Want to make a difference on policy and governance? Become an expert in something specific and boring

I think I mostly disagree with this post. 

I think Michael Webb would be an example of someone who did pretty abstract stuff (are ideas, in general, getting harder to find) at a relatively junior level (PhD student) but then because his work was impressive and rigorous became very senior in the British government and DeepMind. 

Tamay Besiroglu's MPhil thesis on ideas getting harder to find in ML I think should be counted as strategy research by a junior person but has been important in feeding into various Epoch papers and the Davidson takeoff speeds model.  I expect the Epoch papers and the takeoff model to be very impactful. Tamay is now deputy director of Epoch. 

My guess is that it's easier to do bad strategy research than it is to get really good at a niche but important things, but I think it's very plausible that it's the better-expected value decision provided you can make your strategy research legibly impressive, and your strategy research is good research.  It seems plausible that doing independent strategy research one isn't aiming to be published in a journal is particularly bad since it doesn't provide good career capital, there isn't good mentorship or feedback and there's no clear path to impact.  

I would guess that economists are unusually well-suited to strategy research because it can often be published in journals which is legibly impressive and so is good career capital, and the type of economics strategy research that one does is either empirical and so has good feedback loops, or is model-based but drawn from economic theory and so much more structured than typical theory would be. I think this latter type of research can clearly be impactful - for instance, Racing to the Precipice is a pure game theory paper but informs much of the conversation of avoiding race dynamics. Economics is also generally respected within government and economists are often hired as economists which is unusual amongst the social sciences. 

My training is as an economist and it's plausible to me that work in political science, law, and political philosophy would also be influential but I have less knowledge of these areas. 

I don't want to overemphasise my disagreement - I think lots of people should become experts in very specific things - but I think this post is mostly an argument against doing bad strategy research that doesn't gain career capital. I expect doing strategy research at an organization that is experienced at doing good and/or legibly impressive research e.g. in academia mostly solves this problem. 

A final point, I think this post underrates the long-run influence of ideas on government and policy. The neoliberals of the 60s and 70s are a well-known example of this, but also Jane Jacob's influence on US urban planning, the influence of legal and literary theory on the Modern American left, and the importance of Silent Spring for the US environmental movement. Research in information economics has been important in designing healthcare systems, e.g. the mandate to buy healthcare under the ACA. The EUs cap and trade scheme is another idea that came quite directly from pretty abstract research. 

This is a different kind of influence to proposing a specific or implementing a specific policy in government - which is a very important kind of influence - but I suspect over the long run is more important (though with weak confidence and I don't think this is especially cruxy.)

Suggestion for how people go about developing this expertise from ~scratch, in a way that should be pretty adaptable to e.g. the context of an undergraduate or grad-level course, or independent research (a much better/stronger version of things I've done in the past, which involved lots of talking and take-developing but not a lot of detail and publication, which I think are both really important):

1. Figure out who, both within the EA world and not, would know at least a fair amount about this topic -- maybe they just would be able to explain why it's useful in more context than you have, maybe they know what papers you should read or acronyms you should familiarize yourself with -- and talk to them, roughly in increasing order of scariness/value of their time, such that you've at least had a few conversations by the time you're talking to the scariest/highest-time-value people. Maybe this is like a list of 5-10 people?
2. During these conversations, take note of what's confusing you, ideas that you have, connections you or your interlocutors draw between topics, takes you find yourself repeating, etc.; you're on the hunt for a first project.
3. Use the "learning by writing" method and just try to write "what you think should happen" in this area, as in, a specific person (maybe a government agency, maybe a funder in EA) should take a specific action, with as much detail as you can, noting a bunch of ways it could go wrong and how you propose to overcome these obstacles.
4. Treat this proposal as a hypothesis that you then test (meaning, you have some sense of what could convince you it's wrong), and you seek out tests for it, e.g. talking to more experts about it (or asking them to read your draft and give feedback), finding academic or non-academic literature that bears on the important cruxes, etc., and revise your proposal (including scrapping it) as implied by the evidence.
5. Try to publish something from this exercise -- maybe it's the proposal, maybe it's "hey, it turns out lots of proposals in this domain hinge on this empirical question," maybe it's "here's why I now think [topic] is a dead end." This gathers more feedback and importantly circulates the information that you've thought about it a nonzero amount.

