Types of studies

Randomised or quasi‐randomised controlled trials, including cluster‐randomised controlled trials.

Types of participants

Preterm (less than 37 weeks' gestation) newborn infants who received cow's milk formula as their sole or supplemental enteral diet.

Types of interventions

Hydrolysed cow's milk formula versus standard (non‐hydrolysed) cow’s milk formula or another type of hydrolysed cow's milk formula. Formula was to be allocated as at least 20% of the intended enteral diet for at least two weeks to discern measurable effects on growth rates and episodes of feed intolerance. Trials should have compared formulas with similar energy and protein levels (i.e. hydrolysed 'preterm' formula vs non‐hydrolysed 'preterm' formula, or hydrolysed 'term' formula vs non‐hydrolysed 'term' formula).

We planned separate comparisons of trials that assessed:

• empirical use of hydrolysed formulas; and

• indicated (therapeutic) use of hydrolysed formulas to treat infants with feed intolerance or gastro‐oesophageal reflux (and associated apnoea, desaturation, or bradycardia), or following gastrointestinal surgery or necrotising enterocolitis (as defined by the primary investigators).

Types of outcome measures

Electronic searches

We searched the Cochrane Central Register of Controlled Trials (CENTRAL; 2019, Issue 1), in the Cochrane Library; Ovid MEDLINE (1946 to 28 January 2019); Ovid Embase (1974 to 28 January 2019); Ovid Maternity & Infant Care Database (1971 to January 2019); and the Cumulative Index to Nursing and Allied Health Literature (CINAHL; 1982 to 28 January 2019) using a combination of the following text words and medical subject heading (MeSH) terms as described in Appendix 1. We limited search outputs by using relevant search filters for clinical trials, as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We did not apply language restrictions.

We searched ClinicalTrials.gov and the World Health Organization's International Trials Registry and Platform (www.who.int/ictrp/en/) for completed and ongoing trials.

Searching other resources

We examined reference lists in previous reviews and included studies. We searched the proceedings of the annual meetings of the Pediatric Academic Societies (1993 to 29 January 2019), the European Society for Paediatric Research (1995 to 28 January 2019), the Royal College of Paediatrics and Child Health (2000 to 28 January 2019), and the Perinatal Society of Australia and New Zealand (2000 to 28 January 2019). Trials reported only as abstracts were eligible if sufficient information was available from the report, or from contact with study authors, to fulfil the inclusion criteria.

Selection of studies

We screened the title and abstract of all studies identified by the search strategy, and two review authors independently assessed the full articles for all potentially relevant trials. We excluded those studies that did not meet all of the inclusion criteria, and we stated the reasons for exclusion. We discussed any disagreements until consensus was achieved.

Data extraction and management

Two review authors (DN and WM) extracted data independently using a data collection form to aid extraction of information on design, methods, participants, interventions, outcomes, and treatment effects from each included study. We discussed any disagreements until we reached a consensus. If data from the trial reports were insufficient, we contacted the triallists for further information.

Assessment of risk of bias in included studies

Two review authors (DN and JK) independently assessed the risk of bias (low, high, or unclear) of all included trials using the Cochrane ‘Risk of bias’ tool for the following domains (Higgins 2011).

• Sequence generation (selection bias).

• Allocation concealment (selection bias).

• Blinding of participants and personnel (performance bias).

• Blinding of outcome assessment (detection bias).

• Incomplete outcome data (attrition bias).

• Selective reporting (reporting bias).

• Any other bias.

Any disagreements were resolved by discussion or by consultation with a third assessor (WM). See Appendix 2 for a more detailed description of risk of bias for each domain. We requested additional information from the trial authors to clarify methods and results when necessary. We did not exclude trials on the basis of risk of bias, but we did plan to conduct sensitivity analyses if applicable to explore the consequences of synthesising evidence of variable quality (Higgins 2011).

Measures of treatment effect

We analysed treatment effects in individual trials using Review Manager 5 (RevMan 2014), and we reported risk ratio (RR) and risk difference (RD) for dichotomous data, and mean difference (MD) for continuous data, with respective 95% confidence intervals (CIs). We determined the number needed to treat for an additional beneficial outcome (NNTB) or an additional harmful outcome (NNTH) for analyses with a statistically significant difference in the RD.

Unit of analysis issues

The unit of analysis was the participating infant for individually randomised trials, and the neonatal unit (or subunit) for cluster‐randomised trials. For cluster‐randomised trials, we planned to undertake analyses at the level of the participant while accounting for clustering of data using the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Dealing with missing data

Where data were missing and could not be derived as described, we approached the analysis of missing data as follows.

• We contacted the original study investigators to request the missing data.

• Where possible, we imputed missing standard deviations (SDs) using the coefficient of variation (CV) or calculated from other available statistics including standard errors, CIs, t values, and P values.

• If data were assumed to be missing at random, we analysed the data without imputing any missing values.

• If this could not be assumed, then we planned to impute the missing outcomes with replacement values, assuming all to have a poor outcome. We planned sensitivity analyses to assess any changes in the direction or magnitude of effect resulting from data imputation.

Assessment of heterogeneity

Two review authors assessed clinical heterogeneity, with a meta‐analysis conducted only when both authors agreed that study participants, interventions, and outcomes were sufficiently similar.

We examined treatment effects of individual trials and heterogeneity between trial results by inspecting the forest plots. We calculated the I² statistic for each analysis to quantify inconsistency across studies, and we described the percentage of variability in effect estimates that may be due to heterogeneity rather than to sampling error. If we detected moderate or high heterogeneity (I² > 50%), we planned to explore the possible causes (e.g. differences in study design, participants, interventions, or completeness of outcome assessments).

Assessment of reporting biases

If more than 10 trials were included in a meta‐analysis, we planned to examine a funnel plot for asymmetry.

Data synthesis

We used the fixed‐effect model in Review Manager 5 for meta‐analyses (as per Cochrane Neonatal recommendations) (RevMan 2014). Where moderate or high heterogeneity existed, we planned to examine the potential causes in subgroup and sensitivity analyses.

Quality of evidence

We used the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) approach, as outlined in the GRADE Handbook (Schünemann 2013), to assess the quality of evidence for the following (clinically relevant) outcomes: feed tolerance and incidence of necrotising enterocolitis.

Two review authors (DN and JK) independently assessed the quality of evidence for each of the outcomes above. We considered evidence from randomised controlled trials (RCTs) as high quality but downgraded the evidence one level for serious (or two levels for very serious) limitations based upon the following: design (risk of bias), consistency across studies, directness of evidence, precision of estimates, and presence of publication bias. We used the GRADEpro Guideline Development Tool to create Summary of findings table 1 to report the quality of evidence (GRADEpro GDT).

The GRADE approach yields an assessment of the quality of a body of evidence using one of four grades.

• High: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.

• Very low: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate.

Subgroup analysis and investigation of heterogeneity

We planned subgroup analyses by:

• gestational age at birth: very preterm (less than 32 weeks' gestation) infants versus infants born at 32 weeks' gestation or later;

• indication (for therapeutic use): post surgery versus post necrotising enterocolitis versus feeding intolerance or gastro‐oesophageal reflux; and

• extent of protein hydrolysis (as defined by manufacturers): extensively versus partially hydrolysed formula.

Sensitivity analysis

We planned to perform sensitivity analyses to determine if findings were affected by including only studies using adequate methods (low risk of bias), defined as adequate randomisation and allocation concealment, blinding of intervention and measurement, and less than 10% loss to follow‐up.