Is voting theory important? An attempt to check my bias.
You may have seen either or both of my two prior posts here, in which I first said I’m beginning to seek a grant for some voting theory research after I graduate, and then looked into some of the possible sources of such a grant. In this post, I’ll dig into why I think that this research is important. I have plenty of ideas on that issue, and I’m using this writing as an opportunity to get them in order, so you should not expect this to be a well-organized post.
I think that voting theory is important; that is, that it is an area in which further study and the resulting insights can reasonably be expected to lead to improvements in collective welfare that are big enough to make opportunity costs essentially irrelevant. I also know that I’m biased; I’ve invested a significant portion of my identity into thinking about voting theory, and even if I could somehow be dispassionately rational in spite of that, an outside view would have to admit that my assessment of the importance of this area is an outlier.
I can’t possibly detach myself entirely from this bias, but I should at least try. So here, I’m going to argue both sides. First, I’m going to give the reasons that I think this is important; then, I’m going to try to make the best counterarguments I can; then, I’m going to try to weigh both sides. I think that this format, where I write out one side at a time, is probably a better idea than trying to do all three at once, which seems to be what happens when I do it in my head. Not that that interior arguing in circles can’t eventually lead to progress and insight; just that it seems a pretty inefficient and unreliable way of getting there.
I want to be clear about the purpose of writing this. It is, above all, to help me clarify my thinking. I’m going to post it publicly primarily because having a clear idea of my audience helps me write more clearly. I won’t deny that I have other motives in publishing this; I also hope to inspire, inform, and/or impress you. But when I have a choice between spending effort clarifying a point that I’m not yet clear on, and explaining one that I am, I’ll choose the former.
So, here goes:
Yes, voting theory is important.
Direct impact:
Public elections are pivotal for important stuff;
in principle, they could be done better, so as to get better immediate outcomes on average;
those improvements are possible in practice;
and a better understanding of voting theory can help make such improvements more probable.
I recognize that the four-step chain of logic above, though it starts on what I think is pretty solid ground, gets weaker with each link. Nevertheless, I think it almost certainly holds all the way to the end to at least some degree.
Indirect impact:
Aside from encouraging better immediate outcomes, better voting systems would shift the incentive structure for public debate, in a way that could tend to make it healthier over time. The above logic also works with this point in place of step 2.
Prescriptive philosophy:
I believe that understanding the paradoxes, difficulties, and possibilities of collective decisionmaking processes is useful in constructing ethical philosophy.
Ethical philosophy, in turn, is useful not just in everyday life choices, but in how we imagine, design, and collectively choose our future. This includes, but is not limited to, the issue of AI friendliness.
Descriptive philosophy:
Understanding voting theory means understanding multiparty, non-zero-sum, high-stakes (that is, not-frequently-repeated) games, and how the mechanisms in these games can be designed to promote relatively-positive-sum outcomes. This kind of understanding may be useful in thinking about a transhuman future.
This is not the same as the previous point, in which understanding collective decisionmaking is useful prescriptively, as a step in defining what human volition even is in the first place. In this case, it’s about understanding what a post-human-supremacy society of mind might look at descriptively.
No, voting theory isn’t important.
Arguing this side in a vacuum would mean trying to prove a negative. So I’ll mostly focus on refuting and/or undermining the arguments above, one point at a time.
Direct impact:
Public elections are pivotal for some things, but other collective decisionmaking processes (markets, corporate hierarchies, etc.) may be more important.
It’s easy to overestimate how important voting theory and voting methods are. For instance, it’s probable that the majority of the “democratic dividend”, the empirically better welfare of democracies as opposed to autocracies, comes from the mere fact that they allow peaceful transfers of power. A society that regularly chose a new leader by a peaceful lottery would also do better than an autocracy in which the only way to transfer power is through civil war.
Even if voting reform is a good idea in the abstract, it may be so difficult to accomplish as to make other reforms a better investment of effort. In particular, in my country — the USA — there are so many veto points that many reforms, especially any that would require a constitutional amendment, are nearly impossible.
