Mostly bio, occasionally forecasting/epistemics, sometimes stats/medicine, too often invective.

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I have previously let HLI have the last word, but this is too egregious.

**Study quality: **Publication bias (a property of the literature as a whole) and risk of bias (particular to each individual study which comprise it) are two different things.^{[1]} Accounting for the former does not account for the latter. This is why the Cochrane handbook, the three meta-analyses HLI mentions here, *and HLI's own protocol* consider distinguish the two.

Neither Cuijpers et al. 2023 nor Tong et al. 2023 *further* adjust their low risk of bias subgroup for publication bias.^{[2]} I tabulate the relevant figures from both studies below:

So HLI indeed gets similar initial results and publication bias adjustments to the two other meta-analyses they find. Yet - although these are not like-for-like - these other two meta-analyses find similarly substantial effect reductions when accounting for study quality as they do when assessing at publication bias of the literature as a whole.

There is ample cause for concern here:^{[3]}

- Although neither of
*these*studies 'adjust for both', one later mentioned - Cuijpers et al. 2020 -*does*. It finds an*additional*discount to effect size when doing so.^{[4]}So it suggests that indeed 'accounting for' publication bias does not adequately account for risk of bias*en passant*. - Tong et al. 2023 - the meta-analysis expressly on PT in LMICs rather than PT generally - finds higher prevalence of indicators of lower study quality in LMICs, and notes this as a competing explanation for the outsized effects.
^{[5]} - As previously mentioned, in the previous meta-analysis, unregistered trials had a 3x greater effect size than registered ones. All trials on Strongminds published so far have not been registered. Baird et al., which is registered, is anticipated to report disappointing results.

**Evidentiary standards: **Indeed, the report drew upon a large number of studies. Yet even a synthesis of 72 million (or whatever) studies can be misleading if issues of publication bias, risk of bias in individual studies (and so on) are not appropriately addressed. That an area has 72 (or whatever) studies upon it does not mean it is *well-*studied, nor would this number (nor any number) be sufficient, by itself, to satisfy any evidentiary standard.

**Outlier exclusion: **The report's approach to outlier exclusion is *dissimilar* to both Cuijpers et al. 2020 and Tong et al. 2023, and further is dissimilar with respect to *features I highlighted as major causes for concern re. HLI's approach in my original comment.*^{[6]}* *Specifically:

- Both of these studies present the analysis with the full data first in their results. Contrast HLI's report, where only the results with outliers excluded are presented in the main results, and the analysis without exclusion is found only in the appendix.
^{[7]} - Both these studies also report the results with the full data as their main findings (e.g. in their respective abstracts). Cuijpers et al. mentions their outlier excluded results primarily in passing ("outliers" appears once in the main text); Tong et al. relegates a lot of theirs to the appendix. HLI's report does the opposite. (cf. fn 7 above)
- Only Tong et al. does further sensitivity analysis on the 'outliers excluded' subgroup. As Jason describes, this is done alongside the analysis where all data included, the qualitative and quantitative differences which result from this analysis choice are prominently highlighted to the reader and extensively discussed. In HLI's report, by contrast, the factor of 3 reduction to ultimate effect size when outliers are not excluded is only alluded to qualitatively in a footnote (fn 33)
^{[8]}of the main report's section (3.2) arguing why outliers should be excluded, not included in the reports sensitivity analysis, and only found in the appendix.^{[9]} - Both studies adjust for publication bias only on all data, not on data with outliers excluded, and these are the publication bias findings they present. Contrast HLI's report.

The Cuijpers et al. 2023 meta-analysis previously mentioned also differs in its approach to outlier exclusion from HLI's report in the ways highlighted above. The Cochrane handbook also supports my recommendations on what approach should be taken, which is what the meta-analyses HLI cites approvingly as examples of "sensible practice" actually do, but what HLI's own work does not.

The reports (non) presentation of the stark quantitative sensitivity of its analysis - material to its report bottom line recommendations - to whether outliers are excluded is clearly inappropriate. It is indefensible if, as I have suggested may be the case, the analysis with outliers included was indeed the analysis first contemplated and conducted.^{[10]} It is even worse if it was the *publication bias corrections *on the full data was what in fact prompted HLI to start making alternative analysis choices which happened to substantially increase the bottom line figures.

**Bayesian analysis: **Bayesian methods notoriously do *not *avoid subjective inputs - most importantly here, what information we attend to when constructing an 'informed prior' (or, if one prefers, how to weigh the results with a particular prior stipulated).

In any case, they provide no protection from misunderstanding the calculation being performed, and so misinterpreting the results. The Bayesian method in the report is actually calculating the (adjusted) average effect size of psychotherapy interventions in general, not the expected effect of a given psychotherapy intervention. Although a trial on Strongminds which shows it is relatively ineffectual should not update our view much the efficacy of psychotherapy interventions (/similar to Strongminds) as a whole, it should update us dramatically on *the efficacy of Strongminds itself*.

Although as a methodological error this is a subtle one (at least, subtle enough for me not to initially pick up on it), the results it gave are nonsense to the naked eye (e.g. SM would still be held as a GiveDirectly-beating intervention even if there were *multiple* high quality RCTs on Strongminds giving flat or negative results). HLI should have seen this themselves, should have stopped to think after I highlighted these facially invalid outputs of their method in early review, and definitely should not be doubling down on these conclusions even now.

**Making recommendations: **Although there are other problems, those I have repeated here make the recommendations of the report unsafe. This is why I recommended against publication. Specifically:

- Although I don't think the Bayesian method the report uses would be appropriate, if it was calculated properly on its own terms (e.g. prediction intervals not confidence intervals to generate the prior, etc.), and leaving everything else the same, the SM bottom line would drop (I'm pretty sure) by a factor a bit more than 2.
- The results are already essentially sensitive to whether outliers are excluded in analysis or not: SM goes from 3.7x -> ~1.1x GD on the back of my envelope, again leaving all else equal.

(1) and (2) combined should net out to SM < GD; (1) or (2) combined with some of the other sensitivity analyses (e.g. spillovers) will also likely net out to SM < GD. Even if one still believes the bulk of (appropriate) analysis paths still support a recommendation, this sensitivity should be made transparent.

^{^}E.g. Even if all studies in the field are conducted impeccably, if journals only accept positive results the literature may still show publication bias. Contrariwise, even if all findings get published, failures in allocation/blinding/etc. could lead to systemic inflation of effect sizes across the literature. In reality - and here - you often have

*both*problems, and they only partially overlap.^{^}Jason correctly interprets Tong et al. 2023: the number of studies included in their publication bias corrections (117 [+36 w/ trim and fill]) equals the number of all studies, not the low risk of bias subgroup (36 - see table 3). I

*do*have access to Cuijpers et al. 2023, which has a very similar results table, with parallel findings (i.e. they do their publication bias corrections on the whole set of studies, not on a low risk of bias subgroup).^{^}Me, previously:

HLI's report does not assess the quality of its included studies, although it plans to do so. I appreciate GRADEing 90 studies or whatever is tedious and time consuming, but skipping this step to crack on with the quantitative synthesis is very unwise: any such synthesis could be hugely distorted by low quality studies.

^{^}From their discussion (my emphasis):

Risk of bias is another important problem in research on psychotherapies for depression. In 70% of the trials (92/309) there was at least some risk of bias. And the studies with low risk of bias, clearly indicated smaller effect sizes than the ones that had (at least some) risk of bias. Only four of the 15 specific types of therapy had 5 or more trials without risk of bias. And the effects found in these studies were more modest than what was found for all studies (including the ones with risk of bias).

**When the studies with low risk of bias were adjusted for publication bias, only two types of therapy remained significant (the “Coping with Depression” course, and self-examination therapy).**^{^}E.g. from the abstract (my emphasis):

The larger effect sizes found in non-Western trials were related to the presence of wait-list controls, high risk of bias, cognitive-behavioral therapy, and clinician-diagnosed depression (

*p*< 0.05).**The larger treatment effects observed in non-Western trials may result from the high heterogeneous study design and relatively low validity**. Further research on long-term effects, adolescent groups, and individual-level data are still needed.^{^}Apparently, all that HLI really meant with "

**Excluding outliers**is thought sensible practice here; two related meta-analyses, Cuijpers et al., 2020c; Tong et al., 2023,**used a similar approach**" [my emphasis] was merely "[C]onditional on removing outliers, they identify a similar or greater range of effect sizes as outliers as we do." (see).Yeah, right.

