Potential U.S. policy focus areas

Throughout the post, “we” refers to GiveWell and Good Ventures, who work as partners on GiveWell Labs.

Previously, we laid out our basic framework and reasoning for selecting U.S. policy causes to focus on for GiveWell Labs. This post goes through the specific causes that we’re most likely to commit to (and are accordingly performing in-depth investigations of, with some preliminary grantmaking, at the moment).

A few preliminary notes:

  • This post does not offer the same sort of thoroughness and comprehensiveness that people might be accustomed to from our research on top charities. Part of this is because this post is more preliminary than our charity recommendations are, and much of the purpose is to elicit feedback and determine which questions most merit further investigation. (We are not yet committing to causes, and are aiming to do so near the end of the calendar year.) However, we also feel that as we move forward on GiveWell Labs, “accomplishing as much good as possible” and “thoroughly examining every question one might ask” will come into conflict, and the former is more important to us. We are aiming for transparency in the sense of making clear what sort of support we have for all of our major beliefs and statements; we are not aiming for comprehensiveness of investigation.
  • Some of our beliefs at this point come from intuitions that we’re unable to trace back to a particular source – intuitions that have come from the aggregate of many conversations as well as generally following and discussing policy-related topics. We try to make clear what our beliefs are based on, to the extent we’re able, and hope the ensuing discussion will highlight the areas where we have the most work to do in re-examining the bases for our statements.

We are trying to evaluate causes to “commit” to (as discussed previously), and “committing” could end up meaning many different sorts of things in terms of what sort of work we support. In a given cause, we could end up focusing on (a) supporting better research to determine optimal policy; (b) supporting information, education, and advocacy to push for particular policies; (c) working within an already-changing policy landscape and trying to affect the details of how policies change; (d) something else. We’ve tried to assess the importance, tractability, and crowdedness of causes with this broad potential mandate in mind, and to focus on causes that seem to be quite broadly important/tractable/uncrowded rather than simply presenting an opportunity for a specific narrow intervention.

As discussed previously, the causes we find most promising generally stand out on at least one of our three key criteria: tractability, importance, and crowdedness. As such, our discussion of causes is organized by criterion – we discuss which causes stand out on each dimension, followed by discussion of other causes that we find worth discussing for other reasons.

Contents of this post:

A few key resources that provide partial support for much of the reasoning in this post:

Windows of opportunity: outstanding tractability
As discussed previously, it can be very difficult to predict whether and when a policy area might become tractable (i.e., when it might become possible for advocacy infrastructure to play a major role in how policy develops in that area) in the long run. Paying too much attention to very short-run tractability (for example, what issue is in the news or being debated in Congress at the moment) seems inappropriate given the nature of what we’re trying to do: pick areas to commit to and build infrastructure in for several years.

With that said, we’ve come across a few causes that seem to present unusual “windows of opportunity,” in which something highly relevant in the political landscape seems to be changing in a way that could make the issue unusually prone to change for the next several years (and possibly beyond), and we could imagine our involvement helping to shape the specific way in which changes play out.

Perhaps the best example we’ve seen is the criminal justice policy space, which we’ve done a medium-depth writeup on. This space came up as promising early in our conversations with generalists, and was particularly emphasized by Steven Teles. There has long been a humanitarian argument (generally emphasized by people on the political left) for the importance of reducing unnecessary incarceration and the suffering associated with it; what seems to have changed relatively recently, however, is a combination of historically high incarceration rates, declining crime rates, and state budget difficulties – accompanied by a growing interest among the political right in reducing incarceration rates if it can be done without reducing public safety (e.g., Right on Crime.) Between the excitement we saw about tractability and the concrete opportunities we saw to support promising-seeming approaches, we saw this cause as a good one for our first medium-depth investigation in the policy arena; having investigated further and made some grants, we believe there are many promising underfunded approaches, real opportunities to influence policy, and reasonably high humanitarian stakes. More at our writeup on this topic.

Other “window of opportunity” causes that have come up:

  • Public opinion on marijuana over the last ~15 years has shifted dramatically, leading to state-level changes in drug policy and seeming potential for more change. Good Ventures has done some funding and a fair number of conversations in this space, with GiveWell providing support; in addition, there is some overlap between criminal justice and drug policy, particularly the research by Mark Kleiman that we are supporting. We don’t see this cause as particularly crowded, and we see work on designing good regulation (such as Prof. Kleiman’s research) as having a great deal of room for more funding. However, GiveWell’s perception at this moment (though open to revision) is that the net humanitarian benefits of marijuana legalization are unlikely to be as high as for potential reforms in the criminal justice space, and that the aspects of this space that don’t touch on either marijuana legalization or criminal justice policy do not necessarily have much “window of opportunity.”
  • Public opinion has also been shifting on the topic of same-sex marriage, though the people we’ve spoken with have often expressed the sentiment that we’re “in the endgame” at this point, and that the entrance of an additional major funder wouldn’t be likely to have much impact.
  • A couple of people have raised the possibility that surveillance – e.g., policy around what sorts of information U.S. security agencies collect – is becoming a more dynamic area, due to recent revelations (e.g., Edward Snowden’s leaks) and changes in what’s technologically possible. Our impression, based on our general perceptions of what is at stake and common attitudes toward this issue, is that this area is likely to be or become relatively crowded, and that we are unlikely to see opportunities with comparable humanitarian significance to what we’ve seen in the criminal justice space.

We have largely relied on impressions from our conversations with generalists in order to identify the most promising “window of opportunity” causes. Of these, our view is that criminal justice reform is the most promising, having equal or greater humanitarian significance and equal or lesser crowdedness compared to the others.

Ambitious longshots: outstanding importance
There are a couple of obstacles to identifying policy areas with outstanding importance:

  • In order to assess potential humanitarian gains, one must have some idea of what sort of policy change is possible. This seems very hard to assess, and we hope that gaining more intimate familiarity with specific policy areas will give us a better idea of how to do so.
  • The calculations we’ve done attempting to compare the significance of different policy areas are extremely non-robust, and arguably have little value-added on top of intuition. With that said, it does seem to us that one can reasonably distinguish between “contenders for the most important policy area,” “policy areas that have fairly small implications” and “somewhere in between.”

Another challenge here is that from what we’ve seen, the causes that seem like strongest contenders for “most important” tend to have relatively poor, or at least highly ambiguous, scores on the other two criteria (more details below). We haven’t seen any such cause where we are (at this early stage) convinced of a clear opening for a philanthropist and an opportunity to make tangible progress.

