pretty good at doing these case studies to a relatively high standard in a relatively short amount of time (i.e. uncovering/summarising the empirical evidence), I don't think I'm much better placed than anyone else to interpret what the evidence should suggest for individual decisions that an advocate or organisation might face.
  • In practice, I've hardly ever had people actually ask me for this sort of summary or recommendation. Off the top of my head, I can only think of two occasions where this has happened.

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 [EA · GW].

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.

comment by MichaelA · 2020-07-12T10:51:56.570Z · score: 2 (1 votes) · EA(p) · GW(p)

Thanks for those answers and thoughts!

And good idea to add the Foundational Questions link to the directory - I've now done so.

comment by MichaelA · 2020-07-08T02:47:29.139Z · score: 11 (8 votes) · EA(p) · GW(p)

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 [EA · GW]. 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 [EA · GW] so I added a 10th topic related to that.)

comment by Ardenlk · 2020-07-08T12:46:45.520Z · score: 8 (5 votes) · EA(p) · GW(p)

We also had this choice with our other problems and other paths posts, and decided against the listicle style, basically for the reasons you say. I think there is a nacent/weak norm, and think it makes sense to uphold it. The main argument against is that is actually kind of helpful to know if something is a long list or a short list -- esp if I have a small bit of time and won't want to start something long.

comment by MichaelA · 2020-07-08T09:17:33.036Z · score: 10 (4 votes) · EA(p) · GW(p)

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 ...

comment by MathiasKirkBonde · 2020-07-11T01:54:44.376Z · score: 4 (3 votes) · EA(p) · GW(p)

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.

comment by MichaelA · 2020-07-11T02:13:27.039Z · score: 2 (1 votes) · EA(p) · GW(p)

That definitely sounds good to me. My personal impression is that there are many EAs who could be doing some good research on-the-side (in a volunteer-type capacity), and many research questions worth digging into, and that we should therefore be able to match these people with these questions and get great stuff stuff. And it seems good to have some sort of way of coordinating that.

Though I also get the impression that this is harder than it sounds, for reasons I don't fully understand, and that mentorship (rather than just collaboration) is also quite valuable.

So I'd suggest someone interested in setting up that sort of crowdsourcing or coordination system might want to reach out to EdoArad, Peter Slattery, and/or David Janku. The first two of those people commented on my central directory for open research questions [EA · GW], and David is involved with (runs?) Effective Thesis [EA · GW]. All seem to know more than me about this sort of thing. And it might even make sense to somehow combine any new attempts at voluntary research crowdsourcing or collaborations with initiatives they've already set up.

comment by Michael_Wiebe · 2020-08-27T21:40:25.620Z · score: 3 (2 votes) · EA(p) · GW(p)

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.

comment by MichaelA · 2020-08-28T05:56:15.467Z · score: 3 (2 votes) · EA(p) · GW(p)

Yeah, that seems a good next step to me too. 

Another potentially good next step: Just collect relevant sources (as I've done for various topics here [EA · GW]), or go a little further by making annotated bibliographies (as Vaidehi has done for EA analysess of social movements). One could limit this to just sources by historians, or could include any sources that seem relevant

And another potentially good next step would be to write some sort of literature review, or a collection of semi-polished notes. It might make sense to start small, just reading a few papers, not writing that many pages, and not worrying too much about polish. This could help highlight relevant sources and draw some tentative conclusions about how valuable further work would be. But this also might be an ok end-goal for many topics, as often we might be fine with just summaries of the work that exists and its implications for EA, rather than "original research".

I'd encourage anyone interested in these topics to consider taking any of those next steps (including writing research proposals)!

Also, regarding the research proposals idea: I happen to have already essentially written research proposals regarding collapse & recovery, moral circle expansion, and sort-of some other topics. These range in length from a few paragraphs to a few pages. They've been written with job and grant applications in mind, so I haven't posted them to the forum yet. But I plan to post them in the coming weeks/months, and I'm happy to share them as they stand with anyone who's interested. (I have lots of ideas, so if anyone is really excited to pursue something like one of my ideas, I'm happy for them to take that one. Also happy to collaborate, get feedback, etc.)

(Typically I'm not thinking of history alone, but rather some blend of history, psychology, political science, and often other disciplines. But history tends to be in the mix.)

comment by paulk444 · 2020-08-25T07:32:53.078Z · score: 3 (2 votes) · EA(p) · GW(p)

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.

comment by MichaelA · 2020-08-25T10:06:04.878Z · score: 2 (1 votes) · EA(p) · GW(p)

Thanks!

Yeah, I share the view that either more research on that topic or a summary of existing for EAs would be valuable. (I imagine a lot of relevant work on that already exists, but I've been wrong about such things before, and in any case it could be good for someone to read it and extra the most EA-relevant insights.)

I think I'd see this as an (important) subset of "1. The history of various types of growth and progress (economic, intellectual, technological, moral, political, etc.)". Would you agree?

