The war on antidepressants: What we can, and can't conclude, from the systematic review of antidepressant withdrawal effects by Davies and Read

1. Introduction

We read with great interest the recent review of antidepressant withdrawal by Davies and Read and the widespread press coverage which followed. We agree that symptoms associated with withdrawal from antidepressants are important and we do not wish to minimise the impact reported by some individuals. Recognition of withdrawal symptoms following antidepressant treatment is not new: it dates from 1959 (Andersen and Kristiansen, 1959; Mann and Macpherson, 1959), has been reported with practically all antidepressants, and is included in DSM-5. Typically, studies describe sensory, gastrointestinal, somatic, affective disequilibrium and sleep symptoms, though symptoms vary depending on drug class (Haddad and Anderson, 2007). Evidence suggests risk of withdrawal symptoms is associated with plasma elimination characteristics and off-target effects of each drug. This phenomenon is not uniform nor experienced by all people (Renoir, 2013). The incidence, severity and duration of symptoms have not been fully quantified and Davies and Read attempt this in their review (Davies and Read, 2018). They state, in their discussion, “review of the quantitative studies concludes that more than half (56%) of antidepressant users experience withdrawal, with the majority of these describing their withdrawal as moderate or severe, and nearly half (46%) as severe.” This review was carried out for the United Kingdom's All-Party Parliamentary Group for Prescribed Drug Dependence and Davies and Read conclude that guidelines on treatment of depression must be “urgently updated”. We do not agree that the evidence supports these bold statements. Moreover, the interpretation that all such effects can be causally related to pharmacology is wrong and misleading.

2. Adherence to accepted methodology for critical appraisal

It is vital that evidence is appropriately appraised if it is to support changes in policy or guidelines. PRISMA is the widely accepted approach and the authors state that these guidelines (Moher et al., 2009) were used to inform their search strategy. However, PRISMA does not appear to have informed the methodology of the review, it is therefore difficult to follow, and, more importantly, to be confident in its conclusions. Most obviously, the authors invert the traditional hierarchy of evidence, giving most weight to survey data and less to that from randomised controlled trials (Evans, 2003). This is critical for the interpretation that any effect is actually attributable to the pharmacology of a drug treatment. Imagine the scorn if the claim were made that contributions to websites devoted to the positive experience of patients on antidepressants outweighed the small benefits seen in RCTs. Below we outline a number of the specific methodological concerns.

3. Inclusion criteria

There is no evidence that the systematic review inclusion criteria were registered in advance (as recommended in PRISMA). For the three questions addressed (incidence, severity and duration of withdrawal), differing inclusion/exclusion criteria are used. When addressing severity of withdrawal, the authors only consider survey data. The reason given is that many of the randomised trials and naturalistic studies are shortterm, or at risk of potential bias owing to conflicts of interest. However, if Davies and Read are using the latter studies for the quantification of withdrawal incidence, assuming that their data is valid for that purpose, it is baffling why it would not be valid for reporting severity. It would have been legitimate, for example, to report withdrawal severity from all included studies and then stratify for type of study. Similarly, it is unclear if factors such as length of follow-up, length of antidepressant exposure, pharmaceutical company funding and choice of outcome measure were defined a priori as exclusion criteria by the authors.

There appear to be a number of post-hoc decisions about the data. For example, for incidence estimates, the authors describe exclusion of “outlier” studies which report withdrawal incidence at 11–12% and, give various reasons for this. They also exclude a number of studies summarised by Baldwin and colleagues (all of which used the extensive discontinuation emergent signs and symptoms (DESS) questionnaire (discussed below)), which report withdrawal incidence in the ranges of 1.9–12.2% (placebo), 6.9%–27.3% (escitalopram), 28.4–32.7% (paroxetine) and a figure of 31.5% for venlafaxine (Baldwin et al., 2007). It is unclear to us why these studies were excluded for incidence estimates. If they had been included, the definition of what constituted an “outlier” would have changed.

