Review Reports - Antidepressant-like Activity of a Triple Combination of Venlafaxine, Codeine and Nor-Binaltorphimine in the Mouse Tail Suspension Test

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The work by Lungu and co-workers, as mentioned in the title, investigates the antidepressant-like effects of venlafaxine (VEN), codeine (COD), and norbinaltorphimine (norBNI), administered individually or in selected combinations, using the forced swim test (FST) and tail suspension test (TST) in mice. The research question is relevant and clearly defined. The combination of monoaminergic enhancement, µ-opioid modulation and κ-opioid blockade appears conceptually interesting and provides a potentially novel experimental angle. The behavioral experiments are complemented by a molecular docking analysis involving monoamine transporters and opioid receptors. The manuscript is generally well organized, the authors provide extensive statistical analyses, and the distinction between antidepressant-like activity in acute behavioral assays and clinical treatment-resistant depression is appropriately acknowledged. The topic is potentially interesting because it attempts to integrate monoaminergic and opioid mechanisms within a multi-target pharmacological strategy. Nevertheless, several important conceptual issues need to be addressed before the manuscript can be considered for publication.

Major comments

1. The initial selection of the 10-40 mg/kg dose range for venlafaxine and codeine requires stronger justification. Moreover, for codeine, the authors should additionally justify whether the selected dose range was intended to provide increasing µ-opioid receptor engagement. Similarly, the rationale for selecting a single 10 mg/kg dose of norBNI should be explicitly provided. The authors should indicate whether these doses were chosen on the basis of previous behavioral/pharmacological studies, preliminary experiments, receptor pharmacology, or expected systemic exposure. This issue is particularly relevant because changes in immobility in the FST and TST may be influenced by drug-induced alterations in locomotor activity, especially at higher doses. The authors should therefore discuss whether the selected dose ranges are known to produce nonspecific motor, sedative, or stimulant effects and provide appropriate references supporting the chosen doses.

2. Experiment 4 raises some concerns regarding the interpretation of the triple combination. The triple treatment was compared with saline, norBNI alone, COD alone, and norBNI+VEN, but not all relevant single and double combinations were tested within the same experiment. In particular, VEN alone, VEN+COD, and norBNI+COD were not included as parallel groups. This makes it difficult to determine how much each drug contributes to the final effect. This is especially important because the control groups differed considerably between experiments, with particularly high variability in the saline group in Experiment 4 (127.08±104.88s). Therefore, comparisons with treatment groups tested in separate experiments should be interpreted with caution. Importantly, the triple combination was not significantly more effective than norBNI+VEN. Thus, although the results show that the triple combination produces an antidepressant-like effect compared with saline, they do not clearly demonstrate that adding codeine is necessary or that all three drugs act cooperatively. The authors should therefore moderate this conclusion and revise the title, abstract, discussion, and conclusions accordingly, clearly distinguishing the effect of the triple combination from evidence of a true three-drug cooperative interaction.

3. The use of the term “cooperative interaction” needs clarification. Although the authors do not claim formal synergy, this wording may suggest that cooperation between all three components has been demonstrated. However, the triple combination was not significantly more effective than norBNI+VEN. The authors should therefore clearly define what they mean by “cooperativity” and distinguish it from additivity, potentiation, and synergy. The corresponding statement in the Abstract should also be moderated.

4. The lack of an independent assessment of locomotor activity is an important limitation of the study. Although the authors mention that FST and TST results can be influenced by changes in motor activity, this issue is not clearly included in the Limitations section. Without an open-field test or a similar assessment, nonspecific motor effects cannot be excluded. This limitation should be clearly stated and considered when interpreting the antidepressant-like effects. If locomotor data are available, they should be provided.

5. The different response to venlafaxine in the TST and FST is interesting. However, the conclusion that the TST is a more reliable assay for SNRI screening seems too general based on the results obtained with only one drug. The authors can conclude that, under the conditions of this study, the TST was more sensitive to venlafaxine than the FST. The term “clinically relevant doses” should also be used with caution unless the selected doses in mice can be related to therapeutic drug exposure in humans.

