Aging Interventions from Older Publications that Deserve a New Look

Why Read Old Papers?

These days, from what I'm told by knowledgeable people, there's a fairly tight feedback loop between current aging research and the biotech industry. When a new, major aging-related paper comes out, there are people seriously evaluating whether they can start a company around it.

But that isn't necessarily true when it comes to old research. There's no automatic means by which old papers "go viral."  There are no conferences (that I know of) where people call their colleagues' attention to remarkable, decades-old results that haven't received follow-up investigation.

I think old papers deserve a second look, for a few reasons.

1.) Often a result that had little interpretability or applicability in the past can benefit from contemporary tools. 

Let's say, twenty years ago researchers found a way to extend life in rats -- but it was a surgical operation that would be too invasive or risky to try on healthy humans. And maybe that was the end of that research direction.  But now we have lots of new options! We can take tissue samples with and without the intervention, and look at gene and protein expression, even down to the individual cell level. We can identify genetic modifications or drug targets that could be used to simulate the intervention in a safer, more targeted way.  

2.) Looking at old papers reduces some of the biases that come from looking at the latest, most-cited papers.

The volume of scientific publications is increasing at an exponential rate, up to 4% a year.[1] 

However, the reliability of the average publication has probably decreased. If there are indeed "diminishing returns to science" in recent decades, as Patrick Collison and Michael Nielsen argue [2], with roughly constant rates of important discoveries (as rated by experts) and flat economic productivity (a measure that we'd expect to correlate with technological progress) despite exponentially growing numbers of scientists, publications, and dollars devoted to science, then the quality of the average paper, scientist, or dollar allocated to research must have gone down. In that case, a randomly chosen older paper should be more trustworthy than a newer paper.

One might counter that the new papers that get the most attention aren't randomly chosen -- they're the highly cited papers, or the papers in prominent journals. Maybe the average paper has gotten worse, but the average is being pulled down by junk papers in journals so low-quality and obscure that barely anybody reads them; so, perhaps, the typical new paper that a colleague (or your twitter feed) brings to your attention is no less credible than a comparable old paper.

I think that optimistic outlook is doubtful; in fact, articles in prestigious (high-impact-factor) journals are more likely than average to be retracted, and many measures of research reliability anticorrelate with impact factor, implying that articles the most prestigious journals are less trustworthy than average[3]:

  • overestimating effect size in gene-association studies increases with impact factor (more bias in more prestigious journals)
  • sample size in gene-association studies decreases with impact factor
  • statistical power in psychology and cognitive science papers decreases with impact factor
  • randomization in animal studies is reported less frequently in papers from high-impact-factor journals
  • errors in supplemental data (eg Excel auto-converting a gene name to a date) are more common in papers from high-impact-factor journals
  • p-value reporting errors, usually in the direction of misinterpreting a non-significant result as significant, are more common in papers from high-impact-factor journals
  • metrics to identify tell-tale signs of questionable research practices find lower research quality in higher-impact-factor journals.

So, no, we can't assume that the most-cited papers of today are the cream of the crop. If anything, there's more pressure today than ever to get dramatic but trustworthy results, and that pressure is highest at the most competitive journals.

One way to reverse this effect is to go back in time.  If the amount of noise in the system is increasing, an old paper is more likely to have a valid signal than a new one.

3.) Low technology can be a blessing in disguise.

The miracle of modern molecular biology is that we keep developing better tools to affordably do breadth-first searches. "Sequence ALL the genes!" "Quantify ALL the transcripts!" "Quantify ALL the proteins!" And so on.

The danger of having these incredible tools is that you can cherrypick positive results -- and people do.

It's much harder to erroneously get an apparently therapeutic intervention if your tools are blunter and your search space is smaller. If somebody in 1944 says that shining light on a duck's head makes its testes grow[4], then by gum I bet that actually happens!  

Because it's not coming from a breadth-first search, somebody had to have a specific reason to think that the experiment would work, and because there just aren't that many experiments being done at random, you can expect that to be a well-informed reason. The prior is higher.  

There's a similar sense in which lack of standardization is a blessing in disguise. Most mammal experiments today are done on the same handful of strains of inbred mice, for instance. The standardization is a boon to researchers in many ways (you can make apples-to-apples comparisons, you don't have to spend time inventing the basics of experimental methods yourself) but it also means that experimental results can just turn out to be an artifact of the "standard methodology."  Looking at older experiments, which have greater diversity in model organisms and other experimental methods, can be a corrective.

4.) Old papers are undervalued opportunities.

The author of the latest exciting result is a ready-made advocate for the discovery and a potential founder or collaborator for new ventures to put it into practice.  The author of an old paper, by contrast, might be dead or retired, with nobody to champion the potential applications of the discovery. It's very easy for an area of research to quietly fall out of fashion through no inherent lack of merit, just because it never met the right opportunity for application. 

I'm just barely old enough to remember when neural nets were thought of as an embarrassing phase in the history of computer science; they became "hot" again in 2012, with AlexNet, when newly affordable GPUs proved that deep learning algorithms could suddenly outperform the competition. In other words, advances in a totally different technology made a "failed" research approach into an overnight success. 

Going through old, not necessarily well-known experiments to see if there are opportunities is something I don't believe is being done that often, and is probably an unusually good place to apply a little bit of time and attention for big returns.

That said, let's look at some specific examples!  These are all results from prior to the year 2000, that are experimental interventions affecting vertebrate lifespan or aging, and which aren't currently the focus of a research program that I'm aware of.

Lowering Body Temperature: 71% Life Extension in Fish

Unusually long-lived vertebrates (tortoises, sharks, rockfish, etc, which can survive for centuries, or naked mole rats, which are extremely long-lived for their size) are frequently cold-blooded.  Warm-blooded animals which are long-lived (in absolute terms, like whales, or relative to their size, like bats, hummingbirds, and squirrels) often undergo temporary reductions in body temperature, during diving or hibernation.  Moreover, interventions like dietary restriction which extend lifespan have the effect of reducing body temperature.  So can reducing body temperature directly extend life?

For a cold-blooded example, transferring fish from 20-degree water to 15-degree water extended lifespan by 71%, in a 1972 study.[5]

To reduce the body temperature of a warm-blooded animal, it's not enough to reduce ambient temperature, since warm-blooded animals generate heat to compensate. In fact, reducing the ambient temperature actually shortens mouse lifespan. However, there are tricks to lower body temperature in a warm-blooded animal.

Mice genetically modified to overexpress the uncoupling protein, UCP2, in the hypothalamus have lower body temperature than wild-type[6], and they live longer than their wild-type counterparts (20% increase in female median lifespan, 12% in male.)

You can also induce hypothermia by stimulating the heat-detecting cells in the hypothalamus, either by injecting capsaicin [7], heating the hypothalamus directly with a thermode [8], or stimulating the heat-sensing neurons optogenetically [9].

The natural next experiments to do are a.) see if any of these other methods of inducing hypothermia affect lifespan and diseases of aging in mice or other mammals; b.) do longitudinal transcriptomics or other broad assays to see what reduced body temperature is doing and whether its effects can be simulated chemically or genetically.

Altered Photoperiod Cycle Length: Short "Years" Shorten Lifespan 30% in Lemurs

Days get longer in summer and shorter in winter; by lengthening or shortening the cycle of alteration in photoperiod length (by changing artificial lighting) you can give an animal a shorter or longer subjective "year".

This turns out to affect lifespan!

The gray mouse lemur is a prosimian primate, native to Madagascar, that is long-lived for its size. During the long-day summer, gray mouse lemurs breed and are more active; during the short-day winter, they gain weight, become lethargic, and don't copulate. If you alter the photoperiod cycle artificially, you can alter the timing of these behavioral and morphological changes accordingly -- and if you reduce the "year length" by a third, from 12 months to 8 months, lifespan also shortens by 30% and the onset of white fur happens 30% earlier. [10] . In other words, lemurs live 9-10 "subjective years", whether those are 8-month years or 12-month years. 

The obvious follow-up experiment is to go the other direction -- do lemurs (or other animals) live longer if you subject them to 16-month subjective years? And to take some tissue and blood samples and try to identify how this effect works -- do we see pathological changes, transcriptional changes, hormonal changes, metabolic changes?

Constant Light Exposure: 25% Life Extension in Hamsters

A Syrian hamster model of congenital heart disease showed delayed onset of heart failure and 25% life extension if they were kept in continuously lit conditions.[11]

The obvious corollary studies are to take heart tissue samples and blood samples and look for altered gene expression or metabolic parameters that might explain the effect of light exposure on preventing heart failure. It also might be possible to experiment directly with continuous light exposure on humans, since it's probably not dangerous.

