Types of studies

We planned to include randomised controlled trials (RCTs) with open or blinded assessment of outcomes. We required full journal publication with the exception of extended abstracts of otherwise unpublished clinical trials. We excluded short abstracts (usually meeting reports), non‐randomised studies, studies of experimental pain, studies done on animal models, case reports, and clinical observational studies.

Types of participants

We included cachectic patients of 18 years and over with a histological or clinical diagnosis of cancer, or meeting any of the international criteria for cancer cachexia (Bozzetti 2009; Fearon 2006; Fearon 2011). We included both inpatients and outpatients with any type or stage of cancer irrespective of gender or race. We included patients in any healthcare setting (including hospice, hospital, oncology centre or community).

Types of interventions

We expected studies to vary in terms of form, dose, frequency, route and duration of treatment. We included studies in which ghrelin was administered in any form, at any dose, at any frequency, by any route and for any duration, administered for improving food intake, body composition and survival, compared to placebo or no treatment or any active comparator (such as appetisers, nutritional supplements, ghrelin analogues/ghrelin mimetics, ghrelin potentiators/enhancers, etc.). Studies examining ghrelin offered as a sole intervention or in combination with another intervention were eligible.

We had planned to undertake five comparisons. We added a sixth comparison group in this review: higher‐dose ghrelin versus lower‐dose ghrelin, as we found two studies addressing this. We thought it wiser to include this comparison rather than miss data on an intervention.

1. Ghrelin versus placebo

2. Ghrelin versus no treatment

3. Ghrelin versus alternative experimental treatment modality (like appetisers, nutritional supplements, etc.)

4. Ghrelin in combination with other treatments versus ghrelin treatment alone

5. Ghrelin treatment versus ghrelin analogues/ghrelin mimetics (anamorelin, ipamorelin, eganamorelin, hexarelin, MK‐677, etc.) or ghrelin potentiators/enhancers (rikkunshito)

6. Higher‐dose ghrelin versus lower‐dose ghrelin

Types of outcome measures

Electronic searches

We searched the following databases without language restrictions.

1. The Cochrane Central Register of Controlled Trials (CENTRAL; 2017, issue 6) in the Cochrane Library

2. MEDLINE (via Ovid) searched 1947 to 20 July 2017

3. Embase (via Ovid) searched 1974 to 20 July 2017

We used Medical subject headings (MeSH) or equivalent and text‐word terms. We obtained full‐text translations of all relevant non‐English articles and tailored the searches to individual databases. The search strategies used can be found in Appendix 1.

Searching other resources

We searched the metaRegister of controlled trials (mRCT) (www.controlled-trials.com/mrct), National Cancer Institute (www.cancer.gov/clinicaltrials), clinicaltrials.gov (www.clinicaltrials.gov), and the WHO International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) for ongoing trials in July 2017. We also searched ClinicalStudyResults.org (www.clinicalstudyresults.org) for clinical trials.

In addition, we checked the reference lists of reviews, retrieved articles for additional studies, and performed citation searches on key articles. We contacted study authors where necessary for additional information. We searched the British Association for Cancer Research (BACR), Society on Sarcopenia, Cachexia and Wasting Disorders (SCWD), the American Cancer Society. We contacted experts in the field for unpublished and ongoing trials to identify any additional literature related to the review.

Selection of studies

Two review authors (MNK, SG) independently screened the articles retrieved from the searches using the Rayyan online screening tool (Elmagarmid 2014) and determined eligibility by reading the abstract of each study identified by the search. Review authors eliminated studies that clearly did not satisfy inclusion criteria, and obtained full copies of the remaining studies. Two review authors (ZQS, AG) screened full texts of these studies independently to select relevant studies. We contacted study authors by email, if missing information impaired the study selection, to clarify the necessary information. In the event of disagreement, a third author adjudicated (AS). We did not anonymise the studies in any way before assessment. We applied no language restrictions in the selection of studies. We included a PRISMA flow chart in the full review that shows the status of identified studies (Moher 2009) as recommended in Part 2, Section 11.2.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011). We included studies in the review irrespective of whether measured outcome data are reported.

Data extraction and management

Two review authors (MNK, SG) independently extracted the data using a standard form and checked for agreement before entry into Review Manager 5 (RevMan 5) (RevMan 2014). We included information about all the primary outcomes. We collated multiple reports of the same study, so that each study rather than each report is the unit of interest in the review. We collected characteristics of the included studies in sufficient detail to populate a table of ‘Characteristics of included studies’.

Assessment of risk of bias in included studies

This section is taken from the PaPaS template for 'reviews'.

Two authors (MNK, PS) independently assessed risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a) and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion. We completed a 'Risk of bias' table for each included study using the 'Risk of bias' tool in RevMan 5 (RevMan 2014).

We assessed the following for each study.

• Random sequence generation (checking for possible selection bias). We assessed 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). We excluded studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number).

• 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 assessed 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).

• Blinding of participants and personnel (checking for performance bias). We assessed the methods used to blind study participants and personnel about the receipt of the intervention. We assessed the methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding); unclear risk of bias (study states that it was blinded but does not provide an adequate information of how it was done); high risk of bias (no blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding; or blinding of participants of the study and personnel was attempted, but it is likely that the blinding could have been broken).

• Blinding of outcome assessment (checking for possible detection bias). We assessed the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We assessed 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 blinding was achieved).

• Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data). We assessed 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); high risk of bias (used 'completer' analysis).

