Response to the talk by Lewis et al.

In their talk titled “The antidepressant wars”, Glen Lewis, Tania Gergel, and Edoardo Ostinelli from the Royal College of Psychiatrists, argue that critical views on antidepressants parallel climate change denial, post-truth, Trumpism etc. and thus creating discrimination and harm. Issues that I see as deeply problematic and harmful, too. I was provided a recording of this talk and realized that some of my/our scientific work was misrepresented. The talk also includes too many problematic statements from an evidence-based medicine point of view, so I felt like I need to respond.

A goal of their talk was to provide a nuanced summary of the evidence on antidepressants so to “Be able to explain the evidence for and against antidepressants to patients and their families.” Indeed, Lewis et al. do mention some critical points about antidepressants. For example, the ever increasing rates of prescriptions and long-term use is “alarming”. Or that there are some problems with the evidence base (old trials, industry trials, narrow focus, smaller effect sizes in newer trials). This creates some nuance. However, the overall picture emerging from the talk is still too problematic and does not keep the promise of nuance, as I will outline below.

Giving the impression that there is scientific consensus about the efficacy of antidepressants

Lewis et al. claim that there is a lot of evidence about the effectiveness of antidepressants, with the large Cipriani et al. systematic review of clinical trials as highlight (Cipriani et al., 2018). Despite the substantial evidence showing that antidepressants were significantly superior to placebo, Lewis et al. wonder why there is still the “massive” controversy. There is a straighforward answer which Lewis et al. don’t mention clearly enough: when taking into account clinical significance, drug-placebo differences are most likely not clinically meaningful. Furthermore when considering methodological biases, the (small) effects are likely overestimations of actual effects. Consequently, a critical view on antidepressants is the logical conclusion, for example that the efficacy is uncertain (Munkholm et al., 2019) or even that, when considering the harms of antidepressants, these meds should not be used (Jakobsen et al., 2019). These conclusions are from respected researchers and were published in BMJ journals. In our paper in response to Cipriani et al, we come to comparable conclusions, too (Hengartner and Plöderl, 2018).

Misleading reporting and spinning of the PANDA results

The criticism around industry trials done in secondary care is a reason for Lewis et al. to bring in the PANDA trial, where Lewis was author of the related publication (Lewis et al., 2019). They tell the audience that, in the PANDA trial, the main benefit of sertraline is for anxiety, where the effects were clinically significant. Later, they also mention the result for a single item where patients were asked if they felt better: 59% felt better on sertraline and 42% on placebo. For listeners not familiar with the PANDA trial, this sounds like a success story. However, these are case in point examples of spin and outcome-switching, two problematic research practices. To spin a results means the selective reporting of favorable results and hiding of unfavorable results. Outcome switching refers to changing the primary outcome with a secondary outcome which shows more convenient findings. In this case, Lewis et al. did not inform the audience about the pre-specified primary outcome in PANDA, which was the drug-placebo difference in the reduction of depression symptoms as measured with the Patient Health Questionnaire. This primary outcome was not statistically significantly and very small, with an effect size (ES) of 0.09 at week 6 and 0.18 at week 12. Interestingly, in the appendix, there are a lot of subgroup differences and it can be explored if efficacy is better for severely depressed people, but there was no evidence for this. Instead of reporting the results for the PHQ, the primary outcome, Lewis et al. selectively mentioned secondary outcomes with significant drug-placebo differences, but missed to report that the effect sizes were again small (ES < 0.25). Later in the talk, when discussing clinical significance, Lewis et al. said that the efficacy in the PANDA was clinically meaningful for anxiety but “perhaps” not for depression. Both is wrong or at least misleading, because the effects for anxiety were small too, and thus likely not statistically significant. The finding for depression was not of “uncertain” clinical significance but it was clearly not so when using common thresholds of clinical significance. It wasn’t even statistically significant. This kind of spin is also found in the abstract of the original publication in the high-impact Journal of the American Medical Association (JAMA). Despite that PANDA failed in the primary outcome, authors concluded: “Our findings support the prescription of SSRI antidepressants in a wider group of participants than previously thought, including those with mild to moderate symptoms who do not meet diagnostic criteria for depression or generalized anxiety disorder”. This should never have passed peer review. We summarized the criticism in a letter (Hengartner et al., 2020).

Moreover, when giving a talk about the efficacy of antidepressants, instead of relying on results from a single RCT, the audience should have an overview on other existing “real world” studies.

