Types of studies

We considered all prospective, randomized controlled trials (RCTs) of mycophenolate mofetil versus methotrexate utilizing a parallel study design for inclusion in this systematic review. We excluded all other study designs.

Types of participants

We included studies that enrolled participants who were at risk of developing GVHD as a result of undergoing allo‐HCT. We excluded studies that enrolled participants with an existing diagnosis of acute or chronic GVHD. We applied no restrictions on participant gender, ethnic group, or age. We described the disease type and stage of the included participants.

Types of interventions

Included studies reported on the direct comparison of any mycophenolate mofetil‐based regimen versus any methotrexate‐based regimen administered as prophylaxis for acute GVHD in people undergoing allo‐HCT. Specifically, we considered a regimen to be used as prophylaxis for acute GVHD if 1. the investigators specifically stated mycophenolate mofetil or methotrexate was used as prophylaxis for acute GVHD or 2. if the study inclusion/exclusion criteria excluded people with an existing diagnosis of acute or chronic GVHD. Supportive care and other GVHD prophylaxis/therapies, if any, were similar in both arms. In addition, since mycophenolate mofetil and methotrexate were commonly administered in combination with a calcineurin inhibitor (e.g. cyclosporine or tacrolimus), we included all regimens containing mycophenolate mofetil versus all regimens containing methotrexate, regardless of co‐therapies, in the review.

Types of outcome measures

Electronic searches

We conducted an electronic search of Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library) using the search strategy in Appendix 1 and MEDLINE using search strategy in Appendix 2 from inception to 17 March 2014. We applied no date or language limits.

Searching other resources

In order to identify any recently completed studies that had not been published in full, we searched conference abstracts from the last two meetings (2011 and 2012) of the American Society of Clinical Oncology (ASCO), American Society of Hematology (ASH), European Group of Blood and Marrow Transplantation (EBMT), and BMT tandem meetings of the American Society of Blood and Marrow Transplantation (ASABM), Center for International Blood and Marrow Transplant Research (CIBMTR), and European Hematology Association (EHA). We also handsearched references of all identified review articles and included studies. In order to identify unpublished or ongoing studies, we searched ClinicalTrials.gov (www.clinicaltrials.gov/), Novartis Clinical Trial Results Database (www.novctrd.com), Roche Clinical Trial Protocol Registry (www.roche‐trials.com), Australian New Zealand Clinical Trials Registry (ANZCTR), and the metaRegister of Controlled Trials.

Selection of studies

Two review authors (RM and TR) reviewed all titles, abstracts, and full‐text reports independently. We included studies that met the following criteria in the review.

1. Prospective clinical trial.

2. Parallel study design.

3. Participants randomized to prophylaxis with mycophenolate mofetil versus methotrexate.

4. Participants undergoing allo‐HCT.

We matched references on author names, location and setting, specific intervention details, and participants to avoid inclusion of duplicate publications. We resolved any disagreements between review authors during the study selection by consensus with a third review author (MAK‐D or AK).

Data extraction and management

Two review authors independently extracted data according to Chapter 7 of the Cochrane Handbook for Systematic Reviews of Interventions using a standardized data extraction form containing the following items (Higgins 2011):

• general information: study title, authors, source;

• study characteristics: study design, setting, duration of follow‐up;

• participant characteristics: number of participants enrolled, number of participants included in the analysis, specific disease diagnosis, donor status (related or unrelated donor), HLA‐mismatch, participant age;

• interventions: name, dose, route, administration schedule, and associated therapies;

• outcomes: incidence of acute GVHD (grades II to IV and III to IV GVHD), overall survival, median days to neutrophil engraftment, median days to platelet engraftment, incidence of relapse, incidence of chronic GVHD, grade III or IV adverse events, nonrelapse mortality (any death occurring without disease relapse/recurrence), pain;

• risk of bias.

For studies that had multiple publications, we used the publication with longest follow‐up for extracting data on outcomes. We used earlier publications to extract data on methodology and baseline characteristics. In cases where the method of analysis was not specified by the investigators and only the number of events was reported, we used the number randomized as the denominator. That is, we recorded results according to intention‐to‐treat (ITT) analysis.

Assessment of risk of bias in included studies

Two review authors (RM and TR) independently assessed the risk of bias in the included studies using The Cochrane Collaboration's tool for assessing the risk of bias as outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions based on extracted information (Higgins 2011a). A third author (MAK‐D or AK) resolved any disagreements between the two review authors. In addition to risk of bias, we evaluated the risk of random error by extracting data on the investigator's predetermined effect difference, alpha, power, and sample size.

Specifically, for assessment of risk of bias, we graded each component of methodologic quality as low, high, or unclear. We evaluated selection bias by assessing the investigators' description of method of randomization and allocation concealment. The method of randomization was:

• low risk if the investigators described a random component in the sequence generation process (i.e. refer to a random number table, use a computer random number generator, coin toss);

• high risk if the investigators described a nonrandom component in the sequence generation process (sequence generated by odd or even date of birth, some rule based on date (or day) of admission, or some rule based on hospital or clinic record number); and

• unclear risk if there was insufficient information about the sequence generation process to permit judgment of 'low risk' or 'high risk'.

We considered allocation concealment to be:

• low risk if participants and investigators enrolling participants could not foresee assignment (i.e. use of central allocation, sequentially numbered identical drug containers or sequentially numbered, opaque, sealed envelopes);

• high risk if participants or investigators enrolling participants could possibly foresee assignments (allocation based on date of birth, case record number, using an open random allocation schedule); and

• unclear risk if there was insufficient information to permit judgment of 'low risk' or 'high risk'.

