Manipulative therapy for infantile colic
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To evaluate the results of studies designed to address efficacy or effectiveness of manipulative therapies (specifically, chiropractic, osteopathy and cranial manipulation) for infantile colic in infants less than 6 months of age.
Background
Description of the condition
Infantile colic ‐ which presents as excessive crying in healthy, thriving infants ‐ is a common problem during the first months of childhood. Studies on the occurrence of colic have reported incidence rates which vary widely from 2%‐40%, in part as a result of differences in the criteria used to define the condition (Lucassen 2001; Soltis 2004). Crying typically occurs in the evenings, episodes starting in the first weeks of life and ending at the age of four or five months (Illingworth 1985). In studies, the condition is typically defined as crying which lasts at least three hours a day and occurs at least three days per week, over a period of at least three weeks, a definition first proposed by Wessel (Wessel 1954). A number of other definitions exist, possibly reflecting different conditions with other risk factors (Reijneveld 2002). In some definitions the duration criterion relates to both crying and fussing behaviour.
In some literature, symptoms other than crying are mentioned such as: crying in 'bouts' ('paroxysms'); changes to the acoustics of the cry (higher pitch) (Lester 1992), which can be differentiated by the parents (Gustafson 2000); flushing of the face; passing of gas, abdominal distension and difficulty with passing stools (Wessel 1954); drawing up the legs, arching the back, and other indications that indicate the infant may be experiencing pain (Illingworth 1985). It is not clear whether these symptoms are important features of a colic syndrome or relate to other disorders (Reijneveld 2002; Soltis 2004).
The aetiology of infantile colic is unclear. Infantile colic may not have a single cause but rather be the result of a number of different problems, with excessive crying as the final common pathway. Several main causes are suggested in the literature (Lucassen 1998; Savino 2007). Firstly, it is suggested that infantile colic may arise from a problem with the gut (Kirjavainen 2001; Lindberg 1999) and according to this view, excessive crying is the result of painful gut contractions caused, for example, by allergy to cow's milk (Hill 2000; Iacono 2005; Miller 1991), intestinal microflora (Lehtonen 1994; Rhoads 2009; Savino 2004; Savino 2005; Savino 2009), or neutrophilic infiltration (Rhoads 2009), transient lactase deficiency (Kanabar 2001) or motility dysfunction (Hipperson 2004). The meaning of the word 'colic', derived from the Greek word 'kolikos' (large intestine) is a reflection of this hypothesis (St James‐Roberts 1991). Colic can be viewed as a behavioural problem. According to this model, colic may be the result of an infant's perceived 'difficult' temperament (Canivet 2000) leading to inadequate parental reactions, or due to parental distress or depression leading to less‐than‐optimal interaction (Akman 2006; Carey 1984). Some have argued that excessive crying in an infant is not an illness, but merely the extreme end of normal crying (Barr 1991; Soltis 2004). Finally, some believe that infantile colic is merely a collection of aetiologically different problems, which are difficult to disentangle (Treem 1994).
The mean onset of colic is 1.8 weeks of age (Paradise 1966), and infants whose colic begins in the first two weeks of life seem to have a longer duration of symptoms than those whose symptoms start later (Pinyerd 1989). The average duration of symptoms is 13.6 weeks (Paradise 1966). Symptoms generally increase over the first few weeks of life, peaking in both the amount of crying and the intensity of the early‐evening diurnal pattern around the sixth week before reducing until the age of 12 weeks (Brazelton 1962; St James‐Roberts 1991b).
Unexplained crying is the most common presentation to paediatricians in the first 16 weeks of life (Miller 2007), with around one in six families seeking professional advice for a colicky infant (Husereau 2003), despite the fact that most infants with colic no longer have symptoms by the age of four to five months. Because of the serious impact of the condition on parents, most doctors and nurses feel the need to intervene ‐ at a cost to the UK National Health Service in excess of £65m (Morris 2001). Although many observers characterise infantile colic as a benign and self‐limiting problem, there is growing evidence to indicate that there may be serious sequelae to the disorder, such as shaken baby syndrome, child abuse, neglect (for example, Lee 2007; Overpeck 1998; Reijneveld 2004), increased maternal stress (Miller‐Loncar 2004; Neu 2003), later behavioural problems, or lower academic achievement (Canivet 2000; Rao 2004).
