Evaluating StrongMinds: how strong is the evidence?

Thanks for this, Joel. I look forward to reviewing the analysis more fully over the weekend, but I have three major concerns with what you have presented here.

1. A lot of these publication bias results look like nonsense to the naked eye.

Recall the two funnel plots for PT and CT (respectively):

I think we're all seeing the same important differences: the PT plot has markers of publication bias (asymmetry) and P hacking (clustering at the P<0.05 contour, also the p curve) visible to the naked eye; the CT studies do not really show this at all. So heuristically, we should expect statistical correction for small study effects to result in:

1. In absolute terms, the effect size for PT should be adjusted downwards
2. In comparative terms, the effect size for PT should be adjusted downwards more than the CT effect size.

If a statistical correction does the opposite of these things, I think we should say its results are not just 'surprising' but 'unbelievable': it just cannot be true that, given the data we see being fed into the method it should lead us to conclude this CT literature is more prone to small-study effects than this PT one; nor (contra the regression slope in the first plot), the effect size for PT should be corrected upwards.

Yet many of the statistical corrections you have done tend to fail one or both of these basically-diagnostic tests of face validity. Across all the different corrections for PT, on average the result is a 30% increase in PT effect size (only trim and fill and selection methods give families of results where the PT effect size is reduced). Although (mostly) redundant, these are also the only methods which give a larger drop to PT than CT effect size.

As comments everywhere on this post have indicated, heterogeneity is tricky. If (generally) different methods all gave discounts, but they were relatively small (with the exception of one method like a Trim and Fill which gave a much steeper one), I think the conclusions you drew above would be reasonable. However, for these results, the ones that don't make qualitative sense should be discarded, and the the key upshot should be: "Although a lot of statistical corrections give bizarre results, the ones which do make sense also tend to show significant discounts to the PT effect size".

2. The comparisons made (and the order of operations to get to them) are misleading

What is interesting though, is although in % changes correction methods tend to give an increase to PT effect size, the effect sizes themselves tend to be lower: the average effect size across analyses is 0.36, ~30% lower than the pooled estimate of 0.5 in the funnel plot (in contrast, this is 0.09 - versus 0.1, for CT effect size).

This is the case because the % changes are being measured, not against the single reference value of 0.5 in the original model, but the equivalent model in terms of random/fixed, outliers/not, etc. but without any statistical correction technique. For example: row 13 (Model 10) is Trim-and-Fill correction for a fixed effect model using the full data. For PT, this effect size is 0.19. The % difference is calculated versus row 7 (Model 4), a fixed effect model without Trim-and-Fill (effect = 0.2) not the original random effects analysis (effect = 0.5). Thus the % of reference effect is 95% not 40%. In general, comparing effect sizes to row 4 (Model ID 1) generally gets more sensible findings, and also generally more adverse ones. re. PT pub bias correction:

In terms of (e.g.) assessing the impact of Trim and Fill in particular, it makes sense to compare like with like. Yet presumably what we care about to ballparking the estimate of publication bias in general - and for the comparisons made in the spreadsheet mislead. Fixed effect models (ditto outlier exclusion, but maybe not follow-ups) are already an (~improvised) means of correcting for small study effects, as they weigh them in the pooled estimate much less than random effects models. So noting Trim-and-Fill only gives a 5% additional correction in this case buries the lede: you already halved the effect by moving to a fixed effect model from a random effect model, and the most plausible explanation why fixed effect modelling limits distortion by small study effects.

This goes some way to explaining the odd findings for statistical correction above: similar to collider/collinearity issues in regression, you might get weird answers of the impact of statistical techniques when you are already partly 'controlling for' small study effects. The easiest example of this is combining outlier removal with trim and fill - the outlier removal is basically doing the 'trim' part already. 

It also indicates an important point your summary misses. One of the key stories in this data is: "Generally speaking, when you start using techniques - alone or in combination - which reduce the impact of publication bias, you cut around 30% of the effect size on average for PT (versus 10%-ish for CT)".  