I also had the same impression as Jason that HLI's reply repeatedly strawmans me. The passive aggressive sniping sprinkled throughout and subsequent backpedalling (in fairness, I suspect by people who were

*not*at the keyboard of the corporate account) is less than impressive too. But it's nearly Christmas, so beyond this footnote I'll let all this slide.^{^}Me again (my [re-?]emphasis)

Received opinion is typically that outlier exclusion should be avoided without a clear rationale why the 'outliers' arise from a clearly discrepant generating process.

**If it is to be done, the results of the full data should still be presented as the primary analysis**^{^}Said footnote:

If we didn’t first remove these outliers, the total effect for the recipient of psychotherapy would be much larger (see Section 4.1) but some publication bias adjustment techniques would over-correct the results and suggest the completely implausible result that psychotherapy has negative effects (leading to a smaller adjusted total effect). Once outliers are removed, these methods perform more appropriately. These methods are not magic detectors of publication bias. Instead, they make inferences based on patterns in the data, and we do not want them to make inferences on patterns that are unduly influenced by outliers (e.g., conclude that there is no effect – or, more implausibly, negative effects – of psychotherapy because of the presence of unreasonable effects sizes of up to 10 gs are present and creating large asymmetric patterns). Therefore, we think that removing outliers is appropriate. See Section 5 and Appendix B for more detail.

The sentence in the main text this is a footnote to says:

Removing outliers this way reduced the effect of psychotherapy and improves the sensibility of moderator and publication bias analyses.

^{^}Me again:

[W]ithout excluding data, SM drops from ~3.6x GD to ~1.1x GD. Yet it doesn't get a look in for the sensitivity analysis, where HLI's 'less favourable' outlier method involves taking an average of the other methods (discounting by ~10%), but not doing no outlier exclusion at all (discounting by ~70%).

^{^}My remark about "Even if you didn't pre-specify, presenting your first cut as the primary analysis helps for nothing up my sleeve reasons" which Dwyer mentions elsewhere was a reference to 'nothing up my sleeve numbers' in cryptography. In the same way picking pi or e initial digits for arbitrary constants reassures the author didn't pick numbers with some ulterior purpose they are not revealing, reporting what one's first analysis showed means readers can compare it to where you ended up after making all the post-hoc judgement calls in the garden of forking paths. "Our first intention analysis would give x, but we ended up convincing ourselves the most appropriate analysis gives a bottom line of 3x" would rightly arouse a lot of scepticism.

I've already mentioned I suspect this is indeed what has happened here: HLI's first cut was including all data, but argued itself into making the choice to exclude, which gave a 3x higher 'bottom line'. Beyond "You didn't say you'd exclude outliers in your protocol" and "basically all of your discussion in the appendix re. outlier exclusion concerns the results of publication bias corrections on the bottom line figures", I kinda feel HLI

*not*denying it is beginning to invite an adverse inference from silence. If I'm right about this, HLI should come clean.

So the problem I had in mind was in the parenthetical in my paragraph:

To its credit, the write-up does highlight this, but does not seem to appreciate the implications are crazy: any PT intervention, so long as it is cheap enough, should be thought better than GD, even if studies upon it show very low effect size

(which would usually be reported as a negative result, as almost any study in this field would be underpowered to detect effects as low as are being stipulated)

To elaborate: the actual data on Strongminds was a n~250 study by Bolton et al. 2003 then followed up by Bass et al. 2006. HLI models this in table 19:

So an initial effect of g = 1.85, and a total impact of 3.48 WELLBYs. To simulate what the SM data will show once the (anticipated to be disappointing) forthcoming Baird et al. RCT is included, they discount this^{[1]} by a factor of 20.

Thus the simulated effect size of Bolton and Bass is now ~0.1. In this simulated case, the Bolton and Bass studies would be reporting *negative* results, as they would not be powered to detect an effect size as small as g = 0.1. To benchmark, the forthcoming Baird et al. study is 6x larger than these, and its power calculations have minimal detectable effects g = 0.1 or greater.

Yet, apparently, in such a simulated case we should conclude that Strongminds is fractionally better than GD *purely* on the basis of two trials reporting *negative* findings, because numerically the treatment groups did slightly (but not significantly) better than the control ones.

Even if in general we are happy with 'hey, the effect is small, but it is cheap, so it's a highly cost-effective intervention', we should not accept this at the point when 'small' becomes 'too small to be statistically significant'. Analysis method + negative findings =! fractionally better in expectation vs. cash transfers, so I take it as diagnostic the analysis is going wrong.

^{^}I think 'this' must be the initial effect size/intercept, as 3.48 * 0.05 ~ 1.7 not 3.8. I find this counter-intuitive, as I think the drop in total effect should be super not sub linear with intercept, but ignore that.

(@Burner1989 @David Rhys Bernard @Karthik Tadepalli)

I think the fundamental point (i.e. "You cannot use the distribution for the expected value of an average therapy treatment as the prior distribution for a SPECIFIC therapy treatment, as there will be a large amount of variation between possible therapy treatments that is missed when doing this.") is on the right lines, although subsequent discussion of fixed/random effect models might confuse the issue. (Cf. my reply to Jason).

The typical output of a meta-analysis is an (~) average effect size estimate (the diamond at the bottom of the forest plot, etc.) The confidence interval given for that is (very roughly)^{[1]} the interval we predict the true average effect likely lies. So for the basic model given in Section 4 of the report, the average effect size is 0.64, 95% CI (0.54 - 0.74). So (again, roughly) our best guess of the 'true' average effect size of psychotherapy in LMICs from our data is 0.64, and we're 95% sure(*) this average is somewhere between (0.54, 0.74).

Clearly, it is not the case that if we draw another study from the same population, we should be 95% confident(*) the effect size of this new data point will lie between 0.54 to 0.74. This would not be true even in the unicorn case there's no between study heterogeneity (e.g. all the studies are measuring the same effect modulo sampling variance), and even less so when this is marked, as here. To answer that question, what you want is a *prediction interval*.^{[2]} This interval is always wider, and almost always significantly so, than the confidence interval for the average effect: in the same analysis with the 0.54-0.74 confidence interval, the prediction interval was -0.27 to 1.55.

Although the full model HLI uses in constructing informed priors is different from that presented in S4 (e.g. it includes a bunch of moderators), they appear to be constructed with monte carlo on the *confidence* *intervals for the average*, not the *prediction interval for the data.* So I believe the informed prior is actually one of the (adjusted) "Average effect of psychotherapy interventions as a whole", not a prior for (e.g.) "the effect size reported in a given PT study." The latter would need to use the prediction intervals, and have a much wider distribution.^{[3]}

I think this ably explains exactly why the Bayesian method for (e.g.) Strongminds gives very bizarre results when deployed as the report does, but they do make much more sense if re-interpreted as (in essence) computing the expected effect size of 'a future strongminds-like intervention', but not the effect size we should believe StrongMinds actually has once in receipt of trial data upon it specifically. E.g.:

- The histogram of effect sizes shows some comparisons had an effect size < 0, but the 'informed prior' suggests P(ES < 0) is extremely low. As a prior for the effect size of the next study, it is much too confident, given the data, a trial will report positive effects (you have >1/72 studies being negative, so surely it cannot be <1%, etc.). As a prior for the average effect size, this confidence is warranted: given the large number of studies in our sample, most of which report positive effects, we would be very surprised to discover the true average effect size is
*negative*. - The prior doesn't update very much on data provided. E.g. When we stipulate the trials upon strongminds report a near-zero effect of 0.05 WELLBYs, our estimate of 1.49 WELLBYS goes to 1.26: so we should (apparently) believe in such a circumstance the efficacy of SM is ~25 times greater than the trial data upon it indicates. This is, obviously, absurd. However, such a small update is appropriate if it were to ~the average of PT interventions as a whole: that we observe a new PT intervention has much below average results should cause our average to shift a little towards the new findings, but not much.

In essence, the update we are interested in is not "How effective should we expect *future interventions like Strongminds* are given the data on Strongminds efficacy", but simply "How effective should we expect *Strongminds* is given the data on how effective Strongminds is". Given the massive heterogeneity and wide prediction interval, the (correct) informed prior is pretty *uninformative, *as it isn't that surprised by anything in a very wide range of values, and so on finding trial data on SM with a given estimate in this range, our estimate should update to match it pretty closely.^{[4]}

(This also should mean, unlike the report suggests, the SM estimate is not that 'robust' to adverse data. Eyeballing it, I'd guess the posterior should be going down by a factor of 2-3 conditional on the stipulated data versus currently reported results).

