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
Karma: 3,097
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].
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Coincidently, this is (barely) within our most recent confidence interval for comparing the cost-effectiveness of StrongMinds to GiveDirectly (95% CI: 2, 100).
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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).
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The discount on the effect per $1000 is smaller because GiveWell used a 38% smaller cost figure.
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Note that the reduction in cost-effectiveness is only 27% because they also think that the costs are 62% smaller.
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Coincidently, this is (barely) within our most recent confidence interval for comparing the cost-effectiveness of StrongMinds to GiveDirectly (95% CI: 2, 100).
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The text and the table give different values.
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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.
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These are positive psychology interventions (like mindfulness and forgiveness therapy) which might not completely generalise to psychotherapy in LMICs.
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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.
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“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.”
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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.
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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).
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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.
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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.
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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.
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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.
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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.
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This is mostly consistent with 2022 expenses / people treated = 8,353,149 / 107,471 = $78.
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81 WELLBYs per $1000 in our calculations, but they add some adjustments.
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The most favourable position would be assuming deprivationism and a neutral point of zero.
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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.
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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.
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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.
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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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Creating projects that are maximally cost-effective is now comparatively less valuable; creating projects that are highly scalable with respect to funding, and can thereby create greater total impact even at lower cost-effectiveness, is comparatively more valuable.
I think this framing is wrong, or at best unhelpful because we shouldn’t avoid prioritizing cost-effectiveness. When you stop prioritizing cost-effectiveness, it stops being effective altruism. Resources are still finite. The effectiveness of solutions to dire problems still differs dramatically. And we have only scratched the surface of understanding which solutions are gold and which are duds. I think it’s cost-effectiveness all the way down.
I hope Will doesn’t mean “creating maximally cost-effective projects is now less valuable” when he says “creating maximally cost-effective projects is now less valuable”. I hope Will means “We should use average cost-effectiveness instead of marginal cost-effectiveness because cost-effectiveness often decreases with more funding. This means that some projects which were more cost-effective at small levels of funding will become less cost-effective at larger levels of funding, which will shift our priorities.” I hope he means that, because I think that’s the correct take.
To illustrate, imagine there’s two projects, A and B, and we have to decide to allocate all of our funds to one or the other. Project A is more cost-effective if our funding supply is limited. This could be treating an incredibly painful but rare disease, where the cost to find potential patients quickly rises as you run out of people to treat. Then there’s project B, which is about as cost-effective regardless of how much money you spend. A classic example of a “project B” type project is cash transfers.
The figures below depict this. The first is a figure lent to me by Michael Plant. I also attach my less clear hand-drawn figure.
As EA acquires more funds, creating and funding maximally cost-effective projects is just as valuable. But our heuristics for cost-effectiveness will change. Instead of asking, “what’s the average cost-effectiveness of spending $10,000 on project A and B”, which would favor A, we should ask “what’s the cost-effectiveness of spending $10,000,000 on project A and B”, which would favor project B.Cost-effectiveness changes with the supply of funding
I haven’t downvoted or read the post, but one explanation is the title “You’re probably a eugenicist” seems clickbaity and aimed at persuasion. It reads as ripe for plucking out of context by our critics. I immediately see it cited in the next major critique published in a major news org: “In upvoted posts on the EA forum, EAs argue they can have ‘reasonable’ conversations about eugenics.”
One idea for dealing with controversial ideas is to A. use a different word and or B. make it more boring. If the title read something like, “Most people favor selecting for valuable hereditary traits.” My pulse would quicken less upon reading.
Here’s my attempt to summarise some of the discussion that Ryan Briggs and Gregory Lewis instigated in the comments of this post, and the analyses it prompted on my end – as requested by Jason [Should I add this to the original post?]. I would particularly like to thank Gregory for his work replicating my analyses and raising several painful but important questions for my analysis. I found the dialogue here very useful, thought provoking, and civil—I really want to thank everyone for making the next version of this analysis better.
Summary
The HLI analysis of the cost-effectiveness of StrongMinds relies not on a single study, but on a meta-analysis of multiple studies.
Regarding this meta-analysis, some commenters (Ryan Briggs and Gregory Lewis) pointed out our lack of a forest plot and funnel plot, a common feature of meta-analyses.
Including a forest plot shows some outlier studies with unusually large effects, and a wide variance in the effects between studies (high heterogeneity).
Including a funnel plot shows evidence that there may be publication bias. Comparing this funnel plot to the one for cash transfers makes the diagnosis of publication bias appear worse in psychotherapy than cash transfers.
My previous analysis employed an ad-hoc and non-standard method for correcting for publication bias. It suggested a smaller (15%) downward correction to psychotherapy’s effects than what some commenters (Ryan and Gregory) thought that a more standard approach would imply (50%+).
Point taken, I tried to throw the book at my own analysis to see if it survived. Somewhat to my surprise, it seemed relatively unscathed.
After applying the six standard publication bias correction methods to both the cash transfer and psychotherapy datasets in 42 different analyses, I found that, surprisingly:
About half the tests increase the effectiveness of psychotherapy relative to cash transfers, and the average test suggests no adjustment.
Only four tests show a decrease in the cost-effectiveness ratio of psychotherapy to cash transfers below of 9.4x → 7x.
The largest reduction of psychotherapy relative to cash transfers is from 9.4x to 3.1x as cost-effective as GiveDirectly cash transfers. It’s based on the older correction method; Trim and Fill.
I have several takeaways.
I didn’t expect this behaviour from these tests. I’m not sure how I should update on using them in the future. I assume the likeliest issue is that they are unreliable in the conditions of these meta-analyses (high heterogeneity). Any thoughts on how to correct for publication bias in future analyses is welcome!
