Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for the opportunity to review this interesting manuscript. This is a clinically relevant study on an important pediatric nutrition question. The prospective multicenter design, repeated follow-up at 1, 4, 6, and 12 months, and the attempt to distinguish direct breastfeeding from bottle-fed expressed breast milk are notable strengths. The manuscript is generally well structured, and the topic is of interest to readers in pediatric nutrition and gastroenterology.

That said, several methodological and reporting issues should be addressed to strengthen the validity and interpretability of the findings and to improve alignment with STROBE recommendations for cohort studies.

Major comments

1. Residual confounding remains a major concern.
   The most important limitation is the potential for residual confounding. Feeding mode at 1 month is unlikely to be random and may be influenced by infant latch difficulties, maternal breastfeeding problems, early gastrointestinal symptoms, return-to-work status, caregiver feeding practices, bottle nipple flow, and other postnatal factors that may also affect the outcomes. Although the authors adjusted for several maternal and infant covariates using a DAG-informed approach, important determinants of feeding modality do not appear to have been measured or adjusted for. This is especially relevant for the comparison between direct breastfeeding and bottle-fed breastmilk, which is central to the manuscript. The discussion should acknowledge this more explicitly, and the conclusions should be tempered accordingly.
2. Exposure classification at 1 month may not adequately represent feeding over the full follow-up period.
   The exposure is defined according to feeding practices at 1 month of age, while gastrointestinal outcomes are assessed up to 12 months. Because feeding patterns commonly change during infancy, this raises concern for exposure misclassification during follow-up. The manuscript would be strengthened by clarifying how stable feeding categories were after 1 month, if such data are available. If not, the authors should more clearly state that the study examines associations with early feeding practices at 1 month, rather than persistent feeding mode across infancy. This limitation should be given greater emphasis in the discussion.
3. Missing data and attrition are not sufficiently reported.
   According to the flow diagram, 779 mother-infant pairs were initially enrolled and 669 were included in the final analysis, with exclusions due to chronic maternal conditions, loss to follow-up, missing visit data, and incomplete IGSQ data. However, the manuscript does not adequately describe whether excluded participants differed from those retained, whether loss to follow-up varied across exposure groups, or how missing data were handled in the regression and GEE models. Please provide a clearer description of missingness by visit and by key variables, clarify whether analyses were complete-case or available-case, and consider an additional sensitivity analysis if feasible.
4. The longitudinal statistical modeling needs more detail.
   The use of GEE for repeated measurements is appropriate in principle, but the manuscript should specify the working correlation structure used. In addition, Figure 2 indicates that the GEE models included feeding mode and time as fixed effects, without interaction terms. Given that the results appear to vary by age and that some associations seem stronger at 6 months than at other time points, a feeding-by-time interaction is clinically and statistically relevant. Please justify the current specification and consider presenting a sensitivity analysis including an interaction term.
5. Causal language should be softened.
   Some statements in the abstract and discussion imply causality more strongly than is justified by an observational cohort design. For example, phrases such as “can effectively reduce the risk” and “protective effects lasting up to 6 months” should be revised to language that reflects association rather than causal inference. Throughout the manuscript, I recommend using terms such as “was associated with” rather than “reduced the risk” unless stronger causal assumptions are explicitly justified.
6. The subgroup analysis by minimum dietary diversity should be interpreted cautiously.
   The subgroup analysis at 6 months according to minimum dietary diversity is potentially interesting, but it may also be affected by reverse causality and post-exposure conditioning. Feeding diversity at 6 months may itself be influenced by earlier infant gastrointestinal symptoms or caregiver responses to those symptoms. The manuscript does mention reverse causality briefly, but this issue deserves a more careful explanation in the limitations section, and the corresponding conclusions should be more cautious.

Minor comments

1. Clarify the primary endpoint.
   It would be helpful to clearly state whether the primary endpoint is longitudinal IGSQ score, IGSQ score at a specific age, or the set of gastrointestinal symptoms collectively.
2. Consider reporting absolute risks alongside ORs.
   In addition to odds ratios, the clinical interpretation would be improved by providing absolute frequencies or risks for key outcomes across groups.
3. Baseline group differences should be contextualized more carefully.
   Several baseline characteristics differed significantly across feeding groups, including income, gravidity, primiparity, and time to initiation of breastfeeding. Consider reporting standardized differences in addition to p values, as these may be more informative for assessing imbalance.
4. The EBB group appears heterogeneous.
   The category “exclusive breastfeeding with bottle” includes infants fed exclusively by bottle as well as those fed by a combination of bottle and direct breastfeeding. This should be highlighted more explicitly as it may dilute interpretation of the effect attributed to feeding mode.
5. Please reconcile the statements regarding generative AI use.
   The Methods section states that no generative AI tools were used in manuscript preparation, whereas the Acknowledgments state that generative AI was used for language editing and grammar refinement. These statements are inconsistent and should be corrected.
6. Terminology could be clarified.
   The term “exclusive breastfeeding with bottle” may be confusing because “exclusive breastfeeding” has specific public health definitions.