With that said, we see some compelling reasons to get deeply involved with at least one “ambitious longshot” cause, even if the prospects for change seem doubtful and/or the space seems relatively crowded:

  • It’s possible that our assessments of the other two criteria are highly unreliable. It’s possible that the right attitude is: “Any cause has potential for change over the long run, and any cause has plenty of space for a new philanthropist to add value, if one is sufficiently committed. What’s most knowable is which policy areas have the highest stakes.” In particular, if we get deeply involved in a space that initially seems “crowded,” we may discover that there is more value to add than we would have guessed.
  • As discussed in a later section, we are thinking about the long-term goal of promoting a broader political platform. More broadly, we hope to see dramatically higher money moved and influence over time. With this in mind, it is probably worth attacking the question, “What causes would we encourage massively more people to support – with their giving and with their talents – if we could?” For that question, focusing on a relatively overlooked cause of extreme importance – rather than simply on causes that currently seem to present opportunities for major gains with relatively small investments – seems valuable.

What follows is the set of causes that we believe to have overwhelming humanitarian importance (in the sense that an imaginable policy change would create large amounts of economic value and/or affect large numbers of people significantly). They are listed in order of how promising we find them, taking into account other criteria (tractability, crowdedness). Note that the way we’re using “importance” here attempts, when feasible, to incorporate not just the size of the problem, but the likely impact of an improvement in policy if the improvement could be implemented. (In other words, a major problem may still fall short on “importance” if it seems unlikely that one could identify a change in legislation with large expected impact on the problem.) With that said, there are many cases in which we know very little about the details of possible policy fixes, and try to approximate “importance” based primarily on the size of the problem and very rough intuition about how policy change might affect it.

We have created a collection of back-of-the-envelope estimates on the likely impact of policy reform in different areas, which informs the comments below in general, though we do not place much confidence in the particular estimates.

Labor mobility

It appears to us that moving from a lower-income country to a higher-income country can bring about enormous increases in a person’s income (e.g., multiplying it several-fold), dwarfing the effect of any direct-aid intervention we’re aware of. As such, labor mobility seems to us to be an enormously high-stakes issue, whether based on our own back-of-the-envelope calculations for possible legislative changes, academic estimates that sufficient increases in immigration could create value on the order of 50% of world GDP, or just the observation that changes on a per-person-affected basis are impressive.

Additionally, it appears to us that there is relatively little attention paid to this cause in some sense: the humanitarian benefits of migration seem to receive little discussion and emphasis generally, we have not identified any other philanthropic funding focused on labor mobility as an anti-poverty issue, and we note that immediately prior to our involvement, Michael Clemens’s work on this issue at Center for Global Development was in the relatively unusual position of not having specific private support (though it had been supported previously).

With that said, there is another sense in which this cause is quite “crowded”: U.S. immigration policy more broadly is an extremely salient and heavily contested issue, with significant philanthropic involvement as well as interest in allowing more migration from the business community. The debates taking place at the moment seem to center mostly around the treatment of undocumented immigrants, with labor mobility as a secondary issue. Thus, the question of how “crowded” this space is – and what a new funder might be able to contribute – remains very much an open question for us, and one that we are trying to address with deeper investigation and declared interest in funding.

There are a couple of other challenges with this area:

  • There is a high degree of controversy over this issue. We hope to conduct a thorough review of arguments and counterarguments, which we have done some work on but have not yet completed.
  • While we generally feel that “political tractability” is difficult to predict past the short term, immigration seems to be a particularly charged issue where the fundamental obstacles to change may be extremely strong.

Macroeconomic policy

Macroeconomic policy appears to be an area with extraordinarily high stakes, in that a small number of decisions can arguably have substantial effects on national (and global) growth and unemployment.

Our aim in this space would likely be focused on generating better information and new ideas, rather than coming down on one side or the other of a partisan battle.

The question of whether we ought to consider this space “crowded” is a difficult one.

  • Arguments to consider this space “crowded”:
  • Argument to consider this space “uncrowded”:
    • We’re not aware of any major philanthropic funder that has made this area a top priority.
    • The early conversations we’ve had have given us some reason to think that there are certain types of research that are not supported by existing infrastructure.
    • A number of people we spoke to noted the outsize influence of the Fed in monetary policy and macroeconomic research, and argued that support for more independent research and thinking could be useful.
    • We’re not aware of work in this area that focuses on formulating workable legislation to improve on the status quo (e.g., working out the details of “automatic stabilizers” that could be budget-neutral over time, which could be an important criterion for winning support or acceptance from both the right and left). The new Hutchins Center may end up working in this area.
    • It generally seems to us that the importance of macroeconomic policy is underappreciated and rarely discussed outside of a few narrow circles (in particular, the academic field of macroeconomics and a particular set of bloggers and journalists).

We are currently conducting deeper investigation accompanied by readiness to provide funding. We expect to learn more about what gaps and opportunities exist.

Foreign aid and global poverty

We have had a number of conversations about the policy landscape around issues directly affecting the global poor, such as the U.S. foreign aid budget and allocation, trade policy related to the developing world, etc. (We have unfortunately not been able to publish notes from a number of these conversations; others are linked to from our shallow writeup on this topic.)

We see this general cluster of issues as having potentially overwhelming importance, because of the direct relevance to the global poor (whose numbers and degree of poverty both exceed those of the U.S. population).

Our impression is that there is a substantial amount of philanthropic involvement in this area, and a relatively strong infrastructure that analyzes and advocates for policies that benefit the global poor. This infrastructure includes The Center for Global Development (CGD), a think tank we perceive as highly intelligent and effective in developing new ideas; we have supported CGD and may increase our level of support over time, but we also note that CGD has expressed a lack of desire to expand much further. It also includes the ONE Campaign (with a budget of roughly $30 million/year, supported by the Gates Foundation and others) and a network of large aid organizations. It has been argued to us that this infrastructure has been highly successful in preventing cuts to foreign aid despite recent concern over budget balance, and we find this a strong argument. The Bill and Melinda Gates Foundation has made influencing policy in this space a clear priority.

As such, we aren’t sure how much can be accomplished by a new funder in this space, at least at the level we’re currently contemplating (in the $5-25 million per year range). A few possibilities we’ve considered:

  • One issue we perceive relatively little attention to within the anti-global-poverty community is labor mobility, discussed above.
  • We also have the impression that there is relatively little advocacy – in the US policy arena (as opposed to the community around multilateral funders, etc.) – around allocating foreign aid for maximum humanitarian “bang for the buck.” This could mean, e.g., advocating for relatively more to be spent on proven cost-effective global health programs relative to more expensive and/or less proven programs; it could also mean advocating for more structural reforms, of the sort promoted by CGD (e.g., Cash on Delivery Aid). We see some reason to believe work along these lines could do more harm than good (by undermining the attempt to preserve/expand the total level of aid), and we believe that other funders in this space (particularly the Gates Foundation) recognize the importance of these issues, so we are not highly optimistic about pursuing this line of reasoning, but we may do so if capacity permits.

Because we perceive the infrastructure in this space as relatively strong and successful, we’ve considered providing funding and spending time in this area as a way of learning more about what a strong advocacy infrastructure looks like.

