Gwern's Reviews > A History of Life-Extensionism in the Twentieth Century

A History of Life-Extensionism in the Twentieth Century by Ilia Stambler
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Official description sums it well: an ambitious survey of life-extension movements and researchers from the late 1800s onwards across the West (specifically, America, Europe, and Russia), giving capsule biographies of leading figures and brief descriptions of their views & work. Naturally, for some particular parts there are better things to read (for example, Carrel's organ-preservation work is much more interestingly & thoroughly described in Friedman's The Immortalists: Charles Lindbergh, Dr. Alexis Carrel, and Their Daring Quest to Live Forever) but nothing I know of comes anywhere close in being as comprehensive as Stambler in showing all the twists and turns of the field and the various characters that have populated it over the years and the occasional unexpected profit from the basic & applied research they conducted (eg hormone therapy and related techniques like sex reassignment therapy trace directly back to life-extension research), yielding an interesting overall portrait. I particularly appreciated the ample material devoted to Russia: Russia is too often neglected in Western publications because of the language barrier, and Russians feature even more in life-extension than in many fields. (The Russian & American history sections also, incidentally, show that Charlie Stross, in claiming American Singulitarianism directly descends from Nikolai Fyodorov, is guilty not just of an irrelevant genetic fallacy, but also deeply ignorant of the history of both countries' schools of thought, which we can see clearly from Stambler's accounts to be parallel but independent developments.)

Stambler is a little averse to trying to synthesize any lessons from this long litany of failed interventions, but I am opinionated and embittered enough to try some generalizations:

- there are no simple interventions that can change average life expectancy by more than a few years or maximum life span at all
- as a corollary, there is no single or small number of genetic or biochemical 'master switches' of aging, because if there, some of the thousands of interventions during the past 3 centuries of active scientific research would have flipped them directly or as a downstream effect, someone would have exceeded the Calment limit, or heritability estimates of longevity would be far higher
- research proceeding on the basis of 'identify a correlate of aging' is effectively doomed: the signature feature of aging is that it is an exponential acceleration (the Gompertz curve) of mortality due to all causes ie. all organs are simultaneously becoming nonfunctional and losing homeostasis and efficacy, and these problems interact as well. Since the body is an absurdly complex dynamic system which, if drawn out as a causal network resembles the collected graphs of thousands of paranoid schizophrenics, the probability of any pair of variables being correlated is effectively 1 while the probability they are directly causally upstream/downstream of each other is close to zero. (The impressive thing is to find something which doesn't correlate with aging, like blood magnesium levels.) It gets worse. Because the fallout from aging is destroying all bodily systems and impairing homeostasis, this implies there are hundreds or thousands of pseudo-interventions: interventions which deal with some downstream effect of aging and may help on that one thing, but nothing else. For example, if one fed amphetamines to an elderly mouse, it might act 'young' but it will proceed to die on schedule regardless. (This is the more abstract form of observing that curing cancer does not do much about curing aging.) This can very easily mislead one into thinking one is making progress and conducting important work: 'I found a protein which correlates with aging and I even checked that it causally makes rats stupider by injecting it into random rats!' These can both be true and yet I can be extremely confident that this will never lead to a useful anti-aging intervention or shed light on what aging is, and that one certainly cannot "start with an old cell, change its signaling, and make it behave like new again." (Hence, we can predict that any exciting new discovery will turn out to experience an even more than usually severe 'decline effect' where the initial reports turn out to be driven by the usual methodological issues like sampling error & publication bias & non-randomized mice selection & breed-specific responses & mislabeled reagents & non-blinded evaluation & coding errors & etc or turn out to only be a pseudo-intervention on a symptom. This is because our prior for an intervention on aging is, at this point, extremely low and so all the alternative explanations are much more likely. Analogous to psychologists' perennial quest to increase intelligence: no matter how good the study looks, it is more likely that the gains are inflated by bad methodology, the product of publication bias, not g-loaded & restricted to a few subtests, due to error or fraudulent data, or something else which in another context would look like mean-spirited raillery and desperate grabbing at straws, but when it comes to IQ gains, is, sadly, always the correct answer thus far.)
- any life-extension paradigm described as "holistic" is a total and utter failure, incapable of any large effects and worse, scientifically sterile; in the descriptions of French and German 'holistic' attempts at life-extension, I saw them fail at creating a single scientific lead which yielded any new knowledge or techniques, and they (doubtless with the best of intentions) succeeded in creating unfalsifiable nonsense & harmful misinformation which continue to have circulation in the West. The only researchers whose work proved useful were the ones who insisted on 'reductionistic' approaches; Stambler quotes and paraphrases repeatedly (with a distinct tone of sarcasm, if I'm not mistaken) the better researchers noting how ignorant they were and how much research needed to be done before any interventions could hope for success, bug-lt of course they were right
- the failure of holistic approaches is emphasized when one considers where the large life-extension gains in the 20th century came from: better hygiene, antibiotics, and vaccination—all some of the greatest fruits of the reductionistic approach to biology in looking at the tiniest isolated pieces
- rigour was insufficiently valued by many of the researchers, who, neglecting blinding and randomization and large sample-sizes, succeeded only in fooling themselves and wasting the time of fellow researchers, who might try something like the Steinach procedure only to watch the effects vanish quickly, if they ever were
- related: all-cause mortality is the king of endpoints; everything else can be cheated. When it comes to aging, 'the treatment was a success but the patient died' is unacceptable. If the treatment invigorated the patient but they died on schedule, it was not an anti-aging treatment. Use of proxies is the dark side of life-extension research: quick, easy, seductive, encouraging (one is constantly making progress), but a dead end.
- many of the theories appear to have been composed in a vacuum, with little heed given to constraints on possible theories such as evolution: remarkably, it seems the first mention of "evolution" in the text has to wait all the way until the 1930s! How, you might ask, could anyone possibly try to explain the mechanisms of aging, estimate possible maximal lifespans, or give interventions without the Gompertz curve or evolutionary biology? Not well, is the answer. I could forgive the people in the late 1800s for not taking evolution or the Gompertz curve seriously in thinking about interventions, but it is baffling to read about Americans in the 1950s getting excited about organ-transplant and replacements as a path to immortality—and how, pray tell, given the exponential increase with age of all diseases and failure rates of organs, were you planning on handling replacing the brain...?
- Many of the theories are (at least in Stambler's telling), little more than folk biology or moral intuitions dressed up as science to allow righteous lording over others: oddly, it seems that what people are convinced is moral to eat just happens to always coincide with what will make one live longer, and delicious things like bacon never get held up as the Fountain of Youth, and no fruit or vegetable ever turns out to have a terrible drawback. So researchers are almost unanimous about moderate eating, or fruits and vegetables being the path to long life while meat is the path to an early grave? They are just repeating long-standing cultural prejudices about under-eating being morally virtuous and superior and meat (which commits the sin of deliciousness) is bestial and evil, part of the religious attitudes towards food we can see on display at any Whole Foods. (Many of these recommendations are clearly coming less from scientific evidence than from the disgust axis of morality.) Now if any of those researchers had been able to predict that 'intermittent fasting'—with zero net reduction in calories—had benefits, then I might credit more what they say on diet. But as it is, diet is to longevity researchers what the Knights Templar or Jews are to the conspiracy theorists—a predictable sign of derangement.
- incremental research is incremental. Our understanding of human aging is infinitely better than in 1900, yet there are still no meaningful interventions. Multi-decade gaps separate practical and theoretical breakthroughs. The standard medical-academic approach is very slow. It is entirely possible that in 2100, we will not be much beyond where we are in 2015. (I can remark that much gerontology, even today, leaves me simply mystified that anyone would feel it was worth studying: of what possible value is it to report soberly & in detail on how having a house radio during the Great Depression correlates with greater longevity (actual study!), even if we were delusory enough to imagine SES & other confounds could ever be measured to sufficient precision to control for just a few of the more blatant correlates? This is the sort of thing I feel can be described only as frivolous & unserious, and exemplifies how decades can pass with mountains of paper piling up and zero results of any importance.)

