Pacifier use and breastfeeding [1] is  an issue that is highly relevant to health professionals and families, for example this topic was the most accessed among Evidence Updates registrants (http://plus.mcmaster.ca/EvidenceUpdates) and it is relevant to one of the ten steps to successful breastfeeding of the WHO‐UNICEF Baby Friendly Hospital Initiative [2]. 

We believe that this Cochrane review, stating that pacifier does not reduce breastfeeding rates, is severely flawed and biased and therefore should be promptly revised. Here below is our criticism in detail. 

The analysis is based only on two randomized controlled trials (RCTs) [3,4]. Validity of the review authors conclusions is limited as they have excluded from the review a third RCT which shows an association  between pacifier use and breastfeeding discontinuation at four weeks [5]. The reason for this exclusion is reported as being that both groups were exposed to pacifier. Actually, the intervention group was exposed to pacifier soon after birth while the control group was advised to avoid pacifiers up to five weeks of life of the newborn. Therefore, data comparing breastfeeding practice before five weeks of life could have been appropriately included in the review, or at least commented on. 

In addition, the two studies included in the review were not designed to answer the clinical question about the effect of pacifier use for healthy full‐term newborns whose mothers have initiated breastfeeding and intend to exclusively breastfeed, on the duration of breastfeeding. These two trials assessed the effects on breastfeeding of interventions aimed at reducing the use of pacifiers; they did not assess the effect of pacifiers on breastfeeding. Mothers in the pacifier group used it in 71% of cases, while mothers in not pacifier group used it in 44% of cases (overall rates). Contamination between two treatment arms points to no difference or inconclusive results. Your conclusions of a null effect of pacifier on breastfeeding success based only on two studies with high contamination rate are therefore falsely reassuring. 

Major problems of the studies included in the review are insufficiently discussed. The larger of the two included studies (1021 infants out of a total of 1302) [3], has exclusion and inclusion criteria so strict that the population observed is extremely selected, limiting the external validity of the conclusions, which is not even mentioned. For example, participating hospitals had established breastfeeding programs, with early initiation of breastfeeding, lactation consultants, and unrestricted rooming‐in. Mothers were encouraged to avoid pacifier use until breastfeeding was well established. At term healthy infants, exclusively breastfeeding, whose mothers reported an intention to breastfeed for at least three months, not using pacifiers and with lactation well established at the age of 2 weeks were included. Exclusion criteria were breast problems that could interfere with breastfeeding (persistently sore nipples, mastitis, earlier breast surgery, and severely flat or inverted nipples). Mothers who communicated a preference in the introduction or not of a pacifier were also excluded. Further evidence that this study assessed an extremely selected population of women is the remarkably high rate of exclusive breastfeeding at three months for both groups (> 85%), much higher than the rate of exclusive breastfeeding at three months commonly seen in Europe (e.g. 47% in Italy in 2008, and in Sweden ranging between 68% at four months and 79% at two months in 2002) [6,7]. Finally the authors of the study powered the sample to perform an analysis based on intention to treat, but as the trial was non‐inferiority, the ‘according to protocol’ analysis would have been more appropriate [8]. Unfortunately, as the authors admit, the study sample was not sufficiently large to adequately perform this analysis. 

The second RCT included in the review also suggests that the null effect of pacifier on breastfeeding could be a false conclusion [4]. As there was a high contamination rate, results are presented based on actual exposure (observational analysis) in addition to the analysis based on randomized groups. This observational analysis showed a significant difference between pacifier users and not users for weaning by 3 months (RR: 1.9; 95%CI: 1.1, 3.3). Although observational studies are not reliable for assessing the association between pacifier use and breastfeeding practice, due to residual confounding and reverse causality, we think that RCTs with low compliance and high contamination, as in this study, cannot provide a valuable answer, especially when no differences among groups are detected. None of these issues were adequately discussed in this Cochrane review. 