Improving democracy

We’ve been following the Hewlett Foundation’s evolving initiative on aiming to improve the general functioning of the U.S. democratic system, particularly with regard to the highly polarized current environment. We have reviewed an early report on this initiative (not public) and spoken with Daniel Stid and Hewlett Foundation President Larry Kramer about it.

It seems to us that federal politics are currently deeply dysfunctional, and we could imagine enormous gains (though it is hard to lay out the likely specifics of such gains) if we could help ameliorate this issue. However, “size of the problem” is only one part of our definition of “importance.” The other part – “likely impact of hoped-for legislative reforms” – is much less clear for us. It seems to us that past attempts at reforming the political system as a whole haven’t clearly done more good than harm (see, for example, points 1 and 2 at Wonkblog’s discussion of U.S. political dysfunction, which I see as a good concise summary of the major potential factors overall). Reviewing the fairly broad list of potential interventions laid out by Hewlett (in its not-yet-released document, and summarized to some degree in our conversation notes), we are ambivalent regarding what the likely impact of legislative reforms would be, assuming political victory.

“Crowdedness” is somewhat difficult to assess for this cause. The Hewlett Foundation seems likely to make it a real priority, and to try to interest other foundations in it too, which could dramatically increase the amount of philanthropic investment. It’s hard to say, at this point, to what degree this will happen and how much space (and what sort of space) will remain for us to potentially fill.

Overall, we are glad to see that the Hewlett Foundation is taking on what we believe is one of the world’s most pressing issues, and we plan to follow its work with interest. At this time, we see greater likelihood of getting heavily involved (in the sense of “committing” to) the causes listed above, though that may change as we continue to follow Hewlett’s work.

Climate change

We have done a shallow-depth investigation of climate change, an area that gets a great deal of philanthropic attention compared to all of the above causes. The potential impact of climate change mitigation is enormous, but not (by our estimates, based on mainstream projections) clearly larger than that of other causes we’ve classified as “ambitious longshots.” We do see a case that climate change deserves special attention because of its potential as a global catastrophic risk: there is a risk that mainstream projections are badly off and that the consequences will be much worse than currently projected. We will discuss this aspect of climate change (and the interventions we feel are most appropriate to deal with this relatively low-probability, high-impact scenario) in an upcoming discussion of global catastrophic risks.

Tax policy

Tax policy, like macroeconomic policy, has theoretically huge economic stakes and a good deal of attention from intellectuals. We see it as having substantially more attention from funders and nonprofits, and (likely as a consequence) fewer gaps in the work done by intellectuals (particularly with regard to developing workable policy proposals). We also see less room for impact from new academic research on related matters, as the main bottleneck to improved policy seems to be politics (in particular, resistance from groups like Americans for Tax Reform to changes that would involve new taxes or reduced tax expenditures) rather than knowledge. We have done a shallow investigation of this area and will be writing it up in the future.

Green fields: outstanding “room for more philanthropy”
We’ve identified a small number of causes that seem to have at least moderate importance and potential tractability, while being extremely “empty” – very little infrastructure in place pushing for what we would see as positive policy change.

One such area is what Steven Teles calls “rent seeking.” The broad idea is that there are some industries in which government regulation has been captured in a manner that makes it unnecessarily difficult and expensive to provide a service, so the existing providers of this service benefit from inefficiently low levels of competition. Consequently, existing providers tend to push for preserving and expanding such regulation. A classic example would be that of taxis: an artificially restricted supply of taxi medallions makes it artificially difficult and expensive to become a taxi driver, and the existing medallion owners have an interest in continuing to artificially restrict the supply. This dynamic results in unnecessarily high taxi costs, low taxi supply, and fewer job options for people who would consider being taxi drivers. It’s been claimed that similar dynamics apply, to varying degrees, to a broad range of occupations, both lower-skilled and higher-skilled (such as doctors, dentists, lawyers, and accountants).

Prof. Teles believes that there is little in the way of concentrated advocacy groups to counteract “rent seeking” in occupational licensing (by arguing for less protective regulation and more permissiveness in who can e.g. drive taxis), and that even creating a small advocacy infrastructure could make a big difference in combating artificial supply restrictions. Most importantly, a small number of victories at the local and/or state level could (he argues) raise the general profile of these issues, create a model for people in other areas, and lead to “compounding” policy change at the state and local level. We expect that efforts focusing on higher-skilled occupations would have quite a different profile than efforts focusing on lower-skilled occupations, and we do not have a strong sense of which is likely to be more promising.

We have had an initial conversation with Institute for Justice about this topic, and may look into it further.

Other causes in this category:

  • Zoning reform to enable more construction and urban density. It seems possible that there is a currently excessive level of regulation held up by those (property owners) who benefit from a restriction in supply of housing, business space, etc. While specific developers may advocate heavily on behalf of specific projects, it seems to us (from initial conversations) that there is very little advocacy infrastructure making the public-interest case for general increases in how much development is allowed.
  • Incentives for organ donation. GiveWell Senior Research Analyst Alexander Berger has an unusual degree of familiarity with this area. It appears to us that there is practically no work being done on finding, and promoting, ethical and safe ways to provide incentives for organ donation, something that could have large health benefits and save a significant amount of money for the health system.

Other causes of interest
We are interested in a few other causes that don’t fit into any of the above categories.

  • We’ve had some conversations about the idea of improving the general quality of policy analysis available to state-level governments, where there may be a type of void that doesn’t exist at the federal level. This is a very preliminary idea at the moment and we will likely be writing more about it.
  • We are investigating the treatment of animals in industrial agriculture at a medium-depth level, due largely to a particular interest on the part of one of our employees. This is a cause that preliminarily appears relatively “uncrowded,” and according to some moral frameworks could be seen as having enormous importance as well. We’re also intrigued by the possibility that Steve Teles raised of working more generally toward accountability of industrial agriculture companies on a broad array of issues; this could have implications for animal welfare, climate change, antibiotic resistance, farm subsidies, and potentially nutrition as well.
  • Intellectual property reform could present an unusual combination of unusually high tractability (see notes from our conversation with the Electronic Frontier Foundation), unusually high uncrowdedness (see our writeup on software patent reform, though intellectual property reform need not confine itself to software), and reasonably high importance (though we’ve had a good deal of trouble estimating this last piece). There could also be connections with trade policy, as mentioned in our conversations with Steven Teles.

Some major issue areas that we are less likely to prioritize
There are a other issue areas that we may investigate at some point, though we consider them less promising than the issues listed above.