Lewis et al. also referred to the recent FDA study (Stone et al., 2022) where, compared to placebo, an additional 15% of patients on antidepressants were were categorized as having a “large response”, with a mean symptom reduction of 16 points on the Hamilton Depression Rating Scale (HDRS). As many others, Lewis et al. made the error of interpreting this as “15% difference in patients experiencing a large response”. This is erroneous because the latent classes in the statistical model are substantially overlapping. Taking this into account, the drug-placebo difference in „responder“ status is about 11% at best, and only 6% when using a reduction of 16 HDRS points as criterion for “response”, which is the mean symptom reduction in the “large response” category (Plöderl, 2022).

Ignoring the work on clinical significance and accounting for harms of treatment

Next, Lewis et al. talk about how to interpret the clinical importance of the drug-placebo differences. They say that Cipriani et al. reported an ES of 0.2 but that it is difficult to judge if this is clinically important. What they miss to mention is that there is a lot of work about this. In our review of different approaches to estimate clinical significance/importance, it became clear that the efficacy of antidepressants found in clinical trials is not exceeding the lower limit of different cut-offs for clinical significance (Hengartner and Plöderl, 2021). Instead of providing the bigger picture, Lewis et al. again focused on the PANDA trial. And they again do not present the main outcome, that is, the effect on depression symptoms, but on a secondary outcome, anxiety. As already mentioned above, the effect size for anxiety is also small: ES = 0.25 at 6 weeks (estimated from results in Table 3 in the PANDA publication). Clinical meaningful difference usually start at ES = 0.5, thus the efficacy for anxiety is most likely not clinically significant.

From a broader view, which should be taken in a talk about the efficacy of antidepressants, it is important to also look at the harm/benefit ratio. Here, the concept of the “smallest worthwhile difference” is important (Barrett et al., 2005), where patients judge how efficacious a drug must be to be worth using, when also considering costs and harms. According to Barrett, the smallest worthwhile difference is equal or larger then the minimal important difference (clinical significance). Strikingly, despite the longstanding controversy and the ever increasing prescription rates, only very recently a first study on the smallest worthwhile difference appeared for antidepressants (Sahker et al., 2024). The study authors have a high reputation within psychiatry. They found that only two out of three patients (Sahker et al., 2024) considered antidepressants as worthwhile. Put differently, two-thirds of patients would not consider antidepressants as worthwhile, if they really knew about the efficacy and harms.

The incomplete picture on antidepressants and suicides and its controversy

Then there is the section about antidepressants and suicide risk, where our research (Hengartner and Plöderl, 2019a) was criticized for using the wrong method but that a correct method used by others (Hayes et al., 2019) came to different conclusions. Because this was about our research, I provide a more thorough description of the misleading information.

Our study was actually only a short letter in response to a study about the FDA data-set by Khan et al. (2018) who used “patient exposure years” as outcome and concluded that there was no significant drug-placebo difference in suicide risk. However, it is known that most suicidal behavior occurs at the beginning of clinical trials, and when the risk for such events is not constant across time, analysis of patient exposure years is misleading (interestingly, nobody seemed to have issues with this misleading analysis). Therefore, we ran a simple analysis based on the proportion of suicidal events in drug and placebo arms, finding a statistically significant elevated risk for suicides (OR = 2.83, 95% CI = 1.13–9.67, p = 0.02) and suicide attempts (OR = 2.38, 95% CI = 1.63–3.61, p < 0.01) (Hengartner and Plöderl, 2019a). This was not a meta-analysis, as Lewis et al. incorrectly told the audience but only a letter to show that a more appropriate analysis revealed significantly more suicides and suicide attempts with antidepressants than with placebo.

