I am a researcher at the Happier Lives Institute. In my work, I assess the cost-effectiveness of interventions in terms of subjective wellbeing.
JoelMcGuire
I agree that the agency of newer NATO members (or Ukraine) has been neglected. Still, I don’t think this was a primary driver of underestimating Ukraine’s chances—unless I’m missing what “agency” means here.
I assume predictions were dim about Ukraine’s chances at the beginning of the war primarily because Russia and the West had done an excellent job of convincing us that Russia’s military was highly capable. E.g., I was disconcerted by the awe/dread with which my family members in the US Army spoke about Russian technical capabilities across multiple domains.
That said, I think some of these predictions came from a sense that Ukraine would just “give up”. In which case, missing the agency factor was a mistake.
What’s the track record of secular eschatology?
A recent SSC blog post depicts a dialogue about Eugenics. This raised the question: how has the track record been for a community of reasonable people to identify the risks of previous catastrophes?
As noted in the post, at different times:
Many people were concerned about overpopulation posing an existential threat (c.f. population bomb, discussed at length in Wizard and The Prophet). It now seems widely accepted that the risk overpopulation posed was overblown. But this depends on how contingent the green revolution was. If there wasn’t a Norman Borlaug, would someone else have tried a little bit harder than others to find more productive cultivars of wheat?
Historically, there also appeared to be more worry about the perceived threat posed by a potential decline in population IQ. This flowed from the reasonable-sounding argument “Smart people seem to have fewer kids than their less intellectually endowed peers. Extrapolate this over many generations, and we have an idiocracy that at best will be marooned on earth or at worst will no longer be capable of complex civilization.” I don’t hear these concerns much these days (an exception being a recent Clearer Thinking podcast episode). I assume the dismissal would sound something like “A. Flynn effect.[1] B. If this exists, it will take a long time to bite into technological progress. And by the time it does pose a threat, we should have more elegant ways of increasing IQ than selective breeding. Or C. Technological progress may depend more on total population size than average IQ since we need a few Von Neumann’s instead of hordes of B-grade thinkers.”
I think many EAs would characterize global warming as tentatively in the same class: “We weren’t worried enough when action would have been high leverage, but now we’re relatively too worried because we seem to be making good progress (see the decline in solar cost), and we should predict this progress to continue.”
There have also been concerns about the catastrophic consequences of: A. Depletion of key resources such as water, fertilizer, oil, etc. B. Ecological collapse. C. Nanotechnology(???). These concerns are also considered overblown in the EA community relative to the preoccupation with AI and engineered pathogens.
Would communism’s prediction about an inevitable collapse of capitalism count? I don’t know harmful this would have been considered in the short run since most attention was about the utopia this would afford.
Most of the examples I’ve come up with seem to make me lean towards the view that “these past fears were overblown because they consistently discount the likelihood that someone will fix the problem in ways we can’t yet imagine.”
But I’d be curious to know if someone has examples or interpretations that lean more towards “We were right to worry! And in hindsight, these issues received about the right amount of resources. Heck they should have got more!”
What would an ideal EA have done if teleported back in time and mindwiped of foresight when these issues were discovered? If reasonable people acted in folly then, and EAs would have acted in folly as well, what does that mean for our priors?
- ^
I can’t find an OWID page on this, despite google image searches making it apparent it once existed. Might not have fed the right conversations to have allowed people to compare IQs across countries?
While there are some Metaculus questions that ask for predictions of the actual risk, the ones I selected are all conditional of the form, “If a global catastrophe occurs, will it be due X”. So they should be more comparable to the RP question “Which of the following do you think is most likely to cause human extinction?”
I know this wasn’t the goal, but this was the first time I’d seen general polls of how people rank existential risks, and I’m struck by how much the public differs from Rationalists / EAs (using Metaculus and Toby as a proxy). [1]
Risk Public (RP) Metaculus Difference Nukes 42% 31% -11% Climate 27% 7% -20% Asteroid 9%[2] ~0% (Toby Ord) -9% Pandemic 8% Natural: 14%, Eng: 28% 6- 20% AI 4% 46% 42%
In general, i agree politeness doesn’t require that — but id encourage following up in case something got lost in junk if the critique could be quite damaging to its subject.
In case it’s not obvious, the importance of previewing a critique also depends on the nature of the critique and the relative position of the critic and the critiqued. I think those possibly “Punching down” should be more generous and careful than those “punching up”.
The same goes for the implications of the critique “if true”, whether it’s picking nits or questioning whether the organisation is causing net harm.
That said, I think these considerations only make a difference between waiting one or two weeks for a response and sending one versus several emails to a couple of people if there’s no response the first time.
Hi Alex, I’m heartened to see GiveWell engage with and update based on our previous work!
[Edited to expand on takeaway]
My overall impression is:
This update clearly improves GiveWell’s deworming analysis.
Each % point change in deworming cost-effectiveness could affect where hundreds of thousands of dollars are allocated. So getting it right seems important.
More work building an empirical prior seems likely to change the estimated decay of income effects and thus deworming’s cost-effectiveness, although it’s unclear what direction.
Further progress appears easy to make.
This work doesn’t update HLI’s view of deworming much because:
We primarily focus on subjective wellbeing as an outcome, which deworming doesn’t appear to affect in the long run.
The long-term income effects of deworming remain uncertain.
In either case, analysing deworming’s long-term effects still relies on a judgement-driven analysis of a single (well-done) but noisy study.
[Note: I threw this comment together rather quickly, but I wanted to get something out there quickly that gave my approximate views.]
1. There are several things I like about this update:
In several ways, it clarifies GiveWell’s analysis of deworming.
It succinctly explains where many of the numbers come from.
It clarifies the importance of explicit subjective assumptions (they seem pretty important).
It lays out the evidence it uses to build its prior in a manner that’s pretty easy to follow.
Helpfully, it lists the sources and reasons for the studies not included.
2. There are a few things that I think could be a bit clearer:
The decay rate from the raw (unadjusted) data is 13% yearly.
Assuming the same starting value as GiveWell, using this decay rate would lead to a total present value of 0.06 log-income units, compared to 0.09 for their “3% decay” model and 0.11 for their “no-decay” model.
Different decay rates imply very different discounts relative to the “no-decay” baseline / prior, 13% decay→ 49% discount. 3% → 19% discount.