  • U.S. education generally is a popular area among philanthropists, and the education policy space generally seems to be heavily influenced by the agendas of three major foundations: Gates, Broad and Walton (references to this in conversation notes here and here). At the levels of funding we’re currently contemplating, we have difficulty imagining that we could substantially contribute to or alter this agenda.
  • Health care policy is highly important, and there is arguably some degree of “window of opportunity” to affect the specifics of how the system changes in reaction to the recent passage of the Affordable Care Act. However, our loose impression is that (a) this is the major priority of one of the major U.S. foundations (Robert Wood Johnson) and that (b) more generally, this area seems highly crowded and we haven’t become aware of any likely promising angles that we could take on.
  • A very broad area of policy, with potentially very far-reaching repercussions, is the issue of inequality and the question of the extent to which (and manner in which) U.S. governments, at the federal, state and local level, should redistribute wealth. Our impression is that this cause gets far more attention from philanthropists, nonprofits and intellectuals than questions about helping the global poor, who we feel are more numerous and benefit more from redistribution relative to the U.S. poor. We have not come across any aspects of this broad space that seem appealing by the criteria we’ve laid out.
  • Our impression is that environmental issues (aside from climate change, discussed in an earlier section) also receive a great deal of attention from philanthropy, and are not particularly likely to be of comparable humanitarian significance.
  • Trade policy is another major policy area. The main potential benefits we see to working on trade policy pertain to the impact on the developing world, so we’re inclined to classify it with the set of developing-world-oriented policy areas discussed above. Generally, it seems to us (based on loose impressions and no particular source) that there is reasonably strong infrastructure in place representing most relevant perspectives in trade policy, though we have not done a shallow investigation and may in the future.
  • Defense policy seems clearly important, and we aren’t aware of much in the way of advocacy infrastructure pushing to reduce unnecessary military expenditures and unnecessary military engagements. We plan to investigate this area at some point, but intuitively feel that philanthropy is unlikely to have much impact on this front and that the causes discussed earlier are more promising.

Other causes we may focus on in the future, but are not including in the categories above
Helping to strengthen a broad political platform. It can be argued that the strongest impact of philanthropic engagement with policy has been long-term promotion and development of a movement. (For instance, Steve Teles has notably made this argument with respect to the conservative legal movement). Rather than picking individual policy issues in which to invest, a philanthropist with interests in a number of a causes and clear set of values might achieve more by promoting their general values, along with the people and organizations that share them (since much of the long term benefits of investment in a given area may be in the form of empowering the particular individuals who receive support, who may go on to other things). However, we do not feel that our values are broadly shared by any existing, easily located major political movements.

In particular, we generally favor policy focused on benefiting low-income and otherwise disadvantaged people, even when it involves active government – an attitude often associated with the U.S. political “left” – but we place particularly high value on the developing world. Additionally, we place high emphasis on the value of economic growth and innovation (which we feel are likely to benefit future people). In the long term, we could imagine exploring the possibility of helping to promote a political platform consistent with these values and trying to find, connect, and support people and organizations supporting this platform. We’re aware that people who share these values will have many disagreements over policy, but feel that there could nonetheless be major benefits to laying out, and promoting, a platform that emphasizes both global humanitarianism and economic development.

We think of this as a long-term possibility with highly uncertain value. We are doing some very preliminary work now to explore the idea, but feel that more direct engagement with specific issues will make us better-informed, better-connected, and overall better-positioned to explore such a possibility further down the line.

Policy related to global catastrophic risks. We are treating “global catastrophic risks” as a separate category of work at the moment, and we will be writing more later this year about our likely priorities in that category. So far, we haven’t identified clear cases in which a particular policy change seems highly important for one of what we consider the most important global catastrophic risks (other than climate change, discussed above), though this may change. We’re looking to build our general capacity for policy-oriented philanthropy by working on other causes, and will hopefully be well-positioned to do relevant policy-oriented work if and when it becomes important to do so.

Policy related to scientific research. We see policy around scientific research (for example, the budget, mandate and policies of the National Institutes of Health) as potentially extremely important, but at this time we don’t feel that we have strong enough scientific advisory capacity to have a good grasp on the relevant issues. We are building our scientific advisory capacity via separate projects, and will be writing about this more in the future. Again, we will hopefully be well-positioned to do relevant policy work if and when it becomes important to do so.

Other categories. This post has focused exclusively on our medium-term plans for U.S. policy. We continue to explore a broad variety of other sorts of philanthropic work, which we will be writing about in the future.

Bottom line and our plans from here
We’ve spent a good deal of time investigating potential focus areas in U.S. policy, and we have a very large number of questions remaining. There are many causes that we have much to learn about on many dimensions, including both questions like “How should policy change and why?” and questions like “How can a philanthropist increase the odds of a particular policy change?” One of the aims of this post is to stimulate discussion and help determine which questions are most important to focus on. Our hope is to finalize “commitments” to causes by the end of this calendar year.

Our current working agenda is as follows:

Deep investigations of cause areas: looking actively for funding opportunities and being highly open to funding them.

  • We are exploring both labor mobility and macroeconomic policy at this level.
  • We have done a fair amount of work on criminal justice reform, and are pausing our investigation of it for the moment.
  • In addition to finding funding opportunities, we are also interested in (a) doing thorough reviews of academic literature to assess the best arguments on each side of the relevant policy debates; (b) trying to substantially refine our “importance” estimates after gaining more context. Both (a) and (b) could be substantial projects, and we are likely to do them only for causes that we do deep investigations of and seriously consider committing to.
  • Depending on our capacity and on the results of lower-depth investigations, we may do this sort of “deep investigation” of other causes as well.

Medium-depth investigations of cause areas: having 5+ conversations per cause area to get a good sense of the overall landscape.

  • We are hoping to explore the “rent seeking” and “zoning” causes discussed above (under “Green fields”) at this level.
  • We are also conducting a number of conversations on factory farming, currently with a focus on animal welfare implications.
  • There are several other cases in which we have done a medium level of investigation, including foreign aid and organ donation (in the latter case, we feel we have a strong understanding of the issue largely through Alexander Berger’s personal background, as mentioned above).
  • We are likely to do a future investigation on improving the general quality of policy analysis available to state-level governments, which we will be writing about more in the future.
  • Other causes we may investigate at this level include tax policy and intellectual property reform.

Shallow-level investigations of cause areas: having a few conversations to get a basic picture of an area. We hope to look into some of the causes we have done little investigation of, such as health care policy. However, this area is a lower priority than the above, and we aren’t sure whether we’ll get to it this year (whereas we do expect to make significant progress on all of the above points).

Hiring. Having a decent sense of our likely interests, we are working on hiring U.S.-policy-specific staff, so that when we do make commitments, we’ll have the staff available to execute on them. We have a major hire starting in June whom we will be writing more about in the future.

Limited time and capacity. At the moment, we are executing on the above agenda; if and when we complete currently-in-progress items and have more capacity, we may promote some causes from the “medium” to the “deep” level of investigation or (less likely) from “shallow” to “medium.” However, around the end of the calendar year, we expect to use whatever information and staff we have at that time to make commitments.

