Evaluation of Vortioxetine on Global DNA Methylation in Maternal and Offspring Rats and In Silico Molecular Docking to Key Epigenetic Enzymes
Amber Mills
Round 1
Reviewer 1 Report
Comments and Suggestions for AuthorsGunay et at, sought to investigate the impact of Vortioxetine, a new antidepressant, for therapeutic relevance in pregnant women. The authors make a great case for the justification of this study, but I feel they fall short in execution. There are several concerns in this manuscript with the induction of depressive like behaviors the time of mating relative to the start of the SSRI and the behavior tests to prove these depressive like behaviors. The authors make a strong point that DNA methylation is impacted in both the maternal and fetal placenta and cord blood however they only looked at the brain in the offspring and hippocampus in the mothers.
The authors need justification for using 10 week old rats as this seems young for the beginning of their experiment additionally there should be justification for the time of the forced swim test (five days) and justification for why they didn’t use open field before and after the swim test so that they could measure locomotor activity prior and after the supposed depressive like behaviors began.
The authors need to correct the methods as after the swim test the rats should be 11 week old. Additionally they did not say how they confirmed depressive behaviors in the rats and it is not clear whether or not they started the SSRI before or after mating.
In methods 2.4 “substances” were administered via Gavage to all groups starting on the first day of pregnancy it needs to be clear if this is Ssri’s or exactly what was administered to these rats.
Looking at the results, immobility should be defined and there should be a distinction between rats that learn to float instead of swim which may not necessarily be a sign of depression but rather a learned behavior. Additionally the graphs for the studies are har to read and require a larger font size and higher pixel density. Further, individual data points should be shown for all bar graphs. Lastly it needs to be written clearly whether or not standard deviation or standard error of the mean was used, the as statistical manipulations, the samples size, and for the offspring whether male or female offspring were used or # for each in the figure legends.
For the open field test it is confusing why a total inactive time and time spent in corners is on the same graph with no comparison yet they are showing significance. Are these normalized to something there needs to be further explanation as to why these are put together the same can be true for number of square changes and number of rising of the lower extremities and the panel B is completely Illegible when printed out and needs to be enlarged and increase the focus.
Figure three is not legible and it is confusing why some have what are thought to be error bars and others do not. There’s also no significance shown to my understanding and overall it is pretty impossible to read once printed out It is unfortunate that the authors didn’t explore this further as I thought this would be a main focus of the paper and I can’t really determine any conclusions from figure three.
I will defer to other reviewers as to the molecular structure figures 4 through 6 I believe these are concept only and don’t add to the paper I would have liked to have seen DNA methylation levels via RT-PCR and some change between all the groups rather than showing what binding is possible with these SSRIs. Additionally, how are these methylations occurring. There is a school of thought these are due to extracellular vesicles but this is not explored here.
The authors did a great job of introducing the topic however I feel that their overall data presented lack their ability to make specific conclusions and thus weakens their discussion and conclusions overall I would recommend that the authors resubmit when additional data has been collected to support their hypothesis.
Author Response
Dear Reviewer,
First, thank you for reviewing our article. We have carefully reviewed all your suggestions and found them very helpful in improving the study's quality. We have carefully considered all your suggestions and made the necessary revisions. Below, we have listed your suggestions and the changes we made. Thank you again for your suggestions. Changes to the text are highlighted in yellow.
Comments 1: “The authors need justification for using 10 week old rats as this seems young for the beginning of their experiment additionally there should be justification for the time of the forced swim test (five days) and justification for why they didn’t use open field before and after the swim test so that they could measure locomotor activity prior and after the supposed depressive like behaviors began.”
Response 1: We thank the reviewer for this constructive comment. First, we have added a methodological justification for selecting 10-week-old female Sprague–Dawley rats, noting that this age corresponds to young adulthood (post-adolescent, sexually mature) in rats, thereby reducing confounding from ongoing adolescent neurodevelopment while avoiding age-related reproductive/epigenetic changes.
