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This is the first week of my PhD in PoliSci at Georgetown. I broadly agree with the utilitarian ethos of the EA movement so I want to use my career to do the most good (in addition to meeting my personal needs and wants). The first part of that journey is developing a schema for cause prioritization. Whichever research agenda I commit to in grad school, I will spent years or even decades specializing in to achieve impact. Therefore I can get huge benefits from picking a high-leverage research area.

Furthermore, I believe that some research interests are much greater in expected utility without a career cost. I dispute Yudkowsky's argument that QALY-hungry PhD students face a "no free energy" problem because I disagree that PhD students are competent at predicting the most career-advantageous research agenda. From my experience most PhD students choose their topic based on their subjective degree of interest and sense of comparative advantage, rather than adequately predicting the academic job market. Some students do seek high-expected-utility areas, so these areas could be more crowded. But the areas people consider valuable vary highly because of inadequate information sharing Robin Hanson argues they are log-normally distributed here .

Before I address a few specific research agenda I am considering, lets zoom out. How can i categorize the ways that political scientists help the world in general? This post lays out five broad categories of activities.

1. World Modeling

Most political scientists spend their time studying what causes what in the political world.

Michael Albertus studied why some democracies and autocracies redistribute land, and some do not. He finds that autocratic leaders tend to redistribute more land partly because it disrupts the base of landowning rivals
BdMS^2 developed the selectorate model to explain, among other things, why autocrats rule for longer than democrats and why democrats provide more public goods. From this they explain some important distortions and inefficiencies in government to government aid.
Vreeland uses rational choice models of autocrats decision to torture to explain why signatories to the Convention Against Torture actually torture more.

Much of this work is of direct relevance to utility-generating policy interventions. Much of it is of indirect relevance. Much work also is of no relevance.

Broadly, the marginal good I can do on a particular problem area is proportional to the suffering caused (or utility to be gained). For example, reducing the occurrence of civil wars would directly save a few hundred thousand lives, but also spare from devastation the economies of those countries reducing the long term deaths from disease and malnutrition, etc. IMO, Accelerating economic and growth and spreading democracy/slowing authoritarian growth have the highest expected return to political science in general.

Second, it depends on how much influence political science as a whole can have on the issue. For most problems this effect will be small because political scientists are poorer communicators than economists, actors rarely have an incentive to listen to us, and because new knowledge tends to be complicated.

Thirdly, it depends on the crowdedness of the field. My first paper is forthcoming on the politics of water access in Jordan. As one of the worlds most arid countries, tons of water scholars come to Jordan every year to write. To contribute to the literature, I had to find a more niche theoretical question to comment on, which takes longer and usually detracts from relevance. On a personal level I seem to be unusually good good at finding good questions in crowded fields.

2. Studying development political interventions

Another approach is to study altruistic interventions in politics, such as those by development organizations. In general these questions cover the same The most promising interventions I've seen borrow from randomista development and focus on political development. Really a subset of world modeling, each topic This area has two huge advantages over a randomly selected research question.

Firstly, there's already an audience for the work. Instead of shouting in the wind about voting systems, you can engage directly with the actors. For example, Radio Free Europe probably does care about improving grass roots democracy.

Secondly, this area can be surprisingly uncrowded. Here is a quote from Rachel Glennerster's 80k episode -

"I’ve been working on some political stuff, and the implementers we work with just really want to do it beautifully in three villages, and we’re trying to say, “No- whole country, whole country. How do you do this for the whole country?" (...) people want it to be perfect in a few places, rather than (...) slightly better, everywhere.

I suspect that perfectionism is an easy failure mode for an altruistic political scientist. Yes this intervention works slightly better but it still marginalizes this stakeholder / creates this other problem / fails 80% of the time because XYZ. These concerns can distract from the cost-effectiveness of the intervention.

It might be more effective to look for interested actors prior to specializing in an area, to more accurately predict high-impact topics.

3. Improving institutional decision-making

Ex. Eva Vivalts recent paper on how World Bank policymakers update their beliefs on new evidence from RCT's.

