Second‐generation antipsychotic drugs for major depressive disorder
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of second generation antipsychotics for people with major depressive disorder or dysthymia.
Background
Description of the condition
Major depressive disorder is a common condition with a lifetime prevalence of 15‐18% (Berger 2004). Its main symptoms are depressed mood and lack of interest or pleasure in activities. The World Health Organization (WHO) estimates that depression affects about 121 million people in the world (WHO 2005). Some authors describe a lower prevalence of major depression according to DSM‐IV in Japan (lifetime prevalence 3‐7%) compared to Western countries, suggesting that the prevalence of major depression might be lower in Asian countries (Kawakami 2007). In the year 2020 it could become the second disease in the entire world population after cardiovascular diseases (Gayetot 2007).
The degree of suffering and disability of those with depression can be dramatic. For example, in the year 2005 unipolar depressive disorders were in second place for disability adjusted life years (DALY) in Germany (WHO 2005). Suicide rates are as high as up to 15% (Berger 2004).
In the revision of the 2000 British Association for Psychopharmacology guidelines (Anderson 2008), the authors suggest that additional treatment with second generation antipsychotics should be considered in case of treatment resistance. Some antipsychotics have been reported to induce remission in major depression, when added to an antidepressant (Goodwin 2009).
Description of the intervention
While antidepressant drugs are efficacious treatments for depression, the rates of treatment resistance are high. Gayetot 2007 reported that approximately 30% ‐ 45% of patients treated for major depressive disorder show either only a partial response or none at all to treatment with antidepressants. Therefore, there is a need for other agents to alleviate the symptoms of this disorder.
Second‐generation ('atypical') antipsychotic drugs were introduced for the treatment of schizophrenia in the 1990s. This drug class may include: amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, paliperidone, risperidone, sertindole, ziprasidone or zotepine. Their main advantage compared to conventional antipsychotic drugs such as haloperidol is that they induce fewer extrapyramidal side effects, including the disabling, often irreversible and stigmatizing condition of tardive dyskinesia (Correll 2004). Superior tolerability and potential effects on depressive and negative symptoms make them candidates as sole or adjunctive agents for the treatment of disorders other than schizophrenia.
In clinical routine, second‐generation antipsychotics are already frequently being used for depression (Ravindran 2007). There is evidence that 70 % of all prescriptions of second‐generation antipsychotics are for indications other than schizophrenia (Sajatovic 2003). In the US population the rate of antipsychotic use has increased substantially between 1996–1997 and 2004–2005. The rapid diffusion of antipsychotic medications did not occur among individuals with schizophrenia, but proceeded rather from substantial growth among those with newer on‐label conditions (such as bipolar disorder) and a high, constant rate of off‐label use (Domino 2008). In Italy, data from the South‐Verona Psychiatric Case Register 2001–02 indicated that during the two years surveyed nearly 50% of the second‐generation antipsychotic prescriptions were for an off‐label indication (Barbui 2004). Manufacturers of these drugs also aggressively try to expand the indications of their compounds; however, the second‐generation antipsychotic drugs are very costly. For example, the estimated costs of second‐generation antipsychotic drugs totaled $11.7 billion in the United States in 2005 (Vital Signs 2007). Furthermore, some second‐generation antipsychotics are associated with severe adverse events such as weight gain (Allison 1999).
How the intervention might work
Second generation antipsychotic drugs block central dopamine receptors, most of them also block serotonin receptors and many other neuroreceptors (Arnt 1998). Second generation antipsychotics possess pharmacological actions that are associated with antidepressant properties including serotonin 5‐HT (2) receptor antagonist and 5‐HT (1A) and dopamine receptor partial agonist activity (Debattista 2009).
Some types of depression are accompanied by psychotic features. There is some evidence that they might respond to additional antipsychotic treatment (Anderson 2008).
In summary, a number of mechanisms have been hypothesized to explain possible effects of second‐generation antipsychotics on depression (e.g. effects on serotonin, norepinephrine or dopamine receptor systems, for a review of these, see Yatham 2005), but a definitive explanation is not yet available.
Why it is important to do this review
Given the frequent use in practice, the uncertain efficacy, the side‐effects and the high costs of second‐generation antipsychotic drugs in major depressive disorder an systematic review is essential. We identified one systematic review on five of ten second generation antipsychotics (Papakostas 2007) that included ten trials. In a preliminary search we identified more than 20 potentially relevant double‐blind trials, making an up to date systematic review important.
