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I think it's because the standard practices of scientific publishing are very laborious and EA wants to be a bit more agile. 

Having said that I strongly agree that more peer-review is called for in EA, even if we don't move all the way to the extreme of the academic world.

Nope, I've not heard from any current HLI members regarding this in public or private.

A professional psychotherapy researcher, or even just a psychotherapist, would be more appropriate than a psychiatrist no?

Hello Alex,

Reading back on the sentence, it would have been better to put 'many' rather than 'all'. I've updated it accordingly. TLYCS don't mention WELLBYs, but they did make the comment "we will continue to rely heavily on the research done by other terrific organizations in this space, such as GiveWell, Founders Pledge, Giving Green, Happier Lives Institute [...]".

It's worth restating the positives. A number of organisations have said that they've found our research useful. Notably, see the comments by Matt Lerner (Research Director, Founders Pledge) below and also those from Elie Hassenfield (CEO, GiveWell), which we included in footnote 3 above. If it wasn't for HLI's work pioneering the subjective wellbeing approach and the WELLBY, I doubt these would be on the agenda in effective altruism. 

Thanks for editing Michael. Fwiw I am broadly on board with swb being a useful framework to answer some questions. But I don’t think I’ve shifted my opinion on that much so “coming round to it” didn’t resonate

My view is that HLI^[1], GWWC^[2], Founders Pledge^[3], and other EA / effective giving orgs that recommend or provide StrongMinds as an donation option should ideally at least update their page on StrongMinds to include relevant considerations from this RCT, and do so well before Thanksgiving / Giving Tuesday in Nov/Dec this year, so donors looking to decide where to spend their dollars most cost effectively can make an informed choice.^[4]

1. ^{^}

   Listed as a top recommendation

2. ^{^}

   Not currently a recommendation, (but to included as an option to donate)

3. ^{^}

   Currently tagged as an "active recommendation"

^{^}

Acknowledging that HLI's current schedule is "By Dec 2024", though this may only give donors 3 days before Giving Tuesday.

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Thanks for this Gregory, I think it's an important result and have updated my views. I'm not sure why HLI were so optimistic about this. I have a few comments here.

1. This study was performed on adolescents, which is not the core group of women that Strong Minds and other group IPT programs treat. This study might update me slightly negatively against the effectof their core programming with groups of older women but not by much.

As The study said, "this marked the first time SMU (i) delivered therapy to out-of-school adolescent females, (ii) used youth mentors, and (iii) delivered therapy through a partner organization."

This result then doesn't surprise me as (high uncertainty) I think it's generally harder to move the needle with adolescent mental health than with adults.

2. The therapy still worked, even though the effect sizes were much smaller than other studies and were not cost effective.

3. As you've said before, f this kind of truly independent research was done on a lot of interventions, the results might not look nearly as good as the original studies.

4. I think Strongminds should probably stop their adolescent programs based on this study. Why keep doing it, when your work with adult women currently seems far more cost effective?

5. Even with the Covid caveat, I'm stunned at the null/negative effect of the cash transfer arm. Interesting stuff and not sure what to make of it.

6. I would still love a similar independent study on the regular group IPT programs with older women, and these RCTs should be pretty cheap on the scale of things, I doubt we'll get that though as it will probably seen as being too similar and not interesting enough for researchers which is fair enough.

Hello Michael,

Thanks for your reply. In turn:

1: 

HLI has, in fact, put a lot of weight on the d = 1.72 Strongminds RCT. As table 2 shows, you give a weight of 13% to it - joint highest out of the 5 pieces of direct evidence. As there are ~45 studies in the meta-analytic results, this means this RCT is being given equal or (substantially) greater weight than any other study you include. For similar reasons, the Strongminds phase 2 trial is accorded the third highest weight out of all studies in the analysis.

