Efficacy of probiotics in preventing atopic dermatitis in infants: A systematic review and meta-analysis Authors: Tianli Wei, Yingxue Ding Published: 2026 ABSTRACT AbstractObjectiveAlthough probiotic modulation of the gut microbiota in early life has been proposed to prevent atopic dermatitis, supportive evidence remains inconsistent. This systematic review and meta-analysis aimed to determine whether probiotic supplementation initiated during infancy (0–36 months) reduces the risk of atopic dermatitis and provide clinically relevant insights.MethodsThe PubMed, Web of Science, EMBASE, and Cochrane Library databases were searched up to 8 January 2026 for randomized controlled trials comparing probiotics with placebo or no intervention for the prevention of atopic dermatitis. To be eligible, studies needed to have enrolled infants aged 0–36 months. Risk of bias was assessed using the Cochrane risk of bias 2 tool, and a random-effects meta-analysis was performed.ResultsEighteen randomized controlled trials (10,195 participants) were included. Pooled analysis showed that there was no significant protective effect of probiotics against atopic dermatitis (risk ratio = 0.94; 95% confidence interval: 0.72–1.25; p = 0.66), with substantial heterogeneity (I2 = 72.8%). Sensitivity analyses confirmed robustness, and no publication bias was detected (Egger's test, p = 0.15). Two studies featured a high risk of bias, predominantly due to missing outcome data.ConclusionsCurrent evidence does not support routine probiotic supplementation initiated only during infancy for the prevention of atopic dermatitis. Positive preventive effects reported in previous meta-analyses are largely driven by perinatal (maternal-plus-infant) regimens, whereas infant-only supplementation has failed to demonstrate consistent benefit.INPLASY registration number: INPLASY202650128.Keywords: Atopic dermatitis, infants, probiotics, prevention, systematic review, meta-analysis Introduction Atopic dermatitis (AD) is the most common chronic inflammatory skin disease occurring during infancy, which affects children worldwide and serves as the primary entry point of the “atopic march” towards food allergy, asthma, and allergic rhinitis.1,2 In affected infants, chronic pruritus disrupts sleep and development, whereas unwarranted dietary restrictions may compromise growth; consequently, parents experience significant anxiety with regard to their child's health. 3 Recent meta-analyses have reported a worldwide pediatric prevalence ranging from 6% to 20% and an increasing trend over recent decades; this has led to the urgent need to identify safe, effective, and accessible primary prevention strategies that could alter this allergic trajectory.4,5 The “hygiene hypothesis” and the concept of a gut–skin axis provide a compelling biological rationale for microbial interventions in early life.6,7 The gut microbiota perform important functions in the intestine and play a key role in immune regulation and homeostatic maintenance in distant tissues. The gut–skin axis has gained substantial recognition, emphasizing the complex relationship between the gut microbiome and skin health; dysfunctional gut barriers, along with metabolites produced by microorganisms in the gut, can exert profound influence on skin conditions, including AD. 8 Probiotics are live microorganisms that can confer health benefits on a host when administered in sufficient amounts and have emerged as a promising candidate for AD prevention due to their established safety profile, relatively low cost, and wide availability. 9 Mechanistic studies have shown that specific strains of probiotics can restore microbial diversity in the gut, enhance intestinal barrier function, and promote regulatory T-cell differentiation, thereby shifting the immune balance away from a Th2-dominant phenotype toward immune tolerance. 10 Experimental evidence has also provided supporting evidence for the gut–skin axis through microbial metabolites such as short-chain fatty acids and tryptophan derivatives, which promote regulation of the exacerbated AD immune response via regulatory T cells and IL-10 and directly act on keratinocytes after reaching the bloodstream. 