Types of studies

All RCTs, including any cluster‐randomised studies. We will exclude cross‐over RCTs.

Types of participants

Adults (as defined by the study authors) of either sex, with a primary diagnosis of GAD. We will include studies that adopt any criteria to define participants suffering from GAD. More recent studies are likely to have used DSM‐IV‐TR (APA 2000), DSM‐IV (APA 1994), DSM‐5 (APA 2013) or International Classification of Diseases ICD‐10 criteria (WHO 1992). Older studies may have used ICD‐9 (WHO 1978), DSM‐III (APA 1980)/DSM‐III‐R (APA 1987) or other diagnostic systems. We will exclude participants who have a concurrent diagnosis of a medical disorder. However, we will include studies that have participants with co‐occurring psychiatric disorders if the primary diagnosis for inclusion was GAD. We will include studies from any setting.

Types of interventions

Types of outcome measures

Electronic searches

Searching other resources

Selection of studies

Two review authors will independently screen abstracts/titles of the studies identified by the literature searches. Those studies that meet the following inclusion criteria will constitute the preliminary list and we will retrieve their full texts. These inclusion criteria will be:

• randomised trial;

• comparing antidepressants against placebo;

• in people with GAD, regardless of the diagnostic criteria used.

We will then assess all the full‐text articles in this preliminary list to see if they meet the inclusion criteria. If the review authors disagree, the final rating will be made by consensus with the involvement (if necessary) of a third review author. We will report non‐congruence in the selection of trials as percentage disagreement. We will group duplicate publications of the same trial as multiple references to one study. We will record this process with enough details so we can construct a PRISMA diagram.

Data extraction and management

Two review authors will independently extract data using a specially designed form. We will discuss any disagreement with a third review author, document the decisions and, where necessary, contact the study authors to help resolve the issue. When the papers are not in English, authors who are fluent in other languages will extract data, and if no member of the research team is fluent in that language, we will obtain a translation of the paper via CCMD.

Assessment of risk of bias in included studies

Two review authors will independently assess the risk of bias within each included study based on the following six domains as per chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011):

• the method used to generate the allocation sequence should have been described in detail so that we can assess whether it should have produced comparable groups;

• the method used to conceal the allocation sequence should have been described in sufficient detail so that we can assess whether intervention schedules could have been predicted in advance of, or during, recruitment;

• we will assess whether the method by which any measures used to blind (mask) participants adequately limited the chance that any person from any group is able to ascertain which intervention a given participant might have received; this should be done separately for different types of outcomes;

• we will assess whether the method by which any measures used to blind (mask) personnel adequately limited the chance that any person from any group is able to ascertain which intervention a given participant might have received; this should be done separately for different types of outcomes;

• we will assess whether the method by which any measures used to blind (mask) outcome assessors adequately limited the chance that any person from any group is able to ascertain which intervention a given participant might have received; this should be done separately for different types of outcome;

• if studies does not report intention‐to‐treat analyses, we will make attempts to obtain missing data by contacting the study authors. We will extract and report data on attrition and exclusions as well as the numbers involved (compared with total randomised), reasons for attrition/exclusion where reported or obtained from investigators, and any re‐inclusions in re‐analyses will be performed. We will report whether, in our judgement, incomplete data were dealt with adequately (see also Dealing with missing data);

• we will attempt to assess the possibility of selective outcome reporting by investigators. We will rate these items as 'high', 'low' or 'unclear' using the methods described in Chapter eight of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011);

• we will consider and report whether we believe there were any other factors that could put a study at a high risk of bias. We will perform a sensitivity analysis and will exclude any studies that are at high risk of bias.

Measures of treatment effect

We will analyse dichotomous outcomes by calculating risk ratios for each trial with the uncertainty in each result expressed using CIs. We will describe continuous outcomes using mean differences or, if more than one scale is considered to measure the same thing, using standardised mean differences.

Data on continuous outcomes are frequently skewed, the mean not being the centre of the distribution. The statistics for meta‐analysis are thought to be able to cope with some skew, but were formulated for normally distributed data. We will take appropriate care to assure that potentially skewed data did not have undue influence.

Where both change and endpoint data were available for the same outcome category we will only present endpoint data. We will contact study authors who report only change data for endpoint figures. We will report non‐normally distributed data that may adversely affect the results in a table.

Unit of analysis issues

Dealing with missing data

When there are missing data the first approach will be to contact the study authors. We will calculate missing standard deviations (SDs) from other data if possible. If these methods are not sufficient then we will consider imputation of missing data.

If within studies the study authors attempt to correct for missing data, by using multiple imputation or last observation carried forward, then we will use those in preference to the completers data, with appropriate care to determine if this made a substantial difference to results.

Assessment of heterogeneity

We will examine heterogeneity between comparable trials by visual inspection of the forest plot and by considering the I² statistic value.

Heterogeneity will be quantified as follows (Higgins 2011):

• 0% to 40%: may not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: may represent considerable heterogeneity.

We will explore high levels of heterogeneity (where more than 50% of the variability in outcome between trials could not be explained by sampling variation) through the sensitivity analyses specified below. In addition to the I² statistic value (Higgins 2003), we will present the Chi² test for heterogeneity and its P value and consider the direction and magnitude of the treatment effects.

Assessment of reporting biases

We will produce a funnel plot (trial effect versus trial size) if more than 10 trials contributed to a meta‐analysis, in an attempt to investigate the likelihood of small sample biases. We will investigate funnel plot asymmetries (suggesting potential publication bias) (Egger 1997).

Data synthesis

We will perform statistical analysis in accordance with the guidelines for statistical analysis in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will enter data into Review Manager 5 (RevMan 5) (RevMan 2014).

We will combine dichotomous data (e.g. response/not response) using a random‐effects model.

We will also combine continuous data using a random‐effects model. We will conduct a fixed‐effect analysis as part of a sensitivity analysis.

Subgroup analysis and investigation of heterogeneity

Subgroup analyses should be performed and interpreted with caution, because multiple analyses can lead to false positive conclusions (Oxman 1992). We will perform the following subgroup analyses, where possible, for the following a priori reasons:

• diagnosis type: pre‐DSM‐III, DSM‐III and DSM III‐TR, DSM IV and following. This is needed as there have been considerable changes in the criteria for GAD between revisions of the DSM (Wolk 1996). We will analyse studies separately and only combine them if there was no heterogeneity;

• treatment settings (psychiatric inpatients, psychiatric outpatients, primary care);

• elderly participants (65 years of age or older) versus other adult participants;

• trials allowing psychiatric comorbidity versus those excluding such participants;

• trials lasting over 12 weeks: antidepressants can take some weeks to months to work. The longer trials may thus be able to assess the long‐term effect of antidepressants.

We will perform subgroup analyses on the primary outcomes only.

Sensitivity analysis

The following sensitivity analyses will be planned a priori. We will perform sensitivity analyses on the primary outcomes only.

• Excluding trials with unclear or high risk of bias in random allocation, unclear or high risk of bias in blinding, or both;

• excluding trials whose drop‐out rate is greater than 20%;

• excluding trials for which the response rates had to be calculated based on the imputation method (Furukawa 2005), and those for which the SD or ICC had to be borrowed from other trials (Furukawa 2006);

• application of fixed‐effect models will be considered to see if the weighting of small studies might affect the pooled result.

If subgroups within any of the subgroup or sensitivity analyses turn out to differ significantly from one another, we will perform a meta‐regression for exploratory analyses of additive or multiplicative influences of the variables in question.