Methodologically, for incidence and severity estimates, the authors conducted a meta-analysis to calculate a “weighted average”. There is no description of the method used and the statistical reporting is inadequate. There are no confidence intervals included for the summary estimates and no attempt to quantify the heterogeneity between studies. To illustrate these issues, we undertook a re-analysis of the studies included in the original review of withdrawal incidence, along with the excluded studies discussed above and correcting errors in data extraction ¹. We performed a random effects meta-analysis using the Freeman-Tukey transformation for binomial data, using Stata 15 (Stata Corp, 2015). As expected, pooled incidence rate of withdrawal as assessed by survey methods was significantly higher than by randomised controlled trials (RCTs) (Fig. 1). Despite this, heterogeneity was very high in each subgroup, suggesting meta-analysis to be an inappropriate methodology. Similarly, pooled withdrawal rates for individual drugs were highly heterogeneous (as one might expect).

Fig. 1. Occurrence of withdrawal symptoms by antidepressant and study design.

*studies excluded by Davies and Read.

4. Assessment of study quality

If a reader is to make sense of a combination of heterogenous studies, a measurement of study quality would be helpful for data interpretation. Though the authors make a point of identifying studies funded by drug companies, and potential conflicts of interest related to pharmaceutical companies, there is no formal measure of risk of bias.

For example, though undoubtedly rich in qualitative data, convenience sample surveys are not generally accepted for quantitative analysis, with clear criteria set by journals for even including their quantitative measures (Bethlehem, 2010; Colleen Cook, Fred Heath, Russel L. Thompson, 2000). It is tendentious to generalise data from such surveys to the general population of people receiving antidepressants.

The estimates of withdrawal severity are only taken from surveys. Two of the four surveys are from people self-identifying as experiencing withdrawal requiring treatment (people using tapering kits (Groot and Van Os, 2018) and people contacted through withdrawal websites (Davies, Pauli and Montagu, 2018). Therefore, this population of people are more likely, by the very nature of sampling method, to report severe symptoms. The authors do not measure study quality or comment on potential selection bias in these surveys, which is extraordinary. Their interpretation of the effects as drug effects ignores a host of potential attributional and other confounding factors which must contribute to the reporting of withdrawal symptoms under unblinded conditions. They seem also to misunderstand simple principles that underpin why blinded RCTs are necessary. Thus, in the trial by Montgomery et al. (Montgomery et al., 2005), DESS score was higher during placebo treatment than active treatment. This omission then leads the authors to mistakenly state, “Although we were unable to assess what role, if any, nocebo effects played, it is probably minimal due to the nature of the withdrawal symptoms reported.” The findings from the Montgomery study illustrate precisely what a nocebo effect is.

5. Mixing of antidepressant types

It is difficult to understand why antidepressants with different pharmacokinetic properties and modes of action are combined in the analysis. For example, fluoxetine has a half-life of 4–6 days after longterm use (active metabolite half-life 4–16 days) compared to paroxetine (approximately 21 h) and venlafaxine (approximately 5 h). Evidence suggests medications with longer half-lives are associated with fewer withdrawal effects. Furthermore, drugs with similar half-lives can have significantly different effects on neurotransmitter systems. For example, paroxetine has more cholinergic effects than sertraline, despite having a similar half-life. A good example of the fallacy of combining antidepressants is given in a double-blind placebo controlled RCT, in which people were switched from paroxetine or agomelatine to placebo or continued on the original drug, withdrawal being measured using DESS. Whilst there was a statistically significant increase in the paroxetine group compared to placebo, there was no difference in the agomelatine group (Montgomery et al., 2004). Given that this difference in withdrawal is well recognised in the literature, it is a major conceptual failure to not address it in the review.

