An overview of systematic reviews of complementary and alternative therapies for infantile colic

Infantile colic (IC) is a common childhood condition affecting 5% to 20% of infants worldwide [1, 2]. In 2016, the new Rome IV criteria for colic defined it as ‘an infant who is less than five months of age when symptoms start and stop; recurrent and prolonged periods of infant crying, fussing or irritability reported by caregivers that occur without any obvious cause and cannot be prevented or resolved by caregivers; no evidence of infant failure to thrive, fever or illness [3]’. Prior to this, colic the was most commonly diagnosed using the Wessel ‘rule of three’ criteria [4].

Much research has been conducted over the past 50 years to try to establish the underlying aetiology. Formula intolerance, immaturity of gastrointestinal tract, food allergies, intestinal cramping or excessive gas formation have all been suggested [5], alongside psychosocial causes, e.g. maternal anxiety and maternal-infant bonding issues [6], but its pathophysiology remains unclear. Although it is considered a self-limiting condition, it can be distressing for both parents and babies.

There have been several previous overviews of reviews investigating CAM interventions for IC which have predominantly focused on spinal/chiropractic manipulation [11‐13] or have included IC alongside other conditions affecting children [14]. Most lack adequate quality assessment of the included systematic reviews.

Medline, Embase and AMED (via Ovid), Web of Science and Central via Cochrane library were searched from their inception to September 2018. Google Scholar (first 20 pages) and OpenGrey were searched for grey literature and PROSPERO for ongoing reviews. All reviews from 2011 were assessed for eligibility. The search strategy was structured using subject (MeSH) headings, text word terms and their derivatives: homoeopath, acupuncture, spinal manipulation, hypnosis, reflexology, phytotherapy, probiotics, infant, colic, systematic review, meta-analysis. Full details of the search can be found in Additional file 1.

One reviewer (RP) extracted data and summarised the review characteristics (see Table 1). Extracted data was checked by another reviewer (VL or PD). Disagreements were resolved through discussion. Information was extracted on author, date of review, country, list of studies included in the individual review, intervention and comparator summary, number of participants, diagnosis criteria, meta-analysis results or summary of main between-group results, whether a sensitivity or subgroup analysis was conducted, risk of bias assessment and adverse events.

We reported the standard mean difference (SMD) and 95% confidence intervals (CI) and results of any tests of heterogeneity reported in the relevant meta-analyses. Individual study results (mean and standard deviation (SD)) of continuous variables and any between-group statistical analysis were reported when there were no pooled results available (Additional file 1: Table S7). Pooled odds ratios or risk ratios and associated 95% CIs were reported for any dichotomous data.

Due to the expected overlap of studies and heterogeneity between reviews (particularly with regard to intervention and comparator arms), we conducted a narrative synthesis of the findings rather than pooling of meta-analyses from the included reviews. We applied the following thresholds for the interpretation of the reported I² statistic that assesses heterogeneity [18] in any reported meta-analysis.

The quality of each systematic review was assessed using the newly developed AMSTAR-2 scale (Assessing the methodological quality of systematic reviews [19]). This is the revision to the validated and frequently used AMSTAR scale [20]. This was used alongside the ROBIS tool (Risk of Bias in Systematic Reviews tool [21]).

Three reviewers (RP, VL, PD) independently assessed each review using both tools. Two reviewers had limited experience of using the ROBIS tool, so a third reviewer, who helped develop the tool (PD), was asked to complete both ratings. Meta-analyses were checked by a statistician experienced in meta-analyses (CP).

There were two changes to the protocol; originally, we were going to exclude reviews that reported on multiple conditions of which infantile colic was one, but we changed this to include reviews that had at least two studies of IC described, to capture more data. We also allowed active treatments to be the comparator option.

The search identified 903 potentially relevant papers and 669 titles/abstracts were screened (see Fig. 1). Forty-three full text articles were assessed for eligibility and 16 systematic reviews were included in this overview. Results of the included reviews are presented in Table 1 (details of the individual studies can be found in Additional file 1: Table S7). Only identifiable randomised controlled trials (RCTs) from each review are reported. The summarised AMSTAR-2 scores and ROBIS scores are presented in Tables 2 and 3. Further justification statements for ROBIS are presented in Additional file 1: Table S6. All excluded reviews are listed in Additional file 1: Table S5.