6. The docking results are interesting, but some of their interpretation goes too far. Docking may suggest possible binding modes, but it cannot confirm affinity or selectivity. The statements about target preference should therefore be toned down. The Reviewer would also revise the statement that the interaction “must arise downstream of target binding”, as this cannot be concluded from docking alone.

Minor comments

The Title should also be reconsidered. The term “cooperative interaction” may be too strong based on the current results. A more descriptive title focusing on the antidepressant-like effect of the triple combination may better reflect the findings of the study.
The Abstract is quite detailed and contains a large amount of statistical information. It could be shortened to focus on the main findings. Importantly, it should clearly mention that the triple combination was not significantly different from norBNI+VEN.
Please use the term “antidepressant-like effect/activity” consistently when describing the results of the FST and TST, rather than “antidepressant effect”.
The Introduction is rather long and could be shortened. Some information is repeated, and several paragraphs already contain detailed mechanistic interpretation that would be more appropriate for the Discussion. In particular, the extensive description of dynorphin/κ-opioid signaling, the prolonged pharmacological effects of norBNI, and its possible role as a component of combination therapy could be condensed. These points are discussed again later in the manuscript. The same applies to the detailed discussion of previous codeine-antidepressant combinations. The Reviewer suggests focusing the Introduction more clearly on the background, rationale, and main hypothesis of the study, and moving more detailed mechanistic interpretation to the Discussion.
A non-significant result should not be interpreted as evidence of no effect. This is particularly important for the norBNI+VEN combination, for which the study may have been underpowered.
The phrase “statistically indistinguishable from AMI” should be used with caution. The absence of a significant difference does not demonstrate that the treatments are equivalent. For the same reason, the term “AMI-equivalent” should be avoided. It would be more appropriate to state that the effect was of a similar magnitude to that observed with AMI, with no significant difference detected between the groups.
Please reconsider whether “low-efficacy µ-opioid agonism” adequately describes the in vivo effect of codeine, particularly considering its conversion to active metabolites.
The discussion is comprehensive but rather long. Some of the mechanistic interpretation, particularly regarding the dynorphin system, could be shortened or more clearly presented as a possible explanation rather than a demonstrated mechanism.
Please check that all abbreviations are defined when first introduced and are used consistently throughout the manuscript.

Author Response

Response to Reviewer 1, major comments

We thank the reviewer for the careful evaluation of our manuscript and for highlighting the importance of the topic. Your observations were highly valuable and helped us substantially improve the clarity, methodological rigor, and interpretability of our work. All changes have been clearly highlighted in the revised manuscript, in red. Our point-by-point responses are provided below in blue.

Comment 1. The initial selection of the 10-40 mg/kg dose range for venlafaxine and codeine requires stronger justification. Moreover, for codeine, the authors should additionally justify whether the selected dose range was intended to provide increasing mu-opioid receptor engagement. Similarly, the rationale for selecting a single 10 mg/kg dose of norBNI should be explicitly provided. The authors should indicate whether these doses were chosen on the basis of previous behavioral/pharmacological studies, preliminary experiments, receptor pharmacology, or expected systemic exposure. This issue is particularly relevant because changes in immobility in the FST and TST may be influenced by drug-induced alterations in locomotor activity, especially at higher doses. The authors should therefore discuss whether the selected dose ranges are known to produce nonspecific motor, sedative, or stimulant effects and provide appropriate references supporting the chosen doses.