They arrive at a decay rate of 3% instead of 13% because they subjectively discount the effect size from earlier time points more, which reduces the decay rate to 3%. While some of their justifications seem quite plausible[1] -- after some light spreadsheet crawling, I’m still confused about what’s happening underneath the hood here.
The 10% decrease in effectiveness comes because they assign 50% of the weight to their prior that there’s no decay and 50% to their estimate of a 3% decay rate. So whether the overall adjustment is 0% or 50% depends primarily on two factors:
How much to subjectively (unclear if this has an empirical element) discount each follow-up.
How much weight should be assigned to the prior for deworming’s time-trajectory, which they inform with a literature review.
All this being said, I think this update is a big improvement to the clarity of GiveWell’s deworming analysis.
My next two comments are related to some limitations of this update that Alex acknowledges:
It’s possible we’ve missed some relevant studies altogether.
We have not tried to formally combine these to get point estimates over time or attempted to weight studies based on relevance, study quality, etc.
We are combining studies that may have little ability to inform what we’d expect from deworming (twin studies, childcare programs, etc.).
It could be possible to re-assess other studies measuring long-term benefits of early childhood health interventions. When we set our prior, we excluded studies that did not report separate effects on income at different time periods. We guess that for several of these studies, it would be possible to re-analyze the primary data and create estimates of the effect on income at different time periods.
3. After briefly looking over the literature review GiveWell uses to build a prior on the long-term effects of deworming, it seems like further research would lead to different results.
GiveWell takes a “vote counting” approach where the studies are weighted equally[2]. But I would be very surprised if further research assigned equal weight to these studies because they appear to vary considerably in relevance, sample size, and quality.
Deworming analogies include preschool, schooling, low birth weight, early childhood stimulation, pollution, twin height differences, and nutritional school lunches. It’s unclear how relevant these are to deworming because the mechanisms for deworming to benefit income seem poorly understood.
Sample sizes aren’t noted. This could matter as one of the “pro-growth trajectory” studies, Gertler et al. (2021) have a follow-up sample size of around ~50. That seems unusually small, so it’s unclear how much weight that should receive relative to others. However, it is one of the only studies in an LMIC!
There are also two observational studies, which typically receive less weight than quasi-experimental trials or RCTs (Case et al. 2005, Currie and Hyson 1999).
4. Progress towards building a firmer prior seems straightforward. Is GiveWell planning on refining its prior for deworming’s trajectory? Or incentivizing more research on this topic, e.g., via a prize or a bounty? Here are some reasons why I think further progress may not be difficult:
The literature review seems like it could be somewhat easily expanded:
It seems plausible that you could use Liu and Liu (2019), another causal study of deworming’s long-term effects on income, to see if the long-term effects change depending on age. They were helpful when we asked them for assistance.
Somewhat at random, I looked at Duflo et al. (2021), which was passed over for inclusion in the review and found that it contained multiple follow-ups and found weak evidence for incomes increasing over time due to additional education.
The existing literature review on priors could be upgraded to a meta-analysis with time (data extraction is more tedious than technically challenging). A resulting meta-analysis where each study is weighted by precision and potentially a subjective assessment of relevance would be more clarifying than the present “vote counting” method.
It’s unclear if all the conclusions were warranted. GiveWell reads Lang and Nystedt (2018) as finding “Increases for males; mixed for females” and notes some quotes from the original study:
“From ages 30–34 and onwards, the height premium increases over the life cycle for men, starting at approximately 5%, reaching 10% at ages 45-64 and approximately 11-12% at ages 65-79 (i.e., in retirement).” [...] “Almost the opposite trend is found for women. Being one decimeter taller is associated with over 11% higher earnings for women aged 25–29. As the women age, the height premium decreases and levels off at approximately 6–7%.” [...] “The path of the height premium profile over the female adult life cycle is quite unstable, and no obvious trend can be seen (see Fig. 2).” (17-18)
But when I look up that same table (shown below), I see decay for women and growth for men.
- ^
Higher ln earnings effects from KLPS-2 to KLPS-3 are driven by lower control group earnings in KLPS-2 ($330 vs. $1165).[8] In KLPS-3, researchers started measuring farming profits in addition to other forms of earnings,[9]so part of the apparent increase in control group earnings from KLPS-2 to KLPS-3 is likely driven by a change in measurement, not real standards of living or catch-up growth.”
- ^
“We found 10 longitudinal studies with at least two adult follow-ups from a number of countries examining the impact of a range of childhood interventions or conditions (see this table), in addition to the deworming study (Hamory et al. 2021). Of those 10 studies, 3 found decreasing effects on income, 3 found increasing effects, and 4 found mixed effects (either similar effects across time periods, different patterns across males and females, or increases and then decreases over the life cycle). Based on this, we think it makes sense to continue to assume as a prior that income effects would be constant over time. I have low confidence in these estimates, though, and it’s possible further work could lead to a different conclusion.”
Hi John, it’s truly a delight to see someone visually illustrate our work better than we do. Great work!
Great piece. Short and sweet.
Given the stratospheric karma this post has reached, and the ensuing likelihood it becomes a referenced classic, I thought it’d be a good time to descend to some pedantry.
“Scope sensitivity” as a phrase doesn’t click with me. For some reason, it bounces off my brain. Please let me know if I seem alone in this regard. What scope are we sensitive to? The scope of impact? Also some of the related slogans “shut up and multiply” and “cause neutral” aren’t much clearer. “Shut up and multiply” which seems slightly offputting / crass as a phrase stripped of context, gives no hint at what we’re multiplying[1]. “Cause neutral” without elaboration, seems objectionable. We shouldn’t be neutral about causes! We should prefer the ones that do the most good! They both require extra context and elaboration. If this is something that is used to introduce EA, which now seems likelier, I think this section confuses a bit. A good slogan should have a clear, and difficult to misinterpret meaning that requires little elaboration. “Radical compassion / empathy” does a good job of this. “Scout mindset” is slightly more in-groupy, but I don’t think newbies would be surprised that thinking like a scout involves careful exploration of ideas and emphasizes the importance of reporting the truth of what you find.
Some alternatives to “scope sensitivity” are:
“Follow the numbers” / “crunch the numbers”: we don’t quite primarily “follow the data / evidence” anymore, but we certainly try to follow the numbers.
“More is better” / “More-imization” okay, this is a bit silly, but I assume that Peter was intentionally avoiding saying something like “Maximization mindset” which is more intuitive than “scope sensitivity”, but has probably fallen a bit out of vogue. We think that doing more good for the same cost is always better.