Even if voting reform is both desirable and possible, it could be that we already understand exactly what is needed, so that further theoretical work is unnecessary.
Indirect impact:
As above, it’s easy to overestimate the importance of voting methods in structuring the public debate. You should be very skeptical of any suggestion that somebody’s idea will fix the public debate and substantially improve collective rationality.
Prescriptive philosophy:
Philosophers have had over half a century to come to terms with Arrow’s theorem, and they’re generally smart people. Why should any new ideas in voting theory have a significant impact on our understanding of ethics?
In terms of “ethical engineering” (that is, using ethics to design the future, not engineering ethics or engineering ethically), there are probably unanswered questions that come before voting theory. That’s especially true for friendly AI.
The fact I even bring up AI in this context probably has more to do with thinking that that’s a fun thing to talk about, or a reasonably high-status thing to talk about in this context, than with any actual connection between voting theory and AI. (Note: Raemon challenged me somewhat on a related point in a private message, and that’s probably the main reason I’m writing this now.)
Descriptive philosophy:
The chance that the quality of a post-human future actually hinges on our ability to understand now anything about what that future might look like is very, very small. The chance that voting theory will contribute meaningfully to our ability to understand anything about what that future will look like is also pretty small.
OK, so is it important?
So, now that I’ve played the role of lawyer for both sides, here’s where I play that of judge and jury. I realize that this is a stretch; no matter how fair I try to be, I can’t fully remove my bias, or at least not without subtracting an estimator of that bias whose variance would probably be a bigger problem.
Direct impact:
Public elections are not the only way important decisions get made, but they’re still quite important. I’m highly confident of this.
Better voting methods wouldn’t solve all problems or lead to a utopia, but they could help substantially. There’s plenty of research on how political systems correlate with economic or other outcomes, and while I don’t think any of it has successfully established causality, it’s still consistent with the idea that this stuff matters. I’m reasonably confident of this.
Voting reform has happened before in various contexts, and it should be expected that sooner or later and somewhere or other it will happen again. Will it happen in the particular ways and places I’d like it to? There’s no way to be sure either way, but I’d say that the probability is certainly over 1%, and the possible impact is large enough that moving that probability by anything over one chance in a million is worth my time. You could make a reasonable case that I am deluded to think I can have an effect that large, but it wouldn’t be a slam dunk. So I certainly could be wrong here, but when the question is “does anything you do matter at all” it’s better to err optimistically.
The debate among reform activists between various voting methods (IRV, approval, Condorcet, score, STAR, etc.; as well as the understanding of proportional representation) has progressed substantially in the 20 years that I’ve been a part of it, and I think it can progress further. I think I’m as well-positioned and well-qualified as anyone in the world to help that progress happen.
This is probably the point on which my bias as compared to an external view is largest, but it’s also the one on which my expertise is the deepest. So I’m going to take the internal view here, and say I think that my further work in this field can be helpful, but I’d certainly understand if you decide to differ.
Indirect impact:
From an internal view, I actually feel more confident that better voting methods would lead to a healthier public debate, than I do that they would lead to better outcomes in the narrower within-the-ballot-box sense. That is to say, I think that changing the incentive structure — the definition of “political fitness” — will affect political evolution more surely and predictably in a long-term sense than in a short-term, single-election sense.
But from an external view, it seems crazy to say that I can predict second-order effects more confidently than first-order ones. I guess that it’s not so crazy, though, if the second-order effects are smaller and more numerous, such that the law of large numbers applies. Still, it would be unhealthy to be too confident in such a long chain of justification.
Prescriptive philosophy:
Frankly, I think I can be confident that thinking about voting theory from this perspective is fun, but I can’t be confident that it’s important. At best, it could be. For me, “fun and not inconceivably important” is enough; YMMV.
Descriptive philosophy
As above, with an even lower chance of being important.
