The GiveWell Blog

Narrowing down U.S. policy areas

Throughout the post, “we” refers to GiveWell and Good Ventures, who work as partners on GiveWell Labs. [Added August 27, 2014: GiveWell Labs is now known as the Open Philanthropy Project.]

As part of our work on GiveWell Labs, we’ve been exploring the possibility of getting involved in policy-oriented philanthropy (see our previous posts on this subject). At this point, we feel that:

  • We’ve done at least some degree of investigating the causes that seem most promising to us, and we’ve gained an initial level of familiarity with how to think about what a promising cause is.
  • We see major gains to choosing longer-term focus areas – causes that we can commit substantial person-hours, and substantial funding, to over the next several years.

Because of this, we are now laying out the causes we tentatively feel most likely to commit to, and doing substantial investigation (including some grantmaking) in these areas. We aren’t yet committing to these causes, but we think that laying out our current thinking and reasoning will help surface important questions and intensify the period of reflection leading up to a decision.

We previously wrote about the importance of committing to causes.

Why commit to causes in U.S. policy?
We believe that policy-oriented philanthropy is an extremely important type of philanthropy to be familiar and experienced with. The potential leverage of influencing governments (whose budgets and other powers generally dwarf what philanthropists can provide) means that policy-oriented philanthropy on a broad range of causes could potentially be competitive (in terms of “good accomplished per dollar”) with even the most effective direct aid programs. For the moment, we are focused on the U.S., because:

  • GiveWell is located in the U.S. We have a far greater level of background familiarity with the U.S. policy landscape than with policy in other countries.
  • We find it far easier to identify, form relationships, and learn from people with expertise on U.S. policy than people with expertise on other countries’ policy (since the former tend to live in the U.S. and to share language and background knowledge with us).
  • The U.S. is the world’s largest economy and most powerful country, so the potential leverage of affecting U.S. policy is enormous. We don’t perceive that there is an obviously superior country to focus on.

We believe that making commitments to causes (intending to allocate a substantial number of person-hours to them for the next several years, accompanied by substantial potential budgets) would dramatically improve our ability to learn about these causes, and to learn more generally about how to engage in policy-oriented philanthropy. It would also make it easier for us to make plans around hiring and developing policy-focused staff.

With the level of investigation we’ve done so far, we feel we’re hitting diminishing returns on our ability to distinguish between different causes; however, gaining more in-depth experience with the ones that currently seem most promising – including identifying more giving opportunities, following grants, developing more relationships and putting in more time and thought – could improve our ability to think intelligently about what constitutes a promising cause.

By the end of this calendar year, we hope to make substantial commitments to several (probably 1-3) causes in the category of policy-oriented philanthropy.

What we’ve done to investigate policy-oriented philanthropy
We wrote previously about the work we’ve done to gain basic context in policy-oriented philanthropy. Since then, we have done the following.

Conversations with “generalists” who can speak to a variety of different political causes. We previously mentioned speaking with Dylan Matthews, Frank Baumgartner, Steven Teles, Mark Schmitt, Gara LaMarche, and the heads of the Center for Global Development and Brookings Institution. Since then, we have:

  • Spoken further with many of the people mentioned above, especially Steve Teles, whom we have retained as a consultant. Prof. Teles is the only person we’ve come across who has extensively studied the historical role of philanthropy in politics, and seems to have a broad view of the different ways in which philanthropy can influence policy.
  • Posted notes from Matt Stoller, Dean Baker, Keith Humphreys, Philip Heymann, and Robert Greenstein, and had several more general policy conversations that we don’t have notes available for (in some cases the notes are forthcoming).
  • Spoken extensively with people at the Pew Charitable Trusts, a large charity engaged in a great deal of work on a variety of U.S. policy issues, with a high degree of attention to political tractability and a tendency to set concrete goals for policy change. (More extensive notes from Pew are forthcoming.)
  • Tried to deepen our understanding of causes that are highly relevant to global poverty via conversations with two people referred to us by Beth Schwanke, Senior Policy Counsel at Center for Global Development. Unfortunately, we have not been able to publish notes from these conversations.

Shallow investigations.

