Types of studies

We will consider randomised controlled trials (RCTs) that assess the effect of intermittent systemic therapy versus continuous systemic therapy for inclusion. We will include cluster‐RCTs and crossover randomised designs: however, it is unlikely that these designs are used in trials that assess this clinical question. There will be no minimum follow‐up period. We will consider abstracts if sufficient information and data will be available to analyse any of the outlined outcomes of this review.

Types of participants

Male and female adults (≥ 18 years) with unresectable metastatic colorectal cancer (CRC) (TNM stage¹ IV) T1‐4, N0‐3, M1 (NCCN 2014).

¹The TNM staging system for solid tumours uses the size and extension of the primary tumour (T), its lymphatic involvement (N) and the presence of metastases to classify the progression of cancer (M).

Types of interventions

Every intermittent treatment schedule starts with induction chemotherapy. Intermittent therapy in this study is defined as stopping or changing maintenance therapy after initial cycles of chemotherapy and then restarting with any kind of therapy at any point in time. There will be no restrictions regarding type of systemic therapy, as long as the regimes are compliant with this definition. We will consider the comparison between intermittent and continuous chemotherapy independently of the line of therapy.

We will include studies that use any of the four following basic strategies of intermittent therapy:

• intermittent chemotherapy with Fluorouracil (5FU) maintenance therapy;

• intermittent chemotherapy with no maintenance therapy (chemotherapy‐free interval);

• intermittent chemotherapy with biologicals as maintenance therapy;

• intermittent chemotherapy plus intermittent targeted therapy.

Apart from different options in treatment strategies, there are also differences in the length of the interval depriving the patient of therapy. Intermittent therapy can be restarted at progression of disease or at a set point in time. Progression of disease is defined as when the cancer continues to grow or spreads, preferably defined according to the Response Evaluation Criteria In Solid Tumours (RECIST) criteria (Eisenhauer 2009). We will include trials regardless of the duration of the interval.

Continuous systemic therapy can be chemotherapy, targeted therapy or other novel agents. We will select studies for inclusion regardless of the treatment dose, delivery, duration or intensity. We will allow therapy at initial diagnosis or concomitant therapy in the included studies provided that this is equally distributed across all arms of the included trial. Examples of therapy schemes can be found in Table 1. Additional treatments can be of any kind, e.g. best supportive care, radiotherapy or interventional radiological techniques.

We will not use any restrictions regarding RECIST criteria use or grading of toxicity/adverse events. We will use this as described by the trial authors.

Types of outcome measures

For patients with unresectable metastatic CRC, we will compare intermittent systemic therapy with continuous systemic therapy in terms of survival (using a non‐inferiority approach) and side effects (using a superiority approach).

Electronic searches

We will search the following databases to identify studies that meet the inclusion criteria:

• CENTRAL (the Cochrane Central Register of Controlled Trials, the Cochrane Library) (Appendix 1);

• MEDLINE (via Ovid SP) (Appendix 2);

• Embase (via Ovid SP) (Appendix 3);

• PsychInfo.

The CCCG Information Specialist will design the literature search strategy, which the review authors (MF, YC, EB and EK) will provide input on. We will not apply any date or language restrictions. We will not exclude studies based on publication status. We will examine relevant errata or retraction statements for information.

We will search the ClinicalTrials Website (https://clinicaltrials.gov/) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (www.who.int/ictrp/en/) for ongoing trials.

We will search for additional studies by screening the bibliographies of all retrieved and relevant publications identified by the above search strategies. Also we will search for additional trials through the Cochrane specialist register. We will search the grey literature, including conference abstracts and guidelines.

The literature search will be rerun within 12 months of publication of the Cochrane Review.

Searching other resources

We will screen all references of retrieved eligible studies for relevant studies. We will also scan previous reviews on this topic for relevant studies.

Selection of studies

Two review authors (MF and YC) will independently screen the titles and abstracts of all articles we identify in the literature searches, and will code them as either 'retrieve' or 'do not retrieve'. The two review authors will resolve any discrepancies by discussion. In the case of disagreement, we will consult a third review author (EK) in order to reach a consensus on titles and abstracts. We will retrieve the full‐text papers of articles where we consider the titles and abstracts to be relevant or where eligibility is unclear. Two review authors (MF and YC) will independently assess these articles for inclusion and will resolve any discrepancies by discussion. In case of disagreement, we will consult a third review author (EK).

We will contact the study authors in case the information we require for meta‐analysis is not sufficiently reported. We will collate multiple reports of one study and we will indicate a primary data source. In the case of a multiple‐arm study, of which not all arms assess the treatment of interest, we will only consider study arms that compare continuous versus intermittent systemic therapy. As the included trials must be randomised, this will not disturb the baseline characteristics of the study population.