Description of the Intervention
The first person to suggest manipulative therapy as an effective treatment for infantile colic seems to have been AT Still in 1910. For many years, chiropractors, osteopaths and others have reported manually treating infants with symptoms of colic with apparently good results (Biederman 1992; Klougart 1989; Nilsson 1985; Still 1910). It has been reported that as many as 63% of paediatric patients referring to chiropractors may present with prolonged crying (Miller 2007). Chiropractic and osteopathy are health professions concerned with the diagnosis, treatment and prevention of disorders of the musculoskeletal system, and the effects of these disorders on the nervous system and general health. The broad model of health care is holistic, based on the theory that bony misalignments or soft tissue tensions within the body can result in visceral symptoms and that well‐being is dependent on the skeleton, muscles, ligaments and connective tissues functioning smoothly together. Health is viewed as a complex process integrating all parts and systems of the body (General Osteopathic Council 2010; McTimoney 2010; Peterson 2002).
Both professions focus on palpatory techniques to diagnose dysfunction, then use physical manipulation or adjustments, stretches and mobilisation techniques to improve the functioning of joints, to relieve muscle tension, to enhance the blood and nerve supply to tissues, and to help the body's own healing mechanisms (General Chiropractic Council 2010; General Osteopathic Council 2010).
Such manipulatory techniques may include adjustments to dysfunctional vertebrae (identified, for example, by misalignment or by reduced motion), achieved by introducing an impulse into the spinal column to correct the dysfunction. The speed and force applied vary between different techniques (Colloca 2009; Kawchuk 1992; Kawchuk 1993).
Practitioners of different techniques may also recommend different numbers of treatments, or deliver them over a different time frame (dose).
Both professions also use cranial adjustments ‐ usually following specialist training in cranial osteopathy, craniosacral therapy techniques, or applying cranial techniques taught on specialist paediatrics courses (Craniosacral Therapy Association of the UK 2010; McTimoney College of Chiropractic 2010; Sutherland Society 2010). These involve very light pressure to the cranium and associated soft tissue to allow or encourage the bones to assume/resume their normal positioning.
How might the intervention work?
There are several theories for how manipulative therapies might work to relieve infantile colic. Many are based on the belief that the birth process can cause extreme pressures to be exerted on the infant's head, leading to cranial moulding, or that poor positioning in the uterus can create cervical dysfunction, such as poor vertebral alignment if the head is maintained at an angle during pregnancy. These may be uncomfortable for the infant, and may contribute to colic symptoms (Craniosacral Therapy Association of the UK 2010; Sutherland Society 2010). Once such biomechanical problems are resolved, the discomfort is relieved and the symptoms of crying abate.
Other proposed therapeutic mechanisms suggest somatovisceral or spino‐craniovisceral reflex involvement (Biedermann 2005; Hipperson 2004).
However, there is little research evidence to support such arguments so the mechanisms of action of manipulative therapies remain unsubstantiated.
It might also be that different techniques have different mechanisms of action. For example, an adjustment to the upper cervical vertebrae may affect the vagus nerve, whereas realignment of the cranial bones or soft tissue release in the occipital area may relieve sensations of stiffness or soreness.
The number and frequency of treatments required for resolution of the problem is also in question. There is some evidence that chiropractic does have a dose response in other disorders (see, for example, Haas 2004), although it is not known whether this is the case with infantile colic.
