Criteria for considering studies for this review
Types of studies
Published and unpublished randomised controlled trials comparing bupropion with all other active antidepressants as monotherapy for acute phase treatment of major depression will be included. For trials that have a crossover design, only results from the first period prior to crossover will be considered. Cluster randomised trials will be included if the effect of clustering can be accounted for in the statistical analysis.
Quasi-randomised trials, such as those allocating by using alternate days of the week, will be excluded as will trials that randomise participants to receive more than one type of antidepressant simultaneously. We will exclude trials that do not explicitly describe the method of allocation as randomised. We will also exclude trials that are not double-blind.
Types of participants
Age and diagnosis
Patients of both sexes aged 18 years or older with a primary diagnosis of a unipolar major depressive disorder according to any of the following standard operational criteria: Feighner criteria (Feighner 1972), Research Diagnostic Criteria (Spitzer 1978), DSM-III (APA 1980), DSM-III-R (APA 1987), DSM-IV (APA 1994), or ICD-10 (WHO 1992), will be considered for inclusion. Studies using operational diagnostic criteria essentially similar to the above will be included. We will exclude studies using ICD-9 as it has only disease names and no diagnostic criteria. We will also exclude studies which define depression as scoring above a certain cut-off on a screening questionnaire.
Studies in which less than 20% of participants may be suffering from bipolar depression will be included but the validity of this decision will be examined in a sensitivity analysis. Concurrent secondary diagnosis of another psychiatric disorder will not be considered an exclusion criterion. However, studies in which all participants have a concurrent primary diagnosis of another Axis I or II disorder, or resistant depression, will be excluded. Participants with a serious concomitant medical illness or with post-partum depression will be excluded.
Types of interventions
1. Bupropion: any dose and pattern of administration.
2. Conventional anti-depressive agents: any dose and mode or pattern of administration:
2.1 Tricyclics (TCAs);
2.5 MAOIs or newer antidepressants (ADs); and
2.6 Other conventional psychotropic drugs.
3. Non-conventional anti-depressive agents:
3.1 Hypericum; and
3.2 Other non-conventional anti-depressive agents
All interventions must be monotherapies. Trials which allow rescue medications (as required, short-term, infrequent use of medications that aim at emergent symptom relief only, e.g. short-term use of hypnotics) will be included as long as these medications are equally distributed among the randomised arms.
Types of outcome measures
1. Response to treatment - acute phase
The primary efficacy outcome will be the number of participants who respond to treatment, where treatment response is defined as (1) a reduction of at least 50% compared to baseline on the Hamilton Rating Scale for major depression (HRSD) (Hamilton 1960), Montgomery Åsberg Depression Rating Scale (MADRS) (Montgomery 1979), or any other depression scale, depending on the study authors' definition or (2) 'much or very much improved' (score one or two) on the CGI-Improvement scale (Guy 1976). Where both scales are provided, we prefer the former criteria for judging response. We will use the response rate instead of a continuous symptom score for the primary efficacy analysis to make the interpretation of results easier for clinicians (Guyatt 1998).
To avoid possible outcome reporting bias the original authors' definitions of response or remission, if different from above, will not be used in this review (Furukawa 2007a). Response rates will be calculated out of the total number of randomised patients. Intention-to-treat analysis (ITT) will be applied whereby all dropouts not included in the analysis will be considered non-responders.
Taylor 2006 suggested that SSRIs begin to have observable beneficial effects in major depression during the first week of treatment. As such, when studies report response rates at various time points throughout the trial, we have determined a priori to subdivide the treatment indices as follows:
(i) Response - early phase: between 1 and 4 weeks, with the time point closest to 2 weeks given preference;
(ii) Response - acute phase: between 6 and 12 weeks, with preference given to the time point given in the original study as the study endpoint; and
(iii) Response - follow-up phase: between 4 and 6 months, with the time point closest to 24 weeks given preference.
The acute-phase treatment (6 to 12 weeks) response rates will be our primary outcome of interest.
2. Total dropout
The primary harm outcome will be the total number of participants who leave the study early for any reason during the first 6 to 12 weeks of the treatment. Acceptability rates will be calculated out of the total number of randomised participants.