Given the ambivalent results, it doesn’t seem like any action is urgently needed (i.e., immediately pause the StrongMinds recommendation).
However, this discussion has raised my sense of the priority of doing the re-analysis of psychotherapy and inspired me to do quite a few things differently next time. I hope to start working on this soon (but I don’t want to promise dates).
I’m not saying “look, everything is fine!”.I should have investigated publication bias more thoroughly in the original analysis. The fact that after I’ve done that now and it doesn’t appear to suggest substantial changes to my analysis is probably more due to luck than a nose for corners I can safely cut.
1. The story so far
In the comments, Ryan Briggs and Gregory Lewis have pointed out that my meta-analysis of psychotherapy omits several typical and easy to produce figures. These are forest plots and funnel plots. A forest plot shows the individual study effects and the study effects. If I included this, it would have shown two things.
First, that there is quite a bit of variation in the effects between studies (i.e., heterogeneity). What heterogeneity implies is a bit controversial in meta-analyses, and I’ll return to this, but for now I’ll note that some take the presence of high heterogeneity as an indication that meta-analytic results are meaningless. At the other end of professional opinion, other experts think that high heterogeneity is often inevitable and merely warrants prudence. However, even the most permissive towards heterogeneity think that it makes an analysis more complicated.
The second thing the forest plot shows is that there were a few considerable outliers. Notably, some of these outliers (Bolton et al., 2003; Bass et al., 2006) are part of the evidence I used to estimate that StrongMinds is more cost-effective than the typical psychotherapy intervention in LMICs. The other figure I omitted was a funnel plot. Funnel plots are made to show if there are many more small studies that find large effects than small with small, null or negative effects than we would expect due to a random draw. In the funnel plots for the psychotherapy data, which Gregory first provided by using a version of the the data I use, he rightly pointed out that there is considerable asymmetry, which suggests that there may be publication bias (i.e., the small sized studies that find small, null, or negative effects are less likely to be published and included than small studies with larger effects). This finding seemed all the more concerning given that I found pretty much no asymmetry in the cash transfers data I compare psychotherapy to.
I supplemented this with a newer illustration, the p-curve, meant to detect publication bias that’s not just about the size of an effect, but its precision. The p-curve suggests publication bias if there’s an uptick in the number of effect sizes near the 0.05 significance level relative to the 0.03 or 0.04 level. The idea is that researchers are inclined to fiddle with their specifications until they are significant, but that they’re limited in their ambitions to perform questionable research practices and will tend to push them just over the line. The p-curve for psychotherapy shows a slight uptick near the 0.05 level, compared to none in cash transfers. This is another sign that the psychotherapy evidence base appears to have more publication bias than cash transfers.
Ryan and Gregory rightly pushed me on this – as I didn’t show these figures that make psychotherapy look bad. I have excuses, but they aren’t very good so I won’t repeat them here. I think it’s fair to say that these could have and should have been included.
The next, and most concerning point that Ryan and Gregory made was that if we take the Egger regression test seriously (a formal, less eye-bally way of testing for funnel plot asymmetry), it’d indicate that psychotherapy’s effect size should be dramatically reduced[1]. This frankly alarmed me. If this was true, I potentially made a large mistake [2].
2. Does correcting for publication bias substantially change our results?
To investigate this I decided to look into the issue of correcting for publication bias in more depth. To do so I heavily relied upon Harrer et al. (2021), a textbook for doing meta-analyses in R.
My idea for investigating this issue would be to go through every method for correcting publication bias mentioned in Harrer et al. (2021) and show how these methods change the cash transfers to psychotherapy comparison. I thought this would be more reasonable than trying to figure out which one was the method to rule them all. This is also in line with the recommendations of the textbook “No publication bias method consistently outperforms all the others. It is therefore advisable to always apply several techniques…” For those interested in an explanation of the methods, I found Harrer et al. (2021) to be unusually accessible. I don’t expect I’ll do better.
One issue is that these standard approaches don’t seem readily applicable to the models we used. Our models are unusual in that they are 1. Meta-regressions, where we try to explain the variation in effect sizes using study characteristics like time since the intervention ended, and 2. Multi-level meta-analyses that attempt to control for the dependency introduced by adding multiple timepoints or outcomes from a single study. It doesn’t seem like you can easily plug these models into the standard publication bias methods. Because of this uncertainty we tried to run several different types of analyses (see details in 2.1) based on whether a model included the full data or excluded outliers or follow-ups or used a fixed or random effects estimator[3].
I ran (with the help of my colleague Samuel[4]) the corrections for both psychotherapy and cash transfers and then apply the percentage of correction to their cost-effectiveness comparison. It doesn’t seem principled to only run these corrections on psychotherapy. Even though the problem seems worse in psychotherapy, I think the appropriate thing to do is also run these corrections on the cash transfers evidence and see if the correction is greater for psychotherapy.
If you want to go straight to the raw results, I collected them in a spreadsheet that I hope is easy to understand. Finally, if you’re keen on replicating this analysis, we’ve posted the code we used here.
2.1 Model versions
Measures of heterogeneity and publication bias seem to be designed for simpler meta-analysis models than those we use in our analysis. We use a meta-regression with follow-up time (and sometimes dosage), so the estimate of the intercept is affected by the coefficients for time and other variables. Reading through Harrer et al. (2021) and a brief google search didn’t give us much insight as to whether these methods could easily apply to a meta-regression model. Furthermore, most techniques presented by Harrer et al. (2021) used a simple meta-analysis model which employed a different set of R functions (metagen rather than the rma.uni or rma.mv models we use).