“Cost-effectiveness guided” while it sounds technocratic, that’s kind of the point. Ultimately it all comes back to cost-effectiveness. Why not say so?
- ^
If I knew nothing else, I’d guess it’s a suggestion of the profound implications of viewing probabilities as dependent (multiplicative) instead of dependent (addictive) and, consequently, support for complex systems approaches /GEM modelling instead of reductive OLSing with sparse interaction terms. /Joke
Jason,
You raise a fair point. One we’ve been discussing internally. Given the recent and expected adjustments to StrongMinds, it seems reasonable to update and clarify our position on AMF to say something like, “Under more views, AMF is better than or on par with StrongMinds. Note that currently, under our model, when AMF is better than StrongMinds, it isn’t wildly better.” Of course, while predicting how future research will pan out is tricky, we’d aim to be more specific.
A high neutral point implies that many people in developing countries believe their lives are not worth living.
This isn’t necessarily the case. I assume that if people described their lives as having negative wellbeing, this wouldn’t imply they thought their life was not worth continuing.
People can have negative wellbeing and still want to live for the sake of others or causes greater than themselves.
Life satisfaction appears to be increasing over time in low income countries. I think this progress is such that many people who may have negative wellbeing at present, will not have negative wellbeing their whole lives.
Edit: To expand a little, for these reasons, as well as the very reasonable drive to survive (regardless of wellbeing), I find it difficult to interpret revealed preferences and it’s unclear they’re a bastion of clarity in this confusing debate.
Anectdotally, I’ve clearly had periods of negative wellbeing before (sometimes starkly), but never wanted to die during those periods. If I knew that such periods were permanent, I’d probably think it was good for me to not-exist, but I’d still hesitate to say I’d prefer to not-exist, because I don’t just care about my wellbeing. As Tyrion said “Death is so final, and life is so full of possibilities.”
I think these difficulties should highlight that the difficulties here aren’t just localized to this area of the topic.
2. I don’t think 38% is a defensible estimate for spillovers, which puts me closer to GiveWell’s estimate of StrongMinds than HLI’s estimate of StrongMinds.
I wrote this critique of your estimate that household spillovers was 52%. That critique had three parts. The third part was an error, which you corrected and brought the answer down to 38%. But I think the first two are actually more important: you’re deriving a general household spillover effect from studies specifically designed to help household members, which would lead to an overestimate.
I thought you agreed with that from your response here, so I’m confused as to why you’re still defending 38%. Flagging that I’m not saying the studies themselves are weak (though it’s true that they’re not very highly powered). I’m saying they’re estimating a different thing from what you’re trying to estimate, and there are good reasons to think the thing they’re trying to estimate is higher. So I think your estimate should be lower.
I could have been clearer, the 38% is a placeholder while I do the Barker et al. 2022 analysis. You did update me about the previous studies’ relevance. My arguments are less supporting the 38% figure—which I expect to update with more data and more about explaining why I think that I have a higher prior for household spillovers from psychotherapy than you and Alex seem to. But really, the hope is that we can soon be discussing more and better evidence.
My intuition, which is shared by many, is that the badness of a child’s death is not merely due to the grief of those around them. Thus the question should not be comparing just the counterfactual grief of losing a very young child VS an [older adult], but also “lost wellbeing” from living a net-positive-wellbeing life in expectation.
I didn’t mean to imply that the badness of a child’s death is just due to grief. As I said in my main comment, I place substantial credence (2/3rds) in the view that death’s badness is the wellbeing lost. Again, this my view not HLIs.
The 13 WELLBY figure is the household effect of a single person being treated by StrongMinds. But that uses the uncorrected household spillover (53% spillover rate). With the correction (38% spillover) it’d be 10.5 WELLBYs (3.7 WELLBYs for recipient + 6.8 for household).
GiveWell arrives at the figure of 80% because they take a year of life as valued at 4.55 WELLBYs = 4.95 − 0.5 according to their preferred neutral point, and StrongMinds benefit ,according to HLI, to the direct recipient is 3.77 WELLBYs --> 3.77 / 4.55 = ~80%. I’m not sure where the 40% figure comes from.
To be clear on what the numbers are: we estimate that group psychotherapy has an effect of 10.5 WELLBYs on the recipient’s household, and that the death of a child in a LIC has a −7.3 WELLBY effect on the bereaved household. But the estimate for grief was very shallow. The report this estimate came from was not focused on making a cost-effectiveness estimate of saving a life (with AMF). Again, I know this sounds weasel-y, but we haven’t yet formed a view on the goodness of saving a life so I can’t say how much group therapy HLI thinks is preferable averting the death of a child.
That being said, I’ll explain why this comparison, as it stands, doesn’t immediately strike me as absurd. Grief has an odd counterfactual. We can only extend lives. People who’re saved will still die and the people who love them will still grieve. The question is how much worse the total grief is for a very young child (the typical beneficiary of e.g., AMF) than the grief for the adolescent, or a young adult, or an adult, or elder they’d become [1]-- all multiplied by mortality risk at those ages.
So is psychotherapy better than the counterfactual grief averted? Again, I’m not sure because the grief estimates are quite shallow, but the comparison seems less absurd to me when I hold the counterfactual in mind.
- ^
I assume people, who are not very young children, also have larger social networks and that this could also play into the counterfactual (e.g., non-children may be grieved for by more people who forged deeper bonds). But I’m not sure how much to make of this point.
- ^
I’d point to the literature on time lagged correlations between household members emotional states that I quickly summarised in the last installment of the household spillover discussion. I think it implies a household spillover of 20%. But I don’t know if this type of data should over- or -underestimate the spillover ratio relative to what we’d find in RCTs. I know I’m being really slippery about this, but the Barker et al. analysis stuff so far makes me think it’s larger than that.
I find nothing objectionable in that characterization. And if we only had these three studies to guide us then I’d concede that a discount of some size seems warranted. But we also have A. our priors. And B. some new evidence from Barker et al. Both of point me away from very small spillovers, but again I’m still very unsure. I think I’ll have clearer views once I’m done analyzing the Barker et al. results and have had someone, ideally Nathanial Barker, check my work.
[Edit: Michael edited to add: “It’s not clear any specific number away from 0 could be justified.”] Well not-zero certainly seems more justifiable than zero. Zero spillovers implies that emotional empathy doesn’t exist, which is an odd claim.
Joel’s response
[Michael’s response below provides a shorter, less-technical explanation.]