Pineal-Thymus Graft: 24% Life Extension in Aged Mice

Implanting the pineal gland of a young mouse into the thymus of an old (16-22 month) mouse extends lifespan 19% in C57BL6 mice, 20% in Balb/c mice, and 35% in hybrid mice, for an average of 24% overall.[12] This is consonant with a more extensive literature about the pineal gland or the main hormone (melatonin) it secretes having a life-extending effect through preventing the dysregulation of the circadian rhythm which occurs with age.

The obvious follow-up study to do is a replication of the same implantation experiment, along with longitudinal expression data, to find out how this works and work towards identifying how a similar effect could be replicated by a less invasive intervention.

Splenectomy: 19% Life Extension in Aged Mice

In a 1969 experiment, adding spleen cells to mice of the same age as the cell donors shortened lifespan; adding spleen cells from younger mice (14 week) to older mice (76 week) extended median lifespan from 105 weeks to 128 weeks, a 13% lifespan effect; and removing the spleens of mice altogether at age 97 weeks increased median remaining lifespan from 118 to 158 weeks, a 19% lifespan effect.

Clearly, the aged mouse spleen contains some factor that accelerates age-related decline. The obvious question is to find out what this is, through expression or proteomics studies on young, aged, and splenectomized mice, and see if there's a way to target the culprit pharmacologically.

Induced Hypothyroidism: 17% Life Extension in Rats

Exposing newborn rats to thyroid hormone permanently reduces their bodyweight and thyroxine levels; it's a way of artificially inducing hypothyroidism.[13] It also has the effect of dramatically elevating their prolactin levels; as prolactin is stimulated by TSH release from the hypothalamus, clearly neonatal T4 exposure doesn't prevent TSH release in the brain, but rather impairs the thyroid's ability to respond to it.  This induced hypothyroidism also extends median lifespan by 17% and maximal lifespan by 6%.

Obviously, inducing hypothyroidism isn't a viable intervention for humans, but looking at changes in hormone levels and gene regulation in induced hypothyroidism might give clues to what downstream mechanisms are responsible for the lifespan increase and whether there's a less-side-effect-heavy way to induce it.

Castration: 17% Life Extension in Rats

Removing the testes of male Wistar rats has been found to extend lifespan 17% relative to unbred intact males; removing the ovaries extends lifespan 29% relative to unbred females. [14]

This isn't too surprising given that caloric restriction (a reliable life-extending intervention in rodents under typical lab conditions) has antigonadal effects, and that extremely dramatic lifespan effects can come from removing the germ cells in C. elegans.[15] There's also some correlational evidence -- for instance, castrated male cats arriving at veterinary hospitals lived 67% longer than intact males.[16]

Obviously, castration isn't a practical intervention for most humans, but it's possible that there's some downstream effect that doesn't alter fertility or observable sex characteristics and preserves some of the anti-aging effect; this is a good opportunity for looking at longitudinal expression changes in castrated vs. intact animals and trying to identify the mechanism of lifespan extension.

Lateral Hypothalamic Stimulation: 5% Life Extension in Aged Rats

Stimulating the lateral hypothalamus is pleasurable, and animals given the opportunity to self-stimulate will do so; this is what's known as wireheading.  Interestingly enough, there are interactions with aging here as well.  Young adult rats have more neurons and more electrical activity in the lateral hypothalamic area (LHA) than old rats; young rats also exhibit more self-stimulatory behavior than old rats when given access to a button that turns on the electrode. Moreover, in old rats, chronic stimulation in the LHA extended lifespan from 1075 days to 1125 days (5% of total median lifespan, 8% of total maximum lifespan, 35% of residual lifespan); stimulation reduced body mass as well.[17]

Is this just a dietary restriction effect, or is it something else? The natural thing to do is to try the experiment again, this time compared against controls given the exact same amount of food to eat; and also, to take brain samples after death and possibly other blood samples during lifespan to try to identify metabolic or regulatory changes caused by the stimulation.

Blindness: Increases Survival in Rats

Blindness affects the circadian rhythm; it effectively gives the same hormonal signals as perpetual darkness. Rats blinded at 25 days had increased lifespan relative to controls; at 748 days, when the experiment concluded, the blind rats had a 95% survival rate while the control rats had a 50% survival rate.

The natural follow-up is to do a full lifespan study so we can get an actual measurement of the effect on median lifespan, as well as measurements of other biomarkers so we can identify a mechanism and possibly a way to replicate the anti-aging effect without actually inducing blindness.

Fetal Hypothalmic Graft: Restores Fertility and Circadian Rhythm in Rats and Hamsters

In keeping with the pattern of neuroendocrine effects on aging, it turns out that transplanting the suprachiasmatic nucleus (the part of the hypothalamus responsible for entraining the circadian rhythm in response to day length) from fetal animals into the brains of aged animals can restore the periodicity of the circadian rhythm and restore diminished fertility. With age, circadian rhythms become less regular; animals wake more during the periods when they should be sleeping, and/or are more lethargic during the periods when they should be awake.  Fetal SCN grafts reverse this phenomenon in both hamsters [18] and rats.[19]

Moreover, 7 of 10 aged rats given fetal anterior hypothalamus transplants regained fertility and fathered a total of 106 pups[20], while medial basal hypothalamus transplants from rat fetuses into aged female rats reversed hypogonadism.[21]

The hypothalamus regulates a variety of hormonal signals, which become dysregulated with age; it seems that some of these effects can be reversed by transplanting a younger hypothalamus. The most natural question to ask is, first, does this extend life? Second, can we identify on the genetic or molecular level what the younger hypothalamus tissue is doing that improves aging-related phenotypes? If so, there might be a non-invasive way to replicate the effect.

What Now?
These are ten very broad suggestions for animal experiments to run, which might yield targets that are ripe for intervention.  I'd expect, without looking too deeply into details, that each of these ten experiments would have a 6-figure price tag. And I'm aware of nobody who's working on these projects (please correct me if I'm wrong!)

Could these projects turn into biotech companies? It's hard to say, of course; it depends on whether the experimental results are good, among other things. But I'm pretty inclined to believe that we don't know all the aging-modulating targets yet. That points to phenotypic screening approaches (like what we're doing at Daphnia Labsor target-discovery studies (like the ones proposed in this post, or like the ones being done at Gordian, BioAge, or Fauna), being quite valuable. We don't know everything that's out there, and early-stage exploration is a lot cheaper than depth-first drug development, so on the margin more exploration is a "good buy", it seems.

[3]Brembs, Björn. "Prestigious science journals struggle to reach even average reliability." Frontiers in human neuroscience 12 (2018): 37.
[4]Benoit, Jacques, and L. Ott. "External and internal factors in sexual activity: effect of irradiation with different wave-lengths on the mechanisms of photostimulation of the hypophysis and on testicular growth in the immature duck." The Yale journal of biology and medicine 17.1 (1944): 27.
[5]Liu, R. K., and R. L. Walford. "The effect of lowered body temperature on lifespan and immune and non-immune processes." __Gerontology__ 18.5-6 (1972): 363-388.
[6]Conti, Bruno, et al. "Transgenic mice with a reduced core body temperature have an increased life span." __Science__ 314.5800 (2006): 825-82
[7]Jancsó-Gábor, Aurelia, J. Szolcsanyi, and N. Jancso. "Stimulation and desensitization of the hypothalamic heat‐sensitive structures by capsaicin in rats." __The Journal of physiology__ 208.2 (1970): 449-459.
[8]Hammel, H. T., J. D. Hardy, and MiM Fusco. "Thermoregulatory responses to hypothalamic cooling in unanesthetized dogs." __American Journal of Physiology-Legacy Content__ 198.3 (1960): 481-486.
[9]Zhao, Zheng-Dong, et al. "A hypothalamic circuit that controls body temperature." __Proceedings of the National Academy of Sciences__ 114.8 (2017): 2042-2047.
[10]Perret, Martine. "Change in Photoperiodic Cycle Affects Life Span in a Prosimian Primate (Microcebus murinus." __Journal of biological rhythms__ 12.2 (1997): 136-145.
[11]Tapp, Walter, and Benjamin Natelson. "Life extension in heart disease: an animal model." __The Lancet__ 327.8475 (1986): 238-24
[12]Pierpaoli, Walter, et al. "The pineal control of aging: the effects of melatonin and pineal grafting on the survival of older mice." __Annals of the New York Academy of Sciences__ 621.1 (1991): 291-313.
[13]Ooka, Hiroshi, Saori Fujita, and Emiko Yoshimoto. "Pituitary-thyroid activity and longevity in neonatally thyroxine-treated rats." __Mechanisms of ageing and development__ 22.2 (1983): 113-12
[14]Asdell, S. A., and S. R. Joshi. "Reproduction and longevity in the hamster and rat." __Biology of reproduction__ 14.4 (1976): 478-480.
[15]Hsin, Honor, and Cynthia Kenyon. "Signals from the reproductive system regulate the lifespan of C. elegans." Nature 399.6734 (1999): 362.
[16]Hamilton, James B. "Relationship of castration, spaying, and sex to survival and duration of life in domestic cats." __Reproduction and aging. New York, NY: MSS Information Corporation__ (1974): 96-115.
[17]Frolkis, V. V., et al. "The lateral hypothalamic area: Peculiarities of aging and the effect of chronic electrical stimulation on the lifespan in rats." __Neurophysiology__ 32.4 (2000): 276-282.
[18]Viswanathan, N., and F. C. Davis. "Suprachiasmatic nucleus grafts restore circadian function in aged hamsters." __Brain research__ 686.1 (1995): 10-16.
[19]Li, Hua, and Evelyn Satinoff. "Fetal tissue containing the suprachiasmatic nucleus restores multiple circadian rhythms in old rats." __American Journal of Physiology-Regulatory, Integrative and Comparative Physiology__ 275.6 (1998): R1735-R1744.
[20]Huang, H. H., J. Q. Kissane, and E. J. Hawrylewicz. "Restoration of sexual function and fertility by fetal hypothalamic transplant in impotent aged male rats." __Neurobiology of aging__ 8.5 (1987): 465-472.
[21]MATSUMOTO, Akira, et al. "Recovery of declined ovarian function in aged female rats by transplantation of newborn hypothalamic tissue." __Proceedings of the Japan Academy, Series B__ 60.4 (1984): 73-76