Response: Thank you for the insightful comment. We have added a dedicated paragraph. The doses were taken from published rodent pharmacology and not from preliminary experiments of our own, and the new paragraph states this explicitly for each compound. For venlafaxine, the 10 to 40 mg/kg range brackets the doses active in the mouse forced swim test, where 8 to 64 mg/kg reduce immobility and where serotonin reuptake inhibition predominates at the lower end while noradrenaline reuptake inhibition is recruited at the higher end [7,8], and it is the range in which the antidepressant-like effect has been shown to require mu-opioid receptors [12] and an intact opioid system [25]. For codeine, the geometric progression of 10, 20 and 40 mg/kg was chosen precisely to provide increasing mu-opioid receptor engagement above the sub-effective doses that combine with SSRIs in the mouse tail suspension test [54], so that both potentiation and attenuation would have been detectable; this is now stated in those terms. For norBNI, the single dose of 10 mg/kg given 24 h beforehand is the standard regimen for complete and selective kappa blockade in mice [25,39,41], and because the blockade lasts for weeks [39-42], dose escalation within an acute experiment would add nothing. On the motor question we have been deliberately explicit rather than reassuring: the same source that establishes the venlafaxine dose range also reports increased spontaneous locomotor activity in mice at 16 to 64 mg/kg [7], a range that includes two of our three doses, so a motor contribution cannot be excluded. This is now stated in the Methods and developed in the Limitations.

Change and location: Section 4.2, new paragraph headed Dose selection; Section 3.6, paragraph on locomotor assessment, rewritten.

Comment 2. Experiment 4 raises some concerns regarding the interpretation of the triple combination. The triple treatment was compared with saline, norBNI alone, COD alone, and norBNI+VEN, but not all relevant single and double combinations were tested within the same experiment. In particular, VEN alone, VEN+COD, and norBNI+COD were not included as parallel groups. This makes it difficult to determine how much each drug contributes to the final effect. This is especially important because the control groups differed considerably between experiments, with particularly high variability in the saline group in Experiment 4 (127.08 plus or minus 104.88 s). Therefore, comparisons with treatment groups tested in separate experiments should be interpreted with caution. Importantly, the triple combination was not significantly more effective than norBNI+VEN. Thus, although the results show that the triple combination produces an antidepressant-like effect compared with saline, they do not clearly demonstrate that adding codeine is necessary or that all three drugs act cooperatively. The authors should therefore moderate this conclusion and revise the title, abstract, discussion, and conclusions accordingly, clearly distinguishing the effect of the triple combination from evidence of a true three-drug cooperative interaction.

Response: Thank you for the comment. We have revised the manuscript accordingly. The title no longer refers to a cooperative interaction. The abstract now states that the triple combination was not significantly more effective than norBNI + VEN and that the contribution of codeine therefore remains undetermined. In the Results we added a third tempering observation covering exactly the two points raised, namely the unusual dispersion of the Experiment 4 control and the indirect nature of any comparison with groups tested in a different cohort, including VEN alone and VEN + COD from Experiment 3. Section 3.3 was retitled and its concluding paragraph rewritten to state that the pattern is equally compatible with an effect carried mainly by kappa blockade together with the SNRI. The Conclusions were rewritten in the same sense, and the interpretation column of Table 2 no longer describes the result as a cooperative triple interaction. We also accept the implication for the design: Section 3.7 now identifies a complete factorial design within a single cohort, including VEN alone, VEN + COD and norBNI + COD, as the most informative next experiment, and explains why it is required.

Change and location: Title page; Abstract; Section 2.4, third tempering finding; Section 2.6, final sentence; Section 3.3, new heading and final paragraph; Table 2, interpretation column, four rows; Section 3.6; Section 3.7; Section 5, third paragraph.

Comment 3. The use of the term cooperative interaction needs clarification. Although the authors do not claim formal synergy, this wording may suggest that cooperation between all three components has been demonstrated. However, the triple combination was not significantly more effective than norBNI+VEN. The authors should therefore clearly define what they mean by cooperativity and distinguish it from additivity, potentiation, and synergy. The corresponding statement in the Abstract should also be moderated.

Response: Thank you for the comment. A definition has been added. Cooperativity is now defined in a strictly operational sense, namely that a statistically detectable effect is present when the mechanisms are combined and absent when the components are given alone in the same cohort, and the definition states explicitly that the term so used is weaker than potentiation, which requires one agent to increase the effect of another, weaker than synergy, which requires a combined effect exceeding the isobolographic prediction of additivity, that it does not exclude simple additivity, and that it does not establish that every component contributes. The abstract no longer claims cooperativity as a result; it states that the fixed-dose design does not establish cooperativity between all three mechanisms. Section 3.3 uses the term only in the defined sense.