Curious what other approaches people recommend!

Thanks for writing this!

• Another way to think about it: it's much more likely that a boring thing is neglected than something that sounds sexy.

• A potential meta-skill I've been somewhat successful at building is to approach these superficially bland topics like a photographer: [If it's boring, you're not close enough.] (https://www.theartnewspaper.com/2021/07/29/if-your-pictures-arent-good-enough-youre-not-close-enough-vintage-prints-by-war-photographer-robert-capa-to-headline-photo-london) For example, you can challenge yourself to give a 5 minute lightning talk that gets others excited after 1h of research on such a topic!

• I was also really surprised how easy it was to get experts on product certification (CE testing) and standardisation on the phone. They don't seem used to talking to an overly enthusiastic person in their twenties and have been insanely helpful.

I love this post. In the past week I have had a few eye-opening moments which strongly support this way of thinking:

1. I was speaking to a junior EU official, like under 30, less than 3 years in his role. He mentioned that people underestimate the influence people at his level can have in a big organisation. We all know that it is the politicians and very senior officials who decide the budget for important interventions, anything from Developmental Aid to AI Safety. What we often overlook is that it's often very junior people who execute these instructions, and this often means that they get to decide (or at least suggest) how the money the politicians have approved should be spent at a granular level. People who take the time to learn about this process and then look for the appropriate roles can find themselves deciding which charity should get millions of euros, or which initiative to support. People put massive effort into debating policy (how big is the budget) and in this arena, we tend to have very little influence against all the big players. But if we were to focus on how specifically a part of the budget is spent (e.g. ensuring it supports evidence-based, effective interventions), we could have much more impact. And yet, very few of us do this. 

2. I've been following Rutger Bregman for a while now, and one of the things he keeps emphasising is the importance of actually doing something tangible. I also read the following provocative quote from Cate Hall (Useful Fictions) : "Ideas are cheap and easy to find; execution is everything. Effective altruists would be a lot more effective if they internalized this." 
When we do tangible things, we tend to need tangible, boring skill-sets. The ability to parse long legal documents or study financial spread-sheets. A deep understanding of arcane areas of law and precedent - e.g. tax-law, liability law as it relates to tobacco companies, etc. for two of Rutger's initiatives. We all have great theories about how the world should be and those are important visions to keep in mind, but it isn't for the want of these visions that progress is so slow. 

People who work in politics already understand this. The movements which succeed don't just have big visions, they also have thousands of volunteers who study the precise rules of vote-counting, who look at the logistics of getting their voters to the polling stations, who (if they're in the GOP anyway) look for rules that might enable them to prevent likely opponents from voting or even from running as candidates. The boring tedious stuff.

How much of the tragedy of the past 25 years would have been avoided if some Democrat 2000 had spent a few hours studying the legal details of hanging chads and found a way to just count those votes before the whole drama even started? If someone had done that, we would never have known their name or what they did, nobody would write poems about them, but they might have prevented multiple wars and millions of deaths. 

Strongly agree. Having been on both sides of the policy advocacy fence (i.e. in government and as a consultant/advocate working from the ouside), policy ideas have to be concrete. Asking the government to improve disease surveillance (as opposed to something specific like e.g. implementing threatnet) is about as useful as asking a government to improve education outcomes by improving pedagogy, or to boost the economy by raising productivity.

Of course, you don't have to be an expert yourself per se, but you have to talk to those who are, and get their inputs - and beyond a certain point, if your knowledge of that specific space becomes great enough after working in it for a long time, you're practically an expert yourself.

While EA is great, a lot of us have naive views of how governance works, and for that matter have overly optimistic theories of change of how abstract ideas and research affect actual policies and resource allocation, let alone welfare.