11 Despite this strong mechanistic foundation, the translation into consistent clinical benefit has proven remarkably heterogeneous, and results from clinical trials have remained inconclusive. Numerous randomized controlled trials have evaluated probiotics for the prevention of AD, and several meta-analyses have reported modest but statistically significant protective effects. Recent umbrella reviews have confirmed that probiotic supplementation is associated with a reduced risk of AD, irrespective of whether they are administered as combined prenatal and postnatal or postnatal-only regimens.12,13 However, most of these trials included perinatal (prenatal plus postnatal) regimens, and subgroup analyses indicated that the positive signal was largely driven by maternal supplementation during pregnancy rather than by infant-only administration.14,15 For example, meta-analyses have shown that the intake of probiotics by pregnant and breastfeeding mothers reduces the incidence of pediatric AD to a substantially greater extent than infant-only supplementation. 16 This distinction is critical in clinical practice. If the preventive effect requires prenatal immune priming, advising parents to provide probiotics only after birth may be ineffective, leading to wastage of resources and creation of false reassurance. Moreover, several recent large trials have reported neutral or negative results, and the overall evidence base lacks an updated meta-analysis that specifically isolates infant-initiated probiotics.17,18 Therefore, the present systematic review and meta-analysis focuses specifically on a clinically actionable question: does probiotic supplementation that begins during infancy reduce the risk of developing AD? Unlike previous meta-analyses that combined prenatal, postnatal, and mixed regimens, we applied strict inclusion criteria to isolate the direct effect of postnatal administration alone. By synthesizing the totality of available randomized evidence, we aimed to provide a clear, evidence-based answer to guide shared decision-making between clinicians and families. Materials and methods Inclusion criteria This systematic review and meta-analysis was conducted and reported in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) 2020 statement. 19 This study was registered post-study at International Platform of Registered Systematic Review and Meta-analysis Protocols (INPLASY, https://inplasy.com/) with the following registration number: INPLASY202650128. Studies were eligible based on the following Population, Intervention, Comparator, Outcomes, and Study design criteria: (a) Population. Infants aged 0–36 months (both high-risk and general populations); (a) Population. Infants aged 0–36 months (both high-risk and general populations); (b) Intervention. Any oral probiotic strain(s) initiated within the first 36 months of life, without restrictions on formulation, dosage, frequency, or duration; (b) Intervention. Any oral probiotic strain(s) initiated within the first 36 months of life, without restrictions on formulation, dosage, frequency, or duration; (c) Comparator. Placebo, no intervention, standard care, or any non-probiotic control; (c) Comparator. Placebo, no intervention, standard care, or any non-probiotic control; (d) Outcomes. Primary outcome is prevention of AD diagnosed according to recognized criteria or by a physician; (d) Outcomes. Primary outcome is prevention of AD diagnosed according to recognized criteria or by a physician; (e) Study design. Randomized controlled trials (parallel, cluster, factorial), observational studies (cohort, case–control), and non-randomized intervention studies, requiring full-text articles from peer-reviewed journals. No minimum follow-up was required. (e) Study design. Randomized controlled trials (parallel, cluster, factorial), observational studies (cohort, case–control), and non-randomized intervention studies, requiring full-text articles from peer-reviewed journals. No minimum follow-up was required. Exclusion criteria Studies were excluded if any of the following criteria were fulfilled: (a) not published in a peer-reviewed journal (e.g. conference abstracts, dissertations, and preprints); (b) full text inaccessible despite reasonable efforts; (c) primary outcome (AD incidence or prevalence) not reported or not extractable for infants aged 0–36 months at the start of the intervention; (d) probiotic administered only to the mother (prenatally or during lactation) without a separate infant intervention arm; (e) probiotic administered as part of a complex formulation (e.g. synbiotic and medical food) precluding isolation of its specific effect; (f) follow-up ending before 3 months of age, insufficient for the assessment of AD development; and (g) duplicate publications (most complete or recent data retained). Search strategy Four electronic databases were searched on 8 January 2026, including the PubMed, Web of