Congratulations for the work and the results obtained

Author Response

Comment 1 (Reviewer 1):Residual confounding remains a major concern.

Response 1:We thank the reviewer for raising this important issue. We fully acknowledge that residual confounding cannot be completely ruled out in observational studies. To minimize its potential impact, we: (1) Used directed acyclic graphs (DAGs) combined with literature and clinical knowledge to select a minimally sufficient adjustment set, and included 10 covariates in Model 3: maternal age, education, occupation, income, number of pregnancies, parity, mode of delivery, pregnancy complications, time to initiation of breastfeeding, and infant sex. (2) Toned down causal language throughout the manuscript, replacing expressions such as "reduces the risk" or "protective effect" with associational statements (e.g., "was associated with a lower odds ratio"), and explicitly acknowledged in the Discussion that unmeasured confounders (e.g., maternal return-to-work time, nipple flow rate, latching difficulties) may still exist. Nevertheless, we agree that causal inferences should be made with caution.

Comment 2 (Reviewer 1):Exposure classification at 1 month may not represent feeding over the full follow‑up period.

Response 2：We thank the reviewer for pointing out this limitation regarding the timing of exposure assessment. We agree that feeding mode measured at 1 month cannot fully represent the entire 12‑month feeding pattern. To address this concern, we conducted three additional analyses:

(1) Interaction test: We added an interaction term between feeding mode and time in the GEE model. The interaction was not significant (χ²=8.00, P=0.247), suggesting that the effect of feeding mode on IGSQ scores did not differ significantly across months. This finding provides some support for using the 1‑month exposure. This result has been reported in Section 3.4 (page 10, line 339).

(2) Time‑varying exposure sensitivity analysis: We re‑analyzed the data using the feeding mode reported at each visit (categorizing exclusive formula feeding into the mixed feeding group) (Supplementary Tables 10b, 10c). The results showed that the direction of associations for IGSQ scores and most symptoms was completely consistent with the main analysis. Although effect sizes were somewhat attenuated (e.g., the β for mixed feeding on IGSQ score decreased from 0.95 to 0.68), mixed feeding remained significant while exclusive breastfeeding remained non‑significant, and the overall conclusions were unchanged. This suggests that even when feeding patterns change over time, the effect of early exposure is not overturned.

(3) Rationale for choosing 1‑month exposure: The 1‑month time point was the baseline of this study, with complete data. At this time, feeding patterns are relatively clearly classified (mainly mixed feeding, direct breastfeeding, and bottle feeding of breast milk), and complementary foods have not yet been widely introduced, allowing a more direct assessment of early feeding practices. The time‑varying analysis also supports that the 1‑month exposure captures the main direction of association. Therefore, we believe that using the 1‑month exposure is reasonable and relatively conservative.

Comment 3 (Reviewer 1)： Missing data and attrition are not sufficiently reported.

Response 3：We thank the reviewer for pointing out the issues regarding missing data and inadequate reporting of loss to follow-up. We have conducted additional analyses accordingly.

In Supplementary Table 5, we compared baseline characteristics between the included group (n=669) and the excluded group with baseline data (n=100). Results showed no significant differences between the two groups in feeding group distribution, maternal age, education, income, number of pregnancies, parity, pregnancy complications, infant sex, mode of delivery, or time to initiation of breastfeeding (all P > 0.05). Based on the comparison of feeding group distribution (χ²=0.702, P=0.704), there was also no significant difference in loss to follow-up rates across feeding groups.

Regarding missing proportions, the missing rates at each visit were: 8% at 1 month, 12% at 4 months, 15% at 6 months, and 21% at 12 months. The missing rate at 12 months (21%) is slightly above the commonly suggested threshold of 20%. However, the loss-to-follow-up analysis showed no significant differences in baseline characteristics between excluded and included participants, suggesting that the missingness may be random. The GEE method is robust to random missingness in repeated measures, and we used available-case analysis. Furthermore, the 10 participants (1.3%) who were included but lacked baseline data represent a very small number and are unlikely to affect the results. Therefore, we believe the potential impact of loss to follow-up on the conclusions is limited.

Comment 4 (Reviewer 1)：The longitudinal statistical modeling needs more detail (working correlation structure and interaction term).

Response 4：We thank the reviewer for this suggestion. We have clarified the working correlation structure of GEE in Section 2.4 (Methods): based on the QIC criterion, the exchangeable structure had the lowest QIC value (Supplementary Table 4), and we used it for all main GEE analyses. This is a standard practice, i.e., using the same optimally selected working correlation structure for all outcomes to ensure model consistency. Additionally, we tested the interaction term between feeding mode and time, and the result was not significant (χ² = 8.00, P = 0.247), suggesting that the effect of feeding mode on IGSQ scores was relatively stable over the 12-month period. This result has been reported in Section 3.4 (see page 10, line 339).

Comment 5 (Reviewer 1)：Causal language should be softened.