Change and location: Section 1, final paragraph; Abstract, Conclusion’s sentence; Section 3.3, final paragraph; Section 5, third paragraph.

Comment 4. The lack of an independent assessment of locomotor activity is an important limitation of the study. Although the authors mention that FST and TST results can be influenced by changes in motor activity, this issue is not clearly included in the Limitations section. Without an open-field test or a similar assessment, nonspecific motor effects cannot be excluded. This limitation should be clearly stated and considered when interpreting the antidepressant-like effects. If locomotor data are available, they should be provided.

Response: Thank you for the comment. No locomotor data were collected in this study, and we state this plainly rather than argue around it. The first paragraph of the limitations has been rewritten to say that the absence of an independent locomotor assessment is an important limitation, that immobility can be reduced by non-specific motor activation and increased by sedation [13,14], that venlafaxine increases spontaneous locomotor activity in mice at 16 to 64 mg/kg [7], a range including two of the doses used here, and that a motor contribution to the reductions in immobility, in particular for VEN 40 mg/kg and for the combination groups, cannot be excluded, so that every antidepressant-like effect reported here must be read with that reservation. The same point is made in Section 3.1 and in the new dose-selection paragraph, and concurrent locomotor controls are listed first among the required next experiments.

Change and location: Section 3.6, paragraph on locomotor assessment; Section 3.1, final sentences; Section 4.2, Dose selection; Section 3.7.

Comment 5. The different response to venlafaxine in the TST and FST is interesting. However, the conclusion that the TST is a more reliable assay for SNRI screening seems too general based on the results obtained with only one drug. The authors can conclude that, under the conditions of this study, the TST was more sensitive to venlafaxine than the FST. The term clinically relevant doses should also be used with caution unless the selected doses in mice can be related to therapeutic drug exposure in humans.

Response: Thank you for the comment. We have adopted the reviewer's wording. The conclusion now states that, under the conditions of this study, the TST was more sensitive to venlafaxine than the FST in this strain, and adds that a single compound does not support a general ranking of the two assays. The phrase clinically relevant doses has been removed from the manuscript; we did not measure plasma or brain concentrations, so no relation to human therapeutic exposure can be claimed, and this is stated among the limitations.

Change and location: Section 5, first paragraph; Section 3.1, final sentence.

Comment 6. The docking results are interesting, but some of their interpretation goes too far. Docking may suggest possible binding modes, but it cannot confirm affinity or selectivity. The statements about target preference should therefore be toned down. The Reviewer would also revise the statement that the interaction must arise downstream of target binding, as this cannot be concluded from docking alone.

Response: Thank you for the comment. The interpretation has been toned down throughout. The heading of Section 2.7 now reads that the docking is consistent with the target assignment rather than that it supports it. The statement that the interaction must arise downstream of target binding has been removed from both the Discussion and the Abstract and replaced by the weaker claim that the interaction is more likely to arise downstream, with the explicit addition that docking alone cannot establish where, or whether, such an interaction takes place. In Section 3.4 the target assignment is now described as consistent with the docking results rather than as holding, and the structural paragraph of the Conclusions states that separate sites are a necessary but not sufficient condition. We note that the two qualifications we had already placed in Section 3.4, namely that the score does not reproduce the affinity order across targets and that docking cannot demonstrate absence of binding, are retained and have been made more compact.

Change and location: Section 2.7 heading; Section 3.4, three sentences; Section 5, structural paragraph; Abstract, Conclusion’s sentence.

Reviewer 1, minor comments

Comment 7. The Title should also be reconsidered. The term cooperative interaction may be too strong based on the current results. A more descriptive title focusing on the antidepressant-like effect of the triple combination may better reflect the findings of the study.

Response: Thank you for the suggestion. The title has been changed to a descriptive one: Antidepressant-like Activity of a Triple Combination of Venlafaxine, Codeine and Nor-Binaltorphimine in the Mouse Tail Suspension Test.

