Distinct Molecular Responses to Ketamine and Imipramine in Cortical and Striatal Regions Following Acute Swim Stress

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The authors aimed to test, in an acute stress model, whether two antidepressants with markedly different clinical profiles (ketamine as a rapid-acting agent vs. imipramine as a “classical” antidepressant) elicit comparable behavioral effects, yet engage distinct transcriptional mechanisms within key brain regions. They used C57BL/6N mice assigned to three treatment conditions (vehicle, ketamine 10 mg/kg, imipramine 20 mg/kg). Following injection, at 30 min, half of the animals were exposed to a 6-min swim stress; 30 min after stress, mice were euthanized for gene-expression analyses in three brain regions.

Suggestions

1. Clarify the number of biological samples. Although total group sizes are provided (vehicle n = 13; ketamine n = 14; imipramine n = 14) and it is stated that “half” of the animals underwent swim stress, the manuscript later reports “at least 6” independent determinations for behavioral outcomes and “at least 4” for qPCR. The exact n per experimental cell (treatment × stress) should be explicitly reported, along with a clear explanation for any attrition and for discrepancies in n between behavioral and qPCR datasets.
2. Specify the experimental timeline unambiguously. The precise timing of stress exposure and euthanasia relative to injection must be stated clearly. In particular, it should be clarified whether euthanasia in the “no-stress” condition was time-matched to the stressed groups. This is critical for interpreting IEG/BDNF dynamics. A concise methodological timeline schematic would substantially improve clarity.
3. Address potential confounding due to swim stress at 21°C. Water at 21°C may introduce thermal stress and/or hypothermia, potentially confounding the intended psychological stress component. Post-test recovery procedures (e.g., drying and warming, standardized recovery conditions) should be described to distinguish thermal from psychological contributions to the observed responses.
4. Temper the behavioral conclusion. The manuscript’s framing of behavioral convergence appears overstated. While both treatments increase latency to immobility, only imipramine significantly reduces total immobility time. Accordingly, ketamine–imipramine “convergence” should be presented as partial rather than equivalent across endpoints.
5. Resolve the inconsistency between p-values and Cohen’s d (ketamine). Ketamine is described as not producing a significant effect, yet the reported effect size (with confidence intervals) suggests otherwise. Exact p-values should be reported, and the method used to compute confidence intervals for Cohen’s d should be explicitly described.
6. qPCR normalization and statistical analysis require fuller reporting. Reliance on a single housekeeping gene (Gapdh) may be problematic under acute stress conditions. Moreover, ANOVA on fold-change values may violate distributional assumptions; analyses based on ΔCt (or log2 fold-change) are typically more appropriate. At minimum, the manuscript should state what assumption checks were performed (normality, homoscedasticity) and whether transformations were considered.
7. The “Z-activation score” is not reproducible as described. The manuscript indicates that an integrative score was computed, but does not provide the exact formula, standardization procedure, or aggregation steps. These should be specified in Methods (or Supplementary Methods) to enable reproduction.
8. “Fronto-striatal circuit” language is overly inferential. The dissection targets broad regions (frontal cortex/striatum) without measuring connectivity or circuit-level function. More conservative wording is recommended (e.g., “cortical and striatal regions/components” rather than “circuit mechanisms”).
9. Multiple testing across genes and regions needs global consideration. While Tukey’s post hoc test controls comparisons within each ANOVA, the overall number of endpoints (genes × regions) raises multiplicity concerns. Either apply an FDR approach across the gene panel and/or explicitly frame the multi-endpoint analyses as exploratory.
10. Figure 1 legend contains inconsistencies. The legend references “percentage” whereas the axis reports immobility in seconds, and the statistical significance coding appears to include an error. The legend should be corrected for consistency and accuracy.

Author Response

Reviewer 1

The authors aimed to test, in an acute stress model, whether two antidepressants with markedly different clinical profiles (ketamine as a rapid-acting agent vs. imipramine as a “classical” antidepressant) elicit comparable behavioral effects, yet engage distinct transcriptional mechanisms within key brain regions. They used C57BL/6N mice assigned to three treatment conditions (vehicle, ketamine 10 mg/kg, imipramine 20 mg/kg). Following injection, at 30 min, half of the animals were exposed to a 6-min swim stress; 30 min after stress, mice were euthanized for gene-expression analyses in three brain regions.