Genes involved in aging: looking for intersections

A natural type of question you might ask, if you're interested in understanding aging, is which genes are involved in the aging process. The practical upshot of identifying genes with causal roles is that they're potential drug targets.  If diseases of aging are caused or worsened by the excess of some protein, you might want to inhibit the production or activity of that protein. If diseases of aging are caused or worsened by a deficit in some protein, you might want to stimulate its production.

We have a lot of different kinds of experiments that can be run for identifying what genes and proteins are involved in aging, and thus a lot of aging-related "omics" studies. I'll briefly summarize a few categories I know about.

Longitudinal Transcriptomics

You can compare the expression of genes in tissue samples from old vs. young organisms (humans or mice) and see which genes are expressed more or less with age.  Today it's even possible to get single-cell resolution on gene expression; we can identify the rate of gene transcription for each gene in a specific cell at a given time.  Similarly, you can get proteomics data, directly measuring the quantity of each protein in a tissue sample.

This gives us correlational information about which genes are altered in the aging process, in particular tissues and cell types. It doesn't by itself tell us which interventions might prevent disease.  If a particular gene is more expressed with age, it could be because it's a cause of some deleterious process, or because it's a symptom of that process, or because it's part of the body's attempt to mitigate that process.  Whether you want to inhibit that protein's activity or production depends on what it's doing, and expression levels by themselves can't tell you that.

Comparative Genomics

Animals don't all age in the same way. Some are exceptionally long-lived, either in absolute terms (whales, elephants, tortoises, rockfishes, the Greenland shark) or relative to their size (bats, naked mole rats). Some mammals are immune from cancer.  Can we identify "genes responsible for healthy longevity" in the animal kingdom? Could we "borrow" the adaptations that slow-aging animals have developed, as treatments for humans?

Given the genomes for two species, you can identify homologous genes -- genes that have very similar sequences and probably similar functions.  Something like half our genes have homologues in common with insects and all vertebrates.  

If the homologue of a gene in an exceptionally long-lived species is absent or has a loss-of-function mutation, you might ask whether that gene contributes to aging.

If a gene family of similar proteins is "expanded" in a long-lived species (meaning there are more variations on that gene present) or if a gene has a high copy number (meaning there are many identical versions of that gene) you might ask whether that gene has a protective effect.

If a gene shows evidence of positive selection in a long-lived species, you might ask whether that gene has a protective effect against some aging process.

If there's a correlation between copy number or gene family size and lifespan (or lifespan per body weight) across species, that's somewhat stronger evidence that there's an association between those genes and lifespan.

Again, these are all correlational; they don't tell you how the gene works, or what would happen if you interfered with it experimentally.

Experimental Genetic Modifications

If you induce a genetic mutation in a mouse gene and the mouse lives longer or avoids the onset of age-related diseases, then you do have causal evidence that the gene is involved in regulating aging.

There are a variety of ways of inducing specific mutations, some permanent and some temporary, some causing total absence of the gene (knockout) while others cause a deficit (knockdown) or unusually high production of the gene product (overexpression.)

Looking for the Intersection

Most broad studies (longitudinal transcriptomics, comparative genomics) looking for genes involved in aging come up with totally different lists of candidate genes. 

Sometimes, of course, this is expected, because they're looking at different tissues or different organisms. You don't expect all animals or all tissues to change in the same way with age. And, of course, comparing genomes between species and comparing gene expression over time within one species are apples-to-oranges comparisons.

But even in cases where the experiments are supposed to measure the same thing, there's poor replication. And that's not surprising because the samples are so small. It's not uncommon to see longitudinal transcriptomics studies with fewer than ten organisms in the "old" and "young" groups. 

And this matters because if you want to have any hope of translation to humans, you've got to be able to have results that are consistent across different strains of mouse, or even species of mammal; if it's all wiped out by natural variation between organisms, there's no way you're getting signal usable for designing human treatments.

So I did a very, very crude type of meta-analysis; I looked at all the studies I could, out of these three types (transcriptomics and proteomics of aging; comparative genomics of aging in long-lived species; and interventional studies of genetic modifications; all restricted to studies on vertebrates) and ranked genes (or gene families) by the number of papers in which the gene popped out as significant. 

There are a couple of potential flaws in my methodology.

First of all, I used Google Scholar to search, and stopped when the relevant search terms stopped returning studies of the relevant type. There may well have been studies this search method missed; it's just much more time-efficient than using PubMed searches (which reliably produce far less relevant results, but it's easier to document exactly how many papers matched search terms, which is why they're the standard method in formal literature reviews.)

Second of all, I didn't use a consistent cutoff in picking out which genes were significant. (In a study that tests all 20,000 or so human genes for differential expression, "statistically significant" is a very low bar.) I generally noted down the handful of genes that had the highest fold change and lowest p-value, not literally all the ones that met a significance threshold.  

Thirdly, some studies, of course, like lifespan studies of a genetic modification, aren't unbiased screens of all genes; genes that have gained more scientific interest are likely to be studied more often, so in part this list of "top genes" reflects the biases of the research literature.

And, finally, since we're comparing different types of studies, we're not making apples-to-apples comparisons. You don't expect the genes differentially expressed with age to be exactly the same as the genes which are modified in long-lived organisms or the same as those which alter lifespan when experimentally mutated. If a gene shows up in all three types of studies I think that's some sort of evidence that it's "more likely to really be involved" in aging, but not in the same straightforward sense that it's true that a study is more credible when it replicates exactly.

However, I think it's worth doing something in this vein, as a way of helping orient ourselves in a growing field. As more and more papers come out claiming that they've found genes "associated" with aging, we want to be able to be familiar with what the most common ones that keep showing up are.  Just as with genome-wide association studies for genetic predictors of disease, one correlation showing up in a study doesn't mean we've found the "gene for" anything. I think of the aggregation process as a learning experience, for getting a sense of what the field as a whole looks like.




Transcriptional Changes

Comparative Genomics

Experimental Studies

Number of Publications 

IGF family

Insulin-like growth factors and their receptors

Anabolism & growth

increased expression in aged human microglia; increased expression in aged mouse bones; increased expression in aged rotifers; decreased expression in aged mouse hearts

positively selected in the short-lived killifish; reduced expression in the long-lived naked mole rat; mutated in the long-lived Brandt's bat

IGF1R knockout mice live 26% longer; 7 other mutated strains of long-lived mice have decreased IGF expression levels


SERPIN family


Protease inhibitors (prevent protein breakdown)

Increased expression with age across mouse tissues (liver, brain, heart, kidney, lung, neural stem cells, CD4+ T cells); increased expression in aged human microglia

positively selected in all 3 long-lived marine mammal lineages (manatees, walruses, and whales)



FGF family

fibroblast growth factors

promote cell division and growth

FGFr1 expression goes up with age in humans, mice, rats, and wolves, but down in bats; increased FGF6 expression with age in horse cartilage and mouse bone, but reduced with age in rat skeletal muscle

under positive selection in long-lived giant tortoises and whales

transgenic mice overexpressing FGF21 live 36% longer than wild type



Tumor necrosis factor

Inflammatory cytokine

increased expression with age in mouse and human microglia; increased expression in all mouse, rat, killifish, and human tissues with age; increased expression in aged mouse lungs, bones, and CD4+ T cells


long-lived mice with transgenic IKKA inserted into the hypothalamus have lower TNF expression