Lewis et al. explained that their colleague Joe Hayes performed “all these other meta-analysis that he and everybody else know of” and these analyses showed that there is no significant increase of suicides with antidepressants. Lewis was coauthor of the letter which was published in response to our letter (Hayes et al., 2019). In the talk, the impression arose that an appropriate statistical analysis leads to a different picture and that we failed to apply these appropriate methods. Is this true? In response to Hayes et al., we agreed that a meta-analytic method is more appropriate than our crude analysis, but this would have gone beyond the scope of our original letter where we only wanted to show how misleading analysis based on patient exposure years may be. We only had two weeks to reply to the letter by Hayes et al. and our reply, which included different meta-analytic approaches, was then published together with Hayes’ letter (Hengartner and Plöderl, 2019b). The results are summarized in the table below. There are two problems with Hayes et al.’s meta-analyses. First, some of their methods are not optimal for the data at hand, where events were rare and sometimes there we no events at all. There is no consensus how to deal with such data, but some of the methods Hayes et al. used are not recommended in these instances (Ren et al., 2019; Xu et al., 2022). Several methods are recommended, but this was missed by Hayes et al. (e.g, the exact method or the arcsine risk difference method). This gives the impression that Hayes et al. were selective in choosing methods and not aware that some of them are inappropriate. In contrast, in our meta-analyses, we provided more methods and more appropriate ones, and we did it in a transparent way, making the data and code publicly available. In line with Hayes et al., we found that the drug-placebo differences for suicides were not statistically significant anymore. But I want to stress that we described the evidence for suicides as weak already in our original crude analysis. However, for suicide attempts, the drug-placebo differences remained consistently statistically significant. Strikingly, Hayes et al. did not provide any results for suicide attempts! It seems that they not only selectively had chosen the methods but also selectively reported the outcomes.

Because we became aware that two suicides in the placebo groups in the paroxetine trials actually happened in the placebo lead-in phase and were falsely added to the placebo group, we also provided an additional corrected analysis in our reply to Hayes et al. (see third column in the table below). This resulted in three statistically significant findings for suicides out of the five analysis.

Later, two psychiatrists from Germany published a full paper about our letter and the controversy between Hayes et al. and us and and provided their own meta-analysis of the data (Kaminski and Bschor, 2020), which is also summarized in the table below. They provided a wider range of meta-analytical methods (with some of them ending up in a significant difference for suicides) and a more appropriate Bayesian analysis, which is likely the superior approach with the data at hand. Overall, it became clear that, for suicides, the results are sensitive to the choice of the meta-analytic methods. Not so for suicide attempts, where results were statistically significant in most analyses. We then invited Kaminski and Bschor to publish a response together. They accepted, and a collaborative commentary where we outlined our consensus was published (Plöderl et al., 2020). We agreed that it is important to use the corrected data-set (removing the two misclassified suicides) and that their Bayesian method was the method of choice for such data. We also addressed the (fierce) debate on Twitter about our initial analysis. The most important caveat that Micheal Hengartner and me did not discuss in our initial publication (and I regret that until today), but that also Hayes et al., and Kaminski and Bschor missed, is that the analysis may be biased because the trial data-base also included some extension phases where patients on the drug but not on placebo are observed longer. If suicidal behavior occurs in this phase, than this would lead to an overestimation of the harmful effect of antidepressants. On the other hand, it is known that there is selective misclassification, leading to an underestimation of harmful effects of antidepressants, including suicides and suicide attempts (Le Noury et al., 2015; Sharma et al., 2016). Taking these uncertainties into account, we concluded with “Nonetheless, the analyses consistently hint at an elevated risk for suicide attempts and, less reliably, also for suicides in cohorts of adults. This is remarkable for drugs that are used to treat depressive symptoms” (Plöderl et al., 2020). This is a humble and unbiased look at the evidence and can hardly be dismissed.

Unfortunately, Lewis et al. did not provide a more complete summary of the controversy surrounding antidepressants and suicides. Whereas the findings for suicides and antidepressant use may be considered as inconclusive for adults, suicide attempts were consistently more often found in antidepressants than placebo among young adults (Stone et al., 2009) and among children/adolescents for SSRIs as a group compared to placebo (Hetrick et al., 2021). The RCT-data for older adults is inconclusive for suicides but reduced suicide attempt rates were found with antidepressants (Stone et al., 2009). Furthermore, results from longer-term RCTs on adults again show a significant increased risk for suicide attempts for patients on antidepressants compared to placebo, and rates of suicides are higher too, but not statistically significant (Baldessarini et al., 2015; Braun et al., 2016). Then there are the many observational studies, which found an increased risk for suicide attempts and suicides among children and adolescents who used antidepressants compared to non-users (Barbui et al., 2009; Dragioti et al., 2019). Among adults, for suicide attempts the results are also unfavorable for antidepressants, but perhaps inconclusive for suicides (Hengartner et al., 2021). During our systematic review we also found that favorable results from observational studies are selectively published in psychiatric journals and that there is strong evidence for the presence of publication bias, suggesting that unfavorable results are not published/reported (Plöderl et al., 2023a). For a discussion with more updated evidence, see my discussion with Awais Aftab https://www.psychiatrymargins.com/p/antidepressants-and-the-tangle-of.