 

Suggestions

 

1. Clarify the number of biological samples. Although total group sizes are provided (vehicle n = 13; ketamine n = 14; imipramine n = 14) and it is stated that “half” of the animals underwent swim stress, the manuscript later reports “at least 6” independent determinations for behavioral outcomes and “at least 4” for qPCR. The exact n per experimental cell (treatment × stress) should be explicitly reported, along with a clear explanation for any attrition and for discrepancies in n between behavioral and qPCR datasets.

We thank the reviewer for this important comment. We agree that the exact number of biological samples per experimental condition should be clearly reported.

In the revised manuscript, we specified the exact number of animals in each treatment group that were subjected to swim stress (saline n=6; ketamine n=7; imipramine n=7) or left undisturbed (saline n=7; ketamine n=7; imipramine n=7) (please refer to lines 106-108). Accordingly, the expressions “at least 6” and “at least 4” have been removed and replaced in the figures with the precise n values for each dataset.

The differences in sample size between behavioral and qPCR analyses are due to technical issues encountered during RNA extraction and/or the exclusion of samples identified as outliers during qPCR quality control procedures. This clarification has been added to the Methods section of the revised manuscript as follows (lines 156-161): “For molecular analyses, not all samples could be included due to technical issues during RNA extraction. Additionally, outliers in the qPCR data were identified and excluded using SPSS (version 30). Therefore, the number of biological replicates differs between behavioral and gene expression datasets. The exact n for each experimental condition is reported at the base of the bars in every figure.”.

2. Specify the experimental timeline unambiguously. The precise timing of stress exposure and euthanasia relative to injection must be stated clearly. In particular, it should be clarified whether euthanasia in the “no-stress” condition was time-matched to the stressed groups. This is critical for interpreting IEG/BDNF dynamics. A concise methodological timeline schematic would substantially improve clarity.

Thank you for pointing this out. More information on the timing has been added in the material and method section (please see lines 103-118). Additionally, we improved the supplemental Figure 1. We hope these clarifications meet your expectations.

 

3. Address potential confounding due to swim stress at 21°C. Water at 21°C may introduce thermal stress and/or hypothermia, potentially confounding the intended psychological stress component. Post-test recovery procedures (e.g., drying and warming, standardized recovery conditions) should be described to distinguish thermal from psychological contributions to the observed responses.

We thank the reviewer for highlighting the potential role of thermal stress. We agree and added a section in the discussion (lines 355-367) as follows:

“Water temperature is a critical factor influencing both physiological and behavioral responses during forced swimming [28]. Recent work emphasizes that the forced swim paradigm should be interpreted as a multifactorial stressor, combining elements of inescapability with physiological challenges such as immersion and heat loss [29].

Experimental studies show that swimming in relatively cold water induces pronounced reductions in core body temperature in rodents, confirming that thermoregulatory processes contribute to the overall stress response. Consistent with systematic welfare assessments, transient hypothermia represents the most consistent physiological effect of the test, while other long-lasting indicators of distress are limited [30].

Importantly, in our study all animals were exposed to identical water temperature, test duration, and standardized recovery procedures, e.g. drying and warming. Therefore, although thermal effects contribute to the overall stress response, they cannot account for the observed between-group differences.” .

In addition, the materials and method section have been similarly implemented (lines 109-111).

 

4. Temper the behavioral conclusion. The manuscript’s framing of behavioral convergence appears overstated. While both treatments increase latency to immobility, only imipramine significantly reduces total immobility time. Accordingly, ketamine–imipramine “convergence” should be presented as partial rather than equivalent across endpoints.

We thank the reviewer for this helpful comment. We have revised the Discussion and Conclusions to temper the interpretation of behavioral convergence between ketamine and imipramine. In particular, we now clarify that while both treatments significantly increased latency to immobility, only imipramine significantly reduced total immobility time, indicating only a partial overlap in their behavioral effects. The relevant sections of the manuscript have been modified accordingly and now read as follows:

Discussion (lines 368-375):

“Here we found that both ketamine and imipramine significantly increased latency to immobility, indicating a shared ability to delay the transition from active to passive coping strategies under acute stress. While imipramine significantly reduced total immobility time, ketamine produced a smaller effect that did not reach statistical significance. These findings suggest only a partial overlap in the behavioral effects of the two treatments. The dissociation between the two behavioral measures is noteworthy: latency to immobility appears to reflect the threshold for disengaging from active coping, whereas total immobility indexes sustained passive coping capacity [26,27].”

