We’re hoping to set the Open Philanthropy Project’s initial priorities within scientific research this year. That means being in a place roughly comparable to where we currently are on U.S. policy and global catastrophic risks: having a ranked list of focus areas and goals for hiring and grantmaking.

The process is going to have to look very different. For both U.S. policy and global catastrophic risks, we were able to do a relatively large number of “shallow investigations,” in which we quickly got a sense for the importance, tractability, and crowdedness of a cause. By contrast, it seems to us that investigating even a single cause within scientific research – to the level of understanding we achieved with shallow investigations in other areas – is a major project.

Our neglected goal investigations have been proceeding slowly. We’ve been working with scientific advisors who have limited time available, and it’s taken them significant effort to (a) get up to speed on a given area of research (e.g., R&D targeting tuberculosis control); (b) have initial conversations about the most promising paths within the area; (c) begin thinking about how to assess which of these directions seem most promising. One of our major bottlenecks is scientific advisory capacity, and that’s something we hope to change. But even if we did, we wouldn’t anticipate being able to do a large number of shallow investigations of science causes. Meanwhile, investigating other possible approaches to science – such as breakthrough fundamental science or translational science – seems likely to be even more challenging than investigating neglected goals.

Our working plan for the moment aims to set priorities mostly via very high-level, comparative investigations. Our specific goals are as follows:

1. Create a prioritized list of neglected goals via conversations with unusually broad scientists as well as people in the effective altruist community. I have a draft list currently, based on suggestions I’ve picked up over the years. After getting input from 10-15 people – with a mix of junior and senior, science-focused and effective-altruism-focused – I expect to have a reasonable (though far from complete) sense for what is most worth prioritizing. As an aside, I wouldn’t expect this approach to work very well for U.S. policy, where it’s hard to find people who have a good sense both for politics and for our values. But for identifying neglected goals, I believe I can identify people who combine these qualities.

This investigation will not be specific to life sciences. I hope to speak with people who have broad interests and expertise and can identify potential technologies that would be worth more effort to develop than is currently being put in.

We will do as many cause-specific investigations as we can, prioritizing those that rank at the top of our list, in order to further inform our priorities.

For highly prioritized neglected goals, we may (after this year) move toward forming grant advisory committees and providing direct funding of relevant research, or we may think about other ways to raise the profile of the goals in question. My impression is that providing funding for a thin field can create something of a self-reinforcing dynamic, since research often raises new interesting questions and makes it easier and more desirable for other researchers to work on similar issues; I hope to investigate this impression further (more below).

2. Get a sense for potential systemic issues in fields other than life sciences. While “neglected goals” refers to cases where there isn’t enough investment in a particular social problem, “systemic issues” refers to cases where the system for supporting scientific research seems to be falling short on its own terms. I’ve written at length about two potential examples in life sciences: Translational science and the valley of death, Breakthrough fundamental science. (Some other systemic issues are discussed in Science policy and infrastructure as well as previous posts on reproducibility-related issues and open science.)

If we decided to prioritize addressing systemic issues in a particular field, we’re not sure exactly how we’d do it. We might focus on supporting work that directly proposes, and advocates for, improvements to the system rather than on directly funding research that is undervalued due to systemic issues. But both would be strong possibilities.

My understanding of systemic issues in life sciences is high-level and quite limited, but it is sufficient to have a basic sense for the size and shape of potential improvements, and I feel that I hit diminishing returns on understanding these issues after a relatively contained number of conversations. In addition, I felt that the opinions of junior scientists I spoke to early in the process were fairly predictive of what I heard from more prominent scientists later in the process.

We’ve set a goal of coming to a similar level of understanding of systemic issues in fields other than life sciences. Doing so will be a highly informal process, following referrals from contacts I believe understand both science and our values well.

3. Build scientific advisory capacity. We’ve found strong scientific advisors, but their time availability is limited. We’re hoping to find people who can work for us on closer to a full-time basis (ideally full-time). In the short run, such people would help us investigate potential neglected goals. In the long run, they might help us build further capacity after we set our priorities – finding the appropriate hires, constructing the relevant advisory boards, and otherwise finding the best contacts for executing on the science-related objectives we choose.

At this time, we believe our ideal candidate would: (a) have a strong background in life sciences or another scientific area of interest; (b) be available for full-time work; (c) be a generalist, willing and able to put significant effort into networking and recruiting as well as investigation. We are currently informally seeking such people, and may soon develop a job posting and a more formal process.

4. Other projects. We hope to complete a few other cross-cutting projects this year:

• Investigating the question of “differential technological development”: the question of whether it’s desirable to develop some scientific and technological innovations sooner than others, in light of the fact that many of the most dangerous global catastrophic risks seem to hinge on the develop of new technologies (and may be mitigated by the development of other technologies).
• Compiling a rough list of major historical breakthroughs in life sciences. We would then investigate the origins of some such breakthroughs, trying to get more basic context on the roles of different kinds of research – and different kinds of funding – in past breakthroughs.
• Investigating historical cases where a funder took up a “neglected goal” that was getting little attention, and tried to bring it more attention from scientists. This would inform our likely paths forward on top-priority neglected goals.

