Types of studies

We will include clinical trials (randomized or trial). We will include studies reported as full‐text, those published as an abstract only, and unpublished data.There will be no language restriction.

Types of participants

We will include patients older than 18 years, with a diagnosis of PsA as defined by the trial authors (including studies using the classification criteria of Moll and Wright (Moll 1973), or the Classification criteria for Psoriatic Arthritis (CASPAR (Taylor 2006)).

Types of interventions

We will include trials that compare treatment with PDE4 inhibitors (e.g. apremilast) alone or in combination with any DMARD, compared with placebo or another synthetic or biologic DMARD. We will prioritize reporting of the recommended and approved dose (30 mg), but we will also consider all other doses for analysis (FDA 2015).

Types of outcome measures

We have selected the most relevant outcomes for patients and physicians in accordance with those recommended by the Cochrane Musculoeskeletal Group and the current recommendations from the Outcome Measures in Rheumatology initiative (OMERACT), the Group for Research and Assessment of Psoriasis and Psoriatic arthritis (GRAPPA (Helliwell 2014)) and international guidelines (Gladman 2005; Gossec 2016; Coates 2013).

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, and Web of Science. We will also conduct a search of ClinicalTrials.gov and the WHO trials portal. We will search all databases from their inception to the present, and we will impose no restriction on language of publication. For assessments on adverse effects, we will search the websites of the regulatory agencies US Food and Drug Administration‐MedWatch, European Medicines Evaluation Agency, Australian Adverse Drug Reactions Bulletin, and UK Medicines and Healthcare products Regulatory Agency (MHRA) pharmacovigilance and drug safety updates. See Appendix 1 for the MEDLINE search strategy. We will use EndNote X7 software to manage the records retrieved from searches of electronic databases.

Searching other resources

We will hand search the list of references of all included controlled trials and review articles to identify any potentially relevant citations that were not found otherwise. Results from other resources will be kept on a Microsoft Excel spreadsheet. We will attempt to contact the trial authors and manufacturer (Celgene Corporation) for any additional information that has not been published, when trial data are unclear, or further details are needed.

Selection of studies

Two review authors (NVZ, IAVM) will independently screen titles and abstracts of all potential studies identified as a result of the search for inclusion. We will identify and exclude duplicate records. Unique citations will be coded as potentially eligible, unsure, unclear, or exclude. We will retrieve the full‐text of the potentially eligible citations and two review authors (NVZ, IAVM) will independently screen the full‐text and identify studies for inclusion. Reasons for exclusion of the ineligible studies will be recorded. We will resolve any disagreement through discussion or by involving an adjudicator (MLO). We will collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. We will record the selection process in sufficient detail to complete a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow diagram and 'Characteristics of excluded studies' table. Agreement between review authors will be measured according to the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions. We will contact study investigators if clarifications to evaluate study eligibility are needed and to request further information when necessary.

Data extraction and management

One review author (NVZ) will independently extract the data and another review author (IAVM) will cross‐check them for any errors; any discrepancies will be resolved by discussion or by involving a third person (MLO). We will extract:

1. General study information: title, authors, country, follow‐up, year, funding agency, study design, setting, risk of bias, number of patients randomized, number of patients analyzed.

2. Characteristics of participants: age, sex, disease duration, concurrent treatments.

3. Characteristics of intervention: dosages, methods of administration, frequency, duration of treatment, withdrawals, drop‐outs.

4. Characteristics of control: active or placebo; if active, then drug name, dosages, methods of administration, frequency, duration of treatment, withdrawals, drop‐outs.

5. Outcome variables: all outcomes assessed by the authors.

In the 'Characteristics of included studies' table, we will note if outcome data were not reported in a usable way, and when data were transformed or estimated from a graph. Data that are only provided in graphs will be extracted independently by two review authors using PlotDigitizer software. One review author (NVZ) will transfer data into the Review Manager (RevMan 5.3) file and a second review author (IAVM) will double‐check them.

We will identify any a priori decision rules to select which data to extract in the event of multiple outcome reporting, including:

• if both final values and change from baseline values are reported for the same outcome, we will extract final values;

• if data are analyzed based on an intention‐to‐treat (ITT) sample and another sample (e.g. per‐protocol, as‐treated), we plan to extract ITT (for outcomes assessing benefits and harms).

• If multiple time points are given, we will extract data at 12, 24, and 52 weeks, and every year thereafter.

Assessment of risk of bias in included studies

Two review authors (NVZ, IAVM) will independently assess the risk of bias. We will follow the Cochrane recommendations for assessment. In a consensus meeting, the review authors will discuss and resolve disagreements. If disagreement persists, a final decision will be facilitated by a third review author (MLO). We will summarise the 'Risk of bias' judgements across studies for each of the domains listed. We will consider blinding separately for different key outcomes, where necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be different than for a patient‐reported pain scale). We will also consider the impact of missing data by key outcomes (Higgins 2011a). We will grade each potential source of bias as low, unclear, or high, and will provide a quote from the study report and justification for each judgment in the 'Risk of bias' table. The final ratings for all included studies will be presented in a ‘Risk of bias’ summary figure.