Conclusion (lines 476-480):

“In conclusion, our study shows that both ketamine and imipramine increase latency to immobility during swim stress exposure, indicating a shared enhancement of the initial active coping response. However, only imipramine significantly reduces total immobility time, suggesting that the behavioral effects of the two treatments are only partially overlapping.”

 

5. Resolve the inconsistency between p-values and Cohen’s d (ketamine). Ketamine is described as not producing a significant effect, yet the reported effect size (with confidence intervals) suggests otherwise. Exact p-values should be reported, and the method used to compute confidence intervals for Cohen’s d should be explicitly described.

We thank the reviewer for pointing out the apparent inconsistency between p-values and Cohen’s d. We have clarified the methods to specify that statistical significance for pairwise comparisons was determined using Tukey-adjusted p-values (α = 0.05), while Cohen’s d and its 95% confidence intervals are reported as descriptive measures of effect size (please refer to lines 162-217).

 

6. qPCR normalization and statistical analysis require fuller reporting. Reliance on a single housekeeping gene (Gapdh) may be problematic under acute stress conditions. Moreover, ANOVA on fold-change values may violate distributional assumptions; analyses based on ΔCt (or log2 fold-change) are typically more appropriate. At minimum, the manuscript should state what assumption checks were performed (normality, homoscedasticity) and whether transformations were considered.

We thank the reviewer for raising this important point. Gene expression levels were normalized to Gapdh, which showed stable expression across experimental conditions in our dataset. In addition to Gapdh, we initially evaluated other candidate reference genes. However, Gapdh showed the most stable expression across our experimental conditions and was therefore used for normalization.

In addition, in the revised Methods section (lines 213-217), we have clarified the procedures used to evaluate model assumptions. Normality of residuals was assessed using visual inspection of Q–Q plots and the Shapiro–Wilk test, and homoscedasticity was evaluated by inspection of residuals versus fitted values plots. No substantial deviations from model assumptions were observed. Data transformations were considered but were not required, as the models showed acceptable residual distributions and variance homogeneity.

 

7. The “Z-activation score” is not reproducible as described. The manuscript indicates that an integrative score was computed, but does not provide the exact formula, standardization procedure, or aggregation steps. These should be specified in Methods (or Supplementary Methods) to enable reproduction.

We thank the reviewer for pointing this out.

To obtain a composite measure of immediate-early gene (IEG) activation, individual z-scores were computed for each of four IEGs (Arc, Zif268, NPAS4, and c-Fos) per animal, brain region, and experimental condition. For each gene within each brain region, expres-sion values were standardised to the vehicle/no-stress control group (z = [x − Mᵥᴇʜ] / SDᵥᴇʜ). The IEGs z-score for each animal was then calculated as the arithmetic mean of the four gene-level z-scores, yielding a single composite index of IEG induction per region and condition. BDNF total was not included in this composite because it is a neurotrophin rather than an activity-dependent IEG.

The composite IEGs z-scores were analysed separately for each brain region (frontal cortex [FC], hippocampus [HIPP], and striatum [STR]). Within each region, the a priori contrast of interest was the effect of swim stress (no stress vs. forced swim test [FST]) within each treatment group (VEH, KET, IMI), yielding three comparisons per region and nine comparisons in total. Welch’s t-tests were used to accommodate unequal group sizes and potential variance heterogeneity. All nine p-values were corrected for multiple comparisons using the Benjamini–Hochberg (BH) procedure. Cohen’s d with pooled standard deviations was computed for each contrast, and 95% confidence intervals were obtained via the noncentral t-distribution. Statistical significance was set at α = .05 (two-tailed). Please refer to lines 144-151 and 204-212).

 

8. “Fronto-striatal circuit” language is overly inferential. The dissection targets broad regions (frontal cortex/striatum) without measuring connectivity or circuit-level function. More conservative wording is recommended (e.g., “cortical and striatal regions/components” rather than “circuit mechanisms”).

