Bifidobacterium Longum subsp. infantis and Lacticaseibacillus Rhamnosus GG Protect Intestinal Epithelium Against Inflammation-Mediated Damage in an Immunocompetent In-Vitro Model

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for submitting the manuscript entiltled “Bifidobacterium longum subsp. infantis and Lacticaseibacillus rhamnosus GG protect intestinal epithelium against inflammation-mediated damage in an immunocompetent in-vitro model”. This is a well-executed study using an immunocompetent gut-on-chip model to assess the protective effects of Bifidobacterium infantis strains and Lacticaseibacillus rhamnosus GG against inflammation-mediated epithelial damage. The work is timely, methodologically rigorous, and relevant to the fields of probiotics, intestinal barrier function, and malnutrition.

The study convincingly shows that probiotic-conditioned media protect epithelial integrity through modulation of tight junction proteins and upregulation of homeostatic cytokines. The inclusion of PBMC donors increases translational value compared to standard monoculture models. However, there are several areas where the manuscript requires clarification, stronger contextualization, and refinement of claims before being suitable for publication.

Major Comments

1. Novelty and Positioning: The protective effects of infantisand LGG on intestinal barrier integrity are known. The novelty here is the PBMC co-culture gut-on-chip model, yet this contribution is underemphasized. It is suggeseted to strengthen the introduction and discussion by highlighting how this study advances beyond prior Caco-2 monoculture or animal models, and why donor-derived PBMCs add translational value.
2. Conditioned Media vs. Live Probiotics: The study uses bacterial supernatants rather than live probiotics. This is an elegant way to dissect metabolite-mediated effects, but it diverges from clinical use where live organisms are administered.Explicitly acknowledge this limitation in the discussion and frame the findings as “mechanistic insights” rather than directly translatable to supplementation outcomes.
3. Combination Treatment (B. infantis + LGG): The conclusion that LGG provides “no additional benefit” compared to B. infantis alone is underexplored. It is possible that metabolic redundancy, different growth kinetics, or competition explain this observation. Provide a deeper discussion of why the combination may not have added effects, and whether this finding aligns with (or contradicts) existing clinical data where probiotic mixtures are used.
4. Mechanism of Action – Cytokine Independence: The authors suggest the protective effect is “cytokine-independent,” yet the data only partially support this. Reduced diffusion of PBMC-derived cytokines across an intact barrier could also explain the results.It is suggested to reframe this claim more cautiously and add a discussion of alternative mechanisms (e.g., reduced cytokine diffusion due to preserved tight junctions etc).
5. Metabolomic Analysis: The metabolomic profiling (Fig. 5) is compelling but presented only as fold-change heatmaps. Without absolute concentrations, it is hard to judge biological relevance.It is suggested to provide at least representative concentration values for key metabolites (e.g., indole-3-lactic acid, SCFAs). Discuss whether the observed levels are physiologically relevant in vivo.
6. Clinical Implications: The abstract and discussion sometimes overstate the clinical impact (“could contribute to alleviating intestinal enteropathy in malnourished children”). Temper these claims. Recommend wording such as: “Our findings suggest that probiotic metabolites may contribute to epithelial protection and warrant further in vivo investigation.”
7. Strain Variability and HMO Utilization: The manuscript acknowledges that different B. infantis strains may vary in their ability to metabolize HMOs (lines 50–52). However, this is not deeply tied into the results. Since strain-specific differences are central to probiotic efficacy, the authors could strengthen the discussion by explicitly linking their metabolomic findings (e.g., indole-3-lactic acid production) to known genomic or metabolic differences between strains. the authors need to discuss whether the observed protective effects are strain-generalizable or strain-specific, and how this may impact probiotic selection in clinical settings.
8. Statistical Power and Donor Variability: While the authors used PBMCs from multiple donors, variability appears high in some results (e.g., cytokine data, Fig. 6). Although they mention batch effect correction, the manuscript would benefit from more transparency about sample size justification and donor characteristics. It is recommended reporting measures of inter-donor variability and possibly showing donor-level data in supplementary figures.
9. Choice of Endpoints: The reliance on TEER as the main barrier integrity readout is appropriate, but complementary functional assays (e.g., FITC-dextran permeability) could have strengthened conclusions.The authors need to acknowledge this limitation and clarify why TEER was chosen as the sole functional readout.
10. Role of Live Bacteria vs. Metabolites: You already flagged the conditioned media issue. In addition, the authors claim that probiotic effects may be mediated by metabolites like indole derivatives (lines 534–547). However, live bacteria can also interact via direct cell signaling (TLRs, adhesion, etc.).it is suggested to  expand the discussion to contrast metabolite-mediated vs. live-cell-mediated effects, and emphasize that both may be important in vivo.

Minor Comments

1. Abstract: Revise wording: “via modulation of tight-junction proteins and homeostatic cytokines gene transcription”  “via modulation of tight-junction proteins and transcription of homeostatic cytokines.”Avoid clinical extrapolations in the abstract; keep conclusions limited to the in vitro findings.
2. Figures: Figure 2C & Figure 7: The heatmaps are informative but may be hard to read for non-specialists. Consider clearer annotation of up- vs down-regulated genes.
3. Figure 4: The boxplots are cluttered; grouping strains or simplifying the color scheme would improve readability.
4. Methods: Provide demographic details of PBMC donors (age, sex, health status) as these can influence immune responses.Clarify whether donor-to-donor variability was modeled statistically (beyond batch correction).
5. Terminology consistency:The manuscript switches between “Lacticaseibacillus rhamnosus GG” and “LGG®” inconsistently. Recommend standardizing throughout.
6. Figures: 3 and Fig. 4 – The dose-dependent effect of B. infantis ATCC 15697 (Fig. 3) is interesting but not well contextualized later. It is suggested that the authors briefly discuss why this strain’s effect was quantified dose-dependently, whereas others were not.
7. 5 (metabolomics):add inclusion of error bars or variance indicators, not just fold-change heatmaps.
8. Methods clarity:PBMC stimulation was done with a mix of three E. coli LPS strains (line 105). it is suggested that the rationale for using multiple strains be explained.
9. Language: The paper sometimes uses anthropomorphic language (“probiotics protect epithelium”), which could be rephrased more neutrally (“probiotic-conditioned media mitigated TEER reduction”)
10. Language/Clarity: Several long sentences reduce readability (e.g., lines 502–510). Shorten and clarify.Correct typographical errors: page 10 (“Bacteria were growth medium was supplemented”) should be “Bacteria were grown in medium supplemented.
11. Conclusions in the abstract are too strong (“could contribute to alleviating intestinal enteropathy in malnourished children”) for an in vitro study. Should be rephrased to indicate potential relevance and limited to in vitro findings.
12. Species Names:Ensure consistent italicization throughout. Example: “LGGculture” (p. 11) → should be L. rhamnosus GG culture. Use Bifidobacterium longum subsp. infantis (B. infantis) at first mention, then B. infantis consistently (always italicized).
13. Grammar / Typographic Errors:Page 10: “Bacteria were growth medium was supplemented …” → should be “Bacteria were grown in medium supplemented …”.
14. Discussion (lines 502–510):sentence too long and unclear; needs splitting for readability.
15. Review manuscript for minor typos and spacing inconsistencies.
16. References: The discussion cites relevant literature but could expand on mechanistic links between indole metabolites and AhR/Nrf2 pathways in epithelial protection.
17. The manuscript is generally well structured; however, the authors should carefully revise it to fully conform with the Applied Microbiology (MDPI) formatting requirements.