An optimistic view of this research agenda is that it multiplies the effectiveness of all other evidence for policy selection. For a broader introduction see effective thesis .

4. Designing new institutions from principles

Ex. Glen Weyl's quadratic voting

An ocean of ink has been used to take first principle which are desirable and create institutions that align with them. Glen Weyl and Robin Hanson seem to have had real success designing new institutions which could plausibly resolve currently intractable flaws in western democracies. Glen Weyl even got the Colorodo legislature to use it, with some success.

This cause area could significantly improve peoples lives in the rich countries as well as the poor. While rich countries suffer much less from extreme poverty, starvation and childhood illnesses, they often struggle to solve political disputes. The US, for example, struggles with patronage (aka porkbarrel) and NIMBYism. As more countries develop economically the problems of advanced polities will grow in importance. So from a long-term perspective redesigning democratic institutions is more compelling.

Broadly, I'm pessimistic about the expected utility of devoting myself here . Firstly, its been a crowded area of political science since Hobbes's Leviathan. Secondly, my comparative advantages lie in empirical work. Thirdly, the audience for bold redesigns of democratic institutions is small. Hanson himself has been so challenged by the discrepancy between people's stated motives and their actual motives that he moved to studying hidden motives.

5. Disseminating research findings

My preliminary research has found that economists have much more policy influence that political scientists, even on many "political" issues like constitutional design. I could speculate many reasons for this observation, but the most important is that economists work harder to disseminate their findings. They write reductionist blogs pitched at a non-academic audience example example . They write accessible books with clear connections to EA topics. Political scientists occasionally produce similar work - The Dictators Handbook is a masterpiece. But in general I suspect a great deal of good can be done by connecting audiences to results of political science research. Whatever topic I specialize in, i expected most of my impact to come from disseminating other peoples work.

Future work

My next article will look at a few research agenda to discuss their value in greater detail.

Writing this article has updated me toward working in area 2 and 5. I have comparative advantages in area 2 from past work on development interventions and my EA-inspired preference for cost effective interventions. I do not have strong comparative advantages in 5, but I suspect there are more QALY's per hour of work there than any other area.





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Hi, I did an econ PhD with similar motivations.

"I believe that some research interests are much greater in expected utility without a career cost. [....] From my experience most PhD students choose their topic based on their subjective degree of interest and sense of comparative advantage, rather than adequately predicting the academic job market. "

Maybe econ is different from poli sci, but my experience is that grad students are extremely attuned to what the academic job market rewards, and if they don't start out that way, their advisors eventually push them in that direction. How about choosing research topics that do have a career cost? Those areas tend to be quite neglected. Since the academic market rewards difficult, technical work, the sort of work that doesn't do well on the job market can also be fairly tractable. In my final year of my PhD, I asked faculty what they would recommend working on if you want to do good and don't care about career advancement. Their suggestions included

  • Descriptive work. David Deming's work on "The Growing Importance of Social Skills in the Labor Market" is a great example and did happen to publish well, but many attempts to document trends without proving their cause do not.
  • Replications. How common and prestigious this is depends on the field, but published replications remain rare in econ. Since replications don't require originality or great technical skill, they aren't rewarded by the academic job market. A replication could be an exact replica of a lab experiment, a re-analysis of a data set, or checking that code does what it's supposed to. This kind of work can be influential and get attention in the popular press even if it isn't publishable in an academic journal. (See one example here, or the infamous Reinhart and Rogoff spreadsheet error.) You'll probably have to do this for a class, but few of those coursework replications ever get published.
  • Meta-analyses -- also common in some fields and not in others.

I would guess that review articles and syntheses of others' ideas are also under-done, but tenured faculty have a strong comparative advantage in that kind of work.

I'd also love to see some meta-research on what researchers believe to be the highest-impact topics to study. Maybe you could ask faculty in your department what they would recommend an altruist work on? I wish I'd spoken to more of my professors about this since their suggestions were invaluable.

