Types of studies

Randomised controlled trials (RCTs) comparing HRT using any regimen and duration of administration with placebo or no hormone therapy, or trials comparing different regimens or duration of administration of HRT.

Types of participants

We will include women diagnosed with all stages of epithelial ovarian cancer who had surgical treatment, regardless of chemotherapy. We will include women who had fertility‐preserving surgery (retention of uterus and/or one ovary) and we aim to perform a subgroup analysis separating these women from those who have complete pelvic clearance (hysterectomy and bilateral salpingo‐oophorectomy) (see Subgroup analysis and investigation of heterogeneity).

Types of interventions

We will include studies of the delivery of HRT after treatment for EOC and we will not study the aetiological effect of HRT before diagnosis. Any HRT, regimen or duration of administration, compared with placebo or no hormone therapy will be included. Due to pharmacokinetic differences between different regimens and durations of administration, we will review the following three comparisons.:

1. HRT versus placebo or no HRT.

2. Different regimens of HRT.

3. Different durations of administration.

Types of outcome measures

Electronic searches

We will search the following electronic databases.

• Cochrane Central Register of Controlled Trials (CENTRAL, the Cochrane Library, latest issue).

• MEDLINE (1946 to present).

• Embase (1980 to present).

The MEDLINE search strategy is presented in Appendix 1.

For databases other than MEDLINE (Ovid), we will adapt the search strategy accordingly.

Searching other resources

All relevant articles will be identified on PubMed and using the 'related articles' feature a further search will be carried out for newly published articles.

We will search the following for ongoing trials.

• Metaregister (www.controlled‐trials.com/rct).

• Physicians Data Query (www.nci.nih.gov).

• World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (www.who.int/ictrp/en/).

• www.clinicaltrials.gov.

• www.cancer.gov/clinicaltrials.

If ongoing trials that have not been published are identified through these searches, we will approach the principal investigators, and major co‐operative groups active in this area, to ask for relevant data.

We will handsearch the citation lists of included studies, key textbooks, and previous systematic reviews, and contact experts in the field to identify further reports of trials. We will also handsearch the reports of conferences in the following sources.

• Gynecologic Oncology (Annual Meeting of the American Society of Gynecologic Oncology).

• International Journal of Gynecological Cancer (Annual Meeting of the International Gynecologic Cancer Society).

• British Gynaecological Cancer Society (BGCS).

• Annual Meeting of European Society of Gynaecological Oncology (ESGO).

Selection of studies

We will download all titles and abstracts retrieved by electronic searching to a reference management database (Endnote). After duplicates are removed, we will transfer these data to Covidence for study selection. Two review authors (NS and RB) will examine the remaining references independently. We will exclude those studies which clearly do not meet the inclusion criteria. We will obtain copies of the full text of potentially relevant references. Two review authors (NS and RB) will independently assess the eligibility of the retrieved reports/publications. We will resolve any disagreement through discussion or, if required, we will consult a third person (TL). We will identify and exclude duplicates and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (Liberati 2009).

Data extraction and management

Two review authors (NS and KP) will independently extract study characteristics and outcome data from included studies on to a pre piloted data collection form using Covidence. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way. We will resolve disagreements by consensus or by involving a third person (RB). One review author (NS) will transfer data into the Review Manager (RevMan 2014) file. We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports. A second review author (KP) will 'spot‐check' study characteristics for accuracy against the trial report.

For included studies, we will extract the following data.

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

• Country

• Setting

• Inclusion and exclusion criteria

• Study design, methodology

• Study population

  • Total number enrolled

  • Patient characteristics: age, menopausal status at diagnosis, performance status

  • Treatment: type of surgery and chemotherapy

  • Tumour stage, grade and types

• Intervention details

  • all types of HRT: oestrogen‐alone or combined with progestin, oestrogen agonist/antagonist, progestin, testosterone or tibolone

  • duration of administration of HRT in years

  • route and doses of HRT

• Comparison

  • placebo or no treatment

• Risk of bias in study (see Assessment of risk of bias in included studies)

• Duration of follow‐up

• Outcomes: For each outcome, we will extract the outcome definition. For adjusted estimates, we will record variables adjusted for in analyses.

• Results: We will extract the number of participants allocated to each intervention group, the total number analysed for each outcome, and number of drop‐outs, including reason for leaving the study.

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

Results will be extracted as follows.

• For time‐to‐event data (survival and disease progression), we will extract the log of the hazard ratio [log(HR)] and its standard error from trial reports. If these are not reported, we will attempt to estimate the log (HR) and its standard error using the methods of Parmar 1998.

• For dichotomous outcomes (e.g. adverse events or deaths, if it is not possible to use a hazard ratio) we will extract the number of patients in each treatment arm who experienced the outcome of interest and the number of patients assessed at endpoint, in order to estimate a risk ratio.

