Types of studies

We will review prospective studies to evaluate the diagnostic potential of oral water soluble contrast (OWSC) in predicting which malignant small bowel obstructions will resolve with conservative treatment.

To review the therapeutic potential of OWSC in managing malignant bowel obstruction (MBO) at any level we will look at randomised controlled trials. If no randomised controlled trials are found, relevant prospective controlled studies will be discussed but not included in a meta‐analysis.

Types of participants

Adult patients (aged 18 and over) who meet the criteria for MBO as listed above where the obstruction is limited to the small bowel only (diagnostic).

Adult patients (aged 18 and over) who meet the criteria for MBO listed above and where surgery or endoscopic stenting are not appropriate, or with malignant small bowel obstruction who are having a trial of conservative management before a decision on surgery/stenting is made (therapeutic).

Types of interventions

1. The administration of oral water soluble contrast (OWSC) in patients with the diagnosis of malignant small bowel obstruction followed by interval abdominal radiographs to identify contrast in the colon (diagnostic).

2. The administration of OWSC to patients with MBO to assess its ability to resolve the obstruction.

Comparison:

• Placebo;

• No intervention;

• Usual treatment or supportive care.

Types of outcome measures

We will include a 'Summary of findings' table as set out in the PaPaS author guide (AUREF 2012) and recommended in the Cochrane Handbook, chapter 4.6.6 (Higgins 2011). The 'Summary of findings' table will include the primary and secondary outcomes listed below. For each outcome, the overall quality of the evidence will be assessed using the GRADE system (GRADEpro 2015) and also presented in the 'Summary of findings' table. The assessment will be focused on the quality of available evidence, the magnitude of the effect of using OWSC and the sum of available data on the main outcomes. See Appendix 1 for a further description of the GRADE system.

Electronic searches

We will search the following electronic databases:

1. The Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library);

2. MEDLINE (Ovid);

3. EMBASE (Ovid);

4. CINAHL;

5. Science Citation Index (Web of Science);

6. Conference Proceedings Citation Index ‐ Science (Web of Science).

Medical subject headings (MeSH) or equivalent and text word terms will be used. The search strategy for MEDLINE (Ovid) can be seen in Appendix 2. The MEDLINE search strategy suggested by the main author was revised and adapted by the Trials Search Coordinator of the Cochrane Pain, Palliative and Supportive Care Review Group. The Cochrane Highly Sensitive Search Strategy filter for identifying randomised trials in MEDLINE via Ovid (Lefebvre 2008) was also applied. This search will be adapted and modified across the other databases.

Searching other resources

The bibliographic references of any relevant identified studies will be checked in order to find additional trials not identified by the electronic searches. We will also search clinicaltrials.gov (www.Clinicaltrials.gov), the metaRegister of Controlled Trials (mRCT) (www.controlled‐trials.com/mrct/), and the WHO International Clinical Trials Registry Platform (ICTRP) (http://apps.who.int/trialsearch/) to identify any ongoing trials. For grey literature, we will search the Internet using the Google scholar search engine (www.googlescholar.com) and CareSearch Grey Literature databases (http://www.caresearch.com.au) with selected terms from the above strategy.

If only abstracts are identified and no full‐text paper can be retrieved, the study authors will be contacted for further details. We will also attempt to contact authors in the case of incomplete data sets.

The searches will be conducted by the Trials Search Coordinator of the Cochrane Pain, Palliative and Supportive Care Review Group.

Selection of studies

All titles and abstracts of the studies identified by the searches will be independently assessed by at least two of the review authors. Each of these authors will independently select all potentially‐relevant studies by applying the selection criteria outlined in the Criteria for considering studies for this review. Studies meeting the criteria will be included in the review irrespective of whether measured outcome data are reported in a 'usable way'. The authors' selections will then be compared, and any differences discussed and the papers either included or excluded based on a majority decision.

A PRISMA study flow diagram (Liberati 2009) will be included in the full review to document the screening process, as recommended in Part 2, Section 11.2.1 of the Cochrane Handbook (Higgins 2011).

Data extraction and management

For each study at least two review authors will independently extract data using a piloted data extraction form. Data extracted will include information about the year of study, study design, number of participants treated, participant demographic details, type of cancer, drug and dosing regimen, study design (placebo or active control) and methods, study duration and follow‐up, outcome measures (reduction in duration of obstruction, length of stay, likelihood of resolution if contrast reaches colon), withdrawals and adverse events. In studies with more than two intervention arms, this review will only include the intervention and control groups that meet the eligibility criteria. Multi‐arm studies included in the review will have their multiple intervention groups analysed in an appropriate way to avoid arbitrary omission of relevant groups and double‐counting of participants. We will resolve potential disagreements by discussion and majority decision.

Assessment of risk of bias in included studies

The studies will be divided among the author group so that two authors will independently assess the risk of bias for each study. This will be done using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion. We will complete a 'Risk of bias' table for each included study using the 'Risk of bias' tool in RevMan (RevMan 2014). We will assess the following for each study.