Why is it important to do this review
There have been a number of systematic reviews published in recent years, either focusing on chiropractic interventions for colic specifically (Ernst 2009; Husereau 2003), or on manual therapies for non‐musculoskeletal conditions (Ernst 2003; Gotlib 2008; Hawk 2007), but only one (for massage) (Underdown 2006) has been undertaken to the exacting standards of The Cochrane Collaboration or with a meta‐analysis in mind. Carrying out a systematic review on the literature on chiropractic, osteopathy, cranial‐ and spinal‐ manipulative therapy will help to bridge this gap and to create the basis for the incorporation of future studies.
Objectives
To evaluate the results of studies designed to address efficacy or effectiveness of manipulative therapies (specifically, chiropractic, osteopathy and cranial manipulation) for infantile colic in infants less than 6 months of age.
Methods
Criteria for considering studies for this review
Types of studies
We will consider individually randomised, cluster randomised or crossover controlled trials for inclusion.
Types of participants
Infants younger than six months of age (at entry to study) who are assessed by clinicians as suffering from colic, defined as 'crying excessively'. As there is no consensus on the criteria for crying excessively, we will accept all definitions of excessive crying for inclusion in this review. We will not include studies of infants with crying of normal duration. Both breast‐fed and bottle‐fed infants will be eligible.
Types of interventions
The Intervention
We will consider active interventions consisting of manipulative therapies of chiropractic, osteopathy, cranial osteopathy, craniosacral therapy and cranial manipulation for inclusion.
Control arms
We will consider control interventions of no treatment, placebo/sham, standard care or waiting list control for inclusion.
The interventions may be applied either on their own or as an adjunct to conventional treatments (for example, counselling/advice and prescription medication), provided that the same adjunct treatment applies to all participants in the study.
Types of outcome measures
Primary outcomes
1. Changes in hours crying time per day (post‐treatment versus baseline).
2. Presence/absence of colic after treatment and/or at later follow up, i.e. the number of infants in which excessive crying resolved (using the definition of those conducting the trial).
3. Adverse effects: we will include any reported adverse outcomes ‐ for example, injury, stroke, arterial dissection, worsening of symptoms.
Secondary outcomes
1. Changes in frequency of crying bouts (number of crying episodes per day) ‐ post‐treatment versus baseline.
2. Measures of parental or family quality of life.
3. Measures of parental stress, anxiety or depression.
4. Sleeping time, i.e. change in duration of peaceful sleeping: post‐treatment versus baseline.
5. Parental satisfaction.
Timing of outcome assessment
We will evaluate outcomes:
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at the completion of any treatment protocol (i.e. any period, any number of treatments), and
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at a later follow up, where data exists and follow‐up periods are sufficiently homogenous.
We will consider the different timings separately for each outcome, i.e. we will include a study that reports an outcome at the two data points in an analysis of 'post treatment' and at 'follow up'.
Search methods for identification of studies
Electronic searches
We will identify relevant trials through electronic searches of the following sources:
The Cochrane Central Register of Controlled Trials (CENTRAL)
MEDLINE
EMBASE
CINAHL
PsycINFO
LILACS (Latin American and Caribbean Health Sciences Literature)
PEDro
Science Citation Index
Conference Proceedings Citation Index
metaRegister of Controlled Trials
National Research Register Archive (UK)
Center Watch Clinical Trials Listing Service (USA)
Clinicaltrials.gov
UKCRN Portfolio Database
We will devise a search strategy for each database by adapting the following MEDLINE search. Lines 1‐11 (adapted from Lucassen 2003) will retrieve studies about infantile colic. Lines 12‐23 (adapted and extended from Proctor 2006) will retrieve studies about relevant manual therapies. The RCT filter (lines 24‐32) is the Cochrane highly sensitive search strategy for identifying randomized trials in MEDLINE (sensitivity maximising version), in the Cochrane Handbook for Systematic Reviews of Interventions (Lefebvre 2008).
We will impose no language restrictions.
We will collate references in EndNote and process them to remove duplicates.
MEDLINE search strategy
1. crying/
2. (cry or crying or cries).tw.
3. colic/
4. colic$.tw.
5. ((stomach or abdominal or abdomen$) adj3 (spasm$ or pain$ or cramp$)).tw.
