Types of studies

We included randomised controlled trials (RCTs).

Types of participants

Women aged 18 years or over with early‐stage cervical cancer who have undergone radical hysterectomy (Piver type II, Piver type III, Querleu‐Morrow class B2, or class C1). Early‐stage cervical cancer was defined as cervical cancer stage IA2 to IIA2 by either the 2009 or 2018 FIGO staging system. If studies included women with other types of gynaecological cancer (i.e. endometrial cancer), we planned to contact the trial authors to retrieve data related to participants with cervical cancer only. If this was not possible, we planned to include the study only if at least 80% of participants were diagnosed with cervical cancer.

Types of interventions

We planned to include any trial that attempted to compare the following.

• A pharmacological agent and placebo or standard care.

• A non‐pharmacological intervention and a standard care. Specific non‐pharmacological interventions include postoperative suprapubic catheterisation, bladder training and acupuncture.

• A pharmacological agent and a non‐pharmacological intervention.

• A pharmacological agent and another agent.

• A non‐pharmacological intervention and another intervention.

• Combinations of intervention and placebo or standard care.

• Combinations of intervention and single intervention.

• Combinations of intervention and other combinations.

Types of outcome measures

Electronic searches

We searched the following electronic databases on 20 April 2020.

• The Cochrane Central Register of Controlled Trials (CENTRAL; 2020, Issue 4) in the Cochrane Library;

• MEDLINE via Ovid (1946 to April week 2 2020);

• Embase via Ovid (1980 to 2020 week 16).

Appendix 5, Appendix 6, and Appendix 7 display the search strategies for CENTRAL, MEDLINE, and Embase, respectively.

Searching other resources

We searched the World Health Organization International Clinical Trials Registry Platform (who.int/ictrp/en/) and ClinicalTrials.gov to identify any ongoing trials. If we identified ongoing trials that had not been published, we planned to approach the principal investigators and major co‐operative groups active in this area to ask for relevant data. We searched the following databases for grey literature: Open‐Grey (opengrey.eu/) and Index to theses (proquest.com/products-services/pqdt_uk_ireland.html).

Selection of studies

We downloaded all titles and abstracts retrieved via an electronic search of the Endnote reference management database. After duplicates were removed, we transferred these data to Covidence (covidence.org). Two review authors (AA and CK) examined the remaining references independently. We excluded those studies which clearly did not meet the inclusion criteria, and we obtained full‐text copies of potentially relevant references. Two review authors (AA and CK) independently assessed the eligibility of the retrieved reports or publications. We resolved any disagreement through discussion or, if required, we planned to consult a third review author (KG or PL). We identified and excluded duplicates and collated multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. We used the details obtained from the selection process in Covidence to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (Liberati 2009).

Data extraction and management

Two review authors (AA and CK) independently extracted study characteristics and outcome data from included studies using Covidence. We noted in the 'Characteristics of included studies' table if outcome data were not reported in a usable way. We resolved disagreements by consensus or by involving a third review author (KG or TT). One review author (CK) checked study characteristics for accuracy against the trial report.

For included studies, we extracted the following data.

• Author, year of publication, and journal citation (including language).

• Country.

• Setting.

• Inclusion and exclusion criteria.

• Study methodology.

• Study population and disease characteristics:

  • total number enrolled;

  • participant characteristics;

  • age;

  • co‐morbidities;

  • other baseline characteristics;

  • percentage of participants with non‐cervical cancer (only RCTs involving mixed gynaecologic malignancies);

  • FIGO stage of cervical cancer;

  • the histopathological subtype of cervical cancer;

  • tumour size (largest tumour diameter);

  • the radicality of surgery (Piver or Querleu‐Morrow).

• Intervention details:

  • schedule of bladder training;

  • suprapubic cystostomy technique;

  • acupuncture;

  • cholinergic agents (dose, duration).

• Comparison:

  • placebo;

  • no intervention.

• Risk of bias in the study (see below).

• Duration of follow‐up.

• Outcomes: for each outcome, we extracted the outcome definition and unit of measurement (if relevant); for adjusted estimates, we recorded variables adjusted for in analyses.

• Results: we extracted the number of participants allocated to each intervention group, the total number analysed for each outcome, and the missing participants.

• Notes: funding for trial and notable conflicts of interest of trial authors.

Assessment of risk of bias in included studies

We assessed and reported on the methodological quality and risk of bias in included studies in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019), which recommends the explicit reporting of the following individual elements for RCTs.

• Selection bias: random sequence generation and allocation concealment.

• Performance bias: blinding of participants and personnel (treatment providers).

• Detection bias: blinding of outcome assessment.

• Attrition bias: incomplete outcome data.

• Reporting bias: selective reporting of outcomes.

• Other possible bias.

We considered outcome data as complete if at least 80% of participants underwent follow‐ups and were assessed for primary outcomes. Two review authors (AA and CK) independently applied the 'Risk of bias' tool and resolved differences by discussion or by appeal to a third review author (KG or PL). We judged each item as being at high, low or unclear risk of bias as set out in the criteria displayed in Appendix 8. We provided a quote from the study report or a statement, or both, as justification for our judgement for each item in the 'Risk of bias' table. We summarised results in both a 'Risk of bias' graph and a 'Risk of bias' summary. When interpreting treatment effects and meta‐analyses, we took into account the risk of bias in the studies that contribute to that outcome. Where information on risk of bias relates to unpublished data or correspondence with trial authors, we planned to note this in the table.

