Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The main problem is statistical analysis. Maternal treatment was applied to dams, while 72 offspring originated from only 15 litters, but many analyses are reported with denominator F(1,68), suggesting that individual offspring were treated as independent observations. Litter cannot be included simply as ordinary covariate; the data have hierarchical structure and should be reanalysed with litter clustering/random effect, repeated measurements within animal, and also pair dependence for social interaction tests. In addition, very large number of behavioral endpoints, interactions and post-hoc comparisons were analysed without clear correction for multiplicity, while p=0.05–0.10 are repeatedly discussed as “trends”. Therefore, robustness of several behavioral findings is questionable.

The explanation of disagreement with previous studies, including authors’ own Wistar data, is not sufficient. The manuscript attributes these differences mainly to genetic background, but there is no simultaneous Wistar comparator and no direct demonstration that strain is the causal factor. The LPS verification in separate animals also cannot prove equivalent maternal immune activation in the experimental pregnant dams. Thus, “genetic background matters” should be presented as plausible explanation, not demonstrated mechanism.

Interpretation of the elevated plus maze is too free. The authors directly state that “the total number of open arm entrances was very low in all the groups and a high number of animals did not enter the open arms at all.” This clearly indicates a strong floor effect for the main EPM endpoint. Under such conditions, defecation, looking-down and self-grooming cannot simply substitute open-arm measures and then be summarized as an “anxious phenotype”. A recent methodological analysis specifically discussing domain-based interpretation and instability of EPM endpoints is directly relevant here and should be cited and discussed (Pharmacol Biochem Behav. 2026;267:174241; PMID 42431467).

There is also an important internal inconsistency in the ethics information: Methods indicate animal approval 81/2022, whereas the final ethics statement gives 21/2023. This must be clarified. In addition, the Discussion states that PV-positive interneurons were unchanged in hippocampus, PFC and cerebellum, although the described immunohistochemical quantification was performed in PFC. This statement need correction.

• Litter clustering and pseudoreplication problem
• Multiplicity and selective statistical reporting
• Discrepancy with previous Wistar results
• Genetic-background conclusion is overclaimed
• LPS verification does not resolve
• EPM floor effect and interpretation
• Ethics and regional-data inconsistencies

Author Response

Comment 1: The main problem is statistical analysis. Maternal treatment was applied to dams, while 72 offspring originated from only 15 litters, but many analyses are reported with denominator F(1,68), suggesting that individual offspring were treated as independent observations. Litter cannot be included simply as ordinary covariate; the data have hierarchical structure and should be reanalysed with litter clustering/random effect, repeated measurements within animal, and also pair dependence for social interaction tests. In addition, very large number of behavioral endpoints, interactions and post-hoc comparisons were analysed without clear correction for multiplicity, while p=0.05–0.10 are repeatedly discussed as “trends”. Therefore, robustness of several behavioral findings is questionable.

Response 1: Thank you for this suggestion. We have recalculated the statistics using a model with hierarchical structure and reworked the Results, Discussion and Figures accordingly. Some findings are no longer recovered as significant.

Comment 2: The explanation of disagreement with previous studies, including authors’ own Wistar data, is not sufficient. The manuscript attributes these differences mainly to genetic background, but there is no simultaneous Wistar comparator and no direct demonstration that strain is the causal factor.

(…)Thus, “genetic background matters” should be presented as plausible explanation, not demonstrated mechanism.

Response 2: Direct comparison of strains was not the goal of the study. We intended to validate the model in a different setting and extend the earlier results. The failure to replicate the core phenotypes was rather unexpected, yet we consider it of sufficient practical importance to be published. While the genetic background seems to be the most probable cause of the discrepancy with earlier findings, we must take this conclusion as tentative, without establishing a causal or mechanistic link. We changed the wording in the title and the manuscript to emphasize this.

Comment 3: The LPS verification in separate animals also cannot prove equivalent maternal immune activation in the experimental pregnant dams.

Response 3: We agree that the verification experiment performed in separate animals cannot directly demonstrate the magnitude of maternal immune activation in the individual pregnant dams used in the main experiment. The purpose of the verification experiment was to confirm that the LPS preparation and administration protocol used in the study were capable of inducing systemic inflammatory activation. The same LPS batch, dose and experimental procedures were used in the verification and main experiments. The observed increase in serum nitrite/nitrate concentrations confirmed that the applied LPS protocol was a potent systemic inflammatory stimulus in both mice and rats.