1. Response - early phase, and follow-up phase
2. Remission - early phase, acute phase, and follow-up phase
We are interested in the number of patients who achieve remission, defined as (1) a score of < 7 on the HRSD-17 (Furukawa 2007b), or < 8 for all the other longer versions of the HRSD, or < 11 on the MADRS (Bandelow 2006); or (2) patients who were 'not ill or borderline mentally ill' (score one or two) on the CGI-Severity score out of the total number of randomised participants. Where both are provided, we will use the former criterion for judging remission.
3. Group mean scores or group change scores at the end of the trial on a depression scale
4. Social adjustment, social functioning, including the Global Assessment of Function (GAF) scores
5. Health-related quality of life (QOL)
We will use the following validated QOL instruments: SF-12 (Ware 1998); SF-36 (Ware 1992), HoNOS (Wing 1998), and the WHO-QOL (WHOQOL Group 1998).
6. Costs to healthcare services
7. Dropouts due to inefficacy
We will record the number of patients who dropped out during the trial because bupropion was ineffective.
8. Dropout due to adverse effects
We will record the number of patients who dropped out during the trial due to adverse effects.
9. Number of patients experiencing at least one adverse effect
10. Number of patients experiencing the following specific adverse effects
vomiting or nausea
sleepiness, drowsiness or somnolence
agitation, or anxiety
homicidal ideation or aggression
suicide wishes, gestures or attempts
psychosis, delusion or hallucination
mania or hypomania
To avoid missing any relatively rare or unexpected adverse effects in the data extraction phase, we will collect all adverse effect data reported in the literature and discuss ways to summarise them post hoc. We will extract descriptive data regarding adverse effect profiles from all available studies. Only studies reporting the number of patients experiencing individual adverse effects will be retained. Due to a lack of consistent reporting of adverse effects, which came primarily from the study authors' descriptions, we will combine terms describing similar side effects. For example, we will combine 'dry mouth', 'reduced salivation' and 'thirst' into 'dry mouth'. All adverse effect categories will then be grouped by organ system, such as neuropsychiatric, gastrointestinal, respiratory, sensory, genitourinary, dermatological and cardiovascular as suggested by Mottram 2006.
Search methods for identification of studies
Cochrane Depression, Anxiety and Neurosis (CCDAN) Group's Specialised Register (CCDANCTR)
The Cochrane Depression, Anxiety and Neurosis Group (CCDAN) maintain two clinical trials registers at their editorial base in Bristol, UK, a references register and a studies based register. The CCDANCTR-References Register contains over 33,500 reports of randomised controlled trials in depression, anxiety and neurosis. Approximately 60% of these references have been tagged to individual, coded trials. The coded trials are held in the CCDANCTR-Studies Register and records are linked between the two registers through the use of unique Study ID tags. Coding of trials is based on the EU-Psi coding manual. Please contact the CCDAN Trials Search Co-ordinator (TSC) for further details. Reports of trials for inclusion in the Group's registers are collated from routine (weekly), generic searches of MEDLINE (1950 -), EMBASE (1974 -) and PsycINFO (1967 -); quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL) and review specific searches of additional databases. Reports of trials are also sourced from international trials registers care of the World Health Organization's trials portal (ICTRP), ClinicalTrials.gov, drug companies, handsearching of key journals, conference proceedings and other (non-Cochrane) systematic reviews and meta-analyses. Details of CCDAN's generic search strategies (used to identify RCTs) can be found on the Group's website.
1. The CCDANCTR-Studies Register will be searched using the following search terms:
Diagnosis = (Depress* or Dysthymi* or "Adjustment Disorder*" or "Mood Disorder*" or "Affective Disorder" or "Affective Symptoms")
Intervention = Bupropion
2. The CCDANCTR-References Register will be searched using free-text terms to identify additional untagged/uncoded reports of RCTs:
Free-text = ((Depress* or Dysthymi* or "Adjustment Disorder*" or "Mood Disorder*" or "Affective Disorder" or "Affective Symptoms") and Bupropion)
3. The GlaxoSmithKline (GSK) Clinical Study Register will be searched for Bupropion.
4. International Regulatory Authorities and Trial Registries
Websites of the following drug regulatory authorities will be searched for additional unpublished data: The US FDA, the Medicines and Healthcare products Regulatory Agency (MHRA) in the UK, the European Medicines Agency (EMEA) in the EU, the Pharmaceuticals and Medical Devices Agency (PMDA) in Japan, the Therapeutic Goods Administration (TGA) in Australia). International trial registries will also be searched for unpublished or ongoing research: Clinicaltrials.gov, ISRCTN, Nederlands Trial Register, EUDRACT, UMIN-CTR and the Australian New Zealand Clinical Trials Registry and others care of the WHO trials portal (ICTRP).
