Description of the condition
Infantile colic is defined as paroxysmal (sudden, brief and repetitive), excessive, inconsolable crying for more than three hours a day, at least three days a week, for one week or more in an otherwise healthy baby (Wessel 1954; Roberts 2004; Savino 2007a). It is most frequently observed in infants between two weeks and four months of age. Colicky infants typically present with excessive and persistent crying that tends to occur in the evening, peaking at six weeks of age, associated with drawing up of the legs, tension of the body, flushing of the face and meteorism (the accumulation of gas in the lumen of the gastrointestinal tract associated with abdominal distension). The diagnosis is entirely clinical in nature. The infant's discomfort, expressed by crying, can be due to a variety of reasons ranging from benign to life threatening (Freedman 2009). Thus, all colicky infants should have a complete medical assessment in order to exclude underlying medical conditions that may require further evaluation and treatment. The natural history of infantile colic is believed to be self-limiting and symptoms generally improve by three to four months of age. Taking these aspects into consideration, hospital admission for these infants is unnecessary and should be discouraged (Savino 2007b). The prevalence of infantile colic ranges widely from 3% to 40% (Lucassen 2001), and fewer than 5% of distressed infants have identifiable medical explanations for their crying (Heine 2008).
Over the years, many studies have been conducted to determine the cause of this condition, even though its self-limiting nature has precluded the use of invasive investigations. Although the term ‘colic’ implies a gastrointestinal disease, the aetiology remains elusive and is most likely multifactorial (Savino 2007b). Gupta 2002 suggested roles for both behavioural factors (psychological and social) and biological components (food hypersensitivity or allergy, or both, and gut dysmotility), assuming that certain infants are predisposed to visceral hypersensitivity (enhanced sensation of pain from the internal organs of the viscera) and hyperalgesia (a state of abnormally increased sensitivity to pain) in the first weeks of life. In particular, it has been observed that a subset of infants with severe colicky symptoms suffer from cow’s milk allergy and, in these infants, dietetic treatment should be the first therapeutic approach (Iacono 2005). Colic has been found to be more frequent in formula-fed infants than in breast-fed infants (Cohen 2012). Infant colic not only results in increased crying time but is also related to long-term outcomes, such as maternal sensitivity, separation anxiety, temper tantrums and altered sleep patterns (Stifter 1998). While there appears to be no negative effect of infant colic on maternal behaviour, there is some evidence that mothers are affected personally by their interactions with an inconsolable child. The study by Stifter 1998 also reported that mothers of infants who had colic rated themselves as less competent than mothers of infants who did not have colic .
Recently, data supporting the concept of aberrant gut microbiota in infants with colic have been presented, suggesting its influence on gut motor function and gas production (Savino 2009), and possibly emphasising an inflammatory origin for the condition (Savino 2006). Considering the lack of a unifying theory in the pathogenesis of infantile colic, probiotics may offer a promising therapeutic direction.
Description of the intervention
Various therapeutic interventions have been used for infant colic, including simethicone, herbal remedies such as fennel extract and chamomile, sucrose and glucose solutions, manipulation (Dobson 2012), massage and reflexology. Recently, the role of aberrant gut flora in infant colic has resulted in the study of probiotics in this area. Probiotics are orally administered live organisms with potential health benefits to the host. Lactobacillus and Bifidobacterium species are the organisms most commonly used as probiotics. The definitions of probiotic and related interventions are as follows.
Probiotic: an oral supplement or a food product that contains a sufficient number of viable micro-organisms to alter the microflora of the host and has the potential for beneficial health effects (CAST 2010; FAO 2010).
Prebiotic: an indigestible food ingredient that benefits the host by selectively stimulating the favourable growth or activity, or both, of one or more indigenous probiotic bacteria (Roberfroid 2007; CAST 2010; FAO 2010).
Synbiotic: a product that contains both probiotics and prebiotics. Evidence for synergy between a specific prebiotic and a probiotic in the product is not essential. Synbiotics may be separate supplements or may exist in functional foods as food additives (CAST 2010; FAO 2010).
Functional food: any modified food or food ingredient that provides a health benefit beyond that ascribed to any specific nutrient(s) it may contain. It must remain a food, and demonstrate its effect in amounts normally expected to be consumed. Benefits may include functions relevant to improving health and well-being or reducing risk of disease, or both. Any food that contains probiotics or prebiotics is a functional food. An example of a functional food is live-culture yogurt that contains probiotic bacteria, prebiotics and other dietary nutrients.