Instead, we create a simple meta-analysis model to calculate the intercept for psychotherapy and for cash. We then apply the publication bias corrections to these models and get the % change this created. We then apply the % change of the correction to the effect for psychotherapy and cash and obtain their new cost-effectiveness ratio.
Hence, we are not using the model we directly use in our analysis, but we apply to our analysis the change in effectiveness that the correction method would produce on a model appropriate for said correction method.
Because of our uncertainty, we ran several different types of analyses based on whether a model included the full data[5] or excluded outliers[6] or follow-ups[7] or used a fixed or random effects estimator[8].
2.2 Results
The results of this investigation are shown below. Tests that are to the left of the vertical line represent decreases in the cost-effectiveness of psychotherapy relative to cash transfers. The reference models are the six right on the line (in turquoise). I’ll add further commentary below.
Details of the results can be seen in this spreadsheet. We removed tests 28, 29, 30, 34, 35, 36. These were generally favourable to psychotherapy. We removed them because they were p-curve and Rücker’s limit corrections models that we specified as fixed-effects models but they seemed to force the models into random-effects models, making their addition seem inappropriate[9].
Surprisingly, when we apply these tests, very few dramatically reduce the cost-effectiveness of psychotherapy compared to cash transfers, as indicated by changes to their intercepts / the estimated average overall effect.
Only four tests show a decrease below 7x for PT.
The largest correction (using Trim and Fill) reduces PT <> CT from 9.4x to 3.1x as cost-effective as GiveDirectly cash transfers.
Aside: Given that this appears to be the worst case scenario, I’m not actually sure this would mean we drop our recommendation given that we haven’t found anything clearly better yet (see our analyses of anti-malarial bednets and deworming). I think it’s likelier that we would end up recommending anti-malaria bed nets to those with sympathetic philosophical views.
The trim and fill and selection models are the ones most consistently negative to PT.
The worst models for PT are trim and fill, and selection models. But the trim and fill models are the oldest (most outdated?) models that seem to be the least recommended (Harrer et al., (2021) says they are “often outperformed by other methods”). The PET and PEESE models tend to actually make psychotherapy look even better compared to cash transfers.
Surprisingly, many tests increase the cost-effectiveness ratio in favour of psychotherapy!
2.3 Uncertainties
A big problem is that most of these tests are sensitive to heterogeneity, so we’re left with a relatively high level of uncertainty in interpreting these results. Are differences between the minimal or most negative update due to the heterogeneity? I’m not sure.
This should partially be alleviated by adding in the tests with the outliers removed, but while this reduces heterogeneity a bit (PT I^2: 95% → 56%, CT I^2: 75% → 25%), it’s still relatively high.
Further, the largest downwards adjustment that involves removing outliers is from 9.4x → 7.5x.
It’s unclear if these publication bias adjustments would differentially affect estimates for the decay rate of the benefit. Our analysis was about the average effect (i.e., the intercept). It’s unclear how publication bias should affect the estimate of the decay rate of psychotherapy (or cash).
2.4 A note about heterogeneity
Sometimes it’s suggested that the high heterogeneity in a meta-analysis means it is impossible to interpret (see details of heterogeneity in my analyses in this spreadsheet). Whilst heterogeneity is important to report and discuss, we don’t think it disqualifies this analysis.
However, high levels of heterogeneity appear to be a common problem with meta-analyses. It’s unclear that this is uniquely a problem with our meta-analysis of psychotherapy. In their big meta-analysis of psychotherapy, Cuijpers et al. (2023; see Table 2) also have high levels of heterogeneity. Our cash transfer meta-analysis also has high (albeit lower than psychotherapy) levels of heterogeneity.
High heterogeneity would be very problematic if it meant the studies are so different they are not measuring the same thing. Alternative explanations are that (1) psychotherapy is a phenomenon with high variance (supported by similar findings of psychotherapy in HICs), and/or (2) studies about psychotherapy in LMICs are few and implemented in different ways, so we expect this data is going to be messy.
3. Next Steps
4 tests suggest psychotherapy is 3-7x cash, 8 tests suggest psychotherapy is 7-9.4x cash, and 18 tests suggest psychotherapy is 9.4 or more times cash. Because of the ambiguous nature of the results, I don’t plan on doing anything immediately like suggesting we pause the StrongMinds recommendation.
However, this analysis and the surrounding discussion has updated me on the importance of updating and expanding the psychotherapy meta-analysis sooner. Here are some things I’d like to commit to:
Do a systematic search and include all relevant studies, not just a convenience sample.
Heavily consider including a stricter inclusion criteria. And if we don’t perform more subset analyses and communicate them more clearly.
Include more analyses that include dosage (how many hours in session) and expertise of the person delivering the therapy.
Include better data about the control group, paying special attention to whether the control group could be considered as receiving a high, low quality, or no placebo.
In general, include and present many more robustness checks.
Add an analogous investigation of publication bias like the one performed here.
Make our data freely available and our analysis easily replicable at the time of publication.
Am I missing anything?
After updating the psychotherapy meta-analysis we will see how it changes our StrongMinds analysis.
I’ve also expected to make a couple changes to that analysis[10], hopefully incorporating the new Baird et al. RCT. Note if it comes soon and its result strongly diverge from our estimates this could also expedite our re-analysis.
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Note that the Egger regression is a diagnostic test, not a form of correction. However, the PET and PEESE methods are correction methods and are quite similar in structure to the Egger regression test.
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Point taken that the omission is arguably, a non-trivial mistake.