Author Response

Response to Reviewer 1 comments

1. Summary

First, we would like to thank you sincerely for your time and efforts you invested in the thorough review of our manuscript. We believe that thanks to your constructive criticism we could significantly improve the paper, making the main message clearer while avoiding overstatements. We tried to address as many points as possible among those you raised. Besides rewriting the manuscript, we re-analyzed most of the data and generated new, we believe clearer, figures. However, some suggestions involving repeating the experiment are not possible, unfortunately, due to unavailability of the original samples and the actual closure of the lab, as well as the entire Bioaster institute in this month.
Please find below the detailed response to your comments.

2. Major comments
3. Novelty and Positioning: The protective effects of infantis and LGG on intestinal barrier integrity are known. The novelty here is the PBMC co-culture gut-on-chip model, yet this contribution is underemphasized. It is suggeseted to strengthen the introduction and discussion by highlighting how this study advances beyond prior Caco-2 monoculture or animal models, and why donor-derived PBMCs add translational value.
   Response: We agree with this comment. A relevant paragraph was added to the discussion: “Based on previous monoculture studies, both LGG and infantis exhibited protective effects on the epithelial barrier, reducing pro-inflammatory cytokine secretion and stabilizing expression of tight junction proteins such as ZO-1, Occludin, and Claudin-1 [16-20]. However, by incorporating PBMCs into the co-culture, our model revealed additional probiotic effects on homeostatic cytokines (TSLP, IL-18) and Claudin family gene regulation, findings that have not been previously reported. Unlike monoculture-based studies — where inflammation is typically induced by direct epithelial exposure to microbial molecules (e.g. LPS, flagellin) or pro-inflammatory cytokines (e.g. IL-1β) — our model reproduces a systemic inflammation mediated by PBMC activation following simulated microbial translocation to the blood stream. This approach resembles advanced disease states characterized by severe epithelial barrier dysfunction, such as inflammatory bowel disease (IBD), sepsis, and acute malnutrition, thereby providing a relevant platform to study barrier-protective mechanisms of probiotics in the context of systemic inflammation. (Lines 664-677)
4. Conditioned Media vs. Live Probiotics: The study uses bacterial supernatants rather than live probiotics. This is an elegant way to dissect metabolite-mediated effects, but it diverges from clinical use where live organisms are administered. Explicitly acknowledge this limitation in the discussion and frame the findings as “mechanistic insights” rather than directly translatable to supplementation outcomes.
   Response: We agree with his comment. This limitation was acknowledged and discussed:
   “Although live bacteria were not included in our experimental setup, bacterial supernatants likely contained cell debris and extracellular vesicles bearing TLR2 ligands, including lipoproteins, lipoteichoic acid, and peptidoglycan fragments [73] that may have contributed to epithelial reinforcement via TLR-mediated signaling.” “(lines 629 – 632); “Although the current Gut-on-a-Chip model cannot fully replicate the complex interplay among live probiotics, intestinal microbiota, and host tissues in vivo,…” (lines 659 -660)
5. Combination Treatment (B. infantis + LGG): The conclusion that LGG provides “no additional benefit” compared to B. infantis alone is underexplored. It is possible that metabolic redundancy, different growth kinetics, or competition explain this observation. Provide a deeper discussion of why the combination may not have added effects, and whether this finding aligns with (or contradicts) existing clinical data where probiotic mixtures are used.

Response: We agree with his comment. The limitation of this conclusion to the particular in-vitro experimental settings used in this study was acknowledged and the possible explanations discussed: “This lack of synergy may be attributed to differences in bacterial growth kinetics, nutrient competition, or the medium composition in co-culture, which differ substantially from in vivo conditions.” (lines 650-652); “The protective effect of LGG maty rely on other soluble molecules such as previously described Msp1/p75 and p40 proteins and exopolysaccharide components” (lines 656-657).

4. Mechanism of Action – Cytokine Independence: The authors suggest the protective effect is “cytokine-independent,” yet the data only partially support this. Reduced diffusion of PBMC-derived cytokines across an intact barrier could also explain the results.It is suggested to reframe this claim more cautiously and add a discussion of alternative mechanisms (e.g., reduced cytokine diffusion due to preserved tight junctions etc).
   Response: More tight epithelial barrier can indeed slow down the diffusion of cytokines from the Basal to Lumen channel which probably explains some reduction of IL-8 concentration seen when probiotics’ sup were added to the Lumen channel (Fig 4B). We further elaborated this point in the Discussion and mentioned that further investigations are required to clarify this issue: “A plausible explanation is that cytokines detected in the Lumen channel may primarily diffuse from the Basal (PBMC-containing) compartment, rather than being secreted de novo by Caco-2 cells. Once these cytokines reach the epithelial cells grown on a collagen matrix separating the two channels, they induce epithelial barrier loosening, further accelerating diffusion into the Lumen channel. Since probiotic supernatants preserved epithelial integrity, they may have indirectly reduced cytokine diffusion from the Basal compartment. Thus, the observed decrease in luminal cytokine concentrations could reflect reduced permeability, rather than direct modulation of cytokine secretion by epithelial cells—a hypothesis warranting further investigation » (Lines 599 – 607).
   Regarding “Reduced diffusion of PBMC-derived cytokines across an intact barrier “: most of cytokine receptors are found also on the basolateral side of the epithelial cells so cytokines produced by PBMC will diffuse through the Collagen and reach the cells that grow directly on it in a way that no tight junction barriers need to be crossed. Of note, the assessed TEER actually represents the barrier tightness of cells directly growing on Collagen (there is no other way for the current to path between the channels).

• Metabolomic Analysis: The metabolomic profiling (Fig. 5) is compelling but presented only as fold-change heatmaps. Without absolute concentrations, it is hard to judge biological relevance.It is suggested to provide at least representative concentration values for key metabolites (e.g., indole-3-lactic acid, SCFAs). Discuss whether the observed levels are physiologically relevant in vivo.
  Response: Absolute concentrations of upregulated metabolites were presented in a new Figure S2 and added to Results section (lines 485 – 486). The relevance of the observed ILA concentration was acknowledged in the discussion: “Among these, ILA was the most abundant, produced at concentrations of approximately 25–40 µM by infantis strains, consistent with previously reported levels of this metabolite in the feces of healthy infants [77, 78]» (lines 638 -940).