Objectives
To assess the effects of second generation antipsychotics for people with major depressive disorder or dysthymia.
Methods
Criteria for considering studies for this review
Types of studies
We will include all randomized double‐blind trials, meaning that at least the participants, the raters and the treatment team were blinded (double‐blind is a conventional definition of this situation in drug trials). Cluster randomized studies meeting certain criteria will also be included.
Types of participants
People with unipolar major depressive disorder according to DSM‐III (APA 1980) / DSM‐IV (APA 1987; APA 1994) (296.2 or 296.3) or ICD‐10 (F32 or F33) (WHO 1992) will be included. There will be no limits in terms of setting or age of participants. People with dysthymia according to DSM‐III/DSM‐IV (300.4) or ICD‐10 (F 34.1) will also be included, but analysed in a separate comparison. We will exclude the people with comorbid or primary diagnosis of schizophrenia, bipolar disorder, mental retardation or dementia will be excluded. People with primary anxiety disorder will also be excluded. MDD trials in participants with a serious concomitant medical illness will not be excluded.
Types of interventions
Second generation antipsychotics might be given as mono or adjunctive treatment compared to antidepressants, mood stabilizers, benzodiazepines or placebo. There will be no limits in terms of study duration.
1. Experimental treatments will be one of the following second generation antipsychotic drugs, any dose, any oral mode of administration: amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, paliperidone, risperidone, sertindole, ziprasidone, zotepine.
2. Comparator substances will be either placebo, a benzodiazepine or any of the following antidepressants, all at any dose and oral mode of administration: tricyclic/heterocyclic antidepressants, SSRIs (fluoxetine, paroxetine, sertraline, fluvoxamine, citalopram, escitalopram), SNRIs (venlafaxine, duloxetine, milnacipran), MAOIs or newer agents (mirtazapine, bupropion, reboxetine) or St John’s Wort. Treatment can be given either as monotherapy or as add‐on.
We will exclude treatment with first generation antipsychotics, which due to their overall higher risk of extrapyramidal side‐effects are usually not the first line antipsychotics in the treatment of depression. Head‐to‐head comparisons of second generation antipsychotic drugs will also be excluded. Psychological treatment will be allowed as long as it is provided to both the treatment and control group. We will exclude studies with only non pharmacological treatment as comparator.
There will be no limits in terms of duration of treatment. We will classify the outcomes as short term (up to 12 weeks), medium term (3 to 6 months) and long term (longer than 6 months).
Types of outcome measures
Primary outcomes
Number of patients who responded to treatment, showing a reduction of at least 50% on the Hamilton Depression Scale (HAM‐D (Hamilton 1960)) or the Montgomery Åsberg Depression Rating Scale (MADRS (Montgomery 1979)) or at least 'much improved' on the Clinical Global Impressions Scale (CGI) (Guy 1976) score 1 or 2. Only if none of these criteria have been indicated will we use the criteria applied by the authors.
Secondary outcomes
1. MADRS and HAMD scores at the end of the studies.
2. Remission, defined by 7 or less on the 17‐item HAM‐D (8 or less for all the other longer versions of HAM‐D) or 10 or less on the MADRS (Zimmermann 2004).
3. Relapse as defined by the authors.
4. Anxiety symptoms will be addressed by the Hamilton Anxiety Scale (HAM‐A (Hamilton 1959)) scores at the end of the study.
5. Premature study discontinuation due to any reason, due to inefficacy of treatment, due to adverse events.
6. Adverse events (use of antiparkinson medication, tardive dyskinesia, weight gain, sedation, prolactin increase).
7. Service use ‐ numbers of participants rehospitalised.
All efficacy data (CGI, HAMD, MADRS, HAMA) will also be evaluated dichotomously, if data is available.