So all-in-all, I think it’s pretty reasonable for me to think this is worth my time, and even that the case for that is strong enough for me to look for a short-term grant. But in looking for that grant, I may end up making arguments towards the bottom of the thrice-repeated list above, in order to connect it to funders’ stated purposes, even though I am more confident in the arguments towards the top of that list. I think I’m OK with that, because I think that even the arguments at the bottom should be considered, and that there are few who can make them better than I.
Upvoted both for the helpful summary of considerations, as well as for (I think) following a pretty good algorithm (making a good faith effort to assess something important to your identity)
My current take is something like:
One one hand, in the end, I expect you’ll do the thing that your brain is naturally curious about and the justifications are mostly post-hoc. And that’s probably fine and I wouldn’t stress too much about it. I think a lot of good progress comes by people incrementally following their curiosities, and fighting against your natural curiosities doesn’t seem very practical for intellectual work.
But, insofar as your interests are malleable, I think it’d be worth asking more specific questions for each of the plausible ways voting-theory-might matter.
If the goal is “improve elections, largely because of their second-order effects”, then I’d ask what sort of progress is most bottlenecking that. (The answer may be more political than theoretical, and you may or may not be interested in doing political/activism work. But even narrowing the scope to theoretical progress, my guess is that problems vary in how relevant they are to the “get concrete reform passed for government elections”)
If the goal is “figure out how optimal decisionmaking should be made in the transhumanist future, or in CEV”, I’m guessing that the theoretical bottlenecks there are different for the nearterm election reform.
I think that there is a place for basic research here. By that I mean, research which, as much as possible, is motivated by fundamental bottlenecks, not by practical ones. Such research already exists in a tension between the specific and the abstract, and getting too abstract is one failure mode. My way of handling that tension is to metaphorically keep my feet on solid ground even as my eyes are on the horizon, and the specific immediate problems are that solid ground.
This is not to say that it is not good to look at the problem from the transhumanist angle, too. And in the countless hours I spend thinking about this stuff, a few of them point in that direction, even if I don’t write it all here. But I think that even if your primary focus is the transhumanist angle, you should be happy that I’m over here looking at the problem mostly from a different angle.
(“Your” there was directed to a generic/abstract reader, not specifically to Raemon.)
OpenPhil supported the Center for Election Science once, but they’re much more a political action group than a voting theory research group. They primarily do ballot initiatives and public education on what we already know.
If enacting your policies is the real bottleneck, then it makes sense that 90% of your argument is true, but it still doesn’t matter because you can’t enact political change.
I don’t know if I believe that, but it’s imaginable.
EDIT: After seeing that you know way more about this than I do, I’ll leave my thought here, but definitely defer to you.
Like Raemon, I want to echo the point that following your intellectual curiosity is probably the best way to do research work, and generally make the most of your energy/time budget. But some specific considerations:
1. What seems important to Vaniver.
I expect that voting systems mostly won’t matter for AI outcomes. It seems like the primary question is whether or not the AI system we make does anything like what we like/endorse (i.e. whether or not existential accidents happen), and the secondary question is whether or not teams coordinated to form a coalition to build such a safe system (or otherwise prevented the creation of unsafe systems). Voting seems mostly useful for aggregating preferences over scarce joint decisions in a bandwidth-sensitive way (“where should the group go to lunch?” as opposed to “what do you personally want to eat?”, or “which of these four candidates should be president?” as opposed to “what are your complete views on politics?”), and the coalition-building problem will likely look more like negotiation (see this paper by Critch as an example of the sort of thing that seems useful to me in that space) and the preference-satisfaction solution in the glorious transhuman future will likely look more like telling Alexa how you want your personal environment to be and not having to worry much about scarcity or joint decision-making.
It’s possible that government policy will be important, and the health of public discourse will be important, but it seems quite unlikely to me that election reforms will have the desired effects in time.
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2. Whether it’s the core problem of discourse, or will be sufficient to overcome modern challenges.