6. ((gastric or gastro$) adj3 (spasm$ or pain$ or cramp$)).tw.
7. or/1‐6
8. exp infants/
9. (infant$ or newborn$ or baby or babies).tw.
10. or/8‐9
11. 7 and 10
12. Chiropractic/ or manipulation,chiropractic/ or chiropractic$.tw.
13. Osteopathic Medicine/ or Manipulation, Osteopathic/ or osteopath$.tw.
14. Manipulation, Orthopedic/ or (orthop?edic$ adj3 manipulat$).tw.
15. Manipulation, Spinal/ or (spin$ adj3 manipulat$).tw. or (spin$ adj3 adjust$).tw. or (spin$ adj3 mobili#ation).tw. or subluxation.tw.
16. (manual$ adj3 therap$).tw.
17. (manipulat$ adj3 therap$).tw.
18. (craniosacral$ or cranio‐sacral$).tw.
19. cranial.tw.
20. Musculoskeletal Manipulations/
21. musculoskeletal$.tw.
22. Physical Therapy Modalities/ or "Physical Therapy (Specialty)"/ or physical therap$.tw. or physiotherap$.tw.
23. or/12‐22
24. randomized controlled trial.pt.
25. controlled clinical trial.pt.
26. randomi#ed.ab.
27. placebo.ab.
28. drug therapy.fs.
29. randomly.ab.
30. trial.ab.
31. groups.ab.
32. or/24‐31
33. exp animals/ not humans.sh.
34. 32 not 33
35. 11 and 23 and 34
Searching other resources
1. We will identify studies incorporated into previous reviews and systematic reviews of the subject and consider them for inclusion in this review.
2. We will also evaluate bibliographies of articles identified through the search strategy for additional sources.
Grey literature
1. We will contact colleges and other institutions concerned with osteopathy and chiropractic, and other researchers in the areas of osteopathy, chiropractic and infantile colic to identify any unpublished studies.
2. We will undertake searches of Google and Google scholar using the search terms identified above to identify further grey literature.
Wherever we identify references to unpublished or ongoing studies, we will attempt to obtain sufficient details to incorporate them in this review.
Data collection and analysis
Selection of trials
Two authors will independently screen titles and abstracts from the search, discarding any that do not fulfil the inclusion criteria. We will retrieve all potentially relevant articles for an assessment of the eligibility of the full text. We will consult a third author to arbitrate any disagreements. If there is any doubt that a study meets the inclusion criteria, we will contact the authors for clarification. If information is not forthcoming, or dispute remains, we will resolve it by approaching the CDPLPG editorial base.
Data extraction and management
We will develop data extraction forms a priori, per the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008b). We will extract the following information.
1. Methods; study design, duration, sequence generation, allocation concealment, blinding of outcome assessors, evaluation of success of blinding.
2. Participants: source of participants, inclusion/exclusion criteria, total number at baseline, total number at completion, setting, definition of 'colic' applied, diagnostic criteria applied, age at onset of colic and age at commencement of intervention, evaluation of potential effects of confounding characteristics (for example, age, gender, breast/bottle fed).
3. Interventions & controls: number of groups, intervention(s) applied, frequency and duration of treatment, total number of treatments, allowed co‐interventions, evaluation of potential therapeutic value of sham/placebo.
4. Outcomes: list of outcomes assessed, definitions used, values for mean and standard deviation at baseline and at time points as defined by the study protocol (or change from baseline measures, if given).
5. Results: number of participants in each cohort, baseline measures, measures at end of protocol, follow‐up data (including means and standard deviations/standard errors/confidence intervals for continuous data and summary table for dichotomous data), withdrawals and loss to follow up.
6. Other: references to other relevant studies, points to follow up with authors, comments from the authors, key conclusions from the study (by the authors), other comments from reviewers.
Two authors will extract the data independently using the data extraction form. Any disagreements will be resolved by the third author. We will collate the data using Review Manager software (RevMan 2008).