6. Clinical Implications: The abstract and discussion sometimes overstate the clinical impact (“could contribute to alleviating intestinal enteropathy in malnourished children”). Temper these claims. Recommend wording such as: “Our findings suggest that probiotic metabolites may contribute to epithelial protection and warrant further in vivo investigation.”
   Response: “These findings demonstrate that infantis and/or LGG may have the potential to protect the intestinal epithelium and thus could contribute to alleviating intestinal enteropathy in malnourished children.” Had been replaced in the abstract by “These findings show that metabolites from B. infantis and/or LGG probiotics can protect the intestinal epithelium in vitro, warranting further in vivo studies to assess the translational relevance of this effect. » (Line 27)
7. Strain Variability and HMO Utilization: The manuscript acknowledges that different B. infantis strains may vary in their ability to metabolize HMOs (lines 50–52). However, this is not deeply tied into the results. Since strain-specific differences are central to probiotic efficacy, the authors could strengthen the discussion by explicitly linking their metabolomic findings (e.g., indole-3-lactic acid production) to known genomic or metabolic differences between strains. the authors need to discuss whether the observed protective effects are strain-generalizable or strain-specific, and how this may impact probiotic selection in clinical settings.
   Response: We thank the reviewer for the thoughtful comments regarding links between infantis strain genomic variation and metabolite profiles. Nevertheless, we believe that a comprehensive analysis of strain-level genomic differences and metabolomics is beyond the scope of this manuscript, and our experimental design was not powered to detect such differences.

We also used a simplified HMO cocktail (LNT and 2′-FL), which—while among the most abundant HMOs in human milk—may under- or overrepresent strain-specific metabolic differences in vitro relative to the diverse HMO milieu present in vivo. Our main objective was to perform a functional (TEER) comparability study by using the supernatants from multiple B. infantis strains (most already commercialized). Despite known genomic and metabolic differences among B. infantis strains (e.g., PMID: 33114073), the overall metabolomic profile appears similar for the tested strains in our experimental settings (Fig. 5). Moreover, the tested B. infantis strains also had similar epithelial barrier protection capacity (Fig. 4) hence we consider that discussing the different ability to degrade HMOs is irrelevant here. We also remove the mentioned lines from the introduction and discussion for consistency.

8. Statistical Power and Donor Variability: While the authors used PBMCs from multiple donors, variability appears high in some results (e.g., cytokine data, Fig. 6). Although they mention batch effect correction, the manuscript would benefit from more transparency about sample size justification and donor characteristics. It is recommended reporting measures of inter-donor variability and possibly showing donor-level data in supplementary figures.
   Response: Donor inclusion criteria and characteristics were added in Materials & Methods section: - “adult volunteers with no history of chronic inflammatory or autoimmune disorders, and no acute infectious disease at the time of sampling. Participants had not received any antimicrobial, antihistaminic, or anti-inflammatory treatment within the four weeks preceding the sampling. “ (lines 85 – 88) – and in Table S2 respectively.
   One of the objectives of this study was to set up and demonstrate the use of in-vitro Gut-on-Chip model enabling epithelial and immune cells cross-talk. We used LPS-stimulated PBMC to mimic the disease state where microbial antigens have translocated into bloodstream. We demonstrate here that this model can be used for screening for probiotic immunomodulatory/homeostatic effect despite the intrinsic variability of human PBMC from healthy donors. The donor-to-donor variation was corrected during data analysis (explained in Materials & Methods section 2.11). In any case, the overall donors number is not high enough to proceed with donor-level correlation analysis. The raw data is nevertheless available in supplementary material in an Excel file for the interested researchers.
9. Choice of Endpoints: The reliance on TEER as the main barrier integrity readout is appropriate, but complementary functional assays (e.g., FITC-dextran permeability) could have strengthened conclusions. The authors need to acknowledge this limitation and clarify why TEER was chosen as the sole functional readout.
   Response: During the early steps of model set-up we compared the results obtained with TEER and FITC-Dextran permeability and found the former to be more sensitive, besides being technically easier to perform. We consider that the manuscript will not benefit from publishing these results as it will hinder the focus from the central narrative to technical details that do not contribute to the understanding of the study.

1. Role of Live Bacteria vs. Metabolites: You already flagged the conditioned media issue. In addition, the authors claim that probiotic effects may be mediated by metabolites like indole derivatives (lines 534–547). However, live bacteria can also interact via direct cell signaling (TLRs, adhesion, etc.).it is suggested to expand the discussion to contrast metabolite-mediated vs. live-cell-mediated effects, and emphasize that both may be important in vivo.
   Response: We agree with this comment. The relevant sentences were added to the discussion: “Although live bacteria were not included in our experimental setup, bacterial supernatants likely contained cell debris and extracellular vesicles bearing TLR2 ligands, including lipoproteins, lipoteichoic acid, and peptidoglycan fragments [73] that may have contributed to epithelial reinforcement via TLR-mediated signaling. (lines 629 – 632)

 