^{^}I'm aware confidence intervals are not credible intervals, and that 'the 95% CI tells you where the true value is with 95% likelihood' strictly misinterprets what a confidence interval is, etc. (see) But perhaps 'close enough', so I'm going to pretend these are credible intervals, and asterisk each time I assume the strictly incorrect interpretation.

^{^}Cf. Cochrane:

The summary estimate and confidence interval from a random-effects meta-analysis refer to the centre of the distribution of intervention effects, but do not describe the width of the distribution. Often the summary estimate and its confidence interval are quoted in isolation and portrayed as a sufficient summary of the meta-analysis. This is inappropriate. The confidence interval from a random-effects meta-analysis describes uncertainty in the location of the mean of systematically different effects in the different studies. It does not describe the degree of heterogeneity among studies, as may be commonly believed. For example, when there are many studies in a meta-analysis, we may obtain a very tight confidence interval around the random-effects estimate of the mean effect even when there is a large amount of heterogeneity. A solution to this problem is to consider a

**prediction interval**(see Section 10.10.4.3).^{^}Although I think the same mean, so it will give the right 'best guess' initial estimates.

^{^}Obviously, modulo all the other issues I suggest with both the meta-analysis as a whole, that we in fact would incorporate other sources of information into our actual prior, etc. etc.

What prior to formally pick is tricky - I agree the factors you note would be informative, but how to weigh them (vs. other sources of informative evidence) could be a matter of taste. However, sources of evidence like this could be handy to use as 'benchmarks' to see whether the prior (/results of the meta-analysis) are consilient with them, and if not, explore why.

But I think I can now offer a clearer explanation of what is going wrong. The hints you saw point in this direction, although not quite as you describe.

One thing worth being clear on is HLI is not updating on the actual SM specific evidence. As they model it, the estimated effect on this evidence is an initial effect of g = 1.8, and a total effect of ~3.48 WELLBYs, so this would lie on the *right* tail, not the left, of the informed prior.^{[1]} They *discount* the effect by a factor of 20 to generate the data they feed into their Bayesian method. Stipulating data which would be (according to their prior) very surprisingly bad would be in itself a strength, not a concern, of the conservative analysis they are attempting.

Next, we need to distinguish an *average effect size* from a *prediction interval*. The HLI does report both (Section 4) for a more basic model of PT in LMICs. The (average, random) effect size is 0.64 (95% CI 0.54 to 0.74), whilst the prediction interval is -0.27 to 1.55. The former is giving you the best guess of the average effect (with a confidence interval), the latter is telling you - if I do another study like those already included, the range I can expect its effect size to be within. By loose analogy: if I sample 100 people and their average height is roughly 5' 7" (95% CI 5'6" to 5'8"), the 95% range of the individual heights will range much more widely (say 5' 0" to 6' 2")

Unsurprisingly (especially given the marked heterogeneity), the prediction interval is much wider than the confidence interval around the average effect size. Crucially, if our 'next study' reports an effect size of (say) 0.1, our interpretation typically should *not* be: "This study can't be right, the real effect of the intervention it studies must be much closer to 0.6". Rather, as findings are heterogeneous, it is much more likely a study which (genuinely) reports a below average effect.^{[2]} Back to the loose analogy, we would (typically) assume we got it right if we measured some more people at (e.g.) 6'0" and 5'4", even though these are significantly above or below the 95% confidence interval of our average, and only start to doubt measurements much outside our prediction interval (e.g. 3'10", 7'7").

Now the problem with the informed prior becomes clear: it is (essentially) being constructed with *confidence intervals of the average*, not *prediction intervals for its data* from its underlying models. As such, it is a prior *not *of "What is the expected impact of *a given PT intervention*", but rather "What is the expected *average impact of PT interventions as a whole*".^{[3]}

With this understanding, the previously bizarre behaviour is made sensible. For the informed prior should assign very little credence to the *average* impact of PT *overall* being ~0.4 per the stipulated Strongminds data, even though it should not be *that* surprised that a particular intervention (e.g. Strongminds!) has an impact much below average, as many other PT interventions studied also do (cf. Although I shouldn't be surprised if I measure someone as 5'2", I should be very surprised if the true average height is actually 5'2", given my large sample averages 5'7"). Similarly, if we are given a much smaller additional sample reporting a much different effect size, the updated average effect should remain pretty close to the prior (e.g. if a handful of new people have heights < 5'4", my overall average goes down a little, but not by much).

Needless to say, the results of such an analysis, if indeed for "average effect size of psychotherapy as a whole" are completely inappropriate for "expected effect size of a given psychotherapy intervention", which is the use it is put to in the report.^{[4]} If the measured effect size of Strongminds was indeed ~0.4, the fact psychotherapy interventions ~average substantially greater effects of ~1.4 gives very little reason to conclude the *effect of Strongminds* is in fact much higher (e.g. ~1.3). In the same way, if I measure your height is 5'0", the fact the average heights of other people I've measured is 5'7" does not mean I should conclude you're probably about 5'6".^{[5]}

^{^}Minor: it does lie pretty far along the right tail of the prior (<top 1st percentile?), so maybe one could be a little concerned. Not much, though: given HLI was

*searching*for particularly effective PT interventions in the literature, it doesn't seem that surprising that this effort could indeed find one at the far-ish right tail of apparent efficacy.^{^}One problem for many types of the examined psychotherapy is that the level of heterogeneity was high, and many of the prediction intervals were broad and included zero. This means that it is difficult to predict the effect size of the next study that is done with this therapy, and that study may just as well find negative effects. The resulting effect sizes differ so much for one type of therapy, that it cannot be reliably predicted what the true effect size is.

^{^}Cf. your original point about a low result looking weird given the prior. Perhaps the easiest way to see this is to consider a case where the intervention is

*harmful*. The informed prior says P (ES < 0) is very close to zero. Yet >1/72 studies in the sample*did*have an effect size < 0. So obviously a prior of an intervention should not be*that*confident in predicting it will not have a -ve effect. But a prior of the average effect of PT interventions should be*that*confident this average is not in fact negative, given the great majority of sampled studies show substantially +ve effects.^{^}In a sense, the posterior is not computing the expected effect of StrongMinds, but rather the expected effect of a future intervention

*like*StrongMinds. Somewhat ironically, this (again, simulated) result would be best interpreted as an*anti-recommendation*: Strongminds performs much*below*the average we would expect of interventions similar to it.^{^}It is slightly different for measured height as we usually have very little pure measurement error (versus studies with more significant sampling variance). So you'd update a little less towards the reported study effects vs. the expected value than you would for height measurements vs. the average. But the key points still stand.

HLI kindly provided me with an earlier draft of this work to review a couple of weeks ago. Although things have gotten better, I noted what I saw as major problems with the draft as-is, and recommended HLI take its time to fix them - even though this would take a while, and likely miss the window of Giving Tuesday.

Unfortunately, HLI went ahead anyway with the problems I identified basically unaddressed. Also unfortunately (notwithstanding laudable improvements elsewhere) these problems are sufficiently major I think potential donors are ill-advised to follow the recommendations and analysis in this report.

In essence:

- Issues of study quality loom large over this literature, with a high risk of materially undercutting the results (they did last time). The reports interim attempts to manage these problems are inadequate.
- Pub bias corrections are relatively mild, but only when all effects g > 2 are excluded from the analysis - they are much starker (albeit weird) if all data is included. Due to this, the choice to exclude 'outliers' roughly trebles the bottom line efficacy of PT. This analysis choice is dubious on its own merits, was not pre-specified in the protocol, yet is only found in the appendix rather than the sensitivity analysis in the main report.
- The bayesian analysis completely stacks the deck in favour of psychotherapy interventions (i.e. an 'informed prior' which asserts one should be > 99% confident strongminds is more effective than givedirectly before any data on strongminds is contemplated), such that psychotherapy/strongminds/etc, getting recommended is essentially foreordained.

