Types of studies

We included randomized controlled trials (RCTs) that compared macrolides as first‐line therapy with any other antibiotic treatment or any other symptomatic treatment. We also included RCTs that compared different macrolides regimens (by macrolide type) for the treatment of H ducreyi infection.

We excluded quasi‐RCTs because this produces effect estimates that indicate more extreme benefits when they are compared with RCTs (Higgins 2011). We excluded cross‐over and cluster trials, because of the nature of the condition and intervention (Higgins 2011). Finally, we excluded RCTs that assessed the effectiveness of trimethoprim‐sulfamethoxazole because several H ducreyi isolates with resistance to this medication have been reported worldwide (CDC 2015).

Types of participants

We included men and non‐pregnant women over the age of 16 years who presented with purulent genital ulcers compatible with chancroid.

We divided participants into two groups: syndromic (based on the presence of common and reasonably consistent signs and symptoms) and aetiological diagnosis (supporting on a laboratory‐confirmed).

Types of interventions

Macrolides (any dose, frequency, duration and administration route) versus:

• any other antibiotic treatment (any dose, frequency, duration and administration route);

• any symptomatic treatment (e.g. buboes aspiration or analgesic treatment); or

• any other macrolide type (any dose, frequency, duration and administration route).

Types of outcome measures

Electronic searches

We contacted the Information Specialist of the Cochrane STI Group in order to implement a comprehensive search strategy to identify as many relevant RCTs as possible in electronic databases. We used a combination of controlled vocabulary (Medical Subject Headings (MeSH), Emtree terms, DeCS, including exploded terms) and free‐text terms (considering spelling variants, synonyms, acronyms and truncation) for "Haemophilus ducreyi infection" and "Macrolides," with field labels, proximity operators and boolean operators. We listed our search strategies in Appendix 1.

We searched the following electronic databases:

• Cochrane STI Group's Specialized Register, which includes RCTs and controlled clinical trials, from 1944 to 2017, located through: electronic searches of CENTRAL, MEDLINE and Embase; online handsearching of journals not indexed in MEDLINE or Embase, according to the journals' master list of the Cochrane STI Group;

• Cochrane Central Register of Controlled Trials (CENTRAL), Ovid: inception to 30 October 2017;

• MEDLINE, Ovid: inception to 30 October 2017;

• MEDLINE In‐Process & Other Non‐Indexed Citations, Ovid: inception to 30 October 2017;

• MEDLINE Daily Update, Ovid: inception to 30 October 2017;

• Embase (Emabase.com): inception to 30 October 2017;

• LILACS, IAHx interface: inception to 30 October 2017.

For MEDLINE, we used the Cochrane highly sensitive search strategy for identifying RCTs: sensitivity and precision maximizing version (2008 revision), Ovid format (Higgins 2011). We combined the LILACS search strategy with an RCT filter of IAHx interface.

Searching other resources

We searched the following resources for additional trials:

• trials registers:

  • WHO International Clinical Trials Registry Platform (ICTRP) portal (apps.who.int/trialsearch/): inception to 30 October 2017;

  • ClinicalTrials.gov (clinicaltrials.gov/): inception to 30 October 2017;

• Web of Science: inception to 30 October 2017.

Selection of studies

LR and CFG‐A independently screened all the titles and abstracts retrieved from the search strategy to determine which trials we should assessed further. LR and CFG‐A independently investigated the full‐text articles of all potentially relevant articles and we resolved any disagreements through discussion. We presented a PRISMA flow diagram to show the process of trial selection (Figure 1). We listed all articles excluded after full‐text assessment and the reasons for exclusion in the Characteristics of excluded studies table.

Figure 1

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Study flow diagram.

Data extraction and management

We designed a data extraction form, which was pilot tested, to extract data from the included studies. For eligible studies, LR and CFG‐A independently extracted data. We resolved any disagreements through discussion until we reached a consensus.

We extracted data on the following:

• location of the study and setting;

• study design;

• power calculation performed;

• inclusion and exclusion criteria;

• syndromic or aetiological diagnosis.

• baseline information of the participants to ensure comparable intervention groups at entry (number of women, number of men, age, prior treatment for ulcer, presence of buboes, site and number of lesions, HIV coinfection);

• total number of intervention groups;

• types of interventions: macrolide type, concentration, frequency and duration of treatment;

• types of comparison: any other antibiotic treatment (any dose, frequency, duration and administration route) or any symptomatic treatment (e.g. buboes aspiration or analgesic treatment);

• methods used to generate random allocation and maintain allocation concealment;

• use of any method of blinding of researchers or participants to evaluate outcomes;

• number of participants enrolled, randomized, excluded after randomization, and analyzed;

• adherence to the planned intervention and other interventions in the groups under evaluation;

• how the trial authors defined outcomes;

• time of follow‐up of participants to measure outcomes;

• use of intention‐to‐treat (ITT) analysis;

• funding sources;

• ethical issues: use of signed informed consent and ethics approval.