Probiotics may also be delivered by means of faecal bacteriotherapy via the rectal route. These probiotics have been studied in adults, but there are no current data on probiotics delivered by the rectal route in infants.
Safety of probiotics
Probiotic sepsis, long-term altered immune responses and the development of antibiotic resistance are the main concerns with probiotic therapy. Hempel 2011 reported a comprehensive survey assessing the safety of Lactobacillus, Bifidobacterium, Saccharomyces, Streptococcus, Enterococcus and Bacillus strains in the prevention, treatment or risk reduction of disease in humans (including children, adults and the elderly). Their search identified 11,977 publications, of which 622 were included in the review. In 235 studies, only non-specific safety statements were made; the remaining 387 reported the presence or absence of specific adverse events. The studies primarily assessed Lactobacillus alone or in combination with other genera, often Bifidobacterium. Many case reports described fungaemia and bacteraemia as potentially associated with probiotic organisms. Randomised controlled trials (RCTs) showed no significant, increased risk of adverse events associated with short-term probiotic use. Long-term effects remained largely unknown. There was a lack of assessment and systematic reporting of adverse events. Rare adverse events were difficult to assess. They concluded that the current literature is not well equipped to answer questions on the safety of probiotics with confidence.
Ha 1999 systematically reviewed the safety of Lactobacillus and Bifidobacterium as probiotics. Their search revealed many case reports (Husni 1997; Ha 1999; Rautio 1999; Kunz 2004) of sepsis due to Lactobacillus but none from RCTs of probiotics. Systemic probiotic infection was rarely reported with Bifidobacterium. Serious probiotic infections have been reported mostly in high-risk individuals, particularly those who are debilitated, immunocompromised and with indwelling catheters or devices (Broughton 1983; Kalima 1996; Perapoch 2000; Thompson 2001; Salminen 2002; Soleman 2003; Kunz 2004; Salminen 2004; Boyle 2006; Ohishi 2010; Jenke 2012). The American Academy of Pediatrics has also voiced concern as regards the use of probiotics in children with such risk factors (Thomas 2010). It is, however, important to note that prospective studies indicate the safety of probiotics in immunocompromised adults and children with human immunodeficiency virus, and also in preterm, very-low birthweight neonates (Cunningham-Rundles 2000; Salminen 2004; Alfaleh 2011).
A systematic review (Reddy 2013) has reported that there is insufficient evidence on the effects of probiotics in children with short bowel syndrome (SBS) where the risk of adverse effects, such as probiotic sepsis, is high. Overgrowth of commensal lactobacilli can be a feature of individuals, including children, with SBS, and is frequently associated with D-lactic acidosis (Bongaerts 1997). D-Lactic acidosis has been reported in a five-year-old girl with SBS receiving probiotic supplementation containing Lactobacillus acidophilus (suspected causative agent), Lactobacillus bulgaricus, Streptococcus faecalis andStreptococcus faecium (Munakata 2010), which improved after discontinuing the probiotic. Ku 2006 reported a five-year-old boy with SBS who developed recurrent episodes of D-lactic acidosis whilst on L. acidophilus and Bifidobacterium infantis, which resolved when enteral feeds were interrupted. He developed further episodes when his milk formula was inadvertently changed to one containing L. acidophilus and Bifidobacterium spp. (Ku 2006). Consumption of probiotic strains that produce L-lactate exclusively is not likely to present a problem for such infants and may be useful in their treatment (Vanderhoof 1998).
Probiotic prophylaxis with Lactobacillus rhamnosus GG (LGG) has been reported to reduce the frequency of atopic dermatitis (Kalliomäki 2001) in neonates. However, recent trials have reported no such benefits in neonates after supplementation with LGG and L. acidophilus (Ha 1999). Moreover, an unexpected increase in recurrent wheezing bronchitis was observed in children who received LGG (Kopp 2008; Kopp 2009). Taylor 2007 administered L. acidophilus (LAVRI-A1) to newborns for the first six months of life. There was no effect on the prevention of atopic dermatitis, but an increased rate of sensitisation was observed in the probiotic group versus the control group. However, at follow-up, the higher rates of sensitisation seen previously at one year of age in the probiotic group were no longer apparent after the third year of life (Taylor 2007; Prescott 2008). Skin prick test (SPT) responses to three different probiotic preparations (Fiorilac®, Dicoflor® and Reuterin®) were evaluated in addition to relevant food allergens in children with cow's milk allergy (Bruni 2009). The proportion of SPT reactions to all tested probiotic products was significantly lower than to cow's milk. Significantly higher sensitisation was observed for Fiorilac versus Dicoflor and versus Reuterin. It was recommended that probiotic use in individuals with cow's milk allergy has to be limited to products that do not contain milk. It was advised that, in selected individuals, a screening SPT with the product is important to evaluate its potential contamination with milk. Martín-Muñoz 2012 investigated the safety of probiotics in individuals with food allergies. Their results indicated that commercially available probiotic compounds may contain hidden food allergens and may not be safe for those with cow's milk or hen's egg protein allergy.