Search methods for identification of studies
Electronic searches
With the assistance of the Cochrane Collaboration Depression, Anxiety and Neurosis Group's (CCDAN) Trials Search Coordinator (TSC) we will search the Group's Controlled Trials Registers (CCDANCTR‐References and CCDANCTR‐Studies). The CCDANCTR‐References Register contains more than 23,000 references to completed or ongoing trials in depression, anxiety and neurosis, of which 16,000 have been coded in the CCDANCTR‐Studies Register. The CCDANCTR References Register is updated weekly with the results of searches of MEDLINE (1966‐), EMBASE (1980‐) and PsycINFO (1974‐). CENTRAL is searched every 3 months (with each new release of this database on the Cochrane Library); PSYNDEX (1977‐), LILACS (1982‐), KoreaMed and IndMed are searched on an annual basis and AMED (1985‐) and CINAHL (1980‐) are searched on an individual review basis (or at least annually). In addition to this, references to trials identified from hand‐searches of major psychiatric, medical journals and conference proceedings are also included in the CCDAN Registers.
The search terms used will be: ("Depress*" or "Dysthymi*" or "Adjustment Disorder*" or "Mood Disorder*" or "Affective Disorder*" or "Affective Symptoms") and (amisulprid* OR aripiprazol* OR clozapin* OR olanzapin*OR quetiapin* OR paliperidon* OR risperidon* OR sertindol* OR ziprasidon* OR zotepin*).
Searching other resources
KK and AMD will inspect the references of all identified studies and of previous reviews for more trials.
KK and SL will contact the first author of each included study for missing information and for the existence of further studies.
KK and SL will contact the manufacturers of atypical antipsychotic drugs and ask them about further relevant studies and for missing information on identified studies.
Data collection and analysis
Selection of studies
Authors KK and AMD will independently inspect citations identified from the search. All potentially relevant reports this identified will be ordered for reassessment. Where difficulties or disputes arise we will asked authors SL and WK for assistance / adjudication and if it is impossible to decide, full texts will be ordered for assessment. This process will be repeated for the assessment of the full texts. If it is impossible to resolve disagreements, authors of the papers will be contacted for clarification.
Data extraction and management
Authors KK and AMD will independently extract data from included studies. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems SL and WK will assist to clarify issues and those final decisions will be documented.
Data will be extracted onto standard, simple forms.
Assessment of risk of bias in included studies
Again, working independently, KK and AMD will assess risk of bias using the tool described in the Cochrane Collaboration Handbook (Higgins 2008). This tool encourages consideration of how the sequence was generated, how allocation was concealed, the integrity of blinding at outcome, the completeness of outcome data, selective reporting and other potential sources of bias. We will not include studies where sequence generation is assessed as being at a high risk of bias, where allocation is clearly not concealed, and where double‐blinding has not taken place.
If disputes arises as to which category a trial will have to be allocated, again, resolution will be made by discussion, after working with a third reviewer (SL or WK).
Measures of treatment effect
1. Binary data
We will calculate the odds ratio (OR) and its 95% confidence interval (CI).
2. Continuous data
We will calculate the weighted (N) mean differences as it preserves the original units and is therefore easier to interpret.
2.1 Summary statistic
For continuous outcomes we will estimated a random effects standardised weighted mean difference (SMD) between groups.
2.2 Change versus endpoint data
We will use change data only when endpoint data is not available
2.3 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we apply the following standards to all data before inclusion: (a) data from studies of e.g. at least 200 participants will be entered in the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies. (b) Endpoint data: when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation. If this value was lower than 1, it strongly suggests a skew and the study will be excluded. If this ratio is higher than one but below 2, there is suggestion of skew. We will enter the study and test whether its in or exclusion substantially would change the results. If the ratio was larger than 2 the study will be included, because skew is less likely (Altman 1996, Higgins 2008). (c) When continuous data are presented on a scale which includes a possibility of negative values (such as change data), it is difficult to tell whether data is skewed or not. We will enter the study, because change data tends to be less skewed and because excluding studies would also lead to bias, because not all the available information was used.
Unit of analysis issues
1. Cluster trials
Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra‐class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby p values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997, Gulliford 1999).
Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. We will seek to contact first authors of studies to obtain intra class correlation co‐efficient of their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering is incorporated , we will present the data as if from a parallel‐group randomised study, but adjusted for the clustering effect. We will additionally exclude such studies in a sensitivity analysis.
If cluster studies are appropriately analysed taking into account intra‐class correlation co‐efficient and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Cross‐over trials
A major concern of cross‐over trials is the potential for carryover effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence on entry to the second phase the participants can differ systematically from their initial state despite a wash‐out phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in depressive disorder, randomised cross‐over studies will be eligible but only data up to the point of first cross‐over, data from the following (second) period of the cross‐over trial will not be considered for analysis. We will describe cross‐over studies to be at risk of bias and we will exclude cross‐over studies in a sensitivity analysis.