3. Cost effectiveness calculation, again

'Cost effectiveness versus CT' is a unhelpful measure to use when presenting these results: we would first like to get a handle on the size of the small study effect in the overall literature, and then see what ramifications it has for the assessment and recommendations of strongminds in particular. Another issue is these results doesn't really join up with the earlier cost effectiveness assessment in ways which complicate interpretation. Two examples:

1. On the guestimate, setting the meta-regressions to zero effect still results in ~7x multiples for Strongminds versus cash transfers. This spreadsheet does a flat percentage of the original 9.4x bottom line (so a '0% of previous effect' correction does get the multiple down to zero). Being able to get results which give <7x CT overall is much more sensible than what the HLI CEA does, but such results could not be produced if we corrected the effect sizes and plugged them back into the original CEA. 
2. Besides results being incongruous, the methods look incongruous too. The outliers being excluded in some analyses include strong-minds related papers later used in the overall CE calculation to get to the 9.4 figure. Ironically, exclusion would have been the right thing to do originally, as including the papers help derive the pooled estimate and then again as independent inputs into the CEA double counts them. Alas two wrongs do not make a right: excluding them in virtue of outlier effects seems to imply either: i) these papers should be discounted generally (so shouldn't be given independent weight in the CEA); ii) they are legit, but are such outliers the meta-analysis is actually uninformative to assess the effect of the particular interventions they investigate.

More important than this, though, is the 'percentage of what?' issue crops up again: the spreadsheet uses relative percentage change to get a relative discount vs. CT, but it uses the wrong comparator to calculate the percentages. 

Lets look at row 13 again, where we are conducting a fixed effects analysis with trim-and-fill correction. Now we want to compare PT and CT: does PT get discounted more than CT? As mentioned before, for PT, the original random effects model gives an effect size of 0.5, and with T'n'F+Fixed effects the effect size is 0.19. For CT, the original effect size is 0.1, and with T'n'F +FE, it is still 0.1. In relative terms, as PT only has 40% of the previous effect size (and CT 100% of the effect size), this would amount to 40% of the previous 'multiple' (i.e. 3.6x). 

Instead of comparing them to the original estimate (row 4), it calculates the percentages versus a fixed effect but not T'n'F analysis for PT (row 7). Although CT here is also 0.1, PT  in this row has an effect size of 0.2, so the PT percentage is (0.19/0.2) 95% versus (0.1/0.1) 100%, and so the calculated multiple of CT is not 3.6 but 9.0.

The spreadsheet is using the wrong comparison, as we care about whether the multiple between PT and CT is sensitive to different analyses, relative sensitivity to one variation (T'n'F) conditioned on another (fixed effect modelling). Especially when we're interested in small study effects and the conditioned on effect likely already reduces those. 

If one recalculates the bottom line multiples using the first model as the comparator, the results are a bit less weird, but also more adverse to PT. Note the effect is particularly reliable for T'n'F (ID 7-12) and selection measures (ID 37-42), which as already mentioned are the analysis methods which give qualitatively believable findings.

Of interest, the spreadsheet only makes this comparator error for PT: for CT, whether all or lumped (column I and L) makes all of its percentage comparisons versus the original model (ID 1). I hope (and mostly expect) this is a click-and-drag spreadsheet error (or perhaps one of my understanding), rather than my unwittingly recovering an earlier version of this analysis.

Summing up

I may say more next week, but my impressions are

1. In answer to the original post title, I think the evidence for Strongminds is generally weak, equivocal, likely compromised, and definitely difficult to interpret.
2. Many, perhaps most (maybe all?) of the elements used in HLI's recommendation of strongminds do not weather scrutiny well. E.g.
   1. Publication bias issues discussed in the comments here.
   2. The index papers being noted outliers even amongst this facially highly unreliable literature.
   3. The cost effectiveness guestimate not giving sensible answers when you change its inputs. 
3. I think HLI should withdraw their recommendation of Strongminds, and mostly go 'back to the drawing board' on their assessments and recommendations. The current recommendation is based on an assessment with serious shortcomings in many of its crucial elements. I regret I suspect if I looked into other things I would see still more causes of concern.
4. The shortcomings in multiple elements also make criticism challenging. Although HLI thinks the publication bias is not big enough of an effect to withdraw the recommendation, it what publication bias would be big enough, or indeed in general what evidence would lead them to change their minds. Their own CEA is basically insensitive to the meta-analysis, giving 'SM = 7x GD' even if the effect size was corrected all the way to zero. Above Joel notes even at 'only' SM = 3-4GD it would still generally be their top recommendation. So by this logic, the only decision-relevance this meta-analysis has is confirming the effect isn't massively negative. I doubt this is really true, but HLI should have a transparent understanding (and, ideally, transparent communication) of what their bottom line is actually responsive to. 
5. One of the commoner criticisms of HLI is it is more a motivated reasoner than an impartial evaluator. Although its transparency in data (and now code) is commendable, overall this episode supports such an assessment: the pattern which emerges is a collection of dubious-to-indefensible choices made in analysis, which all point in the same direction (i.e. favouring the Strongminds recommendation); surprising incuriousity about the ramifications or reasonableness of these analytic choices; and very little of this being apparent from the public materials, emerging instead in response to third party criticism or partial replication. 
6. Although there are laudable improvements contained in Joel's summary above, unfortunately (per my earlier points) I take it as yet another example of this overall pattern. The reasonable reaction to "Your publication bias corrections are (on average!) correcting the effect size upwards, and the obviously skewed funnel plot less than the not obviously skewed one" is not "Well, isn't that surprising - I guess there's no clear sign of trouble with pub bias in our recommendation after all", but "This doesn't make any sense".
7. I recommend readers do not rely upon HLIs recommendations or reasoning without carefully scrutinising the underlying methods and data themselves.

