Serious Unconventional De Grey

Wednesday’s Washington Post:

Aubrey de Grey may be wrong but, evidence suggests, he’s not nuts. This is a no small assertion. De Grey argues that some people alive today will live in a robust and youthful fashion for 1,000 years. … [he] advocates not myth but "strategies for engineering negligible senescence," or SENS. It means curing aging.  With adequate funding, de Grey thinks scientists may, within a decade, triple the remaining life span of late-middle-age mice. …

By 2005 … De Grey was being pilloried as a full-blown heretic.  "The idea that a research programme organized around the SENS agenda will not only retard ageing, but also reverse it — creating young people from old ones and do so within our lifetime, is so far from plausible that it commands no respect at all within the informed scientific community," wrote 28 biogerontologists in the journal of the European Molecular Biology Organization. 

I enthusiastically support de Grey’s goal of greatly extending life, and his engineering approach would be right, if his project were feasible.  And even a small chance of success could justify the effort he proposes.  I also feel some social pressure to support him, as many of my associates do.  Nevertheless, I feel my that declaring "support" for his project would reasonably be interpreted as my claiming some relevant expertise suggesting his project is feasible enough to have this chance.  Yet I simply cannot claim such expertise.  And given the expert opposition voiced I cannot uncritically accept de Grey’s judgment. 

I take particular exception to this line of reasoning: 

… De Grey’s original academic field is computer science and artificial intelligence. He has become the darling of some Silicon Valley entrepreneurs who think changing the world is all in a day’s work. Peter Thiel, the co-founder and former CEO of PayPal — who sold it in 2002 for $1.5 billion, pocketing $55 million himself — has dropped $3.5 million on de Grey’s Methuselah Foundation.

"I thought he had this rare combination — a serious thinker who had enough courage to break with the crowd," Thiel says. "A lot of people who are not conventional are not serious. But the real breakthroughs in science are made by serious thinkers who are willing to work on research areas that people think are too controversial or too implausible."

[The article ends with a 1903 quote from the New York Times saying flying machines were a million years off.]

We cannot better promote science simply by better funding people who are "not conventional."   As I’ve said before:

Contrary to their self-image, undiscriminating freethinkers are our main obstacle to innovation

I don’t see how it helps if we focus on people who are "not conventional but serious."  Sure it works if "serious" just means "good."  But we should fund "good" people regardless of whether they are conventional.  If "serious" means "unplayful" or "using great effort," I don’t see evidence that unconventional people with these characteristics are much more productive than average unconventional folks.   

What I really want, of course, are betting markets telling the chance de Grey would achieve his goals, given the funding he requests. 

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  • Cynical Masters Student

    Maybe if unconventional thinker can be likened to a high risk (which would fit “out there” I guess) strategy (very high payoff but small chance of success), then maybe it actually DOES make sense to fund a lot of borderline projects with the idea that one may well take off.

    Just think of the way venture capitalists work.

  • Anonymous

    Betting markets would be biased because if de Grey is successful, the “yes” bettors would collect immediately but if he isn’t, the “no” bettors would have to wait until he gives up or loses funding. When you consider that people put a higher value on acquiring money sooner rather than later (partly because of inflation, partly because humans are just irrationally short-sighted) this means the bets would be biased towards “yes”.

  • I think the chance that one of de Grey’s seven SENS interventions works and is helpful, is much higher than the chance that they all work and are together sufficient to halt aging in its tracks. (Sometimes de Grey seems to say that the 7 SENS are all that’s needed, sometimes that it would just buy you an extra couple of decades of life to wait on further interventions.)

    Proving any one of the SENS interventions, even in mice, is easily worth de Grey’s entire budget times 100. My main worry is that de Grey won’t be able to adapt appropriately if, say, the other six SENS interventions turn out to be undoable or dead ends. The chance that at least one intervention fails is very high.

    I’m pretty sure that Thiel doesn’t go around randomly funding unconventional thinkers who make great efforts. There’s plenty of those fish to go around, and Thiel’s hit rate on the unconventional good thinkers is too high.

    With all that said, of course “conventional” thinkers make major breakthroughs. It happens all the time. Sometimes the keys are under the lamppost where everyone’s looking. There’s an argument to be made for the higher marginal utility of looking somewhere different than the crowd, even if it’s not the best search location – I think this was discussed on Overcoming Bias. But I don’t make that particular argument on behalf of my own research. Life is too short to look anywhere you don’t really expect the answer to be found. And in my work there’s too much you have to get right, in sequence, to go around including deliberate errors. The only justification I would accept for thinking outside the box, is if you think the keys really are outside the box.

  • Anon, a good market would bet assets that increase in value with time.

    Eliezer, the article may of course have mis-described Thiel’s reasoning. Hopefully he uses other criteria than mentioned.

  • As I see it, there should be a peculiar bias towards betting “no” on the proposition “de grey will be successful in allowing humans eternal life”.

