University of Wales College of Medicine, Department of Psychological Medicine, Cardiff
Division of Psychiatry, University of Bristol, Bristol, UK
Correspondence: Professor Glyn Lewis, Division of Psychiatry, University of Bristol, Cotham House, Cotham Hill, Bristol BS6 6JL, UK. E-mail: glyn.lewis{at}bristol.ac.uk
Declaration of interest G.L. has received payment for lectures from a number of pharmaceutical companies.
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ABSTRACT |
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Aims To summarise the findings from all randomised controlled trials (RCTs) that have assessed the efficacy of a pharmacological or psychological intervention for treatment-refractory depression.
Method We used a systematic search strategy to identify RCTs that included adults aged 18-75 years with a diagnosis of unipolar depression that had not responded to a 4-week course of a recommended dose of an antidepressant.
Results We identified 16 RCTs. None of the included trials assessed the efficacy of psychotherapy. All the trials were too small to detect an important clinical response. We found only two trials on lithium augmentation, which randomised 50 subjects in total.
Conclusions There is little evidence to guide the management of depression that has not responded to a course of antidepressants. Treatment-refractory depression is an important public health problem and large pragmatic trials are needed to inform clinical practice.
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INTRODUCTION |
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Current guidance
There is little current guidance on the management of treatment-refractory
depression. Current guidelines (American
Psychiatric Association, 1993; Anderson et al, 2000)
suggest increasing the dose of antidepressant, switching to a different class,
adding psychotherapy or augmenting with lithium or electroconvulsive
treatment. The lack of guidance is reflected by variation in the management of
treatment-refractory depression. A third of psychiatrists in the north-east of
the USA preferred lithium augmentation
(Nierenberg & White,
1990). Canadian psychiatrists
(Chaimowitz et al,
1991) had an equal preference for a second tricyclic, augmentation
with a monoamine oxidase inhibitor and augmentation with lithium. The most
popular choice in the UK (Shergill &
Katona, 1996) was to increase the dose or to change class.
However, 39% of respondents in this study stated that they were not confident
when treating this condition.
Previous systematic reviews
Systematic reviews of the literature attempt to provide an unbiased and
succinct summary of all of the available evidence and, when possible, produce
a meta-analysis that summarises results more precisely
(Chalmers & Altman, 1995;
Lewis et al, 1997).
Previous systematic reviews have assessed the efficacy of lithium augmentation
(Austin et al, 1991;
Bauer & Dopfmer, 1999) and
triiodothyronine augmentation (Aronson
et al, 1996). The systematic review of Austin et
al included 5 trials, but 4 of these used only 3 weeks to define
treatment resistance. One of the trials treated subjects with lithium for only
48 hours, and another reported very low (less than 0.3 mmol/l) blood lithium
levels. Bauer & Dopfmer
(1999) included randomised
controlled trials (RCTs) in their review that studied both unipolar and
bipolar depression. It would seem unwise to generalise from patients with
bipolar depression to those with unipolar depression, especially in relation
to lithium use. The systematic review of four randomised double-blind studies
of triiodothyronine (Aronson et
al, 1996) also included studies that used a 3-week criterion
and patients with bipolar depression.
The aim of this systematic review was to identify and summarise all the RCTs that had investigated the pharmacological and psychological management of patients with treatment-refractory depression.
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METHOD |
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When the search strategy had been completed, the authors of all identified trials (both those to be included and the near misses) and all known experts in the field were contacted for any further information on trials that were unpublished, in press or were currently in progress. If trials presented data on both unipolar and bipolar depression the authors were asked for the results of the unipolar participants.
Inclusion criteria
Randomised controlled trials were included in the review if the
participants had a diagnosis of unipolar depression that had not responded to
a minimum of 4 weeks of antidepressant treatment at a recommended dose (at
least 150 mg/day imipramine or equivalent). This definition was chosen in
order to include as much evidence as possible. Trials that concentrated solely
on patient groups either under the age of 18 years or over the age of 75 years
were excluded, as were trials including patients with comorbid schizophrenia.
Participants with bipolar disorder were excluded. These criteria and the
details of the search strategy were decided before beginning the review and
published as a protocol in the Cochrane Database of Systematic Reviews
(Stimpson et al,
2000).
Summary data from each of the identified trials were extracted independently by at least two of the three reviewers and entered onto predesigned data extraction forms. Any disagreements were discussed until a consensus was reached. If additional information was needed the first author of the trials was contacted.