SIRT family


DNA repair, metabolic regulation

expression goes down with age in humans, mice, and wolves, but up in long-lived bats

positively selected in long-lived painted turtles

SIRT1 and SIRT6 overexpressing male mice live 15% longer; SIRT1 expression is higher in long-lived RASGRF1-deficient and NAS1-deficient mice



Growth hormone

Promotes growth


long-lived bats are GH deficient

mice without the growth hormone receptor GHR live 33% longer than wild type; mice without growth hormone releasing hormone live 40% longer; rats deficient in growth hormone live 7-10% longer; two other strains of long-lived mice are deficient in growth hormome


UCP family

Uncoupling proteins

mitochondrial proteins, regulating respiration & thermogenesis

reduced expression in rat skeletal muscle with age

long-lived whales and naked mole rats are deficient in UCP1

higher UCP1 expression in long-lived PTEN-overexpressing mice; hypothalamic UCP2 overexpression extends life 12-20%


CLIC family

chloride intracellular ion channels

regulate cell membrane potential

increased expression in aged human microglia, skin, and macula; reduced expression in aged human brains 




HSP family

Heat shock proteins

Stress response

several HSP's show increased expression with age in mouse bones, while others show decreased expression with age in mouse hearts and brains

duplicated in the long-lived bowhead whale genome



CC family

CC chemokines and receptors

Inflammatory response

CC receptors downregulated with age in humans; CC chemokines overexpressed in aged mouse bones and mouse neural stem cells

CC receptors positively selected in the long-lived painted turtle



Aggregate Stats

I found 84 papers for use in this analysis; 25 were longitudinal transcriptomics papers, 13 were comparative genomics papers, and 45 were lifespan studies of genetic modifications in mammals.

In total, I found 412 genes and gene families whose expression, expansion, unique mutation, or other properties was significantly associated with lifespan with a high magnitude of effect size.  (There would have been far more that simply met the significance thresholds of the studies.) 

Here's a histogram of the frequency of the distribution of the genes.

The majority of genes only appeared in one paper; most genes that were significantly related to age or lifespan in one paper did not show up in any others.  

The top-scoring gene families suggest some conclusions.

1. It's probably worth doing interventional genetic modifications on mammals for genes that show a lot of correlational evidence of being involved in aging. Inhibiting the expression of serpins, heat shock proteins, or chemokines in mice might show a delay in some aging phenotypes.

2. Some of these genes make sense in light of the "hallmarks of aging" -- serpins and heat shock proteins are associated with proteostasis and the elimination of misfolded proteins; IGF, GH, and FGF's are involved in nutrient sensing and growth; UCP is a key mitochondrial function; TNF and the chemokines are inflammatory signals. It would make sense that dysregulation of these functions plays a causal role in age-related disease. 

3. We need much larger sample sizes on longitudinal transcriptomics studies. The typical studies I found, mouse or human, had fewer than ten experimental subjects per age group. As you might expect, this yielded inconsistent results. Between-individual diversity can be a confounding factor that makes it harder to reliably identify age-related changes.

Interestingly, [22] clusters gene transcripts in human T cells according to their aging-related dynamics, and finds three kinds of genes:
  1. genes that follow a "U-shaped" curve, declining in expression level until about age 60 and then rising again; these include growth-and-proliferation-associated signals
  2. genes that follow an inverted-U curve, rising in expression level until about age 70 and then declining; these are mostly cancer-related genes as well as the mTOR and Jak-STAT pathways
  3. genes that start out high in expression level and start to decline at age 80; these are mostly mitochondrial and neurological.

I find this very interesting as a categorization and wonder if it holds up for more cell and tissue types. 

From a therapeutic perspective, if this pattern generalizes, I could imagine we might want to enhance production or activity of proteins in the third cluster, inhibit the production or activity of compounds in the second cluster, and be cautious about the tradeoffs in the first cluster, since both straightforwardly inhibiting and accelerating nonspecific growth signals can have serious side effects.  

It's hard to tell, for now. But in order to replicate this result you'd also need more studies to use multiple time periods, instead of just taking old and young samples; once again, increasing the scale of longitudinal transcriptomic studies would be very valuable.


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Is Stupidity Strength? Part 4: Are VCs Stupid?

Defining the Question

If you want to write a thinkpiece bashing venture capitalists, it's easy enough. All you have to do is find an example of one VC-backed company that sounds stupid or mockable, and generalize that to condemning venture capitalists overall. Instant Valleywag article!

But "can you find a seemingly-dumb VC investment?" isn't an interesting question; the answer is obviously yes, and you can't do anything practical with that answer except drum up the public's knee-jerk resentment against Silicon Valley. I'm not interested in going that route.

Here are two interesting questions:

  1. Are institutional investors who invest in VC firms being economically rational by investing in VC the way they typically do today? Could they make more money doing something different? (That is, is "VC overrated" from the perspective of an institutional investor like a retirement fund or university endowment?)
  2. Are VC's being economically rational by choosing startups to invest in as they typically do today? Could a VC firm make more money doing something different? (That is, are VC's being "stupid" in the sense that a contrarian investment approach could strictly outperform them?)

If the answers to these questions are "no" and "yes" respectively, that doesn't mean all VCs are bad investors, just the typical VC. In fact, quite a few VCs argue that they're reliably beating the market by following a contrarian strategy.

If there's overinvestment in VC on the whole, or if there's a contrarian VC investment strategy that beats the market, that's good news -- it means there's an economic opportunity!

If not, that's a different kind of good news: the market is efficient and pretty much doing as well as a market can at allocating capital where it creates the most value. We can trust price signals to be something like quality signals.

There's upside whichever way the data shakes out, so we can go into this inquiry with open minds.

The VC Industry: How Big Is It? 

The National Venture Capital Association's latest 2019 Q3 report offers the following figures:

  • The US VC industry invests about $100 billion a year into companies
  • There are about 2000 US VC firms
  • US VC firms invest in about 10,000 companies a year
  • Over the past 10 years, total US VC investment has more than doubled

VC is still a tiny fraction of investment capital as a whole, however. The VC industry's total assets under management are worth $524 billion; by comparison, mutual funds manage $17 trillion.    

Most ordinary people don't invest in VC, but VC is popular with institutional investors like college endowments. For instance, 18 percent of Yale's endowment is invested in venture capital. 

Why care about VC, if it's a small fraction of all investments? At the very least, it's a matter of professional interest if you work in VC-funded industries like software or biotech; also, to the extent that VC is involved in funding technological innovation, how well VC does at funding real technologies determines how abundant and productive our future economy will be.

How Good Are Aggregate returns on VC?

Does the VC industry as a whole have a good rate of return on investment compared to other types of asset?  Should institutional investors be investing less in VC, more, or about the same?

This question is mostly about the average performance of VC firms; it could both be true that most VC firms have poor returns but a few exceptional firms excel, so that if you picked  a VC firm at random its expected return would still be good.

Cambridge Associates' venture capital index estimates the returns on venture capital. It depends a lot on the time horizon: the 5-year rate of return is 13%, the 10-year is 14%, and the 30-year is 32%. But it's still clearly higher in long-run growth than the return on stock indexes like the S&P 500, which has a 5-year rate of return of 11%, 10-year rate of 16%, and 30-year rate of 10%. Investing in a random VC is higher-return in expectation, though also higher-variance, than just investing in an index fund.  In other words, investing in VC is not so stupid that you could do strictly better by just putting your money in a random stock instead. But that's a low bar.

A more subtle analysis takes account of risk as well as return. VC's may have higher average returns than the stock market, but they're also more volatile. Investors rationally see a tradeoff between risk (variance) and return (expected value) and are willing to tolerate higher risk only if it also brings higher returns; there's a mathematically optimal balance, defined by standard portfolio theory, defining how a investor with a given level of risk aversion would maximize long-run returns.

 What's the risk-adjusted rate of return, comparing VC returns to the alternative of putting that same investment into an index fund? A 2015 study in the Journal of Finance says it's significantly negative, p=0.015; this means that rational portfolio investors should be investing less in VC. A 2010 study using more conservative assumptions finds a statistically insignificant level of excess returns (alpha = 0.17, p = 0.54), implying that investors are basically investing the right amount in VC; it's neither overrated nor underrated. I'm not sure how to evaluate which set of assumptions is more reasonable.

As of 2018, not a single Ivy League school endowment (which all include VC as part of their investment portfolios) had higher returns than a simple "60-40 portfolio" (60% stocks, 40%  bonds), which would have made a 15% yearly return; and the Ivy portfolios were also much higher risk! So Ivy League fund managers, at least, could do strictly better by investing in no VCs at all!

Is it stupid to invest money in VC at all? It's hard to say, given the conflicting results from the data. But we can at least say that institutional investors shouldn't be putting more of their money into VC.

Variation Within VC: Luck or Skill?

Some VC firms have much higher returns than others.  The Column Group, a biotech VC firm, posted a staggering 408% return in the first quarter of 2019; the same report claims a return of just 10% for the median VC.