    If you can reasonably assume that you would be among those humans who would become immortal, then your income stream would become essentially infinite, and whatever loss you took on the “no” bet would become a drop in an infinitely large bucket. Betting “no” is a win whether you lose or win.

    It gets a lot more complicated if the proposition is only that de Grey will extend life, but extended life -> greater income -> a cheaper “no” bet.

  • Thiel’s hit rate on the unconventional good thinkers is too high

    Such as?

  • Linksvayer: Foresight Nanotech Institute, Singularity Institute for AI, Methuselah Foundation, not to mention Paypal (which used to be a lot wilder before eBay bought it out – Luke Nosek gave a demo at a Foresight Gathering where he created an email address for russiandrugdealer@hotmail and sent it $10). Jury’s still out on Facebook. I don’t recall Thiel funding any obvious crackpots, either, so he’s not just funding absurd-sounding ideas at random.

  • But Bill Mill, if you bet no you have to pay off the bet right when immortality comes on the market, and it might be expensive for early adopters.

  • Richard, my bet is that the government immediately takes control of the marketplace in that case anyway 🙂

    In an ideal market, though, the game is to try and bet as near to $(available money – cost of immortality) as possible, without going over. My real point is that the potential self-referentiality of this particular bet adds some very strange incentives to the mix.

  • Indeed.

  • Another interesting question is, if you can reasonably expect *not* to be able to attain immortality when it’s released, what should you do? If the result is “yes”, your relative value immediately drops to zero.

    Should you bet all available money on no, reasoning that, should your value drop to zero, doubling your initial investment is irrelevant compared to the immortals’ infinite income?

    The only people who should even consider voting “yes” are those who believe their available funds to be within the range [cost of immortality/2, cost of immortality).

  • For those unfamiliar with Aubrey’s ideas, a good introduction is this TED conference video, and if you want to learn more, his recent book with Michael Rae, “Ending Aging” is the next logical step.

  • “I enthusiastically support de Grey’s goal of greatly extending life, and his engineering approach would be right, if his project were feasible.”

    Do you know anyone else who has a *better* project? I’m not aware of anyone else who’s even working on the problem, with the stated goal of ending aging. Even if Aubrey’s research is likely to fail, it’s still a lot better than supporting projects which are certain to fail, or not supporting anyone at all.

  • Tom, if there is nothing cost effective we can do, then we should do nothing.

  • “Tom, if there is nothing cost effective we can do, then we should do nothing.”

    Cost effective as compared to what? Even a project with a 99.9% probability of failure would be more cost effective than the things we normally do with our money (in terms of utility/$).

  • Carl Shulman


    “Sure it works if “serious” just means “good.” But we should fund “good” people regardless of whether they are conventional.”
    ‘Serious’ does mean ‘good,’ but funding is limited (particularly for individual philanthropists). If local career incentives and risk-aversion push talented people and funding agencies to overinvest in conventional lines of research, then diminishing marginal returns can make it more cost-effective to fund good unconventional researchers rather than good conventional ones.


    “I’m not aware of anyone else who’s even working on the problem, with the stated goal of ending aging.”
    There are numerous researchers making substantial advances related to aging. There are several mainstream institutes working to extend healthy lifespan, from the Yeshiva University Institute for Aging Research’s work in identifying genetic variations common among human centenarians, to the Harvard Institute for Aging Research’s work on determining the mechanisms behind calorie restriction, to the numerous projects funded by Larry Ellison’s foundation and the billion dollar federal National Institute on Aging.

    In the corporate world, Sirtris Pharmaceuticals, Elixir Pharmaceuticals, and Geron corporation are working to develop therapies that will help treat the diseases of aging. They use that language because the FDA will not approve a therapy for aging per se, and the studies to demonstrate efficacy would take too long, but they aim to treat those ‘diseases of aging’ by attacking the underlying processes of aging.

    De Grey uses much more optimistic rhetoric, and talks about ultimate goals, but this doesn’t mean that investing in his approach will be more cost-effective than working to increase NIA funding, or passing the money through the Glenn Foundation, which provided funding for the Harvard Institute for Aging Research and its work on resveratrol. The negative reaction to his rhetoric is in many ways similar to the reaction to somewhat claiming that her aggressive research program could completely eliminate cancer in a the medium term (in fact, it’s worse than that, since curing cancer, which has been the aim of many billions of dollars in research funding, is just one of De Grey’s seven targets for SENS). It’s an open question whether the language of SENS and a War on Aging will actually increase funding for aging research more effectively than the Longevity Dividend proposal of Olshansky et al (although it may actually assist the Longevity Dividend effort by allowing it to triangulate politically as the ‘reasonable middle’).

    It appears to me that life extension enthusiasts may be biased to support aging research conducted by ideological kin (who are willing to publicly signal affiliation with ‘life extension’) even if other factors would indicate that this is not the most effective route to the result of effective aging treatments. [I do think that society under-invests in aging research relative to other medical research, and that SENS in fact offers a rather good expected value among the available medical research options, but this argument leads me to rate it less favorably than I otherwise would.]