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Choosing a fixed or random effects model is another important and controversial question in modelling meta-analysis and we wanted to test whether the publication bias corrections were particularly sensitive to it. However, it seems like our data is not suitable to the assumptions of a fixed effects model – and this isn’t uncommon. As Harrer et al., (2021) say: “In many fields, including medicine and the social sciences, it is therefore conventional to always use a random-effects model, since some degree of between-study heterogeneity can virtually always be anticipated. A fixed-effect model may only be used when we could not detect any between-study heterogeneity (we will discuss how this is done in Chapter 5) and when we have very good reasons to assume that the true effect is fixed. This may be the case when, for example, only exact replications of a study are considered, or when we meta-analyze subsets of one big study. Needless to say, this is seldom the case, and applications of the fixed-effect model “in the wild″ are rather rare.”
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If my analyses are better in the future, it’s because of my colleague Samuel Dupret. Look at the increase in quality between the first cash transfer and psychotherapy reports and the household spillover report. That was months apart. You know what changed? Sam.
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The same data we use in our full models.
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Some methods are not robust to high levels of heterogeneity, which is more often present when there are outliers. We select outliers for the fixed and random effects models based on “‘non-overlapping confidence intervals’ approach, in which a study is defined as an outlier when the 95% confidence interval (CI) of the effect size does not overlap with the 95% CI of the pooled effect size” (Cuijpers et al., 2023; see Harrer et al., 2021 for a more detailed explanation).
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We are concerned that these methods are not made with the assumption of a meta-regression and might react excessively to the follow-up data (i.e., effect sizes other than the earliest effect size collected in a study), which are generally smaller effects (because of decay) with smaller sample sizes (because of attrition).
- ^
Choosing a fixed or random effects model is another important and controversial question in modelling meta-analysis and we wanted to test whether the publication bias corrections were particularly sensitive to it. However, it seems like our data is not suitable to the assumptions of a fixed effects model – and this isn’t uncommon. As Harrer et al., (2021) say: “In many fields, including medicine and the social sciences, it is therefore conventional to always use a random-effects model, since some degree of between-study heterogeneity can virtually always be anticipated. A fixed-effect model may only be used when we could not detect any between-study heterogeneity (we will discuss how this is done in Chapter 5) and when we have very good reasons to assume that the true effect is fixed. This may be the case when, for example, only exact replications of a study are considered, or when we meta-analyze subsets of one big study. Needless to say, this is seldom the case, and applications of the fixed-effect model “in the wild″ are rather rare.”
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The only tests that are different from the random effects ones are 32 and 38 because the list of outliers were different for fixed effects and random effects.
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I expect to assign relatively lower weight to the StrongMinds specific evidence. I was leaning this direction since the summer, but these conversations—particularly the push from Simon, hardened my views on this. This change would decrease the cost-effectiveness of StrongMinds. Ideally, I’d like to approach the aggregation of the StrongMinds specific and general evidence of lay-group psychotherapy in LMICs in a more formally Bayesian manner, but this would come with many technical difficulties. I will also look into the counterfactual impact of their scaling strategy where they instruct other groups in how to provide group psychotherapy.
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Trying to hold onto the word “eugenics” seems to indicate an unrealistically optimistic belief in people’s capacity to tolerate semantics. Letting go is a matter of will, not reason.
E.g., I pity the leftist who thinks they can, in every conversation with a non-comrade, explain the difference between the theory of a classless society, the history of ostensibly communist regimes committing omnicide, and the hitherto unrealised practice of “real communism” (outside of a few scores of 20th-century Israeli villages and towns). To avoid the reverse problem when discussing “communist” regimes, I refer to “authoritarian regimes with command economies”. And I’m convinced it’s almost always better to go with “Social Democracy”.
Who cares if no other word has caught on yet. Marketing is a great and powerful force (one EAs seem only dimly to understand). Use more words if you have to. The key point is that “it’s a good idea to avoid tying yourself to words where the most common use is associated with mass murder.” [1]
Turning to the example. I’d pray to Hedone that most EAs can read the room well enough to avoid making such arguments while we still have nuclear wars to stop, pandemics to prevent, diseases to cure, global poverty to stamp out, and many cheap and largely uncontroversial treatments for depression and everyday sadness we’ve yet to scale. But assuming they did make that argument, I think the response to “That’s eugenics” should be something like:
“No, eugenics is associated with stripping a group of people of their right to reproduce. I’m discussing supporting families to make choices about their children’s health. Screening is already supported for many debilitating health conditions because of the suffering they produce, I’m saying that we should provide that same support when the conditions that produce the suffering are mental rather than physical.”
But maybe a takeaway here is: “don’t feed the trolls”?
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Note: One response is, “we can’t give up on every word once it’s tainted by associated with some unseemly set of disreputes.” And that’s fair. For instance, I’m fine being associated with “Happiness Science” because the most common use is associated with social science into self-reported wellbeing, not a genocide-denying Japanese cult. The point is that choice of association depends on what most people associate the word with. Language will always be more bottom-up than top-down and seems much closer to a rowdy democracy than a sober technocracy.
- ^
We’d like to express our sincere thanks to GiveWell for providing such a detailed and generous response. We are delighted that our work may lead to substantive changes, and echoing GiveWell, we encourage others to critique HLI’s work with the same level of rigour.
In response to the substantive points raised by Alex:
Using a different starting value: Our post does not present a strong argument for how exactly to include the decay. Instead, we aimed to do the closest ‘apples-to-apples’ comparison possible using the same values that GiveWell uses in their original analysis. Our main point was that including decay makes a difference, and we are encouraged to see that GiveWell will consider incorporating this into their analysis.
We don’t have a strong view of the best way to incorporate decay in the CEA. However, we intend to develop and defend our views about how the benefits change over time as we finalise our analysis of deworming in terms of subjective wellbeing.