So of course developing expertise in something important is better than "ending up in a never-ending strategy spiral." But I largely disagree about your focus on established, specific, boring, prosaic questions. The relevant way I can impact governance by discovering something good, telling EAs, and thus causing EAs to use their influence to make it happen. And I think I can do that much better by starting at questions like "if AI goes well, what happened" and "what intermediate goals improve AI safety" and "what should labs do" than the kind of topics on your list.

Speaking just to the little slice of the world I know:

Using a legal research platform (i.e. Westlaw, LexisNexis, Casetext) could be really helpful with several of these. If you're good at thinking up search terms and analogous products/actors/circumstances (3D firearms, banned substances, and squatting on patents are good examples here), there's basically always a case where someone wasn't happy someone else was doing X, so they hired lawyers to figure out which laws were implicated by X and file a suit/indict someone, usually on multiple different theories/laws. 

The useful part is that courts will then write opinions on the theories which provide a clear, lay-person explanation of the law at issue, what it's for, how it works, etc. before applying it to the facts at hand. Basically, instead of you having to stare at some pretty abstract, high-level, words in a statute/rule and imagine how they apply, a lot of that work has already been done for you, and in an authoritative, citable way. Because cases rely on real facts and circumstances, they also make things more concrete for further analogy-making to the thing you care about. 

Downside is these tools seem to cost at least ~$150/mo, but you may be able to get free access through a university or find other ways to reduce this. Google Scholar case law is free, but pretty bad. 

Man, the topics you mention feel too boring (i.e. too far removed from the important questions). Quoting from Richard Ngo's AGI safety career advice for another flavor of question:

Here are some topics where I wish we had a world expert on applying it to AGI safety. . . . :

1. What regulatory apparatus within the US government would be most effective at regulating large training runs?
2. What tools and methods does the US government have for auditing tech companies?
3. What are the biggest gaps in the US export controls to China, and how might they be closed?
4. What AI applications or demonstrations will society react to most strongly?
5. What interfaces will humans use to interact with AIs in the future?
6. How will AI most likely be deployed for sensitive tasks (e.g. advising world leaders) given concerns about privacy?
7. How might political discourse around AI polarize, and what could mitigate that?
8. What would it take to automate crucial infrastructure (factories, weapons, etc)?

(I know you weren't just writing about AI safety. Even given that, these questions are substantially more relevant to stuff that matters than yours, and I think that's good.)

I think I strongly agree with this post on becoming specific, having observed how the fossil fuels vs renewables "fight" is playing out. Perhaps it is not directly relevant to bio, but the climate action takes place in obscure places, often at state level in the US where the fossil fuel lobby hired actors to influence some local politics (not recommended!) and how very important decision are made in esoteric hearings of unknown government entities. I am not saying bio will play out similarly, but that it is important to find these arenas/levers within the large and complex government landscape, build alliances and engage on specific points in the bureaucracy. 

I think this is true if for some particular reason you are set on working outside government and want to be an external academic expert advising policymakers. I think this is what the poster’s experience has been.

But if you want to optimise for impacting policy, it is much higher impact to get roles inside government and to become a policymaker yourself, which usually requires broad, generalist expertise and skills, so overall I strongly disagree with this recommendation, but can see how the poster’s personal experience led to them to their view.

At a glance, each of these questions could easily (1 week to 6 mos) be answered by a U.S. lawyer or dedicated law student. If you have money to spend, hire someone; if not, link up with a law firm's pro bono program or a law school's security clinic.

Just a quick note on "Patent law - can companies patent dangerous technology in order to prevent others from developing or misusing it?" -- No. The U.S. patent tradeoff is that you make an idea public (describe it fully and accurately) in return for (max) 20 years of protection. So the patent process would publicize the dangerous tech, and then (at max, if you had good lawyers and good judges) protect the tech for 20 years -- after which anyone could use the tech you had publicized. Please don't do this.