Some observers are even more pessimistic about the median VC; Paul Graham, writing in 2009, said that in his experience the median VC loses money.   Israeli VC Gil Ben-Artzy claims that 95% of VC funds make less than 3x returns over a typically 10-year span, which amounts to about 11% per year -- worse than the S&P 500! 

A sample of 535 VCs also finds they have a median rate of return of 4% -- quite a bit worse than the S&P 500.

Most VCs, it seems, have terrible track records. Only one in every twenty is making more money than you could get by just investing in an index fund (and skip paying the VCs their high fees).

But that doesn't necessarily mean the Column Group is smarter than the median VC; they might have just gotten lucky. A lottery winner has a very large return on investment compared to the median lottery player, but not because she has higher skill.

If you want to ascertain if there's such a thing as investment skill, you need to look at investor track records. Do the same investors make above-average returns year after year? Then it might be skill (though it could also be something else, like monopoly power.)  But if investors show no consistency in returns, it definitely can't be skill.

A 2006 study suggests that investor skill exists. Firms funded by VCs with prior successful investments (where "success" means IPO) are more likely to succeed, but this effect goes away in firms funded by previously successful entrepreneurs.  So, top-tier investors are more likely to pick successful startups, but don't add much benefit to startups with experienced founders.

Looking at VC fund performance, investors who did well in the past continue to do well in the future; top-quartile firms make an average of 7-8 percentage points more each year than bottom-quartile firms.

Another study also shows a large effect of investor skill: VC firms in the 80th percentile for past performance made 15 percentage points more  a year than firms in the 20th percentile.

The evidence is unequivocal: some VCs are much better than others, consistently, and VCs who are any good at all are a minority.

Predictably Wrong Strategies

"Ok, VC as a whole doesn't have great returns relative to its risk, but some investors are much better than that! Why don't institutional investors just invest in good VC's and not bad ones?"

Well, maybe they can't; maybe identifying a VC firm with a good track record is hard. After all, fund performance data is private and jealously guarded, and every VC firm tries to only share numbers that make it look impressive.  

How could we test this hypothesis? Well, there's a way to disprove it: if there were an easy-to-check criterion that accurately distinguished good investors from bad ones, then you'd be able to use that criterion to choose good investors who get above-market returns; which means that anyone not using this criterion is being financially stupid.   

Well, here's such a criterion: investors with strong jawlines lose money. No, really.

Investors with higher facial width-to-height ratios -- a predictor of high testosterone levels -- make over 5 percentage points less a year than their narrow-faced counterparts.

This is a huge effect, comparable to the difference between stocks and cash. If you invested only in funds run by low-testosterone investors, you'd be 6x as wealthy in 20 years.

(To be fair, these are hedge fund managers, not VCs; in this section I'll refer to evidence from a variety of investment types, but there seem to be commonalities). 

What's going on here? Well, clearly, many rich people have a bias towards masculine, confident, charismatic men -- so much so, that they'll even invest money in crappy funds if they're run by guys with strong jawlines. Testosterone empirically causes people to make overly risky investments, which in turn correlates with worse performance.  A lot of investors are apparently letting bias get in the way of profit.

Additionally, hedge fund managers rated as more psychopathic earned about about 2 percentage points less a year than more empathetic managers  (p < 0.05).

Fund managers who attended more selective colleges also outperform those from less selective colleges, by about a percentage point per year.

Conscientiousness correlates positively with investor performance: 80th percentile conscientiousness investors are 6x as likely to achieve top-quartile performance as median-conscientiousness investors.  Conscientiousness is also a strong predictor of success in entrepreneurs.

In venture capital specifically, venture capitalists are much more likely to make successful investments if they have science or engineering degrees, have past VC or startup experience, and don't have MBA's.

Among innovation-intensive businesses, the percent of female executives correlates positively with firm performance; likewise, new businesses founded by men perform better than those founded by women, but this  difference is fully explained by male-founded businesses having more starting capital, being in more tightly clustered regions, and being more likely to focus on high-tech manufacturing.

 Moreover, VCs given identical pitches from entrepreneurs reliably prefer male to female entrepreneurs, and they particularly like pitches from attractive men; attractiveness in women doesn't matter.

What does this all mean? In short: low-testosterone, non-psychopathic, STEM-educated, conscientious people make better investment decisions than aggressive, impulsive risk-takers with MBA's; investors have a bias towards handsome, masculine men; and female founders can do as well as male founders if they enter the most technically innovative industries and get adequate starting capital.

"Just invest in the most macho, wildly confident guy you can find" is a common strategy, and one that fails. These recklessly overconfident, less conscientious individuals are more likely to take unwise risks, and also more likely to commit fraud -- both of which are bad for business in the long run.

(This hypothesis also matches the pattern of big recent failures in startup performance like WeWork and Uber).

You can beat the market as  an institutional investor just by not executing this stupid strategy. Therefore: we can be confident that a lot of capital is being invested stupidly, ie avoidably passing up opportunities for more money.

Do I have a problem with handsome, masculine men? Heck no; I married one!  

I'm claiming that there is a lot of "dumb money" out there, which favors handsome, masculine men even when they lose money. 

Gary Becker's theory about prejudice was that it ought to eventually die out.  racist employers who won't hire black people will eventually go out of business in a competitive market; any irrational prejudice in business owners or investors, should be selected against relative to optimal profit-maximizing behavior. If we see persistent prejudice that goes against financial self-interest, the market must be non-competitive.

Well, we see persistent prejudice in investment! In the most obvious way you'd expect: bias towards traits that make people high-status in our society. People spend money on people who look like winners; they don't check track records of actual winning. Why don't they all go broke and thus remove themselves from the market? I don't know, but they don't. 

I do know, from the account of my friend Zvi who used to work on sports betting, that most people who bet on sports are not even remotely optimizing for making money; they're just sports fans who bet on the home team. You can make money just by always betting on the away team. There are just that many bets made by "dumb money", that you can "beat the market" without doing anything cleverer than betting against blind fandom.

Maybe something not too different is happening in business as well.

This is good empirical corroboration for the existence of a Stupid Coalition in business.  If people who have a preference for macho men disproportionately invest in companies and investment firms run by macho men, they can prop each other up temporarily, but sooner or later these whole clusters of highly correlated bias will experience market crashes. 

Is Stupidity Strength? Part 3: Evolutionary Game Theory

Spite Strategies

Carlo Cipolla defined stupidity as causing harm to others as well as harming oneself, while benefiting nobody.

Another way of looking at this: a stupid decision is one which you could make a Pareto improvement on. A stupid decision means neglecting a win-win opportunity.  

Since people aren't omniscient and omnipotent, and we don't necessarily want to call that stupidity, we can narrow this; a stupid decision is one that avoidably causes harm to self and others.

In the previous post, I mentioned a possible incentive for a coalition of individuals to be stupid -- the "too big to fail" strategy.  If enough people commit to take imprudent risks, all at once, then they can force the prudent people to bail them out when catastrophe eventually comes. In the long term, everyone will be worse off in absolute terms than if the catastrophe had been prudently averted; but the Stupids will be relatively better off than the Prudents.

In evolutionary biology, this is a special case of what's called Hamiltonian spite, after its originator W.D. Hamilton. Imagine a gene that imposes a fitness cost on organisms that bear it, but an even greater fitness cost on members of the same species that do not bear it. This gene might be able to persist in the population, by enabling its bearers to outcompete their neighbors, even though it causes only harm and no benefit to anyone!

Does spite ever happen?  

Many apparently spiteful behaviors in nature are actually selfish; when a male bowerbird destroys the nests of other bowerbirds, his own nest appears more attractive in comparison and he gets more mating opportunities. This is a straightforward case of zero-sum competition, not true spite. 

Hamilton himself thought cases of spite would be vanishingly rare in nature; his own equations show that spiteful strategies are less likely to win, the larger the population size; and since spite strategies diminish absolute fitness (ie the number of offspring), spite-dominated populations will tend to shrink towards extinction.  In his original paper, Hamilton proposed that spite strategies might emerge in small, isolated populations and quickly drive those populations out of existence; we shouldn't expect to see them exist for long.

A more recent paper adds an additional wrinkle, however. Hamilton's original models assumed that populations could be of arbitrary size. But in nature, population sizes are often bounded above by the carrying capacity of the environment -- a given savannah only has enough resources to support so many lions, no matter how fit they are.  If you add a carrying capacity constraint to the equations, you see that spite strategies can persist in the long term, provided the harm to those who don't bear the spite gene is enough larger than the harm to those who do bear it. This critical ratio must be larger, the larger the maximum population size can be; it is easier for spite strategies to survive in environments with smaller carrying capacities.