The 16 included reviews [22‐37] were published between 2011 and 2018. The reviews were conducted from the following countries: three were from the UK and Australia, two from Poland and one each from France, Mexico, Canada, Norway, Germany, Saudi Arabia, China and the USA. The reviews investigated the following therapies: herbal medicine (n = 1), acupuncture (n = 1), manipulation (n = 3), multiple CAMs (n = 4) and probiotics (n = 7). The majority assessed crying time or reduction in symptoms of colic as the main outcome. There was considerable overlap between studies reported in the included reviews (see Additional file 1: Table S7, for clarity).

Spinal manipulation was assessed in six reviews [22, 23, 25‐28]. Two multiple CAM reviews assessed manipulation but did not pool the results [22, 25]. Both found three trials to be effective [68, 69, 72, 73, or] with the exception of one [71].

Dobson et al.’s [26] Cochrane review of spinal manipulation therapy (SMT) found that five of the six included studies reported a beneficial effect on the course of colic. They found manipulation therapies had a greater effect on daily crying time, reducing it by 1 h 12 min/day on average with moderate heterogeneity (MD = − 1.20; 95% CI − 1.89 to − 0.51, I² = 56%). However, there was no evidence of a difference when restricting to the studies judged as having a low risk of performance bias (blinding of parent outcome assessors). Three studies measured full recovery (odds ratio [OR] = 11.12; 95%CI 0.46 to 267.52, I² = 89%), but confidence intervals were extremely wide and heterogeneity was substantial. Adverse events were only assessed in one study [83] and none were found. Overall, firm conclusions cannot be drawn from such limited data. The GRADE (Grading of Recommendations Assessment, Development and Evaluation) evaluation indicates low quality of evidence for both outcomes. The results from AMSTAR-2 and ROBIS indicate a high level of confidence in the findings and were judged to be of low risk of bias in all domains.

Gleberzon et al.’s [27] narrative synthesis included three RCTs of SMT for infantile colic [68, 71, 84]. Two of these RCTs were reported in Dobson et al.’s [26] review. Browning et al.’s [84] trial was excluded from the Dobson review as it compared two active treatments (spinal manipulation and occipito-sacral decompression). Just one trial indicated an effect on IC symptoms compared to comparator [68]. There were issues with both quality (AMSTAR-2) and bias (ROBIS) with this review.

Carnes et al. [28], in their update of the Cochrane review by Dobson et al., [26] identified five RCTs of IC. Browning et al.’s [84] trial was included despite comparisons with an active treatment. They conducted a pooled analysis of four colic studies that were also included in Dobson et al.’s meta-analysis [68, 71, 72, 83] (although Carnes et al. used a different version of Miller et al.’s trial [80]). They reported a similar reduction in crying time ((MD = − 1.27 h, 95% CI − 2.29 to − 0.36, P = 0.006, I² = 69%), again, heterogeneity was substantial and issues with quality and bias were evident.

Gutierrez-Castrellon et al.’s [25] network meta-analysis (NMA) supported the effectiveness of manipulation studies for IC, pooling the results of five RCTs [68, 71, 72, 80, 81] and found a weighted mean difference [WMD] of − 37.4 min (95% CI, − 21.5 to − 67.0), P = 0.001, I² = 78%) compared to control. The overall confidence in results was critically low (AMSTAR-2) and risk of bias high (ROBIS).

There was one main review of herbal medicine [30]. It assessed various types of herbal medicine for several conditions. We extracted just the data on infantile colic. Evidence was found for different fennel preparations (e.g. oil, tea, herbal compound Colimil) in treating children with colic, whereas peppermint oil was not found to be effective. No serious adverse effects were reported.

Herbal medicine was also assessed in the four multiple CAM reviews [22]. The same studies were included. Gutierrez-Castrellon et al. [25] pooled various herbal extract studies (peppermint, fennel seed oil, Colimil (containing Matricariae recutita, Foeniculum vulgare and Melissa officinalis) in their NMA and demonstrated a weak effect, (WMD = − 61.2 min (95% CI 0.8 to − 122.0, P = 0.05, I² is 98%). The wide confidence intervals, considerable heterogeneity and the crossing of the line of no effect suggest that herbal medicine has limited effect on crying time. In conclusion, Gutierrez-Castrellon et al. does not recommend herbal medicine for colic.