HLI's analysis explains the rationale behind the weighting of "using an appraisal of its risk of bias and relevance to StrongMinds’ present core programme". Yet table 1A notes the quality of the 2020 RCT is 'unknown' - presumably because Strongminds has "only given the results and some supporting details of the RCT". I don't think it can be reasonable to assign the highest weight to an (as far as I can tell) unpublished, not-peer reviewed, unregistered study conducted by Strongminds on its own effectiveness reporting an astonishing effect size - before it has even been read in full. It should be dramatically downweighted or wholly discounted until then, rather than included at face value with a promise HLI will followup later.

Risk of bias in this field in general is massive: effect sizes commonly melt with improving study quality. Assigning ~40% of a weighted average of effect size to a collection of 5 studies, 4 [actually 3, more later] of which are (marked) outliers in effect effect, of which 2 are conducted by the charity is unreasonable. This can be dramatically demonstrated from HLI's own data: 

One thing I didn't notice last time I looked is HLI did code variables on study quality for the included studies, although none of them seem to be used for any of the published analysis. I have some good news, and some very bad news. 

The good news is the first such variable I looked at, ActiveControl, is a significant predictor of greater effect size. Studies with better controls report greater effects (roughly 0.6 versus 0.3). This effect is significant (p = 0.03) although small (10% of the variance) and difficult - at least for me - to explain: I would usually expect worse controls to widen the gap between it and the intervention group, not narrow it. In any case, this marker of study quality definitely does not explain away HLI's findings. 

The second variable I looked at was 'UnpubOr(pre?)reg'.^[1] As far as I can tell, coding 1 means something like 'the study was publicly registered' and 0 means it wasn't (I'm guessing 0.5 means something intermediate like retrospective registration or similar) - in any case, this variable correlates extremely closely (>0.95) to my own coding of whether a study mentions being registered or not after reviewing all of them myself. If so, using it as a moderator makes devastating reading:^[2]

To orientate: in 'Model results' the intercept value gives the estimated effect size when the 'unpub' variable is zero (as I understand it, ~unregistered studies), so d ~ 1.4 (!) for this set of studies. The row below gives the change in effect if you move from 'unpub = 0' to 'unpub = 1' (i.e. ~ registered vs. unregistered studies): this drops effect size by 1, so registered studies give effects of ~0.3. In other words, unregistered and registered studies give dramatically different effects: study registration reduces expected effect size by a factor of 3. [!!!]

The other statistics provided deepen the concern. The included studies have a very high level of heterogeneity (~their effect sizes vary much more than they should by chance). Although HLI attempted to explain this variation with various meta-regressions using features of the intervention, follow-up time, etc., these models left the great bulk of the variation unexplained. Although not like-for-like, here a single indicator of study quality provides compelling explanation for why effect sizes differ so much: it explains three-quarters of the initial variation.^[3]

This is easily seen in a grouped forest plot - the top group is the non registered studies, the second group the registered ones:

This pattern also perfectly fits the 5 pieces of direct evidence: Bolton 2003 (ES = 1.13), Strongminds RCT (1.72), and Strongminds P2 (1.09) are, as far as I can tell, unregistered. Thurman 2017 (0.09) was registered. Bolton 2007 is also registered, and in fact has an effect size of ~0.5, not 1.79 as HLI reports.^[4]

To be clear, I do not think HLI knew of this before I found it out just now. But results like this indicate i) the appraisal of the literature in this analysis gravely off-the-mark - study quality provides the best available explanation for why some trials report dramatically higher effects than others; ii) the result of this oversight is a dramatic over-estimation of likely efficacy of Strongminds (as a ready explanation for the large effects reported in the most 'relevant to strongminds' studies is that these studies were not registered and thus prone to ~200%+ inflation of effect size); iii) this is a very surprising mistake for a diligent and impartial evaluator to make: one would expect careful assessment of study quality - and very sceptical evaluation where this appears to be lacking - to be foremost, especially given the subfield and prior reporting from Strongminds both heavily underline it. This pattern, alas, will prove repetitive.