10-week-old corresponds to a post-adolescent/young adult stage, thereby reducing potential confounding from adolescent neurodevelopment while ensuring reliable reproductive maturity for mating/pregnancy. Adolescence in rats is commonly defined as extending to approximately postnatal day ~60; thus, 10 weeks (≈P70) represents post-adolescence (Agarati et al., 2022). This rationale has been added in the Animals subsection (Methods 2.1) with an appropriate reference.
Second, the reviewer refers to a five-day forced swim procedure; however, our induction/screening phase comprised a 15-minute pre-exposure (Day 0) followed by 5-minute sessions once daily for seven consecutive days (Days 1–7). We have clarified the timeline wording in the Methods to prevent misunderstanding and ensured consistency with the Results section.
Third, regarding locomotor assessment, we conducted the open field test after the repeated forced-swim induction as a post-induction locomotor/exploratory control to aid interpretation of forced-swim behavior. At the same time, all animals were drug-naïve during the induction/screening phase. We did not include a baseline (pre-induction) open-field session to minimize potential test-battery order/carry-over effects across behavioral assays and to avoid additional novelty/stress exposure immediately before mating. This rationale is now explicitly stated in the OFT Methods paragraph (Methods, Section 2.2.2) and supported by the added references (Cnops et al., 2022; Blokland et al., 2012). We also acknowledge as a limitation that locomotor activity was not assessed both pre- and post-induction, and note that future work could incorporate repeated locomotor assessments with appropriate inter-test intervals.
Agrati, D. Adolescence and Postpartum: Two Life Periods to Deepen Our Understanding of the Complexity of Female Rat Sexual Behavior. Sexes 2022, 3, 282-297. https://doi.org/10.3390/sexes3020022
Cnops, V., et. al (2022). Test, rinse, repeat: A review of carryover effects in rodent behavioral assays. Neuroscience and biobehavioral reviews, 135, 104560. https://doi.org/10.1016/j.neubiorev.2022.104560
Blokland, A., et. Al. (2012). The use of a test battery assessing affective behavior in rats: order effects. Behavioural brain research, 228(1), 16–21. https://doi.org/10.1016/j.bbr.2011.11.042
Comments-2: “The authors need to correct the methods as after the swim test the rats should be 11 week old. Additionally they did not say how they confirmed depressive behaviors in the rats and it is not clear whether or not they started the SSRI before or after mating. Save as draft (submit later)In methods 2.4 “substances” were administered via Gavage to all groups starting on the first day of pregnancy it needs to be clear if this is Ssri’s or exactly what was administered to these rats.”
Response-2: We thank the Reviewer for these helpful comments and have revised the Methods section for clarity and chronological consistency.
(i) Age of animals: We now specify that females were 10 weeks old at study onset, and we corrected the wording in the group-allocation sentence (Methods 2.3) to reflect that animals were 11 weeks old at the time of allocation, addressing the apparent inconsistency noted by the Reviewer.
(ii) Confirmation of depressive-like behavior: We clarified how the stress-related depressive-like coping phenotype was established, explicitly stating that confirmation relied on the expected increase in immobility (passive coping) across repeated FST sessions, consistent with standard interpretations of the FST, and that the OFT was used as a subsequent locomotor/exploratory readout to mitigate gross motor confounding.
(iii) Timing of SSRI/compound administration and definition of “substances”: We clarified that no treatment was administered before mating and that dosing started after pregnancy confirmation. We also replaced the ambiguous term “substances” with explicit group-specific compounds (vortioxetine/escitalopram/saline) and defined gestational day 0 (GD0) as the day spermatozoa were detected in vaginal smears, indicating that dosing began on GD0 (first day of pregnancy).
Comments-3: Looking at the results, immobility should be defined and there should be a distinction between rats that learn to float instead of swim which may not necessarily be a sign of depression but rather a learned behavior. Additionally the graphs for the studies are har to read and require a larger font size and higher pixel density. Further, individual data points should be shown for all bar graphs. Lastly it needs to be written clearly whether or not standard deviation or standard error of the mean was used, the as statistical manipulations, the samples size, and for the offspring whether male or female offspring were used or # for each in the figure legends.