We’ve tried to approach scientific research funding – focusing initially on life sciences – by looking for gaps and deficiencies in the current system for supporting scientific research. We’ve identified several possibilities, including a set of systematic issues that make it difficult to support attempts at breakthrough fundamental science.

One way to respond to a gap in the system would be to fill it ourselves: support the kind of science that has trouble getting support from existing funding agencies, universities, etc. We believe this is the approach taken by organizations such as Howard Hughes Medical Institute. But another way to respond would be to try to improve the system directly, by funding the development of – and advocacy for – proposals for structural changes. Structural changes could include changes in how government agencies allocate funding, in how universities determine professorships, or in other practices that we believe are important in influencing what scientists are able to do. (We broadly refer to universities, journals, and other institutions that play an important role in scientists’ incentives and support as “infrastructure.”)

We find the latter idea intriguing. It appears to us that the strongest scientific funders have little interest in policy analysis and advocacy, while the strongest funders of policy analysis and advocacy tend not to take interest in the scientific research issues discussed in this post. We’re interested in the idea of combining – in a dedicated organization – great scientists and great policy analysts, in order to put in the substantial amount of work needed to develop and promote the best possible proposals for improving science policy and infrastructure. It would be a high-risk, potentially very high-return project to attempt. We aren’t aware of any attempts to do something along these lines at the moment, and we think it could be a risk worth taking.

The rest of this post outlines:

• Examples of science policy and infrastructure issues we’d like to see more work on. More
• A brief sketch of how an organization dedicated to these issues might operate. More
• What we know about existing attempts to improve science policy and infrastructure, and why we believe a new organization (or a dedicated team within an existing organization) could be a significant addition. More
• Why we believe that supporting such an organization would be worthwhile. More

We previously wrote about claims that the current life sciences system has trouble supporting attempts at breakthrough fundamental science, and we featured a PNAS paper on the subject. This paper gives multiple concrete suggestions for how changes in U.S. policy might reduce competitiveness between scientists, improving prospects for early-career scientists, and supporting higher-risk, higher-reward research:

• Making the government budget for scientific funding more “predictable and stable,” in order to facilitate long-term planning and avoid the sorts of supply-demand imbalances described previously.
• Making changes in what sorts of grants can be used for what sorts of expenses (in particular, putting restrictions on the ability to support graduate students and postdocs using research grant funds), in order to allow more deliberate control of the number of graduate students and postdocs who will end up competing for professorships.
• Aiming to broaden the possible career paths for young scientists, including increasing the use of “staff scientists” rather than trainees to support lab research. These changes could further diminish the intensity of competition for professorships as well as improving the overall productivity of labs.
• Increasing the size of grant programs such as the NIH Director’s New Innovator award, which may be more conducive to supporting attempts at breakthrough fundamental science.
• Improving the quality of grant application evaluation by revising criteria and scoring methodologies, and making more effort to include top scientists in evaluation.

These ideas are, by and large, fairly concrete and (to my eyes) practical-seeming suggestions for policy change. I haven’t been able to find information on the extent to which they are being implemented or actively discussed (other than that the number of Pioneer Award recipients seems to have shrunk rather than grown from last year to this year). To my knowledge, none have been substantially implemented.

In addition to these sorts of ideas, I think the following could also be highly worthwhile:

Thinking through how universities could experiment with new models for determining professorships, as well as how journals could experiment with new processes for highlighting noteworthy science. Both processes are extremely important factors in what kind of work is supported and incentivized in academia. Universities and journals tend to follow certain common cultural norms today, but given the degree of apparent agreement about room for improvement in the current system, it’s plausible to me that a dedicated effort at developing and promoting new approaches could spur experimentation and change.

Examining existing regulations – regulations on research, regulations regarding sharing of data, etc. – from the perspective of optimizing the ability to gain new knowledge and reap the benefits of innovation. Both the paper linked above and the paper I previously discussed on declining pharmaceutical productivity have identified increasing regulatory burdens as a major issue. In addition, from my limited readings on the history of biomedical research, it seems to me that getting new medical technologies tested and approved used to be much easier than it is today, and that many key experiments were highly speculative and dangerous. Such experiments would have been much more difficult to carry out with today’s regulation and social norms. Work in this category could include the following (these ideas are fairly speculative and may overlap to some degree with work being done at existing institutions):

• Improving the balance between patients’ privacy and scientists’ ability to access large amounts of data for research purposes.
• Improving the FDA process with an emphasis on increasing scientists’ ability to experiment and innovate, especially if and when new tools for data sharing present new possibilities for demonstrating safety and efficacy of medical technologies.
• Improving the balance between ethical considerations and scientists’ ability to run informative experiments without excessive overhead.
• Bringing a science- and scientist-focused perspective to debates over intellectual property law.
• Regulating data sharing practices in clinical trials with an eye to enabling “reverse translation” research.
• Working on optimal regulation of emerging technologies, in a framework that emphasizes the importance of innovation’s benefits as much as the importance of caution.