Many lactobacilli strains are naturally resistant to vancomycin (Borriello 2003). The vancomycin resistance genes of Lactobacillus species appear to be chromosomally located and are not easily transferable to other genera (Tynkkynen 1998). Another potential concern is the transfer of plasmid-mediated antibiotic resistance (e.g. tetracycline resistance through a Lactobacillus reuteri strain (Rosander 2008). However, follow-up studies have not indicated antibiotic resistance as a concern, despite the adoption of probiotics on a population level in Finland (Salminen 2002).
Overall, the current evidence indicates that probiotic lactobacilli and bifidobacteria are safe and well tolerated by healthy infants and children, and have no adverse events (Vanderhoof 1998; Pedone 1999; Saavedra 1999; Cunningham-Rundles 2000; Guandalini 2000; Borriello 2003; Petschow 2005). However, considering that their associated risk is not zero, monitoring for adverse events is important even when probiotics are used in otherwise healthy infants with colic.
How the intervention might work
It is hypothesised that infant colic may have medical (organic) or behavioural causes. Among the organic causes, a role for intestinal lactobacilli and a coliform colonisation pattern has been suggested and proposed in the pathogenesis of infantile colic (Savino 2004; Savino 2005; Rhoads 2009; Savino 2009).
Experimental studies suggest a possible mechanism of action of L. reuteri through an improvement in gut motility and function, and direct effects on visceral pain. It has been demonstrated that L. reuteri acts on colon motility by targeting ion channels in enteric sensory nerves (Kunze 2009). More recently,L. reuteri ingestion has been shown to enhance the tonic inhibition of rat colon contractile activity by acting via the intermediate conductance calcium-dependent potassium channel IK
Specific data about the differential effects of probiotics versus probiotic-supplemented infant formula are not currently available, although LGG (as a part of hydrolysed formula) has been shown to decrease faecal calprotectin and improve recovery in infants with blood in their stools and presumptive allergic colitis compared with hydrolysed formula alone (Baldassarre 2010). Currently, two infant formulas contain probiotics: one contains Bifidobacterium lactis and the other LGG. These probiotics are added only to powdered formula at present. The overall health benefit of adding probiotics to infant formula remains to be demonstrated in large RCTs. The effects of probiotics are strain specific (Kirjavainen 1999; Luyer 2005) and their dose-response relationships have been documented in studies (Gill 2001; Larsen 2006; Gao 2010).
Why it is important to do this review
Infantile colic is a common disorder with a prevalence of 3% to 28% in neonates and infants between two weeks and four months of age (Keefe 2006; Savino 2010).The pathogenesis of colic is poorly understood and involves a range of risk factors. Simethicone, the best available and most commonly prescribed treatment for infant colic, has been found to be no more effective than placebo (Garrison 2000; Lucassen 2000; an up-to-date review of the evidence is being carried out Savino 2012a). Gut flora has been recently proposed to play an important role in the pathogenesis of colic (Savino 2007b). Observational studies and clinical trials report probiotics to be beneficial in the treatment of colic (Savino 2010). A recent systematic review on nutritional supplements and complementary medicine in infant colic showed that, although some encouraging results exist for fennel extract, mixed herbal tea and sugar solutions, design flaws and the absence of independent replications preclude practice recommendations (Perry 2011). The methodology of the Perry 2011 review was not rigorous and did not include some recent trials.
Considering the impact of the condition, the increasing scope of oral probiotics in the field of neonatology (necrotising enterocolitis) and paediatrics (allergic enteritis) (Baldassarre 2010; Deshpande 2010; Deshpande 2011), as well as the relatively low cost and easy availability of probiotics, we believe it is important to evaluate the current evidence of probiotics in the field of infant colic, in terms of both effectiveness and safety, using the rigorous methodology of a Cochrane systematic review.
