Psychosocial interventions for recurrent abdominal pain in childhood

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To determine the effectiveness of psychosocial interventions for RAP in children of school age.

Background

Description of the condition

Recurrent abdominal pain (RAP) is a common problem in paediatric practice. It has been suggested that 4% to 25% of school-aged children suffer from RAP that interferes with their activities of daily living (Apley 1958; Øster 1972; Faull 1986; Abu Arafeh 1995; Williams 1996). It is regarded as a benign condition, but it is important to note the morbidity incurred by these children. It is hard to say that the condition is truly benign considering the related school absences, hospital admissions, and appendectomies for symptoms that continue (Stickler 1979; Scharff 1997; Walker 1998; Størdal 2005), sometimes into adulthood (Apley 1975). Moreover, the abdominal pain is commonly associated with other symptoms, including headaches, recurrent limb pains, pallor, and vomiting (Apley 1958; Stone 1970; Øster 1972; Stickler 1979; Faull 1986; Abu Arafeh 1995; Hyams 1995).

It is increasingly recognised that RAP in children represents a group of functional gastrointestinal disorders that have an unclear aetiology. Children suffer either chronic or recurrent gastrointestinal symptoms not explained by a structural, biochemical or inflammatory process. Apley first sought to define the condition in the 1950's and suggested that at least three episodes of severe abdominal pain over three months (Apley 1958), often with associated systemic symptoms but no established organic cause, fulfils a diagnosis of RAP. Now there is international consensus with a symptom-based classification system, the Rome III criteria, which has specific categories for paediatric presentations (Rasquin 2006). The categories include: functional dyspepsia, irritable bowel syndrome, abdominal migraine, and functional abdominal pain syndrome. It should be noted that the pain classification for each of the Rome III diagnoses is defined by at least one episode per week for at least two months; this varies from Apley's original definition of RAP (Apley 1958). The Rome classification is not based on known pathophysiological differences between the conditions but rather the collection of features for each manifestation. Thus, it remains unclear the extent to which separating children into these categories defines groups as distinct clinical entities that are likely to respond differently to treatment. Nonetheless, this classification has been welcomed following the historical use of diverse terms, some implying causation. These include: "abdominal migraine" (Farquar 1956; Bain 1974; Symon 1986; Hockaday 1992), "abdominal epilepsy" (Stowens 1970), "the irritable bowel syndrome in childhood" (Stone 1970), "allergic-tension-fatigue syndrome" (Speer 1954, Sandberg 1973), "neurovegetative dystonia" (Rubin 1967; Peltonen 1970), "functional gastrointestinal disorder" (Drossman 1995), and "the irritated colon syndrome" (Painter 1964; Harvey 1973). The paediatric Rome criteria are an attempt to improve the diagnosis, study and treatment of children with RAP (Walker 1989; Schurman 2005).

There have been several proposed causal pathways that result in the heterogeneous presentations of chronic abdominal pain. It is recognised that physical, emotional, and environmental factors may contribute to the manifestation of unexplained abdominal pain. When considering the diverse causes, it is unsurprising that a variety of treatments have been suggested. The treatment approaches can be grouped as pharmacological, dietary or psychological, and behavioural.

Pharmacological treatments

A range of pharmacological treatments have been tried and tested: analgesics, dicyclomine (Edwards 1994), pizotifen (Christensen 1995; Symon 1995), herbal extracts (Zhang 1991), and many other drugs (Bain 1974; Worawattanakul 1999). A number of randomised controlled trials (RCTs) have reported on the use of peppermint oil for irritable bowel syndrome in adults (Grigoleit 2005), and the results have been interpreted as suggesting it is a beneficial intervention. However, an earlier review reached no clear conclusion on efficacy due to poor methodological quality of the included studies (Pittler 1998). Other possible causal factors have been postulated, including food allergies (Poley 1973), reaction to food additives (Anonymous 1984), infectious agents like Helicobacter pylori (Heldenberg 1995), and parasitic infestation (Primelles 1990; Wardhan 1993).

Dietary interventions

Many dietary inventions have been suggested to improve the symptoms of RAP. These involve either excluding or reducing a food group or specific ingredient from the diet or supplementing it and therefore increasing its intake. The dietary interventions include low oxalate diets (Feldman 1985), eliminating food groups, such as dairy products (Bayless 1971; Bain 1974; Liebman 1979), some fruits, meats or rye (Farquar 1956; Minford 1982), and taking fibre supplements (Feldman 1985; Christensen 1986). Increased dietary fibre may be of benefit in adults with irritable bowel syndrome (Rasmussen 1982; Lambert 1991). Probiotics have also been given to children with RAP (Wilhelm 2008).

It seems likely that many children, especially those at the milder end of the spectrum, do not present to the health care system or only present to primary care. For these children, the principal management is likely to be reassurance that the pain does not represent significant organic pathology. Even in secondary care, a large proportion of children with RAP are treated with reassurance following investigations for treatable causes (Edwards 1994).