Random sequence generation (checking for possible selection bias). We will assess the method used to generate the allocation sequence as: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). Studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number) will be deemed to be at high risk of bias and excluded.

Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated). Studies that do not conceal allocation (e.g. open list, date of birth or any other explicitly unconcealed procedure) will be deemed to be at high risk of bias and excluded.

Blinding of participants, personnel (checking for possible performance bias). We will assess studies as low risk of bias if they adequately describe how the blinding of key study participants and personnel has been assured. Studies will be assessed as high risk of bias if there was no blinding or incomplete blinding which may impact on the assessment of adverse effects from OWSC. An assessment of unclear risk of bias will apply to studies where there is insufficient information to permit judgement of 'high' or 'low' risk.

Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, e.g. identical tablets; matched in appearance and smell); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved). Studies where there was no blinding of outcome assessment or where the blinding may have been broken which may affect outcome measurements (particularly adverse effects of OWSC) will be deemed high risk of bias and excluded.

Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data). We will assess the methods used to deal with incomplete data as: low risk (< 10% of participants did not complete the study and/or used ‘baseline observation carried forward’ analysis); unclear risk of bias (used 'last observation carried forward' analysis); or high risk of bias (used 'completer' analysis).

Selective reporting (checking for reporting bias). We will assess studies as being at low risk of bias (all of the relevant pre‐specified outcomes listed in the protocol and reported in the pre‐specified way); high risk of bias (one or more outcomes of interest are reported incompletely so that they cannot be entered in a meta‐analysis); or unclear risk of bias (insufficient information to permit judgement of 'high risk' or 'low risk').

Size of study (checking for possible biases confounded by small size). We will assess studies as being at low risk of bias (≥ 200 participants per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); or high risk of bias (<50 participants per treatment arm).

Measures of treatment effect

For dichotomous outcomes between groups, we will estimate and compare the risk ratio (RR) using a 95% confidence interval (CI). For continuous outcomes between groups, we will measure arithmetic means and standard deviation (SD) and will report the mean difference (MD) with 95% CI. When an outcome is derived with different instruments measuring the same construct, we will use standardised mean difference (SMD) with 95% CI.

For unwanted effects, we will calculate the numbers needed to treat to harm (NNH) using dichotomous data to calculate RR with 95% CI. We will use the following terms to describe adverse outcomes in terms of harm or prevention of harm:

• When significantly fewer adverse outcomes occurred with oral water soluble contrast than with control (placebo or active) we will use the term 'number needed to treat to prevent one event' (NNTp).

• When significantly more adverse outcomes occurred with water soluble contrast compared with control (placebo or active) we will use the term 'number needed to harm or cause one event' (NNH).

Unit of analysis issues

We will only include studies in which randomisation is by the individual patient; this will include cross‐over or n = 1 studies.

Dealing with missing data

In cases where data are missing, we will contact the authors to request the missing data. Intention‐to‐treat (ITT) analysis will be used. Missing participants or information will be assigned to a zero improvement category where possible. The method of assessing data processed from withdrawals will be ascertained where possible. Where there are substantial numbers (> 10%) of participants missing from analyses, we will perform sensitivity analyses.

Assessment of heterogeneity

We will undertake a meta‐analysis only if participants, interventions, comparisons and outcomes are judged to be sufficiently similar to ensure an answer that is clinically meaningful. There may be an effect of differences between patients, level of obstruction (small bowel versus large bowel) and outcome measures. We will assess heterogeneity by using the I² statistic. We will consider I² values above 50% to represent substantial heterogeneity in line with Higgins 2011, and will assess potential sources of heterogeneity through subgroup analyses.

Assessment of reporting biases

If there are at least 10 studies in the meta‐analysis we will assess the likelihood of publication bias by examining funnel plot symmetry to interpret the results of statistical analysis. If there is evidence of small study effects, we will consider publication bias as only one of a number of possible explanations (Higgins 2011).

Data synthesis

We will enter the data extracted from the included studies into Review Manager software (RevMan 2014) which will be used for data synthesis. Where appropriate, we will pool data for each dichotomous outcome and calculate risk ratios with 95% CI using the fixed‐effect model, together with numbers needed to treat for an additional beneficial outcome (NNTBs) with 95% CIs and, for adverse events, numbers needed to treat for an additional harmful outcome (NNTHs) with 95% CIs.

Subgroup analysis and investigation of heterogeneity

If sufficient data are available, we will perform the following subgroup analyses:

1. Level of obstruction (small bowel or large bowel)

2. Degree of obstruction (partial or complete)

3. Dose of OWSC used

4. Timing of follow‐up abdominal x ray (diagnostic)

5. Type of cancer

Sensitivity analysis

When sufficient data are available, we will examine the robustness of the meta‐analyses by conducting sensitivity analyses using different components of the 'Risk of bias' assessment, particularly those relating to whether allocation concealment and patient/assessor blinding were adequate. We will conduct further sensitivity analyses to examine the impact of missing data on the results as a large proportion of the studies are at an ‘unknown’ or ‘high risk’ of attrition bias, and finally, to examine whether publication status and trial size influenced the results.