A journalist visits GiveDirectly villages in Kenya


In February, Jacob Kushner, a journalist living in Kenya, contacted us. We have long been interested in seeing more substantive coverage of philanthropy, so we were excited to talk to him.

As a pilot project, Mr. Kushner decided to visit villages in which GiveDirectly had distributed some of its earliest cash transfers. We spoke with Mr. Kushner several times to offer thoughts and feedback, but we encouraged him to write about whatever he found (positive or negative about GiveDirectly). We also put him in touch with GiveDirectly to confirm that staff there were amenable to this project.

Mr. Kushner completed his trip in April, and his full article follows. He also shared his full interview notes with us which we’ve posted here.

We’ve summarized what we took away from his article here. Carolina Toth, Manager, People and Partnerships at GiveDirectly responds here.


When giving out cash to the poor, what happens when some are left behind?
A closer look at whether GiveDirectly’s cash transfers stoke community tension in Western Kenya

By Jacob Kushner

For several years now, the charity GiveDirectly has experimented with different ways of deciding who among Western Kenya’s rural poor should receive cash transfers. It’s an important consideration, because $1,000 means a lot to the families that receive it—and it can mean a lot of disappointment to the families that don’t. Last month I traveled to Western Kenya to speak with both lots, and I found that the discrepancy did not go unnoticed in their communities.

To date, GiveDirectly has undergone five different transfer programs in Siaya over the past three years, with different metrics for selecting recipients. I interviewed recipients from three of those cohorts:

  • The Google Cohort (approximately 850 ‘thatch-roof only’ recipients whose transfers were completed in October 2013)
  • The 200k Cohort (approximately 200 ‘thatch-roof only’ recipients whose transfers were completed in January 2013)
  • The 2M cohort (approximately 2,000 recipients divided into ‘thatch-roof only’ villages and ‘saturation’ villages (in which nearly everyone is eligible) who have received one major transfer and will receive the second and final one in July 2014).

In a follow-up to a randomized controlled trial, GiveDirectly asked residents if they’d heard any complaints about GiveDirectly in their community. Sixty-four percent of respondents in Siaya County answered “yes,” as did 48 percent of those in the “Google” cohort (in Rareida it was 28 percent).

Fewer than 6 percent of respondents in all four groups said shouting or angry arguments had ensued because of the transfers, and fewer than 4 percent said they’d experienced crime, theft or violence or felt threatened as a result. Virtually no one said they’d argued with family members over how to spend the money, and no more than 7 percent in any group said their village elder had approached them asking for money.

Carolina Toth, Kenya Field Director for GiveDirectly, explained the results of a series of informal community group meetings in which GiveDirectly led residents in a discussion of who should be eligible for transfers.

Sixty-two percent of respondents in thatch-only villages said they’d heard complaints relating to ineligible households, compared with 46 percent in saturation villages. Thirty percent of those in thatch-only villages said they’d heard complaints about different criteria being used across different villages, compared with only 4 percent in saturation villages.

GiveDirectly concluded that the strongest takeaway from the discussions is that poorer ‘thatched’ households are more deserving but also that certain households that have mabati or permanent houses are deserving of the transfers as well. When asked about their own villages, residents preferred the saturation method. When asked about other villages, they preferred thatch-only. No one thought it would be “bad” if cash were given to some wealthier households.

Because recipients in saturation villages have yet to receive their second transfer (due in July), it’s too early to draw definite conclusions. But this and other previous reports leave several question unanswered:

To the extent that community tension may result in the wake of cash disbursements, how does that tension actually unfold? Who are the parties and what are some examples? Most importantly, what do non-recipients in those communities think about the fairness of the selection process? Do they feel stigmatized for not having received the money, and how does their perception of whether animosity resulted from the cash transfers compare with those of the recipients’ themselves?

In April I made a reporting trip to Siaya County to interview recipient and non-recipients in the communities where GiveDirectly has made those disbursements. Over three days I interviewed 15 people, asking whether they were happy with GiveDirectly’s selection process and whether any tension arose in their communities as a result of it.

I interviewed some recipients from each of the three cohorts and also interviewed recipients and in both the ‘saturation’ and ‘thatch’ divisions of the 2M cohort. I interviewed four non-recipients, at least one in each of the three cohorts.

My interviews seemed to reflect many of the conclusions of the RCT and subsequent follow up interviews and meetings. No one reported intra-family arguments about how to spend the money or being coerced by a spouse or family member to spend it in a particular way. Only one recipient said he’d originally disagreed with his spouse but that they eventually came to a mutual agreement. No one reported theft or that their own money had gone to waste in any way.

But 12 of the 15 respondents did indicate that some amount of tension had fostered in their community as a factor of some people having received money while others did not. By far the most tangible conflict mentioned to me occurred in the 200k cohort in the village of Koga.

There, the village elder did not receive a cash transfer. He was, however, consulted by GiveDirectly staff to assist in a tour of the boundaries of the village so GiveDirectly could identify eligible households, for which he was given a small token payment as compensation for his time. But in the words of one recipient there, “there was a scandal.” The elder “had conspired (to enlist) some households that were outside the area and had better houses, with the understanding that they would give him some money.”

GiveDirectly staff say the elder seems to have directed residents who lived in tin-roof houses to “squat” in vacant thatch roofed houses in order to receive the money. Subsequently, the assistant chief, with the support of the other village council members, dismissed the elder from his position.

When I spoke with the elder, he confirmed that he had misrepresented certain households in the village so they would be enrolled in the program. He justified that decision saying, “I was the village elder and I was working for the (entire) community.”

He said tension resulted when the initial disbursements were made and some families, including his own, were left out.

“I felt degraded by my community members. They were laughing at me that I didn’t receive any help even though I was the leader of the community. I was so humiliated.” He said the incident led him to ‘resign’ after more than 35 years of serving as an elder in Koga (he is 62 years old).

The second most tangible takeaway was the resentment and frustration expressed by the four non-recipients I interviewed. One woman in a “saturation” village was visibly angry as she described how she was not selected because the living room in her tin roof house is cemented, even though her other rooms are not. Another Koga man said he was cheated out of a transfer:

“The time the GiveDirectly team was working in the village, they came to my home but at that time I was grazing cattle outside the compound and I saw them in my sister-in-law’s house. I was curious. But due to how relations within households go sour, my sister told the GiveDirectly team that I had left and was never around.”

Despite an appeal he said he made to GiveDirectly field staff, this man did not receive a transfer. He says his economic situation is similar to that of the other recipients:

“I live in a house like this—(a) grass thatch house. I have children in school and I struggle to pay their fees. Some of my children for lack of funds have to be supported by my relatives in other areas, in Nairobi. I have only two cattle.”