Response 5：We thank the reviewer for pointing out the overly strong causal language. We have carefully revised the entire manuscript, replacing expressions such as "reduce the risk," "protective effects," and "can effectively reduce" with more neutral associational terms such as "was associated with lower odds" and "favorable associations." For example, the conclusion has been changed to "early exclusive direct breastfeeding was associated with lower odds of gastrointestinal symptoms." We believe these revisions are more appropriate for the design of an observational study.

Comment 6 (Reviewer 1)：The subgroup analysis by minimum dietary diversity should be interpreted cautiously.

Response 6：We agree with the reviewer. In the limitations section of the Discussion, we have explicitly stated: “reverse causation cannot be excluded: early symptoms may have influenced feeding choices, and in the MDD subgroup analysis, infants with fewer symptoms may have been more likely to receive a diverse diet.” (see page 16, line 562). This avoids overinterpretation of causality.

Comment 7 (Reviewer 1)：Clarify the primary endpoint.

Response 7：We thank the reviewer for this suggestion. In Section 2.3 (Methods), we have clearly defined the primary outcome as the IGSQ score (overall gastrointestinal burden) and secondary outcomes as six specific gastrointestinal symptoms (abdominal distension, spitting up, dysphagia, constipation, diarrhea, and vomiting).

Comment 8 (Reviewer 1)：Consider reporting absolute risks alongside ORs.

Response 8：We appreciate this suggestion. Absolute risks have been added. Supplementary Table 7 presents the absolute frequencies (n, %) of each symptom by feeding group and month. This table complements Figure 1 (which shows trends) by providing detailed data, and has been cited in Section 3.2 (see page 9, line 297). We hope this enhances interpretability.

Comment 9 (Reviewer 1)：Baseline group differences should be contextualized more carefully (SMD).

Response 9：We thank the reviewer for this recommendation. To assess baseline balance among the three feeding groups, we used effect size measures appropriate for each variable type: standardized mean difference (SMD) for continuous and binary variables, and Cramér’s V for multicategorical variables. We followed the literature and used thresholds of SMD > 0.1 or Cramér’s V > 0.1 to indicate “meaningful imbalance”.

For the non‑normally distributed time to breastfeeding initiation, we still calculated SMD (0.404) based on means and SDs for comparability with other variables, while noting its limitation in the table footnote and providing medians, IQRs, and the Kruskal‑Wallis P‑value.

As shown in Supplementary Table 6:

Variables with |SMD| > 0.1 included: time to breastfeeding initiation (0.404), number of pregnancies (0.406), parity (0.393), annual household income (0.240), maternal age (0.234), pregnancy complications (0.173), mode of delivery (0.159), neonatal diseases (0.157), and infant sex (0.107). These showed meaningful between‑group imbalance.

Variables with |SMD| ≤ 0.1 included: birth weight (0.039) and birth length (0.068).

For multicategorical variables, education (Cramér’s V = 0.082) and occupation (0.066) were both < 0.1, indicating good balance.

 

It should be noted that we used directed acyclic graphs (DAGs) to select the minimally sufficient adjustment set. Model 3 adjusted for maternal age, education, occupation, household income, number of pregnancies, parity, mode of delivery, pregnancy complications, time to breastfeeding initiation, and infant sex. These covariates cover most variables with |SMD| > 0.1. Although neonatal diseases had a slightly elevated SMD, it was not a confounder between feeding mode and gastrointestinal symptoms according to the DAG, and therefore was not included in Model 3. Birth weight and length had very small SMDs and were well balanced, so they were also not included. Consequently, we believe that the effect estimates of feeding mode on outcomes have been adjusted for the major imbalances, and our conclusions are robust.

Comment 10 (Reviewer 1)：The EBB group appears heterogeneous.

Response 10：We thank the reviewer for pointing out the heterogeneity within the EBB group. We acknowledge that this group indeed includes both exclusive bottle feeding and a combination of bottle feeding with direct breastfeeding. However, Supplementary Table 1 shows that the median proportion of direct breastfeeding in this group was as high as 83.3% (range 0‑100%), meaning that the majority of infants still received most of their breast milk directly, with occasional bottle use. This heterogeneity may bias effect estimates toward the null – i.e., the true difference between exclusive bottle feeding and exclusive direct breastfeeding may be larger than what we observed. Therefore, our finding that the EBB group still showed higher odds ratios for symptoms may actually underestimate the adverse effect of exclusive bottle feeding. We have noted in the Discussion limitations that the heterogeneity of the EBB group may dilute the effect estimates (see page 16, line 567).

Comment 11 (Reviewer 1)：Please reconcile the statements regarding generative AI use.

Response 11：We thank the reviewer for pointing out the inconsistency in the AI use statement. We have removed the statement “no AI was used” from Section 2.8 (Methods) and have kept only the following acknowledgement in the Acknowledgements section: “During the preparation of this manuscript, the authors used generative AI to assist with language editing and grammar refinement. After using this tool, the authors reviewed and edited the content as needed and take full responsibility for the content of the publication.”

Comment 12 (Reviewer 1)：Terminology could be clarified.