Harb et al. [24] conducted a subgroup meta-analysis focussing only on extracts containing fennel and demonstrated it to be effective for reducing colic symptoms in solely breast-fed infants. However, this analysis also had considerable heterogeneity and wide confidence intervals (MD = − 72.07, 95% CI − 126.43 to − 17.70, I² = 99.5%). It should be noted that much of the fennel oil evidence stems from one trial (Arikan et al. 2008 [73]) which was at particular risk for blinding, selective reporting and issues of randomisation. Massage was one of the arms in this trial; a therapy where it is impossible to blind the therapist. Further, the wide confidence intervals and the crossing of the line of no effect suggest that this trial has limited, if any, value. These issues certainly cast concern on the overall findings.

Perry et al. [22] and Bruyas-Bertholon et al. [23] both reported results that demonstrated fennel herbal extracts to be effective in reducing colic symptoms, but both concluded that the methodological issues of the individual studies (discussed above) call these results into question.

One systematic review of acupuncture [29] used individual participant raw data (IPD) which is considered the gold standard of evidence synthesis due to the high level of precision and consistency [38]. A difference was found at the mid time-point analysis favouring acupuncture: MD = − 24.9 min (95% CI − 46.2 to − 3.6; P = 0.02, I² = 9%), but not after the removal of the one unblinded trial, [47] (MD = − 13.8, 95% CI − 37.5 to 9.9, P = 0.25, I² = 0%). The GRADE evaluation indicates moderate quality evidence. No major adverse events occurred although acupuncture induced some crying during treatment, believed to be linked to the insertion of needles into the infant [39, 40]. This was a well-conducted review that was judged to be low risk of bias in most domains, but with low confidence in the results (AMSTAR-2). One issue with this review is the authors assessed all their own trials [46, 78, 84], although they appeared to be objective in their evaluation.

Gutierrez-Castrellon et al. [25] pooled two of the above studies [53, 57] and initially found an effect favouring acupuncture (at week 1 and 2) but was no longer evident by week 3 (WMD of − 11.2 min (95% CI 2.0 to − 23.0), P = 0.08, I² = 0%). There were issues with bias and quality in the review process. Bruyas-Bertholon et al. [23] echoed these findings in their multiple CAM review.

We identified seven reviews focussing on probiotics [31‐37]. The most commonly reported probiotic was Lactobacillus reuteri DSM17398. The majority of reviews were rated as having high or unclear risk of bias (ROBIS) and confidence in the results were considered to be critically low (AMSTAR-2).

Sung et al. [31] examined the effectiveness of L. reuteri DSM17938 versus either placebo or the drug simethicone. They meta-analysed three trials of breast-fed infants [15, 62, 74] and found a mean reduction in daily crying time of 67 min compared to control (N = 209; MD = − 67.72 [95% CI − 99.79 to − 35.64]) at day 21 with substantial heterogeneity (I² = 70%). Anabrees et al. [32] pooled the same three trials but found a mean reduction in crying time of 56 min (N = 209:MD = − 56.03; [95% CI − 59.92 to − 52.15], P < 0.00001, I² = 0%) favouring probiotics, which is a different pooled estimate and I² result. This appears to be due to differences in how the authors estimated means + SD from medians. Subgroup analysis of probiotics versus indistinguishable placebo showed a similar reduction in crying time at 21 days (MD = − 55.48 [95% CI − 59.46 to − 51.49], I² = 0%). In a separate analysis, probiotics were also shown to improve treatment success at 21 days (RR = 0.06 (95% CI 0.01 to 0.25), P < 0.000001, I² = 0%).