Statistical methods
Where possible we planned to carry out meta-analysis of the results from
trials. We wished to use a dichotomous outcome, the numbers who had
recovered. This is usually reported as a 50% reduction in
Hamilton Rating Scale for Depression (HRSD) scores
(Hamilton, 1960). This outcome
was chosen for two main reasons. First, it avoids the difficulty of
establishing whether a continuous variable has a normal distribution. Second,
it allows fairly simple analyses that aid interpretation, particularly from a
clinical perspective. We chose to calculate the absolute risk difference (i.e.
the difference in proportion recovered). The reciprocal of this measure is the
number needed to treat (Sackett &
Cook, 1995). A positive value for a risk difference was given when
the proportion recovered was greater in the intervention than in the placebo
group. For the small trials, exact confidence intervals were calculated.
Otherwise, risk difference, 95% confidence intervals and tests for
heterogeneity were calculated using the Metan command within Stata
(StataCorp, 1999).
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RESULTS |
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Exclusions
Fourteen trials were excluded from the review as they included participants
with unipolar and with bipolar depression and it was not possible to extract
data on unipolar depression alone. In 11, participants had been on
antidepressant medication for less than 4 weeks or at a dose of less than 150
mg imipramine or equivalent. Three trials were abandoned on the grounds of the
randomisation. In one relevant trial the randomisation had given rise to a
striking imbalance between the randomised groups
(Gitlin et al, 1987).
This may well have resulted from the small size of these trials
(n=16). One trial randomised participants to identical treatments
(Antonuccio et al,
1984). A full list of excluded studies is available from the
author upon request.
Two crossover trials were also excluded because it was impossible to extract data from the initial phase of the trial before the crossover took place. One published (Gagiano et al, 1993) and one unpublished trial (source available from the author upon request) had to be excluded as they did not describe the study with sufficient detail to know whether the inclusion criteria were met. One trial had to be excluded as data were not available on the subset of participants that were randomly assigned to cognitivebehavioural therapy (Barker et al, 1987). Two papers presented previously published results and the duplicated results are not included in the review (Zohar et al, 1985; Joffe & Singer, 1992).
Included trials
Seventeen RCTs were identified, which included a total of 645 participants.
A variety of different designs were adopted. After extracting the data we have
chosen to classify these designs according to the following four
categories.
Antidepressant (or other) v. placebo
(Table 1)
There were four trials which compared a pharmacological agent with a
placebo (Table 1). The agents
investigated were oestrogen (Klaiber
et al, 1979), viqualine
(Faravelli et al,
1988), ketoconazole (Malison
et al, 1999) and paroxetine
(Tyrer et al, 1987).
Two of these studies were also crossover trials from which we extracted data
for the 2 weeks prior to crossover.
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Two of these trials (Klaiber et al, 1979; Faravelli et al, 1988) found a significant advantage compared with placebo, despite their low statistical power. The largest of these four trials randomised 47 subjects. In three trials that reported recovery rates, none of the 38 subjects randomised to placebo recovered (97.5% CI 0-9%).
We excluded the results from the second phase of the crossover designs.
Comparison of two active treatments
There were four trials that compared two pharmacological agents
(Table 2). The comparisons made
were: intravenous maprotiline v. intravenous clomipramine
(Drago et al, 1983);
brofaromine v. tranylcypromine
(Nolen et al, 1993);
venlafaxine v. paroxetine
(Poirier & Boyer, 1999);
and olanzapine v. fluoxetine
(Shelton et al,
2001).
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The venlafaxine v. paroxetine comparison seems most relevant to current practice. The results of this trial did not support the superiority of one or other compound. Three of the performed analyses led to a result that favoured venlafaxine, but two of these did not adopt an intention-to-treat policy and most were of marginal statistical significance. Almost two-thirds of the subjects had been on a selective serotonin reuptake inhibitor previously. The Shelton study examined the policy of switching between fluoxetine and olanzapine as all the subjects had failed to respond to fluoxetine. There was little information on previous medication for the other studies.