For eligible studies, two review authors (CFG‐A and LR) entered data into Review Manager 5 (RevMan 2014), and checked for accuracy. When information regarding any of the above was unclear, we attempted to contact the authors of the original trial reports for further details. For a single RCT report, we extracted data directly into a data collection form; in cases of multiple reports, we extracted data from each report separately and then combined information across data collection forms.

Assessment of risk of bias in included studies

Two review authors (LR and CFG‐A) independently assessed the risk of bias for each included trial using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved any disagreements by consensus or by consulting a third review author (CH). The review authors who assessed the risk of bias in the included studies were theme and methodology experts.

Measures of treatment effect

For dichotomous data, we presented the results as risk ratios (RRs) with 95% confidence intervals (CIs). The RR was used as a relative effect measure, which works well with a low or high rate of events, and is easy to interpret and use in clinical practice.

We performed meta‐analysis separately for participants with syndromic and aetiological diagnosis. Syndromic management implies an approach in which clinic diagnostic was based on the presence of common and reasonably consistent signs and symptoms without resorting to techniques for laboratory confirmation (WHO 2005).

Unit of analysis issues

Where we identified a clinical trial that randomized participants to several intervention groups, we determined which intervention groups were relevant. To avoid confusion for the reader, we included all intervention groups of the study in the Characteristics of included studies table, and provided a detailed description only of the intervention groups that were relevant to the review, and we only used these groups in the analyses.

Finally, to overcome a unit‐of‐analysis error for a study that could contribute multiple, correlated comparisons, we combined all relevant experimental intervention groups of the studies into a single group and combined all relevant control intervention groups into a single control group, to create a single pair‐wise comparison (Higgins 2011).

The unit of analysis was the participant who received treatment. We performed separate analyses for participants who had microbiological and clinical cure and clinical improvement at first week, between first and second week, or after the second week.

Dealing with missing data

We reported the percentage of observations with missing data of each included trial. For all outcomes, we performed analyses, as far as possible, on an ITT basis (i.e. we attempted to include all participants randomized to each group in the analyses, and we analyzed all participants in the group to which they were allocated, regardless of whether or not they received the allocated intervention). In case that this was not possible, the denominator for each outcome in each trial was the number randomized minus any participants whose outcomes were missing. We contacted the study investigators to request the missing data.

Assessment of heterogeneity

We assessed statistical heterogeneity in each meta‐analysis using the I² statistic and Chi² test values (Higgins 2011). We regarded heterogeneity as substantial if the I² statistic value was greater than 40% and if we found a low P value (less than 0.10) in the Chi² test for heterogeneity, which we plotted in a forest plot (RevMan 2014).

Assessment of reporting biases

We planned to explored publication bias through assessment of funnel plot asymmetry and formal tests. For continuous outcomes, we planned to use the test proposed by Egger 1997, and for dichotomous outcomes we planned to use the test proposed by Harbord 2006. However, we included fewer than 10 trials in the meta‐analysis, so we did not perform these analyses.

Data synthesis

We performed statistical analyses using Review Manager 5 (RevMan 2014). We conducted separate analyses for syndromic and aetiological syndromic and diagnose. Because WHO (WHO 2005) and other clinical practice guidelines (Min Salud 2013) recommend syndromic management for low‐income countries, we presented as primary analysis the effects of the intervention based on those studies that implemented this approach and as secondary analysis, the results from trials that used aetiological diagnosis.

We used a fixed‐effect meta‐analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect (i.e. where trials were examining the same intervention, and the trial populations and methods were judged sufficiently similar). If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or if we detected substantial statistical heterogeneity, we used a random‐effects meta‐analysis to produce an overall summary if a mean treatment effect across trials was considered clinically meaningful. We treated the random‐effects summary as the mean range of possible treatment effects and we discussed the clinical implications of treatment effects differing between trials. If the mean treatment effect was not clinically meaningful, we did not combine trials.

If we used random‐effects analyses, we presented the results as the mean treatment effect with 95% CIs, and the estimates of the Tau² and I² statistics.

Subgroup analysis and investigation of heterogeneity

We explored the following potential sources of heterogeneity using subgroup analyses:

• HIV status (positive versus negative participants);

• disease clinical stage (ulcer versus ulcer plus inguinal buboes).

We restricted subgroup analyses to the primary outcomes: microbiological and clinical cure, clinical improvement and serious adverse events.

Sensitivity analysis

We performed sensitivity analyses to identify aspects of the review that might have affected the results; for example, where there was risk of bias associated with the quality of some of the included trials (low versus unclear or high risk of bias).