To systematically assess the efficacy and adverse effects of oral probiotics in reducing colic in infants less than six months of age.
Criteria for considering studies for this review
Types of studies
RCTs and quasi RCTs.
Types of participants
Inclusion criteria: infants up to six months of age, however fed, with a clinical diagnosis of infant colic that satisfies the modified Wessel’s criteria (Wessel 1954) of at least three hours of crying time per day, for at least three days, for at least a week, prior to enrolment in a trial.
Exclusion criteria: i) preterm infants, ii) infants with clinical chronic gastrointestinal illnesses such as gastro-oesophageal reflux disease, iii) infants who have received antibiotics or probiotics during the period preceding the administration of trial probiotics.
Types of interventions
Oral probiotics of any strain, dose or duration, in any form (i.e. as part of synbiotics or as a functional food in probiotic-supplemented infant formula), compared with conventional care (e.g. simethicone), placebo or no treatment. We will include studies in which probiotics were delivered in conjunction with conventional care versus conventional care alone.
We will exclude studies that involve (i) dietary modifications to the mother's diet and (ii) education interventions that instruct such modifications. For further information on these interventions, we direct authors to the following Cochrane Review 'Dietary modifications for infantile colic' (Savino 2012b).
Types of outcome measures
- A reduction in the duration of crying (post-treatment versus baseline)*. Data may be continuous (e.g. hours per day), or dichotomous (e.g. reduction to below a pre-defined threshold as determined by the trial authors).
- The number of responders in each group after treatment*. Responders will be defined as those who experienced a decrease in the daily, average crying time of 50% from baseline* (dichotomous outcome).
- Reduction in frequency of crying episodes per 24 hours (post treatment versus baseline)* dichotomous outcome.
- Parental or family quality of life, including measures of parental anxiety , stress or depression* (continuous outcome).
- Infant sleep duration per 24 hours at 7, 14, 21 days* (post treatment versus baseline), (continuous outcome).
- Parental satisfaction measured by Likert scale or NRS (Numeric Rating Scale), (continuous outcome).
- Adverse effects: constipation,* vomiting,* sepsis (including probiotic strain sepsis),* diarrhoea, apnoea, ALTE (apparent life threatening event) (dichotomous variable).
- Intestinal microflora analysis to determine the effect of the probiotic on selected intestinal microbiota
Outcomes marked with an asterisk will be used to populate the 'Summary of findings' table.
Search methods for identification of studies
We will search the following databases:
- Cochrane Central Register of Controlled Trials (CENTRAL);
- Ovid MEDLINE;
- Ovid MEDLINE In-Process and Other Non-Indexed Citations;
- Science Citation Index;
- Social Sciences Citation Index;
- Cochrane Database of Systematic Reviews;
- Database of Abstracts of Reviews of Effects (DARE);
- Conference Proceedings Citation Index-Science;
- Conference Proceedings Citation Index-Social Science and Humanities;
- WorldCat (limited to theses);
- Networked Digital Library of Theses and Dissertations (ndltd.org/);
- DART-Europe E-theses Portal (dart-europe.eu/);
- TROVE (limited to theses) (trove.nla.gov.au/);
- MetaRegister of Controlled Trials (controlled-trials.com);
- ClinicalTrials.gov (clinicaltrials.gov);
- Australian and New Zealand Clinical Trials Registry (anzctr.org.au);
- World Health Organization International Trials Registry Platform (apps.who.int/trialsearch)
- PubMed Dietary Supplement Subset (ods.od.nih.gov/Research/PubMed_Dietary_Supplement_Subset.aspx
The search strategy below will be used in Ovid MEDLINE and adapted for the other databases.
3 ((stomach or abdominal or abdomen$) adj3 (spasm$ or pain$ or cramp$)).tw.
4 ((gastric or gastro$) adj3 (spasm$ or pain$ or cramp$)).tw.
6 (cry or crying or cries).tw.
10 Complementary Therapies/
11 Dietary Supplements/
12 Gastrointestinal Agents/
13 exp lactobacillaceae/
15 exp Bifidobacterium/
18 exp Saccharomyces/
22 Lactic acid bacteria$.tw.
23 (Biogaia or Culturelle or Enflora$ or Florastor or ((Gerber$ or Nestle$) adj2 (Goodstart or Good Start)) or Nutramigen or VSL?3).tw.