Summary
Alex’s post has two parts. First, what is the estimated impact of StrongMinds in terms of WELLBYs? Second, how cost-effective is StrongMinds compared to the Against Malaria Foundation (AMF)? I briefly present my conclusions to both in turn. More detail about each point is presented in Sections 1 and 2 of this comment.
The cost-effectiveness of StrongMinds
GiveWell estimates that StrongMinds generates 1.8 WELLBYs per treatment (17 WELLBYs per $1000, or 2.3x GiveDirectly[1]). Our most recent estimate[2] is 10.5 WELLBYs per treatment (62 WELLBYs per $1000, or 7.5x GiveDirectly) . This represents a 83% discount (an 8.7 WELLBYs gap)[3] to StrongMinds effectiveness[4]. These discounts, while sometimes informed by empirical evidence, are primarily subjective in nature. Below I present the discounts, and our response to them, in more detail.
Figure 1: Description of GiveWell’s discounts on StrongMinds’ effect, and their source
Notes: The graph shows the factors that make up the 8.7 WELLBY discount.
Table 1: Disagreements on StrongMinds per treatment effect (10.5 vs. 1.8 WELLBYs) and cost
Note: HLI estimates StrongMinds has an effect of 1.8 WELLBYs per household of recipient. HLI estimates that this figure is 10.5. This represents a 8.7 WELLBY gap.How do we assess GiveWell’s discounts? We summarise our position below.
Figure 2: HLI’s views on GiveWell’s total discount of 83% to StrongMind’s effects
We think there’s sufficient evidence and reason to justify the size and magnitude of 5% of GiveWell’s total discount
For ~45% of their total discount, we are sympathetic to including a discount, but we are unsure about the magnitude (generally, we think the discount would be lower). The adjustments that I think are the most plausible are:
A discount of up to 15% for conversion between depression and life-satisfaction SD.
A discount of up to 20% for loss of effectiveness at scale.
A discount of up to 5% for response biases.
Reducing the household size down to 4.8 people.
We are unsympathetic to ~35% of their total discount, because our intuitions differ, but there doesn’t appear to be sufficient existing evidence to settle the matter (i.e., household spillovers).
We think that for 15% of their total discount, the evidence that exists doesn’t seem to substantiate a discount (i.e., their discounts on StrongMind’s durability).
However, as Michael mentions in his comment, a general source of uncertainty we have is about how and when to make use of subjective discounts. We will make more precise claims about the cost-effectiveness of StrongMinds when we finalise our revision and expansion.
The cost-effectiveness of AMF
The second part of Alex’s post is asking how cost-effective is StrongMinds compared to the Against Malaria Foundation (AMF)? AMF, which prevents malaria with insecticide treated bednets, is in contrast to StrongMinds, a primarily life-saving intervention. Hence, as @Jason rightly pointed out elsewhere in the comments, its cost-effectiveness strongly depends on philosophical choices about the badness of death and the neutral point (see Plant et al., 2022). GiveWell takes a particular set of views (deprivationism with a neutral point of 0.5) that are very favourable to life saving interventions. But there are other plausible views that can change the results, and even make GiveWell’s estimate of StrongMinds seem more cost-effective than AMF. Whether you accept our original estimate of StrongMinds, or GiveWell’s lower estimate, the comparison is still incredibly sensitive to these philosophical choices. I think GiveWell is full of incredible social scientists, and I admire many of them, but I’m not sure that should privilege their philosophical intuitions.
Further research and collaboration opportunities
We are truly grateful to GiveWell for engaging with our research on StrongMinds. I think we largely agree with GiveWell regarding promising steps for future research. We’d be keen to help make many of these come true, if possible. Particularly regarding: other interventions that may benefit from a SWB analysis, household spillovers, publication bias, the SWB effects of psychotherapy (i.e. not just depression), and surveys about views on the neutral point and the badness of death. I would be delighted if we could make progress on these issues, and doubly so if we could do so together.
1. Disagreements on the cost-effectiveness of StrongMinds
HLI estimates that psychotherapy produces 10.5 WELLBYs (or 62 per $1000, 7.5x GiveDirectly) for the household of the recipient, while GiveWell estimates that psychotherapy has about a sixth of the effect, 1.8 WELLBYs (17 per $1000 or 2.3x GiveDirectly[5]). In this section, I discuss the sources of our disagreement regarding StrongMinds in the order I presented in Table 1.
1.1 Household spillover differences
Household spillovers are our most important disagreement. When we discuss the household spillover effect or ratio we’re referring to the additional benefit each non-recipient member of the household gets, as a percentage of what the main recipient receives. We first analysed household spillovers in McGuire et al. (2022), which was recently discussed here. Notably, James Snowden pointed out a mistake we made in extracting some data, which reduces the spillover ratio from 53% to 38%.
GiveWell’s method relies on:
Discounting the 38% figure citing several general reasons. (A) Specific concerns that the studies we use might overestimate the benefits because they focused on families with children that had high-burden medical conditions. (B) A shallow review of correlational estimates of household spillovers and found spillover ratios ranging from 5% to 60%.
And finally concluding that their best guess is that the spillover percentage is 15 or 20%[6], rather than 53% (what we used in December 2022) or 38% (what we would use now in light of Snowden’s analysis). Since their resulting figure is a subjective estimate, we aren’t exactly sure why they give that figure, or how much they weigh each piece of evidence.
Table 2: HLI and GiveWell’s views on household spillovers of psychotherapy
Variable
HLI
GiveWell
Explains how much difference in SM’s effect (%)
Household spillover ratio for psychotherapy
38%
15%
3 WELLBYs (34% of total gap)
Note: The household spillover for cash transfers we estimated is 86%.
I reassessed the evidence very recently—as part of the aforementioned discussion with James Snowden—and Alex’s comments don’t lead me to update my view further. In my recent analysis, I explained that I think I should weigh the studies we previously used less because they do seem less relevant to StrongMinds, but I’m unsure what to use instead. And I also hold a more favourable intuition about household spillovers for psychotherapy, because parental mental health seems important for children (e.g., Goodman, 2020).
But I think we can agree that collecting and analysing new evidence could be very important here. The data from Barker et al. (2022), a high quality RCT of the effect of CBT on the general population in Ghana (n = ~7,000) contains information on both partners’ psychological distress when one of them received cognitive behavioural therapy, so this data can be used to estimate any spousal spillover effects from psychotherapy. I am in the early stage of analysing this data[7]. There also seems to be a lot of promising primary work that could be done to estimate household spillovers alongside the effects of psychotherapy.
