[Added August 27, 2014: GiveWell Labs is now known as the Open Philanthropy Project.]
As noted previously, I’ve been exploring the question, “What are the best opportunities for funders aiming to contribute to progress in life sciences (i.e., biology and medicine)?” This post lays out what we’ve done to date and how we plan to move forward.
The most helpful person in this endeavor has been Dario Amodei. Dario is currently a postdoctoral research fellow at Stanford Medical School studying proteomics; he is a recipient of the Hertz Fellowship and winner of the Hertz Foundation’s 2012 Thesis prize for his Ph.D. dissertation in the field of neuroscience. He is also a longtime GiveWell fan and supporter (see his 2009 guest post on the GiveWell blog), and the two of us have been housemates since GiveWell relocated to San Francisco.
For the early stages of investigation, Dario has served as our informal scientific advisor,* guiding our investigation by recommending readings, offering connections, etc. I feel that he has been a good fit for this role because he combines experience as a scientist with an extremely strong understanding of GiveWell’s values and goals, and is highly accessible to us. We’ve come to believe that in the early stages of an investigation, when we often don’t know which questions to ask, the ability to have extended, repeated, friendly, low-stakes interactions to get “grounded in the basics” is crucial, and we’ve taken a similar approach to exploring policy advocacy (which we wrote about previously).
Under Dario’s guidance, I have:
- Conducted a series of interviews with representatives of major life sciences funders including Howard Hughes Medical Institute (the largest private philanthropic funder of scientific research in the U.S.), Wellcome Trust (the largest private philanthropic funder of life sciences in the U.K., with similar scale to Howard Hughes and to the British government’s research funding), and the American Cancer Society. (We have also had several other off-the-record conversations, including with U.S. government staff.)
- Studied a small amount of the basics of cell biology. Specifically, I read chapters 1, 5, 6, 7, 8, 18 and 20 from Essential Cell Biology; reviewed the more detailed version of chapter 7; and questioned Dario about them at length. The two of us also discussed the abstracts of several NIH grant proposals and Nature papers. The goal here was simply to improve my basic comprehension of common terms used in discussing life sciences; after the calls discussed above, he and I agreed that it was important for me to improve on this front.
- Taken opportunities to attend larger meetings of scientists in appropriate settings: relatively low-stakes settings in which communication in layperson’s terms was encouraged. I attended a meeting at the Banbury Center, intended to bring together people with different areas of expertise to discuss possible approaches to oncology; a meeting organized by Good Ventures (with Dario’s help) to discuss potential prizes in science; and several meetings of Vannevar Group. All of these meetings were organized by Dario or people in his network.
However, the interviews we’ve done so far have led us to believe that this is far from the only – and may not be the best – framework for thinking about “what sorts of science are underfunded.” Much scientific research – including many of the discoveries that have been associated with the Nobel Prize – is not clearly associated with a particular disease or condition at all. Conversely, it’s possible that funding officially directed toward a particular disease or condition is instead used for work with more general ambitions. Thinking about “which disease and condition should be targeted” is a natural framework for humanitarian-oriented non-scientists, but it isn’t necessarily the most natural way of dividing up different types of science from a scientist’s perspective.
The interviews we’ve done so far have included several criticisms of the primary existing science funding mechanisms, particularly those of the National Institutes of Health (NIH). The NIH provides over half of all U.S. funding in life sciences, and about half of all NIH funding is via a particular grant mechanism, called the R01. The R01, and the NIH more broadly, is perceived as a major factor in researchers’ incentives, and observations about “what the science world needs more of” seem closely connected with critiques of the NIH and the R01. I refer to the NIH, and particularly the R01, as “the existing” system in the bullet points below, listing some of the claims discussed in our interviews:
- The existing system favors researchers with strong track records, and is not good at supporting young investigators. This was the most commonly raised concern, and is mentioned in all three of our public interviews.
- The existing system favors a particular brand of research – generally incremental testing of particular hypotheses – and is less suited to supporting research that doesn’t fit into this mold. Research that doesn’t fit into this mold may include:
- Very high-risk research representing a small chance of a big breakthrough.
- Research that focuses on developing improved tools and techniques (for example, better microscopy or better genome sequencing), rather than on directly investigating particular hypotheses.
- “Translational research” aiming to improve the transition between basic scientific discoveries and clinical applications, and not focused on traditionally “academic” topics (for example, research focusing on predicting drug toxicity).
- The existing system focuses on time-consuming, paperwork-heavy grant applications for individual investigators; more attention to differently structured grants and grant applications would be welcome. These could include mechanisms focused on providing small amounts of funding, along with feedback on ideas, quickly and with minimal paperwork, as well as mechanisms focused on supporting larger-scale projects that require collaboration between multiple investigators.