3. Minor comments
   1. Abstract: Revise wording: “via modulation of tight-junction proteins and homeostatic cytokines gene transcription”  “via modulation of tight-junction proteins and transcription of homeostatic cytokines.”Avoid clinical extrapolations in the abstract; keep conclusions limited to the in vitro findings.
      Response: we revised the relevant lines accordingly (lines 25 – 27) and more cautios conclusion statements made without direct clinical implications “These findings indicate that metabolites produced by B. infantis and/or LGG can protect the intestinal epithelium in vitro, warranting further in vivo studies to evaluate the translational relevance of this effect. (Lines 28 -30)
4. Figures: Figure 2C & Figure 7: The heatmaps are informative but may be hard to read for non-specialists. Consider clearer annotation of up- vs down-regulated genes.
   Response: We think that the color code is rather straight forward: upregulated is in red, downregulated is in blue, and not deregulated is in white. We’d like to keep the information of LFC value (and not just the classification up/down) and labelled the tiles by p-values. We consider that adding further information on those heatmaps to flag up and down genes/cytokines/metabolites would result in a too heavy and cluttered figure, and therefore decided not to modify the heatmaps.
5. Figure 4: The boxplots are cluttered; grouping strains or simplifying the color scheme would improve readability.
   Response: We modified the colors of the boxplots and removed the jitter dots, limiting to boxes and outliers.
6. Methods: Provide demographic details of PBMC donors (age, sex, health status) as these can influence immune responses.Clarify whether donor-to-donor variability was modeled statistically (beyond batch correction).
   Response: Donor inclusion criteria and characteristics were added in Materials & Methods section (lines 85 – 87) and in Table S2 respectively. To account for the inter-donor variability in our statistical analyses, we replaced the Wilcoxon test by a linear fixed-effect model, taking the donor information as a random intercept, except for the gene transcription analysis where the donor effect was corrected prior to statistical analysis.
7. Terminology consistency:The manuscript switches between “Lacticaseibacillus rhamnosus GG” and “LGG®” inconsistently. Recommend standardizing throughout.
   Response: Since its appearance in Introduction section “Lacticaseibacillus rhamnosus GG” is replaced with “LGG”.
8. Figures: 3 and Fig. 4 – The dose-dependent effect of B. infantis ATCC 15697 (Fig. 3) is interesting but not well contextualized later. It is suggested that the authors briefly discuss why this strain’s effect was quantified dose-dependently, whereas others were not.
   Response: B. infantis ATCC 15697 was used to set up the experimental system and find the optimal supernatant concentration to be used during the screen of other probiotics. No dose-response experiments were conducted for other strains and mixes. A sentence to clarify this point was added in the Results section: “). Consequently, the 30% (v/v) concentration was used for all subsequent experiments with other probiotic strains.” (Lines 427 – 429).
9. (metabolomics):add inclusion of error bars or variance indicators, not just fold-change heatmaps.
   Response: We have only one data point/condition, no statistics are possible, unfortunately
10. Methods clarity:PBMC stimulation was done with a mix of three E. coli LPS strains (line 105). it is suggested that the rationale for using multiple strains be explained.
    Response: The mix of LPS from three different serotypes of E.coli increases the probability of efficient activation of PBMC and was demonstrated previously by our group. The relevant paragraph in Material and Methods section was improved to clarify this point (lines 118-122).
11. Language: The paper sometimes uses anthropomorphic language (“probiotics protect epithelium”), which could be rephrased more neutrally (“probiotic-conditioned media mitigated TEER reduction”)
    Response: The language was corrected throughout the text
12. Language/Clarity: Several long sentences reduce readability (e.g., lines 502–510). Shorten and clarify.Correct typographical errors: page 10 (“Bacteria were growth medium was supplemented”) should be “Bacteria were grown in medium supplemented.
    Response: The errors were corrected and the general language revised
13. Conclusions in the abstract are too strong (“could contribute to alleviating intestinal enteropathy in malnourished children”) for an in vitro study. Should be rephrased to indicate potential relevance and limited to in vitro findings.
    Response: we revised the relevant lines accordingly (lines 25 – 27) and more cautious conclusion statements made without direct clinical implications “These findings indicate that metabolites produced by B. infantis and/or LGG can protect the intestinal epithelium in vitro, warranting further in vivo studies to evaluate the translational relevance of this effect. (Lines 28 -30)
14. Species Names: Ensure consistent italicization throughout. Example: “LGGculture” (p. 11) → should be L. rhamnosus GG culture. Use Bifidobacterium longum subsp. infantis (B. infantis) at first mention, then B. infantis consistently (always italicized).
    Response: The bacteria names correct writing was verified.
15. Grammar / Typographic Errors:Page 10: “Bacteria were growth medium was supplemented …” → should be “Bacteria were grown in medium supplemented …”.
    Response: The sentence was revised
16. Discussion (lines 502–510):sentence too long and unclear; needs splitting for readability.
    Response: The entire discussion section was as revised
17. Review manuscript for minor typos and spacing inconsistencies.
    Response: The entire manuscript passed revision and proof-reading again
18. References: The discussion cites relevant literature but could expand on mechanistic links between indole metabolites and AhR/Nrf2 pathways in epithelial protection.
    Response: We think that the cited references allow the readers to deepen their knowledge regarding the mechanism of indole metabolites and there is further expansion of this subject might blur the focus of the discussion.
19. The manuscript is generally well structured; however, the authors should carefully revise it to fully conform with the Applied Microbiology (MDPI) formatting requirements.
    Response: The formatting was corrected to fit with MDPI demands

Reviewer 2 Report

Comments and Suggestions for Authors

The present manuscript "Bifidobacterium longum subsp. infantis and Lacticaseibacillus rhamnosus GG protect intestinal epithelium against inflammation-mediated damage in an immunocompetent in-vitro model" by Belotserkovsky et al, describe an immunocompetent gut-on-a-chip model to test whether probiotic conditioned media from several probiotic bacterial strains can mitigate LPS/PBMC-driven epithelial barrier disruption. The authors demonstrated dose-dependent improvement of impaired gut barrier by probiotic supernatants and identified candidate metabolites that possibly mediate this effect. However, there are important gaps in reporting, data presentation and interpretation that limit reproducibility and comprehension.

My comments are as follows:

-The Introduction frames the problem mainly in the context of severe acute malnutrition. Please include epithelial barrier dysfunction (leaky gut) that occurs in other conditions (sepsis, inflammatory bowel disease, chemotherapy-induced mucositis, etc.) and briefly explain how pathophysiology differs between these settings for translational relevance.

-The manuscript explains benefits of organ-on-chip use, but the limitations should be explicit and concrete: lack of secretory intestinal cell types (goblet/Paneth/enteroendocrine), absence of an intact mucous layer, lack of tissue-resident immune cells (intraepithelial lymphocytes, lamina propria subsets), no continuous, full microbial community (including fungi, viruses), no mesenchymal/endothelial compartments. Authors briefly mention epithelial cell lines vs. in vivo models, but the relevant paragraph should list these specific limitations and their impact on interpretation.

-Methods state PBMCs were collected from healthy volunteers, but donor demographics and relevant clinical metadata are not reported (sex, age, vaccination status, antibiotic use, infectious disease history) nor are per-donor PBMC yields/cell counts reported. These factors can strongly impact cytokine responses and variability. Please add a Supplementary Table with: donor ID (anonymized), PBMC yield (cells/mL whole blood) and viability. If available, include: sex, age, relevant medication/antibiotic history, recent infections/vaccination.

-LPS stimulation protocol (timing, concentration, co-administration vs pre-treatment) needs clarification: methods indicate “5 days after Caco-2 seeding the medium in the opposite channel was exchanged with 10^5 PBMC in supplemented RPMI, with (or without) LPS mix of three strains of E. coli … at 100 ng/mL each.” This suggests PBMC and LPS were added together into the basal channel. If so, please state this clearly and justify the LPS dose (is it 100 ng/mL total or 100 ng/mL of each of three LPS preparations i.e., 300 ng/mL total? Rationale for choosing the dose, were dose-response studies conducted?). Also specify the duration of LPS exposure (from Methods and Results it appears cytokines and TEER were read at 3 days post-addition; please state explicitly). Clarify whether any wash or replacement steps occur after LPS addition. Please explain the potential effects of prolonged LPS exposure on PBMCs viability and relevance for real world situation. 