Science, EMBASE, and Cochrane Library. The search was restricted to articles that had been published in English with no date limitation. The strategy combined Medical Subject Headings and free-text terms for three core concepts: (a) infants (e.g. “infant,” “newborn,” “neonate,” “baby,” and “babies”); (b) probiotics (e.g. “probiotic,” “Lactobacillus,” “Bifidobacterium,” and “synbiotic*”); and (c) AD (e.g. “atopic dermatitis,” “atopic eczema,” and “eczema”). Terms were adapted to the syntax of each database using Boolean operators (AND, OR). Eligible study types included randomized controlled trials, observational studies, clinical studies, and clinical trials. Reference lists of included articles and relevant reviews were screened manually for additional studies. Literature screening Following the removal of duplicates, titles and abstracts were independently screened against the eligibility criteria by two reviewers. Records not clearly excluded were subjected to full-text review. The same two reviewers independently assessed full texts; disagreements were resolved through discussion or consultation with a third senior researcher. Reasons for exclusion were recorded and were presented in a PRISMA flowchart. Quality assessment Two reviewers independently assessed the risk of bias (RoB) for the included randomized controlled trials using the cochrane RoB 2 tool. Each study was judged across five domains, with the overall risk rated as “low risk,” “some concerns,” or “high risk.” Disagreements were resolved via discussion or consultation with a third reviewer. Data extraction Two reviewers independently extracted data using a standardized form. Extracted information included study characteristics (authors, year, and design), participant details (sample size per arm, age, sex, and diagnostic criteria), intervention specifics (probiotic strain, dosage, frequency, duration, and control), and outcome data (post-intervention means and SDs for continuous outcomes and event counts for dichotomous outcomes). When multiple follow-up time points were available, the final assessment was used. Missing data were requested from the corresponding authors. All extracted data were entered into statistical software for meta-analysis. Statistical analyses Analyses were performed using the meta and metafor packages in R (version 4.3.0). Two-sided tests with p < 0.05 were considered significant. Heterogeneity was quantified using I2, with low (25%), moderate (50%), and high (75%) thresholds. A fixed-effects model (Mantel–Haenszel) was employed when I2 was <50%; otherwise, a random-effects model (DerSimonian–Laird) was employed. Publication bias was assessed using funnel plots and Egger's test (p < 0.05 indicating significant bias). Sensitivity analyses were conducted by sequentially excluding individual studies. Results The study selection process is summarized in Figure 1. PRISMA flowchart of literature screening. PRISMA: Preferred Reporting Items for Systematic Reviews and Meta-Analyses. Study characteristics This meta-analysis included 18 studies with a total of 10,195 participants.20–37 Individual study sample sizes ranged from 97 to 1223. Geographically, six studies were conducted in Finland, five in Australia/New Zealand, two in the United Kingdom, and one each in the United States, Singapore, France, Korea, and Denmark. Most study populations comprised infants at high risk of allergic diseases, defined primarily by a family history of atopy. Specific high-risk subgroups included very preterm infants, non-breastfed term neonates, and infants of sole European ancestry. Probiotic strains included Lactobacillus (e.g. Lactobacillus rhamnosus GG (GG), and Lactobacillus acidophilus) and Bifidobacterium (e.g. Bifidobacterium breve, Bifidobacterium lactis), often as multi-strain preparations. Some regimens also contained prebiotics (e.g. galacto-oligosaccharides (GOS)). The control groups received matching placebos (e.g. maltodextrin and microcrystalline cellulose), except for one historically controlled cohort study (Damm et al.). 