To be clear, this isn't the bar HLI uses. As I said in section 2:

At HLI, we think the relevant factors for recommending a charity are:

(1) cost-effectiveness is substantially better than our chosen benchmark (GiveDirectly cash transfers); and

(2) strong evidence of effectiveness. 

To elaborate, we interpret "substantially" to mean "around as good as the best charity we've found so far" which is currently 9x GiveDirectly, but I assume the specific number will change over time.

I was trying to propose a possible set of conditions where we could agree that it was reasonable for a charity to be recommended by someone in the EA community. I was aiming for inclusivity here and to leave room for the possibility that Founder's Pledge may have good reasons I'm not privy to for using GiveDirectly as a bar. 

I'm also unsure that GiveWell's bar will generalise to other types of analyses. i.e., I think it's very plausible that other evaluators find that cash transfers are much better than GiveWell does.  

Agreed. For what it's worth GWWC also uses a higher threshold than the 1x cash this post advocates.

"Any form of face-to-face psychotherapy delivered to groups or by non-specialists deployed in LMICs." These three studies below you included don't have psychotherapy as the intervention, unless I'm missing something.

Ah yes, I admit this looks a bit odd. But I'll try to explain. As I said in the psychotherapy CEA on page 9 (I didn't try to hide this too hard!): 

 Similarly, most studies make high use of psychotherapy. We classied a study as making high (low) use of psychological elements if it appeared that psychotherapy was (not) the primary means of relieving distress, or if relieving distress was not the primary aim of the intervention. For instance, we assigned Tripathy et al., (2010) as making low use of psychotherapy because their intervention was primarily targeted at reducing maternal and child mortality through group discussions of general health problems but still contained elements of talk therapy. We classied “use of psychotherapy” as medium if an intervention was primarily but not exclusively psychotherapy.

I also tried to show the relative proportion of papers falling in each category in the first figure: 

The complete list of studies with low or medium use of psychotherapy elements are:

One concern I anticipate is: "were you sneaking in these studies to inflate your effect?" and that's certainly not the case. In a model in an earlier draft of the analysis but didn't make the final cut, I regressed whether a trial made high, medium, or low use of psychotherapy on the effects. I found that, if anything, the trials without "high" use of psychotherapy elements have smaller effects. 

In lieu of a reference, I'll post the R output where the outcome is in SD changes in mental health measures. 

I plan on being stricter with the studies I include in the next analysis version. When I first did this meta-analysis, I thought quantity was more important than quality, and I think my views have changed since then. I don't think including these studies less relevant to psychotherapy affects the results too much other than moving the results to align with the "psychosocial" intervention prior. 

I also recognize that this is probably confusing, and we didn't explain this well. These are things I will return to when we return to this analysis and give it an upgrade in rigour and clarity. 

Nick, thank you for your comment. I always appreciate your friendly tone.  

but I also believe that when an org gets to the scale that StrongMinds have now reached, they should have an RCT vs cash at least in the works.

I agree this would be great ... but this also seems like a really strict requirement, and I'm not sure it's necessary. GiveWell seems nonplussed by not having an RCT comparing deworming to cash transfers or malaria prevention to vitamin-A supplementation, I'm inclined to believe this is something they've thought about. That's not meant to be a knockdown argument against the idea, but if an RCT like this is needed for comparing psychotherapy to cash transfers -- why not every other intervention currently recommended in the EA space? 

More directly, if we have two high-quality trials run separately about two different interventions but measuring similar outcomes -- how much better is this than running an RCT with two arms? It certainly reduces differences in confounders (particularly unobserved) between trials. But I think it's possible it could also have weaknesses. 

• It seems plausibly more expensive to coordinate two high-quality interventions in a single trial than let them be run separately. For instance, IIRC correctly in Haushofer et al., 2020 the comparison between psychotherapy and GiveDirectly was a bit apples to oranges. For psychotherapy, they hired a local NGO to start a new programme from scratch, which they compared to GiveDirectly, which by that time, was a well-oiled cash-slinging machine. To get two organizations that already know how to deploy the intervention well to collaborate on a single RCT seems difficult and expensive.
• It also may have limited generalizability. Running separate trials of charity interventions makes it likelier that the results reflect the circumstances that the charity operates in -- unless they have an area of overlap -- which is possible, but finding that seems like another reason this could be difficult. 