-Several Supplementary Tables were mentioned in the text but I was not able to find any in the attachment. It is essential to provide all tables listed and all materials and results. That said, the text refers to Table S2 listing TaqMan assays/Assay IDs, but authors should confirm whether primer/probe sequences are provided (for custom assays). If TaqMan catalog assays were used, list catalog/assay IDs and vendor; if custom assays were used, provide primer/probe sequences and amplicon sizes in Supplementary Materials. This is essential for reproducibility.

-The authors did not report IL-17 or the Th17 lineage master regulator RORγt. IL-17 and Th17 biology are central to intestinal immunity and epithelial homeostasis; please either measure IL-17A/IL-17F / RORC (RORγt) or explicitly justify omission.

-The authors partly address epithelial transcriptional changes (Fig.7) but did not test PBMC responses to supernatants directly. If feasible, direct vs indirect effects of probiotics should be outlined: 

• The current protocol adds probiotic supernatants apically and LPS-stimulated PBMC basally simultaneously. To dissect whether probiotic supernatants act directly on PBMC (modulating cytokine secretion) or indirectly on epithelium (protecting barrier independent of PBMC cytokines), the authors should perform:
  a) PBMC treated ex vivo with bacterial supernatants ± LPS, then analyze PBMC cytokine output (no Caco-2)
  b) PBMC conditioned medium (after ± supernatant exposure) applied to Caco-2 to assess TEER.  These experiments would clarify direct immunomodulation vs barrier-centric mechanisms. The authors partly address epithelial transcriptional changes (Fig.7) but did not test PBMC responses to supernatants directly.

-Also, in real settings, host exposure includes whole bacteria, cell fragments and secreted metabolites. The authors note they used supernatant and highlight TLR2 ligands could be present, but did not test killed bacteria, cell wall extracts, or purified MAMPs (e.g., peptidoglycan, lipoteichoic acid). Either add these comparisons or explicitly discuss as a limitation and how it might change interpretation.

-The cytokine results are reported as relative changes/heatmaps. Given inter-donor variability and the translational importance of cytokine magnitudes, provide raw pg/mL values for all cytokines measured (provide as Supplementary Table), and please also present representative bar/scatter plots (per donor) for key cytokines (IL-6, IL-8, TNFα, IFNγ). The Methods state Luminex/ELISA was used but raw numbers should be available for comparisons.

-The paper reports both cytokine panels and TEER but does not show whether cytokine levels correlate with TEER changes across donors/conditions. Please analyze and if relevant, present correlation/regression analyses (scatter plots with donors as points, r/ρ and p-value).

-Different figures use different donor numbers. Please provide a table (Supplementary) showing exactly which donors were used for each assay and why numbers differ (sample loss?). This should be noted in figure legends.

-Barrier loss may reflect tight-junction modulation or cell death. Authors should measure epithelial cells viability (e.g., LDH release, live/dead staining) or explicitly state they assessed morphology/ZO-1/Villin only and discuss limitations.

-For the metabolomics and SCFA/Tryptophan analyses please provide absolute concentrations (or at least units and calibration curves) as part of supplementary materials. Also indicate how metabolites were normalized (per mL, per protein?). Could the pH neutralization step could change metabolite composition?

-Figure 3: color coding requires explicit legend (which color = which dose/condition); clarify what the normalization baseline is and, in the main figure or legend, show % change relative to the “No sup, +LPS” condition as that is often the most informative comparator.

-Figure 4: enlarge panels and include legend.

-The Results re-state methods in some parts. Please reduce method details in Results section to improve readability.

Minor comments:

-rewrite line 55 for clarity.

-Add graphical abstract / timeline scheme. A simple schematic timeline (Caco-2 seeding day 0; PBMC ± LPS addition day 5; probiotic supernatant apical addition day 5; sampling points day 0, day1, day2, day3; assays at day3) will greatly increase understanding of the experimental settings. The OrganoPlate figure is useful but a timeline across days would be better to provide.

Author Response

1. Summary

We would like to thank you sincerely for the time and effort you invested in the thorough review of our manuscript. We believe that thanks to your constructive criticism we could significantly improve the paper, making the main message clearer while avoiding overstatements. We tried to address as many points as possible among those you raised. Besides rewriting the manuscript, we re-analyzed most of the data and generated new, we believe clearer, figures. However, some suggestions involving repeating the experiment are not possible, unfortunately, due to unavailability of the original samples and the actual closure of the lab, as well as the entire Bioaster institute in this month.
Please find below the detailed response to your comments.

2. Major comments

• Comment: The Introduction frames the problem mainly in the context of severe acute malnutrition. Please include epithelial barrier dysfunction (leaky gut) that occurs in other conditions (sepsis, inflammatory bowel disease, chemotherapy-induced mucositis, etc.) and briefly explain how pathophysiology differs between these settings for translational relevance.
  Response: We thank the reviewer for pointing out this flaw. A relevant paragraph was added to the Introduction section explaining the “leaky gut” phenomenon and its implication in various diseases: “Disruption of this barrier — often referred to as the “leaky gut” phenomenon — is im-plicated in a wide range of human pathologies, including inflammatory bowel disease (IBD), irritable bowel syndrome (IBS), sepsis, celiac disease and others.” (Lines 37 - 40). Besides, our model mainly recapitulates the epithelial barrier function and immune-cell mediated inflammation which are similar features to acute malnutrition and to other pathologies involving the leaky gut - a relevant sentence was added to the discussion: “our model reproduces a systemic inflammation mediated by PBMC activation following simulated microbial translocation to the blood stream. This approach resembles advanced disease states characterized by severe epithelial barrier dysfunction, such as inflammatory bowel disease (IBD), sepsis, and acute malnutrition, thereby providing a relevant platform to study barrier-protective mechanisms of probiotics in the context of systemic inflammation.” (Lines 671-677).
• Comment: The manuscript explains benefits of organ-on-chip use, but the limitations should be explicit and concrete: lack of secretory intestinal cell types (goblet/Paneth/enteroendocrine), absence of an intact mucous layer, lack of tissue-resident immune cells (intraepithelial lymphocytes, lamina propria subsets), no continuous, full microbial community (including fungi, viruses), no mesenchymal/endothelial compartments. Authors briefly mention epithelial cell lines vs. in vivo models, but the relevant paragraph should list these specific limitations and their impact on interpretation.
  Response: The relevant paragraph in Discussion was expanded: “ The intestinal wall comprises a diverse array of cell populations, including secretory epithelial cells (i.e. Goblet, Paneth, and enteroendocrine cells), intraepithelial and tis-sue-resident immune cells, as well as a dense mesh of vascular and neuronal networks. Several studies have demonstrated that primary, often biopsy-derived, intestinal epithelium containing multiple specialized epithelial cell types—along with endothelial and immune cells—can be successfully integrated into microfluidic systems, thereby reproducing mucus production, barrier function, and inflammatory signaling (reviewed in [55-57]).