I also think a finding like this should prompt an urgent withdrawal of both the analysis and recommendation pending further assessment. In honesty, if this doesn't, I'm not sure what ever could. 

2: 

Indeed excellent researchers overlook things, and although I think both the frequency and severity of things HLI mistakes or overlooks is less-than-excellent, one could easily attribute this to things like 'inexperience', 'trying to do a lot in a hurry', 'limited staff capacity', and so on. 

Yet this cannot account for how starkly asymmetric the impact of these mistakes and oversights are. HLI's mistakes are consistently to Strongmind's benefit rather than its detriment, and HLI rarely misses a consideration which could enhance the 'multiple', it frequently misses causes of concern which both undermine both strength and reliability of this recommendation. HLI's award from Givewell deepens my concerns here, as it is consistent with a very selective scepticism: HLI can carefully scruitinize charity evaluations by others it wants to beat, but fails to mete out remotely comparable measure to its own which it intends for triumph. 

I think this can also explain how HLI responds to criticism, which I have found by turns concerning and frustrating. HLI makes some splashy claim (cf. 'mission accomplished', 'confident recommendation', etc.). Someone else (eventually) takes a closer look, and finds the surprising splashy claim, rather than basically checking out 'most reasonable ways you slice it', it is highly non-robust, and only follows given HLI slicing it heavily in favour of their bottom line in terms of judgement or analysis - the latter of which often has errors which further favour said bottom line. HLI reliably responds, but the tenor of this response is less 'scientific discourse' and more 'lawyer for defence': where it can, HLI will too often further double down on calls it makes where I aver the typical reasonable spectator would deem at best dubious, and at worst tendentious; where it can't, HLI acknowledges the shortcoming but asserts (again, usually very dubiously) that it isn't that a big deal, so it will deprioritise addressing it versus producing yet more work with the shortcomings familiar to those which came before.    

3:

HLI's meta-analysis in no way allays or rebuts the concerns SimonM raised re. Strongminds - indeed, appropriate analysis would enhance many of them. Nor is it the case that the meta-analytic work makes HLI's recommendation robust to shortcomings in the Strongminds-specific evidence - indeed, the cost effectiveness calculator will robustly recommend Strongminds as superior (commonly, several times superior) to GiveDirectly almost no matter what efficacy results (meta-analytic or otherwise) are fed into it. On each.

a) Meta-analysis could help contextualize the problems SimonM identifies in the Strongminds specific data. For example, a funnel plot which is less of a 'funnel' but more of a ski-slope (i.e. massive small study effects/risk of publication bias), and a contour/p-curve suggestive of p-hacking would suggest the field's literature needs to be handled with great care. Finding 'strongminds relevant' studies and direct evidence are marked outliers even relative to this pathological literature should raise alarm given this complements the object-level concerns SimonM presented.

This is indeed true, and these features were present in the studies HLI collected, but HLI failed to recognise it. It may never have if I hadn't gotten curious and did these analyses myself. Said analysis is (relative to the much more elaborate techniques used in HLI's meta-analysis) simple to conduct - my initial 'work' was taking the spreadsheet and plugging it into a webtool out of idle curiosity.^[5] Again, this is a significant mistake, adds a directional bias in favour of Strongminds, and is surprising for a diligent and impartial evaluator to make.  

b) In general, incorporating meta-analytic results into what is essentially a weighted average alongside direct evidence does not clean either it or the direct evidence of object level shortcomings. If (as here) both are severely compromised, the result remains unreliable. 

The particular approach HLI took also doesn't make the finding more robust, as the qualitative bottom line of the cost-effectiveness calculation is insensitive to the meta-analytic result. As-is, the calculator gives strongminds as roughly 12x better than GiveDirectly.^[6] If you set both meta-analytic effect sizes to zero, the calculator gives Strongminds as ~7x better than GiveDirectly. So the five pieces of direct evidence are (apparently) sufficient to conclude SM is an extremely effective charity. Obviously this is - and HLI has previously accepted - facially invalid output. 