21 The primary outcome across all studies was the incidence or prevalence of AD (eczema) diagnosed by physicians, using validated questionnaires (e.g. the Scoring Atopic Dermatitis (SCORAD) questionnaire), or through parental reporting. Secondary outcomes included other allergic manifestations, allergen sensitization, serum immunoglobulin E (IgE) levels, immune marker levels, and gut microbiota composition. With the exception of the study by Damm et al., 21 all studies were randomized controlled trials, most of which were double-blind and placebo-controlled. Two studies were nested sub-studies (Gueimonde et al; 30 Plummer et al. 28 ) (Table 1). Table 1.Characteristics of included studies.StudyRegionSample sizeMales (%)PopulationIntervention strain(s)ControlFollow-upP et a.31Finland79650.8High-risk infantsL. rhamnosus GG, L. rhamnosus LC705, B. breve Bbi99, P. freudenreichii JS + GOSPlacebo6 monthsPlummer et al.28Australia/NZ281a53Very preterm (<32 weeks)B. infantis BB-02, S. thermophilus TH-4, B. lactis BB-12Placebomedian 16 monthsCabana et al.29USANRNRHigh-risk infantsL. casei rhamnosus (LGG) + inulinPlacebo3 yearsSoh et al.26Singapore25348 (probiotic)Asian high-riskB. longum BL999 + L. rhamnosus LPRPlacebo6 monthsRozé et al.35France9758 (experimental)Non-breastfed term neonatesL. rhamnosus LCS742 + B. infantis M63 + prebioticsPlacebo6 monthsGueimonde et al.30Finland128NRHigh-risk infantsL. rhamnosus GGPlacebo6 monthsKukkonen et al.25Finland122350High-risk infantsL. rhamnosus GG, L. rhamnosus LC705, B. breve Bb99, P. freudenreichii JS + GOSPlacebo6 monthsAllen et al.22UK454NRHigh-risk infantsL. salivarius CUL61, L. paracasei CUL08, B. lactis CUL34, B. bifidum CUL20Placebo6 monthsJordan et al.27UK454NRHigh-risk infantsMulti-strain probiotic (not specified)Placebo6 monthsWickens et al.32New Zealand47450.3High-risk infantsL. rhamnosus HN001 or B. lactis HN019Placebo2 yearsPrescott et al.24Australia153NRHigh-risk infantsNot fully reported in tablePlacebo2.5 yearsaFor the study by Plummer 2020, the sample size refers to the allergy sub-study.NR: not reported; GOS: galacto-oligosaccharides; LGG: Lactobacillus rhamnosus GG. Characteristics of included studies. For the study by Plummer 2020, the sample size refers to the allergy sub-study. NR: not reported; GOS: galacto-oligosaccharides; LGG: Lactobacillus rhamnosus GG. Quality assessment Risk of bias. Among the 18 included studies, 17 were randomized controlled trials (RCTs) and underwent RoB 2 assessment. In total, 12 RCTs were included in our meta-analysis; the other five RCTs were excluded from quantitative pooling because they did not report dichotomous incidence data for AD or effect estimates with variance. Domain-specific analysis revealed a more nuanced methodological profile (Figure 2). Domain 1 (randomization process) assessed generation and concealment of allocation sequences. Ten studies were rated as “low risk,” indicating robust randomization procedures; five raised “some concerns,” often due to insufficient detail on allocation concealment; two were judged as “high risk,” suggesting potential selection bias; and one remained “unknown.” Risk of bias summary using the cochrane RoB 2 tool. (a) Domain-level judgments for each study (D1–D5; definitions as in the main text). Symbols: “1” = low risk; “+” = high risk; “.” = some concerns/unclear. The overall judgment is presented on the right. (b) Distribution of risk of bias categories (low, some concerns, high, unknown) across domains and overall, expressed as percentages. Data are derived from the traffic-light plot. RoB: risk of bias. Domain 2 (deviations from intended interventions) evaluated the blinding of participants and personnel as well as protocol adherence. All 18 studies demonstrated a “low risk” of bias, indicating excellent control of performance bias across the entire evidence base. Domain 3 (missing outcome data) pertained to attrition and the handling of incomplete data. This was a notable area of concern; 11 studies were rated as “low risk,” whereas six were judged as “high risk,” primarily due to substantial or imbalanced dropout rates that were not adequately addressed by appropriate analytical methods (e.g. intention-to-treat). One study was classified as having “unknown” risk. Domain 4 (measurement of the outcome) concerned blinding of outcome assessors and objectivity of the AD diagnosis. Results were mixed; a majority (13 studies) were rated as “low risk,” typically because the primary outcome was objectively assessed by blinded personnel; one study was “high risk,” likely due to lack of blinding; and four had an “unknown” risk, usually owing to unreported blinding procedures. Domain 5 (selection of the reported result) assessed selective reporting. Thirteen studies were rated “low risk,” suggesting full reporting of pre-specified outcomes; four raised “some concerns,” often because published reports lacked a clearly accessible protocol or analysis plan for comparison; and one study was judged “high risk.” Taken together, although blinding of participants and personnel (Domain 2) was uniformly