Although such complex co-culture models more accurately mimic in vivo intesti-nal physiology compared to cell line–based systems, they are limited by technical com-plexity, donor-dependent variability, and low throughput, which collectively reduce experimental reproducibility. In the present study, we employed the Caco-2 cell line, which—while unable to replicate the full functional diversity of the intestinal epithelium—provides a robust and reproducible model of epithelial barrier function and cytokine secretion.” (lines 546 – 560).

• Comment: Methods state PBMCs were collected from healthy volunteers, but donor demographics and relevant clinical metadata are not reported (sex, age, vaccination status, antibiotic use, infectious disease history) nor are per-donor PBMC yields/cell counts reported. These factors can strongly impact cytokine responses and variability. Please add a Supplementary Table with: donor ID (anonymized), PBMC yield (cells/mL whole blood) and viability. If available, include: sex, age, relevant medication/antibiotic history, recent infections/vaccination.
  Response: Donor inclusion criteria and available characteristics were added in Materials & Methods section: - “adult volunteers with no history of chronic inflammatory or autoimmune disorders, and no acute infectious disease at the time of sampling. Participants had not received any antimicrobial, antihistaminic, or anti-inflammatory treatment within the four weeks preceding the sampling. “ (lines 85 – 88) – and in Table S2 respectively.
• Comment: LPS stimulation protocol (timing, concentration, co-administration vs pre-treatment) needs clarification: methods indicate “5 days after Caco-2 seeding the medium in the opposite channel was exchanged with 10^5 PBMC in supplemented RPMI, with (or without) LPS mix of three strains of E. coli … at 100 ng/mL each.” This suggests PBMC and LPS were added together into the basal channel. If so, please state this clearly and justify the LPS dose (is it 100 ng/mL total or 100 ng/mL of each of three LPS preparations i.e., 300 ng/mL total? Rationale for choosing the dose, were dose-response studies conducted?). Also specify theduration of LPS exposure (from Methods and Results it appears cytokines and TEER were read at 3 days post-addition; please state explicitly). Clarify whether any wash or replacement steps occur after LPS addition. Please explain the potential effects of prolonged LPS exposure on PBMCs viability and relevance for real world situation. 
  Response: The mix of LPS from three different serotypes of E.coli increases the probability of efficient activation of PBMC from different donors and was demonstrated previously by our group LPS was indeed added together with PBMC and stayed for 3 days. TEER was measured daily while cytokines assessed in the end of the experiment (the third day upon PBMC+LPS administration)
  The relevant paragraph in Material and Methods section was improved to clarify these points (lines 118-122) and a Graphical abstract with improved experimental settings and timeline was provided.
• Comment: Several Supplementary Tables were mentioned in the text but I was not able to find any in the attachment. It is essential to provide all tables listed and all materials and results. That said, the text refers to Table S2 listing TaqMan assays/Assay IDs, but authors should confirm whether primer/probe sequences are provided (for custom assays). If TaqMan catalog assays were used, list catalog/assay IDs and vendor; if custom assays were used, provide primer/probe sequences and amplicon sizes in Supplementary Materials. This is essential for reproducibility.
  Response: We used only catalog assays which is stated in lines 259 -260. The supplier’s name was added to the title of the Table S2 for better clarity. No custom probes were designed. Some of supplementary tables are provided as Excel files due to their size.
• Comment: The authors did not report IL-17 or the Th17 lineage master regulator RORγt. IL-17 and Th17 biology are central to intestinal immunity and epithelial homeostasis; please either measure IL-17A/IL-17F / RORC (RORγt) or explicitly justify omission.
  Response: Although IL-17 play an important role in epithelial homeostasis, it’s main source is Th17 cells that produce it at relatively low levels (18.9 pg/ml) without stimulation while LPS, used in our study, induces only very mild (+2 pg/ml) increase in IL-17 production (DOI: 4149/gpb_2013043). We thus did not expect IL-17 upregulation in our model and, since total cytokine number that we could test was limited, we did not include it in the panel.
• Comment: The authors partly address epithelial transcriptional changes (Fig.7) but did not test PBMC responses to supernatants directly. If feasible, direct vs indirect effects of probiotics should be outlined: 

The current protocol adds probiotic supernatants apically and LPS-stimulated PBMC basally simultaneously. To dissect whether probiotic supernatants act directly on PBMC (modulating cytokine secretion) or indirectly on epithelium (protecting barrier independent of PBMC cytokines), the authors should perform:
a) PBMC treated ex vivo with bacterial supernatants ± LPS, then analyze PBMC cytokine output (no Caco-2)
b) PBMC conditioned medium (after ± supernatant exposure) applied to Caco-2 to assess TEER.  These experiments would clarify direct immunomodulation vs barrier-centric mechanisms. The authors partly address epithelial transcriptional changes (Fig.7) but did not test PBMC responses to supernatants directly.
Response:  In this study we attempted to mimic (to some extent) the physiology in-vivo applying the probiotic supernatants in the apical side of epithelial cells and not mixing it directly with PBMC assuming that such interaction is not happening in humans. We agree that the proposed set of experiments could help clarifying the role of PBMC in the protective effect of probiotic supernatants. Unfortunately, there is no possibility to perform these experiments due to the closure of our lab and the entire institute.

