Note: The Open Philanthropy Project was formerly known as GiveWell Labs. Before the launch of the Open Philanthropy Project Blog, this post appeared on the GiveWell Blog. Uses of “we” and “our” in the below post may refer to the Open Philanthropy Project or to GiveWell as an organization. Additional comments may be available at the original post.
- 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.
- 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.
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.
- We have published shallow investigations on a variety of U.S. policy causes: climate change, labor mobility, foreign aid, intellectual property reform (focusing on software patents), treatment of animals in industrial agriculture, broadband policy and organ transplant supply.
- We also have investigations forthcoming on farm subsidies, occupational licensing, improving the general functioning of democratic processes, tax policy, and urban density/zoning reform.
- We have discussed science policy with Bhaven Sampat and Bruce Alberts; 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).
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.
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).