It is not the only example. It is extremely hard for any reduction of efficacy inputs to the model to give a result that Strongminds is worse than Givedirectly. If we instead leave the meta-analytic results as they were but set all the effect sizes of the direct evidence to zero (in essence discounting them entirely - which I think is approximately what should have been done from the start), we get ~5x better than GiveDirectly. If we set all the effect sizes of both meta-analysis and direct evidence to 0.4 (i.e. the expected effects of registered studies noted before), we get ~6x better than Givedirectly. If we set the meta-analytic results to 0.4 and set all the direct evidence to zero we get ~3x GiveDirectly. Only when one sets all the effect sizes to 0.1  - lower than all but ~three of the studies in the meta-analysis - does one approach equipoise.

This result should not surprise on reflection: the CEA's result is roughly proportional to the ~weighted average of input effect sizes, so an initial finding of '10x' Givedirectly or similar would require ~a factor of 10 cut to this average to drag it down to equipoise. Yet this 'feature' should be seen as a bug: in the same way there should be some non-zero value of the meta-analytic results which should reverse a 'many times better than Givedirectly' finding, there should be some non-tiny value of effect sizes for a psychotherapy intervention (or psychotherapy interventions in general) which results in it not being better than GiveDirectly at all. 

This does help explain the somewhat surprising coincidence the first charity HLI fully assessed would be one it subsequently announces as the most promising interventions in global health and wellbeing so-far found: rather than a discovery from the data, this finding is largely preordained by how the CEA stacks the deck. To be redundant (and repetitive): i) the cost-effectiveness model HLI is making is unfit-for-purpose, given can produce these absurd results; ii) this introduces a large bias in favour of Strongminds; iii) it is a very surprising mistake for a diligent and impartial evaluator to make - these problems are not hard to find.

They're even easier for HLI to find once they've been alerted to them. I did, months ago, alongside other problems, and suggested the cost-effectiveness analysis and Strongminds recommendation be withdrawn. Although it should have happened then, perhaps if I repeat myself it might happen now. 

4:

Accusations of varying types of bad faith/motivated reasoning/intellectual dishonesty should indeed be made with care - besides the difficulty in determination, pragmatic considerations raise the bar still higher. Yet I think the evidence of HLI having less of a finger but more of a fist on the scale throughout its work overwhelms even charitable presumptions made by a saint on its behalf. In footballing terms, I don't think HLI is a player cynically diving to win a penalty, but it is like the manager after the game insisting 'their goal was offside, and my player didn't deserve a red, and.. (etc.)' - highly inaccurate and highly biased. This is a problem when HLI claims itself an impartial referee, especially when it does things akin to awarding fouls every time a particular player gets tackled.

This is even more of a problem precisely because of the complex and interdisciplinary analysis HLI strives to do. No matter the additional analytic arcana, work like this will be largely fermi estimates, with variables being plugged in with little more to inform them than intuitive guesswork. The high degree of complexity provides a vast garden of forking paths available. Although random errors would tend to cancel out, consistent directional bias in model choice, variable selection, and numerical estimates lead to greatly inflated 'bottom lines'. 

Although the transparency in (e.g.) data is commendable, the complex analysis also makes scruitiny harder. I expect very few have both the expertise and perseverence to carefully vet HLI analysis themselves; I also expect the vast majority of money HLI has moved has come from those largely taking its results on trust. This trust is ill-placed: HLI's work weathers scruitiny extremely poorly; my experience is very much 'the more you see, the worse it looks'. I doubt many donors following HLI's advice, if they took a peak behind the curtain, would be happy with what they would discover.  

If HLI is falling foul of an entrenched status quo, it is not particular presumptions around interventions, nor philosophical abstracta around population ethics, but rather those that work in this community (whether published elsewhere or not) should be even-handed, intellectually honest and trustworthy in all cases; rigorous and reliable commensurate to its expected consequence; and transparently and fairly communicated. I think going against this grain underlies (I suspect) why I am not alone in my concerns, and why HLI has not had the warmest reception. The hope this all changes for the better is not entirely forlorn. But things would have to change a lot, and quickly - and the track record thus far does not spark joy.    