It seems like the forces pushing towards political polarization are considerably stronger than just the pressures from electoral systems, and mostly have to do with communication media stuff. Basically, current media technologies push the creation and curation of media closer to the consumer, who has different (and worse) incentives than elites, which leads to a general dumbing-down and coarsening of discourse. Superior election technology seems likely to help broadly-liked centrists defeat people who manage to eke out 51% support and 49% hate, but that doesn’t seem like it’ll fix discussions of cultural hot spots. (Will broadly liked centrists cause American politics to be more sensible on climate change, or the weird mix of negotiations about border security, or so on?)
Figuring out what’s upstream of worsening discourse and pushing on that (or seeking to create more good discourse, or so on) is probably more effective is better public conversations are actually the goal; and even if this effort helps, if it can’t help enough, it may be better to write off the thing that it would help.
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3. Whether or not it’s important if it seems important to Vaniver.
There’s a claim in Inadequate Equilibria, specifically the end of Moloch’s Toolbox, which is that there are lots of problems that don’t get solved because there aren’t all that many people who are unbiased and will float to the problem that seems most important (the ‘maximizing altruists’) compared to the number of problems, and so you get problems that seem ‘quite serious’ but are also neglected because they’re more costly than human civilization can support at present. (This dynamic is common; when I worked in industry, there were many improvements that could be made to the system that weren’t being made because they weren’t the most important improvement to be making at the time.)
But also this sort of meta-work has its own costs. Compare Alice, who views LessWrong on her phone and notices a bug, and then fixes the bug and submits a pull request, and then moves on, with Beatrice, who considers all the bugs on LessWrong and decides which is most important, and then fixes that one and submits a pull request. Then compare both of them with Carol, who also considers all the different projects and tries to figure out which of them is most important, which also maybe requires considering all the different metrics of project importance, which also maybe requires considering all the different decision theories, which also maybe requires...
It seems good for Alice to not pay the costs of optimizing, and just do the local improvements, especially if the alternative is that Alice doesn’t make any improvements. Beatrice will do more important work, but is ‘paying twice’ for it, and in situations where the bugs are roughly equally important this means Beatrice is perhaps less effective than someone less reflective. I think that people who are naturally interested in this sort of maximizing altruism should do it, and people who aren’t (and want to just be Alice instead) should be Alice without worrying about it too much (or trying to convince themselves that, no, they are doing the maximizing altruism thing).
After reading the title, my main objections to voting theory were:
The theory is already understood well enough, what is hard is convincing existing institutions to change.
Convincing existing institutions to change is really hard, so there’s not much point in advancing the theory
Though I do agree that public elections are a process by which huge amount of resources get allocated, in many of the world’s richest countries, so it’s an important problem.
You make some arguments against these two:
Can you point to an example of this? Something the understanding of which has improved in the last 20 years. Also, are activists and the academia one and the same? Is this improved understanding because new theory was developed, or because the activists started understanding theory that had already been developed in the academia.
The key question is not whether it will happen somewhere with a probability of at least 1%, but rather whether you or the people you inspire can move the needle with probability 1 in a millionth (or less), in a place that’s sufficiently big (or even bigger). Are you thinking of influencing the US Gov in particular? That would certainly qualify for a big entity. What are the wins that the voting reform movement has done in the past few years? ( I suppose the #1 USA example is Fargo, in North Dakota, that passed approval voting )
(There’s probably a lot of people unhappy with voting in some way, so if you can convince them that your proposal is going to make their group more powerful, maybe it’s not so hard).
I am a board member of the Center for Election Science, which was behind the campaign in Fargo. They definitely deserve your support, and are a big part of the improvement I see over 20 years. 20 years ago, the debate was largely between IRV and Condorcet; though approval voting had been proposed, its theoretical grounding was still not complete. Now, the theory of cardinal voting is much better, and we’re beginning to seriously look at cardinal/ordinal hybrids such as STAR or 3-2-1. I could go on for pages about the intellectual history of this transition but I have to work on my thesis.