**Study quality**

It perhaps comes as little surprise that different studies on psychotherapy in LMICs report very different results:^{[1]}

The x-axis is a standardized measure of effect size for psychotherapy in terms of wellbeing.^{[2]} Most - but not all - show a positive effect (g > 0), but the range is vast, HLI excludes effect sizes over 2 as outliers (much more later), but 2 is already a large effect: to benchmark, it is roughly the height difference between male and female populations.

Something like an '(weighted) average effect size' across this set would look promising (~0.6) - to also benchmark, the effect size of cash transfers on (individual) wellbeing is ~0.1. Yet cash transfers (among many other interventions) have much less heterogeneous results: more like "0.1 +/- 0.1", not ~"0.6 multiply-or-divide by an integer". It seems important to understand what is going on.

One hope would be this heterogeneity can be explained in terms of the intervention and length of follow-up. Different studies did (e.g.) different sorts of psychotherapy, did more or less of it, and measured the outcomes at different points afterwards. Once we factor these things in to our analysis, this wide distribution seen when looking at the impact of psychotherapy *in general* sharpens into a clearer picture for any *particular *psychotherapeutic intervention. One can then deploy this knowledge to assess - in particular - the likely efficacy of a charity like Strongminds.

The report attempts this enterprise in section 4 of the report. I think a fair bottom line is despite these efforts, the overall picture is still very cloudy: the best model explains ~12% of the variance in effect sizes. But this best model is still better than no model (but more later), so one can still use it to make a best guess for psychotherapeutic interventions, even if there remains a lot of uncertainty and spread.

But there could be another explanation for why there's so much heterogeneity: there are a lot of low-quality studies, and low quality studies tend to report inflated effect sizes. In the worst case, the spread of data suggesting psychotherapy's efficacy is instead a mirage, and the effect size melts under proper scrutiny.

Hence why most systematic reviews do assess the quality of included studies and their risk of bias. Sometimes this is only used to give a mostly qualitative picture alongside the evidence synthesis (e.g. 'X% of our studies have a moderate to high risk of bias') or sometimes incorporated quantitatively (e.g. 'quality score' of studies included as a predictor/moderator, grouping by 'high/moderate/low' risk of bias, etc. - although all are controversial).

HLI's report does not assess the quality of its included studies, although it plans to do so. I appreciate GRADEing 90 studies or whatever is tedious and time consuming, but skipping this step to crack on with the quantitative synthesis is very unwise:^{[3]} any such synthesis could be hugely distorted by low quality studies. And it's not like this is a mere possibility: I previously demonstrated in the previous meta-analysis that study registration status (*one* indicator of study quality) explained a lot of heterogeneity, and unregistered studies had on average a three times [!] greater effect size than registered ones.

The report notes it has done some things to help manage this risk. One is cutting 'outliers' (g > 2, the teal in the earlier histogram), and extensive assessment of publication bias/small study effects. These things do help: all else equal, I'd expect bigger studies to be methodologically better ones, so adjusting for small study effects does partially 'control' for study quality; I'd also expect larger effect sizes to arise from lower-quality work, so cutting them should notch up the average quality of the studies that remain.

But I do not think they help enough^{[4]} - these are loose proxies for what we seek to understand. Thus the findings would be unreliable in virtue of this alone until after this is properly looked at. Crucially, the risk that these features could *confound* the earlier moderator analysis has not been addressed:^{[5]} maybe the relationship of (e.g.) 'more sessions given -> greater effect' is actually due to studies of such interventions tend to be lower quality than the rest. When I looked last time things like 'study size' or 'registration status' explained a lot *more* of the heterogeneity than (e.g.) all of the intervention moderators combined. I suspect the same will be true this time too.

**Publication bias**

I originally suggested (6m ago?) that correction for publication bias/small study effects could be ~an integer division, so I am surprised the correction was a bit less: ~30%. Here's the funnel plot:^{[6]}

Unsurprisingly, huge amounts of scatter, but the asymmetry, although there, does not leap off the page: the envelope of points is pretty rectangular, but you can persuade yourself it's a bit of a parallelogram, and there's denser part of it which indeed has a trend going down and to the right (so smaller study -> bigger effect).

But this only plots effect sizes g < 2 (those red, not teal, in the histogram). If we include all the studies again, this picture looks a lot clearer - the 'long tail' of higher effects tends to come from smaller studies, which are clearly asymmetric.

This effect, visible to the naked eye, also emerges in the statistics. The report uses a variety of numerical methods to correct for publication bias (some very sophisticated). All of them adjust the results much further downwards on the full data than when outliers are excluded to varying degrees (table B1, appendix). It would have a stark effect on the results - here's the 'bottom line' result if you take a weighted average of all the different methods, with different approaches to outlier exclusion - red is the full data, green is the outlier exclusion method the report uses.

Needless to say, this choice is highly material to the bottom line results: without excluding data, SM drops from ~3.6x GD to ~1.1x GD. Yet it doesn't get a look in for the sensitivity analysis, where HLI's 'less favourable' outlier method involves taking an average of the other methods (discounting by ~10%), but not doing no outlier exclusion at all (discounting by ~70%).^{[7]}

Perhaps this is fine if outlier *inclusion* would be clearly unreasonable. But it's not: cutting data is generally regarded as dubious, and the rationale for doing so here is not compelling. Briefly:

- Received opinion is typically that outlier exclusion should be avoided without a clear rationale why the 'outliers' arise from a clearly discrepant generating process. If it is to be done, the results of the full data should still be presented as the primary analysis (e.g.).
- The cut data by and large doesn't look visually 'outlying' to me. The histogram shows a pretty smooth albeit skewed distribution. Cutting off the tail of the distribution at various lengths appears ill-motivated.
- Given the interest in assessing small study effects, cutting out the largest effects (which also tend to be the smallest studies) should be expected to attenuate the small study effect (as indeed it does). Yet if our working hypothesis is these effects are large mainly
*because*the studies are small, their datapoints are informative to plot this general trend (e.g. for slightly less small studies which have slightly less inflated results).^{[8]}

The strongest argument given is that, in fact, some numerical methods to correct *publication bias* give absurd results if given the full data: i.e. one gives an adjusted effect size of -0.6, another -0.2. I could buy an adjustment that drives the effect down to roughly zero, but not one which suggests, despite almost all the data being fairly or very positive, we should conclude from these studies the real effect is actually (highly!) negative.

One could have a long argument on what the most appropriate response is: maybe just keep it, as the weighted average across methods is still sensible (albeit disappointing)? Maybe just drop those methods in particular and do an average of those giving sane answers on the full data? Should we keep g < 2 exclusion but drop p-curve analysis, as it (absurdly?) adjusts the effect slightly *upwards*? Maybe we should reweigh the averaging of different numerical methods by how volatile their results are when you start excluding data? Maybe pick the outlier exclusion threshold which results in the least disagreement between the different methods? Or maybe just abandon numerical correction, and just say "there's clear evidence of significant small study effects, which the current state of the art cannot reliably quantify and correct"?

So a garden of forking paths opens before us. All of these are varying degrees of 'arguable', and they do shift the bottom line substantially. One reason pre-specification is so valuable is it ties you to a particular path before getting to peek at the results, avoiding any risk a subconscious finger on the scale to push one down a path of still-defensible choices nonetheless favour a particular bottom line. Even if you didn't pre-specify, presenting your *first* cut as the primary analysis helps for nothing up my sleeve reasons.

It may be the prespecified or initial stab doesn't do a good job of expressing the data, and a different approach does better. Yet making it clear this subsequent analysis is post-hoc cautions a reader about potential risk of bias in analysis.

Happily, HLI did make a protocol for this work, made before they conducted the analysis. Unfortunately, it is silent on whether outlying data would be excluded, or by what criteria. Also unfortunately, because of this (and other things like the extensive discussion in the appendix discussing the value of outlier removal principally in virtue of its impact on publication bias correction), I am fairly sure the analysis with all data included was the first analysis conducted. Only after seeing the initial publication bias corrections did HLI look at the question of whether some data should be excluded. Maybe it should, but if it came second the initial analysis should be presented first (and definitely included in the sensitivity analysis).