Description of the intervention

Psychosocial interventions

The focus of this review is any intervention based on psychological or behavioural theory. A variety of approaches have been used, including behavioural and cognitive-behavioural techniques (Sanders 1994; Scharff 1997), psychotherapy (Vasquez 1992), family-centred approaches (Liebman 1976; Wetchler 1992; Walker 1999), and multi-component therapies (Finney 1989; Edwards 1991; Humphreys 1998; Hicks 2006).

How the intervention might work

Many clinicians believe that abdominal pain-related functional gastrointestinal disorders originate from, or are contributed to by, psychogenic factors (Friedman 1972; Raymer 1984). Historically, authors have suggested that children with RAP come from "psychosomatic families" (Osborne 1989). These are controversial ideas, although a recent population-based study found that anxiety in parents, added to a specific child temperament before one year of age, which is a strong predictor of RAP in childhood (Ramchandani 2006). Further evidence of psychological factors contributing to presentation of unexplained abdominal pain comes from Campo 2001, which suggested a strong association between RAP in childhood and anxiety in adult life. Therefore, children have received psychological and behavioural interventions for RAP (Heinild 1959; Sank 1974; Miller 1979; Linton 1986).

The aetiology of pain-related functional gastrointestinal disorders is unclear. It has been suggested that visceral hypersensitivity (Di Lorenzo 2001; Van Ginkel 2001), autonomic dysfunction (Good 1995), and gut dysmotility may contribute and this may be initiated by an inflammatory, infective, traumatic or allergic trigger (Milla 1999; Mayer 2002). As with any chronic pain condition, it is likely that psychological factors are also important in presentation and treatment. It is recognised that anxiety in the children and parents can modulate the expression of abdominal symptoms. Children who suffer with RAP are more likely to have poor coping strategies for stressful situations (Walker 2007). Also, depressive symptoms have been linked with a poor ability to cope with RAP (Kaminsky 2006). Therefore, the aim of psychological and behavioural therapies is often to improve the child's mental health and coping strategies or to alter environmental factors that might reinforce pain behaviour.

Why it is important to do this review

RAP in children is very common and in daily clinical practice there is no consensus on which treatments to offer patients. Therefore, there is an inconsistent approach. This review is important to establish if there is evidence for the effectiveness of psychosocial interventions in children with RAP. It updates an earlier version published in 2008 (Huertas-Ceballos 2008b). Companion reviews addressing the effectiveness of pharmacological and dietary interventions for RAP are also being updated (Huertas-Ceballos 2008a; Huertas-Ceballos 2009), so together they can guide clinicians, patients, and their families in treatment decisions.

Objectives

To determine the effectiveness of psychosocial interventions for RAP in children of school age.

Methods

Criteria for considering studies for this review

Types of studies

RCTs.

Types of participants

Children aged five to 18 years old with RAP or an 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 psychosocial intervention compared to standard care, waiting list or no treatment.

Types of outcome measures

Primary outcomes

Pain intensity, duration or frequency.

As 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).

Secondary outcomes

As measured by a validated tool:

  • school performance;

  • social/psychological functioning;

  • quality of daily life.

We will present all outcomes in a 'Summary of findings' table.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases for relevant studies:

We will adapt the following search strategy for Ovid MEDLINE for each database 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.

1 Recurr$.tw.
2 Chronic$.tw.
3 Intermittent$.tw.
4 Bout$1.tw.
5 spasm$.tw.
6 Transitory.tw.
7 Transient.tw.
8 Functional.tw.
9 Continu$.tw.
10 Paroxysmal.tw.
11 Persistent.tw.
12 Idiopathic.tw.
13 unspecifi$.tw.
14 Non specifi$.tw.
15 nonspecifi$.tw.
16 motility.tw.
17 episod$.tw.
18 1 or 2 or 3 or 4 or 5 or 6 or 7 or 8 or 9 or 10 or 11 or 12 or 13 or 14 or 15 or 16 or 17
19 exp Recurrence/
20 18 or 19
21 ((pain$ 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$.tw
26 IBS.tw.
27 Functional dyspepsia.tw.
28 irritable bowel$.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.
35 randomi#ed.ab.
36 placebo$.ab.
37 placebo$.ab.
38 drug therapy.fs.
39 randomly.ab.
40 trial.ab.
41 groups.ab.
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/
49 Child$.tw.
50 Adolescen$.tw.
51 Young person$.tw.
52 Boy$.tw.
53 Girl$.tw.
54 teen$.tw.
55 Schoolchild$.tw.
56 Young adult$.tw.
57 Youth$.tw.
58 P*ediatric$.tw.
59 Student$.tw.
60 Pupil$.tw.
61 Juvenile$.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 by the electronic searches to identify any additional studies not already identified.

Data collection and analysis

Selection of studies

Two review 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 any paper that appears to be potentially suitable for inclusion and 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.