Urbanska et al. [33] and Xu et al. [34] restricted their analysis to trials of L. reuteri versus indistinguishable placebo only. Urbanska et al. [33] pooled three trials and found that L. reuteri DSM17938 reduced crying time by 43 min on day 21, (N = 244:MD = − 43.32 [95% CI − 67.62, − 19.02], P = 00005). Heterogeneity was substantial (I² = 79%). A subgroup analysis of two studies of just breastfed infants was conducted and a greater reduction in crying time of 56 min (I² = 0%) was found. Xu et al. [34] meta-analysed five trials and demonstrated that L. reuteri decreased crying time at 21 days by 45 min (WMD = − 45.83; [95% CI − 59.45 to − 32.2], P = 0.0001). Heterogeneity was moderate (I² = 57%). At 4 weeks, pooling three trials demonstrated a similar effect (WMD = − 56.32 min (95% CI − 89.49 to − 23.16, P = 0.001; I² = 87.7%). They also found that L. reuteri improved colic treatment effectiveness at three but not 4 weeks.

Schreck Bird et al. [35] pooled five trials of L. reuteri (ATCC55730 or DSM17938) versus either placebo or simethicone and found that there were more responders (infants with ≥ 50% reduction in crying/fussing time from baseline) in the probiotic group than the control (2–3-fold greater chance of responding: RR = 2.34, P = 0.01). A fixed-effects model demonstrated substantial heterogeneity (I² = 86.1%). Dryl et al. [36] assessed both probiotics (L. reuteri DSM17938, Lactobacillus rhamnosus GG4.5) and synbiotics and also found a reduction in the average crying /fussing time. Again, responders were defined as above (RR = 1.67[95% CI 1.10 to 2.51]).

The most up-to-date review was by Sung et al. [37] who compared L. reuteri DSM17398 versus placebo using individual participant raw data (IPD). Assessments took place at day 7, 14 and 21. The probiotic group averaged less crying and/or fussing time than placebo group at all time points. The results at day 21 using IPD were − 25.4 min (95% CI − 47.3 to − 3.5) P < 0.05 (adjusted for baseline). Intervention effects were particularly impressive in breastfed infants—MD = 46.4 min (95% CI − 67.2 to − 25.5, P < 0.05), but not so in formula-fed infants—MD = 41.0 (95% CI − 20.1 to 102.2, P > 0.05).

Probiotics were also discussed as part of four multiple CAM reviews [22‐25]. Both the NMA [25] and Harb et al.’s [24] meta-analysis supports the above findings that L. reuteri reduces crying time compared to placebo or simethicone (WMD = − 51.3 min (95% CI − 30.5 to − 72.2), P = 0.0001, I² = 42%; MD = − 55.84, 95% CI − 64.41 to − 47.26), I² = 77.1%, displayed respectively). Bruyas-Bertholon et al. [23] also found probiotics to be effective, whereas Perry et al. [22] did not; however, this latter review was conducted prior to the recent supportive evidence.

Several other CAMs were assessed as part of the multiple CAM reviews [22‐25]. Three trials favoured sugar solutions over either placebo control [59, 61], or no treatment [73]. Three trials [66, 73, 82] assessed massage, of which a pooled estimate of two trials [66, 82] demonstrated an effect. One trial on reflexology [67] found no difference compared to the control. Two trials assessed soy added to formula [60, 78], but it was not possible to report the pre-washout data [60] or distinguish the soy data from other supplements analysed.

With regards to the safety of the reported CAMs, there have been some concerns raised in recent years. In particular, manipulation therapies have come under scrutiny [41, 42] but serious adverse events are rare [43]. Reported adverse events from probiotics are generally mild gastrointestinal disorders such as abdominal cramping, nausea, diarrhoea, flatulence and taste alteration [44].

Poor reporting of adverse events (AEs) is a common criticism of CAM research [45]. It is particularly difficult in infants who cannot communicate their responses effectively. AEs in our included reviews were primarily based on parental reports. However, nine of the 16 reviews did report on AEs with the majority reporting that there were none. The acupuncture review [29] had the highest number of AEs from acupuncture (i.e. bleeding at acupoint, increased hiccoughing), although these are relatively minor. Just six reviews did not report or only partially report on AEs [23, 25, 27, 31, 32, 36]. In addition, several trials ignored safety issues by not providing the reasons why subjects dropped out. Also, due to the small sample sizes of the trials, it is difficult to draw definitive conclusions on safety.

The search was thorough and included grey literature searching. We believe the systematic approach taken in this overview limits bias. Difficulties in using both ROBIS and some questions on AMSTAR-2 may have led to errors in assessment.