There's also a risk the cloud of quantification buries the qualitative lede. Publication bias is known to be very hard to correct, and despite HLI compiling multiple numerical state of the art methods, they starkly disagree on what the correction factor should be (i.e. from <~0 to > 100%). So perhaps the right answer is we basically do not know how much to discount the apparent effects seen in the PT literature given it also appears to be an extremely compromised one, and if forced to give an overall number, any 'numerical bottom line' should have even wider error bars because of this.^{[9]}

**Bayesian methods**

I previously complained that the guestimate/BOTEC-y approach HLI used in integrating information from the meta-analysis and the strongminds trial data couldn't be right, as it didn't pass various sanity tests: e.g. still recommending SM as highly effective even if you set the trial data to zero effect. HLI now has a much cleverer Bayesian approach to combining sources of information. On the bright side, this is mechanistically much clearer as well as much cleverer. On the downside, the deck still looks pretty stacked.

Starting at the bottom, here's how HLI's Bayesian method compares SM to GD:

The informed prior (in essence) uses the meta-analysis findings with some monte carlo to get an expected effect for an intervention with strongminds-like traits (e.g. same number of sessions, same deliverer, etc.). The leftmost point of the solid line gives the expectation for the prior: so the prior is that SM is ~4x GDs cost effectiveness (dashed line).

The x axis is how much weight one gives to SM-specific data. Of interest, the line slopes *down, *so the data gives a negative update on SMs cost-effectiveness. This is because HLI - in anticipation of the Baird/Ozler RCT likely showing disappointing results - discounted the effect derived from the original SM-specific evidence by a factor of 20, so the likelihood is indeed much lower than the prior. Standard theory gives the appropriate weighting of this vs. the prior, so you adjust down a bit, but not a lot, from the prior (dotted line).

Despite impeccable methods, these results are facially crazy. To illustrate:

- The rightmost point on the solid line is the result if you completely discount the prior, and only use the stipulated-to-be-bad SM-specific results. SM is
*still*slightly better than GD on this analysis.^{[10]} - If we 'follow Bayesian updating' as HLI recommends, the recommendation is surprisingly insensitive to the forthcoming Baird/Ozler RCT having disappointing findings. Eyeballing it, you'd need such a result to be replicated
*half a dozen times*for the posterior to update to SM is roughly on a par with GD. - Setting the forthcoming data to basically showing
*zero*effect will still return SM is 2-3x GD.^{[11]}I'd guess you'd need the forthcoming RCT to show*astonishingly and absurdly negative*results (e.g. SM treatment is worse for your wellbeing than bereavement), to get it to approximate equipoise with GD. - You'd need even stronger adverse findings for the model to update all the way down to SM being ineffectual, rather than merely 'less good than GiveDirectly'.

I take it most readers would disagree with the model here too - e.g. if indeed the only RCT on strongminds is basically flat, that should be sufficient demote SM from putative 'top charity' status.

I think I can diagnose the underlying problem: Bayesian methods are very sensitive to the stipulated prior. In this case, the prior is likely too high, and definitely too narrow/overconfident. See this:

Per the dashed and dotted lines in the previous figure, the 'GiveDirectly bar' is fractionally below at the blue dashed line (the point estimate of the stipulated-SM data). The prior distribution is given in red. So the expectation (red dashed line) is indeed ~4x further from the origin (see above).

The solid red curve gives the distribution. Eyeballing the integrals reveals the problem: the integral of this distribution from the blue dashed line to infinity gives the models confidence psychotherapy interventions would be more cost-effective than GD. This is at least 99% of the area, if not 99.9% - 99.99%+. A fortiori, this prior asserts it is essentially certain the intervention is beneficial (total effect >0).

I don't think anyone should think that *any *intervention is P > 0.99 more cost-effective than give directly (or P < 0.0001 or whatever it is in fact harmful) as a *prior*,^{[12]} but if one did, it would indeed take masses of evidence to change one's mind. Hence the very sluggish moves in response to adverse data (the purple line suggests the posterior is also 99%+ confident SM is better than givedirectly).

I think I can also explain the underlying problem of this underlying problem. HLI constructs its priors exclusively from its primary meta-analytic model (albeit adapted to match the intervention of interest, and recalculated excluding any studies done on this intervention to avoid double counting). Besides the extra uncertainty (so spread) likely implied by variety of factors covered in the sensitivity analysis, in real life our prior would be informed by other things too: the prospect entire literatures can be misguided, a general sense (at least for me) that cash transfers are easy to beat in principle, but much harder in practice, and so on.

In reality, our prior-to-seeing-the-metaanalysis prior would be very broad and probably reasonably pessimistic, and (even if I'm wrong about the shortcomings I suggest earlier), the 'update' on reading it would be a bit upwards, and a little narrower, but not by that much. In turn, the 'update' on seeing (e.g.) disappointing RCT results for a given PT intervention would be a larger shift downwards, netting out that this was unlikely better than GiveDirectly after all.

If the Bayesian update was meant only to be a neat illustration, I would have no complaint. But instead the bottom line recommendations and assessments rely upon it - that readers should indeed adopt the supposed prior the report proposes about the efficacy of PT interventions in general. Crisply, I doubt the typical reader seriously believes (e.g.) basically any psychotherapy intervention in LMICs, so long as cost per patient is <$100, is a ~certain bet to beat cash transfers. If not, they should question the report's recommendations too.

**Summing up**

Criticising is easier than doing better. But I think this is a case where a basic qualitative description tells the appropriate story, the sophisticated numerical methods are essentially a 'bridge too far' given the low quality of what they have to work with, and so confuse rather than clarify the matter. In essence:

- The literature on PT in LMICs is a complete mess. Insofar as more sense can be made from it, the most important factors appear to belong to the studies investigating it (e.g. their size) rather than qualities of the PT interventions themselves.
- Trying to correct the results of a compromised literature is known to be a nightmare. Here, the qualitative evidence for publication bias is compelling. But quantifying what particular value of 'a lot?' the correction should be is fraught: numerically, methods here disagree with one another dramatically, and prove highly sensitive to choices on data exclusion.
- Regardless of how PT looks in general, Strongminds, in particular, is looking less and less promising. Although initial studies looked good, they had various methodological weaknesses, and a forthcoming RCT with much higher methodological quality is expected to deliver disappointing results.
- The evidential trajectory here is all to common, and the outlook typically bleak. It is dubious StrongMinds is a good pick even among psychotherapy interventions (picking one at random which
*doesn't*have a likely-bad-news RCT imminent seems a better bet). Although pricing different interventions is hard, it is even more dubious SM is close to the frontier of "very well evidenced" vs. "has very promising results" plotted out by things like AMF, GD, etc. HLI's choice to nonetheless recommend SM again this giving season is very surprising. I doubt it will weather hindsight well.

^{^}All of the figures are taken from the report and appendix. The transparency is praiseworthy, although it is a pity despite largely looking at the right things the report often mistakes the right conclusions to draw.

^{^}With all the well-worn caveats about measuring well-being.

^{^}The Cochrane handbook section on meta-analysis is very clear on this (but to make it clearer, I add emphasis)

**10.1 Do not start here!***It can be tempting to jump prematurely into a statistical analysis when undertaking a systematic review.*The production of a diamond at the bottom of a plot is an exciting moment for many authors,*but results of meta-analyses can be very misleading*if suitable attention has not been given to formulating the review question; specifying eligibility criteria; identifying and selecting studies; collecting appropriate data;*considering risk of bias*; planning intervention comparisons;*and deciding what data would be meaningful to analyse*. Review authors should consult the chapters that precede this one before a meta-analysis is undertaken.^{^}As a WIP, the data and code for this report is not yet out, but in my previous statistical noodling on the last one both study size and registration status significantly moderated the effect downwards when included together, suggesting indeed the former isn't telling you everything re. study quality.

^{^}The report does mention later (S10.2) controlling a different analysis for study quality, when looking at the effect of sample size itself:

To test for scaling effects, we add sample size as a moderator into our meta-analysis and find that for every extra 1,000 participants in a study the effect size decreases (non-significantly) by -0.09 (95% CI: -0.206, 0.002) SDs. Naively, this suggests that deploying psychotherapy at scale means its effect will substantially decline. However, when we control for study characteristics and quality, the coefficient for sample size decreases by 45% to -0.055 SDs (95% CI: -0.18, 0.07) per 1,000 increase in sample size. This suggests to us that, beyond this finding being non-significant, the effect of scaling can be controlled away with quality variables, more of which that we haven’t considered might be included.

I don't think this analysis is included in the appendix or similar, but later text suggests the 'study quality' correction is a publication bias adjustment. This analysis is least fruitful when applied to study scale, as measures of publication bias are measures of study size: so finding the effects of study scale are attenuated when you control for a proxy of study scale is uninformative.