Response-3: We thank the reviewer for these critical suggestions. (i) We have now explicitly defined immobility operationally in the Forced Swim Test as the absence of active escape-directed behaviors with only minimal movements required to keep the head above water. We clarified that FST immobility is interpreted as a stress-coping/energy-conservation phenotype rather than a direct proxy for depression severity, consistent with ongoing conceptual debates in the field.
(ii) To address the concern about learned floating, we added a discussion statement acknowledging that repeated exposure can yield an acquired passive coping strategy, and we framed our conclusions accordingly.
(iii) We improved figure readability by increasing font sizes and exporting high-resolution images in line with MDPI recommendations (≥600 dpi).
(iv) We revised all bar graphs to display individual data points (scatter/“show the dots”). We updated each figure legend to clearly report the mean ± SD, exact n, statistical tests, and, where applicable, the offspring sex distribution and experimental unit.
(v) Section 2.8, the statistics section, has also been updated.
Comments-4: For the open field test it is confusing why a total inactive time and time spent in corners is on the same graph with no comparison yet they are showing significance. Are these normalized to something there needs to be further explanation as to why these are put together the same can be true for number of square changes and number of rising of the lower extremities and the panel B is completely Illegible when printed out and needs to be enlarged and increase the focus.
Response-4:
We agree with the reviewer that the previous open-field figure layout was confusing. The open-field endpoints (immobility time, time spent in corners, square crossings, and rearings) are distinct readouts and were not intended to be statistically compared against each other. The significance markers and the ‘paired t-test’ statement were therefore inappropriate and have been removed. We have redesigned Figure 5 by separating each endpoint into its own panel (A–D), increased font sizes and panel dimensions to ensure print legibility, and clarified in the Methods/Results and legend that the OFT was used as a locomotor/exploratory readout after the swim protocol rather than as a standalone confirmation of depression.
Comments-5: Figure three is not legible and it is confusing why some have what are thought to be error bars and others do not. There’s also no significance shown to my understanding and overall it is pretty impossible to read once printed out It is unfortunate that the authors didn’t explore this further as I thought this would be a main focus of the paper and I can’t really determine any conclusions from figure three.
Response-5: We thank the reviewer for highlighting these issues. We have entirely redesigned Figure 3 to ensure print legibility and to improve clarity and consistency of data presentation. Specifically, we (i) increased the panel size and font sizes and exported the figure at publication-quality resolution; (ii) standardized the display of variability by presenting mean ± SD with error bars in all panels and clearly indicating n = 50 in the figure/legend; and (iii) removed any potentially misleading visual cues to significance.
Comments-6: I will defer to other reviewers as to the molecular structure figures 4 through 6 I believe these are concept only and don’t add to the paper I would have liked to have seen DNA methylation levels via RT-PCR and some change between all the groups rather than showing what binding is possible with these SSRIs. Additionally, how are these methylations occurring. There is a school of thought these are due to extracellular vesicles but this is not explored here.
Response-6: We appreciate this critical critique. We agree that the docking analyses are hypothesis-generating and should not be interpreted as demonstrating enzymatic inhibition or causality in vivo. Accordingly, we have tempered the language throughout the docking Results/Discussion to explicitly state that in silico binding provides a mechanistic context but does not establish functional inhibition. Regarding “RT-PCR methylation,” we believe this comment refers to bisulfite-based methylation qPCR approaches (e.g., MSP/MethyLight) rather than conventional RT-qPCR, which is typically used for gene expression. We now clarify as a limitation that our ELISA-based assay quantifies global 5-mC and cannot resolve locus-specific methylation; we also highlight bisulfite-based assays as an appropriate direction for future validation. Finally, we have expanded the Discussion to outline plausible biological routes by which gestational antidepressant exposure could influence the fetal epigenome, including maternal–placental signalling and the emerging concept that extracellular vesicles may mediate epigenomic reprogramming. We acknowledge that EVs were not measured in the present study and should be addressed in future work.
Comment-7: The authors did a great job of introducing the topic however I feel that their overall data presented lack their ability to make specific conclusions and thus weakens their discussion and conclusions overall I would recommend that the authors resubmit when additional data has been collected to support their hypothesis.