  1. Study characteristics: number of participating patients, inclusion and exclusion criteria, type of intervention and comparison, intervention characteristics (duration, frequency, setting), number of withdrawals.

  2. Participant characteristics: sex, age, diagnosis (for example, RAP or syndrome defined by the Rome criteria).

  3. Outcome measures: measurement of pain and any secondary outcome measured.

Assessment of risk of bias in included studies

We will consider the following domains when assessing risk of bias in included studies:

  • 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. Based on the methods detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), we will classify the risk of bias as "low risk", "high risk" or "unclear risk" (Table 1).

Table 1. Assessment of risk of bias in included studies
Domain Risk of bias judgement
Low High Unclear
Selection bias 
Random sequence generationIf 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 randomisation by an 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 concealmentIf 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 may have been known prior to assignment.

If there is not sufficient detail to judge the risk of bias.

 

Performance bias 
Blinding of participants and personnelIf 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, we do not expect participants and therapists to 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 assessmentIf 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.

 

Attrition bias
Incomplete outcome dataIf 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 if 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.
Reporting bias
Selective reportingIf 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. For example, protocols are unavailable.

We will assess all included studies for other sources of bias that may alter the estimate of treatment effect, for example, we will look for evidence of differential loss to follow-up.

We will consider a trial as having an overall low risk of bias if most of the above domains are assessed as 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 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

We will report study results as follows:

  1. for continuous data (that is, number of days of pain), 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;

  2. for dichotomous data (for example, pain improved, yes or no), we will analyse using odds ratios (ORs).

Unit of analysis issues

If the following three types of trials are found, we will consider their results as per 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. It is unlikely that cross-over trials will be considered an appropriate method for estimating the effectiveness of this type of intervention. But trials will be considered on an individual basis and, if appropriate, will be included.

2. Cluster-RCTs

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 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 use 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 cognitive behavioural therapy or family therapy). 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 are 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 different classes of psychosocial intervention) and this does not require the control group to be 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. We will collect the proportions of participants for whom no outcome data are obtained and report them in the 'Risk of Bias' assessment 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 Chi test to further assess the strength of evidence of 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

Publication bias

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.

Data synthesis

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. For summary statistics for continuous data, we will report the 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. Therefore, we will only conduct a meta-analysis using data from studies with equivalent psychosocial interventions, for example, on the same type of psychosocial intervention. We are aware that given the heterogeneity of the psychological treatments used for RAP and the variety of methods to measure pain, a meta-analysis may not be possible (DerSimonian 1986). In this 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 examine the following subgroups to explore clinical heterogeneity:

  • type of RAP (defined by Rome III criteria) (Rasquin 2006);

  • age;

  • 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 differences within subgroups. Therefore, we will undertake subgroup analyses with caution.

Sensitivity analysis

Our primary analyses will be based 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:

  1. the effect of inadequate allocation concealment, by the removal of studies judged as high or unclear risk of bias for this domain; and

  2. the effect of inadequate blinding to treatment allocation by outcome assessors, by the removal of studies judged as high or unclear risk of bias for 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.

Acknowledgements

We acknowledge the work on the original review done by Angela Huertas-Ceballos, Stuart Logan, Cathy Bennett, Sarah See, Colin Macarthur, and Morris Zwi.

What's new

DateEventDescription
31 January 2014New citation required and major changesUpdated of review with revised protocol

Contributions of authors

Review design: AM, SL
Review co-ordination: AM
Data collection:

  • Search strategy design: AM, AB

  • Searches: AM, AB

  • Search results screening: AM, AB, RA, TN, JTC

  • Retrieval of papers: AM, AB

  • Paper screening and appraisal, and extraction of data: AM, AB, RA, TN, JTC

  • Writing to authors for additional information: AM, AB

  • Entering the data into RevMan: AM, AB, RA, TN, JTC

Analysis of the data: AM, AB, RA, TN, JTC, SL
Interpretation of the data:

  • Methodological perspective: AM, AB, RA, TN, JTC

  • Clinical perspective: AM, TN, SL

Declarations of interest

Alice E Martin (AM) - none known.
Tamsin V Newlove-Delgado (TN) - none known.
Rebecca A Abbott (RA) - none known.
Alison Bethel (AB) - none known.
Jo Thompson-Coon (JTC) - none known.
Stuart Logan (SL) - none known.
Vasilis Nikolaou (VN) - none known.

The authors who practice clinical paediatrics are AM and SL. AM is a paediatric trainee and works under the guidance of various Consultant Paediatricians. SL is a Consultant Paediatrician and treats children according to current best evidence, in light of their preference. Therefore, there are no conflicts of interest with this review.

Sources of support

Internal sources

  • None, Not specified.

External sources

  • None, Not specified.

Notes

This is a new protocol for the update of a previously published review (Huertas-Ceballos 2008b).

Ancillary