What would be informative is the impact measures of 'study scale' or publication bias have on the coefficients for the primary moderators. Maybe they too could end up 'controlled away with quality variables, more of which that we haven't considered might be included'?

^{^}There are likely better explanations of funnel plots etc. online, but my own attempt is here.

^{^}The report charts a much wiser course on a different "Outlier?" question: whether to include very long follow-up studies, where

*exclusion*would cut the total effect in half. I also think including everything here is fine too, but the report's discussion in S4.2 clearly articulates the reason for concern, displays what impact inclusion vs. exclusion has, and carefully interrogates the outlying studies to see whether they have features (beyond that they report 'outlying' results) which warrants exclusion. They end up going 'half-and-half', but consider both full exclusion and inclusion in sensitivity analysis.^{^}If you are using study size as an (improvised) measure of study quality, excluding the smallest studies because on an informal read they are particularly low quality makes little sense: this is the trend you are interested in.

^{^}A similar type of problem crops up when one is looking at the effect of 'dosage' on PT efficacy.

The solid lines are the fit (blue linear, orange log) on the full data, whilst the dashed lines are fits with extreme values of dosage - small or large - excluded (purple). The report freely concedes its choices here are very theory led rather than data driven - and also worth saying getting

*more*of a trend here makes a rod for SM and Friendship Bench's back, as these deliver smaller numbers of sessions than the average, so adjusting with the dashed lines and not the solid ones reduces the expected effect.Yet the main message I would take from the scatter plot is the data indeed looks very flat, and there is no demonstrable dose-response relationship of PT. Qualitatively, this isn't great for face validity.

^{^}To its credit, the write-up does highlight this, but does not seem to appreciate the implications are crazy: any PT intervention, so long as it is cheap enough, should be thought better than GD, even if studies upon it show very low effect size (which would usually be reported as a negative result, as almost any study in this field would be underpowered to detect effects as low as are being stipulated):

Therefore, even if the StrongMinds-specific evidence finds a small total recipient effect (as we present here as a placeholder), and we relied solely on this evidence, then it would still result in a cost-effectiveness that is similar or greater than that of GiveDirectly because StrongMinds programme is very cheap to deliver.

^{^}The report describes this clearly itself, but seems to think this is a feature rather than a bug (my emphasis):

Now, one might argue that the results of the Baird et al. study could be lower than 0.4 WELLBYs. But – assuming the same weights are given to the prior and the charity-specific data as in our analysis -

*even if the Baird et al. results were 0.05 WELLBYs (extremely small), then the posterior would still be 1.49 * 0.84 + 0.05 * 0.16 = 1.26 WELLBYs*; namely, very close to our current posterior (1.31 WELLBYs).^{^}I'm not even sure that "P > 0.99 better than GD" would be warranted as posterior even for a Givewell recommended top charity, and I'd guess the GW staff who made the recommendation would often agree.

I agree - all else equal - you'd rather have a flatter distribution of donors for the diversification (various senses) benefits. I doubt this makes this an important objective all things considered.

The main factor on the other side of the scale is scale itself: a 'megadonor' can provide a lot of support. This seems to be well illustrated by your original examples (Utility Farm and Rethink). Rethink started later, but grew much 100x larger, and faster too. I'd be surprised if folks at UF would not prefer Rethink's current situation, trajectory - and fundraising headaches - to their own.

In essence, there should be some trade-off between 'aggregate $' and 'diversity of funding sources' (however cashed out) - pricing in (e.g.) financial risks/volatility for orgs, negative externalities on the wider ecosystem, etc. I think the trade between 'perfectly singular support' and 'ideal diversity of funding sources' would be much less than an integer factor, and more like 20% or so (i.e. maybe better getting a budget of 800k from a reasonably-sized group than 1M from a single donor, but not better than 2M from the same).

I appreciate the recommendation here is to complement existing practice with a cohort of medium sized donors, but the all things considered assessment is important to gauge the value of marginal (or not-so-marginal) moves in this direction. Getting (e.g.) 5000 new people giving 20k a year seems a huge lift to me. Even if that happens, OP still remains the dominant single donor (e.g. it gave roughly the amount this hypothetical cohort would to animal causes alone in 2022). A diffuse 'ecosystem wide' benefits of these additional funders struggles by my lights to vindicate the effort (and opportunity costs) of such a push.

I'm not sure I count as 'senior', but I could understand some reluctance even if 'all expenses paid'.

I consider my EAG(x) participation as an act of community service. Although there are diffuse benefits, I do not get that much out of it myself, professionally speaking. This is not that surprising: contacts at EAG (or knowledge at EAG, etc. etc.) matter a lot less on the margin of several years spent working in the field than just starting out. I spend most of my time at EAG trying to be helpful - typically, through the medium of several hours of 1-1s each day. I find this fulfilling, but not leisurely.

So from the selfish perspective EAG feels pretty marginal either re. 'professional development' or 'fun'. I'd guess many could be dissuaded by small frictions. Non-hub locations probably fit the bill: "Oh, I could visit [hub] for EAG, and meet my professional contacts in [hub] whilst I'm in town" is a lot more tempting to the minds eye than a dedicated trip for EAG alone.

Hello Jason,

With apologies for delay. I agree with you that I am asserting HLI's mistakes have further 'aggravating factors' which I also assert invites highly adverse inference. I had hoped the links I provided provided clear substantiation, but demonstrably not (my bad). Hopefully my reply to Michael makes them somewhat clearer, but in case not, I give a couple of examples below with as best an explanation I can muster.

I will also be linking and quoting extensively from the Cochrane handbook for systematic reviews - so hopefully even if my attempt to clearly explain the issues fail, a reader can satisfy themselves my view on them agrees with expert consensus. (Rather than, say, "Cantankerous critic with idiosyncratic statistical tastes flexing his expertise to browbeat the laity into aquiescence".)

0) Per your remarks, there's various background issues around reasonableness, materiality, timeliness etc. I think my views basically agree with yours. In essence: I think HLI is significantly 'on the hook' for work (such as the meta-analysis) it relies upon to make recommendations to donors - who will likely be taking HLI's representations on its results and reliability (cf. HLI's remarks about its 'academic research', 'rigour' etc.) on trust. Discoveries which threaten the 'bottom line numbers' or overall reliability of this work should be addressed with urgency and robustness appropriate to their gravity. "We'll put checking this on our to-do list" seems fine for an analytic choice which might be dubious but of unclear direction and small expected magnitude. As you say, a typo which where corrected reduces the bottom line efficacy by ~ 20% should be done promptly.

The two problems I outlined 6 months ago each should have prompted withdrawal/suspension of both the work and the recommendation unless and until they were corrected.^{[1]} Instead, HLI has not made appropriate corrections, and instead persists in misguiding donations and misrepresenting the quality of its research on the basis of work it has partly acknowledged (and which reasonable practicioners would overwhelmingly concur) was gravely compromised.^{[2]}

1.0) **Publication bias/Small study effects**

It is commonplace in the literature for smaller studies to show different (typically larger) effect sizes than large studies. This is typically attributed to a mix of factors which differentially inflate effect size in smaller studies (see), perhaps the main one being publication bias: although big studies are likely to be published "either way", investigators may not finish (or journals may not publish) smaller studies reporting negative results.

It is *extremely* well recognised that these effects can threaten the validity of meta-analysis results. If you are producing something (very roughly) like an 'average effect size' from your included studies, the studies being selected for showing a positive effect means the average is inflated upwards. This bias is very difficult to reliably adjust for or 'patch' (more later), but it can easily be large enough to mean "Actually, the treatment has no effect, and your meta-analysis is basically summarizing methodological errors throughout the literature".

Hence why most work on this topic stresses the importance of arduous efforts in prevention (e.g trying really hard to find 'unpublished' studies) and diagnosis (i.e. carefully checking for statistical evidence of this problem) rather than 'cure' (see eg.). If a carefully conducted analysis nonetheless finds stark small study effects, this - rather than the supposed ~'average' effect - would typically be (and should definitely be) the main finding: "The literature is a complete mess - more, and much better, research needed".

As in many statistical matters, a basic look at your data can point you in the right direction. For meta-analysis, this standard is a forest plot:

To orientate: each row is a study (presented in order of increasing effect size), and the horizontal scale is effect size (where to the right = greater effect size favouring the intervention). The horizontal bar for each study is gives the confidence interval for the effect size, with the middle square marking the central estimate (also given in the rightmost column). The diamond right at the bottom is the pooled effect size - the (~~)^{[3]} average effect across studies mentioned earlier.

