Primary outcomes

1. Incidence of episiotomy wound infection (including oedema, erythema, serosanguinous, or frankly purulent material), as defined by trial authors.

2. Incidence of episiotomy wound dehiscence (breakdown).

3. Incidence of puerperal infection (e.g. endometritis with or without myometritis, and with or without salpingitis causing maternal febrile morbidity after an episiotomy), as defined by authors.

Secondary outcomes

1. Incidence of severe maternal infectious morbidity (septicaemia, septic shock, laparotomy or hysterectomy for infection, or maternal intensive care unit (ICU) admission), as defined by trial authors.

2. Length of maternal hospital stay.

3. Discomfort or pain at episiotomy wound site, as defined by author.

4. Sexual function postpartum (dyspareunia, sexual satisfaction, sexual sensation, time‐to‐resuming sexual intercourse), as defined by trials authors.

5. Adverse effects of antibiotics (maternal: allergic reaction, nausea, vomiting, diarrhoea, skin rashes, anaphylaxis; neonatal: allergic reaction, diarrhoea, skin rashes, anaphylaxis).

6. Cost of care, including re‐admission to hospital, cost of antibiotic treatment.

7. Women's satisfaction with care, as reported by trial authors.

8. Individual antimicrobial resistance (e.g. no response to first‐line antibiotic treatment, culture of antibiotic‐resistant bacterial strains), as reported by trial authors.

(1) Random sequence generation (checking for possible selection bias)

For the included study, we described the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We assessed the method as:

• low risk of bias (any truly random process, e.g. random number table, computer random number generator);

• high risk of bias (any non‐random process, e.g. odd or even date of birth, hospital or clinic record number);

• unclear risk of bias.

(2) Allocation concealment (checking for possible selection bias)

For the included study, we described the method used to conceal allocation to interventions prior to assignment, and assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We assessed the methods as:

• low risk of bias (e.g. telephone or central randomisation, consecutively numbered sealed opaque envelopes);

• high risk of bias (open random allocation, unsealed or non‐opaque envelopes, alternation, date of birth);

• unclear risk of bias.

(3.1) Blinding of participants and personnel (checking for possible performance bias)

For the included study, we described the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed the methods as:

• low, high or unclear risk of bias for participants;

• low, high or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

For the included study, we described the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed methods used to blind outcome assessment as:

• low, high or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

For the included study, and for each outcome or class of outcomes, we described the completeness of data, including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported, and the numbers included in the analysis at each stage (compared with the total randomised participants), whether reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. No missing data were re‐included in the analyses undertaken.

We assessed methods as:

• low risk of bias (e.g. no missing outcome data or less than 20%, missing outcome data balanced across groups);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups, ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);

• unclear risk of bias.

(5) Selective reporting (checking for reporting bias)

For the included study, we described how we investigated the possibility of selective outcome reporting bias and what we found.

We assessed the methods as:

• low risk of bias (where it was clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review were reported);

• high risk of bias (where not all the study’s pre‐specified outcomes were reported, one or more reported primary outcomes were not pre‐specified, outcomes of interest were reported incompletely and so could not be used, study failed to include results of a key outcome that would have been expected to have been reported);

• unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

For the included study, we described any important concerns we had about other possible sources of bias.

We assessed whether the study was free of other problems that could put it at risk of bias:

• low risk of other bias;

• high risk of other bias;

• unclear whether there is risk of other bias.

(7) Overall risk of bias

We made explicit judgements about whether the study was at high risk of bias, according to the criteria given in the Handbook of Systematic Reviews of Interventions (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias, and whether we considered it was likely to impact on the findings. We explored the impact of the level of bias by undertaking sensitivity analyses ‐ see Sensitivity analysis.

Assessing the quality of the evidence using GRADE

We assessed the quality of the evidence using the GRADE approach, as outlined in the GRADE Handbook, in order to assess the quality of the body of evidence relating to the following outcomes for the main comparisons (Schünemann 2013).

1. Incidence of episiotomy wound infection (including oedema, erythema, serosanguinous, or frankly purulent material), as defined by trial authors.

2. Incidence of episiotomy wound dehiscence (breakdown).

3. Incidence of puerperal infection (e.g. endometritis with or without myometritis and with or without salpingitis causing maternal febrile morbidity after an episiotomy), as defined by authors.

4. Incidence of severe maternal infectious morbidity (septicaemia, septic shock, laparotomy, or hysterectomy for infection, or maternal ICU admission), as defined by trial authors.

5. Discomfort or pain at episiotomy wound site, as defined by author.

6. Women's satisfaction with care, as reported by trial authors.

7. Adverse effects of antibiotics (maternal: allergic reaction, nausea, vomiting, diarrhoea, skin rashes, anaphylaxis; neonatal: allergic reaction, diarrhoea, skin rashes, anaphylaxis).

We used the GRADEpro Guideline Development Tool (GRADEpro GDT) to import data from Review Manager 5, in order to create ’Summary of findings’ tables (RevMan 2014). A summary of the intervention effect and a measure of quality for each of the above outcomes were produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.

Dichotomous data

For dichotomous data, we presented results as summary risk ratios with 95% confidence intervals.

Continuous data

We did not identify any continuous outcome data. However, if we identify continuous outcome data in future updates of this review, we will use the mean difference if outcomes are measured in the same way between trials. We will use standardised mean difference to combine trials that measure the same outcome, but use different methods.

Cluster‐randomised trials

We did not identify any cluster‐randomised trials. However, if we identify cluster‐randomised trials in future updates of this review, we will include cluster‐randomised trials in the analyses along with individually‐randomised trials. We will adjust their sample sizes using the methods described in the Handbook of Systematic Reviews of Interventions, Section 16.3.4 or 16.3.6, using an estimate of the intracluster correlation co‐efficient (ICC) derived from the trial (if possible), from a similar trial, or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually‐randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs, and the interaction between the effect of the intervention and the choice of the randomisation unit is considered to be unlikely.

We will also acknowledge heterogeneity in the randomisation unit, and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Cross‐over trials

We did not plan to include cross‐over trials.

Other unit of analysis issues

We did not identify any trials with more than two treatment groups. However, if we identify trials with more than two treatment groups in future updates of this review, we will consider trials with more than two treatment groups for inclusion if at least one intervention group is relevant to the systematic review. If multiple groups from one study are relevant for inclusion, we plan to combine all relevant experimental intervention groups of the study into a single group, and to combine all relevant control intervention groups into a single control group, if appropriate.