Striatal dopamine and serotonin release operate largely in parallel with limited, asymmetric crosstalk

Reviewer #1 (Public review):

In this study, Chaudun et al use optogenetics and genetically encoded neuromodulator sensors to test to what extent dopamine neuron stimulation produces striatal serotonin release, and vice versa. The study is timely given growing interest in dopamine/serotonin interactions, but important controls are missing. The authors find that striatal dopamine and serotonin afferents function largely independently, with dopamine neuron stimulation producing no striatal serotonin release and serotonin neuron stimulation (possibly) producing minimal striatal dopamine release.

In the revised manuscript draft, the authors increased sample sizes for some important experiments, removed inconclusive electrophysiology data, reorganized the figures, and added new anatomical tracing experiments. The critical fluorophore-only controls for the optostimulation experiments requested by reviewers were not done.

Unfortunately, with the exception of increased samples sizes, these revisions have done little to substantially improve the strength of the evidence behind the authors' conclusions. These conclusions, as reflected in the new title of the paper, have also slightly changed in a manner that puts them further at odds with the data presented. As a result, my opinion continues to be that the study is interesting and the experiments are useful, but important controls are missing, a more cautious interpretation is warranted, and the organization of the study is confusing. I explain my reasoning below.

(1) A major criticism of the original manuscript was that the electrophysiology experiments were only tangentially related to the question under study. The manuscript has now been reorganized in such a way that the cocaine experiments are similarly irrelevant. In the authors' own words, the central question of the study is "does activity in one [DA or 5-HT] system directly recruit transmitter release from the other, or do DA and 5-HT operate mainly through parallel circuits?". Optogenetically stimulating release of dopamine while recording serotonin activity (or vice versa) begins to answer this question, and in the original draft, cocaine-evoked dopamine and serotonin recordings were presented side by side with the opto-evoked dopamine/serotonin data. In this configuration, the drug-evoked recording data allowed readers to compare the magnitude of dopamine/serotonin release evoked by an artificial optogenetic manipulation to that evoked by a behaviorally relevant pharmacological treatment. This serves a purpose. In the revised manuscript, the cocaine experiments are presented in a standalone first figure. As the authors themselves note in their response to reviewer 2, cocaine independently evokes dopamine and serotonin accumulation is therefore poorly suited on its own to test how activating one neuromodulatory system affects the other. Thus, the cocaine data presented alone in this way neither address the paper's central question nor support the paper's conclusions.

(2 The original manuscript suggested that one way by which striatal serotonin activity could recruit striatal dopamine release would be if the same serotonin neurons project to both VTA and striatum. To test this, the authors use retrobeads to identify DS-, NAc-, and VTA- projecting dorsal raphe neurons. However, they neither identify whether the labeled neurons are serotonergic nor evaluate colocalization between the retrograde tracers as would be required to ascertain whether the same serotonin send axon collaterals to more than one region. Thus, the anatomical data presented do not answer the question of whether the same serotonin neurons innervate both targets.

(3) As noted in the original round of review, applying light stimulation to mice expressing a fluorophore-only construct without opsin is an important control in optostimulation experiments that is widely standard in the field. The omission of such a control is a weakness of the paper. The authors suggest that other results presented - such as the lack of green serotonin sensor activation when red light is applied in the midbrain in Fig 2G-H - argues against cross-talk between the red and green optical channels. This is technically correct, but ruling out cross-talk between optical channels is not the only reason such a control is necessary. The high intensity red light used for optostim travels several millimeters through tissue and can reach the retina. Although mice do not have cones to detect red light (and therefore cannot distinguish the color red from other colors), their rods are sensitive to red light. As a result, bright red intracranial optostim can be perceived by the animal as a flashing light, and this sensory stimulus can produce a neural response. The absence of such a response in the serotonin system in Fig 2G-H does not rule out the possibility that the small response in the dopamine system observed in Fig 3G-H is driven by sensory input rather than a bona fide physiological effect of serotonin neuron activation on striatal dopamine release. Crucially, sensory responses to the stimulating light would also show 2Hz entrainment to the frequency of the stimulating laser trains. In other words, without a fluorophore-only control, the entirety of the authors' results pertaining to serotonin-evoked dopamine release can be explained by artifactual effects of the optostimulation. If this opsin-negative control is absolutely impossible for the authors to perform, at the very least this major limitation should be clearly and explicitly addressed in the discussion because it pertains directly to the study's main conclusions. This brings me to my final point.