1.2 Conversion between measures, data sources, and units
The conversion between depression and life-satisfaction (LS) scores ties with household spillovers in terms of importance for explaining our disagreements about the effectiveness of psychotherapy. We’ve previously assumed that a one standard deviation (SD) decrease in depression symptoms (or affective mental health; MHa) is equivalent to a one SD improvement in life-satisfaction or happiness (i.e., a 1:1 conversion), see here for our previous discussion and rationale.
Givewell has two concerns with this:
Depression and life-satisfaction measures might not be sufficiently empirically or conceptually related to justify a 1:1 conversion. Because of this, they apply an empirically based 10% discount.
They are concerned that recipients of psychotherapy have a smaller variance in subjective wellbeing (SWB) than general populations (e.g., cash transfers), which leads to inflated effect sizes. They apply a 20% subjective discount to account for this.
Hence, GiveWell applied a 30% discount (see Table 4 below).
Table 3: HLI and GiveWell’s views on converting between SDs of depression and life satisfaction
Variable HLI
GiveWell
Explains what difference in SM’s effect (%)
Conversion from depression to LS 1 to 1
1 to 0.7
3 WELLBYs (34% of total)
Overall, I agree that there are empirical reasons for including a discount in this domain, but I’m unsure of its magnitude. I think it will likely be smaller than GiveWell’s 30% discount.
1.2.1 Differences between the two measures
First, GiveWell mentions a previous estimate of ours suggesting that mental health (MH) treatments[8] impact depression 11% more than SWB. Our original calculation used a naive average, but on reflection, it seems more appropriate to use a sample-size-weighted average (because of the large differences in samples between studies), which results in depression measures overestimating SWB measures by 4%, instead of 11%.
Results between depression and happiness measures are also very close in Bhat et al. (2022; n = 589), the only study I’ve found so far that looks at effects of psychotherapy on both types of measures. We can standardise the effects in two ways. Depending on the method, the SWB effects are larger by 18% or smaller by 1% than MHa effects[9]. Thus, effects of psychotherapy on depression appear to be of similar size as effects on SWB. Given these results, I think the discount due to empirical differences could be smaller than 10%, I would guess 3%.
Another part of this is that depression and life satisfaction are not the same concept. So if the scores are different, there is a further moral question about which deserves more weight. The HLI ‘house view’, as our name indicates, favours happiness (how good/bad we feel) as what matters. Further, we suspect that measures of depression are conceptually closer to happiness than measures of life satisfaction are. Hence, if push came to shove, and there is a difference, we’d care more about the depression scores, so no discount would be justified. From our conversation with Alex, we understand that the GiveWell ‘house view’ is to care more about life satisfaction than happiness. In this case, GiveWell would be correct, by their lights, to apply some reduction here.
1.2.2 Differences in variance
In addition to their 11% conversion discount, GiveWell adds another 20% discount because they think a sample of people with depression have a smaller variance in life satisfaction scores.[10] Setting aside the technical topic of why variance in variances matters, I investigated whether there are lower SDs in life satisfaction when you screen for baseline depression using a few datasets. I found that, if anything, the SDs are larger by 4% (see Table 4 below). Although I see the rationale behind GiveWell’s speculation, the evidence I’ve looked at suggests a different conclusion.
Table 4: Life-satisfaction SD depending on clinical mental health cutoff
Dataset LS SD for general pop
LS SD for dep pop
SWB SD change (gen → dep)
SWB measure
BHPS (UK, n = 7,310) 1.23
1.30
106%
LS 1-10
HILDA (AUS, n = 4,984) 1.65
1.88
114%
LS 0-10
NIDS (SA, n = 18,039) 2.43
2.38
98%
LS 1-10
Haushofer et al. 2016 (KE, n = 1,336) 1.02
1.04
102%
LS (z-score)
Average change
1.58
1.65
104%
Note: BHPS = The British Household Panel Survey, HILDA = The Household Income and Labour Dynamics Survey, NIDS = National Income Dynamics Study. LS = life satisfaction, dep = depression.
However, I’m separately concerned that SD changes in trials where recipients are selected based on depression (i.e., psychotherapy) are inflated compared to trials without such selection (i.e., cash transfers)[11].
Overall, I think I agree with GiveWell that there should be a discount here that HLI doesn’t implement, but I’m unsure of its magnitude, and I think that it’d be smaller than GiveWell’s. More data could likely be collected on these topics, particularly how much effect sizes in practice differ between life-satisfaction and depression, to reduce our uncertainty.
1.3 Loss of effectiveness outside trials and at scale
GiveWell explains their concern, summarised in the table below:
“Our general expectation is that programs implemented as part of randomized trials are higher quality than similar programs implemented at scale. [...] For example, HLI notes that StrongMinds uses a reduced number of sessions and slightly reduced training, compared to Bolton (2003), which its program is based on.48 We think this typeof modification could reduce program effectiveness relative to what is found in trials. [...] We can also see some evidence for lower effects in larger trials…”
Table 5: HLI and GiveWell’s views on an adjustment for StongMind’s losing effectiveness at scale
Variable HLI GiveWell Explains what difference in SM’s effect (%)
Loss of effect at scale discount 0% 25% 0.9 WELLBYs (10.1% of total gap)
While GiveWell provides several compelling reasons for why StongMinds efficacy will decrease as it scales, I can’t find the reason GiveWell provides for why these reasons result in a 25% discount. It seems like a subjective judgement informed by some empirical factors and perhaps from previous experience studying this issue (e.g., cases like No Lean Season). Is there any quantitative evidence that suggests that when RCT interventions scale they drop 25% in effectiveness? While GiveWell also mentions that larger psychotherapy trials have smaller effects, I assume this is driven by publication bias (discussed in Section 1.6). I’m also less sure that scaling has no offsetting benefits. I would be surprised if when RCTs are run, the intervention has all of its kinks ironed out. In fact, there’s many cases of the RCT version of an intervention being the “minimum viable product” (Karlan et al., 2016). While I think a discount here is plausible, I’m very unsure of its magnitude.
In our updated meta-analysis we plan on doing a deeper analysis of the effect of expertise and time spent in therapy, and to use this to better predict the effect of StrongMinds. We’re awaiting the results from Baird et al. which should better reflect their new strategy as StrongMinds trained but did not directly deliver the programme.