Response 12：We thank the reviewer for this suggestion. We have renamed “exclusive breastfeeding with bottle (EBB)” to “bottle‑fed expressed breastmilk (EBB)” and clearly defined it at first use: infants received only breast milk (no formula) during the first month, but the breast milk was fed by bottle – including either completely by bottle or a combination of bottle and direct breastfeeding. This avoids conflict with the WHO definition of exclusive breastfeeding.

Comment 13 (Reviewer 1)：Figures and references (Figure 2 lines overlapping, Figure 3 unclear, Reference 37 possibly incorrect).

Response 13：We thank the reviewer for pointing out these issues. We have made the following revisions:

Figure 2a has been corrected: in the original figure, the lines for the MF and EBB groups were both solid and numerically close, causing overlap. We have now changed the MF group line to a dashed line, while keeping the EBB and EDB groups as solid lines. Additionally, we have used distinct markers: circles (●) for EDB, triangles (▲) for EBB, and squares (■) for MF. This makes the three curves clearly distinguishable.

Figure 3 has been replaced with a high‑resolution image (600 dpi).

Reference 37 (Guo et al., 2025) was on inflammatory bowel disease and did not match the content of our study; it has therefore been removed and replaced with a more relevant citation (Wells et al., 2022, on intestinal barrier function). The reference list has been updated accordingly.

 

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

This is interesting and important work.

A. Grateful if the authors could clarify the following:

1. Was the reason(s) why mothers chose to bottle feed breastmilk (EBB) instead of EDB within the first month of life recorded/ known? What about the MF group? i.e. that it was not due to feeding difficulties, GI symptoms within the first month of life that led mothers to feed EBM via bottle, or to introduce formula. Could there have been another reason that led to the decision to bottle feed EBM or MF that was the cause of the increase in GI symptoms observed subsequently. 
2. Were the researchers collecting survey data from mothers blinded to the group allocated (EDB, EBB, MF)? If not, how was bias in data collection prevented? 
3. The authors collected data on probiotic use. It would be good if that data is also included and analysed. Was there any difference in probiotic use amongst the 3 groups (EDB, EBB, MF), and did it vary with time? If so, this needs to be taken into account during data analysis and in the discussion. 

B. The authors have made some rather strong statements and conclusions regarding possible "'causation"'; that feeding practice (breast milk, bottle feeding) result in increased risk of GI symptoms in infants in the first year of life, and that having adequate DD is protective. I do not think the data in the study is robust enough to substantiate the claims made. The relevant sections in the results and discussion would need to be re-written to reflect the data more accurately. 

1. In the results section, the authors have correctly used OR (odds) to expressed numerical data, but have consistently used the word "'risk"' in the text (e.g. significantly greater risk...... as opposed to significantly greater odds)

2. At best, this study provides evidence for an association between feeding practice and possible GI symptoms in infants. The authors themselves have alluded to reverse causation in the discussion. Reverse causation could be the reason for every single "'association"' the authors have found. Before the authors can state that an association is causal, a dose response should have been demonstrated i.e. if breastmilk was protective, method of feeding was protective, then the findings would have MF > EBB > EDB. I do not think that this was consistently demonstrated in the study. (e.g. in some situations, findings in the EBB group were higher than MF and EDB). 

In this respect, the MF group with infants who were predominantly BF vs those who were predominantly formula fed would have shown that difference as well, which it did not. The authors should include supp Table 1 in the main paper and comment on those (negative) results - possibly underpowered? 

3. Quite a number of statements in the discussion are not accurately substantiated by study data. These need to be corrected. i.e. The whole discussion would need to be re-written to reflect their findings more accurately. 

e.g. of these statements:

"early infant feeding practices significantly influence the development of gastrointestinal function throughout the first 12 months of life."'  

"'EDB consistently presented notable gastrointestinal protective advantages across different ages" 

''...suggesting that EDB may effectively reduce the gastrointestinal burden in infants"' (line 385-7)

Similarly, the comments made about feeding practice, diet diversity and GI symptoms would need to be modified in a similar fashion. The possibility of reverse causation is acknowledged, i.e. it is precisely in infants with less GI symptoms, that caregivers have been able to give a more varied and diverse weaning diet.  

4.The authors have also alluded to the fact that bottle fed infants risk being overfed, hence explaining the increase incidence of GI symptoms in the EBB group compared to the EDB group. Did weight data of their infants in these 2 groups substantiate this? 

C. Some additional minor points:

(i) I believe the blue line (MF group) is missing from the first graph in Figure 2.

(ii) Figure 3 neds to be a clearer image

(iii) Reference 37 may not be a correct reference

Author Response

Comment 1:Were the reasons why mothers chose bottle‑fed breastmilk (EBB) instead of EDB within the first month of life recorded/known?

Response:We thank the reviewer for raising this question. We acknowledge that this study did not systematically record the specific reasons why mothers chose bottle feeding of expressed breast milk or mixed feeding (e.g., return to work, insufficient milk supply, latching difficulties, infant crying). Only partial reasons for stopping breastfeeding were collected, and those data were incomplete. This is a limitation of our study, which we have clearly stated in the Discussion (see page 15, line 558).

