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ORIGINAL RESEARCH COMMUNICATION |
1 From the Koret School of Veterinary Medicine, the Hebrew University of Jerusalem, Rehovot, Israel (EK and AJ); the Center for Vaccine Development and Evaluation, Israel Defense Forces, Ramat-Gan, Israel (EK, RVC, and JB); the Pediatric Gastroenterology Unit, Dana Children's Hospital, Tel-Aviv Sourasky Medical Center, Tel-Aviv, Israel (SR); and the Sackler Faculty of Medicine, Tel-Aviv University, Tel Aviv, Israel (SR)
2 Supported by the Tel-Aviv Sourasky Medical Center. 3 Reprints not available. Address correspondence to E Klement, Koret School of Veterinary Medicine, The Hebrew University of Jerusalem, Pob 12, Rehovot, Israel. E-mail: klement{at}agri.huji.ac.il.
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ABSTRACT |
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 TOP ABSTRACT INTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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Objective: The aim of this meta-analysis was to examine the role of breastfeeding in preventing inflammatory bowel disease and to summarize the evidence gathered about this subject.
Design: A meta-analysis was performed on 17 relevant articles that were found by using MEDLINE, EMBASE, the Internet, and articles' references. The publications were fully reviewed and divided, on the basis of their quality, into 3 groups.
Results: Studies showed heterogeneous results. The pooled odds ratios of all the 17 reviewed studies, calculated according to the random-effects model, were 0.67 (95% CI: 0.52, 0.86) for Crohn disease and 0.77 (0.61, 0.96) for ulcerative colitis. However, only 4 studies for Crohn disease and 4 for ulcerative colitis were eventually included in the highest quality group. In this group, the pooled odds ratio was 0.45 (0.26, 0.79) for Crohn disease and 0.56 (0.38, 0.81) for ulcerative colitis.
Conclusions: The results of this meta-analysis support the hypothesis that breastfeeding is associated with lower risks of Crohn disease and ulcerative colitis. However, because only a few studies were graded to be of high quality, we suggest that further research, conducted with good methodology and large sample sizes, should be carried out to strengthen the validity of these observations.
Key Words: Crohn disease • ulcerative colitis • breastfeeding • meta-analysis • epidemiology
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INTRODUCTION |
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TOPABSTRACTINTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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To determine which environmental factors contribute to the development of CD or ulcerative colitis (UC), numerous epidemiologic studies were performed (4-7). Factors such as smoking (8) and use of oral contraceptives (9) were meta-analyzed to determine their role on the risk of IBD development.
In this meta-analysis, we evaluate another factor, ie, the effect of breastfeeding, on the later development of UC and CD. The reasoning is 3-fold. First, breastfeeding protects against many immune-mediated diseases such as bronchial asthma (10), atopic dermatitis (11), allergic rhinitis (12), and type 1 diabetes mellitus (13). This effect is attributed to the immunomodulatory properties of human milk. From here we hypothesized that if the immunomodulatory effect of breastfeeding offers protection against these diseases, it is plausible to assume similar protection with regard to UC and CD. Second, the infant is exposed to human milk while developing an immune system, which seems to be important in procuring oral tolerance to specific microflora and food antigens, which can play a role in the pathogenesis of IBD (14). Third, breast-milk feeding was shown to limit the development of colitis in mice deficient for interleukin 10. This finding was explained by the change of intestinal flora of the developing mice from pathogenic bacteria to nonadherent bacteria as a result of oligosaccharides found in the milk that stimulate Bifidobacterium and Lactobacillus growth (15). A change in proinflammatory cytokine secretion can also be offered as an explanation (16).