Here, the studies are all over the map, many of which do not overlap with one another, nor with the pooled effect size estimate. In essence, dramatic *heterogeneity*: the studies are reporting very different effect sizes from another. Heterogeneity is basically a fact of life in meta-analysis, but a forest plot like this invites curiousity (or concern) about why effects are varying quite *this* much. [I'm going to be skipping discussion of formal statistical tests/metrics for things like this for clarity - you can safely assume a) yes, you can provide more rigorous statistical assessment of 'how much' besides 'eyeballing it' - although visually obvious things are highly informative, b) the things I mention you can see are indeed (highly) statistically significant etc. etc.]

There are some hints from this forest plot that small study effects could have a role to play. Although very noisy, larger studies (those with narrower horizontal lines lines, because bigger study ~ less uncertainty in effect size) tend to be higher up the plot and have smaller effects. There is a another plot designed to look at this better - a funnel plot.

To orientate: each study is now a point on a scatterplot, with effect size again on the x-axis (right = greater effect). The y-axis is now the standard error: bigger studies have greater precision, and so lower sampling error, so are plotted higher on the y axis. Each point is a single study - all being well, the scatter should look like a (symmetrical) triangle or funnel like those being drawn on the plot.

All is not well here. The scatter is clearly asymmetric and sloping to the right - smaller studies (towards the bottom of the graph) tend towards greater effect sizes. The lines being drawn on the plot make this even clearer. Briefly:

- The leftmost 'funnel' with shaded wings is centered on an effect size of zero (i.e. zero effect). The white middle triangle are findings which would give a p value of > 0.05, and the shaded wings correspond to a p value between 0.05 ('statistically significant') and 0.01: it is an upward-pointing triangle because bigger studies can detect find smaller differences from zero as 'statistically significant' than smaller ones. There appears to be clustering in the shaded region, suggestive that studies may be being tweaked to get them 'across the threshold' of statistically significant effects.
- The rightmost 'funnel' without shading is centered on the pooled effect estimate (0.5). Within the triangle is where you would expect 95% of the scatter of studies to fall in the absence of heterogeneity (i.e. there was just one true effect size, and the studies varied from this just thanks to sampling error). Around half are outside this region.
- The red dashed line is the best fit line through the scatter of studies. If there weren't small study effects, it would be basically vertical. Instead, it slopes off heavily to the right.

Although a very asymmetric funnel plot is not proof positive of publication bias, findings like this demand careful investigation and cautious interpretation (see generally). It is challenging to assess exactly 'how big a deal is it, though?': statistical adjustiment for biases in the original data is extremely fraught.

But we are comfortably in 'big deal' territory: this finding credibly up-ends HLI's entire analysis:

a) There are different ways of getting a 'pooled estimate' (~~average, or ~~ typical effect size): *random effects* (where you assume the true effect is rather a distribution of effects from which each study samples from), vs. *fixed effects *(where there is a single value for the true effect size). Random effects are commonly preferred as - in reality - one expects the true effect to vary, but the results are much more vulnerable to any small study effects/publication bias (see generally). Comparing the random effect vs. the fixed effect estimate can give a quantitative steer on the possible scale of the problem, as well as guide subsequent analysis.^{[4]} Here, the random effect estimate is 0.52, whilst the fixed one is less than half the size: 0.18.

b) There are other statistical methods you could use (more later). One of the easier to understand (but one of the most conservative) goes back to the red dashed line in the funnel plot. You could extrapolate from it to the point where standard error = 0: so the predicted effect of an infinitely large (so infinitely precise) study - and so also where the 'small study effect' is zero. There are a few different variants of these sorts of 'regression methods', but the ones I tried predict effect sizes of such a hypothetical study between 0.17 and 0.05. So, quantitatively, 70-90% cuts of effect size are on the table here.

c) A reason why regression methods methods are conservative as they will attribute as much variation in reported results as possible to differences in study size. Yet there could be alternative explanations for this besides publication bias: maybe smaller studies have different patient populations with (genuinely) greater efficacy, etc.

However, this statistical confounding can go the other way. HLI is not presenting simple meta-analytic results, but rather meta-*regressions*: where the differences in reported effect sizes are being predicted by differences between and within the studies (e.g. follow-up time, how much therapy was provided, etc.). One of HLI's findings from this work is that psychotherpy with *Strongminds-like traits* is ~70% more effective than psychotherapy *in general* (0.8 vs. 0.46). If this is because factors like 'group or individual therapy' correlate with study size, the real story for this could simply be: "Strongminds-like traits are indicators for methodological weaknesses which greatly inflate true effect size, rather than for a more effective therapeutic modality." In HLI's analysis, the latter is presumed, giving about a ~10% uplift to the bottom line results.^{[5]}

1.2) **A major issue, and a major mistake to miss**

So this is a big issue, and would be revealed by standard approaches. HLI instead used a very non-standard approach (see), novel - as far as I can tell - to existing practice and, unfortunately, inappropriate (cf., point 5): it gives ~ a 10-15% discount (although I'm not sure this has been used in the *Strongminds* assessment, although it is in the psychotherapy one).

I came across these problems ~6m ago, prompted by a question by Ryan Briggs (someone with considerably greater expertise than my own) asking after the forest and funnel plot. I also started digging into the data in general at the same time, and noted the same key points explained labouriously above: looks like marked heterogeneity and small study effects, they look very big, and call the analysis results into question. Long story short, they said they would take a look at it urgently then report back.

This response is fine, but as my comments then indicated, I did have (and I think reasonably had) HLI on pretty thin ice/'epistemic probation' after finding these things out. You have to make a lot of odd choices to end up this far from normal practice, nonetheless still have to make some surprising oversights too, to end up missing problems which would appear to greatly undermine a positive finding for Strongminds.^{[6]}

1.3) **Maintaining this major mistake**

HLI fell through this thin ice after its follow-up. Their approach was to try a bunch of statistical techniques to adjust for publication bias (excellent technique), do the same for their cash transfers meta-analysis (sure), then using the relative discounts between them to get an adjustment for psychotherapy vs. cash transfers (good, esp. as adding directly into the multi-level meta-regressions would be difficult). Further, they provided full code and data for replication (great). But the results made no sense whatsoever:

To orientate: each row is a different statistical technique applied to the two meta-analyses (more later). The x-axis is the 'multiple' of Strongminds vs. cash transfers, and the black line is at 9.4x, the previous 'status quo value'. Bars shorter than this means adjusting for publication bias results in an overall discount for Strongminds, and vice-versa.

The cash transfers funnel plot looks like this:

Compared to the psychotherapy one, it basically looks fine: the scatter looks roughly like a funnel, and no massive trend towards smaller studies = bigger effects. So how could so many statistical methods discount the 'obvious small study effect' meta-analysis *less* than the 'no apparent small study effect' meta-analysis, to give an *increased* multiple? As I said at the time, the results look like nonsense to the naked eye.

One problem was a coding error in two of the statistical methods (blue and pink bars). The bigger problem is how the comparisons are being done is highly misleading.

Take a step back from all the dividing going on to just look at the effect sizes. The basic, nothing fancy, random effects model applied to the psychotherapy data gives an effect size of 0.5. If you take the average across all the other model variants, you get ~0.3, a 40% drop. For the cash transfers meta-analysis, the basic model gives 0.1, and the average of all the other models is ~0.9, a 10% drop. So in fact you are seeing - as you should - bigger discounts when adjusting the psychotherapy analysis vs. the cash transfers meta-analysis. This is lost by how the divisions are being done, which largely 'play off' multiple adjustments against one another. (see, pt.2). What the graph should look like is this:

Two things are notable: 1) the different models tend to point to a significant drop (~30-40% on average) in effect size; 2) there is a lot of variation in the discount - from ~0 to ~90% (so visual illustration about why this is known to be v. hard to reliably 'adjust'). I think these results oblige something like the following:

**Re. write-up: **At least including the forest and funnel plots, alongside a description of why they are concerning. Should also include some 'best guess' correction from the above, and noting this has a (very) wide range. Probably warrants 'back to the drawing board' given reliability issues.

