Criteria for considering studies for this review
Types of participants
Children aged five to 18 years old with RAP or a abdominal pain-related functional gastrointestinal disorder defined by the Rome III criteria.
RAP is defined as at least three episodes of pain interfering with normal activities within a three month period. The Rome III criteria recognises four abdominal pain-related categories: "abdominal migraine", "irritable bowel syndrome", "functional dyspepsia", "functional abdominal pain", and "functional abdominal pain syndrome" (Rasquin 2006).
Types of interventions
Any dietary intervention compared to placebo, waiting list, no treatment or standard care.
Types of outcome measures
Pain intensity, duration or frequency.
There is no standard method for measuring pain in this condition. Studies may use any validated measurement of pain, and may report the proportion of participants with significant improvement in pain, as defined by the trial author. We expect studies to vary in their duration of post-intervention follow-up. Therefore we will group studies according to duration of follow-up: immediate outcome measurement, short term (less than three months), medium term (three to 12 months), and long term (greater than 12 months).
As measured by a validated tool:
We will present all outcomes in a 'Summary of findings' table.
Search methods for identification of studies
We will search the following electronic databases for relevant studies:
We will adapt the following search strategy for Ovid MEDLINE for other databases as listed above. The search terms have been revised from the original Cochrane RAP reviews (Huertas-Ceballos 2008a; Huertas-Ceballos 2008b; Huertas-Ceballos 2009); therefore searches will be run for all available years. We will use RCT filters where appropriate and no language limits will be imposed. We will translate any non-English language studies found in order to be screened and considered for inclusion.
14 Non specifi$.tw.
18 1 or 2 or 3 or 4 or 5 or 6 or 7 or 8 or 9 or 10 or 11 or 12 or 13 or 14 or 15 or 16 or 17
19 exp Recurrence/
20 18 or 19
21 ((pain$ or Ache$ or Sore$ or Discomfort$ or Distress$ or Cramp$ or Disorder$1 or Symptom$1 or Migraine$1 or Epilep$ or syndrome$1 or colic$) adj3 (stomach$ or abdom$ or intestin$ or viscera$ or tummy or bowel$ or belly or gastrointestinal or gi or gastric)).tw.
22 exp Colic/
23 exp Irritable Bowel Syndrome/ or exp Colonic Diseases, Functional/
24 exp abdominal pain/ or exp dyspepsia/
25 Colonic disease$.tw
27 Functional dyspepsia.tw.
28 irritable bowel$.tw.
29 exp Abdomen, Acute/
30 22 or 23 or 24 or 25 or 26 or 27 or 28 or 29
31 21 or 30
32 20 and 31
33 randomized controlled trial.pt.
34 controlled clinical trial.pt.
38 drug therapy.fs.
42 33 or 34 or 35 or 36 or 37 or 38 or 39 or 40 or 41
43 exp animals/ not humans.sh.
44 42 not 43
45 exp Child/
46 exp Adolescent/
47 exp Young Adult/
48 exp Students/
51 Young person$.tw.
56 Young adult$.tw.
62 45 or 46 or 47 or 48 or 49 or 50 or 51 or 52 or 53 or 54 or 55 or 56 or 57 or 58 or 59 or 60 or 61
63 32 and 44 and 62
Searching other resources
We will use the Science Citation Index to locate relevant studies using the bibliographic details, and authors' names of relevant papers for forward and backward citations.
We will contact researchers who have published studies in this field to ask for details of any relevant trials.
We will also check the bibliographies of papers retrieved to establish if all pertinent references were found in our search.
Data collection and analysis
Selection of studies
Two authors (AM, TN, RA or AB) will independently screen the titles and abstracts of studies for relevance. We will obtain the full-text articles for all the possible papers and then select them for inclusion against the agreed inclusion criteria. Any disagreements will be resolved through discussion with a third review author (JTC).
Data extraction and management
Two review authors (AM, TN, RA, AB or JTC) will extract data and enter them into the Cochrane Collaboration's statistical software, Review Manager 2013. All review authors will use the same data extraction form. We will collect the following data.
Study characteristics: number of participating patients, inclusion and exclusion criteria, type of intervention and comparison, intervention characteristics (duration, frequency, setting), number of withdrawals.
Participant characteristics: sex, age, diagnosis (for example, recurrent abdominal or syndrome defined by the Rome III criteria).
Outcome measures: measurement of pain and any secondary outcome measured.
Assessment of risk of bias in included studies
We will assess risk of bias in included studies under the following domains:
selection bias (random sequence generation and allocation concealment);
performance bias (blinding of participants and personnel);
detection bias (blinding of outcome assessment);
attrition bias (incomplete outcome data);
reporting bias (selective reporting);
other sources of bias.