Response-7: We appreciate the reviewer’s candid assessment and agree that additional mechanistic and locus-specific epigenetic data would further strengthen the ability to draw concrete causal conclusions. In response, we have reframed the Discussion and Conclusions to ensure that our claims remain fully supported by the presented data. Specifically, we now position the study as a proof-of-concept and hypothesis-generating study, reporting associations between gestational antidepressant exposure and global 5-mC changes (with related transcriptional readouts) rather than implying definitive mechanistic causality. We have also expanded the Limitations and Future Directions to explicitly outline the additional datasets required for mechanistic confirmation (e.g., bisulfite-based locus-specific methylation assays, protein-level validation of DNMT/TET pathways, and investigation of maternal–placental/extracellular vesicle signalling). We believe these revisions appropriately align the manuscript’s scope with the currently available evidence and provide a clear roadmap for subsequent confirmatory work.
Thank you for your consideration.
Reviewer 2 Report
Comments and Suggestions for AuthorsThe paper by Günay et al. „Effect of The Multimodal Antidepressant Vortioxetine on Epi-2 genetic Modification and Gene Expression Levels in Maternal and Offspring Rats”, is an original work that aims to investigates the epigenetic and molecular effects of vortioxetine during pregnancy using a rat model of depression, combining behavioral paradigms, global DNA methylation assays, and molecular docking of vortioxetine with several epigenetic enzymes (TET2, DNMT3A, DNMT3B). Considering the increasing prescription of multimodal antidepressants, investigating how prenatal exposure affects global DNA methylation and potential mechanistic pathways is scientifically relevant.
The authors combine behavioural validation, in vivo ELISA-based global quantification of 5-mC, and in silico docking. The study is novel; however, important methodological and interpretational issues must be addressed before publication. Several parts of the manuscript require clarification, greater methodological transparency, improved data presentation, and a more cautious interpretation of the results.
- The manuscript claims to examine “epigenetic modification and gene expression levels,” yet no gene expression analyses were performed, despite being stated in the title and introduction (see lines 2–4 on page 1: “…on epigenetic modification and gene expression levels…”
Recommendation:
Align the title with the actual experimental design (no RT-qPCR, no transcriptomic profiling). Alternatively, include the minimally required gene-expression assays (e.g., BDNF, DNMT3A/3B, TET2).
- The Forced Swim Test (FST) is used as a depression-inducing test. However, FST is not validated as a depression-induction model.
Recommendation:
Acknowledge that the FST does not induce depression but rather produces acute stress and despair-like behaviour. Consider incorporating chronic stress paradigms (CMS, CUMS) into future studies.
- Figures summarising FST/OFT data (pages 7–8, Figures 1 and 2) present only overall averages for the entire cohort, not group-wise differences. Depression validation must include group-level data before randomisation.
Recommendation:
Provide group-level behavioural data for all five study groups, collected after induction and before intervention. Include ANOVA p-values to confirm depression-like phenotype.
- Lack of numerical values and test statistics
The results state “significant decrease” (p.9, lines 301–304), but no p-values, fold-changes, or confidence intervals are provided.
- Potential misinterpretation of hypomethylation
Global decreases in 5-mC may reflect changes in cell composition, variability in DNA extraction, or non-specific environmental stress.
Recommendation:
Add complete statistical reporting (mean ± SD, p-values, CI).
Add assay sensitivity validation (inter-assay CV, replicate concordance).
Temper conclusions; global hypomethylation cannot be equated with functional epigenetic dysregulation.
- Docking results (pp. 9–13, Figures 4–6) show predicted binding affinities of vortioxetine/escitalopram to TET2, DNMT3A, DNMT3B. However, the manuscript repeatedly implies functional inhibition based solely on docking affinity (e.g., p. 14, lines 417–423; p. 15, lines 431–439). Docking cannot establish inhibition.
Recommendation:
Reframe conclusions to emphasise hypothesis generation rather than mechanistic confirmation. Add MD simulations or remove mechanistic claims. Avoid language implying causal linkage (“inhibition,” “modulation”) without biochemical validation.