Lastly, regarding the making the dream RCT happen, HLI is currently rather resource constrained, so in our work, we have to make do with the existing literature, and we're only just now exploring "research advocacy" as an option. Running an RCT would probably cost a multiple of our annual budget. For StrongMinds, they have more resources, but not much more. If it was desired to have another RCT with a psychotherapy and cash arm, I wonder if the GiveDirectly RCT machine may be the most promising way to get that evidence. 

You also say that there are 39 studies analysed, but it looks like there are a lot less studies than that, with individual studies broken into differnent groups (like a,b,c,d). 

I think what may be happening here is I use "studies" as synonymous with "trials". So in my usage, one paper can analyse multiple studies (or trials). However, on reflection, I realise I sometimes refer to papers as studies -- which is unhelpful, therefore, I think it'd be clearer if I referred to each separate intervention experiment as a "trial".  Another thing that may be confusing is that sometimes authors will publish multiple papers in the same year. I distinguish these papers by adding an "a" or "b" etc to the end of the reference. 

But if you count all of the different unique "trials", it does come out to 39. 

Also have you thought about publishing your Meta-analysis in a peer reviewed journal?

We're keen to do this. But the existing meta-analysis is probably 65% of the rigour necessary for an academic paper. This year we are trying to redo the analysis with an academic collaborator so the search will be systematic, the data will be double-screened, and we have many more robustness tests. 

(I'll answer the selection criterion question separately) 

A couple of quick comments Simon.

First on this comment, which I disagree with - and this is one of the few areas where I think the Effective Altruism community can at times miss something quite important. This isn't really about the StrongMinds charity question, but instead a general bugbear of mine as someone who implements things ;).

" I think the difference here is I wouldn't expect those interventions to be as sensitive to the implementation details." 

Any intervention is extremely sensitive to implementation details, whether deworming or nets or psychotherapy. In fact I think that intervention details are often more important than the pre-calculated expected value. If a given intervention is implemented poorly, or in the wrong place or at the wrong time then it could still have less impact than an intervention that is theoretically 100x worse. As a plausible if absurd example, imagine a vitamin A project which doesn't actually happen because the money is corrupted away.  Or if you you give out mosquito nets in the same village where another NGO gave out nets 2 weeks ago. Or if you deworm in a place where 20 previous deworming projects and sanitation has already drastically reduced the worm burden.

Maybe some interventions are easier to implement than others,  and there might be  more variance  in the effectiveness of psychotherapy compared with net distribution (although I doubt that, I would guess less variance than nets)  but  all are very sensitive to implementation details.
 

And second this statement

"just that it has an effect which is small enough that we are looking at numbers on the order (or lower) than cash-transfers and therefore it doesn't meet the bar of "Top-Charity"."

I'd be interested in you backing up this comment with a bit explanation if you have time (all good if not!). I know this isn't your job and you don't have the time that Joel has, but  what is it that has led you to conclude that the numbers are "on the order (or lower) than cash transfers"?   Is this comment based on intuition or have you done some maths?

Hi Henry, 

I addressed the variance in the primacy of psychotherapy in the studies in response to Nick's comment, so I'll respond to your other issues. 

Some of the studies deal with quite specific groups of people eg. survivors of violence, pregnant women, HIV-affected women with young children. Generalising from psychotherapy's effects in these groups  to psychotherapy in the general population seems unreasonable. 

I agree this would be a problem if we only had evidence from one quite specific group. But when we have evidence from multiple groups, and we don't have strong reasons for thinking that psychotherapy will affect these groups differently than the general population -- I think it's better to include rather than exclude them. 

I didn't show enough robustness checks like this, which is a mistake I'll remedy in the next version. I categorised the population of every study as involving "conflict or violence", "general" or "HIV".  Running these trial characteristics as moderating factors suggests that, if anything, adding these additional populations underestimates the efficacy. But this is a point worth returning to.

Similarly, the therapies applied between studies seem highly variable including "Antenatal Emotional Self-Management Training", group therapy, one-on-one peer mentors. Lumping these together and drawing conclusions about "psychotherapy" generally seems unreasonable.

I'm less concerned with variation in the type of therapy not generalising because  as I say in the report (page 5) "...different forms of psychotherapy share many of the same strategies. We do not focus on a particular form of psychotherapy. Previous meta-analyses find mixed evidence supporting the superiority of any one form of psychotherapy for treating depression (Cuijpers et al., 2019)." 

