To date, our work on GiveWell Labs has been highly exploratory and preliminary, but we’ve recently been refining our picture of what we expect our output to look like in the reasonably near (~1 year) future. Our plans are still tentative, but have changed enough that an update seems worthwhile at this stage.
- Our main goal is to find the most promising charitable causes; we think of the “cause,” rather than the “charity” or “project,” as the most relevant unit of analysis for us at this point.
- We expect to recommend causes that combine high potential for impact with low existing philanthropic resources.
- We currently work closely with Good Ventures on this research. Cari Tuna is an active partner with us on these investigations, and we see Good Ventures as the initial target for our recommendations. Both GiveWell and Good Ventures anticipate other philanthropists (including some portion of GiveWell’s existing audience of individual donors) eventually participating in funding the opportunities we identify.
- We expect to investigate potential cause recommendations for a substantial amount of time before releasing recommendations, but we are not holding ourselves to conducting a “comprehensive” investigation before releasing recommendations. At some point in the future, we will recommend causes based on the information we’ve gained so far, while continuing to explore more. This approach mirrors the approach we’ve taken in the past with charity recommendations: taking some time up front, releasing recommendations, then continuing to seek better recommendations even as we promote our existing ones.
- For the near future, we will focus on exploring causes at limited depth, in order to identify the most promising ones. We are planning to explore many causes at the “shallow” level (~20 hours), and a smaller number of causes at a deeper level (~3 months, with the investigation outsourced to a contractor when possible). The causes we explore at a deep level will be based on the causes we find most promising at a given point in time.
Note that we continue to collaborate closely with Good Ventures on our work in these areas, which constitute a largely shared agenda, and “we” generally refers to “GiveWell and Good Ventures” in this post.
When we first launched GiveWell Labs, we shifted to the idea of finding the best projects. We had realized that many charities are extremely diverse organizations, and many philanthropic opportunities involve funding particular parts of them. (A particularly extreme case might be that of a university, whose professors could be funded to do promising research but which we wouldn’t want to provide unrestricted support to). We laid out a set of criteria for such projects.
However, we’ve since moved to the cause as our fundamental unit of analysis. We’d roughly define a “cause” as “a particular set of problems, or opportunities, such that the people and organizations working on them are likely to interact with each other, and such that evaluating many of these people and organizations requires knowledge of overlapping subjects.”
Some reasons for this shift include:
- It’s generally very difficult to evaluate a project in isolation from knowledge of the cause it sits within.
- Even for the most “proven” interventions we’ve been able to find – such as bednet distribution – we’ve put in a great deal of work to understand the nuances of the evidence base and the funding landscape, and we now feel better positioned to assess other ideas that touch on these areas (for example, funding of research on insecticide resistance).
- An instructive experience was when, last year, we sought to evaluate the Cochrane Collaboration, whose work we were already highly familiar with. Even to get a basic sense of its situation, we felt it necessary to do a miniature survey of the funding landscape, and doing so increased our interest in and understanding of meta-research for biomedical sciences. After this survey, we felt better positioned to understand funding opportunities in this area than in most others, which is why we prioritized it as our first medium-depth cause investigation (more on this in a future post).
- In trying to evaluate giving opportunities in unfamiliar areas – whether brought to us by individuals, charities or foundations – we’ve found that our assessments are highly volatile and tend to change rapidly with new information, making it hard to form confidence without getting a better sense of the cause-level issues.
- In particular, when evaluating a giving opportunity, we feel it’s important to have a sense of who the other funders are in the relevant space, and what sorts of projects they are and aren’t interested in.
- We’ve also come to the view that committing to a cause can be necessary in order to find giving opportunities within that cause. At this point, we don’t think one can take the lack of “shovel-ready” projects within a cause as a sign that the cause doesn’t have room for more funding. More at a previous post on active vs. passive funding.
- Between the above points, it seems to us that it may be appropriate to make a several-year commitment to a cause, in order to form the appropriate relationships, source giving opportunities, try different approaches and learn from them, etc. In speaking with foundations, we’ve generally gotten the sense that their approaches to the causes they’ve focused on have changed dramatically over time.
- Another major input into our thinking has been the fact that nearly every major foundation (some of which we find impressive) seems to approach giving from this basic perspective, i.e., focusing on particular causes.
We do believe there are potential ways to give well without taking a “cause-focused” approach. These may include
- Focusing on interventions with strong formal evidence of effectiveness regardless of cause, as GiveWell has for most of its history. Our take at this point is that such interventions are rare, and such a focus largely ends up leading to a focus on causes within global health and nutrition.