We will explore these biases by judging the following criteria:

1. random or quasi‐random sequence generation,

2. allocation concealment,

3. blinding of participants,

4. blinding of personnel and outcome assessors,

5. incomplete outcome data,

6. free of selective reporting, and

7. other biases (Higgins 2011a).

Measures of treatment effect

We will analyze dichotomous data as risk ratios (RR) or Peto odds ratios (OR) when the outcome is a rare event (approximately less than 10%), and use 95% confidence intervals (CI). We will analyze continuous data as mean differences (MD) or standardized mean differences (SMD), depending on whether the same scale is used to measure an outcome, and 95% confidence intervals. Standardized mean differences will be back‐translated to a typical scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. the standard deviation (SD) of the control group at baseline from the most representative trial (Schünemann 2011b)). For safety outcomes, we will use an intention‐to‐treat model to analyze the data. For studies that report only events (not subjects), we will present the data in a table but not attempt to summarize them.

Unit of analysis issues

For trials with multiple arms (studies comparing more than two dosages), we will analyze all groups separately. Our main comparison will be PDE4 (e.g. apremilast 30 mg twice daily) monotherapy vs DMARD monotherapy. However, we will include the following comparison groups if such trials are identified:

• PDE4 (e.g. apremilast) combined with DMARD versus DMARD alone

• PDE4 approved dose (e.g. apremilast 30 mg twice daily) versus PDE4 non‐approved doses (e.g. apremilast 20 mg twice daily or 40 mg four times a day)

• PDE4 (e.g. apremilast) versus other non‐synthetic DMARD agents (if evidence becomes available).

If two comparisons (e.g. drug A versus placebo and drug B versus placebo) are combined in the same meta‐analysis, we will halve the repeated group to avoid double‐counting.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is identified as an abstract only, or when data are not available for all participants). We will clearly describe any assumptions and imputations used to handle missing data.

For continuous outcomes that only report the median and interquartile ranges (or minimum and maximum values), we will use the median as the mean, and use one half of the difference between the first and third quartile range as the SD (Higgins 2011b).

Where possible, we will compute missing standard deviations from other statistics, such as standard errors, confidence intervals or P values, according to the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c). If standard deviations cannot be calculated, we will impute them (e.g. from other studies in the meta‐analysis; Higgins 2011c).

Assessment of heterogeneity

We will assess clinical and methodological diversity across the included studies in terms of participants, interventions, outcomes, and study characteristics to determine whether a meta‐analysis is appropriate. We will do this by observing these data from the data extraction tables. We will assess statistical heterogeneity by visual inspection of the forest plot to assess for obvious differences in the results between the studies, and use the I² statistical test. An I² value of 0% to 40% will be considered 'not important heterogeneity'; 30% to 60% 'moderate' heterogeneity; 50% to 90% 'substantial' heterogeneity; and 75% to 100% 'considerable' heterogeneity (Deeks 2011). If we identify heterogeneity (I^₂ greater than 40%), we will report it and investigate possible causes by following the recommendations in the Cochrane Handbook of Systematic Reviews of Interventios (Higgins 2011b).

Assessment of reporting biases

If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible publication bias. In interpreting funnel plots, we will examine the different possible reasons for funnel plot asymmetry and relate this to the results of the review (Sterne 2011). We will also check trial protocols against published reports. We will screen the Clinical Trials Register at the International Clinical Trials Registry Platform of the World Health Organiszation for the a priori trial protocol.

Data synthesis

We will analyze the results of the studies using Review Manager 5.3 (RevMan 2014). We will undertake meta‐analyses only where this is meaningful (i.e. if the treatments, participants, and the underlying clinical question are similar enough for pooling to make sense). We will use a random‐effects model.

The basis of a random‐effects meta‐analysis is that combining the estimate of effect across studies incorporates an assumption that the studies are not all estimating the same intervention effect, but following a distribution across studies (see Section 9.5.4; Higgins 2011b). Alternatively, if one assumes that each study is estimating exactly the same quantity, a fixed‐effect meta‐analysis is performed.

The primary analysis for our reviews for self‐reported outcomes (e.g. outcomes such as pain, function, health‐related quality of life, participant global assessment of treatment success or well‐being), the results that go in 'Summary of findings' table 1, and thus the abstract and plain language summary, will be restricted to trials with low risk of detection and selection bias.

Subgroup analysis and investigation of heterogeneity

We will conduct subgroup analyses to determine the effects of disease duration (shorter than two years versus two years or longer) and previous DMARD treatment (DMARD‐naive versus prior DMARD exposure versus prior biologic DMARD exposure). We will restrict subgroup analyses to the ACR improvement criteria of 50%. We will use the formal test for subgroup interactions in Review Manager 5.3 (RevMan 2014). We will compare the magnitude of the effects between the subgroups by assessing the overlap of the confidence intervals of the estimated summaries. Non‐overlap of the confidence intervals indicates statistical significance.

Sensitivity analysis

If sufficient trials are identified, we plan to conduct a sensitivity analysis comparing the results when we use all trials with high methodological quality; studies classified as having a 'low risk of bias' versus those identified as having a 'high risk of bias' in allocation concealment and blinding for the ACR improvement criteria of 50% (Higgins 2011a). We will explore the effects of imputation, and the effects when we conduct the meta‐analyses using the fixed‐effect model.