In summary, an unbiased view on the evidence about antidepressants and suicides should be cause for concern. It is striking that, in their talk, Lewis et al. only mentioned our study and their correction, but missed to give a broader view on the evidence. Instead, they say they wonder why there is still the controversy despite no evidence for an increase of suicides with antidepressants. This is obviously a misleading and biased view on the evidence.

Undermining the scientific consensus, headlines, populism, post-truth, Trumpism,…

In their conclusion, Lewis et al. draw parallels between the antidepressant controversy and conspiracy, post-truth, Trumpism, anti-elite, undermining liberal democracy, undermining scientific consensus such as with climate change and that “facts seem less influential almost than a kind of opinion an emotional personal belief”. In my opinion, these are very bad comparisons. For example, for climate change, no serious scientist would doubt the scientific consensus that human carbon emission is causally responsible for global warming. Critical positions were perhaps possible many years ago, but scientific data converged.

For antidepressants, the picture is quite different. With more and better research and the consideration of unpublished trials, efficacy got smaller, and it is now more certain that the efficacy is poor and most likely not clinically meaningful for a majority of patients. New research about the smallest worthwhile difference confirmed this. Furthermore, we now know that efficacy is not better (or not much better) for severe depression (also confirmed with the PANDA data), as often claimed, and guidelines had changed accordingly. Now antidepressant are one of several options even for severe depression, whereas previous guidelines clearly recommended antidepressants as first line here. Even in the latest analysis of the FDA database, it became clear that the vast majority does not improve more on antidepressants compared to placebo (Stone et al., 2022). Therefore, in contrast to climate change debates, there is simply no scientific consensus that antidepressants are “working”, therefore the ongoing controversy within the scientific community. I don’t like the binary “work” vs. “does not work” because “work” is an ambiguous term, but the evidence base is more compatible with a “does not work” conclusion than with the claim that antidepressant work. The widespread (over)prescription and the common public believe that antidepressants correct a chemical imbalance contrasts with the evidence about the poor efficacy and the problematic harm/benefit ratio for most patients who take antidepressants. No wonder that journalists and people are surprised or angry to be informed about this discrepancy. And of course I totally agree it is not good to see how this fuels conspiracy and causes further loss of trust. Here it is important to mention that one does not need to assume conspiracy, as many do on social media. Much simpler, it is just typical for systems to confirm their own beliefs and to prevent criticism. That’s just human. But this shows that critical viewpoints from outside are urgently needed (BTW, as someone working in psychiatry, I consider myself as insider).

There’s hypocrisy in Lewis et al.s’ line of argumentation. When there was enthusiasm about the new generation antidepressants with overblown news headlines, it was already discussed that the efficacy is not so good and that there are safety issues (Prozac, for example, was initially rejected in Germany until a key opinion leader took action). Where was the complaint of serious, evidence based psychiatrists about the overly optimistic media presentations? I want to give some more examples where psychiatry reacted with silence mainly/only.

First, when newer generation antidepressants were introduced and increasingly prescribed, there was a reduction of suicide rates in many countries and this was seen as evidence that antidepressants reduced suicide rates and that antidepressants might be a medical breakthrough in suicide prevention (Isacsson, 2000; Mann et al., 2005; Zalsman et al., 2016). However, in the past 10-20 years, the association between antidepressant prescriptions (which are ever increasing) and suicide rates were not in favor of antidepressants anymore (Amendola et al., 2024; Högberg and Bremberg, 2018). No related papers appeared in typical psychiatric journals anymore. Second, in the new Cochrane review on antidepressants for children and adolescents (Hetrick et al., 2021), efficacy of fluoxetine imploded and was only around ES = 0.2 anymore. This is an example of novelty bias where it turns out that drugs loose efficacy in trials not done by the sponsor and where the older drug is used as comparator drug. In contrast, the effect size of fluoxetine was around ES = 0.5 in an influential older meta-analysis (Cipriani et al., 2016) and also the only drug with a significant drug-placebo difference and thus the only recommended drug according to Cipriani et al. Since the appearance of the Hetrick et al. meta-analysis I did not come across any correction of the now outdated recommendation for fluoxetine, increasing the risk of exposing children and adolescents unnecessarily with flouxetine. Third, there was the recent approval of escitalopram for generalized anxiety disorders in children and adolescents. However, in the approval study, it turned out that it was more likely that children/adolescents became suicidal during the trial than to improve in anxiety symptoms (Plöderl et al., 2023b). I am not aware of any critical response from mainstream psychiatry. And it was impossible for us so far to publish a short letter in psychiatric journals, despite several attempts. I want to add another recent very disturbing study which found that most patients who start an antidepressant prescribed by GPs are not monitored as recommended (Hansen et al., 2024), potentially creating harm. I wonder if this study, which did not appear in a psychiatric journal, will be discussed in mainstream psychiatry and efforts will be taken to improve the situation.