- Focusing on finding and funding outstanding people. I believe that this approach can be very effective when one uses one’s own network (and thus effectively trades deep knowledge of causes for deep knowledge of people), but that it’s more difficult to carry out such an approach with scale and systematicity. Funders aiming to do the latter include Ashoka, Echoing Green, Draper Richards Kaplan, and the Skoll Foundation.
- Funding prominent organizations and individuals whose prominence makes it relatively easy to assess them (e.g., by triangulating others’ opinions).
- We seek to cast a wide net, considering many options. At the same time, we focus our resources on the options that seem most promising.
- We will be asking a set of consistent critical questions of each cause we consider. At this point, these questions are tentatively: “What is the problem?”, “What are possible interventions?” and “Who else is working on it?”, and we are looking for causes where the philanthropic funding and presence are unusually low relative to the importance, tractability, and opportunities around the problem(s) in question.
- We expect the answers to these questions to involve judgment calls, and we aim to be transparent about such judgment calls.
- We seek to release recommendations at the point where we (a) have put substantial time into research, and (b) feel that our recommendations are highly likely to be better than what our audience can come up with on its own.
- We do not seek perfect or comprehensive knowledge, preferring to issue recommendations once they’ve crossed a certain threshold of thoroughness and then continue to refine them over time. Early recommendations may have some element of arbitrariness in them (e.g., being sensitive to what we chose to prioritize), and we expect recommendations to become more systematically grounded over time.
In the past, this approach has applied to recommended charities; at this point, we tentatively anticipate applying it to charitable causes. While we aren’t yet ready to set a deadline, we hope that we will have recommendations as soon as possible regarding which charitable causes are most promising for a major philanthropist to invest in. We expect to recommend to major philanthropists that they consider hiring specialized staff to explore these causes.
- Lower-depth investigations. So far we have published 3 of these, and they are available here. We have examined climate change, international migration (report forthcoming), promotion of in-country migration, and detection of near-earth asteroids. Some investigations have taken relatively little time (in the range of 20 person-hours) while some have taken substantially longer (getting a basic feel for the climate change literature took a significant investment).In all cases, we’ve sought to get a basic sense of (a) the significance of the problem to be addressed; (b) broad possible avenues of intervention; (c) who else is working in this area. By collecting this basic information for many causes, we hope to be able to identify the ones that have a particularly strong combination of humanitarian significance, tractability, and “room for more philanthropy” (i.e., being under-invested in relative to other causes). We feel that most of the time we’ve spent on these investigations has been necessary to produce a basic understanding of these issues, and that it would take much more time to gain high confidence or gain a strong sense of the specific giving opportunities that are out there.
- Higher-depth investigations. We are currently working on a higher-depth investigation of a particular sub-field of meta-research. The investigation has involved a large number of conversations and, unlike the lower-depth investigations, is aiming to give us a fairly clear sense of what the major players and the giving opportunities in this space look like. It is difficult to say how much longer this investigation will take; when it is complete, we hope it will become a template for future high-depth investigations, which we may look for contractors (e.g., subject matter experts) to work on.
- Cross-cutting projects intended to put us in better position to look at large numbers of causes. These include our work on understanding the basics of scientific research and political advocacy (which we will write more about in the future), our work on history of philanthropy, and co-funding work.
So far, we have not prioritized areas solely on the basis of how promising they seem: we’ve also factored in how prepared we felt to investigate them, given our existing background knowledge. For example, as mentioned above, we felt that we were better grounded in the issues around meta-research than in most issues, so we chose this area for our first high-depth investigation. As we develop a better sense of what these investigations involve, such considerations will become less of a factor.
When it comes to higher-depth investigations, we are hoping to try outsourcing these investigations to contract researchers. We are planning to produce a meta-research writeup that can serve as a fairly concrete template for what we’re looking for, and we believe it’s possible that a contract researcher – perhaps a subject-matter expert in the relevant field, perhaps a consulting firm that has done this sort of work for other foundations – can create a similar writeup for other causes.
We expect finding such contractors to be challenging, and we expect working with such contractors to involve significant investment on our part in terms of specifying what we’re looking for and managing the process. For this reason, we’re not currently seeking to outsource our lower-depth investigations in the same way; we’d need a good deal of output to justify the investment we expect to make. Also for this reason, we’re hoping to begin experimenting with contractors soon, rather than waiting until we’re confident in which causes are most worth exploring at greater depth.
All of the above plans are tentative; we plan to move forward as outlined and change course if/when it makes sense to do so.