We divide our scientific research funding into two categories: neglected goals and basic research. We believe that some research areas are underfunded because achieving the relevant research objectives is underrated by the “broad market” (according to our values). We call such research objectives “neglected goals.”
In 2014, we set a goal to be in a position to identify focus areas in science by the end of 2016. This post explains our initial plan for this work, our original hopes and expectations, what we have done so far, and our plans for work in this area going forward. In brief:
- Our initial plan was to identify focus areas using a series of shallow and medium-depth investigations, analogous to the process we used to identify focus areas in U.S. policy and global catastrophic risks.
- We found that our investigations took longer than expected and we felt that they gave us an inadequate basis to declare focus areas and hire specialist program staff to lead our work in those areas. Moreover, we could not envision investigations with acceptable time costs that would form an adequate basis for making such decisions.
- However, our investigations did, in multiple cases, result in our science advisors’ identifying “standout” giving opportunities: giving opportunities that seemed unusually promising by the standards of the field they were investigating, and strong compared to giving opportunities we’ve seen generally.
- We decided to pivot to a model in which generalist scientific advisors are given a broad mandate to opportunistically identify standout giving opportunities within about a dozen areas. Rather than investigating each area in depth and choosing a few as focus areas, they investigate one at a time, looking primarily for standout opportunities, and choose which area to investigate based on their subjective estimate of the odds of finding standout opportunities. We’re very excited by the giving opportunities that the science team is finding under this model, and it’s unclear whether it would have been better to use our previous model and hire staff specializing in just a couple of program areas.
- A spreadsheet summarizing our list of priorities and cause-specific progress so far (listed in alphabetical order) is here.
We are likely to give a separate, shorter update on basic research in the future.1
Our initial plan
Our initial plan for identifying neglected research goals to fund was modeled on the process that we used to identify focus areas in U.S. policy and global catastrophic risks. The general strategy was to quickly get basic information about the comparative importance, tractability, and neglectedness of the potential focus areas and then select those that seemed outstanding relative to those criteria. The key steps of that process were as follows:
- Collect dozens of potential focus areas from conversations with experts, conversations with others in our network, and our background knowledge
- Select about a dozen potential focus areas for “shallow investigations”
- Select several for “medium-depth investigations”
- Potentially identify specialists to lead our work in the most outstanding areas identified (relative to the criteria)
Our hopes and expectations
When applying this process to global catastrophic risks and U.S. policy, we found that relatively brief investigations of potential focus areas were able to give us a sense of the comparative importance, tractability, and neglectedness of the areas we investigated. We hoped that something similar would be true when investigating potential science focus areas, and some areas we considered would emerge as outstanding focus areas to support in comparison with the others.
We also hoped, but did not expect with confidence, that we would find some areas of science to fund that would have outstanding returns in comparison with the best-in-class giving opportunities that Open Philanthropy has discovered so far.
Our process applied to biology
We began to apply this strategy to neglected research goals in mid 2015. We first brainstormed about 40 biology-related areas to investigate. (We started with biology for reasons discussed in this post.) We selected about 15 for special consideration based on simple estimation of problem size (drawing from disease burden estimates or prior investigations or other causes); available information on funding to the field (e.g. from grantome.com or the NIH website); and our intuitions about neglectedness.
We started “shallow” investigations while hiring generalist scientific advisors. Job candidates worked with us on these investigations as trial assignments. Our current scientific advisors joined the organization full time in mid 2016.
Results vs. hopes and expectations
After some iteration, we settled on a process in which our scientific advisors spend a month surveying a field and trying to identify outstanding grant opportunities, prepare an internal report, and then seek to make grants that are either (i) potentially very high upside (even if not shovel-ready) or (ii) good, shovel-ready, and requiring limited investigation. Right now, the best illustration of this process is our report on the mechanisms of aging.
We’ve now investigated five goals using this approach, including mechanisms of aging, obesity, novel platforms for vaccine development (for biosecurity), broad-spectrum antivirals (for biosecurity), and developing world agriculture. (We also investigated some other areas with other methods, including malaria, tuberculosis, STDs, gene drives, animal product alternatives, and Alzheimer’s.) Given the time cost involved and the fact that we already seek and receive input from subject matter experts privately, we currently don’t have plans to produce public write-ups related to most of these investigations.2
We found the “shallow” investigations useful for getting an overview of the technical challenges in a field and highlighting dynamic areas of research that could be considered for additional grantmaking. However, we found these investigations less useful for getting a sense of what sorts of scientific advances might be realistic on what timelines, how much funding fields could productively absorb, or what fraction of the most important work would happen anyway without our support. When we began this process, we guessed that a handful of potential focus areas were most promising. While our opinions about how best to pursue grantmaking in these areas changed (in some cases, substantially so), our list didn’t change very much. We didn’t feel this would be an adequate basis for declaring specific program areas or hiring people to lead them, and we could not envision investigations with acceptable time costs that would form an adequate basis for making such decisions. So we began to consider alternatives to our previous model for identifying focus areas and finding staff to lead our work in those focus areas.