1. ^{^}

   Really surprised I missed this last time, to be honest. Especially because it is the only column title in the spreadsheet highlighted in red. 

2. ^{^}

   Given I will be making complaints about publication bias, file drawer effects, and garden of forking path issues later in the show, one might wonder how much of this applies to my own criticism. How much time did I spend dredging through HLI's work looking for something juicy? Is my file drawer stuffed with analyses I hoped would show HLI in a bad light, actually showed it in a good one, so I don't mention them?

   Depressingly, the answer is 'not much' and 'no' respectively. Regressing against publication registration was the second analysis I did on booting up the data again (regressing on active control was the first, mentioned in text). My file drawer subsequent to this is full of checks and double-checks for alternative (and better for HLI) explanations for the startling result. Specifically, and in order:

   - I used the no_FU (no follow-ups) data initially for convenience - the full data can include multiple results of the same study at different follow-up points, and these clustered findings are inappropriate to ignore in a simple random effects model. So I checked both by doing this anyway then using a multi-level model to appropriately manage this structure to the data. No change to the key finding. 

   - Worried that (somehow) I was messing up or misinterpreting the metaregression, I (re)constructed a simple forest plot of all the studies, and confirmed indeed the unregistered ones were visibly off to the right. I then grouped a forest plot by registration variable to ensure it closely agreed with the meta-regression (in main text). It does.

   - I then checked the first 10 studies coded by the variable I think is trial registration to check the registration status of those studies matched the codes. Although all fit, I thought the residual risk I was misunderstanding the variable was unacceptably high for a result significant enough to warrant a retraction demand. So I checked and coded all 46 studies by 'registered or not?' to make sure this agreed with my presumptive interpretation of the variable (in text). It does.

   - Adding multiple variables to explain an effect geometrically expands researcher degrees of freedom, thus any unprincipled ad hoc investigation by adding or removing them has very high false discovery rates (I suspect this is a major problem with HLI's own meta-regression work, but compared to everything else it merits only a passing mention here). But I wanted to check if I could find ways (even if unprincipled and ad hoc) to attenuate a result as stark as 'unregistered studies have 3x the registered ones'. 

   - I first tried to replicate HLI's meta-regression work (exponential transformations and all) to see if the registration effect would be attenuated by intervention variables. Unfortunately, I was unable to replicate HLI's regression results from the information provided (perhaps my fault). In any case, simpler versions I constructed did not give evidence for this.

   - I also tried throwing in permutations of IPT-or-not (these studies tend to be unregistered, maybe this is the real cause of the effect?), active control-or-not (given it had a positive effect size, maybe it cancels out registration?) and study Standard Error (a proxy - albeit a controversial one - for study size/precision/quality, so if registration was confounded by it, this slightly challenges interpretation). The worst result across all the variations I tried was to drop the effect size of registration by 20% (~ -1 to -0.8), typically via substitution with SE. Omitted variable bias and multiple comparisons mean any further interpretation would be treacherous, but insofar as it provides further support: adding in more proxies for study quality increases explanatory power, and tends to even greater absolute and relative drops in effect size comparing 'highest' versus 'lowest' quality studies.

   That said, the effect size is so dramatic to be essentially immune to file-drawer worries. Even if I had a hundred null results I forgot to mention, this finding would survive a Bonferroni correction. 

3. ^{^}

   Obviously 'is the study registered or not'? is a crude indicator of overal quality. Typically, one would expect better measurement (perhaps by including further proxies for underlying study quality) would further increase the explanatory power of this factor. In other words, although these results look really bad, in reality it is likely to be even worse. 