Medium-depth investigations. We have done deeper investigations on criminal justice reform and macroeconomic policy, and we have explored giving opportunities in labor mobility. We have also gained relatively deep familiarity with drug policy (this is a Good Ventures interest, with GiveWell providing support consistent with our policy on general support) and with organ transplant supply policy (via Alexander Berger’s personal interests and networking on this topic).

Finally, we have made a general informal effort to be more attentive to news and debates relating to U.S. policy, including regularly reading Wonkblog and now Vox (which we have found particularly helpful).

Our investigations have been far from comprehensive; we’ve prioritized causes we’ve had some reason to think were particularly promising, often because we suspected a relative lack of interest from other philanthropists relative to the causes’ humanitarian importance or because we encountered a specific idea from someone in our network. With that said, at this point we have put a great deal of work into discussing and investigating different possible ways of engaging with U.S. policy, and have put at least some consideration (not always including a formal investigation) into every potential cause we can identify. We’ve also tried to expand the horizons of the causes we’re considering via activities like scanning the publication lists of major think tanks, scanning summaries of the U.S. budget and scanning the list of federal agencies.

General patterns in what causes we find promising
At any given time, we have both a working theory of what our criteria should be (what makes a cause promising, and hence what we should focus our information-gathering efforts on for a given cause) and of what the most promising causes are (considered holistically, without necessarily relying on our existing criteria). Reflecting on the latter (what causes seem most promising to us) often causes us to modify the former (what our list of criteria looks like), while collecting information using the rubric provided by our criteria often causes us to update our views of what the most promising causes are.

So far, it seems to us that the most important broad qualities that make a political area seem promising are:

  • Importance: how much humanitarian benefit would a small, medium, or large “victory” – in the sense of impacting a change in policy (or defending the status quo when a change would have been negative) – bring about?
  • Tractability: what do the prospects seem to be for achieving a victory over the short or long term? Is the status quo too politically entrenched to overcome?
  • Crowdedness (analogous to room for more funding): how much of the existing advocacy infrastructure is pushing for goals similar to ours? Are there gaps in this infrastructure that we might fill?

Speaking generally (more details in the next post), we’ve been able to assess these aspects of a cause only at fairly low resolution, and we haven’t fully explored their interrelations.

  • Re: importance. Importance can’t be assessed fully in isolation from tractability-related concepts, since we need a sense of what a small, medium and large “victory” would look like, and that in turn requires a sense of what might be possible. We’ve done back-of-the-envelope estimates for a variety of causes and generally believe that we can tell the difference between an enormously important policy area (one in which changes in policy could dramatically affect large numbers of people), a reasonably important area, and a relatively unimportant area, but that we can’t say much with confidence beyond that (and even our confidence in assigning an issue to one of those three categories is quite limited). We believe that exploring causes more deeply will improve our ability to think about what a small, medium and large victory would look like, and thus to assess importance.
  • Re: tractability. As discussed previously, it can be very difficult to predict whether and when a policy area might become tractable, and there is an argument against putting too much weight on the apparent tractability of a cause that one seeks to work on for the long run. We have been hesitant to dismiss any issue as fully intractable where we see room for improvement (from a humanitarian perspective) in policy. In addition, tractability can’t be assessed fully in isolation from crowdedness: the more gaps there are in existing efforts, the more reasons one might have to hope that entering a space will change the dynamics. We generally believe that we can distinguish between (a) an “unusually tractable” cause – one in which dynamics are shifting and a “window of opportunity” for change seems to be present or imminent; (b) an “unusually intractable” cause – a highly crowded cause which seems to be at a stalemate; and (c) causes that fit neither category.
  • Re: crowdedness. Crowdedness is also a complex thing to assess, since it can encompass several different questions. Does a policy area get (a) a lot of attention? (b) a lot of funding from relevant interest groups? (c) a lot of funding from philanthropy specifically (which may have structural strengths and weaknesses relative to other interest groups, and therefore may have things to offer that they don’t)? A policy space may be highly crowded in some respects and uncrowded in others – for example, there may be a great deal of academic research but little think tank work (more on the different types of infrastructure that can work toward policy change). We believe that we will improve our understanding of how to assess the crowdedness of a cause as we get deeper into areas and see whether ideas that look neglected from the outside turn out to be truly neglected. With that said, we have done a good deal of work on assessing the crowdedness of different causes, and often have a sense for how much work – and of what type – goes into a particular policy space.