• For continuous outcomes (e.g. QoL measures), we will extract the final value and standard deviation of the outcome of interest and the number of patients assessed at endpoint in each treatment arm at the end of follow‐up, in order to estimate the mean difference between treatment arms and its standard error.

Where possible, all data extracted will be those relevant to an intention‐to‐treat analysis, in which participants will be analysed in groups to which they were assigned. We will note the time points at which outcomes were collected and reported.

Assessment of risk of bias in included studies

We will assess and report on the risk of bias of included studies in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), which recommends the explicit reporting of the following individual elements for RCTs.

1. selection bias: random sequence generation and allocation concealment

2. detection bias: blinding of outcome assessment.

3. attrition bias: incomplete outcome data.

4. reporting bias: selective reporting of outcomes.

5. other potential sources of bias.

Two review authors (NS and KP) will apply the 'Risk of bias' tool independently and resolve differences by discussion or by appeal to a third review author (EM). We will judge each item as being at high, low or unclear risk of bias as set out in the criteria provided by Higgins 2011 (and shown below), and provide a quote from the study report and/or a statement as justification for the judgement for each item in the 'Risk of bias' table. We will summarise results in both a 'Risk of bias' graph and a 'Risk of bias' summary. When interpreting treatment effects and meta‐analyses, we will take into account the risk of bias for the studies that contribute to that outcome. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

• Random sequence generation

  1. Low risk of bias e.g. participants assigned to treatments on basis of a computer‐generated random sequence or a table of random numbers

  2. High risk of bias e.g. participants assigned to treatments on basis of date of birth, clinic ID number or surname, or no attempt to randomise participants

  3. Unclear risk of bias e.g. not reported, information not available

• Allocation concealment

  1. Low risk of bias e.g. where the allocation sequence could not be foretold

  2. High risk of bias e.g. allocation sequence could be foretold by patients, investigators or treatment providers

  3. Unclear risk of bias e.g. not reported

• Blinding of participants and personnel (NB. Blinding of patients and treatment providers is usually possible only for pharmacological interventions)

  1. Low risk of bias if participants and personnel were adequately blinded

  2. High risk of bias if participants were not blinded to the intervention that the participant received

  3. Unclear risk of bias if this was not reported or unclear

• Blinding of outcomes assessors

  1. Low risk of bias if outcome assessors were adequately blinded

  2. High risk of bias if outcome assessors were not blinded to the intervention that the participant received

  3. Unclear risk of bias if this was not reported or unclear

• Incomplete outcome data: we will record the proportion of participants whose outcomes were not reported at the end of the study. We will code a satisfactory level of loss to follow‐up for each outcome as:

  1. Low risk of bias, if fewer than 20% of patients were lost to follow‐up and reasons for loss to follow‐up were similar in both treatment arms

  2. High risk of bias, if more than 20% of patients were lost to follow‐up or reasons for loss to follow‐up differed between treatment arms

  3. Unclear risk of bias if loss to follow‐up was not reported

• Selective reporting of outcomes

  1. Low risk of bias e.g. review reports all outcomes specified in the protocol

  2. High risk of bias e.g. it is suspected that outcomes have been selectively reported

  3. Unclear risk of bias e.g. it is unclear whether outcomes have been selectively reported

• Other biases

  1. Low risk of bias ‐ if you do not suspect any other source of bias and the trial appears to be methodologically sound

  2. High risk of bias ‐ if you suspect that the trial was prone to an additional bias

  3. Unclear risk of bias ‐ if you are uncertain whether an additional bias may have been present

Measures of treatment effect

We will use the following measures of the effect of treatment.

• For time‐to‐event data, we will use the hazard ratio, if possible.

• For dichotomous outcomes, we will analyse data based on the number of events and the number of people assessed in the intervention and comparison groups. We will use these to calculate the risk ratio (RR) and 95% confidence interval (CI).

• For continuous outcomes, we will analyse data based on the mean, standard deviation (SD) and number of people assessed for both the intervention and comparison groups to calculate mean difference (MD) between treatment arms with a 95% CI. If the MD is reported without individual group data, we will use this to report the study results. If more than one study measures the same outcome using different tools, we will calculate the standardised mean difference (SMD) and 95% CI using the inverse variance method in RevMan 2014.

Unit of analysis issues

We will exclude cluster‐randomised and cross‐over trials.

Dealing with missing data

We will attempt to contact study authors to obtain missing data (participant, outcome, or summary data). We will report on the levels of loss to follow‐up and assess this as a source of potential bias. The impact of including studies with high levels of missing data in the overall assessment of treatment effect will be explored by using sensitivity analysis. We will impute missing outcome data for the primary outcome.