• Comment: Also, in real settings, host exposure includes whole bacteria, cell fragments and secreted metabolites. The authors note they used supernatant and highlight TLR2 ligands could be present, but did not test killed bacteria, cell wall extracts, or purified MAMPs (e.g., peptidoglycan, lipoteichoic acid). Either add these comparisons or explicitly discuss as a limitation and how it might change interpretation.
  Response: We agree with this comment. This limitation was acknowledged and discussed:
  “Although live bacteria were not included in our experimental setup, bacterial supernatants likely contained cell debris and extracellular vesicles bearing TLR2 ligands, including lipoproteins, lipoteichoic acid, and peptidoglycan fragments [73] that may have contributed to epithelial reinforcement via TLR-mediated signaling.” “(lines 629 – 632); “Although the current Gut-on-a-Chip model cannot fully replicate the complex interplay among live probiotics, intestinal microbiota, and host tissues in vivo,…” (lines 659 -660)
• Comment: The cytokine results are reported as relative changes/heatmaps. Given inter-donor variability and the translational importance of cytokine magnitudes, provide raw pg/mL values for all cytokines measured (provide as Supplementary Table), and please also present representative bar/scatter plots (per donor) for key cytokines (IL-6, IL-8, TNFα, IFNγ). The Methods state Luminex/ELISA was used but raw numbers should be available for comparisons.
  Response: The raw data of absolute cytokine concentrations (pg/mL) per donor is now shown in supplementary Figure S3
• Comment: The paper reports both cytokine panels and TEER but does not show whether cytokine levels correlate with TEER changes across donors/conditions. Please analyze and if relevant, present correlation/regression analyses (scatter plots with donors as points, r/ρ and p-value).
  Response: One of the objectives of this study was to set up and demonstrate the use of in-vitro Gut-on-Chip model enabling epithelial and immune cells cross-talk. We used LPS-stimulated PBMC to mimic disease state where microbial antigens have translocated into bloodstream. We demonstrate here that this model can be used for screening for probiotic immunomodulatory/homeostatic effect despite the intrinsic variability of human PBMC from healthy donors. The donor-to-donor variation was corrected during data analysis (see section 2.11 in Material and Methods). In any case, the overall donors number is not high enough to proceed with donor-level correlation analysis. The raw data is nevertheless available in supplementary material in an Excel file for the interested researchers.
  • Comment: Different figures use different donor numbers. Please provide a table (Supplementary) showing exactly which donors were used for each assay and why numbers differ (sample loss?). This should be noted in figure legends.
    Response: The requested information is now presented in Table S2 and figure legends were revised for better clarity.
• Comment: Barrier loss may reflect tight-junction modulation or cell death. Authors should measure epithelial cells viability (e.g., LDH release, live/dead staining) or explicitly state they assessed morphology/ZO-1/Villin only and discuss limitations.
  Response: During the early steps of model set-up we assessed the effect of inflammation on TEER, LDH release and Live/dead staining of Caco-2. We found that TEER was much more sensitive compared to other two tests reacting rapidly (16 – 24h) to inflammation induction while cell death and LDH release were mostly evident after 3 days. We consider that the manuscript will not benefit from publishing these results as it will hinder the focus from the central narrative to technical details that do not contribute to the understanding of the study.
  While cell morphology alteration could be of real additional value, we had to choose between this readout and gene transcription analysis that demands cell lysis. Besides, TEER assessments using OrganoTEER equipment is the only method compatible with the mid-throughput approach that we are demonstrating in the present manuscript.
  • Comment: For the metabolomics and SCFA/Tryptophan analyses please provide absolute concentrations (or at least units and calibration curves) as part of supplementary materials. Also indicate how metabolites were normalized (per mL, per protein?). Could the pH neutralization step could change metabolite composition?
    Response: Absolute concentrations (in µM) of upregulated metabolites are now presented in Figure S2.

During the analysis of the SCFAs the samples are derivatized with hydrochloric acid to make them more volatile which reduces hydrogen bonding and improves peak shape in the GC. Without this step, the SCFAs won’t vaporize properly in the injector. As the samples in the study were analysed with absolute quantification using calibration curves in the run, this means that all changes affecting the samples will also be reflected in the calibration curves; therefore, the composition in terms of metabolite quantities were accurately calculated.

• Comment: Figure 3: color coding requires explicit legend (which color = which dose/condition); clarify what the normalization baseline is and, in the main figure or legend, show % change relative to the “No sup, +LPS” condition as that is often the most informative comparator.
  Response: Normalizing the data to the control will make it easier to see the effect of the treatments but this way the important temporal data regarding the TEER evolution of the controls will be lost. We modified the colors of the figures and added a grey horizontal line to emphasize the TEER level used for comparison at each time point.
• Comment: Figure 4: enlarge panels and include legend.
  Response: The figure was modified to improve clarity
• Comment: The Results re-state methods in some parts. Please reduce method details in Results section to improve readability.
  Response: As this model is not widely used and the understanding of the experimental settings is vital for the understanding of the results we prefer to provide the necessary details in the Results section despite some redundancy with Materials&Methods section.

 

3. Minor comments

• Comment: rewrite line 55 for clarity.
  Response: The sentences was revised: “All strains were cultured in a medium supplemented with two abundant HMOs found in human breast milk: 2′-Fucosyllactose (2′-FL) and Lacto-N-tetraose (LNT)” (line 64-65).
• Comment: Add graphical abstract / timeline scheme. A simple schematic timeline (Caco-2 seeding day 0; PBMC ± LPS addition day 5; probiotic supernatant apical addition day 5; sampling points day 0, day1, day2, day3; assays at day3) will greatly increase understanding of the experimental settings. The OrganoPlate figure is useful but a timeline across days would be better to provide.
  Response: Graphical abstract with experimental settings and timeline was added.

Reviewer 3 Report

Comments and Suggestions for Authors

While the manuscript addresses a relevant and timely question including probiotic effects on epithelial barrier function in the context of malnutrition, the experimental design, data presentation, and interpretation fall short of the standards required for publication.

1. The manuscript frequently refers to malnourished children in the Abstract and Discussion. However, the experiments were conducted entirely in an in vitro co-culture model. While the model may mimic some aspects of enteropathy, the direct extrapolation to malnourished children is overstated. The authors must clarify this limitation and temper their claims accordingly.
2. The Methods describe the use of 2′-fucosyllactose (2′-FL) and Lacto-N-tetraose (LNT), and the Introduction highlights the strain-specific capacity of B. infantis to metabolize HMOs. Yet, the Abstract only briefly mentions HMO, and the Discussion does not sufficiently elaborate on how HMO metabolism may influence the outcomes.
3. The Results section lacks clear subheadings and logical flow. The narrative moves between TEER data, cytokine secretion, and gene expression without clear transitions.
4. The results for the ATCC 15697 reference strain are presented as an isolated section. This figure could be streamlined by directly comparing its effects with the other tested strains, rather than devoting an entire figure to one strain alone.
5. The rationale for choosing Bifin02, LGG, and their combination is not fully explained. Moreover, some experiments include LGG alone, while others omit it. This inconsistency raises questions about the overall experimental design and interpretation. The absence of LGG-only conditions in certain assays is particularly problematic.
6. The study focuses primarily on IL-8 secretion as the major cytokine outcome, despite having multiplex cytokine data. Why was IL-8 prioritized? Were other cytokines consistently non-significant, or was the analysis incomplete? The justification is lacking.
7. The figures are presented in different formats (heatmaps, bar graphs, line graphs) with inconsistent color schemes. This inconsistency makes interpretation difficult. The figures should be standardized in style and formatting.
8. Although metabolomics data are provided, no functional validation experiments are included. Without additional mechanistic studies such as blocking indole signaling or tight-junction protein modulation, the conclusions remain largely correlative.
9. Many of the observed probiotic effects were modest, variable, or not statistically significant (e.g., cytokine modulation). The Discussion nonetheless extrapolates these results to propose protective roles in malnourished children, which is premature and unsupported by the evidence.
10. The final paragraph of the Discussion claims that probiotics “demonstrate the potential to protect the intestinal epithelium” and suggests translational implications. Given the largely descriptive results and lack of mechanistic validation, this conclusion is overstated. A more cautious interpretation is warranted.