Thank you for this important comment. Following your suggestion, we have revised the wording to avoid overly inferential language. Specifically, the terminology has been modified in both the title and the abstract, replacing “fronto-striatal circuit” with “cortical and striatal regions” (lines 3 and 35).

 

9. Multiple testing across genes and regions needs global consideration. While Tukey’s post hoc test controls comparisons within each ANOVA, the overall number of endpoints (genes × regions) raises multiplicity concerns. Either apply an FDR approach across the gene panel and/or explicitly frame the multi-endpoint analyses as exploratory.

We thank the reviewer for raising the issue of multiple testing across genes and brain regions. To address this, all gene expression data were analyzed using a linear mixed-effects model accounting for repeated measures across genes and regions within each animal. Post hoc pairwise contrasts (stress and treatment comparisons) across all genes and regions were corrected for multiple comparisons using the Benjamini–Hochberg false discovery rate procedure. Effect sizes (Cohen’s d) and 95% confidence intervals are reported as descriptive measures. These analyses ensure that multiplicity concerns are properly accounted for while preserving interpretability of the data.

 

10. Figure 1 legend contains inconsistencies. The legend references “percentage” whereas the axis reports immobility in seconds, and the statistical significance coding appears to include an error. The legend should be corrected for consistency and accuracy.

Thank you for pointing this out. The Figure 1 legend has been carefully checked and corrected.

 

Reviewer 2 Report

Comments and Suggestions for Authors

The study has merit and scientific impact; however, it needs some adjustments.

Comments:

The manuscript abstract suggests direct clinical relevance (“classical vs. rapid-acting antidepressant action”), but lacks translational validation. In this sense, some adjustments to the writing or the addition of translational limitations are necessary.

The abstract does not present the main statistical results, and furthermore, it should explore the study's gap more clearly.

Methodologically, the study adopts a mechanistic view of antidepressant inferences; it could be reclassified as a stress-coping model.

In terms of pharmacology, the authors use Imipramine as an effect to minimize stress and consequently neural depression resulting from stress-induced events. However, the drug requires chronic treatment for an antidepressant effect; I would like a clearer explanation of its use in acute doses.

Another point is the measurement of BDNF, which, in its evaluative capacity, becomes more effective as a late marker (hours–days); however, it is measured and evaluated within a 30-minute period after stress. The authors could explain this aspect.

The authors report Cohen's d for multiple comparisons without proper statistical adjustment.

I couldn't understand this quote: "Experimental unit = individual animal."

At some points in the discussion, the authors mix evaluation relationships at a single point in time with causality. They interpret gene suppression as a mechanism of antidepressant action.

The analyses with 4 genes × 3 regions × 2 factors generate immense interactions; however, the process of adjustment and statistical correction for multiple evaluations of the interaction was not described.

The manuscript is important and, after adjustments, has potential for publication.

Best regards!

Author Response

Reviewer 2

The study has merit and scientific impact; however, it needs some adjustments.

 

Comments:

 

1. The manuscript abstract suggests direct clinical relevance (“classical vs. rapid-acting antidepressant action”), but lacks translational validation. In this sense, some adjustments to the writing or the addition of translational limitations are necessary.

We thank the reviewer for this comment. We agree that, while our findings suggest distinct molecular mechanisms, the translational relevance to human clinical outcomes is not directly demonstrated. In response, we have revised the abstract to explicitly acknowledge this limitation as follows (lines 36-39):

“While these findings suggest potential translational relevance for understanding distinct mechanisms, further studies in humans are required to validate these signatures and their clinical implications.”

 

2. The abstract does not present the main statistical results, and furthermore, it should explore the study's gap more clearly.

We thank the reviewer for this helpful comment. The abstract has been revised to better clarify the knowledge gap addressed by the study and to more explicitly report the main findings. In particular, we now state that the reported effects represent statistically significant changes where appropriate.

 

3. Methodologically, the study adopts a mechanistic view of antidepressant inferences; it could be reclassified as a stress-coping model.

We appreciate the reviewer’s observation. We agree that the swim stress paradigm is progressively interpreted as a measure of stress-coping strategies rather than a direct model of depressive-like behavior. Our intention was not to propose antidepressant mechanisms in a clinical sense, but rather to examine how acute antidepressant administration modulates molecular and behavioral responses to an acute stress challenge.