^{^}

HLI's write up on Bolton 2007 links to this paper (I did double check to make sure there wasn't another Bolton et al. 2007 which could have been confused with this - no other match I could find). It has a sample size of 314, not 31 as HLI reports - I presume a data entry error, although it less than reassuring that this erroneous figure is repeated and subsequently discussed in the text as part of the appraisal of the study: one reason given for weighing it so lightly is its 'very small' sample size. 

Speaking of erroneous figures, here's the table of results from this study:



I see no way to arrive at an effect size of d = 1.79 from these numbers. The right comparison should surely be the pre-post difference of GIP versus control in the intention to treat analysis. These numbers give a cohen's d ~ 0.5. 

I don't think any other reasonable comparison gets much higher numbers, and definitely not > 3x higher numbers - the differences between any of the groups are lower than the standard deviations, so should bound estimates like Cohen's d to < 1. 

[Re. file drawer, I guess this counts as a spot check (this is the only study I carefully checked data extraction), but not a random one: I did indeed look at this study in particular because it didn't match the 'only unregistered studies report crazy-high effects' - an ES of 1.79 is ~2x any other registered study.] 

^{^}

Re. my worries of selective scepticism, HLI did apply these methods in their meta-analysis of cash transfers, where no statistical suggestion of publication bias or p-hacking was evident.

^{^}

This does depend a bit on whether spillover effects are being accounted for. This seems to cut the multiple by ~20%, but doesn't change the qualitative problems with the CEA. Happy to calculate precisely if someone insists. 

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Props on the clear and gracious reply. 

we think it's preferable to rely on the existing evidence to draw our conclusions, rather than on forecasts of as-yet unpublished work.

I sense this is wrong, if I think the unpublished work will change my conclusions a lot, I change my conclusions some of the way now though I understand that's a weird thing to do and hard to justify perhaps. Nonetheless I think it's the right move.

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.

1. ^{^}

   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.

2. ^{^}

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

3. ^{^}

   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.

^{^}

Cochrane

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.

Show all footnotes

Hello Jason. FWIW, I've drafted a reply to your other comment and I'm getting it checked internally before I post it.

On this comment about you not liking that we hadn't updated our website to include the new numbers: we all agree with you! It's a reasonable complaint. The explanation is fairly boring: we have been working on a new charity recommendations page for the website, at which point we were going to update the numbers at add a note, so we could do it all in one go. (We still plan to do a bigger reanalysis later this year.) However, that has gone slower than expected and hadn't happened yet. Because of your comment, we'll add a 'hot fix' update in the next week, and hopefully have the new charity recommendations page live in a couple of weeks.

I think we'd have moved faster on this if it had substantially changed the results. On our numbers, StrongMinds is still the best life-improving intervention (it's several times better than cash and we're not confident deworming has a longterm effect). You're right it would slightly change the crossover point for choosing between life-saving and life-improving interventions, but we've got the impression that donors weren't making much use of our analysis anyway; even if they were, it's a pretty small difference, and well within the margin of uncertainty. 

+1 Regarding extending the principle of charity towards HLI. Anecdotally it seems very common for initial CEA estimates to be revised down as the analysis is critiqued. I think HLI has done an exceptional job at being transparent and open regarding their methodology and the source of disagreements e.g. see Joel's comment outlining the sources of disagreement between HLI and GiveWell, which I thought were really exceptional (https://forum.effectivealtruism.org/posts/h5sJepiwGZLbK476N/assessment-of-happier-lives-institute-s-cost-effectiveness?commentId=LqFS5yHdRcfYmX9jw). Obviously I haven't spent as much time digging into the results as Gregory has made, but the mistakes he points to don't seem like the kind that should be treated too harshly.

As a separate point, I think it's generally a lot easier to critique and build upon an analysis after the initial work has been done. E.g. even if it is the case that SimonM's assessment of Strong Minds is more reliable than HLI's (HLI seem to dispute that the critique he levies are all that important as they only assign a 13% weight to that RCT), this isn't necessarily evidence that SimonM is more competent than the HLI team. When the heavy lifting has been done, it's easier to focus in on particular mistakes (and of course valuable to do so!).