How to weigh the decay model: We agree with Alex’s proposal to put some weight on the effects being constant. Again, we haven’t formed a strong view on how to do this yet and recognise the challenges that GiveWell faces in doing so. We look forward to seeing more of GiveWell’s thinking on this.
Improving reasoning transparency: We strongly support the plans quoted below and look forward to reading future publications that clearly lay out the importance of key judgements and assumptions.
We plan to update our website to make it clearer what key judgment calls are driving our cost-effectiveness estimates, why we’ve chosen specific parameters or made key assumptions, and how we’ve prioritized research questions that could potentially change our bottom line.
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.
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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.”
I’m belatedly making an overall comment about this post.
I think this was a valuable contribution to the discussion around charity evaluation. We agree that StrongMinds’ figures about their effect on depression are overly optimistic. We erred by not pointing this out in our previous work and not pushing StrongMinds to cite more sensible figures. We have raised this issue with StrongMinds and asked them to clarify which claims are supported by causal evidence.
There are some other issues that Simon raises, like social desirability bias, that I think are potential concerns. The literature we reviewed in our StrongMinds CEA (page 26) doesn’t suggest it’s a large issue, but I only found one study that directly addresses this in a low-income country (Haushofer et al., 2020), so the evidence appears very limited here (but let me know if I’m wrong). I wouldn’t be surprised if more work changed my mind on the extent of this bias. However, I would be very surprised if this alone changed the conclusion of our analysis. As is typically the case, more research is needed.
Having said that, I have a few issues with the post and see it as more of a conversation starter than the end of the conversation. I respond to a series of quotes from the original post below.
I’m going to leave aside discussing HLI here. Whilst I think they have some of the deepest analysis of StrongMinds, I am still confused by some of their methodology, it’s not clear to me what their relationship to StrongMinds is.
If there’s confusion about our methodology, that’s fair, and I’ve tried to be helpful in that regard. Regarding our relationship with StrongMinds, we’re completely independent.
“The key thing to understand about the HLI methodology is that it follows the same structure as the Founders Pledge analysis and so all the problems I mention above regarding data apply just as much to them as FP.”
This is false. As we’ve explained before, our evaluation of StrongMinds is primarily based on a meta-analysis of psychological interventions in LMICs, which is a distinction between our work and Founders Pledge that means that many of the problems mentioned apply less to our work.
I also have some issues with the claims this post makes. I’ll focus on Simon’s summary of his argument:
“I think the strongest statement I can make (which I doubt StrongMinds would disagree with) is: ’StrongMinds have made limited effort to be quantitative in their self-evaluation, haven’t continued monitoring impact after intervention, haven’t done the research they once claimed they would. They have not been vetted sufficiently to be considered a top charity, and only one independent group has done the work to look into them.”
Next, I remark on the problem with each line.
“I think the strongest statement I can make (which I doubt StrongMinds would disagree with) is – ”
I think StrongMinds would disagree with this argument. This strikes me as overconfident.
“StrongMinds have made limited effort to be quantitative in their self-evaluation, haven’t continued monitoring impact after intervention…”
If quantitative means “RCTs”, then sure, but until very recently, they surveyed the depression score before and after treatment for every participant (which in 2019 meant an n = 28,294, unpublished data shared with me during their evaluation). StrongMinds also followed up 18 months after their initial trial and in 2019 they followed up with 300 participants six months after they received treatment (again, unpublished data). I take that as at least a sign they’re trying to quantitatively evaluate their impact – even if they could do much better (which I agree they could).
“[StrongMinds] haven’t done the research they once claimed they would.”
I’m a bit confused by this point. It sounds more like the appropriate claim is, “they didn’t do the research they once claimed they would do fast enough.” As Simon pointed out, there’s an RCT whose results should be released soon by Baird et al. From conversations we’ve had with StrongMinds, they’re also planning on starting another RCT in 2023. I also know that they completed a controlled trial in 2020 (maybe randomised, still unsure) with a six-month and year follow-up. However, I agree that StrongMinds could and should invest in collecting more causal data. I just don’t think the situation is as bleak as it has been made out to be, as running an RCT can be an enormous undertaking.
“They have not been vetted sufficiently to be considered a top charity, and only one independent group has done the work to look into them.”
This either means (a) only Founders Pledge has evaluated StrongMinds, which is wrong, or (b) HLI doesn’t count because we are not independent, which would be both wrong and uncharitable.
“Based on Phase I and II surveys, it seems to me that a much more cost-effective intervention would be to go around surveying people. I’m not exactly sure what’s going on with the Phase I / Phase II data, but the best I can tell is in Phase I we had a ~7.5 vs ~5.1 PHQ-9 reduction from “being surveyed” vs “being part of the group” and in Phase II we had ~5.1 vs ~4.5 PHQ-9 reduction from “being surveyed” vs “being part of the group”. For what it’s worth, I don’t believe this is likely the case, I think it’s just a strong sign that the survey mechanism being used is inadequate to determine what is going on.”
I think this could have a pretty simple explanation. StrongMinds used a linear model to estimate: depression reduction = group + sessions. This will lead to a non-zero intercept if the relationship between sessions and depression reduction is non-linear, which we see in the graphs provided in the post.
Even if all those things apply … this post may not be for you! Last year I tried to replace sleep with caffeine, and it did not go well. Even if you think you’re happy and emotionally stable, you may discover that stimulants are anxiogenic for you, and you may be dumb enough (i.e., me) not to make that connection for a year.