well-executed, significant methodological concerns emerged in other domains. The high RoB in Domain 3 for several studies is a particular limitation as it may have introduced attrition bias. Furthermore, variability in the randomization process (Domain 1) and outcome measurement (Domain 4) contributed to heterogeneity in overall bias judgments. These findings highlight the need for cautious interpretation of the pooled results, considering the high proportion of studies with methodological shortcomings (Figure 2). Pooled analysis showed that there was no significant protective effect of probiotics against atopic dermatitis (risk ratio (RR), 0.94; 95% confidence interval (CI): 0.72–1.25; p = 0.66), with substantial heterogeneity (I2 = 72.8%) (Figure 3). The pooled evidence does not support a statistically significant preventive effect of probiotics on AD in infants. The high heterogeneity observed highlights the need for further research to identify potential effect modifiers, including specific probiotic strains, dosages, and target populations. Forest plot of the pooled effect size. Risk ratios (RR) and 95% confidence intervals (CIs) from each included study are shown. The size of each square is proportional to the study's weight in the random-effects model (DerSimonian–Laird method). The diamond represents the pooled RR with its 95% CI. The vertical line at RR = 1 indicates no effect. Data are presented as RR, 95% CI, and percentage weight (%W(random)). RoB: risk of bias; CI: confidence interval. Publication bias assessment. Publication bias was assessed using funnel plot inspection, Egger's test, Begg's test, and trim-and-fill analysis. Figure 4 shows a funnel plot for the 11 included studies. Visual inspection revealed no obvious asymmetry. Egger's test (p = 0.155) and Begg's test (p = 0.938) did not indicate significant publication bias. Trim-and-fill analysis imputed four studies, shifting the pooled RR from 0.945 (95% CI: 0.716–1.246) to 1.122 (95% CI: 0.831–1.513); both intervals included 1, and p-values remained non-significant (original p = 0.658, adjusted p = 0.425). Collectively, these findings suggest a low risk of substantial publication bias (Table 2). Funnel plot for assessment of publication bias. Each point represents an individual study (n = 11). The horizontal axis shows the effect size (log risk ratio), and the vertical axis shows the standard error of the log RR (inverse scale). The vertical dashed line indicates the pooled effect estimate (log RR = −0.056, corresponding to RR = 0.945). The diagonal lines represent the pseudo 95% confidence limits around the summary effect. RR: risk ratio. Table 2.Publication bias assessment.TestParameterValueEgger's testEffect size (β)−1.3255Standard error (seβ)0.85318Intercept0.20753Standard error of intercept (sei)0.11028t-value−1.5536p-value0.1547Degrees of freedom (df)9Begg's testKendall's score−1Standard error12.845z-value−0.07785p-value0.9379Trim-and-fill methodPre-trim effect size0.94477Pre-trim 95% CI0.71609 to 1.2465Pre-trim p-value0.6576Post-trim effect size1.1217Post-trim 95% CI0.83138 to 1.5134Post-trim p-value0.4246Degrees of freedom (df)14Β: effect size; seβ: standard error of the effect size; sei: standard error of the intercept; CI: confidence interval; df: degrees of freedom. Publication bias assessment. Β: effect size; seβ: standard error of the effect size; sei: standard error of the intercept; CI: confidence interval; df: degrees of freedom. Results of the sensitivity analysis. Leave-one-out sensitivity analysis confirmed the robustness of the pooled estimate (Table 3). Recalculated RRs ranged from 0.902 to 1.007, all 95% CIs included 1, and all p-values were >0.05, indicating that no single study disproportionately influenced the results. Table 3.Sensitivity analysis (leave-one-out method).Study omittedRR95% CIzp-valueτ2I2 (%)Soh et al.260.9470.691–1.299−0.3890.7060.13274.95Taylor et al.360.9240.678–1.261−0.5720.5810.12875.47Kalliomäki et al.331.0070.773–1.3110.0560.9560.08268.48Rozé et al.350.9600.721–1.279−0.3190.7570.11374.55Gueimonde et al.300.9020.717–1.134−1.0190.3350.05470.27Jordan et al.270.9050.665–1.231−0.7350.4810.11759.29Damm et al.210.9560.698–1.309−0.3260.7520.13074.18Kim et al.230.9870.754–1.292−0.1110.9140.09272.34Prescott et al.240.9120.673–1.237−0.6820.5130.11975.07Marlow et al.340.9570.698–1.312−0.3170.7590.13073.68Kuitunen et al.370.9450.685–1.304−0.3980.7000.13370.75RR: risk ratio; CI: confidence interval; z: test statistic for the overall effect; τ2: between-study variance. Sensitivity analysis (leave-one-out