Thanks for the comment. I've decided the most important thing is to learn to do my own expected value analysis for research programs.

Maybe econ is different from poli sci, but my experience is that grad students are extremely attuned to what the academic job market rewards, and if they don't start out that way, their advisors eventually push them in that direction."

I've been exploring this, and it appears to be a difference between the disciplines. Not sure why yet.

Since the academic market rewards difficult, technical work, the sort of work that doesn't do well on the job market can also be fairly tractable."

This makes sense. For example, looking at why some countries start charter cities and some do not would be very qualitative and poorly rewarded. But it would be really high-QALY.

Descriptive work

That actually makes a lot of sense. There could be some great descriptive work on aid which is non-causal.

Replications get okay rewards in Poli-Sci, since you might find a different method decision and be able to publish a new results. I plan to do lots of these.

I'd also love to see some meta-research on what researchers believe to be the highest-impact topics to study. Maybe you could ask faculty in your department what they would recommend an altruist work on? I wish I'd spoken to more of my professors about this since their suggestions were invaluable.

Thanks for this advice. It is valuable and I have already started doing it. Responses vary by professor. Some of them are like "utility...for people...we've never asked that question in this field. I have no idea" and some are like "yes of course, here are my thoughts". As a culture, political science is surprisingly non-activist compared to economics, in the sense that many pol scientists take no normative positions. Lots to learn about here.

I think there's a bunch of prior thinking on fairly related questions:

I'm not saying it's bad to try to think through things yourself as a political scientist, but it perhaps it would be useful to contrast your thoughts with the analyses from related fields, to talk about how your question differs, and how your answers differ, insofar as they do.

Great suggestions.

Tyler John and Will MacAskill also have this paper, "Longtermist Institutional Reform" (in the forthcoming book The Long View, edited by Natalie Cargill).

Just read the paper and you are correct, my questions do differ. I should just make a post of my own about this I guess.

Firstly, I am skeptical that the future is best represented by creating special institutions. If people lose trust that their government cares about their interests the risks to democracy and state capacity are large, and introducing a new interest group endangers that trust. The alternative to directly representing the future is to consider which institutional arrangements create policies most beneficial to future people. They acknowledge a similar critique on page 15.

Future's assemblies - the analogy to the Irish assemblies is interesting. However, the Irish assemblies were selected for each issue separately, not for life. Here are several reasons they shouldn't be selected for life.

1. Selecting representatives for life greatly increases the benefits to actors that capture members.

2. Factions that by chance are under-represented in the future assembly must wait a long time for a change, so exiting is a more appealing option to them.

3. Are we sure why the Irish assemblors chose to think about the issue One possible explanation is that because they were only asked to make 1 decision, selecting an ideology and selecting a position on the issue were equally as cognitively expensive (they didn't have to think that hard). If that hypothesis is true, then when we ask the same set of assemblers to make many decisions they might realize that adopting an ideology makes the decision easier and they feel just as "right" afterward.

Well that's enough for now, I should get back to work. Thanks for sending the paper, hopefully I can write a full post on it.

I guess Tyler, Will, etc are approaching governance from a general, and highly idealised perspective, in discussing hypothetical institutions.

In contrast, folks like GovAI are approaching things from a more targeted, and only moderately idealised perspective. I expect a bunch of their questions will relate to how to bring existing institutions to bear on mitigating AI risks. Do your questions also differ from theirs?

The question of how best to represent the interests of future persons is a good core question. My problem is more with their method of answering it. There's a great tradition of political philosophers thinking "what would be the ideal institution according to X moral philosophy" and then designing an institution backward from that. I consider this approach both crowded and low-leverage (John and McAskill are more in a middle position). The alternative is to look at how institutions work in practice then judge them against different ethical objectives, which is a bit more neglected. I also think the second approach is more effective. So writing at the same questions as John and McAskill could have good added value. If I have time I will take a look at Gov AI

I think it would be useful to get a political science take on the question of what the probability might be of collapse of civilization/long-term future impact at different levels of severity of catastrophe. Intuitions vary orders of magnitude on this.