Although we did not record the reasons for feeding choice, we used directed acyclic graphs (DAGs) combined with literature and clinical knowledge to select a minimally sufficient adjustment set, and adjusted for 10 covariates in multivariable regression (Model 3): maternal age, education, occupation, income, number of pregnancies, parity, mode of delivery, pregnancy complications, time to initiation of breastfeeding, and infant sex. In addition, we conducted several sensitivity analyses (time‑varying exposure, adjustment for probiotic use), and none of them changed the main conclusions. Therefore, despite the lack of detailed information on reasons for feeding choice, we believe the main findings remain robust.

 

Comment 2: Were the researchers collecting survey data from mothers blinded to the group allocation (EDB, EBB, MF)?

Response: We thank the reviewer for this question and understand that the core concern is about information bias.

It should be noted that “blinding” is typically used in randomized controlled trials. This study is an observational cohort study. Feeding groups (EDB, EBB, MF) were determined post‑hoc based on the feeding mode reported by mothers at 1 month, not by random assignment. At the time of baseline data collection, the researchers did not yet know the future feeding group allocation of the infants; therefore, there is no classical “blinding” issue in this context.

To reduce potential information bias, we took the following measures:

Standardized data collection: We used structured standardized questionnaires to collect data. All researchers received uniform training to ensure consistency in the data collection process.

Outcome assessment: The gastrointestinal symptom assessment used items derived from the validated PedsQL™ Infant Scales, with clear definitions for each symptom, helping to reduce differences in subjective judgment.

We believe that through these methods, potential information bias has been reduced to some extent and is unlikely to materially affect the study conclusions.

 

Comment 3:The authors collected data on probiotic use. Was there any difference in probiotic use amongst the 3 groups (EDB, EBB, MF), and did it vary with time? If so, this needs to be taken into account during data analysis and in the discussion.

Response:We thank the reviewer for pointing this out.The analysis showed that probiotic use differed significantly among the three groups (P = 0.009) and decreased over time (P < 0.001) (Supplementary Table 11a). Because probiotic use could vary at each visit (i.e., time‑varying), we included it as a time‑varying covariate in the main GEE model to evaluate its potential confounding effect on the association between feeding mode and gastrointestinal symptoms. We chose GEE because it can handle both time‑varying exposure (probiotic use) and repeated outcome measures, whereas cross‑sectional logistic regression cannot effectively use time‑varying information from multiple visits, and adjusting for a fixed baseline value could introduce bias.

After adjusting for time‑varying probiotic use, the effect estimates for feeding mode remained almost unchanged (e.g., the β for mixed feeding on IGSQ changed from 0.950 to 0.943; the OR for vomiting changed from 1.70 to 1.68; all changes <5%), and all significance conclusions were consistent (Supplementary Tables 11b, 11c). This indicates that although probiotic use differed among feeding groups and varied over time, it was not a major confounder of the observed association between feeding mode and gastrointestinal symptoms.

 

Comment 4: In the results section, the authors have correctly used OR (odds) to express numerical data, but have consistently used the word “risk” in the text (e.g. significantly greater risk… as opposed to significantly greater odds). (Similar to Reviewer 1’s comment)

Response: We thank the reviewer for pointing this out. We have carefully revised the entire manuscript, replacing all instances of “risk” with “odds” or “likelihood” to accurately reflect the nature of the odds ratio (OR). For example, “significantly greater risk” has been changed to “significantly higher odds.” These revisions have been made in the Results and Discussion sections. We believe this change makes the wording more precise and avoids causal implications.

 

Comment 5: At best, this study provides evidence for an association between feeding practice and possible GI symptoms in infants. a dose response should have been demonstrated i.e. MF > EBB > EDB. I do not think that this was consistently demonstrated in the study.

Response: We thank the reviewer for this important comment. We agree that this study cannot infer causality, and reverse causation may indeed exist. Regarding the dose‑response pattern (MF > EBB > EDB), we did not observe a consistent trend.

It should be noted that to rigorously test a dose‑response, precise quantification of breast milk intake would be required. However, in this study, breast milk intake was nearly impossible to obtain for directly breastfed infants, and intake data for bottle‑fed and mixed‑fed infants were largely missing. We attempted to use feeding frequency at 1 month as a proxy (Supplementary Tables 2, 3), but the analysis showed no significant differences in gastrointestinal symptoms among groups with different feeding frequencies.

Furthermore, there is substantial heterogeneity within the EBB group: the median proportion of direct breastfeeding in this group was as high as 83.3% (range 0‑100%), meaning that the majority of infants still received most of their breast milk directly, with occasional bottle use. This within‑group heterogeneity may mask the true dose‑response relationship between exclusive bottle feeding and exclusive direct breastfeeding, implying that the effect we observed for the EBB group may be underestimated.