1.4 Disagreements on the durability of psychotherapy
GiveWell explains their concern summarised in the table below, “We do think it’s plausible that lay-person-delivered therapy programs can have persistent long-term effects, based on recent trials by Bhat et al. 2022 and Baranov et al. 2020. However, we’re somewhat skeptical of HLI’s estimate, given that it seems unlikely to us that a time-limited course of group therapy (4-8 weeks) would have such persistent effects. We also guess that some of the factors that cause StrongMinds’ program to be less effective than programs studied in trials (see above) could also limit how long the benefits of the program endure. As a result, we apply an 80% adjustment factor to HLI’s estimates. We view this adjustment as highly speculative, though, and think it’s possible we could update our view with more work.”
Table 6: HLI and GiveWell’s views on a discount to account for a decrease in durability
Variable HLI GiveWell Explains what difference in SM’s effect (%)
Decrease in durability 0% 20% 0.9 WELLBYs (10.1% of total gap) Since this disagreement appears mainly based on reasoning, I’ll explain why my intuitions—and my interpretation of the data—differ from GiveWell here. I already assume that StrongMinds decays 4% more each year than does psychotherapy in general (see table 3). Baranov et al. (2020) and Bhat et al. (2022) both find long-term effects that are greater than what our general model predicts. This means that we already assume a higher decay rate in general, and especially for StrongMinds than the two best long-term studies of psychotherapy suggest. I show how these studies compare to our model in Figure 3 below.
Figure 3: Effects of our model over time, and the only long-term psychotherapy studies in LMICs
Edit: I updated the figure to add the StrongMinds model, which starts with a higher effect but has a faster decay.
Baranov et al. (2020, 16 intended sessions) and Bhat et al. (2022, 6-14 intended sessions, with 70% completion rate) were both time limited. StrongMinds historically used 12 sessions (it may be 8 now) of 90 minutes[12]. Therefore, our model is more conservative than the Baranov et al. result, and closer to the Bhat et al. which has a similar range of sessions. Another reason, in favour of the duration of StrongMinds, which I mentioned in McGuire et al. (2021), is that 78% of groups continued meeting on their own at least six months after the programme formally ended.
Bhat et al. (2022) is also notable in another regard: They asked ~200 experts to predict the impact of the intervention after 4.5 years. The median prediction underestimated the effectiveness by nearly 1/3rd, which makes me inclined to weigh expert priors less here[13].
Additionally, there seems to be something double-county in GiveWell’s adjustments. The initial effect is adjusted by 0.75 for “Lower effectiveness at scale and outside of trial contexts” and the duration effect is adjusted by 0.80, also for “lower effectiveness at scale and outside of trial contexts”. Combined this is a 0.55 adjustment instead of one 0.8 adjustment. I feel like one concern should show up as one discount.
1.5 Disagreements on social desirability bias[14]
GiveWell explains their concern, which is summarised in the table below: “One major concern we have with these studies is that participants might report a lower level of depression after the intervention because they believe that is what the experimenter wants to see [...] HLI responded to this criticism [section 4.4] and noted that studies that try to assess experimenter-demand effects typically find small effects.[...] We’re not sure these tests would resolve this bias so we still include a downward adjustment (80% adjustment factor).”
Table 7: HLI and GiveWell’s views on converting between SDs of depression and life satisfaction
Variable HLI GiveWell Explains what diff in SM’s effect (%)
Social desirability bias discount 0% 20% 0.5 WELLBYs (5.1% of total gap) Participants might report bigger effects to be agreeable with the researchers (socially driven bias) or in the hopes of future rewards (cognitively driven bias; Bandiera et al., 2018), especially if they recognise the people delivering the survey to be the same people delivering the intervention[15].
But while I also worry about this issue, I am less concerned than GiveWell that response bias poses a unique threat to psychotherapy. Because if this bias exists, it seems likely to apply to all RCTs of interventions with self-reported outcomes (and without active controls). So I think the relevant question is why the propensity to response bias might differ between cash transfers and psychotherapy? Here are some possibilities:
It seems potentially more obvious that psychotherapy should alleviate depression than cash transfers should increase happiness. If so, questions about self-reported wellbeing may be more subject to bias in psychotherapy trials[16].
We could expect that the later the follow-up, the less salient the intervention is, the less likely respondents are to be biased in this way (Park & Kumar, 2022). This is one possibility that could favour cash transfers because they have relatively longer follow-ups than psychotherapy.
However, it is obvious to cash transfer participants whether they are in the treatment (they receive cash) or control conditions (they get nothing). This seems less true in psychotherapy trials where there are often active controls.
GiveWell responded to the previous evidence I cited (McGuire & Plant, 2021, Section 4.4)[17] by arguing that the tests run in the literature, by investigating the effect of the general propensity towards socially desirable responding or the expectations of surveyor, are not relevant because: “If the surveyor told them they expected the program to worsen their mental health or improve their mental health, it seems unlikely to overturn whatever belief they had about the program’s expected effect that was formed during their group therapy sessions.” But, if participants’ views about an intervention seem unlikely to be overturned by what the surveyor seems to want—when what the surveyor wants and the participant’s experience differs—then that’s a reason to be less concerned about socially motivated response bias in general.
However, I am more concerned with socially desirable responses driven by cognitive factors. Bandiera et al. (2018, p. 25) is the only study I found to discuss the issue, but they do not seem to think this was an issue with their trial: “Cognitive drivers could be present if adolescent girls believe providing desirable responses will improve their chances to access other BRAC programs (e.g. credit). If so, we might expect such effects to be greater for participants from lower socioeconomic backgrounds or those in rural areas. However, this implication runs counter to the evidence in Table A5, where we documented relatively homogenous impacts across indices and time periods, between rich/poor and rural/urban households.”
I agree with GiveWell that more research would be very useful, and could potentially update my views considerably, particularly with respect to the possibility of cognitively driven response bias in RCTs deployed in low-income contexts.
1.6 Publication bias
GiveWell explains their concern, which we summarise in the table below: “HLI’s analysis includes a roughly 10% downward adjustment for publication bias in the therapy literature relative to cash transfers literature. We have not explored this in depth but guess we would apply a steeper adjustment factor for publication bias in therapy relative to our top charities. After publishing its cost-effectiveness analysis, HLI published a funnel plot showing a high level of publication bias, with well-powered studies finding smaller effects than less-well-powered studies.57 This is qualitatively consistent with a recent meta-analysis of therapy finding a publication bias of 25%.”