We will present the study selection process in a PRISMA flow chart (Figure 1). We will list the excluded studies and their reasons for exclusion in a 'Characteristics of excluded studies' table. We will include studies irrespective of whether the study presents outcome data. We will use Covidence software for reference handling (Covidence 2013).

Figure 1

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Study flow diagram.

Data extraction and management

Two review authors (MF and YC) will independently extract data from the included studies. We will pilot test the data extraction form first.

The data collection form will contain the following items.

• General information: study title, study author(s), source, publication date, contact address, language, funding sources and author declaration(s) of interest;

• Study characteristics: number, age, gender, site of metastatic disease, whether or not participants received previous adjuvant systemic therapy (in curative setting), site of primary tumour (colon or rectum), performance status (if available), how resectability was measured, method of chemotherapy administration, dosage and duration of the intervention, moment of restart of intermittent therapy, how progression was measured, type of quality of life measurement scale, type of toxicity measurement scales, toxicities, details of comparison regimen, number of participants that dropped out or that were lost to follow‐up;

• Outcomes: overall survival, toxicities, progression‐free survival and quality of life.

We will check both the magnitude and the direction of the effect size reported by the included studies to ensure that we do not include any incorrect values in the pooled analysis. We will resolve any disagreements regarding data collection by consulting a third review author (EK). We will use Covidence software for data extraction (Covidence 2013).

Assessment of risk of bias in included studies

Two review authors (MF and YC) will assess and discuss the following methodological 'Risk of bias' domains according to the Cochrane 'Risk of bias' assessment tool (Higgins 2011, chapter 8.5.d), using Covidence software (Covidence 2013).

• sequence generation;

• concealment of treatment allocation;

• blinding of participants and personnel;

• blinding of outcome assessment (in this case partly only secondary objectives, primary objective cannot be blinded);

• incomplete outcome data;

• selective outcome reporting;

• other potential threats to validity (considering external validity, e.g. relevant use of co‐interventions in both study arms, or selection of specific patient groups).

We will judge each domain as either at low risk, high risk or unclear risk of bias according to criteria used in the Cochrane ‘Risk of bias’ assessment tool (see Appendix 4) (Higgins 2011a, chapter 8.5.d).

We will obtain support for our judgements from reports, personal correspondence and previous comparable trials from the same research team.

Measures of treatment effect

For time‐to‐event data (e.g. progression‐free survival and overall survival), we will calculate the hazard ratios (HR) and their 95% confidence intervals (CI) for each trial. If no HRs are reported, we will extrapolate them from the reported Kaplan‐Meier curves (Parmar 1998).

For dichotomous variables (e.g. toxicity rates), we will calculate relative ratios (RR) and their 95% Cl.

For continuous outcomes (e.g. quality of life measurements), we will use mean differences (or standardised mean differences if results are expressed on different scales) along with their 95% CI as summary statistic in meta‐analyses.

We will check the magnitude and direction of the effect size reported to ensure we avoid errors.

When possible, we will pool summary data for dichotomous, continuous and time‐to‐event outcomes obtained by means of meta‐analysis using a random‐effects model (DerSimonian 1986).The estimation of between study heterogeneity might be inaccurate when we identify a small number of trials for inclusion and the random‐effects model might be biased. If the number of included trials is lower than 10, we will also perform a meta‐analysis using a fixed‐effect model. We will use the inverse variance method to run both the fixed‐effect and random‐effects model.

Unit of analysis issues

For parallel group individually randomised trials, the unit of analysis will be the individual patient.

We do not expect to find either cross‐over RCTs or cluster‐RCTs. However, in case we identify cluster RCTs or crossover trials that meet the inclusion criteria of this review, we will handle unit of analysis issues.

Dealing with missing data

We will contact the study authors by e‐mail or telephone to retrieve any missing information concerning missing or dropout data. If we do not receive a reply from the study authors, we will consider both the best‐case and worst‐case scenarios for dropouts.

Assessment of heterogeneity

We will assess the level of heterogeneity between the included studies using the Chi² test (P < 0.05). We will quantify the level of heterogeneity between studies using the I² statistic. We will present data in a qualitative analysis if there is heterogeneity. We will interpret the I² statistic value according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c, chapter 9.5.2).

We will not pool data if heterogeneity is high (i.e. if the I² statistic value is greater than 75%). We will investigate potential sources of between‐study heterogeneity by means of subgroup analysis (see Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

We will present a funnel plot for the detection of potential reporting bias if we analyse more than 10 studies. We will check these against the protocols, if available, and compare the outcomes reported with those planned.