5.1. Outcome measures

In addressing incidence of withdrawal symptoms, Davies and Read consider the 43 item DESS questionnaire as the definitive measure of withdrawal, as do many regulatory agencies (Baldwin et al., 2007). This was developed as a continuous measure by Rosenbaum and colleagues (Rosenbaum et al., 1998), The DESS appears somewhat non-specific because it includes items that are very likely to be confounded by mood or anxiety symptoms. However, since it does not rely on spontaneous report, it should be quite sensitive.

Reporting of DESS in the review is not uniform. It is usually given as a mean and a dichotomous outcome based on thresholding the scale for the presence or absence of a discontinuation syndrome. Thus, the authors report the incidence ≥4 symptoms from four studies (Montgomery et al., 2005; Fava et al., 2007; Rosenbaum et al., 1998; Hindmarch et al., 2000), ≥ 3 symptoms from two studies (Tint et al., 2008; Yasui-Furukori et al., 2016), and ≥ 2 symptoms in one study (Bogetto et al., 2002), the remainder are even less stringent. The primary studies themselves use a mixture of definitions, some a total score, some a change in score. Using a total score as low as four is problematic and is only plausible because mean increases are so low in many RCTs with most SSRIs. Indeed, that the high rates of “discontinuation syndrome” when the DESS is used as a dichotomous outcome may be misleading, was remarked soon after its introduction (Hindmarch et al., 2000).

Most studies do not use a change in symptoms, but simply presence of symptoms in the discontinuation period, and therefore exclude effects of baseline scores, which is not addressed in the review. Furthermore, withdrawal symptoms themselves are not homogeneous; they vary amongst medications, across physiological systems and individuals and no effort is made to unpick this complexity or even acknowledge it. The generally very small average increases in the DESS seen under double blind conditions are the basis for the consensus view that the pharmacological contribution to what happens when patients stop SSRIs (with the partial exception of paroxetine) are mild and transient.

5.2. Selective reporting

Throughout the review there appear to be examples of selective reporting of study findings. For example, in the Zajecka trial, where incidence of withdrawal symptoms was numerically higher in those continuing antidepressants (76%), compared to those stopping (67%), the authors of the review report only the latter figure and do not mention to readers that the study included a control arm. Furthermore, in citing this trial as evidence of prolonged withdrawal, the authors neglect to mention the trial authors' statement that withdrawal symptoms were “of little clinical significance”, reporting only that the trial reported withdrawal lasting at least 6 weeks in 40% of people. (Zajecka et al., 1998). As noted above, the authors do not mention withdrawal symptoms occurring in people receiving placebo, as opposed to active drug (Oehrberg et al., 1995), which invalidates statements about the frequency of withdrawal due specifically to antidepressants.

6. Conclusion

In conclusion, the review clearly illustrates the contrast between the modest, albeit heterogeneous average effects of antidepressant drug discontinuation in RCTs and the anecdotal reporting of severe symptoms related to open label discontinuation of antidepressants in ordinary practice. However, on the basis of our critique, this review fails to adhere to widely accepted standards. More importantly, it is difficult to see how the evidence that Davies and Reed present can be extrapolated to the general population of people taking antidepressant medication. Finally, it is simply misleading to suggest that the evidence supports a simple pharmacological explanation for what some patients report. We urge readers to view the results and particularly the conclusions they present with great caution.

In the Montgomery study the incidence of withdrawal symptoms following escitalopram treatment is presented as 27% at 2 weeks, when it is 16% (Montgomery et al., 2005); there are 97 people in the Bogetto study, rather than the 95 reported (Bogetto et al., 2002); there are 8 patients prescribed paroxetine in the Tint study, rather than 9 (Tint, Haddad and Anderson, 2008); the Hindmarch and colleagues paper was published in 2000, rather than 2017 (Hindmarch, Kimber and Cockle, 2000); the total number experiencing withdrawal in the study by Sir and colleagues is 83 rather than 110 by Davies and Read's categorisation of individual antidepressants in this study (Sir et al., 2005). Whilst each of these errors is minor, they suggest this review did not undergo the rigorous level of quality checking which the readership should expect.