I mostly agree. Though having worked in research, policy and now policy analysis, it's also the case that sectors can get stuck in established practices. Big-picture /blue sky thinking is of course also important. But I agree that the value of work to get the basics/details right is under recognised. So thumbs up for your post, except the framing of "boring"; one person's boring is another's wildly fascinating - who are we to judge. 

I mostly agree with this, with one addition. 

You yourself probably know better than ASB or anyone else what are the specific boring areas in which you could become an expert that would be useful and impactful. 

Or maybe you already are an expert in a boring area and just need to build on that. 

For example, a chemical engineer will already have studied areas like explosion risk-management, quality control/assurance and safety. An engineer with Pharma experience might also have had extensive dealings with the FDA and their audits. To you, this might seem obvious - but you can be sure that your knowledge represents a vast, complex and yes, boring field of knowledge to someone who hasn't had your experience and learning. 

It feels like these all provide important perspective to any discussions on AI Safety, Safety verification, etc., that probably most of the people working on this topic will not have. There are so many comments like "we need an agency like the FDA or the IAEA" from people who only have a superficial notion of how these agencies operate. So if you have a deep understanding, that could be valuable, impactful knowledge. In a policy discussion, it is powerful perspective if you can argue that "this is how the FDA does it". 

One area where there seems to be a huge lack of expertise among the EA community is China. I don't know how many discussions I've had about AI Safety and Governance in the context of China, but almost nobody (certainly not me!) has been in the discussions providing perspective of how things actually work in China, how policies can be influenced, how corporations and government actually influence each other (i.e. who meets whom, when, where, what flexibility do they have, ...). So this could be a great area for someone who has worked in that kind of area in China, or who has a network of people in that area. 

ASB - thanks for sparking a fascinating discussion, and to the many comment-writers who contributed. 

I'm left with mixed feelings about the pros and cons of developing narrow, 'boring', expertise in specific policy topics, versus more typical EA-style big-picture thinking.

The thing is, there are important and valuable roles for people who specialize in connecting these two approaches, in serving as 'middle men' between the specialist policy wonks and the EA strategists. This requires some pro-active networking, some social skills, a capacity for rapid getting-up-to-speed in new areas, a respect for subject matter experts, and an ability to understand what can help policy experts do their jobs, and advance their careers, more effectively. This intermediary role could probably benefit from a few years of immersion in the gov't/policy/think tank world -- but not such deep immersion that one soaks up all of the conventional wisdom and groupthink and unexamined assumptions that tend to characterize many policy subcultures. So, the best intermediaries may still keep one foot in the EA subculture and one foot in a very specialized policy subculture.

(I say this as someone who's spent most of his academic career trying to connect specialist knowledge in evolutionary and genetic theory to bigger-picture issues in human psychology.)

A Biosecurity area I'd add to the list is regulation and policy around contact tracing apps.

Example questions:

1. How come Google and Apple got to dictate the privacy constraints rather than democratic governments?
2. What policies could boost uptake if the apps?
3. Why didn't politicians make the tracing legally enforceable, unlike traditional contact tracing (this was the case in the UK, I'm not sure the international situation)?

Add Electromagnetic Spectrum policy and regulations to the list. The world is wireless and a few experts at the ITU-R, as well as state run regulatory bodies like the USA's NTIA, decide what that wireless world will be. Become an expert in Electromagnetic Spectrum policy and regulations is a great way to change the world. (and the money isn't bad either)

Terrible advice. I did that, became a Superforecaster. Checked a bazillion boring facts. Came to the conclusion of a 1% AI X-Risk in the XPT tournament, together with many of my thoughtful peers. 

Then our (repeated, active) attempts to actively engage and foster a dialog with the "AI experts" in the tournament went to nowhere. There was disagreement at the end of the tournament. All the pundits, once results went up, said surely this can't possibly be. Pundits also missed that in areas where we did engage in productive reasoning with actual experts during the tournament (cough cough nuclear X-risk) there was a lot of agreement in the end.

Motivated reasoning beats boring each time. Become a pompous self promoter, please! EA needs more egomaniacs!