Though our investigations left many important questions unanswered, they did serve a number of other valuable purposes. Most importantly, they gave our scientific advisors enough familiarity with the area investigated that they could seek out and evaluate opportunities in the area, and some of these opportunities led to grants or investments that seem outstanding to us. Examples include: Target Malaria (global health), Impossible Foods (animal welfare), and some ideas for broad-spectrum antivirals (biosecurity, currently under investigation). These opportunities were (often large) grants/investments with a clear potential path to solving or substantially alleviating a major problem related to one of our existing program areas.
These opportunities seem ballpark-competitive with, and in some cases superior to, other best-in-class giving opportunities that we are aware of. In addition, they seem relatively exceptional to us in the sense that we don’t think we can identify many comparable opportunities in those areas - global health, biosecurity, and animal welfare - in the near future. For example, GiveWell’s estimated cost per life saved for AMF is roughly $7500, and I’d estimate that the expected cost per life saved for our grant to Target Malaria is substantially lower (perhaps 5-20x lower, though less robust).3 However, based on a cursory investigation of other opportunities to fund science relevant to tuberculosis and malaria, most other opportunities in related areas seem substantially less promising than Target Malaria and therefore unlikely to offer expected returns much better than AMF.
We also explored some funding opportunities through two other methods: a RFP in partnership with NIH for high-risk, high-reward research (write-up forthcoming) and a series of brainstorming conversations with scientists whose work we find especially interesting.4 These approaches led to some exciting grant opportunities, though at a lower rate per unit staff time than the approaches discussed above.
Our new plan
In light of:
- challenges to getting the information that would be needed to select science focus areas and hire specialist program staff to run them,
- the fact that our generalist scientific advisors were able to find outstanding giving opportunities without hiring program staff for specific focus areas, and
- the fact that these giving opportunities seemed superior to the opportunities we could find using other methods,
we abandoned our previous cause selection model (in this instance) in favor of a more opportunistic approach.
We now plan for our generalist scientific advisors to do exploratory grantmaking relevant to potential neglected goals we have identified, in accordance with the following principles:
- Prioritize exploratory grantmaking aiming for standout giving opportunities addressing the neglected goals we consider reasonably high-priority.
- Other things being equal, give priority to investigations in areas related to existing program areas (especially biosecurity and farm animal welfare) and Alzheimer’s disease (which is a high priority for Good Ventures, and which we have agreed to help with research on for this reason; we expect grants in this category to be classified as Good Ventures grants that we assisted with, rather than as Open Philanthropy Project grants that went through our full process).
We see this as a relatively natural division of cognitive labor: generalist staff with a deep understanding of Open Philanthropy’s values and objectives identify goals that would be valuable to accomplish and are likely to be neglected, and generalist scientific advisors are given a broad mandate to opportunistically identify projects and program strategies that would be likely to accomplish the objectives. Currently, we’re very excited by the giving opportunities that the science team is finding under this model, and it’s unclear whether it would have been better to use our standard model and hire specialist staff in just a couple of program areas. If we repeatedly find outstanding work to fund in some of these areas, we’ll consider making them permanent focus areas and hiring dedicated program staff in those areas.
A spreadsheet summarizing our list of priorities and cause-specific progress so far (listed in alphabetical order) is here.
- 1. Note that we have funded some basic research that is not related to neglected goals (example), and we plan to fund more such basic science in the future.
- 2. Our scientific advisors prefer not to publish the rough internal reports produced without doing a significant amount of work to clarify and refine them, and Open Philanthropy decided it would not be an optimal use of time for them to do so at this time.
- 3. Given our rough cost-effectiveness calculation, this range would correspond to an assumption that the grant accelerates Target Malaria’s timeline by 2-10 expected months in worlds where they succeed at their long-term objective.
- 4. No public notes from the latter set of conversations are available, though we may summarize our process and conclusions in the future.
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