Measures of treatment effect

We used the following measures of the effect of treatment.

• For dichotomous outcomes (e.g. rate of spontaneous voiding recovery one week after surgery, rate of urethral catheter removal, rate of urinary tract infections, number of participants with normal detrusor pressure at maximum flow, adverse events), we analysed data based on the number of events and the number of women assessed in the intervention and comparison groups. We used these to calculate the risk ratio and 95% confidence interval.

• For continuous outcomes (e.g. duration of postoperative retained urethral catheterisation, post‐void residual urine volume and QoL measures), we analysed data based on the means, standard deviations and number of women assessed for both the intervention and comparison groups to calculate the mean differences between treatment arms with their 95% confidence intervals. If the mean difference was reported without individual group data, we used this to report the study results. If more than one study measured the same outcome using different tools, we calculated the standardised mean difference and 95% confidence interval using the inverse variance method.

• For time‐to‐event data (e.g. time after surgery to a post‐void residual urine volume of 50 mL or less), we planned to extract the log of the hazard ratio (log_HR) and its standard error from trial reports. If these were not reported, we planned to estimate the log_HR and its standard error using the methods of Parmar 1998.

Unit of analysis issues

We included studies in which individual women were randomised. In a study with multiple intervention groups, we planned to combine all relevant experimental intervention groups into a single group to create a single pair‐wise comparison, where possible (Higgins 2019).

Dealing with missing data

We planned to contact the original investigators to request missing data. If we could not contact the investigators or could not obtain the requested missing data, we planned to analyse only the available data and not to impute missing outcome data for any of the outcomes.

Assessment of heterogeneity

We clinically assessed heterogeneity by visual inspection of forest plots. We assessed statistical heterogeneity in each meta‐analysis using the I² statistic and Chi² test (Higgins 2003). We regarded heterogeneity as substantial if the I² statistic value was greater than 50% or there was a low P value (< 0.10) in the Chi² test for heterogeneity (Deeks 2001; Higgins 2019). If there was substantial statistical heterogeneity, we planned to carry out subgroup analyses to assess differences among the included studies. However, if there was both clinical and methodological heterogeneity across included studies, we planned to not report pooled results from meta‐analysis, but instead use a narrative approach to data synthesis.

Assessment of reporting biases

See Differences between protocol and review.

We were unable to assess reporting bias, as only four studies met our inclusion criteria.

Data synthesis

We applied the random‐effects model with inverse variance weighting for all meta‐analyses (DeSimonian 1986). We performed statistical analysis using Review Manager 5.4 (Review Manager 2014).

• For time‐to‐event data, we planned to pool hazard ratios using the generic inverse variance.

• For any dichotomous outcomes, we calculated the risk ratios for each study and then pooled them.

• For continuous outcomes, we pooled the mean differences among the treatment arms, if all trials measure the outcome on the same scale; otherwise we planned to pool standardised mean differences

Subgroup analysis and investigation of heterogeneity

See Differences between protocol and review.

We intended to carry out subgroup analyses in order to assess the effect of the following factors.

• Tumour size (2 cm or less versus more than 2 cm).

• Surgical approach (laparotomy versus minimally invasive surgery).

• Nerve‐sparing approach during a radical hysterectomy (yes versus no).

• Radicality of surgery (Piver type II versus Piver type III, or Querleu‐Morrow class B2 versus class C1).

• Extent of pelvic lymph node dissection determined by the number of lymph nodes removed.

We planned to assess subgroup differences using the interaction tests available within Review Manager 2014. We planned to report the results of subgroup analyses by quoting the Chi² statistic and P value, the interaction test, and the I² statistic. However, we did not perform subgroup analysis, as most analyses were based on only one or two included studies. Nevertheless, we acknowledged these factors in the interpretation of review findings.

Sensitivity analysis

See Differences between protocol and review.

We were unable to conduct any of the planned sensitivity analyses due to insufficient data. If more studies are included in a future update, we plan to perform sensitivity analyses in order to assess the effect of the following factors.

• Repeating the analysis excluding unpublished studies (if any).

• Repeating the analysis excluding studies judged to be at 'high' or 'unclear' risk of bias for allocation concealment.

Summary of findings and assessment of the certainty of the evidence

We created Summary of findings tables to summarise the results of the meta‐analyses conducted for each of the outcomes, as outlined in the section Types of outcome measures. We graded the overall certainty of the evidence for each outcome according to the GRADE approach, which takes into account issues related not only to internal validity (risk of bias, inconsistency, imprecision, publication bias) but also to external validity, such as directness of results (Langendam 2013). We created a 'Summary of findings' table based on the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011), and used GRADEpro GDT (summary of findings Table 1; summary of findings Table 2).

• High certainty: the true effect lies close to that of the estimate of the effect.

• Moderate certainty: 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 certainty: the true effect may be substantially different from the estimate of the effect.

• Very low certainty: the true effect is likely to be substantially different from the estimate of effect.

We downgraded the evidence from 'high' certainty by one level for each serious (or by two for each very serious) limitation.