Change and location: Title page.

Comment 8. The Abstract is quite detailed and contains a large amount of statistical information. It could be shortened to focus on the main findings. Importantly, it should clearly mention that the triple combination was not significantly different from norBNI+VEN.

Response: Thank you for the suggestion. The abstract has been rewritten and shortened from 540 to 395 words. Most of the statistical detail has been removed, including the effect sizes, confidence intervals, Bayes factors and correlation coefficients, and only the figures needed to follow the main findings were kept. It now states explicitly that the triple combination was not significantly more effective than norBNI + VEN and that the contribution of codeine remains undetermined, and it also states that the non-significant results were obtained in a design underpowered for intermediate effects.

Change and location: Abstract.

Comment 9. Please use the term antidepressant-like effect/activity consistently when describing the results of the FST and TST, rather than antidepressant effect.

Response: Thank you for the comment. We checked every occurrence in the manuscript. In the body of the paper the term antidepressant-like effect or antidepressant-like activity is now used throughout; the expressions antidepressant effect and antidepressant efficacy no longer appear outside the titles of cited articles in the reference list, where they are part of the original titles and cannot be changed.

Change and location: Throughout the manuscript.

Comment 10. The Introduction is rather long and could be shortened. Some information is repeated, and several paragraphs already contain detailed mechanistic interpretation that would be more appropriate for the Discussion. In particular, the extensive description of dynorphin/kappa-opioid signaling, the prolonged pharmacological effects of norBNI, and its possible role as a component of combination therapy could be condensed. These points are discussed again later in the manuscript. The same applies to the detailed discussion of previous codeine-antidepressant combinations. The Reviewer suggests focusing the Introduction more clearly on the background, rationale, and main hypothesis of the study, and moving more detailed mechanistic interpretation to the Discussion.

Response: Thank you for the insightful comment. The Introduction has been condensed from 1806 to 1655 words. The two opening paragraphs on the burden of depression were merged into one. The three passages named by the reviewer were shortened: the paragraph on dynorphin and kappa-opioid signalling, the paragraph on the duration of action of norBNI and its use in combination, and the paragraph on previous codeine and antidepressant combinations. The paragraphs on venlafaxine pharmacology, on treatment-resistant depression, on the three compounds, on the opioid dependence of the venlafaxine effect, on target distribution and on the two behavioural assays were also tightened. The mechanistic detail removed is not lost to the reader, since it is developed in Sections 3.2 to 3.4, where the reviewer rightly says it belongs. We kept the paragraph on the locomotor profile of venlafaxine in the Introduction, because the reviewer's first major comment asks for exactly that information as part of the justification of the dose range.

Change and location: Section 1, nine paragraphs rewritten or merged.

Comment 11. A non-significant result should not be interpreted as evidence of no effect. This is particularly important for the norBNI+VEN combination, for which the study may have been underpowered.

Response: Thank you for the comment. We have removed every formulation that treated a non-significant result as absence of effect. In the Discussion, kappa blockade and mu agonism are no longer described as inert; the text now states that they produced no significant change. In Table 2 the interpretation column no longer reads that kappa blockade alone is behaviourally silent or that mu agonism alone is insufficient, but that no significant effect was detected. The abstract, the Results and the Conclusions now state that these non-significant results were obtained in a design underpowered for intermediate effects and do not establish the absence of an effect. The observed power of 0.36 for the norBNI + VEN contrast and the approximately 35 animals per group that would be required were already reported in Section 2.5 and are retained.

Change and location: Abstract; Section 2.4; Section 3.3, first paragraph; Table 2, interpretation column; Section 5, third paragraph.

Comment 12. The phrase statistically indistinguishable from AMI should be used with caution. The absence of a significant difference does not demonstrate that the treatments are equivalent. For the same reason, the term AMI-equivalent should be avoided. It would be more appropriate to state that the effect was of a similar magnitude to that observed with AMI, with no significant difference detected between the groups.