So, those are the hard and painful lessons taught by 3 centuries of life-extension work. Sometimes life gives you a Moore's law or vaccines, where the work goes deliriously well and the wildest forecasts still fall short of the mark; and sometimes it just puts up a brick wall to let generations of researchers smash their face into and babble TBI-induced nonsense into journals. What are some of the more hopeful aspects?

- somewhat like cryonics, which could have been killed along the way by any number of fundamental research findings such as the original 'exploding lysosomes' theory or by human memory turning out to be implemented as fragile electrical pulses/dynamics rather than stabler chemical encodings in synapses, one of the more hopeful things about aging is that we have not found any fundamental reason why it should be impossible to slow or eliminate it. (And if not, then in the long run there may be escape hatches through cryonics or plastination.)
- theories seem to be converging on error theories of aging: accumulating damage that results in nonlinear increases in mortality, with many of the cross-species correlates explained by different evolutionary pressures driving more or less investment into repair mechanisms. This is not as we might wish it (programmed-aging would be easier to defeat) but it at least suggests we can make progress by brute-force inference of the entire causal network and figure out what repair mechanisms are necessary (which may or may not be covered by SENS's current proposals).
- all the investment into biomedical research is starting to pay off with instruments & measurements of unparalleled precision. Early life-extension researchers could not possibly hope to measure genetic changes with age; today, it's both possible and relatively cheap. Things like Horvath's epigenetic clock suggest that we are increasingly getting the big picture, instead of being forced to focus on one or two isolated variables (which is hopeless as outlined earlier).

Some of the book is a misfire. Stambler's constant interest in researchers' personal politics ultimately winds up showing nothing other than no particular consistency or trend, and he can only lamely remark that there was some tendencies towards conservatism; less kindly-inclined readers might not grant even that and note simply that interest in gerontology is orthogonal to politics except for tactical necessity. Far too much relevant content is buried in the footnotes where few readers will check. I could wish Stambler made more of an effort to evaluate researchers on scientific grounds and give a better idea of where ideas have been vindicated or refuted by subsequent work; one would hope he had learned something from his long-term perspective, but it's unclear what he or we should take away from turning over this long account (especially if one is not already familiar with the area). Some of the things he mentions were not worth mentioning (eg the farcical 'Turing test passed' a few years ago by a chatbot pretending to be a non-native-speaking child) or should have been examined much more critically (whether the free-radical theory of aging, and the use of antioxidant supplements, is still viable). And the description of contemporary research is lacking in both detail and evaluation (eg I thought a historically-informed discussion of Aubrey Grey & SENS and how far they've gotten would be most interesting, but instead he settles for some cursory mentions).
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August 19, 2015 – Started Reading
August 19, 2015 – Shelved
August 31, 2015 – Finished Reading

Comments Showing 1-2 of 2 (2 new)

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message 1: by Andreas (new)

Andreas Great review! You might want to fix the links to the online text, they have changed.


message 2: by Douglas (new)

Douglas Summers-Stay I don't know much about the topic, but it seems to me ther eis another factor complicating research: that humans already are pretty much optimized for long life (compared to chimpanzees or mice) so even if we manage to find interventions that significantly increase the lifespan of chimps or mice, probably it won't work in people because it's already happening in people to make us live so long already. That means experiments in human longevity have to take place in humans, which takes so much longer, because its hard to get approval and you don't get results until the humans (and scientists studying them) die of old age.


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