There will be no restrictions on date, language or publication status applied to the searches.
Searching other resources
Appropriate journals and conference proceedings relating to the treatment of depression with bupropion have already been handsearched and incorporated into the CCDANCTR.
2. Personal communication
Pharmaceutical companies and experts in this field will be asked if they know of any additional studies which meet the inclusion criteria of this review.
3. Reference checking
Reference lists of all included studies, previous systematic reviews and major textbooks of affective disorder written in English will be checked for published reports and citations of unpublished research.
Data collection and analysis
Selection of studies
Two review authors will independently check to ensure that studies relating to bupropion generated by the search strategies of the CCDANCTR-References and the other complementary searches meet the inclusion criteria, firstly based on the title and abstracts. All of the studies rated as possible candidates for inclusion by either of the two review authors will be added to the preliminary list, and the full text articles will be retrieved. We will then assess all of the full text articles in this preliminary list to see if they still meet the inclusion criteria. If the raters disagree, the final rating will be made by consensus with the involvement, if necessary, of another review author. Considerable care will be taken to exclude duplicate publications.
Data extraction and management
At least two independent review authors will extract data from the included studies. Any disagreement will be discussed, and decisions documented. If necessary, we will contact authors of studies for clarification. We will extract the following data:
(i) participant characteristics (age, sex, depression diagnosis, comorbidity, depression severity, antidepressant treatment history for the index episode, study setting);
(ii) intervention details (intended dosage range, mean daily dosage actually prescribed, co-intervention if any, duloxetine as investigational drug or as comparator drug, sponsorship); and
(iii) outcome measures of interest from the included studies.
The data extraction results will be compared to reviews of individual antidepressants in The Cochrane Library.
Main planned comparisons
1.Bupropion against the following conventional anti-depressive agents:
1.1 Tricyclics (TCAs);
1.5 MAOIs or newer ADs;
1.6 Other conventional psychotropic drugs.
2. Bupropion against the following non-conventional anti-depressive agents:
2.2 Other non-conventional anti-depressive agents
Assessment of risk of bias in included studies
Two review authors will independently assess trial quality using the Cochrane risk of bias tool (Higgins 2011a). We will assess the following factors: sequence generation, allocation concealment, blinding, incomplete outcome data, selective reporting and other potential sources of bias. Each item will be rated as high, low or unclear risk of bias, and a justification from the study report will be supplied to support the judgement as appropriate.
If the raters disagree, the final rating will be made by consensus with the involvement, if necessary, of another review author. Non-congruence in quality assessment will be reported as the percentage of disagreement. The ratings will also be compared with those from reviews of individual antidepressants in The Cochrane Library. If there are any discrepancies, they will be fed back to the authors of the applicable reviews.
Measures of treatment effect
All comparisons will be performed between bupropion and comparator ADs as a class and as individual ADs.
We will calculate the odds ratio (OR) with corresponding 95% confidence interval (95% CI) for dichotomous or event-like outcomes. For statistically significant results, we will calculate the number needed to treat to provide benefit (NNTb) and the number needed to treat to induce harm (NNTh) as a function of the pooled OR and the average control event in all the control groups combined.
We will calculate the mean difference (MD) or standardised mean difference (SMD) along with corresponding 95% CI for continuous outcomes. The MD will be used where the same scale was used to measure an outcome. The SMD will be employed where different scales were used to measure the same underlying construct.
Unit of analysis issues
A major concern of cross-over trials is the potential of carry-over effects. 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 major depression, we will only use data from the first phase of cross-over studies. However, we are aware that cross-over trials for which only first-period data are available should be considered to be at risk of bias (Higgins 2011b), so careful attention will be paid to retrieve only unbiased data available from such studies.
We will include cluster-randomised trials if either of the two methods below is possible.