Antidepressant+augmenter v. antidepressant+placebo
The comparison of an augmentation startegy with a placebo seems the most
relevant to clinical practice. Two trials of lithium as an augmentation agent
(Zusky et al, 1988;
Joffe et al, 1993;
Table 3) could be included and
a meta-analysis performed. In summary, lithium had a recovery rate by the end
of the trial 25% greater than placebo (95% CI 2-49%), corresponding to a
number needed to treat of 4 (95% CI 2-50). In all, there were only 50 patients
in the two lithium trials. There was no statistical evidence to support
heterogeneity between the trials (2=0.6, d.f.=1,
P=0.44).
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There were also three trials of pindolol as an augmenter
(Maes et al, 1996; Moreno et al, 1997;
Perez et al, 1999)
reporting on 106 subjects, although one of these
(Moreno et al, 1997)
did not report any recoveries and therefore does not contribute towards the
summary estimate. Overall, those given pindolol had an 8% better recovery rate
(95% CI 21% to -6%) but this was not statistically significant. There was
little evidence to support any heterogeneity between the three pindolol trials
(2=5.46, d.f.=2, P=0.07). Three further trials also
used this design but investigated different augmentation strategies
(Maes et al, 1996; Clifford et al, 1999;
Shelton et al,
2001).
The overall recovery rate on placebo in all the eight trials was 14 out of 107 subjects or 14.4% (95% CI 7.9-23.4%).
Augmentation without a placebo
There were three trials that investigated augmentation of an antidepressant
but did not compare with a placebo (Joffe
& Singer, 1990; Fava
et al, 1994;
Rybakowski et al,
1999) (Table
4).
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Methodological quality of trials
None of the trials would have met all the requirements of the CONSORT
guidelines on reporting results of randomised trials
(Begg et al, 1996).
Two of the trials mentioned that the random numbers were generated with a
computer program. Of the ten trials that used a placebo, four mentioned that
the placebos were identical in appearance to the active treatment. None of the
trials gave an indication of how the allocation of randomisation was
conducted, and only one trial (Perez
et al, 1999) described how the randomisation was
concealed. The two lithium trials mentioned that faked blood results were used
to maintain blindness.
Four studies (Joffe & Singer, 1990; Joffe et al, 1993; Perez et al, 1999; Poirier & Boyer, 1999) reported a power calculation, although one reported a power of 20%. Two trials recruited the exact number of participants required by their power calculations (Joffe & Singer, 1990; Perez et al, 1999). One trial reported that the small sample size recruited had limited the power of their trial (Joffe et al, 1993) and one trial reported a power calculation incorrectly and did not report the sample size it required (Poirier & Boyer, 1999). The size of the randomised groups ranged from a maximum of 62 participants to a minimum of 5 participants. Only 2 of the 17 trials had a group with 25 or more subjects.
Issues not addressed by studies
No RCTs were identified that assessed the efficacy of psychotherapy and
also met the inclusion criteria. A number of trials of psychotherapy were
excluded on various grounds (further details available from the author upon
request).
No RCTs were identified that investigated increasing the dose of antidepressant, or that compared switching to a new class of antidepressant with remaining on the original antidepressant.
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DISCUSSION |
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Methodology
The systematic review used a thorough search strategy as part of the
Cochrane Collaboration. It is still possible, however, that some trials have
not been identified despite our efforts, and we would welcome any information
about trials, particularly those that are unpublished.
The major limitation of the review reflects the major weakness of the constituent trials. Almost all the studies were small in size. Only 2 of the 17 trials had 25 or more subjects in a randomised group. A trial with 25 subjects in each group would be able to detect the difference between 10% and 50% recovery with 80% power and 5% significance. This is a large difference in outcome, much larger than the 14% difference reported in a recent meta-analysis of fluoxetine v. placebo (Bech et al, 2000). A trial would have to randomise 219 subjects to each group to detect a difference between 10% and 20% recovery with 80% power and 5% significance. All the trials in this study were therefore severely underpowered. Small trials can also lead to a failure of randomisation, resulting in an imbalance between the randomised groups. We came across two studies where this had occurred and excluded them, but smaller degrees of imbalance might still be present.
Publication bias was impossible to assess as the trials studied such a diverse range of interventions. It is usually assumed that systematic reviews of small trials are likely to be more susceptible to publication bias than those that include larger trials. Even meta-analysis of moderately sized trials can provide biased conclusions (LeLorier et al, 1997).