Table 8: HLI and GiveWell’s views on a publication bias discount
Variable HLI GiveWell Explains what diff in SM’s effect (%)
Publication bias discount 11% 15% 0.39 WELLBYs (4.5% of total gap) After some recent criticism, we have revisited this issue and are working on estimating the bias empirically. Publication bias seems like a real issue, where a 10-25% correction like what GiveWell suggests seems plausible, but we’re unsure about the magnitude as our research is ongoing. In our update of our psychotherapy meta-analysis we plan to employ a more sophisticated quantitative approach to adjust for publication bias.
1.7 Household size
GiveWell explains their concern, which we summarise in the table below: “HLI estimates household size using data from the Global Data Lab and UN Population Division. They estimate a household size of 5.9 in Uganda based on these data, which appears to be driven by high estimates for rural household size in the Global Data Lab data, which estimate a household size of 6.3 in rural areas in 2019. A recent Uganda National Household Survey, on the other hand, estimates household size of 4.8 in rural areas. We’re not sure what’s driving differences in estimates across these surveys, but our best guess is that household size is smaller than the 5.9 estimate HLI is using.”
Table 9: HLI and GiveWell’s views on household size of StrongMind’s recipients
Variable HLI GiveWell Explains what diff in SM’s effect (%)
Household size for StrongMinds 5.9 4.8 0.39 WELLBYs (4.5% of total gap) I think the figures GiveWell cites are reasonable. I favour using international datasets because I assume it means greater comparability between countries, but I don’t feel strongly about this. I agree it could be easy and useful to try and understand StrongMinds recipient’s household sizes more directly. We will revisit this in our StrongMinds update.
1.8 Cost per person of StrongMinds treated
The one element where we differ that makes StrongMinds look more favourable is cost. As GiveWell explains “HLI’s most recent analysis includes a cost of $170 per person treated by StrongMinds, but StrongMinds cited a 2022 figure of $105 in a recent blog post”
Table 10: HLI and GiveWell’s views on cost per person for StrongMind’s treatment
Variable HLI GiveWell % Total Gap Explained cost per person of StrongMinds $170 $105 -75% According to their most recent quarterly report, a cost per person of $105 was the goal, but they claim $74 per person for 2022[18]. We agree this is a more accurate/current figure, and the cost might well be lower now. A concern is that the reduction in costs comes at the expense of treatment fidelity – an issue we will review in our updated analysis.
2. GiveWell’s cost-effectiveness estimate of AMF is dependent on philosophical views
GiveWell estimates that AMF produces 70 WELLBYs per $1000[19], which would be 4 times better than StrongMinds. GiveWell described the philosophical assumptions of their life saving analysis as: “...Under the deprivationist framework and assuming a “neutral point” of 0.5 life satisfaction points. [...] we think this is what we would use and it seems closest to our current moral weights, which use a combination of deprivationism and time-relative interest account.”
Hence, they conclude that AMF produces 70 WELLBYs per $1000, which makes StrongMinds 0.24 times as cost-effective as AMF. However, the position they take is nearly the most favourable one can take towards interventions that save lives[20]. But there are other plausible views about the neutral point and the badness of death (we discuss this in Plant et al., 2022). Indeed, assigning credences to higher neutral points[21] or alternative philosophical views of death’s badness will reduce the cost-effectiveness of AMF relative to StrongMinds (see Figure 3). In some cases, AMF is less cost-effective than GiveWell’s estimate of StrongMinds[22].
Figure 4: Cost-effectiveness of charities under different philosophical assumptions (with updated StrongMinds value, and GiveWell’s estimate for StrongMinds)
To be clear, HLI does not (yet) take a stance on these different philosophical views. While I present some of my views here, these do not represent HLI as a whole.
Personally, I’d use a neutral point closer to 2 out of 10[23]. Regarding the philosophy, I think my credences would be close to uniformly distributed across the Epicurean, TRIA, and deprivationist views. If I plug this view into our model introduced in Plant et al. (2022) then this would result in a cost-effectiveness for AMF of 29 WELLBYs per $1000 (rather than 81 WELLBYs per $1000)[24], which is about half as good as the 62 WELLBYs per $1000 for StrongMinds. If GiveWell held these views, then AMF would fall within GiveWell’s pessimistic and optimistic estimates of 3-57 WELLBYs per $1000 for StrongMinds’ cost-effectiveness. For AMF to fall above this range, you need to (A) put almost all your credence in deprivationism and (B) have a neutral point lower than 2[25].
- ^
Coincidently, this is (barely) within our most recent confidence interval for comparing the cost-effectiveness of StrongMinds to GiveDirectly (95% CI: 2, 100).
- ^
This calculation is based on a correction for a mistake in our spillover ratio discussed here (a spillover ratio of 38% instead of 53%). Our previous estimate was 77 WELLBYs per $1000 (Plant et al., 2022; McGuire et al., 2022).
- ^
The discount on the effect per $1000 is smaller because GiveWell used a 38% smaller cost figure.
- ^
Note that the reduction in cost-effectiveness is only 27% because they also think that the costs are 62% smaller.
- ^
Coincidently, this is (barely) within our most recent confidence interval for comparing the cost-effectiveness of StrongMinds to GiveDirectly (95% CI: 2, 100).
- ^
The text and the table give different values.
- ^
But if you want to accept that the results could be very off, see here for a document with tables with my very preliminary results.
- ^
These are positive psychology interventions (like mindfulness and forgiveness therapy) which might not completely generalise to psychotherapy in LMICs.
- ^
Psychotherapy improved happiness by 0.38 on a 1-10 score and reduced depression by 0.97 (on the PHQ-9’s 0-27 scale). If we convert the depression score to a 1-10 scale, using stretch transformation, then the effect is a reduction in depression of 0.32. Hence, the SWB changes are 18% larger than MHa changes. If we convert both results to Cohen’s d, we find a Cohen’s d of 0.167 for depression and a Cohen’s d of 0.165 for happiness. Hence changes in MHa are 1% greater than SWB.
- ^
“it seems likely that SD in life satisfaction score is lower among StrongMinds recipients, who are screened for depression at baseline46 and therefore may be more concentrated at the lower end of the life satisfaction score distribution than the average individual.”