Author Response

Summary

We would like to thank you for the time and effort you invested in the review of our manuscript. We believe that thanks to your remarks we could significantly improve the paper, making the main message clearer while avoiding overstatements. Besides rewriting the manuscript, we re-analyzed most of the data and generated new, we believe clearer, figures. However, some suggestions involving repeating the experiment are not possible, unfortunately, due to unavailability of the original samples and the actual closure of the lab, as well as the entire Bioaster institute in this month.
Please find below the detailed response to your comments.

Detailed reply

• Comment 1: The manuscript frequently refers to malnourished children in the Abstract and Discussion. However, the experiments were conducted entirely in an in vitro co-culture model. While the model may mimic some aspects of enteropathy, the direct extrapolation to malnourished children is overstated. The authors must clarify this limitation and temper their claims accordingly.

Response: the Abstract was modified to address this point: “These findings indicate that metabolites produced by B. infantis and/or LGG can protect the intestinal epithelium in vitro, warranting further in vivo studies to evaluate the translational relevance of this effect.” (lines 28 -30).
The discussion was revised and the claims were modified to focus on only mechanistic investigations use of the model: “This approach resembles advanced disease states characterized by severe epithelial barrier dysfunction, such as inflammatory bowel disease (IBD), sepsis, and acute malnutrition, thereby providing a relevant platform to study barrier-protective mecha-nisms of probiotics in the context of systemic inflammation.” (lines 673 – 677).

• Comment 2: The Methods describe the use of 2′-fucosyllactose (2′-FL) and Lacto-N-tetraose (LNT), and the Introduction highlights the strain-specific capacity of  infantisto metabolize HMOs. Yet, the Abstract only briefly mentions HMO, and the Discussion does not sufficiently elaborate on how HMO metabolism may influence the outcomes.

Response: The role of HMO metabolism was strengthened in the Discussion section: “Notably, ILA is found at higher concentrations in breastfed infants, who are enriched Bifidobacterium species, supporting a correlation between HMO consumption, bifidobacterial abundance, and ILA production [77-81]. Our results align with earlier studies describing HMO-dependent ILA biosynthesis by B. infantis [78, 81, 82], …”  (lines 640 – 644)

• Comment 3: The Results section lacks clear subheadings and logical flow. The narrative moves between TEER data, cytokine secretion, and gene expression without clear transitions.

Response: The study consists of three major parts: model set up (Fig. 1 - 3); screen of 6 probiotics using TEER and IL-8 as read-outs accompanied by metabolomic analysis of the supernatants (Fig. 4); and finally mode-of -action investigation of three selected probiotics using extended cytokine and gene transcription analysis (Fig. 6 – 7). The results section was modified to make the narrative clearer.

• Comment 4: The results for the ATCC 15697 reference strain are presented as an isolated section. This figure could be streamlined by directly comparing its effects with the other tested strains, rather than devoting an entire figure to one strain alone.

Response: This figure demonstrates the dose-dependent effect of probiotic supernatant which was tested only for the ATCC 15697 strain. This is an important finding and we think that it is better to keep it in the main text of the manuscript.

• Comment 5: The rationale for choosing Bifin02, LGG, and their combination is not fully explained. Moreover, some experiments include LGG alone, while others omit it. This inconsistency raises questions about the overall experimental design and interpretation. The absence of LGG-only conditions in certain assays is particularly problematic.

Response:
The rational for choosing ATCC, Bifin02 and Combo for the third part of the study is now explained: “Given the similarity in metabolomic profiles and biological effects among the individual B. infantis strains on epithelial barrier integrity and IL-8 secretion, we next investigated the potential mechanism of action focusing on the reference strain ATCC 15697, the Bifin02 probiotic strain, and the combination of Bifin02 with LGG (“Combo”) to evaluate the possible additive contribution of LGG within the two-strain formulation” (Lines 495 -499).
The objective of the study was to assess possible additional effect of LGG when it is added to B. infantis. Investigating LGG effect alone was not in the scope of the study.

• Comment 6: The study focuses primarily on IL-8 secretion as the major cytokine outcome, despite having multiplex cytokine data. Why was IL-8 prioritized? Were other cytokines consistently non-significant, or was the analysis incomplete? The justification is lacking.

Response: We focused on IL-8 secretion as widely recognized pro-inflammatory protein which is secreted at high amounts only for the initial screen of all 6 probiotics (Fig. 4B). Once we began to investigate the possible mechanism of epithelial barrier protection using the 3 chosen probiotics, a large panel of cytokines was tested (Fig. 6). The logic of the read-out choice is now better explained (Lines 495 -499).

• Comment 7: The figures are presented in different formats (heatmaps, bar graphs, line graphs) with inconsistent color schemes. This inconsistency makes interpretation difficult. The figures should be standardized in style and formatting.

Response: The figures were modified to improve clarity. The box-plots were standardized as much as possible.

• Comment 8: Although metabolomics data are provided, no functional validation experiments are included. Without additional mechanistic studies such as blocking indole signaling or tight-junction protein modulation, the conclusions remain largely correlative.

Response: We agree that the proposed experiments are of important interest, however, are not practically possible because of the laboratory (and the institute) closure. The conclusions are now rewritten in a more cautious manner.

• Comment 9: Many of the observed probiotic effects were modest, variable, or not statistically significant (e.g., cytokine modulation). The Discussion nonetheless extrapolates these results to propose protective roles in malnourished children, which is premature and unsupported by the evidence

Response: We disagree that the effect was modest as we clearly show, despite the variability caused by the use of PBMC from donors, that probiotics significantly protect the epithelial barrier while some (ATCC, EVC001, Combo) even reaching the baseline of “No LPS” condition (Fig 4A). The effect of probiotics on gene transcription was also striking reaching 20 – 40 folds of change for statistically significant results (Fig. 7). The very modest and often insignificant effect on cytokine secretion was admitted and served as the basis of “cytokine independent mechanism” hypothesis for the tested probiotics. The overstatements regarding the “protective roles in malnourished children” was deleted from the discussion and abstract.

• Comment 10: The final paragraph of the Discussion claims that probiotics “demonstrate the potential to protect the intestinal epithelium” and suggests translational implications. Given the largely descriptive results and lack of mechanistic validation, this conclusion is overstated. A more cautious interpretation is warranted.

Response: The abstract was revised accordingly – “These findings indicate that metabolites produced by B. infantis and/or LGG can protect the intestinal epithelium in vitro, warranting further in vivo studies to evaluate the translational relevance of this effect.” (lines 28 – 30) and the overstatements deleted from the discussion

 

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

I thank the authors for their response. The manuscript is significantly improved.

Reviewer 3 Report

Comments and Suggestions for Authors

I think the authors have adequately responded to the comments presented.