We don’t yet endorse any of these claims, and we’re aware that in many cases the NIH has mechanisms that intend to address alleged shortcomings. In order to assess these claims, we feel that we would need staff and/or advisors with substantial technical knowledge, as discussed in the next section.
- Generalist GiveWell staff (everyone we currently employ should be thought of as a generalist) gather information on many different causes, through methods including interviewing those with relevant expertise, and seek to understand different causes’ importance, tractability, and “crowdedness” at a high level.
- For particularly promising causes, GiveWell will consider hiring staff to specialize in these causes (or recommending that major philanthropists hire staff for this purpose), since we believe that having the appropriate amount of context to evaluate giving opportunities in a cause may take in excess of a year (even with good access to relevant experts).
- Generalist staff will be responsible for evaluating cause-specific staff; cause-specific staff will be responsible for synthesizing expert opinion and other information to make giving recommendations. However, when investigating scientific research, we believe that another link in the chain is needed. We believe that we need generalist scientific advisors in order to evaluate and compare different approaches to scientific funding at a high level. This is because, based on the early investigation detailed above, I don’t feel positioned even to understand the meaning – much less the plausibility – of many key claims. For example, in order to evaluate the claim that “high-risk” research is under-invested in, I’d want to be able to distinguish high-risk from lower-risk research and be able to assess how much is invested in each – something that I believe is likely to require substantial technically informed judgment calls. To some degree, this dynamic holds for any cause. In any field, there will be people whose greater experience makes subtle contributions to how they see many debates and evaluate many interventions. But scientific research is distinguished from other fields I’ve investigated by the degree to which expertise (often in the form of understanding a very specific, near-universal knowledge base that requires extended study to absorb) is a prerequisite to understanding the basics of what people are claiming and how one might reasonably go about comparing and drilling down on claims. Therefore, we chose to pause further investigation of scientific research until we recruit an appropriate set of generalist scientific advisors. (We have very recently – as of this week – formed a few new advisory relationships and restarted research.)
GiveWell’s ultimate goal is to accomplish humanitarian good, but it believes that some of the most beneficial scientific breakthroughs will come via long-term, high-risk fundamental research and is highly open to promoting work in this category.
GiveWell is not limited to any particular field, disease, biological condition, or population. We seek to broadly consider and identify the approaches that are most (a) promising and (b) under-invested in by other funders. We are likely to focus initially on life sciences (though this will include other areas with applications to life sciences, e.g., novel measurement platforms), but intend to explore other areas as well. We are seeking both advisors with backgrounds in life sciences and/or physical sciences who think strategically about future implications of fundamental research, with an eye to long-term, transformative impact.
GiveWell seeks scientists who are deeply experienced and (depending on career stage) accomplished, and who are committed to identifying the most promising science, regardless of how unconventional it may be. GiveWell hopes to find opportunities that are potentially transformative, and appear after substantial scrutiny (by world-class scientists) to represent intelligent (if sometimes risky) philanthropic investments.
- Interviewing other funders’ staff and scientific advisors to evaluate different approaches to research funding.
- Finding, interviewing, and evaluating scientists doing particularly promising work.
- Assessing (via literature review, interviews, etc.) the tractability of particular scientific goals and the likely future progress of particular fields
- Seeking out, and presenting arguments regarding, inefficiencies in the current infrastructure for funding scientific research
GiveWell expects advisors to serve on a part-time basis, with significant variability in time commitment from week to week. In our early stages, we will likely seek to work with advisors on a trial basis, without long-term commitments. GiveWell’s staff will provide support (scheduling, documentation, etc.) as appropriate.
- Strong scientific accomplishments for one’s career stage.
- Technical intelligence, as assessed by both track record and by interviews (with scientists we retain for interviewing).
- Breadth of interests and abilities. Generalist scientific advisors should be interested in – and good at – comparatively assessing science and scientists in a broad variety of fields.
- Willingness and ability to think critically and strategically but unconventionally, in order to find the ways in which existing funding infrastructure for science falls short of its potential.
- Deep and broad network of high-quality scientific colleagues with whom the advisor may consult for specific technical expertise as needed to assess opportunities.
- Willingness and ability to communicate one’s views to non-technical people, and technical experts outside one’s own scientific field.
- Interest in assessing the potential connection between scientific progress and humanitarian progress, both over the short and long run.