To clarify this conceptual framework, we have revised the manuscript to further emphasize that the behavioral outcomes should be interpreted as coping responses to acute stress, and that the molecular analyses capture drug-dependent modulation of stress-evoked neuronal activation rather than antidepressant efficacy per se.

These clarifications have been incorporated in the Abstract (line 29), Introduction (line 78) and Discussion (lines 489-491) sections.

 

4. In terms of pharmacology, the authors use Imipramine as an effect to minimize stress and consequently neural depression resulting from stress-induced events. However, the drug requires chronic treatment for an antidepressant effect; I would like a clearer explanation of its use in acute doses.

Thank you for this comment. The choice of acute imipramine administration was based on preclinical evidence showing that imipramine produces effects after acute treatment in rodent behavioral models, whereas in humans, efficacy typically requires chronic treatment. To clarify this point, we have added in line 75 the appropriate reference in the manuscript supporting the use of acute imipramine in preclinical studies.

 

5. Another point is the measurement of BDNF, which, in its evaluative capacity, becomes more effective as a late marker (hours–days); however, it is measured and evaluated within a 30-minute period after stress. The authors could explain this aspect.

We thank the reviewer for this observation. We agree that BDNF is generally considered a later marker, with transcriptional and protein changes often emerging several hours after stimulation. In the present study, the primary aim of the chosen time point (30 minutes after swim stress) was to capture the peak transcriptional activation of immediate early genes, which typically occurs within 30–60 minutes following neuronal activation. BDNF was included in the analysis as an additional plasticity-related factor to assess whether early transcriptional engagement of this pathway could already be detected at the early time point. Moreover, measuring BDNF at the same time point as the IEGs provided a useful comparison between rapid transcriptional responses of IEGs and a plasticity-related factor with slower kinetics. To clarify these aspects, we have revised the Discussion accordingly (lines 441-446).

 

6. The authors report Cohen's d for multiple comparisons without proper statistical adjustment.

We thank the reviewer for raising this point. In the revised analysis, all post hoc pairwise contrasts across genes and brain regions were corrected for multiple comparisons using the Benjamini–Hochberg false discovery rate procedure applied across the full set of contrasts. Cohen’s d values are reported as descriptive effect size estimates to quantify the magnitude of the observed differences and were therefore not subjected to additional multiplicity correction. We have clarified this point in the Methods section (lines 162-217).

 

7. I couldn't understand this quote: "Experimental unit = individual animal."

The experimental unit for the analysis is based on results of each mouse rather than cage or any other measure. Stating the experimental unit is pivotal and required according to the ARRIVE guidelines.

 

8. At some points in the discussion, the authors mix evaluation relationships at a single point in time with causality. They interpret gene suppression as a mechanism of antidepressant action.

We thank the reviewer and we agree that the present study does not allow causal inference regarding the role of specific transcriptional changes in antidepressant action. To address this point, we have revised the Discussion (lines 378-379; 404; 410-413; 427-430) to clarify that our results describe transcriptional correlates of drug-modulated stress responses rather than causal mechanisms.

 

9. The analyses with 4 genes × 3 regions × 2 factors generate immense interactions; however, the process of adjustment and statistical correction for multiple evaluations of the interaction was not described.

We thank the reviewer for raising this point. In the revised analysis, gene expression data were analysed using a single linear mixed-effects model including the full factorial interaction of treatment, stress, gene, and brain region. This approach evaluates all main effects and interactions within one unified model, thereby avoiding separate statistical tests for each gene–region combination. Multiple testing arises only at the level of post hoc pairwise contrasts. These contrasts (stress and treatment comparisons across all gene × region combinations) were corrected for multiple comparisons using the Benjamini–Hochberg false discovery rate procedure applied across the full set of contrasts. The description of this procedure has been clarified in the Methods section (lines 162-217).

 

10. The manuscript is important and, after adjustments, has potential for publication.

We thank the reviewer for this positive assessment and for recognizing the importance of the manuscript.

 

 

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The improvement in the paper is evident; the authors should be congratulated. My suggestions and some questions raised by this reviewer have been addressed. The paper is ready for publication.