24 (Baby$ Bliss or Baby$ Own or Colic Calm or Colic Ease or colic drops or Colief or Dentinox or Gripe Water or Infacol or Little Tummy$).tw.
26 exp infant/
27 (baby or babies or infant$ or child$ or newborn$ or neonat$).tw.
28 26 or 27
29 7 and 25 and 28
Searching other resources
References from published studies
We will scan the bibliographies of included and excluded studies for possible references to RCTs.
In addition to searching the trials registers and theses repositories listed above, we will obtain additional information on unpublished, ongoing trials via correspondence with trial authors. We will also contact the manufacturers of relevant probiotics (including Biogaia®, Culturelle®, Florastor®, Mead Johnson®, Nestle®). We will search the world wide web using Bing, Google and Google Scholar using the search criteria described above to identify grey literature. When relevant unpublished or ongoing studies are identified, we will then attempt to obtain sufficient details to incorporate them in the review.
We will handsearch the abstracts of meetings of the Pediatric Academic Societies - Society for Pediatric Research and Pediatric Gastroenterology for further RCTs.
We will search for adverse effects of probiotics used in the treatment of infant colic. For common adverse event data we will use RCT data only. Formulating a separate search and strategy for rare adverse events in studies with other designs is outside the purview of the current review. Any findings will be summarised qualitatively in the 'Discussion' section of the review.
We will not impose any language restrictions and we will seek translations where applicable.
Data collection and analysis
Selection of studies
Two review authors (VP and SP) will independently select studies for inclusion in the review. We will screen the search results using titles of papers and abstracts when available. We will retrieve the full text of the selected articles and assess them for inclusion according to prespecified selection criteria. We will measure inter-rater reliability using kappa statistics and we will explore reasons for disagreement between reviewers based on the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).
Data extraction and management
Two authors (GD, VP) will independently extract the following data using a standardised data extraction form: author, year of publication, language, study setting, funding source, definition and diagnostic criteria for infant colic, inclusion and exclusion criteria for participants, participant characteristics (age, preterm or term, gender, diagnosis), probiotic, synbiotic or probiotic-supplemented formula (strain, dose, frequency, duration), outcome measures (mean daily duration of crying, number of inconsolable crying episodes, number of responders at various time periods, intestinal microflora analysis using fluorescence in situ hybridisation, number of adverse events (sepsis, vomiting, constipation, diarrhoea), number of participants allocated to each group, presence or absence of intention-to-treat analysis (whether participants for whom data were available were analysed as randomised), participants lost to follow up and reasons for loss to follow up, information about methods of imputation and measures of compliance. When necessary, we will individually contact the lead authors of studies that do not report relevant statistical data such as odds ratios (OR) and standard errors. Any differences of opinion will be resolved by team authors, SP and GD.
Assessment of risk of bias in included studies
Two authors (VP and SP) will independently assess the risk of bias in each included trial for the following six components: sequence generation, allocation concealment, blinding or masking, incomplete outcome data, selective outcome reporting and other biases. For each of these components, we will assign an assessment of risk of bias as high, low or unclear (Higgins 2011b). These assessments will be analysed independently by the other authors (GP and SP). We will resolve differences by discussion. We will attempt to contact the trial authors for clarification when methodological details are unclear. We will record these assessments in standard 'Risk of bias' tables in Review Manager (RevMan) 5 (Review Manager 2011) and summarise them in a 'Risk of bias' figure and graph. We will use these assessments in making judgements about overall study quality when preparing 'Summary of findings' tables.
We will assess randomisation as at 'low risk of bias' if the procedure of sequence generation was explicitly described and considered adequate to produce comparable groups. Examples include computer-generated random numbers, a random numbers table or coin tossing. We will assess randomisation as at 'high risk of bias' if sequence generation was based on participant record numbers, date of birth, day or week of presentation or alternation. If the authors of the trial mention randomised sequence generation without completely defining the actual process, we will assess the trial as at 'unclear risk of bias'.
We will assess concealment of treatment allocation as at 'low risk of bias' if the procedure was explicitly described and adequate to ensure that intervention allocations could not be foreseen in advance of, or during, enrolment. Examples include centralised randomisation, numbered or coded containers or sealed envelopes. We will assign a 'high risk of bias' to studies in which inadequate procedures were applied, such as alternation or references to case record numbers or dates of birth. We will assign an 'unclear risk of bias' if there is insufficient information to permit a judgement of either a 'low risk of bias' or a 'high risk of bias' to be made (e.g. the use of assignment envelopes is described but it is unclear that they were sequentially numbered, opaque and sealed).