Assessment of risk of bias in included studies
Two authors will independently evaluate each study for risk of bias using the criteria recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008), specifically: sequence generation; allocation concealment; blinding of participants, personnel and outcome assessors; incomplete outcome data; selective outcome reporting; other potential threats to validity. We will judge each domain as at low or high risk of bias, or at unclear risk of bias according to the criteria in the Handbook.
Sequence generation
We will assess randomisation as 'low risk of bias’ if the procedure of sequence generation was explicitly described and considered adequate to produce comparable groups. Examples are computer‐generated random numbers, a random numbers table, or coin‐tossing.
Allocation concealment
We will assess concealment of treatment allocation as ‘low risk of bias’ if the procedure was explicitly described and adequate to ensure that intervention allocations could not have been foreseen in advance of, or during, enrolment. Examples are centralised randomisation, numbered or coded containers, or sealed envelopes. Clearly inadequate procedures are alternation, or reference to case record numbers, dates of birth.
Blinding of participants, clinicians and outcome assessors
We will assess the risk of bias associated with the blinding of participants, personnel and outcome assessors based on the likelihood that such blinding was sufficient to ensure that outcome assessors (generally parents) had no knowledge of which intervention the infant received. Blinding of patients is not, of course, considered necessary in this population. It is not possible to blind clinicians in the field of manipulative therapies, but we will consider the likely impact of their knowledge and any mechanisms used to minimise this bias (such as by using a detailed clinical protocol or minimising contact between parents and practitioners) during the evaluation and take this into account when determining an overall risk of bias.
Incomplete outcome data
We will assess reporting of incomplete outcome data as ‘low risk of bias’ if attrition and exclusions were reported, reasons for attrition were reported and any re‐inclusions in analyses were performed by the authors. We will consider this adequate if there are no missing data, or if missing outcome data are unlikely to be related to the true outcome, similar across groups, or of no clinically relevant impact on the intervention effect estimate, etc.
Selective outcome reporting
We will assess reporting of outcomes as ‘low risk of bias’ if all the study outcomes have been reported in the way pre‐specified in the protocol.
Other potential threats to validity
We will assess other threats to validity as ‘low risk of bias’ if the study appears to be free of other sources of bias, such as being stopped early due to a data‐dependent process or had a baseline imbalance between the groups.
Where the risk of bias is unclear from published information, we will attempt to contact authors for clarification. If this is not forthcoming, we will assess studies as at unclear risk of bias. The review authors will not be blinded to the titles of journals or the identities of authors, as they are familiar with the field. In case of differently scored items, two authors will try to find agreement by discussion. We will resolve any persisting disagreement by consulting the third author.
Measurements of treatment effect
If outcomes are reported as dichotomous variables, we plan to calculate the risk ratio with 95% confidence interval from a meta‐analysis. If we identify a positive effect for manipulative therapies, we will calculate the number needed to treat, if data permits.
Where outcomes are measured as continuous data, we will compare the mean differences of change scores, depending on the data available. If standard deviations or standard errors are not available, we will attempt to extract p value, t value and the confidence intervals to impute standard deviations and standard errors.
If authors have used different scales to measure similar outcomes, we will use standardised mean difference. If crossover trials are reported, we will use the mean and standard error of paired t‐tests for the meta analysis.
Unit of analysis Issues
For each included study, we will determine whether the unit of analysis is appropriate for the unit of randomisation and the design of each study (i.e. whether the number of observations matched the number of 'units' that were randomised ‐ Deeks 2008).
If cluster‐randomised trials are included, we will use the Intraclass correlation coefficient (ICC) to convert trials to their effective sample size before incorporating them into the meta‐analysis, per recommendation in the Cochrane Handbook for Systematic Review of Interventions (Higgins 2008c).
If we include studies containing three or more intervention arms, we will incorporate appropriate pair‐wise comparisons, providing there is no evidence of bias, such as the authors introducing the additional groups after seeing the data (i.e. the groups were determined a priori in the protocol) or of selective reporting (i.e. data for all cohorts were reported). For the meta‐analysis, we will consider which of the approaches recommended in the Cochrane Handbook for Systematic Review of Intervention (Higgins 2008c) is most appropriate (for example, combining control groups, or combining intervention groups).