It seems to me that there could be a great deal of value in an organization dedicated to bringing together great scientists and great policy analysts, in order to develop and promote the best possible proposals for improving science policy and infrastructure. I would see such work as primarily aiming to have influence on universities, journals, and government agencies via developing well-thought-through ideas and making the case for them on the merits, rather than via exerting political pressure based on grassroots mobilization, media, etc. This strategy of aiming for impact would be comparable to that of organizations such as Center for Global Development and Center on Budget and Policy Priorities. (Note that claims of impact are available for both CGD and CBPP; we have not vetted either list but find both lists quite plausible.)

I think this kind of activity could be quite influential, and that the difference between a dedicated effort to carry it out and the status quo could be substantial. This would be consistent with my understanding of many past cases of nonprofits influencing policy, as well as with my understanding of how both corporate and nonprofit actors often have influence.

I discussed this idea at some length in my conversation with Neal Lane.

My impression is that there are no organizations playing the role described above. The policy issues I’ve laid out have been raised by scientists via op-eds (such as the PNAS paper discussed above) and committee reports (such as a recent piece released by the American Academy of Arts and Sciences), but are not the focus of any dedicated organizations (or teams within organizations).

It’s possible that such an organization or team does exist – I haven’t searched exhaustively – but I have several reasons to believe it does not:

• Most importantly, I have discussed this topic with many people, including those mentioned in our previous post. I have generally asked explicitly whether the kind of organization I’m envisioning already exists, and sought referrals to others who are knowledgeable on the subject. None of the people I’ve asked have been aware of such an organization – so even if one does exist, it seems unlikely that it has achieved much prominence. Neal Lane seemed particularly interested in these issues, and stated that he is not aware of such an organization (see public conversation notes).
• I’ve searched the web for groups focused on science policy. At the moment, my impression is that “science policy” (as commonly used) tends to refer to some combination of (a) promoting a high level of funding for science; (b) working on policy around science education and outreach; (c) working on a wide range of policy issues, such as climate change mitigation, in a way that is informed by science (and/or emphasizes the importance of scientific knowledge and evidence in decision-making). I’ve examined Wikipedia’s category page on science advocacy organizations, and these organizations seem to generally be in one of the aforementioned categories. None of them seem to be focused on the sorts of issues I’ve discussed in this post. Note that Wikipedia’s list excludes Research!America, an organization that focuses on making the case for a high level of government support for science.
• I’ve examined a list of think tanks by category, and none of those listed under “Science and technology” appear to do significant work on the sorts of issues discussed in this post.

Speaking generally from conversations I’ve had with major funders, it appears that the strongest scientific funders have little interest in policy analysis and advocacy, while the strongest funders of policy analysis and advocacy tend not to take interest in the scientific research issues discussed in this post.

In conversations about this idea so far, I’ve encountered a mix of enthusiasm and skepticism. (I’ve also generally heard from science funders that it would be outside of their model, regardless of merits, because of the focus on influencing policy rather than directly supporting research.) Most of the skepticism has been along the lines of, “The current system’s cultural norms and practices are too deeply entrenched; it’s futile to try to change them, and better to support the best research directly.”

This may turn out to be true, but I’m not convinced:

• There is already a great deal of private money attempting to support the best research directly (including ~$700 million per year from Howard Hughes Medical Institute). Directly supporting research is generally expensive, especially in biomedical sciences. The NIH’s research project grants cost an average of ~$500,000 per year. We have previously remarked that policy-oriented philanthropy seems to “cost less” in some broad sense than scientific research funding. As a very rough argument along these lines, if an organization the size of Center for Global Development (~$15 million per year) or Center on Budget and Policy Priorities (~$30 million per year) could make the NIH (~$30 billion per year) 1% more efficient, it seems it would be more than justifying its existence.
• In general, I think it is best to avoid putting too much weight on arguments of the form “It’s futile to try to influence policy X.” We have argued previously against placing excessive weight on seeming political tractability. My general impression is that policy change has often quickly moved from “seemingly futile” to “inevitable”; for examples of this, see our conversation with Frank Baumgartner. I’m particularly inclined to think that change is possible when (a) there is a high degree of agreement on what needs to change; (b) the key institutions are largely technocratic, with strong scope to do what they judge best rather than what a particular constituency supports; (c) there is no existing dedicated effort to optimize and build momentum around specific proposals; (d) there is no clear opposing constituency for many of the possible changes outlined above.

So far, we haven’t been able to find a person or organization who seems both qualified and willing to lead the creation of the sort of organization described in this post. We plan to continue looking for such a person or organization, while continuing to discuss, refine and reflect on these ideas.