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

• Selective outcome reporting (checking for reporting bias). We assessed studies as being at low risk of bias (the study protocol is available; or the study protocol is not available but the study reported all expected and pre‐specified outcomes); high risk of bias (the study reported one or more outcomes of interest incompletely); unclear risk of bias (the study provides insufficient information to permit judgement of ‘low risk’ or ‘high risk’).

• Other bias. We assessed the study as: low risk of bias (the study appears to be free of other sources of bias); unclear risk of bias (there may be a risk of bias, but there is insufficient information to judge whether risk of bias exists; or insufficient evidence that a problem under consideration will introduce bias); or high risk of bias (there is at least one important risk of bias).

Measures of treatment effect

We planned to record number of events and total number of participants in both the arms for dichotomous variables. For continuous variables we planned to record means with standard deviations and total number of participants in both the arms. We planned to summarise each study in our meta‐analysis using risk ratio (RR) or odds ratio (OR) with 95% confidence intervals (CI) for dichotomous variables and mean difference (MD) with 95% CI for continuous variables, then pool these effect estimates in a meta‐analysis. For continuous data we planned to use mean differences (MD) with 95% CI when the results were measured in the same way in different studies. We planned to use standardised mean differences (SMD) when the results obtained were conceptually the same but used different measurement scales. We planned to use a fixed‐effect model or random‐effects model to estimate the overall direction, size and consistency of an effect and obtain the change in standard deviation from CI, standard errors, t values, P values or F values (whichever was available) using the RevMan 5 calculator. If there was not enough information available to calculate the standard deviations for the changes, we planned to impute the values of the same. If the required data were not available, we planned to use a comparison of final measurements. We planned to evaluate the direction and size of the effect as well as looking at the consistency of the effect across the selected studies. We planned to consider clinically meaningful change taking into account the change in weight and appetite with a measurable entity and time span.

Unit of analysis issues

In parallel‐group RCTs, we considered an individual participant as the unit of analysis. When incorporating cross‐over trials into a meta‐analysis, we would have followed the approach suggested by Elbourne (Elbourne 2002). We would have incorporated these trials by taking measurements from experimental intervention periods and measurements from control intervention periods and analysing these as if the trial were a parallel group trial of intervention versus control. If carry‐over was thought to be a problem, we would have included only data from the first period. We would have included the effect estimate of cross‐over trials in meta‐analysis using the generic inverse‐variance method.

Dealing with missing data

If enough studies were available; we would have carried out an intention‐to‐treat analysis. We asked for further information from the authors or manufacturers when published data were missing, incomplete or inconsistent with RCT protocols. We contacted authors by email if studies did not report the outcome measures of interest, did not describe randomisation or intention‐to‐treat analysis or had missing data.

Assessment of heterogeneity

We planned to assess clinical heterogeneity by using the Chi² test (P value < 0.10 for statistical significance) and use the I² statistic to quantify heterogeneity. We would have regarded heterogeneity as considerable if I² was more than 75%; substantial if it was between 50% and 90%; moderate if it was between 30% and 60% and mild if less than 40% (Deeks 2011). If we had identified statistical heterogeneity (I² greater than, or equal to 50%); we would have reported it and explored possible causes by prespecified subgroup analysis, and would have applied a random‐effects model.

Assessment of reporting biases

If there would have been 10 or more included studies; we planned to conduct a funnel plot test for asymmetry to assess for any evidence of reporting bias. Additionally; we had planned to explore the possible sources of asymmetry in a funnel plot.

Data synthesis

We planned to undertake a meta‐analysis only if participants, interventions, comparisons and outcomes were judged to be sufficiently similar to ensure an answer that is clinically meaningful and relevant. For analysis, we planned to use RevMan 2014, the statistical package provided by the Cochrane Collaboration.

If statistical heterogeneity (I² greater than, or equal to 50%) was detected, we would have identified the sources of the heterogeneity and would have performed subsequent meta‐analysis using a random‐effects model. When meta‐analysis seemed inappropriate, we did not pool the results of the included studies, but presented a qualitative description of these studies with supporting tables. We planned to perform a meta‐analysis using a fixed‐effect model if there were sufficient and homogeneous data with consistent or comparable outcomes.

‘Summary of findings' tables

We included 'Summary of findings' (SoF) tables as set out in the PaPaS author guide (AUREF 2012) and recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011). We have presented the SoF tables under the following comparisons for all of the primary outcomes:

1. Ghrelin versus placebo

2. Ghrelin versus an alternative experimental treatment modality

3. Ghrelin in combination with other treatments versus ghrelin treatment alone

4. Higher‐dose ghrelin versus lower‐dose ghrelin

Two review authors (ZQS, MNQ) assessed the overall quality of the evidence for each of the primary outcome using the GRADE system (GRADEpro GDT 2015) and presented the findings in the 'Summary of findings' tables. In particular, we included key information concerning the quality of evidence. We planned to include the magnitude of effect of the interventions examined, and the sum of available data on the main outcomes.

We decreased the grade rating if there was:

1. A serious (‐1) or very serious (‐2) limitation to study quality;

2. Important inconsistency (‐1);

3. Some (‐1) or major (‐2) uncertainty about directness;

4. Imprecise or sparse data (‐1);

5. High probability of reporting bias (‐1).

We have justified all decisions to downgrade the quality of studies using footnotes.

Subgroup analysis and investigation of heterogeneity

We planned to undertake subgroup analyses for form, dose, duration and route of administration of ghrelin, and for different types of cancer.