Two review authors (AM, TN, RA, AB or JTC) will independently assess each study. We will classify the risk of bias as "low risk", "high risk" or "unclear risk" in line with the methods detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) (Table 1).
Table 1. Assessment of risk of bias in included studies
| Domain|| Risk of bias judgement|
| Low|| High|| Unclear|
|Selection bias |
| Random sequence generation||If the study details any of the following methods: simple randomisation (such as coin-tossing, throwing dice or dealing previously shuffled cards, a list of random numbers, or computer generated random numbers) or restricted randomisation: blocked, ideally with varying block sizes or stratified groups, provided that within groups randomisation is not affected.||If the study details no randomisation or other inadequate method such as alternation, assignment based on date of birth, case record number, and date of presentation. These may be referred to as ‘quasi-random’.|
If there is not sufficient detail to judge the risk of bias.
| Allocation concealment||If the study details concealed allocation sequence in sufficient detail to determine that allocations could not have been foreseen in advance of or during enrolment.||If the study details a method where the allocation is known prior to assignment.||If there is not sufficient detail to judge the risk of bias. |
|Performance bias |
| Blinding of participants and personnel||If the study details a method of blinding the participants and personnel. This requires sufficient detail to show they were unable to identify the therapeutic intervention from control intervention.||Considering the nature of the interventions, the participants and therapists may not be able to be blinded. The effect of this will be addressed in the discussion.||If there is not sufficient detail to judge the risk of bias.|
|Detection bias |
| Blinding of outcome assessment||If the study details a blinded outcome assessment. This may only be possible for outcomes that are externally assessed.||If the outcome assessment is not blinded. We expect this may be unavoidable for self-rated outcomes of unblinded interventions.|
If there is not sufficient detail to judge the risk of bias.
| Incomplete outcome data||If the study reports attrition and exclusions, including the numbers in each intervention group (compared with total randomised participants), reasons for attrition or exclusions, and any re-inclusions. And the impact of missing data is not felt to alter the conclusions, and there are acceptable reasons for the missing data.||We may judge the risk of attrition bias to be high due to the amount, nature or handling (such as per-protocol analysis) of incomplete outcome data.||If there is not sufficient detail to judge the risk of bias. For example, if the number of people randomised to each treatment is not reported.|
| Selective reporting||If there is judged to be complete reporting, this will be found on comparison of the protocol and published study, if available.||If the reporting is selective, so some outcome data is not reported.||If there is not sufficient detail to judge the risk of bias, such as protocols not available.|
We will assess all included studies for other sources of bias that may alter the estimate of treatment effect, for example, differential loss to follow-up. In cross-over studies it should be clear that the order of receiving treatments was randomised. There should be no assumed carry-over effects and, therefore, an adequate wash-out period. All the data should be available at the baseline, and before and after changing treatments; caution is required as although RAP is a chronic condition, most patients do improve with time (risk of period effects).
We will consider a trial as having an overall low risk of bias if most of the above domains are assessed as a low risk of bias. We will consider a trial as having an overall high risk of bias if several of the above domains are assessed as high risk of bias or unclear risk of bias.
We will use the Grading of Recommendations, Assessment, Development, and Evaluation (GRADE) approach to assess the overall quality of the body of evidence for a specific outcome (Higgins 2011). This will involve a consideration of within-study risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias. This study includes RCTs only. Although RCTs will begin as high quality evidence, they will be downgraded if most of the evidence comes from studies with a high risk of bias.
Measures of treatment effect
Our study results may be reported as:
continuous data (that is, number of days of pain), for which we will analyse by means and standard deviations if available or can be calculated, and if there is no clear evidence of skewness in the distribution. If different scales are used to measure the same clinical outcome, we will combine standardised mean differences (SMDs) across the studies.
dichotomous data (that is, pain improved, yes or no), which will be analysed using odds ratios (ORs).
Unit of analysis issues
If the following three types of trials are found, we will consider their results using the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
1. Cross-over trials
For cross-over trials with random allocation to period and an appropriate washout period, we will include the relevant effect estimate within the meta-analysis using the generic inverse variance method in Review Manager 2013. An appropriate washout period will vary with the interventions (including drug pharmacokinetics) and outcome measurements. Considering RAP can be a stable and chronic condition, a washout period of several weeks may be sufficient.
Cluster-randomised trials randomise groups of people rather than individuals. For each cluster-randomised trial, we will first determine whether or not the data incorporate sufficient controls for clustering (such as robust standard errors or hierarchical linear models). If data do not have proper controls, then we will attempt to obtain an appropriate estimate of the data's intracluster correlation coefficient (ICC). If we cannot find an estimate in the report of the trial, we will request an estimate from the trial report authors. If the authors do not provide an estimate, if possible, we will obtain one from a similar study and conduct a sensitivity analysis to determine if the results are robust when different values are imputed. We will do this according to procedures described in Higgins 2011. This process will prevent the meta-analysis from being based on clustered data that have not been properly controlled.