Yet, most of the findings about the beneficial effect of breastfeeding derive from epidemiologic studies. Indeed, some studies found breastfeeding to be protective against UC or CD (17-22). However, most of the studies failed to achieve statistically significant results or found no association at all (4, 5, 23-30). Meta-analyses of observational studies present particular challenges because of inherent biases and differences in study designs (31). Thus, this meta-analysis, which is reported here according to the "proposal for reporting" published previously by Stroup et al (32), does not presume to provide a precise estimate of the association between breastfeeding and IBD but rather attempts to either support or weaken this hypothesis and to summarize the evidence that was gathered about this subject.
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SUBJECTS AND METHODS |
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TOPABSTRACTINTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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From the abstracts identified in the database search, 14 described relevant epidemiologic studies and were selected for full review (4, 5, 17-26, 28, 29). By reviewing the references of these articles, 2 additional studies were discovered (27, 30). An Internet search was conducted as well by using the same terms used in the database search to locate published studies not registered in MEDLINE or EMBASE. This search recovered one additional study (33). Thus, a total of 17 studies were fully reviewed in this meta-analysis.
We selected all studies in which the primary or secondary goal was to evaluate the association between breastfeeding and UC or CD as separate entities. These articles were independently reviewed by the authors (EK and RVC) by using a standardized report form. The articles were graded according to predefined guidelines that will be further detailed. Discrepancies were resolved in conferences.
A primary prerequisite for the inclusion of studies in the meta-analysis was the presence of a control group, which could be formed by population controls, by hospital inpatients, or by outpatients who did not suffer from IBD or other chronic diseases that might be related to lack of breastfeeding. Studies, in which the control subjects were recruited to the study by the case subjects, with no supervision of the investigators or coinvestigators, were considered to be of lower quality, because this recruitment method could inflict a serious selection bias. To further deal with the problem of selection bias, we categorized the studies according to the percentage of subjects willing to participate from the total number of subjects approached by the investigators (response rate); ie, articles in which the investigators did not detail response rates or recorded response rates of <80% in either the case or the control subjects were ranked as having a lower quality.
Studies were categorized according to the age of diagnosis, from birth to adolescence (0–18 y) or adults (>18 y). To decrease information bias, studies of adults, which did not specifically note that the classification of breastfeeding was based on information collected from parents or another older relatives of the participating subjects, were classified as low quality. This classification was not a requirement in pediatric studies (provided that data were collected during childhood), because it was assumed that the information was obtained from a parent or an older relative. No restrictions were imposed on the method in which this information was obtained (mail, interview, or clinical files).
No restrictions were imposed on the method of diagnosis of CD and UC. As long as the diagnosis was confirmed by a physician, we assumed that well-trained specialists diagnosed the cases. Otherwise, the study was assigned to the low quality group.
Breastfeeding was defined as either exclusive or nonexclusive breastfeeding for any given duration. Accordingly, no breastfeeding was defined as nonexclusive or exclusive bottle-feeding from birth. When odds ratios (ORs) were calculated for both definitions, we used the OR for "not exclusively breastfed" for any duration compared with "exclusively bottle-fed from birth" for the calculation of the pooled estimate. Duration of breastfeeding was sought and documented.
We did not exclude studies in which the investigators stated that the correlation between breastfeeding and CD or UC was insignificant and, therefore, presented neither OR nor crude data. Instead, the OR was estimated to be 1, and the CI was calculated by assuming participation of all subjects in the study, and by arbitrarily assigning them a rate of 20% bottle-feeding. In this manner we maintained a conservative attitude in which it was more difficult to spuriously reject the null hypothesis of no relation between breastfeeding and IBD.
To sum up this section, studies were graded for quality levels as follows. For grade 1 (best quality), case and control subjects were recruited by the investigators or coinvestigators. Diagnosis was always confirmed by a physician, and breastfeeding information was always confirmed by patients' mothers or other older close relative (as previously mentioned, this was not a requirement in pediatric studies). Response rate is mentioned in the article and is 
80% for both case and control subjects. Grade 2 was the same as grade 1, except that the response rate is not mentioned or is <80%. For grade 3 (lowest quality), either breastfeeding information was not provided by the mother or a close relative of the patient, diagnosis was not confirmed by a physician, or control subjects were recruited to the study by the patients.