Are activists and academia one and the same? Sadly, not at all. That’s why I, an activist, am at Harvard doing a PhD in statistics.
Yes, my ultimate targets are the big ones: the federal governments of the USA, Canada, and the UK. Aside from the Fargo case you mentioned, I was also deeply involved in the BC referendum on proportional representation last year; though this failed, I think we laid some good groundwork for future similar attempts in Quebec, PEI, and eventually Ontario. There’s also some good reform energy in the US Pacific Northwest, with groups like equal.vote, Counted, and Sightline. I could go on, but you get the idea.
I’m rather cynical about the value of academic research to the general public, as applied to civic voting in modern Western jurisdictions. But I realize that I’m assuming far too much about what you mean by “voting theory” based only on outside reading, this post, and your post asking about basic research grants.
There are a LOT of decisionmaking, conflict-resolution, and preference-sharing topics that could be extremely interesting and useful outside of the political domain (and a number of important topics inside that domain that I wouldn’t call “voting theory”, but maybe you do).
Some of the topics mentioned in https://80000hours.org/problem-profiles/improving-institutional-decision-making/ would be extremely useful to solve (or even just to measure better), and in most cases can be applied to smaller organizations and firms without the constraint of appearing to have equal votes over a large, diverse (and “diversely-rational”) electorate. And even there, they note that implementation may be more difficult (and valuable) than research.
Gah, I meant simply to note my ignorance on your actual proposed area of work, and to ask “Do you have a summary of the research domain you’re proposing?”? Please pretend I wrote that rather than the rest of my rambling.
I strongly doubt this point. The reasons that current election systems are horrendous are _not_ related to lack of academic research. The reasons are historical and social, not mathematical. The only way to get better elections is to get a better selectorate (cf raising the sanity waterline).
I _do_ think there’s a lot of value in some aspects of voting theory research, but not really having to do with political voting, more about how to combine/compare human desires: utility/preference aggregation limits and theorems.
Is any form of utilitarianism anywhere close to sane? In a world with https://en.wikipedia.org/wiki/Theory_of_the_second_best and https://en.wikipedia.org/wiki/Arrow%27s_impossibility_theorem, is there _ANY_ aggregation function suitable for use in any moral calculus?
The thing that I can imagine making theory relevant is for the vote-reform activists being in agreement on which system to strive for.
For example, my current impression is that it’s actually slightly annoying that Massachusetts passed (if I recall correctly) ranked voting, instead of approval voting (which I think makes better tradeoffs in vote-counting pragmatics and ease-of-use.)
I’m not sure what counts as theory or not, vote-counting pragmatics and ease of use are a different class of problem than “what sorts of decisions an idealized election would get the right answer on”, but it does seem like you need both the theory and the nitty-gritty pragmatics in order to decide “which voting system we’re going to push for nationwide, starting at the local level and working our way up as we build momentum.”
I’m amused by the irony of vote-reform activists being thwarted by an inability to pick the best result from diverse beliefs/preferences. I strongly doubt that more research on voting theory can resolve it for activists any more than it can for the public.
But perhaps I’m wrong—there’s probably some aspects of voting BOOTSTRAP theory that bears investigation. I suspect that even that falls more into social/political science than what is commonly called “voting theory”, which is more abstract and mathematical, closer to game theory.
I think there is a paper somewhere on which voting systems win when voted on under which voting systems by voting experts.
You might be thinking of “And the loser is… Plurality Voting” which describes a 2010 voting systems conference, where Approval Voting ended up winning the approval vote. (I do wish they had had the experts vote under a bunch of different systems, but oh well.)
Maine, not Massachusetts. Massachusetts will probably pass ranked voting in 2020, though.
“Starting at the local level and building up” is a good plan, but not the only one. For anti-gerrymandering fixes (that is, proportional representation), starting with the federal level could make sense.
Nod. But it seemed like the “start from local level and build up” was what was in fact happening, when it came to changing the voting methods themselves.