Hmmm. That is an interesting question.

I was thinking recently about how stable patronage networks are during currency collapses, which might bear on the question.

Very rapid state collapses have occurred when side lost access to arms, as in Afghanistan in 1992. Investigating state collapse instances to estimate how much economic or social damage causes state collapse should be possible.

The world wars probably contain the closest example of a middle-income country undergoing state-collapse. Come to think of it, you could make an argument that state collapse occurs quickly during food shortages by looking at Austria-Hungary's collapse in 1918. There could be interesting arguments there.

I think the collapse of a civilization is a bit conceptually unclear, so that would be very difficult to investigate. Is civilization collapsed when regional leaders cease to identify with a westphalian state? Is civilization collapsed when the social contract is rewritten to return to the coercive premodern order? To make these questions more practical, did Italy collapse in 1943, when Italy became divided but Italians mostly refused to kill each other. Or did Austria-Hungary collapse in 1918 when it broke up into multiple sovereignty? But I could assert a few different definitions then construct a set of cases for each of them.

I'll look into past work on this subject.

Good questions-usually when EAs talk about loss of civilization, they mean a loss of electricity/industry globally, or a loss of cooperation outside the tribe globally (loss of cities, the anthropological definition of civilization). One recent 80,000 Hours podcast guest estimated 10% chance of collapse of civilization with 2°C slow global warming. This has a survey with large variation in the percentage loss in value of the long-term future associated with full-scale nuclear war and with 10% agricultural shortfalls (e.g. regional nuclear war, such as India Pakistan). This has a poll with large variation in the percentage loss in the value of long-term future associated with either 10% or global loss of electricity/industry. This has a collection of existential risk estimates, and some relate to loss of civilization.

The electricity one is outside of our data range. States occasionally fail to provide electricity for weird price-politics reasons. But when that occurs, private sector electricity suppliers form fast (this can be a self-reinforcing policy as the new suppliers resist centralization). But that does suggest that as long as a community can pay for fuel, they will produce electricity. If our current institutions fail to provide electricity, people can form new ones fast.

I'll think about agricultural output for the moment. I would, anecdotally, assume political effects from that. Bread protests remain pretty common and many states continue bizarrely inefficient bread subsidies. Rulers probably do this because they believe that grain prices are related to their survival. Furthermore, if bread price increases are correlated with anti-government actions or violence, then it's plausible to to forecast an increase in civil wars with a 10% decrease in agricultural output.

But let's step back. By comparing changes in agricultural production with changes in grain prices I am comparing apples to oranges. The relevant object is the change in price of grains year-on-year. So how much would a 10% drop in agricultural production actually change the price of grains? And how has the salary of the very poor evolved relative to that price of grain over time? The global price of wheat has doubled once since WW2 . Of course there was also a major fuel shock that year. Country level data would probably be more useful for relating food price shocks to political effects.

A second problem is that the long term political effects could be negative or positive. Civil wars seem really bad for political systems partly because they often end in systems with more veto points and less independent problem-solvey states. But there's also evidence that the pressure of regime change is good, since it incentivizes a ruler to grow their economy to meet higher demands for food. De Mesquita and Easterly would both argue that leaders often lack incentives to improve the lives of their people (over satisfying narrow special interests). Translating changes in regime type to long term utility AFAIK has not been done, at least outside the most simplistic categories.

Actually, that could be a starting point. If we don't know the long term effects of majoritarian, minoritarian, concosiational, corporatist, monist, pluralist state structures, we cannot translate those values to long term utility. For example, it might be that majoritarian middle-income states are more likely to grow than minoritarians. Political scientists as a group hesitate t o assign utility values to different traits of political systems, so doing that would be fun and useful.

Sorry for rambling.

This says a trebling of grain prices is likely if there is an abrupt 10% food production shortfall. Rice price ~tripled in a year in 2007 - the shortfall was small but there were a lot of export restrictions. There has been some work on the correlation of food prices and riots and other political turmoil.

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