Criteria for considering studies for this review
Types of studies
We will include randomised controlled trials (RCTs).
Types of participants
Adult women (aged 18 and over) diagnosed with epithelial ovarian, tubal or primary peritoneal cancer (FIGO stage I to IV), previously treated with platinum-based chemotherapy, and with recurrent disease.
Types of interventions
We will include trials comparing two or more taxane monotherapy regimens.
We will exclude trials comparing taxane monotherapy to combination chemotherapy; trials using other chemical derivatives of taxanes, such as taxanes bound to proteins or nanoparticles; and trials of maintenance chemotherapy for women following front-line cancer treatment with no evidence of recurrence.
Types of outcome measures
Overall survival (OS): survival until death from all causes. We will assess survival from the time when women are enrolled in the study.
Response rate: the sum of complete and partial responders as defined by a standardised response criterion such as Response Evaluation Criteria in Solid Tumours (RECIST) or that of the World Health Organization (WHO) (Litière 2016; Park 2003).
Progression-free survival (PFS): survival until progression of disease. We will assess survival from the time when women are enrolled in the study.
Neurotoxicity (Grade 3 to 4)
Neutropenia (Grade 3 to 4)
Alopecia (Grade 3 to 4)
Quality of life, measured using a scale that has been validated through reporting of norms in a peer-reviewed publication.
We will present a 'Summary of findings' table reporting the following outcomes listed in order of priority:
Timing of outcome assessment
For time-to-event data (OS and PFS) our preferred method of outcome assessment is to extract the hazard ratio and its confidence interval from the Kaplan‒Meier curves in each study. However, should data be presented as a percentage of women our chosen time points are 12 months for PFS and 24 months for OS.
Search methods for identification of studies
There will be no language or date restrictions for our searches. We will search for papers in all languages and have them translated as necessary.
We will search the following electronic databases.
Cochrane Central Register of Controlled Trials (CENTRAL; latest issue in the Cochrane Library);
MEDLINE (1946 to present);
Embase (1980 to present);
PubMed (1996 to present).
We present the MEDLINE search strategy in Appendix 1.
For databases other than MEDLINE we will adapt the search strategy accordingly.
Searching other resources
We will identify all relevant articles on PubMed (ncbi.nlm.nih.gov/pubmed) and we will make a further search for newly published articles using the 'related articles' feature.
Unpublished and grey literature
We will search the following for ongoing trials.
If through these searches we identify ongoing trials that have not been published, 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. We will also handsearch the reports of conferences from the following sources. The date range of our searches will be 1983 to present as the first clinical trials of paclitaxel started in 1983 (Donehower 1996).
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 Journal of Cancer;
British Cancer Research Meeting;
Annual Meeting of European Society of Medical Oncology (ESMO);
Annual Meeting of the American Society of Clinical Oncology (ASCO).
Data collection and analysis
Selection of studies
We will download all titles and abstracts retrieved by electronic searching to the reference management database Endnote X8, and remove duplicates. Two review authors (BS, NH) will examine the remaining references independently. We will exclude those studies that clearly do not meet the inclusion criteria, and obtain copies of the full text of potentially relevant references. Independently, two review authors (BS, NH) will assess the eligibility of the retrieved reports/publications. We will resolve any disagreement through discussion or, if required, we will consult a third person (RK). We will identify and exclude duplicate reports 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 a 'Characteristics of excluded studies' table (Liberati 2009).
Potential reasons for exclusion of studies that appear eligible are as follows.
Includes a mixture of cancer types where ovarian cancer cannot be extracted.
Includes non-epithelial ovarian cancer where epithelial ovarian cancer cannot be extracted.
Includes women with epithelial ovarian cancer who have not relapsed after first-line therapy.
The study is not a RCT.
Data extraction and management
Independently, two review authors (BS, NH) will extract study characteristics and outcome data from included studies onto a piloted data collection form. 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 (RK). One review author (BS) will transfer data into the Review Manager 5 (RevMan 5) software (Review Manager 2014). We will double-check that data has been entered correctly by comparing the data presented in the systematic review with the study reports. A second review author (NH) will 'spot-check' the accuracy of the study characteristics against the trial report.
For included studies, we will extract the following data.
Author, year of publication and journal citation (including language)
Start and end date of patient enrolment
Total number enrolled, total number eligible and total number treated
Number of previous regimens of chemotherapy (dichotomised 1 or 2; and ≥ 3)
FIGO stage FIGO stage (dichotomised I or II; and III or IV)
Performance status (dichotomised 0 to 2; and ≥ 3)
Histology (dichotomised serous or non-serous)
Taxane pre-treatment status (dichotomised naive or pre-treated; women recruited prior to 1995 will be assumed to be taxane naive)
Platinum resistance status (dichotomised platinum resistant or sensitive; platinum refractory participants will be included with resistant)
Dose of drug
Method of administration
Risk of bias in study (see below)
Duration of follow-up
Outcomes: for each outcome, we will extract the outcome definition and unit of measurement (if relevant). For adjusted estimates, we will record variables adjusted for analyses.
Results: we will extract 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.
Results will be extracted as follows:
For time-to-event data (survival and disease progression), we will extract the hazard ratio (HR) and 95% confidence interval (CI) and then convert these to a log(HR) using RevMan 5. If the 95% CI is not reported, we will attempt to estimate the log(HR) and its standard error using the methods of Parmar 1998 and Tierney 2007.
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 participants in each treatment arm who experienced the outcome of interest and the number of participants 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 participants 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.