Due to the fact most types of psychotherapy seem about as effective, and expertise doesn't seem  to be of first order importance, I formed the view that if you regularly get someone talk to about their problems in a semi-structured way it'll probably be pretty good for them. This isn't a view I'd defend to the death, but I held it strongly enough to justify (at least to myself and the team) doing the simpler version of the analysis I performed. 

With the difficulty of blinding patients to psychotherapy, there seems to be room for the Hawthorne effect to be skewing the results of each of the 39 studies: with patients who are aware that they've received therapy feeling obliged to say that it helped.

Right, but this is the case with most interventions (e.g., cash transfers). So long as the Hawthorne effect is balanced across interventions (which I'm not implying is assured), then we should still be able to compare their cost-effectiveness using self-reports. 

Furthermore, only 8 of the trials had waitlist or do nothing controls. The rest of the trials received some form of "care as usual" or a placebo like "HIV education".  Presumably these more active controls could also elicit a Hawthorne effect or response bias? 

Hi Henry. Thanks for your feedback! I'll let Joel respond to the substantive comments but just wanted to note that I've changed the "Appendix D" references to "Appendix C". Thanks very much for letting us know about that. 

I'm not sure why Appendix B has hyperlinks for some studies but not for others. I'll check with Joel about that and add links to all the papers as soon as I can. In future, I plan to convert some of our data tables into embedded AirTables so that readers can reorder by different columns if they wish.

Hi Rina! I appreciate the nice words. 

Could I add on to Nick's comment and an ask for clarification about  including"Any form of face-to-face psychotherapy delivered to groups or by non-specialists deployed in LMICs." -- it seems in your Appendix B that the studies incorporated in meta-regression include a  lot of individually delivered interventions, do you still use them and if so how/any differently?

Yes, we still use individually delivered interventions as general evidence of psychotherapy's efficacy in low and middle-income countries. We assigned this general evidence 46% of the weight in the StrongMind's analysis (see Table 2 in the StrongMinds report). 

While we found that group-delivered psychotherapy is more impactful, I'm not entirely clear what the causal mechanism for this would be, so I thought it'd be appropriately conservative to leave in that evidence. We showed and discussed this topic in Table 2 of our psychotherapy report (page 16).

This type of generally recruited and potentially partially biased sample seems a little different than a sample that includes women survivors of torture/ violence/ SA/ in post-conflict settings of which you have a number of RCTs.

I discussed the potential issues with the differences in samples and the way I try to address them in my response to Henry, so I won't repeat myself unless you have a further concern there. 

Regarding the risk of bias due to mistaken beliefs about receiving material benefits -- this is honestly new to me since Nick Laing brought it up a couple of months ago. Insomuch as this bias exists, I assume for StrongMinds, this will have to go down over time as word travels that they do not, in fact, do much other than mental health treatments. 

And to reiterate the crux here: for this to affect our comparison to, say, cash transfers, we need to believe that this bias leads to people over-reporting their benefits more (or less) than it would for the people who receive cash transfers who hope that if they give positive responses, they'll get even more cash transfers. 

I'm not trying to dismiss this concern out of hand, but I'd prefer to collect more evidence before I change my analysis. I will, if possible, try to make that evidence come to be (just as I try to push for the creation of evidence to inform other questions we're uncertain about) -- if I can do so cost-effectively, but in my position, resources are limited. 

Are there baseline mental health scores for all these samples that you could look at?

There are in many cases, but that's not data we recorded from the samples, but I think for most studies, the sample was selected for having psychological distress above some clinical threshold. That may be worth looking into. 

I should also say, if there is a replication package available for the analysis (I didn’t see one) then I should be able to do this myself and I can share the results here.

If we all agree that this topic matters, then it is pretty important to share this kind of normal diagnostic info. For example, the recent water disinfectant meta-analysis by Michael Kremer’s team shows both graphs. https://papers.ssrn.com/sol3/papers.cfm?abstract_id=4071953

That's so reasonable.

I think that we can all agree that the analysis was done in an atypical way (perhaps for good reason), that it was not as rigorous as many people expected, and that it had a series of omissions or made atypical analytical moves that (perhaps inadvertently) made SM look better than it will look once that stuff is addressed. I don't think anyone can speak yet to the magnitude of the adjustment when the analysis is done better or in a standard way. 

But I'd welcome especially Joel's response to this question. It's a critical question and it's worth hearing his take.

Fair point! I'll try to to summarize things from my perspective once things have settled a bit more. 

Yes, the pooled results are mostly done with meta-regressions where studies are weighted by the inverse of the standard error (so more imprecisely estimated effect sizes are weighted less).