Given the generally low level of resolution at which we understand all three of these factors, we have become most interested in causes that seem to clearly stand out on at least one dimension while performing relatively well (compared to other standout causes on the same dimension) on other dimensions. In other words, we are interested in causes that seem to have enormous importance, while being at least as tractable and uncrowded as similarly important causes; causes that seem to have unusual “windows of opportunity,” while being at least as important and uncrowded as similarly tractable causes; and causes that seem to be extremely uncrowded/neglected, while being at least as important and tractable as similarly uncrowded causes. We could imagine that any of these three profiles could turn out to be optimal for a philanthropist, since we could imagine that any one of these three criteria turns out to be more robustly detectable than the others.

In the next post, we will discuss specifics of what causes we feel stand out on each dimension, and which causes we believe we are most likely to commit to (and are accordingly investigating deeply at the moment).

Comments

  • Kris Zyp on May 22, 2014 at 6:50 pm said:

    I know you have done some evaluation on this already (http://www.givewell.org/labs/causes/advocacy-foreign-aid), but I would be interested to see the foreign aid policy on these three dimensions as well. It still seems to me this would be the most natural policy area for GiveWell to pursue since it is most closely aligned with GiveWell’s existing recommendations and conclusions for charities. And GiveWell has built such extensive expertise in the areas that directly relate to making informed assessments of foreign aid policies, leveraging this expertise would give GiveWell substantial ability to make nuanced recommendations on precisely which policies or areas (GAVI, EFA, etc.) to invest advocacy effort towards (rather than just broadly push for more aid). And I would be a bit surprised that you could determine with much certainty that there really is substantially more tractability in other policy areas (of course determining past and predicting future causality in advocacy will always be extremely difficult).

    But thank you for the research either way, very interesting!

  • Nick Beckstead on May 23, 2014 at 5:04 am said:

    I’d be interested in learning more about the causes that GiveWell has considered, but did not formally investigate. Even moving from the whole universe of US policy areas to 12 areas for shallow investigations presumably involves a lot of important work and judgment. Is this something you plan to say more about in the future?

  • Nick Beckstead on May 23, 2014 at 5:05 am said:

    To be clear, I’d be most interested in seeing a list of causes that were sort of borderline for shallow investigations, or causes that someone else doing similar work might have highlighted for shallow investigation but you did not.

  • Robert Wiblin on May 23, 2014 at 6:28 am said:

    You might want to add a measure of how confident you are that you would be pushing policy in the right direction. This is most clearly relevant in the case of macroeconomic policy. Surely the gains from better monetary policy would be enormous, but it would be hard to know you are pushing things in the right direction, such is the level of expert disagreement.

  • chaos on May 24, 2014 at 10:46 pm said:

    I’d suggest you consider alternatives to influencing the US government. I think that lack of familiarity with other countries is not a good long term reason to avoid influencing them. You should work on developing familiarity with other countries rather than excusing ignorance about them.

    The US government is more powerful than other governments. But that meets only one of your three criteria. I think there are other countries where you would be able to develop more influence and where there is more low hanging fruit. I also think that even a government which is not powerful in terms relative to other governments can still be extremely powerful in terms of global well-being.

  • Colin Rust on May 25, 2014 at 11:00 am said:

    You are quite reasonably focussed for the time being on influencing US government policy.

    When you’re ready, in terms of influencing the governments of developing nations, I would suggest one interesting area for a shallow investigation would be tobacco policy. Developing nations are under a lot of pressure from tobacco companies to minimize regulation of tobacco. I would guess that a relatively modest investment in legal and policy assistance could go a long way in resisting this pressure, and reducing the growth of smoking (and smoking-related deaths) in the developing world.

  • Holden on May 30, 2014 at 6:56 pm said:

    Thanks for the comments, all.

    Colin: thanks for the suggestion. We have done a shallow investigation on tobacco policy (though we think of it as part of the “foreign aid” category rather than the “U.S. policy” category).