Stimulants, at least for me, are much better at making me feel productive than increasing my total output. I regularly wasted 3-6 hours chunks plumbing the depths of a rabbit hole that unstimulated me would have rightly avoided. A moderate caveat emptor here.
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
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.
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?
This an interesting topic, but one I haven’t looked into much. I would like to see more work on this because while some claim that the link between prosocial spending and well-being is universal (Aknin et al., 2013) I wonder if that was a bit premature . The study I reference found cross sectional correlations between subjective well-being and prosocial spending in 136 countries and followed this up with a few small experiments that concurred.
Some other literature in the area for what it’s worth: A series of recent pre-registered experiments (n =~ 7k) found mixed results (2 positive, 1 null) on the effect of prosocial spending (not giving exactly) on happiness (Aknin et al., 2020). Another experiment (n = 615) finds that people do not adapt to giving like they adapt to spending on themselves (O’Brien and Kassirer, 2018). Several studies find that the degree of warm glow is increased by being informed about its impact and having a greater orientation towards “meaning and authenticity” (n = 126) (Lai et al., 2020), another found that happier giving experiences were marked by feeling as if the choice was freely chosen, has a clear impact or is made towards a cause that the giver is connected to (Lok & Dunn, 2020 ).
Chapter four of the 2019 World Happiness Report reviews some of the evidence of prosocial behavior and subjective-well being (although it does not appear to mention the studies I reference above).
Now comes the controversial line from a recent study (n = 325) that takes a different tact: “Regression results showed that saving a life decreased long-run happiness by 0.26 SD (P < 0.01) (Table 1, column 4) relative to receiving money, conditional on individual-specific baseline levels of happiness.” from Falk & Graeber (2020).
Some comments on the above study (I haven’t look at it in detail): By long-run they mean four weeks and they think saving a life means saving a life.
Under conservative assumptions, a donation of 350 euros—roughly $400 at the time—covers all costs incurred by Operation ASHA to identify, treat, and cure five more patients, which is equivalent to saving one additional human life in expectation.
Another relevant quote from the Falk & Graeber paper:
A positive correlation between prosocial behavior and happiness is a central empirical justifi- cation for the quest to donate more. Philosopher Peter Singer forcefully argues that altruism is not about self-sacrifice, but that the greatest happiness arises from helping other people (33).
I appreciate this post! Loneliness is something I think about often because it appears to be, alongside mental health issues, as one of the things that appears relatively worse for people’s subjective wellbeing than say, their income.
That being said, it was always unclear what can be done, and this review doesn’t seem to suggest there’s a frontrunner in terms of interventions.
I’m puzzled that so many interventions involve 1 on 1 interactions. This doesn’t seem scalable or in the spirit of well, decreasing loneliness.
Group interventions seem more promising but there appears to be less evidence.
I wonder if the reason why group-psychotherapy in some cases appears better than 1 on 1 therapy is because of an added loneliness reduction bonus.
I’d also be curious to hear what ideas there are for new interventions / RCTs.
Intergenerational cohabitation seems like a plausible way to solve two problems at once. Older people are lonelier and have more housing. Younger people don’t have much housing. Why not connect them? I’d be curious to see the results for an RCT of a matchmaking programme.
I feel like there are obvious intervention’s no one’s tested: try to connect lonely people to one another, perhaps in a group setting with a facilitator? How much does a website/ app like Meetup already do this?
I’d also be interested to know if there are any quasi-experiments that could be studied related to larger scale interventions. I.e., does the walkability of a city increase wellbeing through decreases in loneliness? What about more social clubs?
A question I’m curious about is what are the biggest barriers to lonely people going out and making friends on their own? Is it transportation? Cost? Unclear where to go? Church used to be the easy button, but many people aren’t religious anymore and we don’t have a clear substitute. Why isn’t this a problem that markets can solve?
What about digital interventions? Some people seem to be content with forming and maintaining relationships through a digital medium (e.g., online gaming).
I’d also really like to know how common loneliness is in low income countries, and how the barriers differ towards forming more positive social bonds.
“In LEEP’s second year (this year), we started working in six more countries, bringing the total to nine. We received another government commitment and paint manufacturers in two countries started switching to lead-free.”
I would just like to point out that this is incredible. Policy advocacy seems very hard. To have two commitments from two countries in two years seems very unusual for any domain of policy or regulation. Keep in mind that this domain involves one of the most potent poisons we managed to spread everywhere. Even if these countries drag their feet, they would have to drag very hard for the value of these two years, and the expected value of LEEP to not be very high.
The cost-effectiveness looks strong with this one.
Given that this post has been curated, I wanted to follow up with a few points I’d like to emphasise that I forgot to include in the original comment.
To my knowledge, we were the first to attempt to estimate household spillovers empirically. In hindsight, it shouldn’t be too surprising that it’s been a messy enterprise. I think I’ve updated towards “messiness will continue”.
One hope of ours in the original report was to draw more attention to the yawning chasm of good data on this topic.
“The lack of data on household effects seems like a gap in the literature that should be addressed by further research. We show that including household spillovers can change the relative cost-effectiveness of two interventions, which demonstrates the need to account for the impact of interventions beyond the direct recipient.”
Relatedly, spillovers don’t have to be huge to be important. If you have a household of 5, with 1 recipient and 4household non-recipients, household spillovers only need to be 25% that of the recipient effect for the two effects to be equivalent in size. I’m still pretty confident we omit an important parameter when we fail to estimate household spillovers.
So I’m pleased with this conversation and hopeful that spillovers for all outcomes in the global health and wellbeing space will be given more empirical consideration as a consequence.
There are probably relatively cost-effective ways to gather more data regarding psychotherapy spillovers in particular.