1. When the cluster-randomised trial is correctly analysed in the original report, we will enter the effect estimate and standard error using the generic inverse variance method in RevMan.
2. If the original report has failed to adjust for cluster effects, such a trial can still be included in the meta-analysis if the following information can be extracted:
2.1 number of clusters randomised to each intervention or the average size of each cluster;
2.2. outcome data ignoring the cluster design for the total number of individuals; and
2.3. estimate of the intracluster correlation coefficient (ICC).
The ICC may be borrowed from similarly designed studies when such are available. The approximately correct analysis will then be conducted following the procedures as described in 16.3.4 of the Cochrane Handbook (Higgins 2011b).
Studies with multiple treatment groups
Where a study involves more than two treatment arms, we will include all relevant treatment arms in comparisons. If data are binary, we will simply add and combine them into one group or divide the comparison arm into two (or more) as appropriate. If data are continuous, we will combine data following the formula in section 184.108.40.206 of the Handbook (Higgins 2011c).
Dealing with missing data
Responders and remitters to treatment will be calculated on a strict ITT basis: dropouts will be included in the analysis. Where participants were excluded from the trial before the endpoint, we will assume that they experienced a negative outcome (e.g. failure to respond to treatment). We will examine the validity of this decision in sensitivity analyses by applying worst- and best-case scenarios (i.e. missing data will be assumed to be responders or non-responders in the corresponding sensitivity analyses).
When dichotomous outcomes are not reported but baseline mean, endpoint mean and corresponding standard deviations (SDs) of the HRSD (or other depression scale) are reported, we will convert continuous outcome data expressed as mean and SD into the number of responding and remitted patients, based on a validated imputation method (Furukawa 2005). When the more sophisticated and arguably more valid imputation method (e.g. mixed-effects model, multiple imputation) is reported in the original study, we will use these numbers to impute the number of responders. We will examine the validity of this imputation in sensitivity analyses.
When there are missing continuous data and the method of 'last observation carried forward' (LOCF) was used to perform an ITT analysis, then the LOCF data will be used.
We will contact the original study authors for missing data.
When only the standard error (SE) or T-test or P values are reported, SDs will be calculated as suggested by Altman 1996. Where SDs are not reported, we will contact trial authors and ask them to supply the data. In the absence of a response from the trial authors, we will borrow SDs from other studies in the review (Furukawa 2006). We will examine the validity of this imputation in sensitivity analyses.
Assessment of heterogeneity
We will first investigate heterogeneity between studies by visual inspection of the forest plots. If the 95% CIs of the ORs for each study in the pooled analysis do not overlap, potential sources of heterogeneity will be investigated. We will also calculate the I2 statistic (Higgins 2003). We will use the Handbook's rough guide to its interpretation as follows: 0% to 40% might not be important; 30% to 60% may represent moderate heterogeneity; 50% to 90% may represent substantial heterogeneity; and 75% to 100% considerable heterogeneity. We will also keep in mind that the importance of the observed value of I2 depends on (i) the magnitude and direction of effects and (ii) the strength of evidence for heterogeneity (e.g. P value from the Chi2 test, or a confidence interval for I2). If the I2 value is below 50% but the direction and magnitude of treatment effects were suggestive of important heterogeneity, we will investigate the potential sources of heterogeneity. Finally, we will perform subgroup analyses to investigate heterogeneity.
Assessment of reporting biases
Data from included studies will be entered into a funnel plot (trial effect against trial variance) to investigate small-study effects (Sterne 2000). We will use the test for funnel plot asymmetry only when there are at least 10 studies included in the meta-analysis. Results will be interpreted cautiously, with visual inspection of the funnel plots (Higgins 2011a). When evidence of small-study effects is identified, we will investigate possible reasons for funnel plot asymmetry, including publication bias (Egger 1997).
For the primary analysis, we will calculate the pooled OR with corresponding 95% CI for dichotomous outcomes. A random-effects model will be used because it has the highest generalisability for empirical examination of summary effect measures in meta-analyses (Furukawa 2002). The robustness of this summary measure will be routinely examined by calculating the fixed-effect model OR and the random-effects model risk ratio (RR). Material differences between the models will be reported.