Dealing with missing data
Where possible, we will assess missing data and drop‐outs for each study. Where we cannot include data in the meta‐analysis, the assessment will be qualitative.
It is to be expected that, with a disorder that causes such distress to parents, that there will be a certain impatience with any interventions. It seems therefore logical to expect fairly high drop‐out rates. In all groups, parents may withdraw their child either:
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if they see no improvement ‐ in order to try a different solution to the problem; or
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if the child recovers completely ‐ in order that they can resume normal family life as quickly as possible.
There is no logic, therefore, to defaulting data points or outcomes for participants who drop out during the study or are lost to later follow up. An available case analysis will therefore be attempted wherever data permit, including by seeking additional data from the authors, where possible.
Assessment of heterogeneity
We will review any reported characteristics from the studies to evaluate clinical diversity (such as participant current age versus age at onset of the disorder, etc.) to ensure that the group of studies is sufficiently homogeneous to provide a meaningful meta‐analysis.
We will assess consistency using forest plots and the Chi² test from the analysis in RevMan (RevMan 2008), according to the current recommendations in the Cochrane Handbook for Systematic Review of Interventions, using a p value of 0.10 for statistical significance, if one or more included studies have a small sample size (Deeks 2008). To assess the impact of any heterogeneity on the meta‐analysis, we will also calculate I² (Higgins 2002; Deeks 2008).
Assessment of reporting bias
In order to minimise publication bias, we will attempt to obtain the results of any unpublished studies.
If there are more than 10 studies we will evaluate whether bias may be present using funnel plots to investigate any relationship between effect estimates and study size/precision, as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 2008). If we identify asymmetric funnel plots, we will review possible alternative explanations, such as reporting bias, publication bias, different study sizes or poor study design as part of the sensitivity analysis.
Data synthesis
If two or more studies prove suitable for inclusion and measure the same outcomes, we will perform a meta‐analysis of the results. In the first instance, we will group all manipulative therapies together. If there are common characteristics, we will group studies and further investigate by using sub‐group analyses (see below).
We will use the random‐effects methods as described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2008).
For continuous variables, we will use a meta‐analysis of change scores because "it removes a component of between‐person variability from the analysis" (Deeks 2008) and we will apply the mean difference approach where data allow. Where data allow, we will also include the baseline outcome measurements as a covariate in an analysis of covariance (ANCOVA).
If studies measure the same outcome using different scales we will apply the standardised mean difference approach.
For dichotomous outcomes, we will perform a meta‐analysis of risk ratios and a calculation of the number needed to treat, since these (in combination) provide good consistency, mathematical properties and ease of interpretation (Deeks 2008). We will base the assumed control group risks on an assessment of typical risks, calculated from the control groups in different patient groups, if appropriate, or at different lengths of follow up. if there is little variation in baseline risk we will use the median control group risk across the studies.
Subgroup analysis and investigation of heterogeneity
Where we identify significant levels of heterogeneity, and there are sufficient observations (at least ten studies for each characteristic modelled (Deeks 2008)) we will investigate for any subgroup relationships in order to establish whether there is a single intervention effect, specifically:
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type of intervention (different techniques may impact the outcomes)
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treatment dose (total number of treatments, number of treatments per week, or overall duration of treatment protocol)
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mean age of the participants at onset of colic (earlier onset may imply greater severity of symptoms)
Sensitivity analysis
We will conduct sensitivity analyses, where data permit, to determine whether findings are sensitive to restricting inclusion to studies judged to be at low risk of bias. In these analyses we will re‐evaluate the findings, limiting the inclusion to those studies that:
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have a low risk of selection bias (associated with sequence generation or allocation concealment)
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have a low risk of performance bias (associated with issues of blinding)
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have a low risk of attrition bias (associated with completeness of data)
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are published