Statistical analysis
The pooled OR and its confidence limits were calculated by using the DerSimonian and Laird method (34), which is based on the random-effects model. The fixed-effects model–based OR, calculated as previously described by Greenland (35), is also presented. In both methods, the weight of each study depends on the inverse of the variance of log OR, which is estimated by the 95% CI of each study.
Heterogeneity of the studies was calculated with the following formula:
 | (1) |
The df for the chi-square test was defined as the number of studies minus one [wi represents the weight (calculated by the inverse of the variance) of each study].
In studies in which both crude and adjusted OR were reported, we included the adjusted OR in our calculation of the pooled estimate. If no single adjusted OR was presented, we included the crude OR. If no OR was presented in a given study, we calculated it and its 95% CI according to the raw data presented in the article.
Publication bias was investigated by funnel plots and by the regression asymmetry test for skewed funnel plot introduced by Egger et al (36). A low P value in this test suggests the possibility of a publication bias.
Data analysis was performed by using PEPI 4.0 and COMPARE2 version 1.25 statistical package (Sagebrush Press, Salt Lake City) (37). A P value < 0.05 was considered to be statistically significant.
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RESULTS |
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TOPABSTRACTINTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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) and for CD (Table 2). Four studies did not present the exact findings about breastfeeding (4, 23, 27, 30). Instead, they merely claimed that the OR was close to unity. The OR in those studies was estimated as 1, and the CI was calculated as described in "Subjects and Methods." An exception was made for the study of Gilat et al (4), because this researcher calculated the OR from the number of discordant pairs of each case subject and the matched control subject. Thus, the CI for that study was calculated with half of the control subjects mentioned in the article (302 pairs of control and case subjects for CD and 197 pairs for UC).
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). Overall, only 4 studies (consisting of 397 patients with UC and 766 control subjects and 583 patients with CD and 876 control subjects) were included in the highest quality groups for either CD (18, 20, 21, 24) or UC (17, 21, 24, 26). The pooled ORs and 95% CIs (calculated according to the random-effects model) for these studies were 0.56 (95% CI: 0.38, 0.81) for UC and 0.45 (95% CI: 0.26, 0.79) for CD. ORs for the 8 UC studies and the 7 CD studies graded in quality groups 1 and 2 were 0.61 (95% CI: 0.46, 0.83) and 0.55 (95% CI: 0.34, 0.87), respectively. When all studies were included in the pooled estimate, the random-effects model OR was 0.77 (95% CI: 0.61, 0.96) for UC and 0.67 (95% CI: 0.52, 0.86) for CD (Table 4, Figures 1 and 2). Thus, the protective effect of breastfeeding against both diseases remained statistically significant for all calculated pooled ORs. However, the results for both diseases appeared to be heterogeneous, primarily after adding the studies of lower quality (Pheterogeneity < 0.001 for CD and Pheterogeneity = 0.002 for UC). Heterogeneity was further explored by dividing the studies according to various characteristics related to population differences, exposure definition, and methodologic issues and by calculating summary estimates of the OR for the association of UC and CD with breastfeeding for each group (Table 5).
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and 4) indicated a possible publication bias in the studies for CD. P value for a skewed funnel plot, calculated by the regression asymmetry test, was 0.23 for the UC studies and 0.003 for CD studies.
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DISCUSSION |
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TOPABSTRACTINTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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The test for heterogeneity, however, was statistically significant for both UC and CD. This finding can be partly explained by differences in the case subjects' age (children and adolescents compared with adults), control subjects characteristics (hospital based compared with population based), matching variables, and the exact definition of breastfeeding (Table 5
). Heterogeneity of the studies can also be attributed to the differences in the quality of the studies, because the results become more heterogeneous when studies with lower quality are included. These differences can be due to biased results of these studies. Of special concern is the study of Thompson et al (28). That study incorporated hundreds of CD and UC case subjects in its investigation. Thus, despite methodologic problems, which made it highly prone to various biases, it had the highest influence on the pooled OR and the heterogeneity of the studies.