I’ve heard that some people working with Vida-Plena are trying to find funding for an RCT that includes spillovers — but I haven’t spoken to Joy about this recently.
StrongMinds could be willing to do more work here. I think they’re planning an RCT — if they get it funded, I think adding a module for household surveys shouldn’t be too expensive.
There’s also a slew of meta-analyses of interventions aimed at families that didn’t always seem jointly to target parents and children that may include more RCTs where we can infer spillovers. Many of these I missed before: Siegenthaler et al. (2012), Thanhäuser et al. (2017), Yap et al. (2016), Loechner et al. (2018), Lannes et al., (2018), and Havinga et al. (2021)
In general, household spillovers should be relatively cheap to estimate if they just involve surveying a randomly selected additional household member and clarifying the relationships between those surveyed.
I still don’t have the Barker et al. RCT spillover results, but will update this comment once I know.
A note on the “positive utility” bit. I am very uncertain about this. We don’t really know where on subjective wellbeing scales people construe wellbeing to go from positive to negative. My best bet is around 2.5 on a 0 to 10 scale. This would indicate that ~18% of people in SSA or South Asia have lives with negative wellbeing if what we care about is life satisfaction (debatable). For the world, this means 11%, which is similar to McAskill’s guess of 10% in WWOTF.
And insofar as happiness is separate from life satisfaction. It’s very rare for a country, on average, to report being more unhappy than happy.
Simon,
It’s helpful to know why you thought the relationship was unclear.
But I don’t think us (HLI) publishing research during the giving season is “cynical timing” any more than you publishing this piece when many people from GWWC, FP, and HLI are on vacation is “cynical timing”.
When you’re an organization without guaranteed funding, it seems strategic to try to make yourself salient to people when they reach for their pocketbooks. I don’t see that as cynical.
FWIW, the explanation is rather mundane: the giving season acts as hard deadline which pushes us to finish our reports.
Hi Simon, I’m one of the authors of HLI’s cost-effectiveness analysis of psychotherapy and StrongMinds. I’ll be able to engage more when I return from vacation next week.
I see why there could be some confusion there. Regarding the two specifications of WELLBYs, the latter was unique to that appendix, and we consider the first specification to be conventional. In an attempt to avoid this confusion, we denoted all the effects as changes in ‘SDs’ or ‘SD-years’ of subjective wellbeing / affective mental health in all the reports (1,2,3,4,5) that were direct results in the intervention comparison.
Regarding whether these changes are “meaningful at all”, -- it’s unclear what you mean. Which of the following are you concerned with?
That standard deviation differences (I.e., Cohen’s d or Hedges g effect sizes) are reasonable ways to do meta-analyses?
Or is your concern more that even if SDs are reasonable for meta-analyses, they aren’t appropriate for comparing the effectiveness of interventions? We flag some possible concerns in Section 7 of the psychotherapy report. But we haven’t found sufficient evidence after several shallow dives to change our minds.
Or, you may be concerned that similar changes in subjective wellbeing and affective mental health don’t represent similar changes in wellbeing? (We discuss this in Appendix A of the psychotherapy report).
Or is it something else I haven’t articulated?
Most of these issues are technical, and we recognise that our views could change with further work. However, we aren’t convinced there’s a ready-to-use method that is a better alternative for use with subjective wellbeing analyses.
I also welcome further explanation of your issues with our analysis, public or private. If you’d like to have low stakes chat about our work, you can schedule a time here. If that doesn’t work, email or message me, and we can make something work.
James courteously shared a draft of this piece with me before posting, I really appreciate that and his substantive, constructive feedback.
1. I blundered
The first thing worth acknowledging is that he pointed out a mistake that substantially changes our results. And for that, I’m grateful. It goes to show the value of having skeptical external reviewers.
He pointed out that Kemp et al., (2009) finds a negative effect, while we recorded its effect as positive — meaning we coded the study as having the wrong sign.
What happened is that MH outcomes are often “higher = bad”, and subjective wellbeing is “higher = better”, so we note this in our code so that all effects that imply benefits are positive. What went wrong was that we coded Kemp et al., (2009), which used the GHQ-12 as “higher = bad” (which is usually the case) when the opposite was true. Higher equalled good in this case because we had to do an extra calculation to extract the effect [footnote: since there was baseline imbalance in the PHQ-9, we took the difference in pre-post changes], which flipped the sign.
This correction would reduce the spillover effect from 53% to 38% and reduce the cost-effectiveness comparison from 9.5 to 7.5x, a clear downwards correction.
This is how the forest plot should look.
2. James’s other critiques
I think James’s other critiques are also pretty reasonable. This updates me towards weighting these studies less. That said, what I should place weight on instead remains quite uncertain for me.
I’ve thought about it a bit, but I’m unsure what to make of the observational evidence. My reading of the observational literature mostly accords with James (I think), and it does appear to suggest smaller spillovers than the low quality RCTs I previously referenced (20% versus the now 38%). Here’s a little table I made while doing a brief review during my discussion with James.
0.00%
0.00%
25%[1]
5.25%
7.00%
25%
22.50%
30.00%
25%
3.75%
5.00%
25%
10.00%
40.00%
50%[3]
7.88%
10.50%
14.00%
25%
12.00%
16.00%
25%
43.50%
58.00%
25%
40.00%
40.00%
50%
16.50%
33.00%
50%
24.50%
20.34%
31.50%
35.00%
10%
35.00%
35.00%
0%
34.00%
34.00%
0%
60.00%
60.00%
0%
40.13%
63.00%
63.00%
0%
63.00%
57.28%
However, I wonder if there’s something about the more observational literature that makes household spillovers appear smaller, regardless of the source. To investigate this further, I briefly compared household spillovers from unemployment and mental health shocks. This led me to an estimate of around 57% as the household spillover of unemployment, which I think we could use as a prior for other economic shocks. This is a bit lower than the 86% I estimated as the household spillover for cash transfers. Again, not quite sure what to make of this.