GiveDirectly staff pointed out that “targeting” is a universal problem in development aid. Other methods used to select recipients—such as letting communities vote on who should receive, or requiring people to go to some lengths to prove they are indeed quite economically poor-off—have major drawbacks: Cronyism, and excessive bureaucracy and burdens, respectively. As an alternative, GiveDirectly employs another common method that uses easy-to-observe characteristics such as roof style to judge how wealthy or poor a household is. According to GiveDirectly’s own research, less than 5 percent of people in the 2M cohort villages complained, legitimately or otherwise, of being unfairly excluded. (In comparison, a recent study of the Kenya Hunger Safety Net Program found an exclusion error rate of 46 percent).

The man in Koga who says he was unfairly excluded also expressed sympathy for the Koga village elder. “I would not be happy with what has happened to him, because the feeling he has now at losing his job is the same feeling I have at not getting the money. I feel bad for him because I am also going through some pain.”

The man also aired some critiques as to how some people in the community spent their money.

“I saw some beneficiaries, the way they misbehaved when they got the money, and that made me feel it is important that recipients receive training on how to spend it. For example there are people who wasted it on drinking sprees, and others bought items that they didn’t understand how they would maintain. For example, one bought a motorbike and used it for a few months, but now it is unused and has not really helped him.”

Indeed, several interviewees mentioned the need for training to accompany the transfer process. GiveDirectly currently does not provide training or advise recipients as to how they should spend their money. GiveDirectly does, however, provide a brochure that lists different possible categories of expenditure such as home construction, business, and farming. GiveDirectly is considering experiments in which brochures also list the average returns that previous beneficiaries earned on each category of investment.

After completing the interviews, I asked Carolina Toth, the GiveDirectly field director, what she made of it all. I asked Toth what she thought about the village elder scandal in Koga—that a man who had served as elder for 35 years lost that position not because he violated a community custom, but simply a rule imposed by GiveDirectly.

“The village elder more often than not is one of the richer members of the community,” Toth said. As to his “previous feelings of entitlement to benefit from whatever is happening … I don’t think that’s an expectation we want to uphold.”

Toth and I also discussed the consequences for individuals who are excluded in a community where most residents receive the cash.

“It’s definitely a psychological event in their live,” Toth said. “But we know from the (randomized controlled trial) that there are huge spillover effects to the people who didn’t receive.”

When I asked Toth about the man who says he missed out on the transfer because his sister-in-law misinformed the GiveDirectly staff that he was not living in the village, Toth said it’s certainly true that some people get left out by mistake. But she said such cases are rare. As to the woman with the cemented living room who didn’t receive cash even though the rest of her home is not yet cemented, Toth said the GiveDirectly field staff can only make decisions based upon what they see—and that the distinction between a cemented house and a non-cemented house is not always entirely clear under such circumstances.

The vast majority of people who aren’t selected, said Toth, are skipped because they come from a marginally higher socioeconomic standing to whom the money would be less useful.

“What is the value of $250 given to a family that’s richer? Wouldn’t that be more valuable in the hands of people who are really poor?” Toth asked. “We have a mission of giving to the extreme poor, so by excluding some people who are not in the extreme poor, you are able to reach more extreme poor.”

Ultimately, the question any cash transfer implementer must decide is, “Is the possibility that community tension may result from a non-universal disbursement so great or concerning that transfers should be made to all residents in a village despite the opportunity cost that fewer, even poorer people in other villages will not receive any cash?”

Thus far GiveDirectly has answered that question in the negative. With certain exceptions (such as allowing communities to nominate a pre-determined number of otherwise unqualified people for the disbursements) and with increased nuance (by considering more advanced criteria than simply thatch versus tin roofs and indoor plastering), GiveDirectly intends to continue excluding those residents who do not qualify as the poorest of the poor.

Jacob Kushner is a journalist based in Nairobi. He reports on foreign aid and investment in Africa, human rights and the extractives sector.

Narrowing down U.S. policy areas

Throughout the post, “we” refers to GiveWell and Good Ventures, who work as partners on GiveWell Labs.

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).

Nothing But Nets

In 2014, we prioritized Nothing But Nets (http://nothingbutnets.net) as a potential GiveWell top charity because it funds insecticide-treated nets to prevent malaria, one of our priority programs.

In early 2014, we contacted Nothing But Nets to explain our process and to invite it to apply for a recommendation. Nothing But Nets provided brief responses to questions we had previously sent them (.docx), but has decided not to fully participate in our review process at this time.

In our 2013 annual review, we wrote that we were seeing more interest from charities in participating in our process and expected fewer organizations to decline to participate. We’ve written this post to share our impression about Nothing But Nets’ decision.

Our understanding is that Nothing But Nets has a small team (~2 staff members) focused directly on fundraising, and that it would be challenging for its existing staff to engage with GiveWell in our process. Our review process would require a significant time investment, including at the very least, (a) several lengthy (~2-hour) phone calls to understand Nothing But Nets’ role and value added; (b) submission of documents we request and email responses to questions we ask; c) a multi-day site visit with GiveWell staff, and (d) review of any write-up we produce about Nothing But Nets.

Although GiveWell’s recent money moved is high relative to Nothing But Nets’ funding — in 2013, GiveWell directed more than $17 million to the 4 organizations recommended throughout the year, with more than $2 million going to each organization, and Nothing But Nets has raised approximately $50 million since its founding in 2007 — it would not surprise us if the amount of time needed to meaningfully engage with us would be a major cost for an organization Nothing But Nets’ current size.

With that said, based on the information Nothing But Nets has shared with us (its brief responses to questions we had previously sent, linked above) – as well as our view that we have been clear about the requirements and the likely benefits of becoming recommended – our impression is that that Nothing But Nets’ decision not to apply has not caused us to miss out on a likely top charity.

Notwithstanding this impression, we remain interested in Nothing But Nets and hope that they will engage with us in the future.

Update on GiveWell’s web traffic / money moved: Q1 2014

In addition to evaluations of other charities, GiveWell publishes substantial evaluation of itself, from the quality of its research to its impact on donations. We publish quarterly updates regarding two key metrics: (a) donations to top charities and (b) web traffic.

The table and chart below present basic information about our growth in money moved and web traffic in the first quarter of 2014 (note 1).

Money moved: first quarter

Growth in money moved, as measured by donations from donors giving less than $5,000 per year, was strong in the first quarter of 2014 (money moved was 96% higher than in the first quarter of 2013), and was substantially stronger than growth in the first quarter of 2013. The total amount of money we move is driven by a relatively small number of large donors. These donors tend to give in December, and we don’t think we have accurate ways of predicting future large gifts (note 2). We therefore show growth among small donors, the portion of our money moved about which we think we have meaningful information at this point in the year.

Growth in number of donors was also strong, and similar to growth in this metric in the first quarter of 2013.