For clarity being 2x better than cash transfers would still provide it with good reason to be on GWWC's top charity list, right? Since GiveDirectly is?

I think GiveDirectly gets special privilege because "just give the money to the poorest people" is such a safe bet for how to spend money altruistically.

Like if a billionaire wanted to spend a million dollars making your life better, they could either:

1. just give you the million dollars directly, or
2. spend the money on something that they personally think would be best for you

You'd want them to set a pretty high bar of "I have high confidence that the thing I chose to spend the money on will be much better than whatever you would spend the money on yourself."

Hello Nathan. Thanks for the comment. I think the only key place where I would disagree with you is what you said here

If, as seems likely the forthcoming RCT downgrades SM a lot and the HLI team should have seen this coming, why didn't they act?

As I said in response to Greg (to which I see you've replied) we use the conventional scientific approach of relying on the sweep of existing data - rather than on our predictions of what future evidence (from a single study) will show. Indeed, I'm not sure how easily these would come apart: I would base my predictions substantially on the existing data, which we've already gathered in our meta-analysis (obviously, it's a matter of debate as to how to synthesise data from different sources and opinions will differ). I don't have any reason to assume the new RCT will show effects substantially lower than the existing evidence, but perhaps others are aware of something we're not. 

Man, why don't images resize properly. I've deleted it because it was too obnoxious when huge.

HLI - but if for whatever reason they're unable or unwilling to receive the donation at resolution, Strongminds.

The 'resolution criteria' are also potentially ambiguous (my bad). I intend to resolve any ambiguity stringently against me, but you are welcome to be my adjudicator. 

[To add: I'd guess ~30-something% chance I end up paying out: d = 0.4 is at or below pooled effect estimates for psychotherapy generally. I am banking on significant discounts with increasing study size and quality (as well as other things I mention above I take as adverse indicators), but even if I price these right, I expect high variance. 

I set the bar this low (versus, say, d = 0.6 -  at the ~ 5th percentile of HLI's estimate) primarily to make a strong rod for my own back. Mordantly criticising an org whilst they are making a funding request in a financially precarious position should not be done lightly. Although I'd stand by my criticism of HLI even if the trial found Strongminds was even better than HLI predicted, I would regret being quite as strident if the results were any less than dramatically discordant. 

If so, me retreating to something like "Meh, they got lucky"/"Sure I was (/kinda) wrong, but you didn't deserve to be right" seems craven after over-cooking remarks potentially highly adverse to HLI's fundraising efforts. Fairer would be that I suffer some financial embarrassment, which helps compensate HLI for their injury from my excess.

Perhaps I could have (or should have) done something better. But in fairness to me, I think this is all supererogatory on my part: I do not think my comment is the only example of stark criticism on this forum, but it might be unique in its author levying an expected cost of over $1000 on themselves for making it.]   

I guess I would very slightly adjust my sense of HLI, but I wouldn't really think of this as an "error." I don't significantly adjust my view of GiveWell when they delist a charity based on new information.

I think if the RCT downgrades StrongMinds' work by a big factor, that won't really introduce new information about HLI's methodology/expertise. If you think there are methodological weaknesses that would cause them to overstate StrongMinds' impact, those weaknesses should be visible now, irrespective of the RCT results.

Okay buutttt..

I know Michael and have a bias towards concensus.

"We’re now in a position to confidently recommend StrongMinds as the most effective way we know of to help other people with your money".^[1]

• Michael has expressed regret about this statement, so I won't go further into this than I already have. However, there is a framing in that comment that suggests this is a exception, because "HLI is quite well-caveated elsewhere", and I want to push back on this a little.

Fair enough

HLI has previously been mistaken for an advocacy organisation (1, 2). This isn't HLI's stated intention (which is closer to a "Happiness/Wellbeing GiveWell"). I outline why I think this is a reasonable misunderstanding here (including important disclaimers that outline HLI's positives).