We have reported the observed association patterns as they are (e.g., higher symptom odds in the MF group, increased symptoms in the EBB group at 6 months), and we have acknowledged measurement limitations in the Discussion. We have revised the wording to emphasize associational rather than causal interpretations. Although a dose‑response cannot be demonstrated, through multivariable adjustment and multiple sensitivity analyses, we believe the results still provide valuable evidence suggesting a meaningful association between early feeding practices and infant gastrointestinal symptoms.

 

Comment 6: In this respect, the MF group with infants who were predominantly BF vs those who were predominantly formula fed would have shown that difference as well, which it did not. The authors should include supp Table 1 in the main paper and comment on those (negative) results - possibly underpowered?

Response: We thank the reviewer for this suggestion. We understand the desire to include the stratified analysis within the MF group in the main paper for greater transparency.

Regarding the grouping criterion: we stratified infants in the MF group into “predominantly breastfed” (>80% of feeds from breast milk) and “predominantly formula‑fed” (≤80%) based on the median proportion (80%) of breast milk feeding frequency at 1 month.

The analysis showed no significant differences between the two subgroups in IGSQ scores or most gastrointestinal symptoms (except for diarrhea at 1 month, which was in the opposite direction) (original Supplementary Tables 2, 3). Given that this stratified analysis was exploratory and the results were negative, and they do not affect the core conclusions of the main analysis (comparison among EDB, EBB, MF), we chose to keep them in the supplementary materials to maintain the coherence of the main manuscript. At the same time, we have commented that the negative results may be partly due to limited sample size in the subgroups (predominantly breastfed n=131, predominantly formula‑fed n=152), leading to insufficient statistical power, but they also suggest that within the MF group, the exact proportion of breast milk to formula may not be a major determinant of gastrointestinal symptoms.

 

Comment 7：Quite a number of statements in the discussion are not accurately substantiated by study data. These need to be corrected. i.e. The whole discussion would need to be re-written to reflect their findings more accurately.

Response: We thank the reviewer for pointing out the issues in the Discussion. We have thoroughly and carefully revised the Discussion section, making the following main adjustments:

(1) Weakened causal language: We replaced all strongly causal expressions (e.g., “influence”, “reduce”, “protective”) with associational descriptions (e.g., “associated with”, “lower odds”, “favorable associations”) to avoid over‑inference.

(2) Openly discussed reverse causation and residual confounding: We explicitly acknowledge that observational studies cannot completely rule out the possibility of reverse causation and residual confounding. For residual confounding, we selected a minimally sufficient adjustment set based on DAGs (Model 3) to control for known confounders as much as possible. For reverse causation, we clearly state in the Discussion that infants with fewer symptoms may have been more likely to receive a diverse diet. Although reverse causation may exist for some associations, it does not entirely explain all associations, and we have verified the robustness of the conclusions through multiple sensitivity analyses.

(3) Detailed reporting of sensitivity analyses: We added discussion of several sensitivity analyses to demonstrate the robustness of the main conclusions under different assumptions:

Time‑varying exposure analysis: Re‑analysis using the actual feeding mode reported at each visit (classifying exclusive formula feeding into the mixed feeding group) showed that the direction of associations for IGSQ and most symptoms was consistent with the main analysis; effect sizes were somewhat attenuated, but the overall conclusions remained unchanged (Supplementary Tables 10b, 10c).

Adjustment for probiotic use: After adjusting for time‑varying probiotic use as a covariate, effect estimates remained almost unchanged (changes <5%), and all significance conclusions were consistent (Supplementary Tables 11b, 11c), indicating that probiotics were not a major confounder.

Stricter symptom definition analysis: Using a stricter definition of symptoms (excluding “rarely”), the association between constipation and mixed feeding remained significant (OR=1.40), while other symptoms were attenuated or reversed, partly due to reduced event numbers (Supplementary Table D‑GEE). These analyses indicate that the main conclusions are not sensitive to changes in key assumptions.

 

Comment 8: The authors have also alluded to the fact that bottle fed infants risk being overfed, hence explaining the increase incidence of GI symptoms in the EBB group compared to the EDB group. Did weight data of their infants in these 2 groups substantiate this?

Response: We thank the reviewer for pointing this out. We acknowledge that this study did not obtain postnatal weight data for the infants – this was not because the cohort did not collect it, but because we did not request these data when applying for data access. Therefore, we cannot directly verify the hypothesis that “overfeeding leads to increased symptoms in bottle‑fed infants.” We have weakened this explanation in the Discussion to a speculative mechanism and explicitly noted that the lack of weight data is a limitation of this study. Future studies should collect longitudinal weight data to directly test this hypothesis. The relevant revisions have been made in the fifth paragraph of the Discussion.