This is an opportunity to influence the scientific priorities of a potentially major source of funds whose focus is on humanitarian good accomplished, without pre-commitments to particular fields, diseases, conditions, or populations. We are seeking people who are excited by the opportunity to have this influence, passionate about finding opportunities for scientific funders to accomplish good, and accordingly prepared to accept compensation that is reasonable but below what they could earn consulting for for-profit organizations.
* We’ve recently started paying Dario for work that is focused on GiveWell’s priorities. These expenses have fallen under the heading of “independent research contractors,” which are covered by a specially earmarked grant from Good Ventures.
“The existing system favors researchers with strong track records, and is not good at supporting young investigators”.
I’ve considered this problem. One solution is to direct the funding equally to all the assistant professors in designated departments at a favored university. They have already met a standard of highly competitive selection.
I liked this one
He argues that the existing system doesn’t effectively track negative results. A third party mechanism that tracks the current research of all scientists and the studies they are currently pursuing would make it easier to find out what fraction of their results are valid.
I did life science research for many years and was repeatedly surprised that the culture of academic researchers is based on the motivation of curiosity for how biology works, rather than the motivation to cure disease. For example, one of my closest friends studies a cow parasite. I asked if her goal was to create a vaccine. She said no, she just wants to understand the basics of how the parasite works and she leaves creating a vaccine to others. She said there was one scientist she knew of who did want to create a vaccine for this cow parasite, but he found that all the academic research that had been done was not pertinent to that task. Nonscientists would just assume that because she was studying a disease, her work must be helping find a cure. But the scientist has to actually have his/her primary motivation be the cure for him/her to direct her research in that direction. Similarly, I worked with some of the most highly regarded researchers in the field of learning and memory. Yet their research is driven by the motivation to understand how it works, not on how to treat learning disorders. With their knowledge, they could easily create animal models of learning disorders, and study what’s going wrong and how to fix it, but they aren’t motivated to do that. In another example, I worked in a couple of labs that studied circadian rhythms. Surprisingly, there was no interest there in coming up with treatments for the sleep disorders that are caused circadian rhythm abnormalities. In the early 90s, I worked in a lab that was studying the human cold virus. My boss said he had chosen to study cold virus instead of HIV because “we already know everything interesting about HIV”. And I said “Except how to cure it!” Yet another example, I worked with someone who studied anhedonia, one of the core symptoms of depression. She was so self-conscious about the reaction from fellow scientists that many of her papers did not mention that her findings were even related to depression. But that meant,of course, that her research publications would not even be found in literature searches done with the keyword of ‘depression’ for anyone but basic scientists who know the lingo to find.
When you talk to biological researchers, they claim that curing disease is their motivation, but they have learned to say this to get grant funding. When you work with them for a while, it becomes clear that their true motivation is curiosity. They leave the curing to unnamed other scientists. In this scientific culture, there is more status to having basic science interests and its kind of considered lower status to be interested in applied science. So it seems like the most brilliant minds do the basic science, and the mediocre scientists to the applied science. If you confront one of these brilliant minds who have been rewarded in the system as it is now, like probably Dario, with this criticism, they strenuously deny it. They say you can’t cure disease until you understand the basic science of it. The trouble is, when you put the curiosity first and the cure second, you do tons of detailed basic research that NEVER becomes relevant to curing disease – like my friend’s research on the cow parasite. If instead she were driven by the desire to produce a cure, she could have seen immediately, as her colleage did, what type of research was needed and what wasn’t. Dario will probably tell you that you have to support basic science because every once in a while there are breakthroughs, like discovering restriction enzymes that enabled us to move pieces of DNA around, that help the applied researchers to cure disease. Well, not if all the public life science money is going to the basic researchers and there’s none left for the applied researchers!
So for those reasons, I would suggest that to find out how to get money into the hands of life scientists who can best make a difference in health, consult people who have diseases, consult scientists who have loved ones dying from the disease they’re studying, and consult scientist who themselves have made a direct impact on health. Ask them how they think life science charitable donations could make the biggest impact on health. No offense to Dario, but without realizing it, he will mislead you with advice whose unconscious motivation is to benefit scientists like him, not public health. Its natural for young ambitious people – I was of a similar mind when I was young. It was only after I developed a health condition myself that I realized that the simplest research that could have helped me address it had never been done, that research that was relevant hadn’t made it out of obscurity in pubmed and into physicians knowledge base. Only then that I got mad that the system had rewarded me (runner up for breakthrough of the year, science magazine, for my graduate work) for doing tons of work that was completely irrelevant to actually helping people, when other work that could help was lying undone.
Karen, thanks for the thoughts. We are trying to look seriously into both sides of the debate, evaluating the arguments that fundamental breakthroughs are most important to aim for and the arguments that ‘translational’ work (aiming directly at clinical applications) is paramount.
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