This fact is suggestive for the question of whether spite strategies could have evolved in humans.  We are a highly K-selected species (compared to other mammals like mice) -- we have large bodies, slow metabolisms, and long lives, developing slowly, reproducing infrequently, and investing a lot of care into our offspring.  This pattern tends to evolve in organisms close to their environment's carrying capacity, such as in predators at the top of the food chain. Vast litters of offspring would do a K-selected mother no good; they would bump into the harsh limitations of the food supply and starve before they had children of their own. She would be better off investing resources into making her few offspring more robust; building them bigger, more long-lasting bodies, with bigger brains more able to adapt their behavior to survive; and guarding and feeding them while young; and, perhaps, sabotaging their competition!  It is in K-selected animals like us that spiteful behaviors have a plausible evolutionary advantage, since populations are stably small; just as it is in oligopolies, not competitive markets, where sabotaging a competitor can be a winning strategy.  

(Of course, the environment in which modern Homo sapiens evolved was the harsh Malthusian context of the Pleistocene; for the past 300 years the human population has exploded exponentially. Perhaps the spite strategies we evolved with are no longer adaptive in a context of improving technology and global trade.)

Likewise, there is a wider range of conditions under which spiteful strategies can persist when competition is more localized, so that only small populations can interact with each other. Global competition punishes lose-lose strategies, since these diminish the absolute fitness of those who carry them and their non-carrier victims; local competition can preserve these strategies in isolated enclaves.

In nature, we see spiteful behavior in the social insects; worker bees, wasps, and ants prevent other workers from reproducing by killing their eggs, and red fire ant workers kill unrelated queen ants. These actions do not provide any direct fitness benefit to the specific workers that do the killing; rather, they provide an indirect benefit to their sisters, the queens, by killing their unrelated rivals. 

It has been hypothesized that primates engage in spiteful behavior; they certainly engage in apparently spiteful behaviors like harassing copulating couples and killing non-kin infants, but there's no consensus I can find as to whether this is true Hamiltonian spite or mere self-interested competition for food and mates.

Spite and rent-seeking

In Tullock's model of rent-seeking, individuals compete to take a winner-take-all prize; each individual decides how much to spend, and the more you spend, relative to all the other individuals, the more likely you are to get a prize.  What's the optimal amount to spend?

There is a unique Nash equilibrium strategy of how much to spend on trying to get the prize; that is, you can't improve your expected net gain by spending any more or any less. However, this is not an evolutionarily stable strategy! Populations that bid the Nash equilibrium will get overtaken by populations that spitefully bid more, at cost to themselves.

The two strategies are rather close, and get closer asymptotically in large populations; the Nash equilibrium bid is (n-1)/n^2 rV (where n is population size, V is the payout value, and r is a shape parameter of the win-probability function), while the ESS bid is rV/n.  Evolutionarily optimal play is slightly more aggressive than individually optimal play, in a large population with many-to-many competition. But in a small population, or in a tournament-like setup where pairs of individuals play one on one and losers get knocked out of the game, this difference is magnified, and of course compounds with time.

Direct resource competition between conspecifics is many-to-many competition; as soon as I eat a bite, it simultaneously becomes unavailable to everyone else.

Fighting between conspecifics, however, is one-to-one competition; only two rams can butt heads at once. 

We should expect to see "overinvestment" in adaptations that increase individuals' abilities to win such head-to-head conflicts (pun intended), relative to the individually "rational" Nash equilibrium amount.  Competing for resources is not in general a spite strategy, because the winner of a conflict does directly benefit; but overinvestment in resource competition can be a spite strategy.  It's net harmful to the individual, in expectation, but it's more net harmful to his opponent.

Spite and intergroup conflict

If we allow different evolutionary strategies to detect each other -- to treat "in-group" members differently from "outgroup" members, as human nations do (as well as other species; ants go to war) we see even more interesting things about the dynamics of spite.

If individuals are assumed to interact only with local neighbors, to migrate around somewhat, but to be able to distinguish kin from non-kin even if migration has occurred, we observe that individuals tend to be altruistic (hurting themselves to help others) towards kin, and spiteful (hurting themselves to hurt others) towards non-kin. 

Moreover, minorities living in non-kin territory tend to be strongly altruistic towards their kin and only mildly spiteful towards the majority; while majorities tend to be only mildly altruistic towards each other and strongly spiteful towards minorities. This seems to match available evidence about human ethnic conflict.

Spite in human experiments

Humans display spiteful behavior in game-theoretic experiments:

Zizzo (2003a) in his paper on burning money experiments reported that subjects are often willing to reduce, at a cost for themselves, the incomes of players who had been given higher endowments. In some instances subjects with the same or less endowment were also targeted. In a similar vein, Dawes, Fowler, Johnson, McElreath and Smirnov (2007) find that subjects are willing to reduce other group members’ income independently of the history of interaction...

In their experiments on competitive behavior, Rustichini and Vostroknutov (2007) find that participants are more inclined to reduce someone else’s income if the punished subject has earned more money than the punisher. Surprisingly, this effect is stronger when the higher incomes of the punished subjects are due to merit rather than luck...
The most extreme form of anti-social punishment, where the punishment is directed against those who had previously behaved nicely towards the punisher, has been observed in public good games with punishment. In these games those who are more cooperative than others are frequently punished. Such evidence is reported in Cinyabuguma, Page and Putterman (2006), Gächter, Herrmann and Thöni (2005) and Herrmann et al. (2008).

In a "rent-seeking game" played with 3500 undergraduates, players significantly "over-spent" on winning relative to the Nash equilibrium; in particular, they spent twice as much when playing against another human vs the computer, which suggests that spite is a social emotion.  Players who defected on the Prisoner's Dilemma game engaged in more spiteful overspending than cooperative players, and players who were more risk-prone in a lottery test were also more prone to overspend. Finally, after engaging in a rent-seeking game, players cooperated significantly less on the Prisoner's Dilemma.

While players of a public good game punished free riders in all cities, in some cities players also engaged in antisocial punishment -- selectively penalizing the most generous contributors. This happened least in Anglophone cities (Boston, Melbourne, Nottingham) and most in Mediterranean, Middle Eastern, or Slavic cities (Muscat, Athens, Riyadh, Samara, Minsk, Istanbul); countries with high scores on social trust and rule of law displayed more "prosocial punishment" of free-riders and less "antisocial punishment" of contributors.

Several hundred Portuguese schoolchildren were assigned to play a spite game, where they could either play cooperatively or spitefully. If both players cooperate, both gain 15 points; if one cooperates and the other spites, the spiteful player gains 11 points (paying a cost) but his opponent only gains 5 points (a greater loss). Finally, if both players spite, they each get 2 points (a severe loss). 

This game can either be played with proportional winnings (each player gets a piece of candy for every 15 points), in which case playing cooperatively is optimal, or with winner-take-all conditions (the player with the most points gets a fancy chocolate), in which case playing spitefully is optimal.

The experiment found that younger children (5th-7th grade) usually played cooperatively, while older children (8th-10th grade) played cooperatively in the proportional-rewards conditions and spitefully in the winner-take-all conditions. Students repeating a grade were much more likely to behave spitefully.  This suggests that spiteful behavior in humans may emerge in the teenage years.

The economic experimental literature is clear that spiteful strategies do exist in humans, that they correlate with social trust and rule of law in the expected (inverse) direction, and that they seem to emerge in adolescence.

Is Stupidity Strength Part 2: Confidence

One very common way people believe stupidity can be a strength is that it can give give greater confidence, which brings advantages.

If you are ignorant of your own flaws, you can perform self-assurance and boldness, which makes it more likely you will win success, especially in social competitive situations. (Getting the girl, getting the raise, winning the election.)

If you are ignorant of the risks of a new venture, you will be more likely to boldly attempt it; and many risky ventures are high in expected value.

If you are ignorant of the weaknesses in your ideas, you will proclaim them confidently and have more influence in society, and more of a sense of joyful certainty, than more reflective, self-critical people.  "The best lack all conviction, while the worst are full of passionate intensity."

Not knowing the flaws in your own character, your own plans, or your own opinions, seems like it might carry an advantage. Even those who think it's morally unacceptable to engage in self-serving delusion often think that the deludedly confident obtain selfish gain from their stupidity. After all, look what it got Adam Neumann -- a CEO so brashly incompetent and unscrupulous that he was recently paid over a billion dollars to leave his company.

But what is this "confidence", why is it good, and why can't you get it without self-delusion?

Confidence Is Willingness To Act

William James, in his "The Will to Believe", was obsessed with the question of whether it could be acceptable to choose a belief, for which you had no evidence, if it made you more decisive and better at functioning in life. 

This was a practical issue for James, as he was plagued with pathological indecisiveness and self-doubt all his life, as Louis Menand's wonderful group biography of the Pragmatists recounts. James spent 15 years deciding on a profession; he was speaking of himself when he said "There is no more miserable human being than one in whom nothing is habitual but indecision."