Since 1996, the CONSORT statement has provided guidance on the reporting of RCTs (Begg et al, 1996). None of the 17 studies, including those published after the CONSORT statement, followed all aspects of its guidance. Trials with inadequate concealment of allocation are associated with an increased estimate of benefit (Moher et al, 1998). Only one trial described how they kept the allocation of subjects concealed from the clinicians involved in their care (Perez et al, 1999). Overall, the trials did not meet the current expectations concerning the adequate reporting of randomised trials.
Inclusion criteria
The World Psychiatric Association
(1974) defined
treatment-refractory depression as a failure to respond after a 4- to 6-week
period on a recommended dose of antidepressant. When planning the review and
without prior knowledge of the included studies, we chose to set our inclusion
criteria using a time limit of 4 weeks. This minimum time limit was considered
appropriate for a systematic review as it would ensure that we collected all
relevant studies. It also reflected the commonest clinical dilemma: what to do
next after lack of response to an antidepressant. We were surprised that we
excluded nine trials on the grounds that they defined treatment-refractory
depression using a time limit of 3 weeks. Because the response to
antidepressants can be delayed, we think this definition is rather too broad.
We also excluded 14 trials on the grounds that they included both patients
with bipolar and with unipolar depression. The management of depression in
those with bipolar depression differs in some important respects from those
with unipolar depression. Antidepressants are used more cautiously in case
this precipitates a manic relapse. In the context of a trial, a manic relapse
might lead to an apparent improvement in depression scores. Most
people with established bipolar disorder would also be on a mood stabiliser
such as lithium.
Design of trials
We excluded the second phase of crossover designs as these are
inappropriate for antidepressant trials in which subjects may recover.
Antidepressants have a delay of 2-3 weeks before they take effect and so short
periods before crossover are uninformative, as acknowledged by Tyrer et
al (1987).
We identified four different designs in our included studies. Four studies compared an antidepressant v. a placebo, thus investigating removing an antidepressant agent and replacing with placebo. Because some subjects with treatment-refractory depression will have had a partial response, removal of antidepressant would be expected to lead to a worsening of symptoms. Two of the four trials using this design found improved recovery on active antidepressant. These results argue against stopping antidepressant medication in those who have not had a good response.
Four trials compared two active treatments. This also investigates switching to another antidepressant following failure to respond. However, the most relevant trial (Poirier & Boyer, 1999), which compared venlafaxine and paroxetine, included subjects that had been exposed to either selective serotonin reuptake inhibitors, tricyclics or both. To study the policy of switching to a new antidepressant, a more informative design would be to recruit subjects who had been treated with a single class of antidepressant and then randomise to either staying on the same class of antidepressant or switching to an alternative class. This design was used (Shelton et al, 2001) to compare remaining on fluoxetine with switching to olanzapine.
Augmentation
The most informative designs were those in which an augmenting agent was
added to antidepressant medication and compared with a placebo and
antidepressant. Our finding that 14% (95% CI 8-23%) of the placebo group
recovered emphasises the necessity of a placebo comparison for studies of
augmentation.
The two lithium trials were small, with only 50 patients in all, and treated subjects for 1-2 weeks, a relatively short duration. Although there was a statistically significant benefit for lithium, the confidence intervals are so wide (2-49%) that it does not exclude an inconsequential benefit. Meta-analysis of small trials often leads to unreliable results as randomisation is less effective and publication bias more common. These studies provide very weak evidence to support the use of lithium, although it is a common strategy and has widespread clinical support.
Pindolol is a ß-adrenoceptor/5-HT1A receptor antagonist and has been investigated as an augmentation agent in three randomised trials. Overall, there was no significant benefit demonstrated in these three trials. In aggregate, only 106 patients were studied and the wide confidence intervals did not exclude the possibility that pindolol would be an effective augmenting agent.
Further research
The results of our review support the view that further RCTs need to be
conducted to investigate the management of treatment-refractory depression.
The STAR*D project
(http://www.edc.gsph.pitt.edu/stard/)
funded by the US National Institute of Mental Health will hopefully address a
number of the deficiencies in the current literature. We suggest that future
RCTs should concentrate on studying the effectiveness of psychotherapy as it
is a popular and acceptable option for many patients. The second area of
research should be into augmentation strategies. Lithium is supported by the
most encouraging results at present, but the evidence is still weak. Further
trials should estimate the likely benefits of lithium more accurately and also
attempt to refine the indications for its use.
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Clinical Implications and Limitations |
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LIMITATIONS
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Received for publication November 29, 2001. Revision received May 14, 2002. Accepted for publication May 17, 2002.
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