Blinding of participants, clinicians and outcome assessors
We will assess the risk of bias associated with the blinding of participants, clinicians and outcome assessors based on the likelihood that such blinding is sufficient to ensure that the outcome assessors (usually parents) had no knowledge of which intervention the infant received. Blinding of infants is not, of course, considered necessary in the infant study population. We will assign a 'high risk of bias' to studies that used no or incomplete blinding, or in which there is a likelihood that the binding was broken. We will assign an 'unclear risk of bias' if there is inadequate information to permit a judgement of either a 'low risk of bias' or a 'high risk of bias' to be made, or if the study does not address the outcome.
Incomplete outcome data
We will assess the reporting of incomplete outcome data as at '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 assess the reporting of incomplete outcome data as at 'high risk of bias' in case of one or more of the following situations:
i) if a difference in the proportion of incomplete outcome data across groups is determined by a participant's true outcomes;
ii) if the reasons for missing outcomes differ among the groups;
iii) the proportion of missing outcome data when compared to observed event risk is sufficient to cause clinically relevant bias in the intervention size estimate;
iv) in the case of studies that report 'as-treated analyses' with substantial departure from the intervention assigned at the time of randomisation;
v) in the case of the potentially inappropriate imputation of missing outcomes data as if they were real measurements.
We will assess the reporting of incomplete outcome data as at 'unclear risk of bias' if there is insufficient reporting of attrition or inclusion data, or both, to permit a judgement of either a 'low risk of bias' or a 'high risk of bias' to be made (i.e. if unstated numbers are randomised or reasons for missing data are not provided or if the study did not address the outcome).
If all of the outcomes mentioned in the Methods section of the study article have been reported in the Results section then we will assess selective reporting to be at 'low risk of bias'. We will also look at different reported versions of the same study, including protocols, and examine them for any evidence of selective outcome reporting. We will assign a 'high risk of bias' if not all of the study's prespecified outcomes are reported, outcomes are reported using subscales that were not prespecified or if key outcomes are excluded. The criterion for a judgement of an 'unclear risk of bias' will be insufficient information to permit a judgement of either a 'high risk of bias' or a 'low risk of bias' to be made.
Other potential threats to validity
We will assess other threats to validity as at 'low risk of bias' if the study appears to be free of other sources of bias, such as the study being stopped prematurely due to a data-dependent process or 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 the study as at 'unclear risk of bias'. A 'high risk of bias' will be assigned if the study has a potential source of bias relating to a specific type of study design or if the study was claimed to have been fraudulent. The review authors will not be blinded to the titles of the journals or the identities of the authors, as they are familiar with the field.
Measures of treatment effect
For dichotomous outcomes, we shall use OR and 95% confidence intervals (CI).
For continuous outcomes assessed using the same rating scale in all studies in the comparison, we shall use the mean difference with 95% CI; where different rating scales have been used to measure the same outcome for a comparison, we shall extract the mean values and their standard deviations, and combine them using the standardised mean difference (SMD).
Unit of analysis issues
We shall use the statistical methods described by Higgins 2008 if cluster-randomised trials are included in this review. If included trials are randomised by clusters, and the results have been adjusted for clustering, then we will combine the adjusted measures of effects of these cluster-randomised trials. If results have not been adjusted for clustering, we will attempt to adjust the results for clustering by multiplying the standard errors of the estimates by the square root of the design effect, where the design effect is calculated as DEff = 1 + (M - 1) ICC, where M is the average cluster size and ICC is the intra-cluster coefficient (an estimate of the relative variability within and between clusters within the studies) (Donner 1980). We will attempt to obtain the ICC from the article and if it is not available we will use external estimates obtained from similar studies. Subsequently, the estimates and their corrected standard errors from the cluster-randomised trials will be combined with those from parallel-group designs using the generic inverse variance method in RevMan 5 (Review Manager 2011). If necessary, we shall seek statistical advice from the editorial base of the Cochrane Developmental, Psychosocial and Learning Problems Group (CDPLPG).