- Several figures are lacking:
Scale bars, statistical significance marking, clear y-axis labels (“% methylation? absolute OD?”), legends describing sample sizes
Recommendation: Revise all figures for professional publication standards.
Minor
- The title should be revised (no gene expression analysis performed).
- Abstract overstates mechanistic certainty; results should be described more cautiously.
- Methods must specify:
– exact sample per litter (offspring pooling or individual testing?),
– sex of offspring analysed (epigenetic outcomes often sex-specific),
– whether samples were randomised/blinded. - Docking methods: include justification of grid size and rationale for exhaustiveness.
- English grammar throughout needs moderate editing.
- What is Scheme 2005?
Author Response
Dear Reviewer,
Thank you for taking the time to review our article. We have thoroughly examined each of your recommendations and appreciate their enhancement of the quality of our study. After considering all your input, we have made the necessary revisions. Below, we have outlined your suggestions alongside the modifications we implemented. We appreciate your feedback once more. Changes to the text are highlighted in yellow.
Comment-1 The manuscript claims to examine “epigenetic modification and gene expression levels,” yet no gene expression analyses were performed, despite being stated in the title and introduction (see lines 2–4 on page 1: “…on epigenetic modification and gene expression levels…”
Recommendation: Align the title with the actual experimental design (no RT-qPCR, no transcriptomic profiling). Alternatively, include the minimally required gene-expression assays (e.g., BDNF, DNMT3A/3B, TET2).
Response-1: Based on your title suggestions, it has been revised as follows:“Evaluation of Vortioxetine on Global DNA Methylation in Maternal and Offspring Rats and in Silico Molecular Docking to Key Epigenetic Enzymes”
Comment-2: The Forced Swim Test (FST) is used as a depression-inducing test. However, FST is not validated as a depression-induction model.
Response-2 We thank the reviewer for this important clarification and agree with the concern. We have revised the manuscript to avoid describing the Forced Swim Test (FST) as a “depression-inducing” paradigm. The FST is now described as a behavioral assay that quantifies immobility/passive coping (i.e., cessation of active escape-directed behaviors), which is commonly used as a screening readout for stress-coping/antidepressant-like effects rather than as a validated depression-induction model. Accordingly, all wording implying that FST induces depression has been removed or rephrased throughout the manuscript, and the corresponding Results/Methods descriptions were updated to reflect this conceptual framing.
Replaced “depression-inducing” terminology with “behavioral assay of immobility/passive coping” in the relevant Methods/Results text. Ensured consistent terminology in the Abstract and Discussion to prevent overinterpretation of FST as a depression induction model. Introduction and Discussion wording to avoid framing the repeated FST as a ‘perinatal depression model’ and consistently describe it as a pre-mating stress-coping behavioral screening.”
Comment-3: Figures summarising FST/OFT data (pages 7–8, Figures 1 and 2) present only overall averages for the entire cohort, not group-wise differences. Depression validation must include group-level data before randomisation
Response-3: We thank the reviewer for this valuable recommendation regarding the validation of the behavioral phenotype. In the revised manuscript, we have reorganized the data presentation to ensure transparency and confirm baseline equivalence. For the Forced Swim Test (FST): As requested, the baseline immobility data (pre-randomization) are now presented stratified according to the groups to which the animals were subsequently assigned (Groups 1–5). This group-level breakdown confirms that all study groups exhibited comparable passive stress-coping phenotypes prior to the initiation of pharmacological treatment (Figure). For the Open Field Test (OFT), we clarified that this test was used primarily to rule out locomotor deficits across the entire cohort. The relevant text in Section 3.1 (Results) has been updated to reflect these stratified baseline characteristics.
Comment-4: Lack of numerical values and test statistics. The results state "significant decrease", but no p-values, fold-changes, or confidence intervals are provided.
Response-4: We appreciate the reviewer’s attention to the precision of data reporting. In the revised manuscript, we have updated the relevant figures and text to improve quantitative transparency: Numerical Data: We have explicitly added the numerical values (Mean ± Standard Deviation) directly to the bars in Figure 3 (e.g., Offspring Control: 40 ± 12 vs. Vortioxetine 2.0 mg: 16 ± 8) to clearly present the magnitude of the differences.
