Givewell’s Holden Karnofsky, who has previously posted his thoughts on Givewell supporting SI/MIRI recently discussed the potential for Givewell to begin evaluating biomedical charities, in Givewell’s Yahoo Group. Someone suggested (as I have through less direct means) that they take a hard look at SENS Research Foundation, and then Aubrey de Grey appeared and began an interesting discussion with Holden.
The thread begins with Holden’s long initial post about Givewell’s stance on investigating and recommending biomedical charities, which is definitely worth the read for greater insight. The rest of the conversation is aggregated below for anyone else who can’t stomach Yahoo Groups’ interface.
Overall, Holden seems to agree with the goal of SENS, and interested in the details, but the conversation seems to have ended in October 2012 with Holden stating that he was waiting for Dario Amodei’s thoughts on SENS.
First, I think that this is an excellent document. I checked for a
number of things that I had heard about (Breakout Labs, John
Ioannidis, Cochrane Collaboration) and they're all there in your
The one thing that's not explicitly mentioned: longevity and life
extension research. At least prima facie, this seems like something
that should be more important than individual disease research, and it
seems like a classic "Valley of Death" case (pun unintended, but
noted) -- T1 stage to use your terminology. I think the SENS website
http://www.sens.org would be a good starting point for one of the (to
me promising) approaches to life extension. I recall from past
conversations that you were aware of SENS, so this is not new to you,
but I think that longevity should be included as part of any
discussion of biomedical research and given separate consideration
given that it has a much lower status than research into specific
conditions such as cancer, dementia, etc. You may ultimately conclude
that not enough can be done in this area, but I think it should be
part of your preliminary stuff. [btw, the United States has a National
Institute of Aging, but it's much lower-status than most of the other
grantmakers mentioned here].
Thanks for the thoughts. I had a followup conversation with Dario about this topic a few days ago. I think the question of "could one fund translational research to treat/prevent aging?" provides an interesting illustration of some of the tricky dynamics here for a funder:
- It's possible that if there were a great deal more attention giving to treating/preventing aging, we would have some promising treatments. So in a broad sense it's possible that aging is underinvested in.
- A lot of the best basic biology research isn't clearly pointing toward one treatment/condition or another; it's about understanding the fundamentals of how organisms operate. So having an interest in treating aging, as opposed to cancer, might not have a major impact on which projects one funds, if one's main goal is to fund outstanding basic biology research.
- Perhaps because of the lack of emphasis on treating aging (or perhaps because it's simply too difficult of a problem), there don't seem to be promising findings in the "Valley of Death" relevant to aging; the few promising leads have been explored.
- So even if, in a broad sense, there is too little attention given to this problem, knowing this doesn't necessarily yield a clear direction for a relatively small-scale funder of biomedical research.
My attention was brought to this thread, by virtue of the fact that it was my work that gave rise to SENS Foundation, and I'm looking forward to getting more involved here; I've held the Effective Altruism movement in high regard for some time. However, given my newbie status here I want to start by apologising in advance for any oversight of previously-discussed issues etc. I'm naturally delighted both at Holden's post and at Vipul's reply (which I should stress that I did not plant! - I do not know Vipul at all, though I look forward to changing that). I would like to mention just a few key points for discussion:
- Holden, I want to compliment you on your appreciation of how academia really works. Everything you say about that is spot on. The aversion to "high risk high gain" work that has arisen and become so endemic in the system is the most important point here, in terms of why parallel funding routes are needed.
- I'm slightly confused that a lot of Holden's remarks are focused on the private sector (i.e. startups), since my understanding was that GiveWell is about philanthropy; but I realise that there is not all that clear a boundary between the two (and I note the mention of Breakout Labs, with which I have close links and which sits astride that divide more than arguably anyone). The "valley of death" in pre-competitive translational research is a rather different one than that encountered by startups, but the principle is the same, and research to postpone aging certainly encounteres it.
- Something that I presume factors highly among GiveWell's criteria is the extent to which a cause may be undervalued by the bulk of major philanthropists, such that an infusion of additional funds would make more of a difference than in an area that is already being well funded. To me this seems to mirror the logic of focusing on the shortcomings (gaps) in NIH's funding (and that of traditional-model foundations). Holden notes that "Anyone we consider for funding ought to be able to explain why they're better at allocating the funds than the NIH" and I agree wholeheartedly, but my inference is that he thinks that some orgs may indeed be able to explain that. I certainly think that SENS Foundation can.
- Coming to aging: research to postpone aging has the unique problem of quite indescribeable irrationality on the part of most of the general public, policy-makers and even biologists with regard to its desirability. Biogerontologists have been talking to brick walls for decades in their effort to get the rest of the world to appreciate that aging is what causes age-related ill-health, and thus that treatments for aging are merely preventative geriatrics. The concept persists, despite biogerontologists' best efforts, that aging is "natural" and should be left alone, whereas the diseases that it brings about are awful and should be fought. This is made even more bizarre by the fact that the status of age-related diseases as aspects of the later stages of aging absolutely, unequivocally implies that efforts to attack those diseases directly are doomed to fail. As such, this is a (unique? certainly very rare) case where a philanthropic contribution can make a particularly big difference simply because most philanthropists don't see the case for it. It underpins why having an interest in treating aging, as opposed to cancer, absolutely has a major impact on which projects one funds. It's also a case for (if I understand the term correctly) meta-research.