Data synthesis

Regarding the toxicity endpoint, the interpretation of the results will follow the usual superiority (or inferiority) approach: that is, in the intermittent versus continuous schedule comparison, a summary relative risk of less than one with the CI not crossing the null value (i.e. one) will mean that the intermittent schedule is associated with a significantly lower toxicity rate. We will use an alpha level of 5% as a level of significance.

In contrast, when we will interpret the survival findings, we will use a non‐inferiority analysis (D'Agostino 2003). In the intermittent versus continuous schedule comparison we do not need the former to be better in terms of efficacy, but we do need to assess whether the former can be considered equivalent to the latter in terms of expected patient survival. This can be done by setting a margin, that is, the maximum acceptable impairment/reduction in efficacy observed in patients undergoing the experimental treatment as compared to those undergoing the reference treatment. In other words, the margin is the maximum value of the effect difference between experimental and control treatment that can be acceptable to still consider the former non‐inferior to the latter. For the present study, we will consider a margin of 20%: in other words the CI of the summary HR (resulting from the intermittent versus continuous schedule comparison) should not cross the value of 1.2 for the experimental schedule to be considered non‐inferior to the reference schedule.

We chose the 20% margin based on the clinical (and ethical) consideration that an experimental treatment could be of clinical value if it is less toxic than the comparator treatment and if its efficacy is not worse than the comparator by more than 20%, a margin often used in the oncology field (especially in the metastatic setting, where even larger margins are often accepted) (Hong 2012; Hu 2015; Muro 2010; Tsuburaya 2014; Yamada 2013). Moreover, the conclusion of a recent meta‐analysis on the same subject further justifies the use of this margin as the difference between the two treatments was lower than the margin we chose (Berry 2015). The constancy assumption for non‐inferiority approach is likely to be met because, to the best of our knowledge, we have no reason to believe that over time changes have occurred in disease or outcome which could negatively have affected the choice of the margin.

We have presented a schematic on how to interpret all possible results of the meta‐analysis in the non‐inferiority perspective in Figure 2.

Figure 2

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Non‐inferiority interpretation of meta‐analysis findings

Intention‐to‐treat (ITT) analysis is usually considered as an unbiased approach for superiority trials. However, ITT analysis may not be conservative in the case of non‐inferiority trials (inclusion of dropouts tends to bias the findings toward equivalence). Accordingly, we will retrieve data from both ITT and per‐protocol analysis; then we will assess the impact of the type of analysis (or the lack of such a type of information) by means of sensitivity analysis. Regarding the ITT analysis, for dropouts we will consider the best‐case and worst‐case scenarios. We will retrieve data from both the ITT and per‐protocol analysis, and then we will assess the impact of the type of analysis by means of sensitivity/subgroup analysis. We will determine the impact of the type of analysis by means of sensitivity/subgroup analysis. Regarding toxicity, we will consider best‐case and worst‐case scenarios in the analyses.

We will enter survival data (HRs and corresponding CI) directly in RevMan when reported (RevMan 2014); when unavailable, we will extrapolate them from Kaplan‐Meier survival curves using dedicated methods (Parmar 1998; Tierney 2007).

If the included studies report continuous outcomes using different scales, we will ensure that higher scores have the same meaning for any particular outcome; furthermore, we will report in which cases the effect direction will be reversed to guarantee consistency across results and thus to correctly pool the data.

Subgroup analysis and investigation of heterogeneity

In order to investigate the potential sources of heterogeneity, we will consider the following pre‐specified subgroups (also see Figure 3): a subgroup of studies where the arm of intermittent chemotherapy has:

Figure 3

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Planned subgroup analysis

• no maintenance therapy (therapy‐free interval); versus

• has any (simplified) form of systemic therapy (after induction chemotherapy)

Within these subgroups, our interpretation of the results in terms of survival will follow the non‐inferiority design described in the above paragraph.

Sensitivity analysis

We will use sensitivity analysis to assess the robustness of the meta‐analysis findings. To achieve this we will investigate whether exclusion of lower quality trials or exclusion of trials reporting per‐protocol analysis results (or not reporting the type of analysis) changes the results of our meta‐analysis. Moreover, we will use sensitivity analysis by excluding trials with specific trial characteristics (e.g. cluster‐RCTs, crossover trials and differences in between studies regarding the moment of randomisation) to assess whether specific trial features (e.g. design) might affect heterogeneity. If this is the case, the interpretation of results in terms of survival will follow the non‐inferiority design described in the above paragraph.