  • michael vassar

    You know everyone, it’s worth mentioning that Aubrey had two distinct theses and two distinct projects.

    His primary thesis is that direct biomedical efforts at ending aging in this generation have a higher expected value than most other uses of money. People who believe this thesis should donate money to the Methusaleh Prize or

    His quite distinct secondary proposition is that SENS is the best currently known technical proposal for ending aging. People who believe this thesis as well as the first thesis should instead directly fund his SENS research.

    As for others that share his goals and accept his primary thesis, arguably Alcor and other cryonics organizations have been working on “ending aging” for decades at this point, but it is arguable that their approach is best seen as informational rather than biomedical.

  • Douglas Knight

    claiming some relevant expertize

    Surely you do have a relevant expertize that the biogerontologists lack, namely a belief in the relevance of probability and decision theory. Don’t you think that they fail to understand claims like “a small chance of success could justify the effort” and that this is a key point of departure in your opinions?

  • My 2c:

    Thiel is funding a paradigm struggle in aging science, aimed at restructuring the field for greater progress – just as he is for AI research.

    Many more than 28 researchers are just as much on de Grey’s side, for sound scientific reasons, as the 28 opposed who sat up and said something. It’s a paradigm shift, and a necessary one if this moribund field of aging research is going to produce the results that are plausible within our lifetime.

    However, the nature of the beast today is that there are strong economic incentives not to speak out on this topic if you are a career scientist who is pro-SENS/other radical life extension research. Please see:

    That has to change, and it is this change that is the real point of the exercise.

  • Yudkowsky: I misunderstood what constitutes a hit. Of the attempts you list I’d say the jury is out to way out on Foresight, Methuselah, and SIAI, that Paypal, while clearly a hit, only survived because it abandoned the wild ideas of its founders, and that there’s nothing at all unconventional about Facebook.

    I’m wildly enthusiastic for all of the ideas represented by the above (excepting Facebook again, which I don’t care about in terms of the ideas it represents, if there are any), merely skeptical that each of the individual projects will manage to produce any breakthroughs.

    I also want prediction markets on these matters.

  • Carl wrote “…or passing the money through the Glenn Foundation…”. It appears from the Foundation’s website that it does “not solicit or accept charitable contributions”.

    I would like to know what the best funding target would be for somebody who wants to promote life-extension through biogerontology, because I sometimes get asked this question. My current guess is that the M-Prize is a good option, but I haven’t spent much effort trying to evaluate the alternatives.

  • Carl Shulman


    Yes, that’s a problem, they probably don’t want to deal with the legal hassles of accepting contributions. However, if you wanted to take advantage of their expertise, you could contact them to find out what research they are funding, so as to mimic their strategy/provide matching funds.

    On other funding targets, it’s plausible that political lobbying is the most effective place to expend funds at this time. California’s Proposition 71 allocated $300 million per annum to the stem cell research over 10 years. The total cost of the campaign (acquiring signatures, ads, etc) was approximately $34.7 million, but the initial sponsor and creator of the initiative, Robert Klein, spent only ~$3 million. With a three year delay between the bulk of campaign spending (2004) and the disbursement of funds (2007), the 2004 NPV of the resulting funding stream was $1.071 billion using even a 25% interest rate (to reflect opportunities for private philanthropists to direct funding better than a state institution, the compounding effects of earlier research funding, etc). If we halve that value to reflect the risk of failure (the initiative won 59:41, but polls were less favorable when it was launched), and reduce it again to reflect the fact that political contributions are not tax-deductible (with the effect depending on one’s state and proportion of capital gains to ordinary taxable income), Klein might still have expected a hundredfold improvement in the effectiveness of his donations in funding stem cell research.

    A similar initiative ($3 billion for cancer research) will be put to the voters on November 6th in Texas with very bright prospects. Financially backing such initiatives in other wealthy states with accessible initiative processes (e.g. Florida, Ohio, and Michigan) might be a rather effective way of mobilizing funding.

    The Alliance for Aging Research, possibly the leading advocacy group for federal funding for aging research and backer of the Longevity Dividend effort, spent $1.7 million in 2006, less than 10% directly on ‘Public Policy’ (although some overhead and fundraising costs should be attributed to this), and much of that advocacy was directed to issues other than funding for basic research on aging. Given the limited scale of federal lobbying, the marginal return on further investment may still be rather high.

    However, it may be that the most effective way to influence funding is by demonstrating the potential of promising new approaches via selection of particular good unconventional projects with high expected value. Or one might invest in a for-profit startup to try to get at least one anti-aging therapy in broad use, enhancing public support and interest. Unfortunately, such efforts require greater than average ability to evaluate scientific approaches and researchers (not just biologically, but also from economic and probabilistic viewpoints). The advantage of the M-Prize is that it evades the need for such evaluative capacity (or the ability to identify such capacity in others), while promoting good novel approaches and drawing media attention to aging research.