3. Other factors that influence my priors / fuzzy tummy feelings about psychotherapy spillovers.
Mother’s mental health seems really important, over and above a father’s mental health. Augustijn (2022) finds a higher relationship between mother<> child MH than father<>child mental health (a 1 LS point change in the mother predicts a 0.13 change in LS for child (as compared to 0.06 for fathers). Many of the studies above seem to have larger mother → child effects than father → child. This could be relevant as StrongMinds primarily treats women.
Mental health appears important relative to the effect of income.
See figure from Clark et al., (2018) -- shown below.
Mcnamee et al., (2021) (published version of Mendolia et al., 2018) finds that having a partner with a long term emotional or nervous condition that requires treatment has a −0.08 effect on LS, and that log household income has a 0.064 effect. If we interpret 0.69 log-units as leading to a doubling, and assume that most $1000 CTs lead to about a doubling in household income, then the effect of doubling income is 0.064 * 0.69 = 0.04 effect on LS. If I assume that the effect of depression is similar to “long-term emotional or nervous condition that requires treatment” and psychotherapy cures 40% of depression cases, then this leads to an effect of psychotherapy of 0.4 * −0.08 = 0.032. Or the effect of psychotherapy relative to doubling the income on a partner is 73%. Applying this to the 86% CT spillover would get us a 63% spillover ratio for psychotherapy.
You could compare income and mental health effects on wellbeing in other studies—but I haven’t had time to do so (and I’m not really sure of how informative this is).
Powdthavee & Vignoles (2008), which found the effect of mother distress in the previous period on children is 14% of the effect that the child’s own wellbeing in the previous period had on their present wellbeing. But it also seems to give weirdly small coefficients (and non-significant) for the effect of log-income on life satisfaction (0.054 for fathers, negative −0.132 for mothers).
Early life exposure to a parent’s low mental health seems plausibly related to very long term wellbeing effects through higher likelihood of worse parenting (abuse, fewer resources to support the child; Zheng et al., 2021)
I’m unsure if positive and negative shocks spillover in the same way. Negativity seems more contagious than positivity. For instance in Hurd et al. (2014) the spillover effects of re-employment seemed less than the harms of unemployment. Also see Adam et al., (2014)[4] – I’m sure there’s much more on this topic. This makes me think that it may not be wild to see a relatively smaller gap between the spillovers of cash transfers and psychotherapy than we may initially expect.
Most of these studies are in HICs. It seems plausible that spillovers for any intervention could be different and I suspect higher in LMICs than HICs. I assume emotional contagion is a function of spending time together, and spending more time together seems likelier when houses are smaller (you can’t shut yourself in your room as easily), transportation is relatively more expensive, difficult, and dangerous – and you may have fewer reasons to go elsewhere. One caveat is that household sizes are larger, so there may be less time directly spent with any given household member, so that’s a factor that could push in the other direction.
4. What’s next?
I think James and I probably agree that making sense out of the observational evidence is tricky to say the least, and a high quality RCT would be very welcome for informing our views and settling our disagreements. I think some further insight could come sooner rather than later. As I was writing this, I wondered if there was any possibility of household spillovers in Barker et al., (2022), a recent study about the effects of CBT on the general population in Ghana that looked into community spillovers of psychotherapy (-33% the size of the treatment effect but non-significant – but’s that’s a problem for another time).
In section 3.2 the paper reads, “At the endline we administered only the “adult” survey, again to both the household head and their spouse… In our analysis of outcomes, we include the responses of both adults in control households; in households where an individual received CBT, we only include treated individuals.’”
This means that while Barket et al. didn’t look into it we should be able to estimate the spousal mental health spillover of having your partner receive CBT. In further good news, the replication materials are public. But I’ll leave this as a teaser while I try to figure out how to run the analysis.
Why a 25% discount? I guess partners are likelier to share tendencies towards a given level of wellbeing, but I think this “birds of a feather” effect is smaller than the genetic effects. Starting from a 50% guess for genetic effects (noted in the next footnote), I thought that the assortative mating effects would be about half the magnitude or 25%.
How did I impute the parent/child effect? The study was ambiguous about the household relations being analysed. So I assumed that it was 50-50 parents and children and that the spouse-to-spouse spillover was a 1/4th that of the parent-to-child spillover.
Why a 50% discount? There appears to be an obvious genetic factor between a parent and child’s levels of wellbeing that could confound these estimates. Jami et al., (2021) reviews ~30 studies that try to disentangle the genetic and environmental link between families affective mental health. My reading is that environmental (pure contagion) effects dominate the anxiety transmission, and genetic-environmental factors seem roughly balanced for depression. Since we mostly consider psychotherapy to treat depression, I only reference the depression results when coming up with the 50% figure.
“When positive posts were reduced in the News Feed, the percentage of positive words in people’s status updates decreased by B = −0.1% compared with control [t(310,044) = −5.63, P < 0.001, Cohen’s d = 0.02], whereas the percentage of words that were negative increased by B = 0.04% (t = 2.71, P = 0.007, d = 0.001). Conversely, when negative posts were reduced, the percent of words that were negative decreased by B = −0.07% [t(310,541) = −5.51, P < 0.001, d = 0.02] and the percentage of words that were positive, conversely, increased by B = 0.06% (t = 2.19, P < 0.003, d = 0.008).