Statistical Significance: The statistical significance is now clearly indicated in the figure legends and charts with asterisks (*p < 0.05) to confirm the "significant decrease" mentioned in the text.
We believe that presenting the data as Mean ± SD, alongside the significance thresholds, provides a clear and standard representation of the biological variation and treatment effects observed in the study.
Comment-5: Potential misinterpretation of hypomethylation Global decreases in 5-mC may reflect changes in cell composition, variability in DNA extraction, or non-specific environmental stress. Recommendation: Add complete statistical reporting (mean ± SD, p-values, CI). Add assay sensitivity validation (inter-assay CV, replicate concordance). Temper conclusions; global hypomethylation cannot be equated with functional epigenetic dysregulation.
Response-5:
We agree with the reviewer that global methylation changes should be interpreted with caution. We have revised the manuscript to reflect a more conservative interpretation and improved data presentation:
Statistical Reporting: We have updated the Figure to explicitly display Mean ± SD values for all groups, ensuring full transparency of the variation within the data.
Assay Validity: We emphasized in the Methods section that all ELISA measurements were performed in triplicate to ensure technical replicate concordance and minimize measurement error. Tempering Conclusions: Most importantly, we have extensively revised the Discussion and Conclusion sections. We no longer equate global hypomethylation with definitive functional dysregulation. Instead, we explicitly frame our findings as "hypothesis-generating" and a "proof of concept" (Section 4 and Conclusions). We have also added a Limitation stating that without gene-specific profiling, downstream functional consequences cannot be causally confirmed.
Comment-6: Docking results (pp. 9–13, Figures 4–6) show predicted binding affinities of vortioxetine/escitalopram to TET2, DNMT3A, DNMT3B. However, the manuscript repeatedly implies functional inhibition based solely on docking affinity (e.g., p. 14, lines 417–423; p. 15, lines 431–439). Docking cannot establish inhibition. Recommendation: Reframe conclusions to emphasise hypothesis generation rather than mechanistic confirmation. Add MD simulations or remove mechanistic claims. Avoid language implying causal linkage (“inhibition,” “modulation”) without biochemical validation.
Response-6: We appreciate your comment. We carefully read the all related part and rewrite the sentences.
Comment-7:Several figures are lacking:
Scale bars, statistical significance marking, clear y-axis labels (“% methylation? absolute OD?”), legends describing sample sizes
Recommendation: Revise all figures for professional publication standards.
Response-7: Many of the figures have been redesigned and new figures added, and their quality has been improved.
Minor Revisions
Minor 1. The title should be revised (no gene expression analysis performed).
Response: The title has been revised.
- Abstract overstates mechanistic certainty; results should be described more cautiously.
Response: The summary has been revised.
- Methods must specify: – exact sample per litter (offspring pooling or individual testing?), – sex of offspring analysed (epigenetic outcomes often sex-specific), – whether samples were randomised/blinded.
Response: The method has been revised.
- Docking methods: include justification of grid size and rationale for exhaustiveness.
Response: Thank you for your helpful suggestion regarding the docking methodology. We have revised the Methods section to explicitly justify both the grid-box dimensions and the exhaustiveness setting used in our docking simulations. Specifically, we added a short rationale indicating that the 30 × 30 × 30 Å grid was selected to fully encompass the catalytic pocket and adjacent subpockets of TET2, DNMT3A, and DNMT3B, while providing sufficient margin for ligand translation/rotation and minimizing boundary artefacts that could bias pose generation. We also clarified that an exhaustiveness value of 24 was chosen as a pragmatic balance between computational feasibility and thorough conformational sampling, and that this setting was applied consistently across all targets to maintain methodological comparability between docking runs. These changes have now been incorporated into the revised manuscript.
- English grammar throughout needs moderate editing.
Response: English editing was done.
- What is Scheme 2005?
Response: It was left there by mistake; it has been deleted.
Thank you for your consideration.
Round 2
Reviewer 2 Report
Comments and Suggestions for AuthorsThe authors addressed all comments. The manuscript has been significantly improved and meets the criteria for publication.