For James, the critical issue for decisive confidence was faith in God. He thought there was no adequate evidence for either believing or disbelieving in God, but that without religious faith, nobody could have the confidence to engage in a life of action or purpose. We would languish in passive despair, sure that our lives had no meaning. 

James defended the choice to believe because he thought the very nature of "belief" or "truth" is rooted in its function as an aid to decision. We are living creatures; we only evolved the capacity to apprehend the world because knowledge helps us make more survival-promoting decisions; a "belief" that doesn't cash out to anticipated experiences that matter to the holder of the belief, is in a sense not a belief at all, but an empty string of syllables he parrots. 

Therefore, a belief in a ground of meaningfulness or worthwhileness in the universe, a belief that anything at all is worth doing, is by the above decision-theoretic standard not only true, but the necessary foundation of all true beliefs.  And this, says James, is essentially what it means to believe in God. 

He's very carefully not saying that you may believe anything that makes you feel better, even if it's false; he's saying that the "belief" that it ever does any good to act is actually true, by the only reasonable and non-circular definition of truth he can come up with.

"A man's religious faith (whatever more special items of doctrine it may involve) means for me essentially his faith in the existence of an unseen order of some kind in which the riddles of the natural order may be found explained...
"Our only way, for example, of doubting, or refusing to believe, that a certain thing is, is continuing to act as if it were not. If, for instance, I refuse to believe that the room is getting cold, I leave the windows open and light no fire just as if it still were warm. If I doubt that you are worthy of my confidence, I keep you uninformed of all my secrets just as if you were unworthy of the same. If I doubt the need of insuring my house, I leave it uninsured as much as if I believed there were no need. And so if I must not believe that the world is divine, I can only express that refusal by declining ever to act distinctively as if it were so...
"So far as man stands for anything, and is productive or originative at all, his entire vital function may be said to have to deal with maybes. Not a victory is gained, not a deed of faithfulness or courage is done, except upon a maybe; not a service, not a sally of generosity, not a scientific exploration or experiment or text-book, that may not be a mistake. It is only by risking our persons from one hour to another that we live at all. And often enough our faith beforehand in an uncertified result is the only thing that makes the result come true. Suppose, for instance, that you are climbing a mountain, and have worked yourself into a position from which the only escape is by a terrible leap. Have faith that you can successfully make it, and your feet are nerved to its accomplishment. But mistrust yourself, and think of all the sweet things you have heard the scientists say of maybes, and you will hesitate so long that, at last, all unstrung and trembling, and launching yourself in a moment of despair, you roll in the abyss. In such a case (and it belongs to an enormous class), the part of wisdom as well as of courage is to believe what is in the line of your needs, for only by such belief is the need fulfilled. Refuse to believe, and you shall indeed be right, for you shall irretrievably perish. But believe, and again you shall be right, for you shall save yourself. You make one or the other of two possible universes true by your trust or mistrust,—both universes having been only maybes, in this particular, before you contributed your act.

Now, it appears to me that the question whether life is worth living is subject to conditions logically much like these. It does, indeed, depend on you the liver. If you surrender to the nightmare view and crown the evil edifice by your own suicide, you have indeed made a picture totally black. Pessimism, completed by your act, is true beyond a doubt, so far as your world goes. Your mistrust of life has removed whatever worth your own enduring existence might have given to it; and now, throughout the whole sphere of possible influence of that existence, the mistrust has proved itself to have had divining power. But suppose, on the other hand, that instead of giving way to the nightmare view you cling to it that this world is not the ultimatum. Suppose you find yourself a very well-spring, as Wordsworth says, of—

"Zeal, and the virtue to exist by faith

As soldiers live by courage; as, by strength

Of heart, the sailor fights with roaring seas."

Suppose, however thickly evils crowd upon you, that your unconquerable subjectivity proves to be their match, and that you find a more wonderful joy than any passive pleasure can bring in trusting ever in the larger whole. Have you not now made life worth living on these terms? 

Courage, here, is the willingness to act under uncertainty, the willingness to live at all rather than committing suicide or passively waiting out your years hoping for death.

Faith, to James, is simply the conviction that something you have not yet seen will someday resolve your uncertainties; that the universe makes sense and your life matters, even if the reasons are outside the frame of your current knowledge. This faith is the difference between seeing a life of hardships as a determined struggle rather than an inescapable hell; it is the difference between seeing your problems and questions as ultimately resolvable and seeing the universe as a perverse, absurd, inherently unintelligible chaos, at every level fractally resisting your comprehension.  You cannot prove you don't live in such a universe; but your ability to live, act, and learn, to obtain any good things in life, to have anything beyond depressive nihilism, depends on your believing the opposite.

In a more secular age, you might call this "faith" simply the belief in an intelligible universe in which survival is possible. But even traditional theologies often makes sense if you translate "God" to mean "the universe, which is singular, and which exists even outside the frame of our perception and all our mental models." Witness all the prayers and holy texts that say that following God's teachings will help us flourish and make our descendants prosper and multiply; this is simply the claim that understanding the laws of Nature (and the decision-theoretic laws of ethics, or the social/psychological foundations of good societies) is to our long-run best interest.  What is "I Am that I Am" but a poetic way of expressing the notion of existence itself, the Universe, the world "out there" that our words and guesses ultimately refer to?

The "faith" or stance that there is one universe, which is ultimately intelligible and habitable, even if we can't see how at the moment, is also held to be important by scientific atheist philosophers like David Deutsch, who calls it the conviction that "problems are solvable". Without a stance of optimism that coherent explanations are possible, no science could actually be done; nobody would ever search for an explanation for the brute facts they observe.

The stance that life matters and that you personally are overall capable of handling life and worthy to make your own decisions is called "self-esteem" in psychology. One can improve it -- and thereby improve performance on a variety of practical tasks -- by writing personal essays about what one values in life.  (This is the original, older meaning of self-esteem, before it became redefined as "agreeing with positive statements about oneself", which doesn't correlate with work or school performance, improved mental health, or suchlike practical successes. Exercises in which you praise yourself don't work; exercises in which you think about your values and priorities do. )  

The "faith" that the universe makes sense and that it's worthwhile to live actively, making plans and decisions, is one of the key things that is destroyed in PTSD. 

This is not a loss of "confidence" or "trust" in any particular thing, which might well be rational after a traumatic experience (after being raped it is rational to have less trust in your rapist or in people similar to him), but a loss of the ability to have self-confidence generally or to trust in anything generally.  The idea of a generalized "loss of confidence" can't be interpreted as an epistemic belief; it's a change in stance, a change in the ground of all belief or action.

Jenny Holzer's art really captures this aspect of the traumatized experience:

This article investigates the philosophical interpretation of the generalized loss of trust, confidence, or meaning that occur after trauma.

The Istanbul Protocol, a United Nations guide to documenting cases of torture, claims that torture survivors lose the will to look forward to, or shape, their own future.  "The victim has a subjective feeling of having been irreparably damaged and having undergone an irreversible personality change. He or she has a sense of foreshortened future without expectation of a career, marriage, children, or normal lifespan."

In PTSD, "we experience a fundamental assault on our right to live, on our personal sense of worth, and further, on our sense that the world (including people) basically supports human life. Our relationship with existence itself is shattered. Existence in this sense includes all the meaning structures that tell us we are a valued and viable part of the fabric of life..."

What, exactly, does this “shattering” involve? It could be that experiencing significant suffering at the hands of another person leads to a negation of engrained beliefs such as “people do not hurt each other for the sake of causing pain,” “people will help me if I am suffering,” and so on. Then again, through our constant exposure to news stories and other sources, most of us are well aware that people seriously harm each other in all manner of ways. One option is to maintain that we do not truly “believe” such things until we endure them ourselves, and various references to loss of trust as the overturning of deeply held “assumptions” lend themselves to that view. For example, Herman (1992/1997, p. 51) states that “traumatic events destroy the victim’s fundamental assumptions about the safety of the world,” and Brison (2002, p. 26) describes how interpersonal trauma “undermined my most fundamental assumptions about the world.” An explicitly cognitive approach, which construes these assumptions as “cognitive schemas” or fundamental beliefs, is adopted by Janoff-Bulman (1992, pp. 5–6), who identifies three such beliefs as central to one-place trust: “the world is benevolent;” “the world is meaningful;” and “the self is worthy.”