Response: Thank you for the comment. Both expressions have been removed from the manuscript. The wording now follows the reviewer's suggestion: the effect was of similar magnitude to that of amitriptyline, with no significant difference detected between the groups. In Section 2.2 we added that the absence of a significant difference does not establish equivalence.

Change and location: Abstract; Section 2.2; Section 2.6; Section 3, opening paragraph; Table 2, VEN 40 row and triple combination row; Section 5, third paragraph.

Comment 13. Please reconsider whether low-efficacy mu-opioid agonism adequately describes the in vivo effect of codeine, particularly considering its conversion to active metabolites.

Response: Thank you for the comment. The expression has been removed from the abstract, which now refers simply to mu-opioid receptor activation by codeine. We agree that the in vivo effect of codeine cannot be described in terms of intrinsic efficacy alone, since it depends on conversion to morphine; this is discussed in Sections 3.5 and 3.6, where the CYP2D6-dependent biotransformation of codeine, the dependence of its mu-opioid activity on that conversion [86,87] and the differences between murine and human metabolism [88,89] are set out.

Change and location: Abstract, Background sentence; Sections 3.5 and 3.6, unchanged text retained.

Comment 14. The discussion is comprehensive but rather long. Some of the mechanistic interpretation, particularly regarding the dynorphin system, could be shortened or more clearly presented as a possible explanation rather than a demonstrated mechanism.

Response: Thank you for the suggestion. The dynorphin passage in Section 3.2 has been shortened and reframed. It now opens by stating that a counter-regulatory process is one pharmacologically plausible explanation, and it closes by saying explicitly that we present it only as a hypothesis, for two stated reasons: the evidence for mu-agonist-driven dynorphin upregulation comes mainly from spinal and dorsal striatal preparations rather than from mesolimbic circuits, and the present study measured no neurochemical variable that could test it. Sections 3.4 and 3.5 were also condensed.

Change and location: Section 3.2, final paragraph; Section 3.4, qualifications paragraph; Section 3.5, first paragraph.

Comment 15. Please check that all abbreviations are defined when first introduced and are used consistently throughout the manuscript.

Response: Thank you for the pointing this out. All abbreviations were checked against their first occurrence in the text and against the abbreviation list. Two entries that were used in the text but missing from the list have been added, namely the 5-HT3 receptor and ligand efficiency. The remaining uppercase terms in the text are software names, database identifiers or trial acronyms defined at the point of use.

Change and location: Abbreviations list, two new entries; text unchanged elsewhere.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

In this paper the authors report results of a study in which three compounds that differentially effect monoamine and opioid systems interact when co-administered in two behavioral tests that have been thought to model depression as well as for molecular modeling to evaluate whether concurrent administration might alter binding sites of these compounds. The authors find a surprising and profound differences between one compound in the two behavioral tests but do find that co-administration of all three compounds does anti-depressant like effects comparable but not greater than a well-accepted control compound. The protocols and analysis are of good quality.

A major limitation, for this reviewer, was the extent to which current results would help direct clinically relevant future studies. The authors, to their credit, appropriate cite numerous limitations of many aspects of the current study but based on their own comments, it is unclear whether, for example, extending a similar approach to more currently acceptable behavioral models of depression as well as to both male and female mice of different strains would provide additional insight. The dramatic and unexpected difference between tail suspension and forced swim were not accompanied, in this reviewer’s opinion, by a reasonable, testable hypothesis. The interactions between the three systems targeted by the authors is of interest but the best response only mimiced the behavioral effects of one well-accepted control compound. The significance of the current study and future studies based on these data needs to be better developed.

Comments on the Quality of English Language

Clearly presented

Author Response

Response to Reviewer 2

Comment 1. A major limitation, for this reviewer, was the extent to which current results would help direct clinically relevant future studies.