• Despite claims that HLI does not advocate for any particular philosophical view, I think this is easily (and reasonably) misinterpreted.

I find this hard to parse.

James' comment thread below: "Our focus on subjective wellbeing (SWB) was initially treated with a (understandable!) dose of scepticism. Since then, all the major actors in effective altruism’s global health and wellbeing space seem to have come around to it"

1. I think James seems to dislike being misquoted more than he's saying he disagrees with SWB. I am unsure his position there
2. If he supports SWB then while I think it's fair for him to dislike being misquoted I think I would call this an "edge case"
3. To me this does give the flag of "there is something else going on here". I think it seems like a stronger reaction than I'd expect. I guess there is a reason for that.

See Alex's comment below, where TLYCS is quoted to say: "we will continue to rely heavily on the research done by other terrific organizations in this space, such as GiveWell, Founders Pledge, Giving Green, Happier Lives Institute [...]"

• I think excluding "to identify candidates for our recommendations, even as we also assess them using our own evaluation framework" [emphasis added] gives a fairly different impression to the actual quote, in terms of whether or not TLYCS supports WELLBYs as an approach.

Again, this reads to me as a fair enough criticism, but one that it would surprise me if someone made without some kind of background here. 

My model would be that there is bad blood in a number of places and that errors have been made too many time and so people have started to play hardball. I am not saying that's wrong or unfair, but just to note that it's happening. I suggest the things people are quoting here are either examples of a larger pattern or not actually the things they are upset about.

But I say that weakly. Mainly I say "something seems off"

This is speculative, and I don't want this to be read as an endorsement of people's critical comments; rather, it's a hypothesis about what's driving the "harsh discussion":

It seems like one theme in people's critical comments is misrepresentation. Specifically, multiple people have accused HLI of making claims that are more confident and/or more positive than are warranted (see, e.g., some of the comments below, which say things like: "I don't think this is an accurate representation," "it was about whether I thought that sentence and set of links gave an accurate impression," and "HLI's institutional agenda corrupts its ability to conduct fair-minded and even-handed assessments").

I wonder if people are particularly sensitive to this, because EA partly grew out of a desire to make charitable giving more objective and unbiased, and so the perception that HLI is misrepresenting information feels antithetical to EA in a very fundamental way.

Thank you! I think if any of my non-EA friends ask about donating to mental health charities (which hasn't happened recently but is the type of thing my friends sometimes asks about in the past), I'd probably recommend to them to adopt a "wait and see" attitude.

The first two are good.

"Growth + more runway"? (plus a brief discussion of why you think adding +6 months runway would increase impact). Optimal could imply a better rate of growth, when the difference seems to be more stability.

Anyway, just donated -- although the odds of me moving away from GiveWell-style projects for my object-level giving is relatively modest, I think it's really important to have a good range of effective options for donors with various interests and philosophical positions.

Thanks Michael. My main concern is that it doesn't seem that there is enough clarity on the spillovers, and spillovers are likely to be a large component of the total impact. As Joel says there is a lack of data, and James Snowden's critique implies your current estimate is likely to be an overestimate for a number of reasons. Joel says in a comment "a high quality RCT would be very welcome for informing our views and settling our disagreements". This implies even Joel accepts that, given the current strength of evidence, there isn't clarity on spillovers.

Therefore I would personally be more inclined to fund a study estimating spillovers than funding Strongminds. I find it disappointing that you essentially rule out suggesting funding research when it is at least plausible that this is the most effective way to improve happiness as it might enable better use of funds (it just wouldn't increase happiness immediately).

I’ve just realized you were probably referring to Strongminds not HLI?

Funding Strongminds to carry out research into the efficacy of their own intervention seems a very bad idea to me given their incentive for the results to be favorable.

The studies I had in mind would be empirical field studies best carried out by academic economists. The studies a charity like HLI would then make use of the results from.