Finally, we believe that a potentially very relevant conflict of interest in one of the trials included [3] was not mentioned: the authors of the study report as a funding source an association (the International Children Medical Research Association) whose characteristics are unclear, since it is not possible to find any information on it in the web. The only other citation of this association we have traced is a letter by Dr Peter PW Weiss to Pediatrics [9] criticizing a paper that reported a relationship between reduced pacifier use and reduced acute otitis media incidence. Is he maybe the same Peter Weiss, consultant for a manufacturer of pacifiers, that appears in the acknowledgment section of the trial report [3]? A Dr Peter Weiss is also the vice‐president (the president is unknown) of the International Children Medical Research Society, which is, maybe, another name of the International Children Medical Research Association, created in Switzerland by a company founded by the same manufacturers of pacifiers. Should this be made clear to the readers of the Cochrane review? 

Our view is that these issues raise questions about the validity of the conclusions of this Cochrane review.  Considering that Cochrane reviews represent a seal of quality among health professionals and the public, we think that it is responsibility of the Cochrane Collaboration to scrutinize the evidence selection, its critical appraisal and the validity of the conclusions, specially for a hot topic relevant for public health, as is the case for breastfeeding.

Simona Di Mario¹, Adriano Cattaneo², Vittorio Basevi¹, Nicola Magrini¹

¹ NHS CeVEAS, NHS Centre for the Evaluation of the Effectiveness of Health Care, WHO Collaborating Centre for Evidence‐based Research Synthesis and Guideline Development in Reproductive Health, Emilia‐Romagna, V. le L. Muratori 201, Modena, Italy, 41100
² Unit for Health Services Research and International Health, WHO Collaborating Centre for Mother and Child Health, Institute of Child Health, IRCCS Burlo Garofolo, Trieste, Italy

References

1. Jaafar SH, et al. Pacifier use versus no pacifier use in breastfeeding term infants for increasing duration of breastfeeding. Cochrane Database Syst Rev. 2011 Mar 16;3:CD007202. 
2. Kramer MS, et al; PROBIT Study Group (Promotion of Breastfeeding  Intervention Trial). Promotion of Breastfeeding Intervention Trial (PROBIT): a randomized trial in the Republic of Belarus. JAMA 2001;285:413‐20. 
3. Jenik AG, et al; Pacifier and Breastfeeding Trial Group. Does the recommendation to use a pacifier influence the prevalence of breastfeeding? J Pediatr 2009;155:350‐4.e1.
4. Kramer MS, et al. Pacifier use, early weaning, and cry/fuss behavior: a randomized controlled trial. JAMA 2001;286:322‐6.
5. Howard CR, et al. Randomized clinical trial of pacifier use and bottle‐feeding or cupfeeding and their effect on breastfeeding. Pediatrics 2003;111:511‐8.
6. Cuoghi C, et al. Prevalence of breastfeeding in Emilia‐Romagna Region in 2008. [Prevalenza dell'allattamento al seno in Emilia‐Romagna. Ricerca anno 2008] Fifth Edition. Bologna: Regione Emilia‐Romagna; 2010 [Italian].
7. Statistics Health and Diseases. Breast‐feeding, children born 2002. The National Board of Health and Welfare. Centre for epidemiology. Stockholm 2004 [Swedish, English summary].
8. Gøtzsche PC. Lessons from and cautions about noninferiority and equivalence randomized trials. JAMA 2006;295:1172‐4 9. Weiss PP, Nowak AJ. Pacifier as a risk factor for acute otitis media. Pediatrics 2002;109:351‐2.

Reply

We thank De Mario et al for their comments, and have responded in the order they made their comments.

We disagree that our review is ‘severely flawed and biased’. The protocol and review have been prepared according to Cochrane methods.