Response: Thank you for the comment. We have added a paragraph that states what these data do and do not support for clinical direction, and it is deliberately modest. Two consequences are drawn. First, the pairing that carries most of the observed effect is kappa-opioid blockade combined with an SNRI rather than the addition of a mu-opioid agonist, so the next preclinical step is a complete factorial design in a single cohort and not a further dose escalation of codeine. Second, because the effect was obtained in acute assays in naive animals, the clinical question these data inform is narrow, namely whether kappa antagonism added to an SNRI improves the stress-coping and reward-related domains that such assays engage. We also name the regimen that would be of translational interest, an SNRI combined with a kappa antagonist usable in humans such as aticaprant, and the conditions under which it would have to be tested.

Change and location: Section 3.5, new paragraph.

Comment 2. The authors, to their credit, appropriate cite numerous limitations of many aspects of the current study but based on their own comments, it is unclear whether, for example, extending a similar approach to more currently acceptable behavioral models of depression as well as to both male and female mice of different strains would provide additional insight.

Response: Thank you for the comment and for the suggestion. Section 3.7 has been rewritten so that each proposed experiment is tied to the question it would answer. The complete factorial design in a single cohort would establish whether codeine adds anything to kappa blockade combined with an SNRI and would remove the cross-cohort comparisons that limit the present study; isobolographic or response-surface designs would determine whether the interaction is supra-additive; concurrent locomotor controls and separate scoring of active behaviours would separate motor from affective components; chronic stress models with anhedonia and effort-based outcomes would test whether the effect extends to the domains that matter clinically; and both sexes and more than one strain would test generalisability. We say explicitly that these steps are necessary before the strategy can be considered translationally relevant.

Change and location: Section 3.7, rewritten; Section 3.5, new paragraph.

Comment 3. The dramatic and unexpected difference between tail suspension and forced swim were not accompanied, in this reviewer's opinion, by a reasonable, testable hypothesis.

Response: Thank you for the insightful comment. We have added one. The new passage proposes that the forced swim test imposes a thermoregulatory and energetic load that the tail suspension test does not, and that immobility is scored over a shorter window after a stabilisation period, so that a serotonergic-preferring drug may redistribute active behaviours without reducing total immobility. Three predictions follow and are stated as such: that venlafaxine increases active behaviours in the forced swim test without changing total immobility when swimming and climbing are scored separately; that reducing the thermoregulatory load by raising water temperature increases the sensitivity of the forced swim test to venlafaxine; and that the dissociation persists when a concurrent locomotor control is included. We also state that until these experiments are done, the conclusion is restricted to the sensitivity observed under the conditions of this study.

Change and location: Section 3.1, final sentences of the last paragraph.

Comment 4. The interactions between the three systems targeted by the authors are of interest but the best response only mimiced the behavioral effects of one well-accepted control compound.

Response: Thank you for the comment. The revised manuscript no longer leaves it implicit. The triple combination did not exceed amitriptyline; it reached an effect of similar magnitude, with no significant difference detected, and the text now says so in those words wherever the comparison appears. We do not claim superiority over an established antidepressant. The interest of the regimen, as we now state in Section 3.5, lies in the mechanism rather than in the size of the acute effect: a combination that matches a tricyclic in an acute assay is worth pursuing only if it acts through a route that remains available when monoaminergic treatment fails, and that is a question these acute assays in naive animals cannot answer. Chronic stress models are needed, and are proposed.

Change and location: Abstract; Section 2.6; Section 3, opening paragraph; Section 3.5; Section 5, third paragraph.

Comment 5. The significance of the current study and future studies based on these data needs to be better developed.

Response: Thank you for the comment. Addressed by the two additions described above, taken together: the new paragraph in Section 3.5 on what the data do and do not support clinically, and the rewritten Section 3.7, in which each proposed experiment is linked to the specific question it would resolve. The Conclusions were also rewritten so that the claims they make match the evidence, and they end by stating what the structural data can and cannot establish.

Change and location: Sections 3.5, 3.7 and 5.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have adequately addressed all the comments and suggestions raised during the review process. The revised manuscript has been satisfactorily improved, and there are no further comments. Therefore, the Reviewer recommends accepting the manuscript for publication in its present form.