We evaluated performance bias by assessing the investigators' description of blinding of participants and investigators. Performance bias was:

• low risk if no blinding was used, but the outcome was not likely to be influenced by lack of blinding or participants and key study personnel were blinded;

• high risk if no blinding or incomplete blinding was used, and the outcome was likely to be influenced by lack of blinding; and

• unclear risk if there was insufficient information to permit judgment of 'low risk' or 'high risk'.

We judged detection bias due to knowledge of the allocated interventions by outcome assessors to be:

• low risk if no blinding of outcome assessment was used, but the outcome measurement was not likely to be influenced by lack of blinding or blinding of outcome assessment was ensured;

• high risk if there was no blinding of outcome assessment, and the outcome measurement was likely to be influenced by lack of blinding; and

• unclear risk if there was insufficient information to permit judgment of 'low risk' or 'high risk'. 

We judged attrition bias due to the amount, nature, or handling of incomplete outcome data to be:

• low risk if there were no missing outcome data, reasons for missing outcome data were unlikely to be related to true outcome, or missing outcome data were balanced in numbers across intervention groups, with similar reasons for missing data across groups;

• high risk if the reasons for missing outcome data were likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups. For dichotomous outcome data, the proportion of missing outcomes compared with the observed event risk is enough to induce clinically relevant bias in the intervention effect estimate, or uses 'as‐treated' analysis with substantial departure of the intervention received from that assigned at randomization or uses potentially inappropriate application of simple imputation;

• unclear risk if there was insufficient reporting of attrition/exclusions to permit judgment of 'low risk' or 'high risk' (e.g. number randomized not stated, no reasons for missing data provided).

We considered reporting bias due to selective outcome reporting to be:

• low risk if the study protocol was available and all of the study's prespecified (primary and secondary) outcomes that were of interest in the review had been reported in the prespecified way or the study protocol was not available but it was clear that the published reports included all expected outcomes, including those that were prespecified;

• high risk if the study's prespecified primary outcomes had not been reported, primary outcomes were reported using measurements that were not prespecified, primary outcomes were not prespecified, outcomes of interest in the review were reported incompletely so that they could not be entered in a meta‐analysis, or the study report did not include results for a key outcome that would be expected to have been reported for such a study; and

• unclear if there was insufficient information to permit judgment of 'low risk' or 'high risk'.

For the evaluation of risk or random error, we captured whether investigators report predetermined effect difference, alpha, power, and sample size calculation (yes/no and reported values) and if they were able to enroll the prespecified number of participants (prespecified sample size versus total number enrolled per arm).

Measures of treatment effect

Unit of analysis issues

The unit of analysis for this review was individual study. In the case of repeated follow‐up (e.g. reporting of survival at three and six months), we used the longest follow‐up from each study. We treated recurring events (e.g. adverse events) as a single event occurring in one participant (e.g. we considered four instances of nausea in one participant as one participant with nausea). In the case of multiple intervention arms, we combined arms together to create a single pair‐wise comparison.

Dealing with missing data

As suggested in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), in the case of missing outcome data, we attempted to contact the principal investigator or corresponding author (or both) of the study. If the corresponding author was unable to provide the missing data for an outcome, we included the study in the systematic review but excluded it from the meta‐analysis for the outcome with missing data. We undertook no imputation of missing individual participant data.

Assessment of heterogeneity

To evaluate heterogeneity between pooled studies, we calculated the Chi² and I² statistics (Deeks 2011). We considered an I² statistic > 50% to indicate substantial heterogeneity or a Chi² test with a significance level at P value < 0.1 to indicate statistically significant heterogeneity.

Assessment of reporting biases

We planned to assess publication bias using a funnel plot if more than 10 studies were included in the review (Egger 1997; Sterne 2011). We evaluated selective reporting of outcomes within studies by comparing outcomes reported with outcomes specified in protocols, when available.

Data synthesis

We performed pooled analysis using Review Manager 5 (RevMan 2011). We employed a random‐effects model using the DerSimonian‐Laird approach to pool studies for all analyses (DerSimonian 1986).

We constructed a 'Summary of findings' table using the most clinically and participant‐relevant outcomes (Guyatt 2011). These outcomes included: overall survival, incidence of relapse, incidence of grade II to IV acute GVHD, incidence of chronic GVHD, nonrelapse mortality, and incidence of any grade III to IV adverse events. In addition, we evaluated and reported the quality of evidence for each outcome according to GRADE guidelines (Balshem 2011; Guyatt 2011a; Guyatt 2011b; Guyatt 2011c; Guyatt 2011d; Guyatt 2011e).

Subgroup analysis and investigation of heterogeneity

Originally we planned to conduct subgroup analyses on prognostically relevant factors including gender, age (adult versus child), disease stage, previous treatment, differences in therapy regimen (co‐therapies), remission status prior to conditioning (complete remission), and type of donor (sibling versus unrelated). However, due to the small number of studies identified and lack of reporting by subgroup, we did not perform any subgroup analyses.

Sensitivity analysis

Originally we planned to conduct a sensitivity analysis on all aspects of methodological quality. Due to the small number of studies identified by this systematic review, we have not performed any sensitivity analyses proposed in the protocol.