**Re. overall recommendation: **At least a very heavy astericks placed besides the recommendation**. **Should also highlight both the adjustment and uncertainty in front facing materials (e.g. 'tentative suggestion' vs. 'recommendation'). Probably warrants withdrawal.

**Re. general reflection: **I think a reasonable evaluator - beyond directional effects - would be concerned about the 'near'(?) miss property of having a major material issue not spotted before pushing a strong recommendation, 'phase 1 complete/mission accomplished' etc. - especially when found by a third party many months after initial publication. They might also be concerned about the direction of travel. When published, the multiplier was 12x; with spillovers, it falls to 9.5%; with spillovers and the typo corrected, it falls to 7.5x; with a 30% best guess correction for publication bias, we're now at 5.3x. Maybe any *single* adjustment is not recommendation-reversing, but in concert they are, and the track record suggests the next one is more likely to be further down rather than back up.

What happened instead 5 months ago was HLI would read some more and discuss among themselves whether my take on the comparators was the right one (I am, and it is not reasonably controversial, e.g. 1, 2, cf. fn4). Although 'looking at publication bias is part of their intended 'refining' of the Strongminds assessment, there's been nothing concrete done yet.

Maybe I should have chased, but the exchange on this (alongside the other thing) made me lose faith that HLI was capable of reasonably assessing and appropriately responding to criticisms of their work when material to their bottom line.

**2) The cost effectiveness guestimate.**

[Readers will be relieved ~no tricky stats here]

As I was looking at the meta-analysis, I added my attempt at 'adjusted' effect sizes of the same into the CEA to see what impact they had on the results. To my surprise, not very much. Hence my previous examples about 'Even if the meta-analysis has zero effect the CEA still recommends Strongminds as several times GD', and 'You only get to equipoise with GD if you set all the effect sizes in the CEA to near-zero.'

I noted this alongside my discussion around the meta-analysis 6m ago. Earlier remarks from HLI suggested they accepted these were diagnostic of something going wrong with how the CEA is aggregating information (but fixing it would be done but not as a priority); more recent ones suggest more 'doubling down'.

In any case, they are indeed diagnostic for a lack of face validity. You obviously* *would, in fact, be highly sceptical if the meta-analysis of psychotherapy in general was zero (or harmful!) that nonetheless a particular psychotherapy intervention was extremely effective. The (pseudo-)bayesian gloss on why is that the distribution of reported effect sizes gives additional information on the likely size of the 'real' effects underlying them. (cf. heterogeneity discussed above) A bunch of weird discrepancies among them, if hard to explain by intervention characteristics, increases the suspicion of weird distortions, rather than true effects, underlie the observations. So increasing discrepancy between indirect and direct evidence should reduce effect size beyond impacts on any weighted average.

It does not help the findings *as-is* are highly discrepant and generally weird. Among many examples:

- Why are the strongminds like trials in the direct evidence having among the greatest effects of any of the studies included - and ~1.5x-2x the effect of a regression prediction of studies with strongminds-like traits?
- Why are the most strongminds-y studies included in the meta-analysis marked outliers - even after 'correction' for small study effects?
- What happened between the original Strongminds Phase 2 and the Strongminds RCT to up the intevention efficacy by 80%?
- How come the only study which compares psychotherapy to a cash transfer comparator is also the only study which gives a negative effect size?

I don't know what the magnitude of the directional 'adjustment' would be, as this relies on specific understanding of the likelier explanations for the odd results (I'd guess a 10%+ downward correction assuming I'm wrong about everything else - obviously, much more if indeed 'the vast bulk in effect variation can be explained by sample size +/- registration status of the study). Alone, I think it mainly points to the quantative engine needing an overhaul and the analysis being known-unreliable until it is.

In any case, it seems urgent and important to understand and fix. The numbers are being widely used and relied upon (probably all of them need at least a big public astericks pending developing more reliable technique). It seems particularly unwise to be reassured by "Well sure, this is a downward correction, but the CEA still gives a good bottom line multiple", as the bottom line number may not be reasonable, especially conditioned on different inputs. Even more so to persist in doing so 6m after being made aware of the problem.

^{^}These are mentioned in 3a and 3b of my reply to Michael. Point 1 there (kind of related to 3a) would on its own warrant immediate retraction, but that is not a case (yet) of 'maintained' error.

^{^}So in terms of 'epistemic probation', I think this was available 6m ago, but closed after flagrant and ongoing 'violations'.

^{^}One quote from the Cochrane handbook feels particularly apposite:

**Do not start here!**It can be tempting to jump prematurely into a statistical analysis when undertaking a systematic review. The production of a diamond at the bottom of a plot is an exciting moment for many authors, but results of meta-analyses can be very misleading if suitable attention has not been given to formulating the review question; specifying eligibility criteria; identifying and selecting studies; collecting appropriate data; considering risk of bias; planning intervention comparisons; and deciding what data would be meaningful to analyse. Review authors should consult the chapters that precede this one before a meta-analysis is undertaken.

^{^}In the presence of heterogeneity, a random-effects meta-analysis weights the studies relatively more equally than a fixed-effect analysis (see Chapter 10, Section 10.10.4.1). It follows that in the presence of small-study effects, in which the intervention effect is systematically different in the smaller compared with the larger studies, the random-effects estimate of the intervention effect will shift towards the results of the smaller studies. We recommend that when review authors are concerned about the influence of small-study effects on the results of a meta-analysis in which there is evidence of between-study heterogeneity (I2 > 0), they compare the fixed-effect and random-effects estimates of the intervention effect. If the estimates are similar, then any small-study effects have little effect on the intervention effect estimate. If the random-effects estimate has shifted towards the results of the smaller studies, review authors should consider whether it is reasonable to conclude that the intervention was genuinely different in the smaller studies, or if results of smaller studies were disseminated selectively. Formal investigations of heterogeneity may reveal other explanations for funnel plot asymmetry, in which case presentation of results should focus on these. If the larger studies tend to be those conducted with more methodological rigour, or conducted in circumstances more typical of the use of the intervention in practice, then review authors should consider reporting the results of meta-analyses restricted to the larger, more rigorous studies.

^{^}This is not the only problem in HLI's meta-regression analysis. Analyses here should be pre-specified (

*especially*if intended as the primary result rather than some secondary exploratory analysis), to limit risks of inadvertently cherry-picking a model which gives a preferred result. Cochrane (see):Authors should, whenever possible, pre-specify characteristics in the protocol that later will be subject to subgroup analyses or meta-regression. The plan specified in the protocol should then be followed (data permitting), without undue emphasis on any particular findings (see MECIR Box 10.11.b). Pre-specifying characteristics reduces the likelihood of spurious findings, first by limiting the number of subgroups investigated, and second by preventing knowledge of the studies’ results influencing which subgroups are analysed. True pre-specification is difficult in systematic reviews, because the results of some of the relevant studies are often known when the protocol is drafted. If a characteristic was overlooked in the protocol, but is clearly of major importance and justified by external evidence, then authors should not be reluctant to explore it. However, such post-hoc analyses should be identified as such.

HLI does not mention any

*pre*-specification, and there is good circumstantial evidence of a lot of this work being ad hoc re. 'Strongminds-like traits'. HLI's earlier analysis on psychotherapy in general, using most (?all) of the same studies as in their Strongminds CEA (4.2, here), had different variables used in a meta-regression on intervention properties (table 2). It seems likely the change of model happened after study data was extracted (the lack of significant prediction and including a large number of variables for a relatively small number of studies would be further concerns). This modification seems to favour the intervention: I think the earlier model, if applied to Strongminds, gives an effect size of ~0.6.^{^}Briggs comments have a similar theme, suggestive that my attitude does not solely arise from particular cynicism on my part.

Here's the OWID charts for life satisfaction vs. GDP/capita. First linear (per the dovecote model):

Now with a log transform to GDP/capita (per the MHR):

I think it is visually clear the empirical relationship is better modelled as log-linear rather than linear. Compared to this, I don't think the regression diagnostics suggesting non-inferiority of linear GDP (in the context of model selected from thousands of variables, at least some of which could log-linearly proxy for GDP, cf. Dan_Key's comment) count for much.

Besides the impact of GDP (2.5% versus 40%), I'd expect which other variables end up being selected also to be sensitive to this analysis choice. Unfortunately, as it is the wrong one, I'd expect (quasi-)omitted variable bias to distort both which variables are included, and their relative contributions, in the dovecote model.