(4) Taken together, the authors' data appear to support two primary conclusions. First, optogenetic dopamine stimulation has no effect on striatal serotonin release. Second, synchronous and supra-physiological activation of the serotonin system has a very modest effect on striatal dopamine release that might be entirely explained by artifacts of the optostimulation protocol. The miniscule magnitude of the evoked dopamine response observed following maximally strong (15-20 mW) optogenetic serotonin stimulation also bears consideration here. It argues that even if the observed dopamine release effect is not an artifact of the optostimulation protocol, serotonin-evoked dopamine release is likely to be vanishingly small or absent in other conditions when serotonin neuron firing is neither supraphysiological nor synchronous. The new title strongly implies the existence of significant cross-talk, which is not well supported by the data. Claims throughout the text that call the cross-talk effect reliable or otherwise robust are similarly overstated.

Reviewer #3 (Public review):

The authors suggest that the small release of DA may be due to a release of glutamate from DRN 5-HT neurons to the VTA that stimulates weakly and in a transient fashion the VTA DA neurons, which in the end, produce a transient and small release of DA in the NAc.

Their findings give more information on the previously reported complex and partial known crosstalk between 5-HT and DA in the NAc.

Comments on revised version.

The authors have added several new experiments that address some of the prior concerns. However, there are still points of confusion. For example, the authors repeatedly argue that 5HT or DA are synaptic when in fact most of the transduction mechanisms for these neuromodulators and their transporters are extra synaptic, as indicative of volume transmission. This is not well articulated in the authors' interpretative scheme.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment:

This useful study employs optogenetics, genetically-encoded dopamine and serotonin sensors, and patch-clamp electrophysiology to investigate modulations of neurotransmitter release between striatal dopamine and serotonin neurons - a topic of interest to neuroscientists studying the basal ganglia. The results suggest that the dopamine and serotonin systems operate largely in parallel, with the activation of serotonin neurons resulting in a small, transient dopamine release. The authors suggest that this interaction occurs via glutamate release in the ventral tegmental area, findings that are closely related to previous work. Some conclusions are incomplete requiring larger samples-sizes and controls.

We sincerely thank the editor and reviewers for their thoughtful and constructive comments. Addressing their concerns required extensive additional experimental work and the involvement of new personnel. We increased sample sizes, completed previously missing experimental groups, generated a largely new dataset, and performed additional anatomical experiments and analyses. We also removed the patch-clamp electrophysiology experiments to sharpen the study’s focus and extensively revised and reorganized the manuscript to address methodological and interpretative inconsistencies. Although the central concept remains unchanged, the revised manuscript provides a substantially more rigorous and consistent account of the limited and directionally asymmetric circuit-level coupling between striatal dopamine and serotonin release.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, Liu et al use optogenetics and genetically encoded neuromodulator sensors to test the extent to which dopamine neuron stimulation produces striatal serotonin release, and vice versa. The study is timely given growing interest in dopamine/serotonin interactions and in the context of recent work showing bidirectional and dynamic regulation of striatal dopamine by another neuromodulator, acetylcholine. The authors find that striatal dopamine and serotonin afferents function largely independently, with dopamine neuron stimulation producing no striatal serotonin release and serotonin neuron stimulation producing minimal striatal dopamine release. This work will inform future work seeking to dissect the contributions of striatal dopamine, serotonin, and their interactions to various motivated behaviors. While the paper's main conclusions are adequately supported (see Strengths), additional controls and experiments would significantly broaden the paper's impact (see Weaknesses). Finally, this draft of the work is poorly presented with numerous errors, omissions, and inconsistencies evident throughout the text and the figures that should be addressed.

Strengths:

The study employs optogenetic stimulation simultaneously with fiber photometry recording of dopamine or serotonin release measured with genetically encoded sensors. These methods are state-of-the-art, offering tighter temporal control compared to pharmacological methods for manipulating dopamine and serotonin and improved selectivity over techniques like electrochemistry and microdialysis used to record neuromodulator release in previous studies on the subject. As a result, the paper's main conclusions are well supported.