- A lot of the chatter about treating aging revolves around longevity, but it shouldn't. I'm all in favour of longevity, don't get me wrong, but it's not what gets me up in the morning: what does is health. I want people to be truly youthful, however long ago they were born: simple as that. The benefits of longevity per se to humanity may also be substantial, in the form of greater wisdom etc, but that would necessarily come about only very gradually (we won't have any 1000-year-old for at least 900 years whatever happens!), so it doesn't figure strongly in my calculations.
- When forced to acknowledge that the idea of aging being a high-priority target for medicine is an inescapeable consequence of things they already believe (notably that health is good and ageism is bad), many people retreat to the standpoint that it's never going to be possible so it's OK to be irrational about whether it's desirable. The feasibility of postponing age-related ill-health by X years with medicine available Y years from now is, of course, a matter of speculation on which experts disagree, just as with any other pioneering technology. I know that Holden and others have expressed caution (at best) concerning the accuracy of any kind of calculation of probabilities of particular outcomes in the distant (or even not-so-distant) future, and I share that view. However, an approach that may appeal more is to estimate how much humanitarian benefit a given amount of progress would deliver, and then to ask how unlikely that scenario needs to be to make it not worth pursuing. My claim is that the benefits of hastening the defeat of aging by even a few years (which is the minimum that I claim SENS Foundation is in a position to do, given adequate funding) would be so astronomical that the required chance of success to make such an effort worthwhile would be tiny - too tiny for it to be reasonable to argue that such funding would be inadvisable. But of course that is precisely what I would want GiveWell to opine on.
- In the event that GiveWell (or anyone else) were to decide and declare that the defeat of aging is indeed a cause that philanthropists should support, there then arises the question of which organisation(s) should be supported in the best interests of that mission. We at SENS Foundation have worked diligently to rise as quickly as possible in the legitimacy stakes by all standard measures, but we are still young and there remains more to do. If I were to offer an argument to fund us rather than any other entity, it would largely come down to the fact that no other organisation has even a serious plan for defeating aging, let alone a track record of implementing such a plan's early stages.
- A significant chunk of what we do is of a kind that I think comes under "meta-research". A prominent example is a project we're funding at Denver University to extend the well-respected forecasting system "International Futures" so that it can analyse scenarios incorporating dramatically postponed aging.
I greatly welcome any feedback.
Thanks for the thoughts.
The NIH appears to have a division focused on research relevant to this topic: http://www.nia.nih.gov/research/dab . Its budget appears to be ~$175 million (per year). The National Institute on Aging, which houses this division, has a budget of about $1 billion per year, including a separate ~$400 million for neuroscience (which may also be relevant) as well as $115 million for intramural research. Figures are from http://www.nia.nih.gov/about/budget/2012/fiscal-year-2013-budget. The Institute states that its mandate includes translational research (http://www.nia.nih.gov/research/faq/does-nia-support-translational-research). How would you distinguish your work from this work?
(For the moment I'm putting aside the question I raised in my previous response to Vipul on this topic, regarding whether it's best to approach biology funding from the perspective of "trying to treat/cure a particular condition" or "trying to understand fundamental questions in biology whose applications are difficult to predict.")
Hi Holden - many thanks.
First: yes, there are really three somewhat separate questions for someone trying to evaluate whether to support SENS Foundation:
1) Is the medical control of aging a hugely valuable mission?
2) Assuming "yes" to (1), is it best achieved by basic research or translational research?
3) Assuming translational, is SENS Foundation the organisation that uses money most effectively in pursuit of that mission?
I had rather expected that you would take some convincing on item (1), and much of what I wrote last time was focused on that. Since it isn't the focus of your question to me, I'm now going to assume until further notice that there is no dissent on that.
So, to answer your question: actually you're not putting aside the basic-vs-translational question as much as you may think you are. The word "translational" is flavour of the month in government funding circles these days (not only in the USA), so it's not surprising that the NIA has a public statement of the kind you pointed to. However, notice that the link they give "for more information" is to a page listing ALL "Funding Opportunity Announcements". There is no page specifically for translational ones, and the reason there isn't is that the amount of work that the NIA actually funds that could really be called translational is tiny. In other words, the page you found is actually just blatant spin. The neuroscience slice you mention is an anomaly arising from the way NIA was founded (the natural place for that money is clearly NINDS): the fact that it's NIA money does not, in practice, translate into its being spent on work to prevent neurodegeneration by treating its cause (aging). Instead, just like NINDS money, it's spent on attacking neurodegeneration directly, as if such diseases could be eliminated from the body just like an infection: the same old mistake that afflicts, and dooms, the whole of geriatric medicine.