Data from cross-over trials will be pooled according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c). The mean of the within-participant difference and the standard error of the mean difference will be entered into RevMan 5 (Review Manager 2011) using the generic inverse outcome type. Where the standard error of the difference in means is not reported, the original data will be requested from study authors or the value will be imputed. Correlation coefficients will be calculated from studies where sufficient data are available and, if consistent, will be used to calculate the missing standard errors for other studies.
The analysis of a cross-over trial should take advantage of the within-person design, and use some form of paired analysis (Elbourne 2002). In the presence of carry-over in cross-over trials, a common strategy is to base the analysis on only the first period. Although the first period of a cross-over trial is, in effect, a parallel-group comparison, use of data from only the first period will be biased if, as is likely, the decision to do so is based on a statistically significant test of carry-over. Cross-over trials for which only first period data are available will be considered to be at risk of bias, especially when the two-stage strategy is used. This ‘two stage analysis’ has been discredited (Freeman 1989) but is still used. Also, use of the first period data only removes the main strength of the cross-over design, the ability to compare treatments within individuals.
Although trial authors may have analysed paired data, poor presentation may make it impossible for review authors to extract paired data. Unpaired data may be available and, generally, will be unrelated to the estimated treatment effect or statistical significance. While this is not a source of bias, it usually leads to a trial getting (much) less than its due weight in a meta-analysis.
Dealing with missing data
We shall attempt to obtain unreported missing data from the trial's corresponding author. Where possible, we will extract data to allow an intention-to-treat analysis in which all randomised participants are analysed in the groups to which they were originally assigned, regardless of whether or not they received the allocated intervention. If there is discrepancy in the numbers randomised and in the numbers analysed in each treatment group, we will calculate and report the percentage lost to follow-up in each group. If dropouts exceed 10% for any trial, we shall assign a worse outcome to those lost to follow-up for dichotomous outcomes and assess the impact of this in sensitivity analyses with the results of completers.
For continuous data that are missing standard deviations, we will either calculate these from other available data, such as standard errors (SE), or we will enter them using methods suggested by Higgins 2011b. We shall not make any assumptions about losses to follow-up for continuous data and we shall analyse results for those who complete the trial. We will perform a sensitivity analysis by calculating the treatment effect including and excluding the imputed data to determine whether they altered the outcome of the analysis. Where studies do not report response rates, values will be imputed using the method described in Furukawa 2005.
If the relevant studies do not report OR or standard errors, or both, then we will contact the authors for raw data (numbers of events and denominators for outcomes of interest) for both arms of the study) and use these to derive the summary data such as OR (Odds ratio), RR (Relative risk) and 95% CI.
Where it is not possible to obtain missing data, we will record this in the Data Collection Form, report it in the 'Risk of bias' table and discuss the extent to which the missing data could alter the results of the review.
We will look for attrition in all of the included studies and we will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analyses.
Assessment of heterogeneity
We will assess the following sources of heterogeneity: clinical heterogeneity (e.g. differences in study participants; interventions); methodological heterogeneity (e.g. differences in study design, randomisation concealment, blinding of outcome assessment, losses to follow up) and statistical heterogeneity.
We will assess heterogeneity between the trials by visually examining the forest plot to check for overlapping CI, using the Chi
In general, we shall interpret an I
The classic measure of heterogeneity is Cochran's Q, which is calculated as the weighted sum of squared differences between individual study effects and the pooled effect across studies, with the weights being those used in the pooling method. Q is distributed as a Chi
We will use the random-effects model. This assumes that the effects being estimated in the different studies are not identical but follow some distribution. The model will represent our lack of knowledge about why real, or apparent, intervention effects differ by considering the differences as if they were random. The centre of the distribution will describe the average of the effects, and its width, the degree of heterogeneity. RevMan implements a version of random-effects meta-analysis as described by DerSimonian and Laird (DerSimonian 1986).
Assessment of reporting biases
We will assess all included studies for the adequacy of reporting of data for prestated outcomes and for selective reporting of outcomes. We will attempt to obtain the results of any unpublished studies in order to compare results extracted from published journal reports with results obtained from other sources. We will base our judgements on the risk of selective reporting in the 'Risk of bias' tables for each included study. We will assess the likelihood of potential publication bias using funnel plots (Egger 1997), as recommended in the Cochrane Handbook of Systematic Reviews of Interventions (Sterne 2008), provided that there are at least 10 trials in a forest plot assessing a particular outcome. Asymmetry in a funnel plot may be due to reasons other than publication bias, such as small-study effects, heterogeneity and chance. We will then apply the Egger's test.