Web traffic: first quarter

In the past, we have relied on data from the web analytics company Clicky for our metrics updates. We also track web traffic through Google Analytics, and between January 2012 and February 2014, Google Analytics consistently tracked lower overall traffic than Clicky. We do not know what the cause of the discrepancy between the two sources is, and do not have a view on which data source is more likely to be correct. For that reason, we present data from both sources here. Full data set available at this spreadsheet. (Note on how we count unique visitors.)

Traffic from AdWords decreased in the first quarter because in early 2014 we removed ads on searches that we determined were not driving high quality traffic to our site (i.e. searches with very high bounce rates and very low pages per visit).

Data in the chart below is an average of Clicky and Google Analytics data, except for those months for which we only have data (or reliable data) from one source (see full data spreadsheet for details).


Note 1: Since our 2012 annual metrics report we have shifted to a reporting year that starts on February 1, rather than January 1, in order to better capture year-on-year growth in the peak giving months of December and January. Therefore metrics for the “first quarter” reported here are for February through April.

Note 2: In total, GiveWell donors have directed $1.45 million to our top charities this year, compared with $0.70 million at this point in 2013. For the reason described above, we don’t find this number to be particularly meaningful at this time of year.

Note 3: We count unique visitors over a period as the sum of monthly unique visitors. In other words, if the same person visits the site multiple times in a calendar month, they are counted once. If they visit in multiple months, they are counted once per month.

Note 4: Google Analytics provides ‘unique visitors by traffic source’ while Clicky provides only ‘visitors by traffic source.’ For that reason, we primarily use Google Analytics data in the calculations of ‘unique visitors ex-AdWords’ for both the Clicky and Google Analytics rows of the table. See the full data spreadsheet, sheets Data and Summary, for details.
 

The Importance of Committing to Causes

Throughout the post, “we” refers to GiveWell and Good Ventures, who work as partners on GiveWell Labs.

In our work on GiveWell Labs, we’ve consistently found that the level of interest we show in a cause – including our perceived willingness to provide funding within it – is a major driver of what sorts of giving opportunities we’re able to find.

This dynamic has been one of the major factors in the grants we’ve made so far, and it’s also a major reason that we’re eager to “commit” to causes, as mentioned earlier this year. We believe that there’s a limited amount we can learn about a cause when presenting ourselves as “potentially interested in providing moderate amounts of funding” rather than “strongly interested in providing major funding.”

We’ve come to believe in the importance of committing to causes in order to investigate them, and in the importance of “giving to learn” for GiveWell Labs, via the following process:

  • We initially envisioned a process that first gathers information on giving opportunities and then identifies which grants should be made.
  • However, from observing the behavior of potential grantees and other funders, we came to believe that a funder must be highly prepared (and likely) to make grants in an area in order to find giving opportunities in that area. Many people will only make the relevant referrals, propose relevant ideas, etc. once they are convinced of a philanthropist’s serious interest in providing funding.
  • As such, we have in many cases tried offering funding in an area – or at least expressed strong interest in the area – before knowing what giving opportunities would turn out to be available. This approach has led to multiple cases in which much of the learning value of a grant (from our perspective) comes from the process leading up to the grant.
  • “Giving to learn” can mean multiple things. It can mean (a) funding research in order to gain specific knowledge; it can also mean (b) funding a project in order to learn from following the project’s progress. The dynamic laid out in the above bullet points represents perhaps the most counterintuitive meaning: “giving to learn” can mean (c) offering funding in order to learn from the process of finding grantees.

This post lays out:

  • An overview of the paths we’ve taken in the last few years to find giving opportunities for GiveWell Labs. More
  • Examples of where showing strong interest in a cause, and particularly in making grants within it, led to information that we couldn’t have gathered in any other way. More
  • The implications of this dynamic – including why we do not believe (contrary to what some have suggested) that funding research is necessarily the best way to gather more information relevant to our work (more) and why we think it is important to commit to specific causes fairly soon (more).

Approaches we’ve taken to finding giving opportunities for GiveWell Labs
Early on in our work on GiveWell Labs, we spoke to a broad array of people and organizations – including academics, funders and nonprofits – and asked them for their opinions on the best giving opportunities, broadly speaking. (We also asked for referrals to other people who might be able to help us with this question.) As noted in a previous post, this approach generally didn’t yield much in the way of actionable ideas (and was often met with responses like “That question is too broad” or “First I need to know what causes you’re passionate about”).

We gravitated toward assessing “causes”, which helped us to ask more focused questions (rather than “What is the best giving opportunity you know about?” we could instead ask something like “What would you do if you were a funder seeking to make progress in solving problem X?”) But as we conducted shallow (and even medium) investigations, we still encountered relatively few “shovel-ready” giving opportunities. We encountered organizations seeking more funding generally, but we didn’t see many cases where we had a clear sense that more funding would play a crucial role in allowing particular promising work to go forward.

At the same time, we were speaking with major foundations and trying to understand how they go about finding giving opportunities. We explored the possibility of co-funding projects with them, and we encountered ideas – such as a project combating malaria drug resistance in Myanmar (with the Gates Foundation) and the Service Delivery Indicators (with the Hewlett Foundation) – that seemed like interesting and relatively tangible (in the sense of understanding what activities were made possible by the funders’ support) giving opportunities.

In addition to these co-funding conversations, we devoted substantial time to exploring the cause of meta-research and observing how funders in that space were finding giving opportunities. We noticed that:

  • The “meta-research” ideas we saw, such as a registry for randomized controlled trials, were brought straight to the funders who already were known for supporting relevant research, and it seemed to us that the projects might get sufficient support this way without needing a broader search for funds. These funders seemed to us to be well-connected to the people best positioned to come up with ideas for working toward “meta-research” related goals.
  • A similar dynamic seemed like it might apply more broadly. We knew that as a grantee ourselves, we had been connected to the Hewlett Foundation by someone who knew of their interest in improving philanthropy; if not for that connection, it wouldn’t have occurred to us to approach them. Generally, it seemed to us (both from our reading of philanthropic success stories and from our conversations regarding “co-funding”) that funders encounter many opportunities via being approached, such that their reputation for being interested in one cause or another directly affects what opportunities they come across.
  • While investigating meta-research broadly, we sourced the proposal for a meta-research-oriented center at Stanford that we wrote about previously. This was a clear-cut case in which actively expressing an interest in funding certain kinds of projects led to discovery of a giving opportunity we couldn’t have encountered otherwise.

We started to feel that we might need to “invert” our investigative process: rather than (a) first “exploring” a cause, finding potential giving opportunities, and then deciding whether we were interested in providing funding, we should perhaps (b) pick a few causes and definitively express an interest in providing funding, before knowing of any particular giving opportunities. Our initial thinking that led to this idea was outlined in a 2013 post, Challenges of Passive Funding.

This shift led to a noticeable improvement in our ability to source tangible giving opportunities.