method). RR: risk ratio; CI: confidence interval; z: test statistic for the overall effect; τ2: between-study variance. Discussion This systematic review and meta-analysis of randomized controlled trials provides a clear answer to a focused clinical question: does probiotic supplementation initiated during infancy (0–36 months) reduce the risk of subsequent AD? The pooled estimate revealed no statistically significant protective effect, with a CI that crossed the null and spanned from a potential modest benefit to no effect or even a slight increase in risk. Therefore, current evidence does not support the routine administration of probiotics to prevent AD in the general infant population. This null finding is robust, as confirmed by leave-one-out sensitivity analyses and multiple publication bias tests and was not driven by any single study. The absence of a significant effect from infant-initiated probiotics stands in apparent contrast to the positive results reported in several previous meta-analyses and systematic reviews. 38 However, this contrast is not a contradiction but rather a refinement of the evidence. Most earlier syntheses that demonstrated a protective effect, typically a 20%–30% relative reduction in risk, included studies with perinatal (prenatal plus postnatal) probiotic regimens. Importantly, subgroup analyses from those same reviews explicitly showed that infant-only supplementation was not effective, whereas maternal-plus-infant or maternal-only supplementation was effective.39,40 Our meta-analysis applied a stricter inclusion criterion in that we specifically included direct infant administration and excluded studies in which only the mother received probiotics without a separate infant intervention arm. Consequently, our null finding does not invalidate the positive evidence for perinatal probiotics; instead, it isolates the effect of postnatal administration alone and reveals that prenatal exposure is likely the critical component for any meaningful preventive effect. Biologically, this is plausible because the fetal immune system receives regulatory signals from the mother via the placenta during gestation, and prenatal probiotics may prime the developing immune system towards tolerance before birth.41,42 Postnatal-only supplementation may simply miss this narrow window for immune programming. A striking feature of the present analysis was the substantial heterogeneity across the included trials, which persisted even under a random-effects model. This heterogeneity is not a statistical nuisance but a clinically informative signal as this suggests that the effect of infant-initiated probiotics, even if non-significant overall, varies considerably depending on factors such as the specific strain(s) used, exact timing of initiation (first days vs. first months of life), duration of supplementation, and characteristics of the target population (high-risk vs. general population, mode of delivery, and breastfeeding status). 43 Some individual trials have reported a strong protective trend, whereas others showed no difference; a few even suggested potential harm. This divergence reinforces a key message in that probiotics should not be treated as a single class of intervention. Different strains of Lactobacillus and Bifidobacterium possess distinct metabolic and immunomodulatory properties and pooling these together may obscure genuine strain-specific effects or adverse signals. Although formal subgroup analyses were precluded by the limited number of studies, a descriptive examination of the individual trial estimates pointed to several variables that warrant further investigation. Trials initiating supplementation within the first 2 weeks of life tended to show point estimates further from the null, whereas those with later initiation yielded estimates closer to unity. Studies using multi-strain preparations displayed wider CIs and greater variability in effect estimates than those using single strains, although no consistent directional difference emerged. By contrast, baseline risk status (high-risk vs. general population) and geographic region showed no apparent differential patterns. These observations are exploratory and hypothesis-generating rather than confirmatory. They nonetheless highlight the need for future trials with sufficient statistical power and prespecified subgroup hypotheses to clarify which infant subgroups—if any—are most likely to benefit from probiotic supplementation. Unfortunately, the limited number of studies involved in our analyses precluded robust strain-level or