(That wouldn't negate the value of your comment - many of the topics I listed are very broad, and this post becomes more useful to people if commenters break them down into more specific topics, suggest ways they could be investigated, etc.)

comment by paulk444 · 2020-08-28T07:50:16.920Z · score: 3 (2 votes) · EA(p) · GW(p)

I agree that the "first approximation" I mentioned -- looking at generic factors that we expect to correlate with wellbeing, such as slavery or servitude, personal freedoms, violence -- would be a subset of "1. The history of various types of growth and progress...".

But I feel like a more detailed investigation of wellbeing/suffering through history lies outside of "1. The history of various types of growth and progress...". I say this because what we call "progress" does not necessarily correlate with wellbeing/suffering. And I think this *might* lead charities and movements such as EA to potentially overestimate the effects of intuitively useful interventions. I should add that this is potentially speculative and controversial! But I feel that there are important questions that haven't been fully tackled: Does growth really improve wellbeing? Does increasing life expectancy really reduce suffering, or does it make people overly sensitive to death? Were people in previous centuries -- where violence and disease were high -- as unhappy as we'd expect if we just look at these factors? Or are there more subtle factors that affect happiness?

Sometimes I feel like "progress" is about "satisfying people's stated preferences" rather than "making people happy". And what we think we want isn't always what makes us happy!

So rather than looking directly at violence, growth, death rates, etc, (which I expect has been done many times), I'd like to see a detailed study that looks at more direct indicators of wellbeing such as mental health, self-reported happiness, suicide rates -- and many more. And then a comparison between this and the usual "progress" studies. Perhaps this has also been done though and I've missed it.

Anyway I'd be very interested to hear what you think as I've not properly discussed these ideas before!

comment by MichaelA · 2020-08-28T10:31:17.190Z · score: 2 (1 votes) · EA(p) · GW(p)

I have a draft, which I'll hopefully publish in the coming weeks/months, on "Will humanity achieve its full potential, as long as existential catastrophe is prevented?"

I think an argument in favour of "Yes" is that it might be highly likely that, if we don’t suffer an existential catastrophe, there will be positive trends across the long-term future in all key domains. And I think that that argument could in turn be supported by the argument that such trends have been the norm historically, or that human agency will ensure such positive trends.

 So I thought a bit about how true that seems to be. I'll quote the relevant part of the draft, as it seems somewhat relevant here. (Note that I'm not an expert, and barely even did any googling; this was based on intuitions and what I happened to already know/believe.)

---

  • I believe there’s strong evidence that there have been positive trends in many domains in many periods and places before the Industrial Revolution. Relevant domains may include violence levels, the size of people’s moral circles, and use of reason and scientific thinking.
    • See e.g. The Better Angels of Our Nature.
  • I believe there’s some evidence that this represents a fairly widespread pattern. But I’m less certain of that. And there’ve definitely been “negative” trends in certain domains, times, and places (e.g., [insert example here; I have some ideas but should Google them]).
  • I believe there’s strong evidence that, since sometime around the Industrial Revolution, there have been positive trends across most of the world and in most domains that matter.
  • But even since the Industrial Revolution, there have been at least some negative trends or stagnation in some domains, times, and places. And these might include some of the “most important” domains, times, and places in relation to evaluating the FINE hypothesis.
    • Here are some plausibly important domains where I think there’s at least some evidence of negative trends recently in the developed world:
      • Human-caused animal suffering (especially on factory farms)
      • Political discourse
      • Political polarisation
      • Respect for science, scientists, and/or truth
      • Mental health [maybe also suicide rates? should google this]
      • Drug abuse
      • Incarceration rates (perhaps especially or only in the US)
      • Economic inequality
    • There were also some negative trends in particular domains, times, and places that were later reversed, but seem like they plausibly could’ve become quite lastingly bad. E.g., various trends in Germany and Russia leading up to and during WWII.
    • And there are plausibly important domains for which I’m not aware of evidence of substantial progress recently (e.g., democratisation in China).

Overall, I think historical trends are more consistent than inconsistent with the [argument that, if we don’t suffer an existential catastrophe, there will be positive trends across the long-term future in all key domains]. But that the matter isn’t totally clear-cut, and would likely benefit from much more detailed analysis.

comment by Stefan_Schubert · 2020-08-28T11:12:09.498Z · score: 6 (3 votes) · EA(p) · GW(p)
"Will humanity achieve its full potential, as long as existential catastrophe is prevented?"
I think an argument in favour of "Yes" is that it might be highly likely that, if we don’t suffer an existential catastrophe, there will be positive trends across the long-term future in all key domains.

That there will be positive trends doesn't necessarily entail that humanity (or some other entities) will achieve its full potential, however. It's possible that the future will be better than the present, without humanity achieving its full potential. And the value difference between such a future and a future where humanity achieves its full potential may be vast.