Unfortunately, in their attempt to provide a nuanced view on antidepressants, Lewis et al. made too many problematic and misleading claims. They should have done better. Having published several critical papers on antidepressants myself, I experienced that this only can be done very carefully and with much rigor and with way more nuance than what can be found in the talk by Lewis et al., or in typical reviews in psychiatric journals. For example, I would never have chosen strong titles such as “The war on antidepressants.” In the figure below I try to visualize the the double-standards as landscape of biases”.

Interestingly, in a study where psychiatrists were asked what they would do when they were depressed themselves, the majority of psychiatrists would not take antidepressants but would nonetheless recommend antidepressants to depressed patients. Furthermore, if asked by patients what they would do for themselves, they would not admit not to take antidepressants (Mendel et al., 2010) (this study was replicated recently with similar findings and should be published soon). Fortunately, there is an increasing number of physicians and psychiatrists who take the evidence seriously and change their practice accordingly.

References

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Table

	Suicide attempts	Suicides	Suicides, corrected data b
Khan et al. 2018 (PEY)	p > 0.05	p > 0.05
Hengartner & Plöderl 2019a	2.4 (1.6–3.6)*	2.8 (1.1–9.7)*
Hayes et al. 2019
Bayesian	nothing reported	1.2 (0.5–2.3)
Peto	nothing reported	1.7 (0.8–3.9)
MH without cc c	nothing reported	0.7 (0.2–2.2)
MH with cc	nothing reported	1.4 (0.6–3.2)
Inverse variance heterogeneity model (with cc)	nothing reported	1.1 (0.5–2.6)
DerSimonian and Laird (with cc)	nothing reported	1.1 (0.5–2.6)
Reciprocal of opposite treatment arm correction (including both-armed zero event studies)	nothing reported	1.6 (0.7–3.5)
Hengartner & Plöderl 2019b
Bayesian	1.7 (1.1-2.9)*a	2.5 (0.8–45.3)	5.7 (1.4–427.5)*
Exact method	1.6 (1.1-2.50*a	1.9 (0.6–15.0)	3.5 (0.8–768.6)
Peto	1.5 (1.1-2.2)*a	1.7 (0.8-3.9)	2.4 (1.1–5.5)*
MH	1.6 (1.1-2.4)*a	2.00 (0.7-5.5)	4.0 (1.00–16.2)
Arcsine (% risk difference)		0.1 (0.0-0.2)	0.1 (0.0–0.2)*
Kaminski & Bschor (2020)
Bayesian (replication Hengartner & Plöderl)	1.7 (1.1-2.9)*	2.5 (0.8-38.2)
Bayesian 2 (weakly informative prior)	1.7 (1.1-3.0)*	2.0 (0.8-6.1)
Peto without cc	1.5 (1.1-2.2)*	1.7 (0.8-3.9)
MH without cc	1.6 (1.1-2.4)*	2.0 (0.7-5.5)
MH with cc	1.6 (1.1-2.4)*	1.8 (0.7-4.4)
Beta binomial model	1.6 (0.6-4.5)	2.3 (1.1-4.8)*
Arcsine,fixed effect (risk difference)	0.02 (0.0-0.03)*	0.01 (0.0-0.02)*
Arcsine, random effects (risk difference)	0.2 (0.0-0.4)*	0.02 (0.0-0.05)*
Inverse variance with cc (risk difference)	1.5 (1.0-1.3)	1.1 (0.5-2.6)
Inverse variance with treatment arm cc	1.5 (1.0-2.27)	1.1 (0.4 to 3.0)
Plöderl, Hengartner, Bschor, Kaminski (2020)
Bayesian, noninformative prior	1.7 (1.1 - 3.0)*		3.7 (1.2 - 18)*
Bayesian, weakly informative prior	1.7 (1.1 - 3.0)*		3.5 (1.2 - 15)*
Bayesian, very informative prior	1.7 (1.1 - 2.9)*		2.9 (1.1 - 10)*

^a Not reported in paper but, Median instead of mean (skewed distribution)
^b There were misclassified suicides
^c cc: continuity correction
* 95%-confidence interval or 95%-credible interval excluding the null-effect (OR = 1)

Figure