dose-level subgroup analyses, which remains a major gap in the field. Next, we need to consider the clinical implications of our findings for practitioners and families. First, our findings indicate that routine universal probiotic supplementation for AD prevention is not supported by current evidence in the general infant population. The expected absolute risk reduction, even under optimistic assumptions, is small and uncertain. Given that probiotics are generally safe and well-tolerated, some families may still choose to use them, particularly for infants with a strong family history of atopy, those born via cesarean section, and those with early antibiotic exposure. However, shared decision-making must clearly communicate that the evidence does not guarantee benefit and that results from several trials are inconsistent. Second, and equally important, probiotics should not displace established preventive measures with stronger evidence, such as exclusive breastfeeding for the first 4–6 months, appropriate emollient use for dry skin from birth, avoidance of tobacco smoke exposure, and ensuring adequate vitamin D status during pregnancy.44,45 Third, if a family is committed to using probiotics for AD prevention, the available evidence, including separate meta-analyses of perinatal interventions, suggests that a prenatal-plus-postnatal regimen (mother starting probiotic intake in late pregnancy and continuing it for the infant) is more likely to be beneficial than infant-only supplementation. This recommendation, however, is based on complementary evidence rather than the present data. Certain limitations of this meta-analysis must be acknowledged. First, our inclusion criteria did not restrict probiotic formulation, dosage, frequency, or duration; this practice may have introduced heterogeneity and could have influenced the results as some infants may not have been given probiotics long enough to observe an effect. Second, the substantial heterogeneity could not be fully investigated through subgroup analyses due to the limited number of studies, precluding definitive identification of effect modifiers. Third, the diagnostic criteria for AD varied across trials and included physician diagnoses, diagnosis using validated instruments, parental reporting; this may have introduced outcome misclassification. Fourth, most of the included studies had relatively small sample sizes, and several exhibited methodological concerns, particularly missing outcome data, as reflected in the risk-of-bias assessment. Fifth, the restriction to articles published in English may have introduced language bias, although empirical evidence suggests that this is unlikely to alter the overall conclusion in this field. 46 Sixth, follow-up duration was generally ≤2 years; therefore, we cannot conclude whether infant-initiated probiotics may have a very delayed effect or influence the later atopic progression towards asthma and allergic rhinitis. 47 Finally, post-study registration may have introduced bias in our results, which remains a potential limitation. Looking forward, trials directly comparing prenatal to postnatal initiation, powered for subgroup effects, are needed to resolve the current uncertainty. Nested mechanistic studies, including gut microbiome analysis and metabolomics, would help elucidate why certain strains might work in some populations but not in others. 48 Such studies should use standardized AD diagnostic criteria and include long-term follow-up to assess effects on the atopic march, and extended intervention and observation periods >2 years would help clarify whether longer exposure confers additional benefit. 49 Conclusion This meta-analysis was restricted to infant-initiated probiotic supplementation and found no statistically significant reduction in the risk of developing AD. Routine universal probiotic use for AD prevention is not supported by the current evidence. However, this null finding does not contradict the positive evidence for perinatal (prenatal-plus-postnatal) probiotic interventions reported in other meta-analyses. Rather, our findings highlight timing as the critical effect modifier in that prenatal exposure appears to be necessary for the meaningful prevention of AD. If probiotics are to be used in clinical practice, a prenatal-plus-postnatal regimen is more likely to confer benefit than infant-only supplementation. Thus, in current clinical practice, decisions should be individualized, and parents should be counseled regarding the uncertainty of the current evidence for infant-only probiotics.