I agree that there is an historical argument for positive future trends, but it seems that one needs additional steps to conclude that humanity will achieve its full potential.

comment by MichaelA · 2020-08-28T13:43:49.513Z · score: 6 (3 votes) · EA(p) · GW(p)

Yeah, I definitely agree. This was part of my motivation for writing that draft. (Also, even if just "positive trends" was enough - which I agree that it isn't - finding that were positive trends in the past doesn't guarantee there will be positive trends in the future.)

More broadly, my impression is that some EAs are very confident the answer to the titular question is "Yes", and I feel like I haven't seen very strong arguments for such high confidence.

The draft is not necessarily arguing in favour of "Yes" (or "No") overall; it's primarily intended to highlight the question and stimulate and scaffold discussion.

(Happy to share the draft, if you or others are interested.)

comment by Stefan_Schubert · 2020-08-28T14:02:17.639Z · score: 2 (1 votes) · EA(p) · GW(p)

Thanks, yes I'd be interested.

comment by MichaelA · 2020-08-28T18:04:40.776Z · score: 4 (2 votes) · EA(p) · GW(p)

Ok, I've sent you a message :)

comment by MichaelA · 2020-08-28T10:26:18.347Z · score: 2 (1 votes) · EA(p) · GW(p)

I think these are good points.

Stepping back first: I'm quite morally uncertain [EA · GW], but the moral theory I have the highest degree of belief in is "something like classical hedonistic utilitarianism, with a moral circle [EA · GW] that includes basically sentient beings, across any point in time". (My moral circle therefore may or may not include mammals, insects, digital minds, etc., depending on whether they "empirically turn out to be sentient" - though it's quite unclear what that means. For expected value reasons, concerns about digital minds, insects, etc. play a substantial role in my priorities.)

The classical hedonistic utilitarianism bit (setting aside the moral circles bit) makes me very strongly inclined to agree that: 

  1. what really matters is how (human) wellbeing has changed over time, and 
  2. that it's unfortunate that discussion/studies of "growth" and "progress" often focus on things that may not be strongly correlated with (human) wellbeing. 

I'd say the focus is, as you suggest, often on "satisfying people's stated preferences". But I'd even go further and say that it's often on one of the following things:

  • what the person in this discussion or doing this study thinks is a typical or ideal preference
  • what that person themselves thinks is terminally valuable (regardless of preferences)
  • whatever is easiest to measure/discuss and seems plausibly related somehow to wellbeing, preferences, or valuable things

Two EAs who've done what seems to me good work in relation to subjective wellbeing, its measurement, and its correlation with other things are Michael Plant [EA · GW] and Derek Foster. (Though I don't think they focused much on history.) 

...but then there's the moral circles bit. This makes me think that (a) human wellbeing is unlikely to be a dominating concern, and (b) wellbeing at the moment or so far is unlikely to be a dominating concern. 

So I care about present-day human wellbeing primarily to the extent that it correlates with across-all-time, across-all-sentient-life wellbeing. And this means that, for instrumental reasons, I probably actually should pay more attention to other proxies, like GDP or technological developments, than to wellbeing. (This doesn't mean it's clear to me that GDP growth or technological developments tend to be good, but that they're likely important, for good or ill. See differential progress [? · GW].)

So, in contrast to what I might have said a few years ago when my moral circle hadn't expanded to consider nonhumans and future beings more, I wouldn't personally be extremely excited about historical analysis of changes in human wellbeing over time, and what affected those changes. But:

  • I think that'd be quite exciting from a human-centric, non-longtermist perspective
  • I think it's still net-positive, and maybe quite positive, from my perspective, because understanding this may help us make various predictions about important aspects of the future, and work out how we should intervene
    • I'll sort-of elaborate on this in a separate comment
comment by paulk444 · 2020-08-28T18:17:30.714Z · score: 1 (1 votes) · EA(p) · GW(p)

You've made some really good points here and I agree with most of it! And we're on the same page in terms of "hedonistic utilitarianism, with a moral circle [EA · GW] that includes basically all sentient beings, across any point in time".

I guess my main motivation for wanting to see a historical study of well-being is because I feel that, to fully understand what makes humans happy, it is valuable to consider a wide range of possible human life experiences. Studying history does this: we can consider a wide range of societies, lifestyles, circumstances etc, and ask which humans were happy and which were suffering. And comparing this to standard "progress" measures such as violence and life expectancy can help us understand whether interventions to improve such measures are the best we can do. Then this can help us design and implement future strategies to improve well-being moving forward.

comment by Ardenlk · 2020-07-08T12:41:23.976Z · score: 3 (2 votes) · EA(p) · GW(p)

Thank you for writing this up!

comment by MichaelA · 2020-08-24T18:24:11.176Z · score: 2 (1 votes) · EA(p) · GW(p)

Update: I've now created the Facebook group History and Effective Altruism, to hopefully serve as one home for people interested in these and other topics at the intersection of EA and history. 

This was prompted by: 

  • me having become even more convinced over the last month of the value of historical research
  • this post being featured in the EA newsletter, alongside a call for historically inclined people to engage on the forum

I'd encourage anyone interested to join that group!