If reported, we will extract both unadjusted and adjusted statistics. Where possible, all data extracted will be those relevant to an intention-to-treat analysis, in which we will analyse participants in the groups to which they were assigned. We will note the time points at which outcomes were collected and reported.
Dealing with duplicate and companion publications
In the event of duplicate publications, companion documents or multiple reports of a primary study, we will maximise yield of information by collating all available data and use the most complete dataset aggregated across all known publications. In case of doubt, we will give priority to the publication reporting the longest follow-up associated with our primary or secondary outcomes. If possible, we will combine study references under the overall trial ID.
Assessment of risk of bias in included studies
We will assess and report on the methodological 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 (Appendix 2).
Selection bias: random sequence generation and allocation concealment
Performance bias: blinding of participants and personnel (i.e. treatment providers)
Detection bias: blinding of outcome assessment
Attrition bias: incomplete outcome data
Reporting bias: selective reporting of outcomes
Other possible sources of bias such as the source of funding for the study
Two review authors (BS, NH) will apply the 'Risk of bias' tool independently and resolve differences by discussion or by appeal to a third review author (RK). 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 provide a quote from the study report or a statement (or both) 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.
We define the following endpoints as subjective outcomes: progression-free survival, response, neurotoxicity, quality of life.
We define the following endpoints as objective outcomes: overall survival, neutropenia.
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 women 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 women 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 (Review Manager 2014).
We will undertake meta-analyses only where this is meaningful, i.e. if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense. We will describe skewed data that are reported as medians and interquartile ranges narratively. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. drug A versus placebo and drug B versus placebo) are combined in the same meta-analysis, we will halve the control group in each case to avoid double-counting.
Unit of analysis issues
Two review authors (BS and NH) will review unit of analysis issues according to guidelines described in Higgins 2011 and resolve differences by discussion. These include reports where:
groups of women were randomised together to the same intervention (i.e. cluster-randomised trials);
individual women underwent more than one intervention (e.g. in a cross-over trial);
there are multiple observations for the same outcome (e.g. repeated toxicity measurements).
Dealing with missing data
We will attempt to contact study authors to obtain missing data (participant, outcome, or summary data). For participant data we will, where possible, conduct analysis on an intention-to-treat basis; otherwise we will analyse data as reported. We will report on the levels of loss to follow-up and assess this as a source of potential bias. For missing outcome or summary data we will not impute missing data.
Assessment of heterogeneity
Where we consider studies are similar enough, based on consideration of populations and interventions, to allow pooling of data using meta-analysis, we will assess the degree of heterogeneity by visual inspection of forest plots. If heterogeneity is such that we consider pooling data unlikely to be clinically meaningful, we will not perform a meta-analysis and will instead use a narrative approach. In this event we will investigate and report the possible clinical or methodological reasons for substantial heterogeneity. Clinical markers of patient heterogeneity that we intend to extract from each study are as follows.
Number of previous regimens of chemotherapy (dichotomised 1 or 2; and ≥ 3)
FIGO stage (dichotomised I or II; and III or IV)
Performance status (dichotomised 0-2 or 3+)
Histology (dichotomised serous or non-serous)
Assessment of reporting biases
If we include 10 or more studies that investigate a particular outcome, we will examine funnel plots corresponding to meta-analysis of the outcome to assess the potential for small-study effects such as publication bias. We plan to assess funnel plot symmetry visually; and if asymmetry is suggested, we will perform exploratory analyses to investigate it.
If a sufficient number of 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 < 30%), we will pool their results in meta-analyses using the fixed-effect model in Review Manager 2014. If statistical heterogeneity is substantial (I² > 30%) 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 in Review Manager 2014.
For any dichotomous outcomes, we will calculate the risk ratio (RR) and 95% confidence interval (CI) for each study and these will then be pooled.
For continuous outcomes, we will pool the mean differences (MD) with a 95% CI 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 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 'paclitaxel' or 'docetaxel'; and 'weekly administration' or '3-weekly administration'. Depending on the assembled research, we may also explore the possibility of organising the data by our identified participant subgroups of 'platinum resistant' or 'platinum sensitive'; and 'taxane naive' or 'taxane pre-treated'. Within the data categories we will explore the main comparisons of the review.
Main outcomes of 'Summary of findings' table for assessing the certainty of the evidence
The review's main outcomes in order of priority are:
overall survival (OS);
progression-free survival (PFS);
neutropenia (Grade 3 to 4);
neurotoxicity (Grade 3 to 4);
quality of life.
We will present the overall certainty of the evidence for each outcome according to 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(Appendix 3) based on the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011); and using GRADEPro GDT. We will use the GRADE checklist and GRADE Working Group certainty of evidence definitions (Meader 2014). We will downgrade the evidence from 'high certainty' by one level for serious (or by two for very serious) for each limitation, as follows.
High certainty: we are very confident that the true effect lies close to that of the estimate of the effect.
Moderate certainty: 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 certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.
Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.
If meta-analysis is not possible we will present results in a narrative ‘Summary of findings’ table format, such as that used by Chan 2011.
Subgroup analysis and investigation of heterogeneity
We will perform subgroup analyses for the following factors: type of taxane; platinum-resistance status; and taxane pre-treatment status. We will consider factors such as age, FIGO stage, number of cycles of prior chemotherapy, performance status, histology, length of follow-up and risk of bias status in interpretation of any heterogeneity.
We will perform sensitivity analyses, excluding studies with a high risk of bias to determine the impact of these studies on the final outcome of the review.