Examples of the “giving to learn” dynamic
The first cause we chose for a relatively deep investigation – including some grants – was criminal justice reform. Of the causes we were interested in, it seemed to offer the best odds of quickly finding “shovel-ready” giving opportunities, based on the comments of Steven Teles. We told Prof. Teles that we were interested in making some initial grants in this cause, and he quickly connected us to Mark Kleiman and Angela Hawken, each of whom sought funding. We also informed the relevant team at Pew Charitable Trusts that we were actively looking for giving opportunities, and discovered that this team was seeking funding (something that hadn’t come up in the first conversation we conducted with this team). We have since begun a thorough investigation of this organization’s track record in this space, with their help – something that wouldn’t have been as feasible if we hadn’t seriously been considering providing the requested funding.

Over time, we’ve seen more giving opportunities come up. We’ve been approached by multiple groups with confidential proposals to work toward reducing incarceration. In addition, Prof. Hawken contacted us when her organization, BetaGov, came across a seemingly unique and temporary opportunity to study the impact of changing marijuana policy in the state of Washington (more details forthcoming). These are giving opportunities we’re convinced we couldn’t have come across without expressing strong, credible interest in funding work on criminal justice reform (and in some cases, particularly Prof. Hawken’s, actually providing such funding).

In the meantime, Prof. Teles has continued to think actively about the topic of criminal justice reform, and has come up with multiple new ideas for things a funder might do. We are currently seeking to pause our work in this space, as we try to investigate other causes to a similar level of resolution; however, we’ve now gotten multiple people and organizations to see us as a potential source of funding and to start thinking about more work that would align with the aspects of the space we’re interested in.

Similar dynamics have applied to the other causes we’ve explored:

  • Malaria control and elimination. We commissioned Dr. Steve Phillips to explore this space for us and identify giving opportunities. We had substantial discussion with Dr. Phillips around setting expectations appropriately – in particular, what to say about the likelihood of funding – which he found important in order to have conversations about possible projects. In this particular case, we did not commit any funds to malaria control and elimination projects, but we wouldn’t have been able to conduct this project if we hadn’t seen a legitimate possibility of doing so, and we’d be hesitant to dig further on these proposals (or to do a similar project in another area of global health) without having a relatively strong expectation of following up with funding.
  • Labor mobility. We did a shallow investigation of the cause of labor mobility that included a conversation with Michael Clemens, a researcher on the global economics of migration who has been a leading voice on the humanitarian benefits of labor mobility.. However, it wasn’t until we communicated an intent to fund labor-mobility-related work that Dr. Clemens approached us with giving opportunities, including support of his own work as well as another project that we will be writing about in the future. We find the project both promising and unlikely to get funded without our involvement, and believe that we wouldn’t have been able to find out about it without specifically communicating an intent to provide funding. In addition, Dr. Clemens offered to introduce us to a person who might consider leaving their current post in order to pursue work in this area, but wouldn’t want this information widely disseminated.
  • New top charities. We have also been interested in making grants to increase the supply of evidence-backed charities serving the global poor. Here too, we have started conversations with research organizations that we wouldn’t have been able to have without a strong interest in (and high likelihood of) providing funding.

Why expressing stronger interest can lead to better giving opportunities
Without pretending to know exactly how the dynamics work, it seems to us that:

  • People are often hesitant to ask for funding, or even mention that they’re seeking it, until and unless they perceive a strong specific interest on the part of the person they’re talking to. (Just knowing that the person they’re talking to is a funder and “open to many possibilities” is often not enough.) Part of this may be a fear of being perceived as “unsuccessful” if they are public about having an idea that they can’t find funding for.
  • People are often hesitant to put time into fleshing out an idea until they see a potential path to getting it funded. This seems rational, especially since different funders will often have different preferences in terms of what information they find most important, what sorts of proposals they want to see, and what aspects of the work are most important to prioritize from their perspective.
  • Many people seem to seek funding primarily by going through their networks, and seeking out people who are clearly interested in what they’re doing (rather than by publicly disseminating their ideas).

In theory, it seems possible to have a world in which funding ideas are written up and posted publicly for anyone to browse. In reality, funding ideas are often not even internally fleshed out (much less written up) until specific interest is perceived. Because of this, asking someone for giving opportunities often means asking for substantial amounts of their time and energy, and it can be inappropriate to do so except when one has a high probability of following through with funding.

The approach we’re taking
Our basic heuristics for deciding what and how much to fund has been:

  • Be very thoughtful and careful about how we spend our time, and realize that making grants will almost always have implications for how we spend our time (by signaling our interests, by causing more people doing similar work to approach us, by forming relationships with grantees, etc.)
  • When we’re interested in an area, be willing to express strong interest in providing funding and to follow through with high probability.
  • Fund projects we come across that seem reasonable, that we’re willing to spend some time following up on, and that fit within our interests in terms of what areas we want to learn more about and see more proposals from.

Our priority at the moment is asking what sorts of giving opportunities might exist in different causes (and, along with this, learning about meta-issues such as the “giving to learn” dynamic described in this post). We think of this as an learning/information-gathering agenda, supported by “giving to learn” grants whose informational value comes from (a) following through on initial expressions of interest; (b) signaling our further interests; and (c) giving us opportunities to follow up over time and learn about the relevant people and organizations and their progress.

We’ve seen a few comments that we don’t seem to place much value on “value of information,” since we’re primarily funding direct work of various kinds rather than research projects aiming to identify the best causes. I disagree with comments along these lines. Our work is a research project aiming to identify the best causes, and funding projects in causes of interest is an important tool for carrying this project out. This sort of “giving to learn” provides certain kinds of information (e.g., “what are the giving opportunities in cause X like?”) relatively quickly and efficiently; more broadly, it is a form of “learning by doing” that has already yielded insights about grantmaking (such as how the “giving to learn” dynamic works) that would have been difficult to pick up in any other way. By contrast, funding studies would introduce the management challenge (costly in terms of person-hours, our scarcest resource) of trying to align researchers’ work with our own interests, and could take years to produce actionable information.

The importance of committing to causes
To date, we’ve quite deliberately limited our involvement in – and commitments to – any given cause. We believe that this has placed limits on how well we’re able to get to know the fields in question. If we were to make a substantial “commitment” to a cause – intending to allocate a substantial number of person-hours to it for the next several years, accompanied by a substantial potential budget – we would be able to:

  • Network more extensively, get to know the relevant people and organizations, and communicate the nature of our interests.
  • Encourage people to come to us with ideas, without having to caveat that our interest is preliminary and we may not be able to provide stable/renewable funding over time.
  • Generally do more investigation and learning about the cause, leading to refinements in the specific types of projects we’re looking to fund – which in turn would affect the types of projects that would come to our attention.

We believe these activities would lead to deeper understanding of the few causes we investigate, which would likely inform how we approach our lower-depth investigations of all causes. Accordingly, we see a great deal of value in making such commitments relatively soon, rather than trying to be comprehensive in doing lower-depth investigations of every possible cause of interest.