Assessment of heterogeneity

Where studies are considered similar enough in terms of data for age, stage and histological type to allow pooling of data using meta‐analysis, we will assess the degree of heterogeneity by visual inspection of forest plots, by estimation of the percentage of heterogeneity (I² statistic) between trials which cannot be ascribed to sampling variation (Higgins 2003), by a formal statistical test of the significance of the heterogeneity (Chi²) (Deeks 2001) and, if possible, by subgroup analyses. We will regard heterogeneity to be substantial if I² is greater than 50% and either T² is greater than zero, or there is a low P value (< 0.10) in the Chi² test for heterogeneity. If substantial heterogeneity is found, the subgroup and sensitivity analyses will be used to explore the causes of heterogeneity. If substantial heterogeneity exists the random‐effects model will be used instead of fixed‐effect model.

If there is evidence of substantial clinical, methodological or statistical heterogeneity across included studies we will not report pooled results from meta‐analysis but will instead use a narrative approach to data synthesis. In this event we will investigate and report the possible clinical or methodological reasons for this.

Assessment of reporting biases

If more than ten studies are identified, we will examine funnel plots corresponding to meta‐analysis of the primary outcome to assess the potential for small study effects such as publication bias. We plan to assess funnel plot asymmetry visually, and if asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

If sufficient, clinically‐similar studies (in terms of participants, settings, intervention, comparison and outcome measures) are available to ensure meaningful conclusions, and if statistical heterogeneity is low (I² less than 30%) we will pool their results in meta‐analyses using the fixed‐effect model in Cochrane Review Manager software (RevMan 2014). If there is variability in the data for age, stage and histological type in the included studies, or if statistical heterogeneity is substantial (I² more than 50%) we will use the random‐effects model with inverse variance for meta‐analysis (DerSimonian 1986).

• For time‐to‐event data, we will pool hazard ratios using the generic inverse variance facility of RevMan 2014.

• For dichotomous outcomes, we will calculate the risk ratio (RR) for each study and these will then be pooled.

• For continuous outcomes, will pool the mean differences (MD) between the treatment arms at the end of follow‐up, if all trials measure the outcome on the same scale; otherwise we will pool standardised mean differences (SMD).

If any trials have multiple treatment groups, we will divide the ‘shared’ comparison group into the number of treatment groups and comparisons between each treatment group and treat the split comparison group as independent comparisons.

If we are unable to pool the data statistically using meta‐analysis we will conduct a narrative synthesis of results. We will present the major outcomes and results, organised by intervention categories according to the major types and/or aims of the identified interventions. Depending on the assembled research, we may also explore the possibility of organising the data by population. Within the data categories we will explore the main comparisons of the review.

We will present the overall quality of the evidence for each outcome listed below, using the GRADE approach, which takes into account issues not only related to internal validity (risk of bias, inconsistency, imprecision, publication bias) but also to external validity such as directness of results (Langendam 2013). We will create a 'Summary of findings' table based on the methods described Chapter 12.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Schunemann 2011) and using GRADEpro GDT (Appendix 2). We will use the checklist to maximise consistent GRADE decisions and the GRADE Working Group quality of evidence definitions (Meader 2014). We will downgrade the evidence from 'high' quality by one level for serious (or by two for very serious) limitations for each outcome, and outline our rationale in the footnotes.

• High quality: Further research is very unlikely to change our confidence in the estimate of effect.

• Moderate quality: Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate.

• Low quality: Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.

• Very low quality: We are very uncertain about the estimate.

Outcomes:

1. Overall survival

2. Disease‐free survival

3. Incidence of breast cancer

4. Incidence of thromboembolic events (DVT/PE, stroke, MI)

5. Incidence of gallstones

6. Quality of life assessment

Subgroup analysis and investigation of heterogeneity

We aim to perform subgroup analyses.

Of clinical interest will be to investigate the safety (risk and benefits) as per the prespecified outcomes in this protocol for:

1. menopausal status at diagnosis: premenopausal versus postmenopausal. If menopausal status is not extractable from studies, we will analyse by age (under 50 years versus 50 years or older);

2. hysterectomy versus no hysterectomy;

3. retention of ovary for fertility preservation versus removal of both ovaries;

4. stage: stage I‐II versus stage III‐IV;

5. tumour types: endometrioid versus non‐endometrioid; and

6. BRCA mutation status.

Sensitivity analysis

If necessary we will assess the robustness of results due to the impact of notable assumptions, imputed data, borderline decisions, choice of meta‐analysis method and inclusion of studies at high risk of bias using a sensitivity analyses and repeat the primary analyses of the review, e.g. by comparing fixed‐effect versus random‐effects methods or removing lower quality studies. The aim is to determine how robust the results of the review are to the decisions that were made in conducting the review.