All but 2 studies recovered in this meta-analysis were retrospective case-control studies. That type of study constitutes a drawback because case-control studies are subject to misclassification as a result of recall bias and to selection bias. It is, however, difficult to conduct a prospective study that tests the relation between IBD and breastfeeding, because the lag between breastfeeding and the development of IBD is substantial. In 2 of the studies (24, 29), however, data about breastfeeding was collected from medical records and, thus, did not rely on the recall of mothers. Nevertheless, these data were recorded merely a few days after labor. The implications of this data collection will be further discussed later in this article.
Selection bias is potentially present in all of the reviewed studies, because no study described a comparison between subjects participating in the study and subjects excluded or not willing to participate. We set a low rank to studies in which the case subjects were instructed to obtain replies to the control subject's questionnaire by themselves, because the process of selecting and questioning the control subjects by the case subjects without the supervision of the investigators is, in our opinion, highly prone to selection bias. To further minimize the possibility of selection bias, we calculated a distinct pooled OR for the studies in which response rate was specified and was 80%.
Another potential source of bias is related to imprecise recall of breastfeeding. Thus, studies in which information about breastfeeding was not provided by the mother of the patient or an older close relative were assigned to the lowest quality group. Data provided by mothers, theoretically, could also be prone to recall bias, when one considers the prolonged lag time elapsing from infancy to development of the disease. However, we tend to think that this kind of bias was not an important problem in those studies. Our thought is supported by a study conducted by Launer et al (38) that demonstrated a high accuracy in the recall of breastfeeding duration at 18 mo after birth. Although in the reviewed studies, breastfeeding practices were inquired years after birth, the information that the mothers were asked to obtain was simple (breastfeeding, yes or no); hence, we believe it was accurate. F urthermore, our thoughts are supported by Bergstrand and Hellers (18), who mentioned in their study that "most living mothers were remarkably exact in their information regarding breastfeeding." Nevertheless, duration of breastfeeding was not documented in most of the studies. In light of the dose–response effect found for both CD and UC by Rigas et al (21) and for CD by Bergstrand and Hellers (18), we think that these missing data are probably of high importance.
As was mentioned previously in this report, most studies did not define duration and exclusivity of breastfeeding precisely, and it was not clear whether exclusive breastfeeding was being compared with nonexclusive breastfeeding or whether nonexclusive breastfeeding was being compared with exclusive bottle-feeding. Thus, it cannot be stated whether the absence of breastfeeding is the risk factor for IBD or the presence of bottle-feeding. It is also worth noting that this inadequate definition of breastfeeding duration and exclusivity can lead to nondifferential misclassification, which might obscure the protective association between breastfeeding and IBD (39). A good example for this type of nondifferential misclassification can be drawn from the study of Ekbom et al (24). That study, although conducted with almost perfect methodology, defined breastfeeding according to medical records, which merely documented breastfeeding status in the first few days after labor. It is possible that a significant portion of mothers that were assigned in this study as exclusive breastfeeders moved to partial breastfeeding or totally gave up breastfeeding a few days later. Thus, the lack of association found in that study can actually be an underestimation of an existing association that would have been discovered had breastfeeding status been recorded for a longer duration.
Confounding was not treated statistically in most of the studies. Confounding can potentially bias the results, but the few studies in which adjusted and crude OR were calculated (17, 19-21) showed little difference between the adjusted OR that controls for various confounders (diarrheal disease during infancy, sex, age, race, birthplace, sibship size, birth order, maternal age, smoking, and the use of oral contraceptives) and the crude OR. We, therefore, believe that the lack of adjustment to confounders in most of the studies probably did not lead to a significant bias of the results.