We did not collect additional blood samples from the experimental pregnant dams because this would have required additional blood sampling and/or repeated interventions during pregnancy, potentially imposing unnecessary stress or harm on the animals. Sacrificing a dedicated group of pregnant females to obtain terminal blood samples was not practically possible, as the study was already constrained by problematic breeding of the PV-Cre dams, limiting the number of runs and litters. Even if it wasn’t the case, it would violate the RRR principle and go beyond the scope of our approved ethics statement.

Nevertheless, given that the same LPS preparation was used in the verification and experimental groups, the verification experiment provides evidence that the treatment regimen was biologically active.

Comment 4: Interpretation of the elevated plus maze is too free. The authors directly state that “the total number of open arm entrances was very low in all the groups and a high number of animals did not enter the open arms at all.” This clearly indicates a strong floor effect for the main EPM endpoint. Under such conditions, defecation, looking-down and self-grooming cannot simply substitute open-arm measures and then be summarized as an “anxious phenotype”. A recent methodological analysis specifically discussing domain-based interpretation and instability of EPM endpoints is directly relevant here and should be cited and discussed (Pharmacol Biochem Behav. 2026;267:174241; PMID 42431467).

Response 4: We have emphasized the problem with the floor effect in open arm entrances and added discussion related to the interpretations of grooming and looking down. We have removed any claims of anxious phenotype, also because some of the anxiety-related changes failed to reach significance with the adjusted statistical model.

Comment 5: There is also an important internal inconsistency in the ethics information: Methods indicate animal approval 81/2022, whereas the final ethics statement gives 21/2023. This must be clarified.

Response 5: In fact, the experiments were approved on two levels: first by the Institutional Animal Care and Use Committee at NIMH (project no. 81) and then by the Departmental Expert Committee for the Approval of Projects of Experiments on Animals of the Ministry of Health of the Czech Republic (document number 21/2023). We corrected the statement for better clarity (lines 549-553 and 857-861).

Comment 6: In addition, the Discussion states that PV-positive interneurons were unchanged in hippocampus, PFC and cerebellum, although the described immunohistochemical quantification was performed in PFC.

Response 6: Thank you for pointing out this mistake. We corrected the statement (line 439).

Comment 7: Quality of Figures

Reviewer 1 Figures and tables must be improved

Response 7: Figures have been changed to reflect the updated statistical model.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors demonstrated that prenatal treatment by LPS caused behavioral changes in adolescence and adulthood of the offspring in PV-Cre Long-Evans rats. Specifically, LPS altered anxiety and risk assessment behavior, and locomotor activity. However, the direction of changes was dependent on sex and age. The behavioral impacts of MIA are strongly strain-dependent. Overall, the results are well presented and potential mechanisms are proposed. This article can be published after a few minor revisions.

Below are my comments:

Methods:

Why only chose nitrite/nitrate for immune reaction?

Discussion:

There were several timepoints, P21, P27, P45, P90, of animal used in this study. The author could briefly discuss the rat age equivalents corresponding to human ages.

Minor concerns:

Abbreviations: P stands for p value?

Typos: Line 849: +-, etc; SI (p 654); are (P 810);

Author Response

Comment 1:

Methods:

Why only chose nitrite/nitrate for immune reaction?

Response 1: We selected serum nitrite/nitrate concentrations as a marker of systemic inflammatory activation because lipopolysaccharide (LPS) is a potent inducer of nitric oxide (NO) production. NO is subsequently oxidized to nitrite and nitrate, which can therefore be quantified as indirect indicators of systemic NO production and inflammatory activation. Importantly, nitrite/nitrate can be readily measured in serum from both mice and rats using the same analytical approach, allowing a direct comparison between the two experimental species. Explanation was added to the Methods sections (lines 558-561).

We acknowledge that other inflammatory mediators, such as TNF or IL-6, could also have been assessed and would provide complementary information about the inflammatory response. However, the primary purpose of this experiment was to verify systemic inflammatory activation following LPS administration rather than to provide a comprehensive characterization of the cytokine response. The nitrite/nitrate assay was therefore considered an appropriate and practical readout for this purpose, particularly given its applicability to both species and the relatively low analytical cost compared with multiplex cytokine measurements.