So, the first answer to your question is that SENS Foundation really DOES focus on translational research, with an explicit goal of postponing age-related ill-health. But there's also another big difference: we can attack this problem relatively free of the other priorities that afflict mainstream funding (whether from NIH or from trasitional foundations). Most importantly, though we do and will continue to publish our interim results in the peer-reviewed literature, we are much less constrained by "publish or perish" tyranny than typical academics are. This allows us to proceed by constructing and implementing a rational "project plan" (namely SENS) to get to the intended goal (the defeat of aging), whereas what little translational work is funded by NIA or others is guided overwhelmingly by the imperative to get some kind of positive result as quickly as possible, even when it's understood that those results are not remotely likely to "scale", i.e. to translate into eventual medical treatments that significantly delay aging. A great example of this is the NIA's Interventions Testing Program (ITP) to test the mouse longevity effects of various small molecules. The ITP only exists at all (and in a far smaller form than originally intended) as a result of several years of persistence by the then head of the NIA's biology division (Huber Warner), and it focuses entirely on delivery of simple drugs starting rather early in life, with the result that no information emerges that's relevant to treating people who are already in middle age or older. (This is despite the fact that by far the most high-profile result that the ITP has delivered so far, the benefits of rapamycin, actually WAS a late-onset study: it wasn't meant to be, but technical issues delayed the experiment.) In a nutshell, there is a huge bias against high-risk high-gain work.
The third thing that distinguishes SENS Foundation's approach is that we can transcend the "balkanisation" (silo mentality) that dominates mainstream academic funding. When one submits a grant application to NIA, it is evaluated by gerontologists, just as when one submits to NCI it is evaluated by oncologists, etc. What's wrong with this is that it biases the system immensely against cross-disciplinary proposals. SENS is a plan that brings together a large body of knowledge from gerontology but also a huge amount of expertise that was developed for other reasons entirely - to treat acute disease/injury, or in some cases for purposes that were not biomedical at all (notably environmental decontamination). It doesn't matter how robust the objective scientific and technological argument is for work of that sort: it will never compete (especially in today's very tight funding environment) with more single-topic proposals all of whose details can be understood by reviewers from a particular single field.
The final thing to mention, and this actually also answers your question to Vipul about basic versus translational research, is that SENS is a plan that has stood the test of time. I've been propounding it since 2000, well before SENS Foundation existed, and it used to come in for a lot of criticism (initially more in the form of off-the-record ridicule, and latterly, at my behest, in print), but in every single case that criticism was found to stem from ignorance on the part of the detractor, either of what I proposed or of published experimental work on which the proposal was based. That's why I'm now regularly asked to organise entire sessions at mainstream gerontology conferences, whereas as little as five years ago I would never even be invited to speak. It's also why the Research Advisory Board of SENS Foundation consists of such prestigious scientists. This is a very strong argument, in my view, for believing that now is the time to sink a proper amount of money into translational gerontology (though certainly not to cease doin basic biogerontology too). It's well known that basic scientists are often not the most far-sighted when it comes to seeing how to apply their discoveries (attitudes in 1900 to the feasibility of powered flight being the canonical example). It is therefore a source of concern that almost all the experts who have the ear of funders in this field are basic scientists, whose instinct is to carry on finding things out and to deprioritise the tedious business of applying that knowledge. SENS has achieved a gratisfying level of legitimacy in gerontology, but it is still foreign to most card-carrying gerontologists, and as such it remains essentially unfundable via mainstream mechanisms. Hence the need to create a philanthropy-driven entity, SENS Foundation, to get this work done.
Let me know if this helps, or if you have further questions.
Thanks again for engaging so thoughtfully.
I agree that a new technology/treatment that could delay or reverse aging (or aspects of it) would be enormously valuable. Regarding the rest of your argument, this is a good example of the challenges I've been discussing in understanding biomedical research.
You state that you have a high-expected-value plan that the academic world can't recognize the value of because of shortcomings such as "balkanisation" and risk aversion. I believe it may be true that the academic world has such problems to a degree; however, I also believe that there are a lot of extremely talented people in academia and that they often (though not necessarily always) find ways to move forward on promising work. Without more subject-matter expertise (or the advice of someone with such expertise), I can't easily assess the technical merits of your argument or potential counterarguments. Hopefully we'll have a better system for doing so at some point in the future.
I'll be very interested to see Dario's thoughts on the matter if he responds. I'd cite Dario as an example of an academic who ultimately wants to do work of the greatest humanitarian value possible, regardless of whether it is prestigious work. And as my summary of our conversation shows, he acknowledges that the world of biomedical research may have certain suboptimal incentives, but didn't seem to think that these issues are leaving specific, visible outstanding research programs on the table the way that your email implies.
Excellent. I too am keen to see Dario's comments. Dario also has the advantage of being based just a few miles from SENS Foundation's research centre, so we can definitely get together f2f soon if he wants.