Most of the studies matched case with control subjects for sex and age. Some studies also matched other variables (region or country of birth, residential neighborhood), and in some matching was inherent in the control subject selection (neighbors, acquaintances, siblings). However, only in a few of the studies was matching statistically treated through conditional logistic regression or McNemar test. The lack of this statistical treatment in most studies can lead to bias of the OR toward unity (no relation); thus, the result presented in these studies might lead to underestimation of the protective association between breastfeeding and IBD (40).
Finally, publication bias, which results from a tendency to publish only significant data, constitutes a potential problem in every meta-analysis. The funnel plots of both CD and UC show that most of the studies have about the same precision. The funnel plot of the CD studies has an asymmetric appearance. This asymmetry is supported by the low P value (0.003) result in the test for skewed funnel plot for CD. In meta-analysis of observational studies, however, larger sample sizes do not necessarily indicate a higher validity (36). For example, it can be seen that the distorted shape of the plot is caused primarily by the study of Thompson et al (28), which, as was previously outlined, has the largest sample size but suffers from some important methodologic problems. In addition, most of the studies were performed for both CD and UC; thus, it is unlikely that publication bias exists for one but not for the other. Nevertheless, publication bias cannot be ruled out in this meta-analysis.
In conclusion, our study supports the hypothesis that breastfeeding provides protection against CD and UC development. However, it does not presume to provide an exact estimate of the OR for a certain definition of breastfeeding, but rather to provide a rough measure of the relation between breastfeeding and the risk of IBD. Our thought is that, because of a result of nondifferential misclassification, which, as we stated earlier, is inherent in many of the studies reviewed, the actual effect of breastfeeding is higher than the one estimated here. Furthermore, most of the best quality studies showed a significant protective effect. Nevertheless, because the effect found was minor and inconsistent, our study should not be regarded as final proof of this hypothesis. We think that a well-performed, documented prospective study should be held. Studies of high-risk populations that will specifically address the influence of breastfeeding (as well as its duration) are of particular importance. Because there is a clear genetic predisposition to IBD, these populations should probably be composed of families that include persons who already have IBD [such as the studies conducted by Koletzko et al (20, 26)]. That kind of study will enable the generation of breastfeeding recommendations to mothers of infants with a history of IBD in first-degree relatives.
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ACKNOWLEDGMENTS |
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EK designed the study, conducted the database search, reviewed the articles, analyzed the data, and wrote the manuscript. RVC reviewed the articles, helped in designing the study and analyzing it, and reviewed the manuscript; JB reviewed the manuscript; AJ reviewed the manuscript; SR reviewed the articles and manuscript. None of the authors had any financial or personal conflicts of interest in any of the subjects discussed in this article.
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REFERENCES |
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TOPABSTRACTINTRODUCTIONSUBJECTS AND METHODSRESULTSDISCUSSIONREFERENCES |
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This article has been cited by other articles:
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  L. Schack-Nielsen and K. F. Michaelsen Advances in Our Understanding of the Biology of Human Milk and Its Effects on the Offspring J. Nutr., February 1, 2007; 137(2): 503S - 510S. [Abstract] [Full Text] [PDF]
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 E. Peters, K.-H. Wehkamp, R. E. Felberbaum, D. Kruger, and R. Linder Breastfeeding duration is determined by only a few factors Eur J Public Health, April 1, 2006; 16(2): 162 - 167. [Abstract] [Full Text] [PDF]
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 P. Jantchou, D. Turck, M. Balde, and C. Gower-Rousseau Breastfeeding and risk of inflammatory bowel disease: results of a pediatric, population-based, case-control study Am. J. Clinical Nutrition, August 1, 2005; 82(2): 485 - 486. [Full Text] [PDF]
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E. Klement and S. Reif Breastfeeding and risk of inflammatory bowel disease Am. J. Clinical Nutrition, August 1, 2005; 82(2): 486 - 486. [Full Text] [PDF]
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