Comment 2:

Discussion:

There were several timepoints, P21, P27, P45, P90, of animal used in this study. The author could briefly discuss the rat age equivalents corresponding to human ages.

Response 2: Comparing rat and human age is complicated, because the development rates differ across different organ systems and even specific brain structures, and their temporal dynamic is also different. This is partly determined by the life history and ecological needs of the species. Therefore, one can establish a corresponding stage of development in a rat and a human for a particular brain structure, but not the brain, or the entire organism, as a whole. For example, neonatal rat is underdeveloped relative to a human newborn as far as certain brain structures and the visual system are concerned, but its capacities of independent locomotion and the underlying neural systems are greatly superior. There is an entire field of literature dedicated to the topic, and the suggested rat-human age equivalency differs considerably among the authors. Therefore, we have limited ourselves to broad developmental stages anchored mainly in the social/ecological development of the individual. Namely, ages P21 and P27 are described as “juvenile”, P45 comes under “adolescence” and P90-aged rat is “adult”. See for example Fig. 1 in Juraska and Drzewiecki, 2020, (https://doi.org/10.1016/j.dcn.2020.100857); McCutcheon and Marinelli, 2009 (https://doi.org/10.1111/j.1460-9568.2009.06648.x); Sengupta, 2013 (PMCID: PMC3733029) etc.

Comment 3:

 Minor concerns:

Abbreviations: P stands for p value?

Typos: Line 849: +-, etc; SI (p 654); are (P 810);

Response 3: 

“P” is the abbreviation for “postnatal day” as it is stated in Abbreviation section (page 29, line 873) and at lines 89 and 109. For p value, we use the usually established abbreviation “p”.

We corrected the typo “+-“ to “±”. “SI” abbreviation is explained earlier in the text (line 268 and 292), and in the Abbreviation section; therefore, we decided not to explain it again in the method section just as the other behavioral tests. The sentence at line 810 was removed during the major revision of the statistical part of the manuscript.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The revision substantially addresses the previous concerns. Before acceptance, please clarify how dependence within social pairs and multiplicity were handled in Supplement 1, and avoid interpreting non-significant “trends” as evidence of treatment effects. The concluding statement that the results “demonstrate” strain dependence remains unsupported without a direct strain comparison and should be qualified. Please also reconcile the intraperitoneal administration used for LPS verification with the subcutaneous administration in the main experiment; the verification supports biological activity of the preparation, but does not establish equivalent immune activation in the experimental pregnant dams.

Author Response

Comment 1: please clarify how dependence within social pairs and multiplicity were handled in Supplement 1

Response 1: Pair dependency of animals tested in pairs in social interactions test and social play test was accounted for by including a random intercept for pair in the mixed model, in addition to random intercepts for litter, experimental run and individual animal. Multiplicity was addressed at two levels. First, post-hoc pairwise comparisons were performed only for effects that were significant in the omnibus test (ART ANOVA or linear mixed model, p < 0.05). Second, all post-hoc p-values were adjusted using the Benjamini–Hochberg false discovery rate procedure. We clarified both statements in Supplement 1 (pages 3-4).

 

Comment 2: avoid interpreting non-significant “trends” as evidence of treatment effects

Response 2: We mentioned trends in the Results section but we take care never to pretend the trend was significant and often emphasize that the trend was insignificant to avoid confusion. In the Discussion section, we removed a statement, which remained there from the version with the original statistics and was now referring to a trend (lines 458-460). Nowhere else in the discussion, we are discussing or mentioning any trends.

 

Comment 3: The concluding statement that the results “demonstrate” strain dependence remains unsupported without a direct strain comparison and should be qualified.

Response 3: We changed wording to “suggest” (line 847).

 

Comment 4: Please also reconcile the intraperitoneal administration used for LPS verification with the subcutaneous administration in the main experiment; the verification supports biological activity of the preparation, but does not establish equivalent immune activation in the experimental pregnant dams.

Response 4: We agree with your statement, which is fully true. However, in our study, the verification was actually intended to prove the biological activity of the preparation and nothing more; we do not claim anything else. Showing the actual character of immune reaction during our experimental protocol would require a different kind of experiment (resembling the study by Murray et al., 2019, ref. 20) and it is beyond the scope of our study.