We will calculate the pooled MD or SMD as appropriate with corresponding 95% CI for continuous outcomes. We will also use the random-effects model for continuous outcomes. However, fixed-effect analyses will be performed routinely as well, to investigate the effect of the choice of method on the effect estimates. Material differences between the models will be reported. Skewed data and non-quantitative data will be presented descriptively. An outcome that has a minimum score of zero could be considered skewed when the mean is smaller than twice the SD. However, the skewness of change scores is difficult to depict as the possibility of negative values exists. Therefore, we will use change scores for meta-analysis of mean differences.
A P value of less than 0.05 and a 95% CI that does not cross the line of no effect will be considered statistically significant.
Subgroup analysis and investigation of heterogeneity
As multiple analyses will lead to false positive and false negative conclusions, subgroup analyses should be performed and interpreted with caution (Brookes 2001; Brookes 2004). The following subgroup analyses will be performed where possible for the following reasons:
1. Depression severity (severe major depression, moderate or mild major depression)
'Severe major depression' was defined by a threshold baseline severity score for entry of 27 or more for the 17-item HRSD (Furukawa 2007b), and 31 or more for MADRS (Müller 2003).
2. Treatment settings (psychiatric in-patients, psychiatric outpatients, primary care)
Because depressive disorder in primary care has a different profile than that of psychiatric in-patients or outpatients (Suh 1997), it is possible that results obtained from either of these settings may not be applicable to the other settings (Arroll 2009).
3. Elderly patients ( > 65 years of age), separately from other adult patients
Older people may be more vulnerable to adverse effects associated with antidepressants and a decreased dosage is often recommended. Groups whose mean age was > 65 will be pooled.
4. Formulations and dosage of bupropion
We will conduct subgroup analyses by formulation and dosage. The formulations will be subgrouped for bupropion immediate release, bupropion sustained release, and bupropion extended release. Because the target dose of all the formulations is 300 mg/day, the dosage will be subgrouped into those less than or equal to 300 mg and those more than 300 mg/day.
The following sensitivity analyses for primary outcome are planned a priori. By limiting the included studies to those with higher quality (analyses one to five) or to those free from some 'bias' (analyses six and seven), we will examine whether the results change and we intend to check for the robustness of the observed findings.
We will exclude trials with unclear allocation concealment or unclear double blinding.
We will exclude studies that included patients with bipolar depression or psychotic features.
We will exclude studies with unfair dose comparisons (Cipriani 2009).
We will exclude trials with a dropout rate greater than 20%.
We will exclude trials for which the response rates had to be calculated based on an imputation method (Furukawa 2005), and for which the SD had to be borrowed from other trials (Furukawa 2006).
We will examine a 'wish bias' by comparing the trials where bupropion was used as an investigational drug, to the trials where citalopram was used as a comparator, since some evidence suggests that a new antidepressant might perform worse when used as a comparator than when used as an investigational agent (Barbui 2004).
We will exclude trials funded by, or with at least one author affiliated with, a pharmaceutical company marketing bupropion. This sensitivity analysis is particularly important in light of the recent repeated findings that industry funding strongly affects outcomes of research studies (Perlis 2005), and because industry sponsorship and authorship of clinical trials have increased over the past 20 years (Buchkowsky 2004).
Our routine comparisons of random-effects and fixed-effect models, as well as our secondary outcomes of remission rates and continuous severity measures, may be considered additional forms of sensitivity analyses.
Summary of findings table
We will construct a summary of findings (SoF) table for each comparison between bupropion and another antidepressive agent, with regard to the following seven outcomes:
Response -- acute phase;
Response -- early phase;
Response -- follow-up phase;
Remission -- acute phase;
Severity of depression at end of trial; and
Dropouts due to adverse effects.
In the SoF tables we will use the principles of the GRADE approach which assesses the quality of a body of evidence based on the extent to which there can be confidence that the obtained effect estimate reflects the true underlying effect. The quality of a body of evidence is judged on the basis of the included studies' risks of bias, the directness of the evidence, unexplained heterogeneity, imprecision, and the risk of publication bias.
We will use the average rate in all the arms of the included trials as the 'Assumed risk' for each outcome because we do not expect salient differences in such risks among bupropion and the other antidepressive agents. We will therefore not target any particularly high or low risk populations but all the tables will be for medium risk populations.