The study by Howard et al is excluded because the study population do not meet our inclusion criteria, as it included women who did not intend to breastfeed. Also, the results for breastfeeding duration are presented as adjusted odds ratios and the primary data are not reported.  Finally, our review did not have an outcome ‘breastfeeding at five weeks, as this is too short a duration to be clinically meaningful. Whilst preparing this response we noticed that the text in ‘types of participants’ was not as explicit as the text in our objectives. We have therefore modified ‘types of participants’ so that it matches the objectives. 

We agree our review is about the effect of recommending restricted pacifier use. For clarification we have modified the title of the review, and the background text. This clarification also means that contamination between the two intervention groups is no longer an issue. In addition, we disagree that contamination could have been the reason for the null effect. If the high baseline rate of pacifier use had any diluting effect on the final pooled results it would be very small, as the relative risks were consistently close to 1.00 with extremely tight confidence intervals. This is now clarified in the discussion.

Di Mario, Cattaneo, Basevi and Magrini wrote: Major problems of the studies included in the review are insufficiently discussed. The larger of the two included studies (1021 infants out of a total of 1302) [3] has exclusion and inclusion criteria so strict that the population observed is extremely selected, limiting the external validity of the conclusions, which is not even mentioned. For example, participating hospitals had established breastfeeding programs, with early initiation of breastfeeding, lactation consultants, and unrestricted rooming‐in. Mothers were encouraged to avoid pacifier use until breastfeeding was well established. At term healthy infants, exclusively breastfeeding, whose mothers reported an intention to breastfeed for at least three months, not using pacifiers and with lactation well established at the age of two weeks were included. Exclusion criteria were breast problems that could interfere with breastfeeding (persistently sore nipples, mastitis, earlier breast surgery, and severely flat or inverted nipples). Mothers who communicated a preference in the introduction or not of a pacifier were also excluded. Further evidence that this study assessed an extremely selected population of women is the remarkably high rate of exclusive breastfeeding at three months for both groups (> 85%), much higher than the rate of exclusive breastfeeding at three months commonly seen in Europe (e.g. 47% in Italy in 2008, and in Sweden ranging between 68% at four months and 79% at two months in 2002) [6,7]. Finally the authors of the study powered the sample to perform an analysis based on intention to treat, but as the trial was non‐inferiority, the ‘according to protocol’ analysis would have been more appropriate [8]. Unfortunately, as the authors admit, the study sample was not sufficiently large to adequately perform this analysis.

The report of Jenik 2009 does state this was a non‐inferiority trial. Whilst an ‘according to protocol analysis’ might have been appropriate for this trial, that is not relevant for this review as we specified we would use intention‐to‐treat analysis, which complies with Cochrane methods. We have included a paragraph in the discussion about external validity of the included trials.

We agree that the high contamination between intervention groups in Kramer 2001 may have had a diluting effect, and have included this in the discussion.

Jenik 2009 states that the sponsors had no role in any part of the study. However, the report does acknowledge helpful advice from Peter Weiss. We agree this may be the same Peter Weiss who is the vice president of the funding body, as well as a consultant for a pacifier company.  We have now included this information in the Table of ‘Characteristics of Included Studies’.

Contributors

Jacqueline J Ho, Sharifah Halimah Jaafar, Shayesteh Jahanfar

There is a mistake in this review. In the table of characteristics of included studies, Kramer 2001 is stated to have 140 women in the intervention group (avoid pacifiers), and 141 women in the control group (use a pacifier). Under incomplete data it states data were available for 127 women in the intervention group (avoid pacifiers) and 131 in the control group (use a pacifier). In the data analysis, data for this study from the intervention and control group are switched. It should be 44/131 for the use pacifier group (not 46/127) and 46/127 for the avoid pacifier group (not 44/131). This means that the total and risk ratio are also incorrect.

[Feedback received from Valérie Paulussen, 7 February 2012] 

Reply

We thank Valérie Paulussen for pointing out this mistake, which we have now corrected in this update. The correction does not alter or change the finding and conclusion of the review.

Contributors

Sharifah Halimah Jaafar