- ^
Sample selection based on depression (i.e., selection based on the outcome used) could shrink the variance of depression scores in the sample, which would inflate standardised effects sizes of depression compared to trials without depression selection, because standardisation occurs by dividing the raw effect by its standard deviation (i.e., standardised mean differences, such as Cohen’s d). To explore this, I used the datasets mentioned in Table 4, all of which also included measures of depression or distress and the data from Barker et al. (2022, n = 11,835). I found that the SD of depression for those with clinically significant depression was 18 to 21% larger than it was for the general sample (both the mentally ill and healthy). This seems to indicate that SD changes from psychotherapy provide inflated SD changes in depression compared to cash transfers, due to smaller SDs of depression. However, I think this may be offset by another technical adjustment. Our estimate of the life-satisfaction SD we use to convert SD changes (in MHa or SWB) to WELLBYs might be larger, which means the effects of psychotherapy and cash transfers are underestimated by 14% compared to AMF. When we convert from SD-years to WELLBYs we’ve used a mix of LMIC and HIC sources to estimate the general SD of LS. But I realised that there’s a version of the World Happiness Report that published data that included the SDs of LS for many countries in LMICs. If we use this more direct data for Sub-Saharan Countries then it suggests a higher SD of LS than what I previously estimated (2.5 instead of 2.2, according to a crude estimate), a 14% increase.
- ^
In one of the Bhat et al. trials, each session was 30 to 45 minutes (it’s unclear what the session length was for the other trials).
- ^
Note, I was one of the predictors, and my guess was in line with the crowd (~0.05 SDs), and you can’t see others’ predictions beforehand on the Social Science Prediction Platform.
- ^
Note, this is more about ‘experimenter demand effects’ (i.e., being influenced by the experimenters in a certain direction, because that’s what they want to find) than ‘socially desirability bias’ (i.e., answering that one is happier than they are because it looks better). The latter is controlled for in an RCT. We keep the wording used by GW here.
- ^
GiveWell puts it in the form of this scenario “If a motivated and pleasant IPT facilitator comes to your village and is trying to help you to improve your mental health, you may feel some pressure to report that the program has worked to reward the effort that facilitator has put into helping you.” But these situations are why most implementers in RCTs aren’t the surveyors. I’d be concerned if there were more instances of implementers acting as surveyors in psychotherapy than cash transfer studies.
- ^
On the other hand, who in poverty expects cash transfers to bring them misery? That seems about as rare (or rarer) as those who think psychotherapy will deepen their suffering. However, I think the point is about what participants think that implementers most desire.
- ^
Since then, I did some more digging. I found Dhar et al. (2018) and Islam et al. (2022) which use a questionnaire to test for propensity to answer questions in a socially desirable manner, but find similarly small results of socially motivated response bias. Park et al. (2022) takes an alternative approach where they randomise a subset of participants to self-survey, and argue that this does not change the results.
- ^
This is mostly consistent with 2022 expenses / people treated = 8,353,149 / 107,471 = $78.
- ^
81 WELLBYs per $1000 in our calculations, but they add some adjustments.
- ^
The most favourable position would be assuming deprivationism and a neutral point of zero.
- ^
People might hold that the neutral point is higher than 0.5 (on a 0-10 scale), and thereby reduce the cost-effectiveness of AMF. The IDinsight survey GiveWell uses surveys people from Kenya and Ghana but has a small sample (n = 70) for its neutrality question. In our pilot report (n = 79; UK sample; Samuelsson et al., 2023) we find a neutral point of 1.3. See Samuelsson et al. (2023; Sections 1.3 and 6) for a review of the different findings in the literature and more detail on our findings. Recent unpublished work by Julian Jamison finds a neutral point of 2.5 on a sample size of ~1,800 drawn from the USA, Brazil and China. Note that, in all these cases, we recommend caution in concluding that any of these values is the neutral point. There is still more work to be done.
- ^
Under GiveWell’s analysis, there are still some combinations of philosophical factors where AMF produces 17 WELLBYs or less (i.e., is as or less good than SM in GiveWell’s analysis): (1) An Epicurean view, (2) Deprivationism with neutral points above 4, and (3) TRIA with high ages of connectivity and neutral points above 3 or 4 (depending on the combination). This does not include the possibility of distributing credences across different views.
- ^
I would put the most weight on the work by HLI and Jamison and colleagues, mentioned in above, which finds a neutral point of 1.3/10 and 2.5/10, respectively.
- ^
I average the results across each view.
- ^
We acknowledge that many people may hold these views. We also want to highlight that many people may hold other views. We encourage more work investigating the neutral point and investigating the extent to which these philosophical views are held.
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Joel from HLI here,
Alex kindly shared a draft of this report and discussed feedback from Michael and I more than a year ago. He also recently shared this version before publication. We’re very pleased to finally see that this is published!
We will be responding in more (maybe too much) detail tomorrow. I’m excited to see more critical discussion of this topic.
I’d assume that 1. you don’t need the whole household, depending on the original sample size, it seems plausible to randomly select a subset of household members [1](e.g., in house A you interview recipient and son, in B. recipient and partner, etc...) and 2. they wouldn’t need to consent to participate, just to be surveyed, no?
If these assumptions didn’t hold, I’d be more worried that this would introduce nettlesome selection issues.
- ^
I recognise this isn’t necessarily simple as I make it out to be. I expect you’d need to be more careful with the timing of interviews to minimise the likelihood that certain household members are more likely to be missing (children at school, mother at the market, father in the fields, etc.).
- ^
Fair jabs, but the PRC-Taiwan comparison was because it was the clearest natural experiment that came to mind where different bits of a nation (shared language, culture, etc.) were somewhat randomly assigned to authoritarianism or pluralistic democracy. I’m sure you could make more comparisons with further statistical jiggery-pokery.
The PRC-Taiwan comparison is also because, imagining we want to think of things in terms of life satisfaction, it’s not clear there’d be a huge (war-justifying) loss in wellbeing if annexation by the PRC only meant a relatively small dip in life satisfaction. This is the possibility I found distressing. Surely there’s something we’re missing, no?
I think inhabitants of both countries probably have similar response styles to surveys with these scales. Still, if a state is totalitarian, we should probably not be surprised if people are suspicious of surveys.
Sure, Taiwan could be invaded, and that could put a dampener on things, but, notably, Taiwan is more satisfied than its less likely to be invaded peers of similar wealth and democracy: Japan and South Korea.
I expect one response is, “well, we shouldn’t use these silly surveys”. But what other existing single type of measure is a better assessment of how people’s lives are going?
Taiwan has about a 0.7 advantage on a 0 to 10 life satisfaction scale, with most recently, 5% more of the population reporting to be happy.