If two or more studies prove suitable for inclusion (i.e. are similar in i) type of probiotic species, ii) type of primary outcome and iii) type of colic) we will perform a meta-analysis of the results. In other words, if two or more studies assess the effects of a probiotic in otherwise healthy infants with colic and both measure daily crying time, then we will perform a meta-analysis. If there are common characteristics, we will group studies and further investigate by using subgroup analyses (see below). As we anticipate clinical heterogeneity to impact our results given the wide scope of the types of interventions included, we will use the random-effects methods as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 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” (Higgins 2008) and we will apply the mean difference approach where data allow. If studies measure the same outcome using different scales, we will apply the SMD approach.
For dichotomous outcomes, we will perform a meta-analysis of OR and a calculation of the number needed to treat for an additional beneficial outcome, since these (in combination) provide good consistency, mathematical properties and ease of interpretation (Higgins 2008).
If both continuous and dichotomous outcome data are available for a particular outcome, then we will include only continuous data in the primary analysis. If one study reports outcome data as dichotomous data while another reports the same outcome as continuous data, we will convert the former from OR to SMD, provided the continuous data have an approximate normal or logistic distribution. If not normally or logistically distributed, then we will conduct separate analyses.
We will base the assumed control-group risks on an assessment of typical risks, calculated from the control groups in different participant 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.
If the studies are too heterogeneous to preclude data synthesis then we will conduct a narrative analysis on the different studies and explore the reasons for such differences in the studies.
Skewed data: we will look at the availability of transformed data in a log scale, if reported by the trials. We will collect appropriate data summaries and individual participant data from the trialists, and consult the statistician of the CDPLPG for appropriate analysis strategies.
We will carry out statistical analysis using RevMan software (Review Manager 2011).
Subgroup analysis and investigation of heterogeneity
If moderate heterogeneity is detected, and if data permit, the following subgroup analyses will be carried out for each comparison and outcome.
- Type of probiotic, synbiotic or probiotic-supplemented infant formula.
- Dosage of probiotic.
- Type of feeding: infants on both breast milk and formula feeds will be grouped according to the predominant type of feed: A) infants receiving more than 85% feeds comprising breast milk will be grouped as predominantly breast-fed babies; B) infants receiving more than 85% feeds comprising formula will be grouped as predominantly formula-fed babies.
- Outcome time points: based on the clinical course of infant colic, we will define outcome time points as short term if the infant is younger than six months of age and long term if the infant is older than six months of age.
Where data permit, we will conduct sensitivity analyses to determine whether findings are sensitive to restricting inclusion to studies judged to be at low risk of bias. In these analyses we will limit inclusion to those studies that: have a low risk of selection bias (associated with sequence generation or allocation concealment), performance bias (associated with issues of blinding), and attrition bias (associated with completeness of data), and are published.
We shall undertake sensitivity analyses if trials report dropout rates of 10% or greater in order to ascertain differences in outcomes between intention-to-treat analyses (all dropouts will be assigned to the worst outcome for dichotomous outcomes) and analyses of completers. If the results of these analyses differ significantly with relation to direction of effect, we shall perform two additional analyses:
- a best-case scenario favouring probiotics (i.e. none of the dropouts from the probiotics arm had the unfavourable outcome but all dropouts from the control group had the outcome);
- a worst-case scenario favouring the control (i.e. all the dropouts from the probiotics arm had the unfavourable outcome but none from the control group had this poor outcome).
We shall report the results of all such analyses.
In addition, we shall undertake sensitivity analyses for any outcomes from cluster-randomised trials where ICCs were used from external sources, or where missing standard errors of the differences in means from cross-over trials were imputed.
The protocol was produced within the CDPLPG.
Contributions of authors
Vijayakumar Praveen, Shama Praveen - prepared the initial draft of the protocol.
Sanjay K Patole, Girish Deshpande - reviewed the protocol.
Vijayakumar Praveen, Sanjay K Patole - reviewed search results.
Declarations of interest
Vijayakumar Praveen - none known.
Sanjay K Patole - none known.
Shama Praveen - none known.
Girish Deshpande - I am the principal investigator for the project Probiotics for Preterm Neonates, which is conducted at the Nepean Neonatal Intensive Care Unit, Sydney, Australia. This project is partly funded by the Nepean Neonatal Parents Support Group ($5000 for year 2011 to 2012).