3. Trials with multiple intervention groups
This is a common scenario. To avoid any unit-of-analysis errors in the meta-analysis, we will take the following approach for a study that could contribute multiple comparisons.
The interventions will only be analysed together if they are clinically similar, that is equivalent dietary interventions (such as eliminating or supplementing the same food group). In this situation the control group will not be split, but the intervention groups will be combined to enable a single pair-wise comparison for the meta-analysis. If the interventions are similar enough to be in a single meta-analysis but not able to be combined, then the control group will be split.
If the interventions are not similar, the data will be used in separated meta-analyses. So a single study may contribute data to different meta-analyses (for example if the interventions involved eliminating different food groups) and this does not require the control group to split.
We will not perform a multiple treatment meta-analysis as the clinical heterogeneity will make the results uninterpretable.
Dealing with missing data
In the first instance, we will contact the original investigators to request any missing data. If it is not possible to obtain the data from the original investigators, we will not impute values. A sensitivity analysis may be carried out to establish if inclusion of studies with high levels of missing data significantly alters the finding of the review. If there are proportions of participants for whom no outcome data are obtained, we will report them as a source of bias as described above. We will explore the potential impact of missing data on the findings of the review in the 'Discussion' section.
Assessment of heterogeneity
We anticipate finding considerable heterogeneity between included studies. We will assess clinical heterogeneity by examining the distribution of relevant participant characteristics (for example, age, definition of RAP) and study differences (for example, concealment of randomisation, blinding of outcome assessors, interventions or outcome measures). We will describe statistical heterogeneity (observed variability in study results that is greater than that expected to occur by chance) by calculating I2 (Higgins 2003). I2 describes approximately the proportion of variation in point estimates due to heterogeneity rather than sampling error. I2 more than 50% may indicate significant heterogeneity.
We will use Chi2 test to further assess the strength of evidence for the heterogeneity. Any result with a P value lower than 0.10 will be regarded as indicating significant statistical heterogeneity. We will interpret this cautiously and use it to help quantify the impact of heterogeneity on the results of the meta-analysis (Higgins 2003).
Assessment of reporting biases
If we identify sufficient trials (at least 10), outcome data will be used to produce a funnel plot to investigate the likelihood of overt publication bias (Sutton 2000). Any asymmetry of the funnel plot may indicate possible publication bias. We will explore other reasons for asymmetry such as poor methodological quality or heterogeneity. We could also look for publication bias by comparing the results of the published and unpublished data.
Outcome reporting bias
We will examine reports of a study to assess for selective outcome reporting. The study will be assessed as adequate if it meets the following criteria:
the study protocol is available and all of the study's pre-specified (primary and secondary) outcomes that are of interest to the review have been reported in the pre-specified way;
the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre-specified.
We will use Review Manager 2013 for statistical analysis. Two review authors (AM, TN, RA, AB or JTC) will enter data into Review Manager 2013 independently. We will report summary statistics for continuous data as mean differences (MDs) or SMDs using a random-effects model. For dichotomous data, we will calculate the ORs using a random-effects model. We will use a random-effects model as we anticipate significant statistical and clinical heterogeneity.
A meta-analysis will only be carried out if it is appropriate to do so, that is, if the studies are sufficiently homogeneous. We will thus only carry out a meta-analysis using data from studies with equivalent dietary interventions, for example excluding the same food group. We are aware that given the heterogeneity of the dietary manipulations investigated for RAP and the variety of methods to measure pain, a meta-analysis may not be possible (DerSimonian 1986). In that case, we will provide a narrative description of the results.
Subgroup analysis and investigation of heterogeneity
If sufficient trials are available and statistical heterogeneity is evident, we will conduct the following subgroup analyses to explore clinical heterogeneity:
type of RAP (defined by the Rome III criteria) (Rasquin 2006);
duration of follow-up: immediate outcome measurement, short term (less than three months), medium term (three to 12 months), and long term (greater than 12 months).
Subgroup analysis can be misleading because the studies may not be designed and powered to show difference within subgroups. Therefore, we will undertake subgroup analyses with caution.
We will base our primary analyses on available data on the outcomes of interest.
Following this, we will use a sensitivity analysis to assess the robustness of conclusions in relation to two aspects of study design. We will assess:
the effect of inadequate allocation concealment, by the removal of studies judged as high or unclear risk of bias in this domain; and
the effect of inadequate blinding to treatment allocation by outcome assessors, by the removal of studies judged as high or unclear risk of bias in this domain.
A sensitivity analysis may also be carried out to establish the effect of missing data on the estimate of treatment effect. Therefore, we will perform the analysis with and without the studies with significant missing data to see if this alters the conclusions.