 

Comment 9: Reference 37 may not be a correct reference. (Similar to Reviewer 1’s comment)

Response: We thank the reviewer for pointing this out. The original reference 37 (Guo et al., 2025) was on inflammatory bowel disease and did not match the content of our study. It has therefore been removed and replaced with a more relevant citation (Wells et al., 2022, on intestinal barrier function). The reference list has been updated accordingly.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I appreciate the authors’ responses to the reviewer’s comments and suggestions. I believe they have addressed most of the comments.
Congratulations and thank you for your efforts

Author Response

Dear Reviewer, thank you very much for your positive assessment and for your time. We are pleased that you found the English language, study design, methods, results, conclusions, figures, and tables clear and acceptable. We have carefully revised the manuscript in response to all reviewers’ comments. We greatly appreciate your guidance and encouragement.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have appropriately clarified and made changes based on earlier comments.

I still have a few more observations and comments for clarification. 

1.It would be good if the authors can state if the formula fed infants were given formulas containing pre and/or probiotics. They had alluded to the impact of pre-probiotics in infant formula in the discussion, and readers would then question whether the infants in this particular study had pro or prebiotics in their formula.

2. Caregivers and recall bias. The authors could include more explicitly if it were mothers who completed the questionnaires at all time points or whether alternative caregivers did so.

3. Blinding - the word blinding basically means - unaware of which group the patient (infant) belonged to. i.e. it does not only apply to RCTs. The authors need to state clearly if interviewers were aware which group the infant was in - whether the infant was EBB, EDB, or MF. The student would be most robust if the interviewers had no knowledge of which feeding group the infant belonged to. If they were aware if it, the authors would need to state it in the methods section and acknowledge it as a potential bias in data collection, even if the interviewers were trained. 

4. The IGSQ scores at 1 month, as well as presence of the various GI symptoms (vomiting, feeding difficulties etc) were already different in all 3 groups. Authors themselves stated that at month 1 MF group was significantly different using all 3 models.

This in itself means that reverse causation could be the explanation for all the subsequent differences the authors have noted in this study. In addition, if at month 1, these differences were present, then should it not be a confounding factor (baseline characteristic) that would need to be corrected for in the analysis (just like baseline characteristics of maternal education etc)

 5. I think the data in supp table 10c is interesting and worth including in the main paper. Particularly the time varying exposure data. The time varying exposure seems to imply that no significant difference between EBB and EBD with regards to vomiting, constipation and diarrhoea - this makes physiological and biological sense. There is a difference/ trend to difference in bloating and swallowing difficulties - which has a plausible explanation. Bottle fed infants are likely to complain of more bloating than direct breast-fed infants. Bottle fed infants also likely to have more associated perceived swallowing difficulties. These differences are more consistent between MF and EDB.

It would be good if authors highlight data which can be explained in a biologic/ physiologic manner, rather than make inference which are likely associations or could be explained by reverse causation

Author Response

Comment 1

It would be good if the authors can state if the formula fed infants were given formulas containing pre and/or probiotics. They had alluded to the impact of pre-probiotics in infant formula in the discussion, and readers would then question whether the infants in this particular study had pro or prebiotics in their formula.

Response :

We thank the reviewer for this comment. We acknowledge that we did not systematically collect information on whether the formula contained prebiotics or probiotics. In this real‑world observational study, the choice of formula brand in the MF group was made by families. We recorded the main brands used by each infant (including ZChO, Aitaimi, Feihe, Royal Friso, Wyeth Illuma, a2, Jindingguan, Biostime, Mead Johnson, Youbo, Nestlé, Junlebao, Beingmate, Kabrita, Hipp, etc.). According to publicly available product information, some brands (e.g., Biostime, Youbo Ruimu, Jindingguan Zhenhu) explicitly add probiotics or prebiotics, while others do not or have unclear information. Because we did not require a uniform formula type and did not quantitatively analyze the intake of probiotics/prebiotics for each infant, we cannot evaluate their independent effect on gastrointestinal symptoms. This missing information is acknowledged as a potential source of residual confounding in the limitations section (page 17, line 544).

 

Comment 2

Caregivers and recall bias. The authors could include more explicitly if it were mothers who completed the questionnaires at all time points or whether alternative caregivers did so.

Response :

We thank the reviewer for this clarification. According to the study protocol, each follow‑up visit (1, 4, 6, and 12 months of age) required the collection of biological samples (e.g., breast milk, infant stool), so the infant’s mother had to be present. The protocol explicitly stated that all questionnaires (including infant feeding and gastrointestinal symptom questionnaires) must be completed by the mother herself under the guidance of research staff, with her signature at the end of each questionnaire; no other caregiver (e.g., father, grandparent) was allowed to fill them in. This design ensured that the questionnaires at all time points were completed by the same reporter (the mother), minimizing recall bias due to different reporters. We have added this clarification in the Methods section (2.5 Quality control, page 5, line 194).

Comment 3

Blinding - the word blinding basically means - unaware of which group the patient (infant) belonged to. i.e. it does not only apply to RCTs. The authors need to state clearly if interviewers were aware which group the infant was in - whether the infant was EBB, EDB, or MF. The study would be most robust if the interviewers had no knowledge of which feeding group the infant belonged to. If they were aware of it, the authors would need to state it in the methods section and acknowledge it as a potential bias in data collection, even if the interviewers were trained.