    Kris: our recent post discusses how we think foreign aid does on these criteria. We’re strongly considering getting involved in some way, but I broadly feel that there’s much less room to expand and improve the existing set of advocacy organizations than in our highest-priority areas. (This is less of a strict “tractability” issue than a “crowdedness” issue, though the two are related to some degree.)

    Nick: our recent post should address your question. Please let me know what you think.

    Rob: I think you’re right to raise this important consideration. It is worth noting that we are picking relatively broad areas; that we could support further research among other things; that we intend to become much better informed about any given focus area than we are now; and that even within an area that has many hard-to-resolve debates, there may be some key issues that we’re able to become confident in. With that said, I do think there are differences between causes in terms of how confident we can reasonably expect to become in the highest-value policy changes, and that we should take this into consideration. To some extent we have discussed this issue in relation to our current priorities (for example, our view on the “improving democracy” space, discussed in our more recent post).

    I wouldn’t consider a cause to be outstanding on the basis of this quality, so I don’t think it belongs as one of our key three criteria the way we’re using them, but I do think it’s important to factor this consideration in when deciding between different standout causes.

    chaos: If you have a specific country in mind and an associated argument, I’d be interested to consider it. However, I think the bar for “clearly better opportunities for impact (taking into account both likelihood of having influence and the leverage/importance of policy change)” is quite high. Working in another country, just about everything would be substantially harder: network building, recruiting, basic/background understanding, meeting grantees, etc. We’d have to be highly confident in our choice of country to justify that sort of up-front cost. And I don’t think that exploring several countries in this way is an option. Generally speaking, we tend to try to broaden our research in ambitious but tractable steps and to accept some tradeoff of comprehensiveness for practicality at each step.

  • Nick Beckstead on June 1, 2014 at 3:32 am said:

    Holden, yes your list addresses my question. Thank you. It also made me feel that you were covering a larger swath of the possibilities than I thought when I made that comment.

    Some categories that seem maybe interesting to me that aren’t on your list: promoting the use of experiments and cost-effectiveness analysis in governments (I have no idea how widespread this is, but David Halpern and the What Works Network do it in the UK, and it sounds interesting), emerging technology governance (including things like driverless cars), energy policy (unless it all falls under climate change), internet policy. The first two categories are interesting to me, though they are probably “supercauses” rather than causes.

  • Holden on June 3, 2014 at 5:31 pm said:

    Nick, thanks for the thoughts. A few notes on the issues you raise:

    1. Regarding experiments and cost-effectiveness analysis in government, this is similar to the area I was describing when I stated (in this post, not the more recent one): “we have also had discussions on the general topic of incorporating the findings of behavioral economics and social science research into policy (mostly off the record, though note that we are supporting BetaGov, which aims to encourage formal experimentation by policymakers, as part of our work on criminal justice reform).” For the most part, we think it is likely more useful to look for opportunities for experimentation and cost-effectiveness analysis within areas of interest rather than promoting experimentation as a whole, though there may be some opportunities for the latter (BetaGov is one).

    2. Regarding emerging technology governance, some of this will likely play into our work on global catastrophic risks. We have also done a shallow investigation on driverless cars. Our sense at the moment is that that space is likely to get plenty of attention, though we are open to revisiting if this turns out not to be the case.

    3. Regarding energy policy, we haven’t looked at it beyond the overlap with climate change. Are there other areas within it that you think we should consider?

    4. We have done a shallow investigation and writeup on broadband policy.

  • Nick Beckstead on June 4, 2014 at 1:53 pm said:

    Holden,

    2. I was thinking of looking at the area more generally, not just driverless cars. I don’t know enough about the area to have much idea what to expect to find.

    3. Sorry, I don’t have much of an idea of what to look for there.

    4. Are you saying that broadband policy covers internet policy in general? I was thinking there might be interesting stuff in the area that, e.g., the Electronic Frontiers Foundation works, but I know very little about this subject.

  • Alexander on June 4, 2014 at 6:00 pm said:

    Nick – on #4, while we definitely haven’t looked at all internet policy issues, the broadband policy shallows also covered net neutrality. EFF also works on free speech, privacy/surveillance, IP, and government transparency, most of which we’ve covered to some extent under other topics.

Comments are closed.