3. Studies with multiple treatment groups
1. Multiple dose groups
We expect that some studies will address the effects of different doses of the same compound compared to the competitor (e.g. amisulpride 200mg/day, amisulpride 400mg/day and placebo). In the case of dichotomous outcomes we will sum up the sample sizes and the number of people with events across both (amisulpride) groups. For continuous outcomes means and standard deviations will be combined using methods described in chapter 7 (section 7.7.3.8) of the Cochrane Handbook (Higgins 2008).
2. Multiple medications
We expect that some other studies will combine several interventions with one comparison group (e.g. a three arm study comparing amisulpride and olanzapine with placebo). In this case we will analyse the effects of the amisulpride and olanzapine group versus placebo separately, but will divide up the total number of participants in the placebo group. In the case of continuous outcomes the total number of participants in the placebo group will again be divided up, but the means and standard deviations will be left unchanged (see chapter 16, section 16.5.4 in Higgins 2008).
Dealing with missing data
1. Missing participants
Dichotomous data:
All data will be analysed on the basis of the ITT principle: dropouts will always be included in this analysis. Where participants have withdrawn from the trial before the endpoint, it will be assumed their condition would have remained unchanged if they had stayed in the trial. This is conservative for outcomes related to response to treatment (because these participants will be considered to have not responded to treatment). It is not conservative for adverse events, but we think that for the adverse events of interest in our review (see outcomes) a worst case scenario is clinically unlikely. When there are missing data and the method of “last observation carried forward” (LOCF) has been used to do an ITT analysis, then the LOCF data will be used, with due consideration of the potential bias and uncertainty introduced. We are not going to perform a “worst case” and “best case” ITT analysis.
Continuous data:
Concerning continuous data, the Cochrane Handbook recommends avoiding imputations of continuous data and suggests rather that the data must be used in the form they have been presented by the original authors. Whenever ITT data have been presented by the authors they will be preferred to ‘per protocol/completer’ datasets. Furthermore, we acknowledge that all methods of imputation to deal with missing data introduce uncertainty about the reliability of the results. This will depend on the degree of ‘missingness’, the pooled estimate of the treatment effect and the variability of the outcomes. We will consider variation in the degree of missing data as a potential source of heterogeneity.
2. Missing statistics
When only the SE or p values are reported, SDs are calculated according to Altman (Altman 1996). In the absence of supplemental data after requests to the authors, the SDs will be calculated according to a validated imputation method (Furukawa 2006). We will examine the validity of these imputations in the sensitivity analyses (Cipriani 2007).
Assessment of heterogeneity
We will assess heterogeneity on the basis of the Cochrane Handbook's recommendations (I2 values of 0‐40%: might not be important ; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: considerable heterogeneity). In addition to the I 2 value (Higgins 2003) we will present the χ2 and its p‐value and consider the direction and magnitude of the treatment effects. As in meta‐analysis with few studies the χ2 test is underpowered to detect heterogeneity should it exist, a p‐value of 0.10 is used as a threshold of statistical significance.
Assessment of reporting biases
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook (Higgins 2008). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are ten or fewer studies, or where all studies are of similar sizes.
Data synthesis
We will employ the random‐effects model for analysis (Der‐Simonian 1986). We understand that there is no closed argument for preference for use of fixed or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This does seem true to us as we are a priori expecting some clinical heterogeneity between the patients in the different trials.Therefore, we chose the random effects model for all analyses
Subgroup analysis and investigation of heterogeneity
We plan a subgroup analysis based on whether response to treatment depended on whether or not participants with a history of treatment resistance were included. We will also analyse whether the response of people with psychotic depression differs from that of people without psychotic features.
When we find high inconsistency of effects by the measures explained above and clear reasons explaining the heterogeneity are present, we will present the data separately. If not, we will comment on the heterogeneity of the data.
Sensitivity analysis
We will conduct the following sensitivity analyses to investigate the degree to which the effect sizes depend on the assumptions made by the reviewers: we will exclude cluster trials, cross‐over trials, children included, imputed statistics and risk of bias assessment.