Response :

We thank the reviewer for this definition. We clearly state that the interviewers were not blinded to the infants’ feeding groups. At each visit, interviewers recorded detailed feeding behaviours (direct breastfeeding, bottle‑feeding of expressed breast milk, or formula introduction) using structured questionnaires; therefore, they were aware of whether an infant belonged to the EDB, EBB, or MF group. To minimize potential information bias, all interviewers received standardized training and used closed‑ended questions without probing or interpretation during data collection. We have stated the lack of blinding in the Methods section (2.5 Quality control, page 5, line 197) and acknowledged it as a potential bias in data collection, particularly for subjective symptom assessment, in the limitations section (page 16, line 542).

 

Comment 4

The IGSQ scores at 1 month, as well as presence of the various GI symptoms (vomiting, feeding difficulties etc) were already different in all 3 groups. Authors themselves stated that at month 1 MF group was significantly different using all 3 models. This in itself means that reverse causation could be the explanation for all the subsequent differences the authors have noted in this study. In addition, if at month 1, these differences were present, then should it not be a confounding factor (baseline characteristic) that would need to be corrected for in the analysis (just like baseline characteristics of maternal education etc).

Response:

We thank the reviewer for this important point. We agree that reverse causation is a potential source of bias. In the main analysis, because feeding practices and 1‑month outcomes were collected at the same time point, we included 1 month as baseline in the GEE model (without adjusting for itself) to estimate the average differences over the entire follow‑up. In addition, following the reviewer’s suggestion, we performed a sensitivity analysis: we excluded the 1‑month outcome data, analyzed only outcomes at 4, 6, and 12 months, and additionally adjusted for the corresponding symptom at 1 month (or baseline IGSQ score) as a baseline covariate. The results are presented in new Tables 8a (symptoms) and 8b (IGSQ score). The main findings are as follows:

EBB group: Associations with constipation, diarrhoea, and vomiting were no longer significant after adjustment. This suggests that these associations in the main analysis may be partly due to reverse causation (i.e., symptoms present at 1 month influenced the mother’s choice of feeding mode).

MF group: Associations with constipation, vomiting, swallowing difficulty, and IGSQ score remained significant after adjustment. This indicates that the effects of mixed feeding on these outcomes are independent of baseline symptoms and more robust.

Bloating: Became significant for both EBB and MF after adjustment, supporting the biological plausibility that bottle‑feeding may increase the risk of bloating.

We have added a description of this sensitivity analysis in the Methods section (3.7, page 5, line 179) and discussed reverse causation in the limitations section (third point, page 16, line 546). We again thank the reviewer for this valuable suggestion.

 

Comment 5

I think the data in supp table 10c is interesting and worth including in the main paper. Particularly the time varying exposure data. The time varying exposure seems to imply that no significant difference between EBB and EBD with regards to vomiting, constipation and diarrhoea - this makes physiological and biological sense. There is a difference/ trend to difference in bloating and swallowing difficulties - which has a plausible explanation. Bottle fed infants are likely to complain of more bloating than direct breast-fed infants. Bottle fed infants also likely to have more associated perceived swallowing difficulties. These differences are more consistent between MF and EDB. It would be good if authors highlight data which can be explained in a biologic/ physiologic manner, rather than make inference which are likely associations or could be explained by reverse causation.

Response :

We thank the reviewer for this suggestion. In response, we have made the following modifications:

The key results of the time‑varying exposure analysis have been moved from the supplementary material to the main Results section (page 12, line 403). We clearly report that EBB was not significantly different from EDB for vomiting, constipation, or diarrhoea; bloating remained significantly higher (OR = 1.31, P = 0.042); and swallowing difficulty showed a borderline trend (OR = 1.48, P = 0.056).

In the Discussion section, we have added a new paragraph (page 15, line 503) explaining the biological mechanisms for both bloating and swallowing difficulty:

Bloating: The faster flow rate during bottle‑feeding may lead to increased air swallowing (aerophagia), thereby causing bloating. This association was significant in both the time‑varying and baseline‑adjusted sensitivity analyses, providing relatively robust evidence.

Swallowing difficulty: The faster flow rate during bottle‑feeding may challenge the infant’s oral motor coordination, leading to perceived swallowing difficulty. However, it should be noted that this association was not significant after adjustment for baseline symptoms (P = 0.158) and was unstable under the stricter symptom definition (possibly due to limited sample size); therefore, it should be interpreted with caution.

These modifications have been incorporated into the manuscript. We again thank the reviewer for the insightful comments.

 

Supplement: Removal of MDD Subgroup Analysis

We have removed the subgroup analysis based on minimum dietary diversity (MDD) at 6 months of age. The reasons are as follows: the non‑MDD subgroup had a very small sample size (n=129); only swallowing difficulty showed a significant interaction (P=0.045), with no consistent interactions for other symptoms; and the overall findings lacked robustness and were exploratory. To keep the main text focused on the most robust conclusions, we decided not to present these analyses.

Author Response File: Author Response.pdf