Many of us anticipate most things with habitual confidence. It does not occur to us that we will be deliberately struck by a car as we walk to the shop to buy milk or that we will be assaulted by the stranger we sit next to on a train. There is a sense of security so engrained that we are oblivious to it. Indeed, the more at home we are in the world, the less aware we are that “feeling at home in the world” is even part of our experience (Baier, 1986Bernstein, 2011). It is not itself an object of experience but something that operates as a backdrop to our perceiving that p, thinking that q or acting in order to achieve r. To lose it is not just to endorse one set of evaluative judgments over another. It is more akin to losses of practical confidence that all of us feel on occasion, in relation to one or another performance. Suppose, for instance, one starts to “feel” that one can no longer teach well. Granted, evaluative judgments have a role to play, but loss of confidence need not originate in explicit judgments about one’s performance, and its nature is not exhausted by however many judgments. The lecture theater looks somehow different – daunting, oppressive, unpredictable, uncontrollable. Along with this, one’s actions lack their more usual fluidity and one’s words their spontaneity. The experience is centrally one of feeling unable to engage in a habitual, practical performance. And loss of confidence can remain resistant to change even when one explicitly endorses propositions such as “I am a good teacher.”
Such an experience can be fairly circumscribed, relating primarily to certain situations. However, we suggest that human experience also has a more enveloping “overall style” of anticipation. This view is developed in some depth by the phenomenologist Husserl (1991). According to Husserl, all of our experiences and activities incorporate anticipation. He uses the term “protention” to refer to an anticipatory structure that is integral to our sense of the present.
The 19th-century philosopher Edmund Husserl, much like contemporary neuroscientists, believed there is no perception without anticipation; all sensory perceptions and indeed all motor actions involve hypotheses about what we will observe next, or what will happen if we do this or that.  The basic function of the brain is to form predictions and measure how and in what way they differ from our subsequent observations.  There is no level at which our senses provide us with an unmediated, judgment-free snapshot of reality; it's prediction and error-correction all the way down. 

Loss of trust in our ability to make correct predictions thus means a generalized weakness in our ability to perceive, think, and act.  It is loss of trust in the intelligibility of the universe and in our own ability to act to achieve goals; it is loss of trust that the future can be predicted, and thus that there's any point in planning or investing in the future. It is overall a loss of meaningfulness, a loss of the sense that anything has a point, a loss of will to act, a loss of confidence.  In other words, the problem caused by trauma is exactly the problem that confronted William James.

It's a common observation that the risk of PTSD is not predicted so much by the severity of the trauma as by the degree to which the victim is persuaded to deny her own experience; pressured (by abusers or bystanders) to believe that it didn't really happen, that it wasn't so bad, or that she deserved it. It's not surprising that this particular experience is damaging to one's trust in one's own ability to make sense of reality or rationally assess risk to oneself.

Confidence Without Self-Delusion

The above model of how confidence works makes it clear that we don't have to be stupid or delusional to get most of the benefits of high confidence.  

Confidence is not a belief, in the ordinary sense.  It is not the belief that you are beautiful or brilliant or that your plans will work or that your ideas are right.  It is a stance of willingness to act, decisively and uninhibitedly. You can make a choice to act, without changing your assessment of any hypothesis; in machine-learning terms, confidence is a hyperparameter, an error threshold for "enough certainty" required before taking action or asserting a conviction, which you can lower if it is too high.

Eliezer Yudkowsky has remarked that he often thinks projects are worth trying on net despite only having, in his estimate, a 10% probability of success; while other people, in order to be motivated to try at all, need to psych themselves up into the unrealistically "confident" belief that success is virtually certain.  Most people conflate self-esteem or global self-confidence or courage, the willingness to try, with over-optimism about one's chances; but this is a needless error.

The need for external "validation" of one's basic worth as a person is likewise an error of looking for evidence of one's worthiness, when what you really want is permission to act as you desire; or, one might cash this out as a decision to act as you desire.  Repeatedly looking for validation, when you aren't really seeking new information, because you know what answer you expect and want to get, isn't going to work, because data only conveys information (in the Shannon sense) if it's surprising.  You can't come to "believe in yourself" by spamming your brain with the same data over and over. But if you know you want more self-confidence, you already have all the data you need to know more confidence would be good for you. You don't need to seek any more reassurance; you need to unilaterallly change your stance to a decisive one.

Easier said than done! But here's some tactics that have worked for me:

1.) Writing about my values! It's the time-honored, evidence-based trick for increasing self-esteem, and it works for me.  (Yes, this blog post is itself an example.)

2.) Unilaterally doing something I feel like doing in the moment. (Usually a bodily craving like food or exercise, or a minor breach of social propriety like making ugly faces or shouting in my own home.)  

If I'm wrapped up in an anxious obsession with being liked or validated or given approval, I can break that cycle by proving to myself that I have "permission" to do whatever I feel like, except for a really sparse set of ethical and practical constraints that I'm truly committed to. I don't have to be good, in the sense of an identity or "personal brand"; there is what I impulsively feel like doing, there is what I really absolutely must do, and that's all. 

(I usually fast, as is traditional, on the Jewish holiday of Yom Kippur, the Day of Atonement; but this year I actually got a lot of mileage and dare-I-say spiritual growth out of breaking the rule and eating food, when I was falling into an unhealthy spiral of shame and resentment about the idea of "being good," and becoming unpleasant to my family due to hunger.  Eating made me a better mom and wife that day, and the insight catalyzed me being a better friend to my friends in the following few days. Real ethics isn't about being any particular way, in the sense of an aesthetic or persona; that's fake "ethics," which is advertising. If there's anything you actually have to do, in reality rather than in a performative sense, then it will have a function ascertainable through ordinary cause and effect.  The goal of real ethics is not to maintain a goody-two-shoes persona but to exert agency towards good outcomes.  Violating a taboo, on an occasion when the taboo-violation directly helps someone and doesn't break any principle you're truly serious about, can help concretize this to yourself. )

False Confidence As Fraud

There's another kind of benefit self-deluded confidence can have, however, that courage and decisiveness by themselves cannot match; it can be part of a coalitional Stupid Strategy, as mentioned in the previous post. False beliefs are a luxury, an ornament, a costly signal that you are in a secure enough social position that you do not need to be realistic; if you fail, someone else will bail you out.

There is a common phenomenon that "mediocre white men" are given advantages for being unrealistically overconfident, while more-competent, humbler, more serious people who have less privilege (women, upwardly-mobile lower-class people, foreigners and immigrants, especially East Asians today and Jews historically) are seen as less appealing, less "likable", dispreferred as recipients of resources and privileges.  

Part of this is simply that the "overconfident" privileged people are acting on the correct amount of ambition for optimal outcomes, and others would do well to emulate their confidence. We should apply to more things, speak up more, negotiate more for ourselves, try more new things.

Another part of it is that having more resources makes it rational to take more risks; if you have savings or an inheritance, it actually is less risky to start a business. People born rich are free to be bolder; that's part of what wealth means. That's an argument that more people should have access to enough wealth to enable them to take useful calculated risks, but not that there's anything wrong with taking advantage of your good fortune, should you happen to have it.

But a third, perverse possible component of the "overconfidence of the privileged" is that they are signaling their ability to be wrong so they can align in a "too big to fail" coalition that is parasitic on the more-productive, less-grandiose people's work. For this purpose, it isn't enough to just be ambitious, bold, or confident; you have to be shamelessly wrong, to prove your membership in the Stupid Coalition of those privileged to be "secure" in their entitlement to valuable resources that other people produce.  Wrongness -- particularly in the form of excess confidence, where you make bets that would be disastrous in expectation for yourself unless someone else bailed you out -- is an unfakeable signal that you are sure other people will bail you out.  It's a form of playing Chicken with the (social) universe.

Like the tail of the peacock, irrational overconfidence is a self-imposed handicap; it's a gloriously flamboyant waste of resources, as a way of proving its bearer has resources to burn.

To the extent that this is true, we ought to see supernormal returns from investing in individuals who have the same apparent level of performance (in profits, product quality metrics, test scores, whatever) but are a.) from less-privileged backgrounds (women, minorities, LGBT individuals, people from working-class families) or b.) who have a manner that's more serious, modest, down-to-earth, and less entitled or grandiose. There's actually some evidence to that effect; women-led firms have more than twice the average annual rate of return of companies worldwide (24% vs. 11%).

The logic is, someone who's performing at the top, but is "spending" less than her equally high-performing peers on wasteful display signaling, is a much better bet. Your dollar goes farther, in the long run, if you aren't spending half of it on peacock tails.

An actual peacock bears the weight of its tail with its own strong muscles. But the Stupid Coalition's "peacock tail" is supported by the too-big-to-fail dynamics that rely on someone outside the coalition bailing them out.  If you are confident you can find a "greater fool" to enter your Ponzi scheme, or that the use of force will ensure payment of your unsustainable debts (e.g. the government printing more money to continue funding your project, or a Saudi sovereign-wealth fund backed ultimately by violence will invest in the next round), then peacock tails can be a good investment -- if you think the bubble, or Ponzi scheme, or public trust in government, will hold.  If there's enough risk the whole system will crash, "too big to fail" or not, then peacock tails are a terrible investment and you'll do much better optimizing for long-run, resource-efficient value creation.