Weaknesses:

(1) The electrophysiology experiments in Figure 3 are only tangentially related to the focus of the study, and their findings are almost entirely irrelevant to the paper's main conclusions. The results of these experiments are also not novel. Glutamate corelease from 5-HT neurons has been previously shown, including in the OFC and VTA (Ren et al, 2018, Cell, McDevitt et al, 2014, Cell Rep, Liu et al 2014, Neuron; and others). The authors should explain more clearly what they think these data add to the manuscript and/or consider removing them altogether.

We thank the reviewer for their insightful comments regarding the patch-clamp electrophysiology data. We acknowledge the concerns raised by multiple reviewers and have therefore removed these data from the revised manuscript to improve clarity and focus.

(2) Related to the point above, as far as I can tell, the only value the electrophysiology data add is to suggest that perhaps activation of serotonin neurons may drive minimal striatal dopamine release via glutamate corelease in the VTA. The evidence provided in this version of the manuscript is insufficient to support that claim, but the manuscript would be significantly strengthened if the authors tested this hypothesis more directly. One way to do that could be to stimulate serotonin axons in the striatum (as opposed to the serotonin cell bodies) and record striatal dopamine release.

This is an interesting approach. However, given the divergent projection of serotonin fibers and the need for a strict spectral separation between excitatory opsin and transmitter sensor fluorescence, we retained the current approach, which allows us to investigate circuit-level interactions while minimizing technical confounds.

A complementary anatomical approach would be to use retrograde tracing to test whether the DR 5-HT neurons projecting to the striatum are the same or different from the VTA projecting population.

We performed the suggested experiment and have included the new data in the revised manuscript (Figure 1F–H). This approach revealed a clear topographical organization. These results indicate that the identified neuronal populations are largely segregated.

(3) The findings would be strengthened by the addition of a fluorophore-only control group lacking opsin expression in all experiments in Figures 1 and 2.

We thank the reviewer for this important suggestion. We requested authorization to add an opsin-negative control cohort, but this request was not approved under the applicable animal-welfare regulations. We therefore cannot fully exclude nonspecific physiological effects of light delivery and now acknowledge this limitation in the Discussion. Nevertheless, the stimulation-locked response was confined to the biosensor channel and absent from the isosbestic channel, arguing against direct optical contamination. Moreover, application of the same optical stimulation protocol in the VTA did not generate a detectable stimulation-locked 5-HT signal. Although these observations do not fully replace an opsin-negative control, they support the interpretation that the response reflects a biological signal rather than direct optical interference.

(4) The experiment of stimulating serotonin neurons and recording serotonin release in the NAc was not performed. It would be useful to be able to compare the magnitudes of evoked serotonin release in these two striatal regions, though it is not central to the main claims of the paper.

This point has now been addressed with additional experiments, and the figure has been reformatted accordingly in the revised manuscript.

(5) The interpretation of the results from Figure 2 is described inconsistently throughout the manuscript. The title implies there is significant crosstalk between the dopamine and serotonin systems. The abstract calls the crosstalk "transient", which is a description of its temporal dynamics, not its magnitude. Then the introduction figures and discussion all suggest the crosstalk is minimal. I suggest the authors describe the main findings - minimal crosstalk between the dopamine and serotonin systems - clearly and consistently in the title, abstract, and main text.

We agree with the reviewer and have revised the title, abstract, Results, figure legends, and Discussion to describe the magnitude and directionality of the interaction consistently. The revised manuscript now emphasizes that striatal dopamine and serotonin release operate largely in parallel, with limited and asymmetric crosstalk: activation of VTA dopamine neurons did not produce detectable serotonin release, whereas activation of dorsal raphe serotonergic neurons induced only a weak, stimulation-locked dopamine signal without a sustained increase in dopamine amplitude. The revised title, “Asymmetric Circuit-Level Crosstalk Between Dopamine and Serotonin Release in the Striatum,” and the corresponding changes throughout the manuscript now more accurately reflect these findings.

Reviewer #2 (Public review):

Summary:

This brief communication aims to clarify interactions between the dopamine (DA) and serotonin (5-HT) systems of mice. The authors use optogenetic stimulation of DA neurons in the VTA or of 5-HT neurons in the DRN, while monitoring the fluorescence of DA and 5-HT sensors in the nucleus accumbens (NAc) and dorsal striatum (DS) using fiber photometry. The authors report on a small release of DA in the NAc following DRN stimulation, which they attribute to glutamate co-release onto VTA DA neurons using slice electrophysiology. The authors also report on cocaine-induced 5-HT release in the striatum.

Strengths:

This is a topic well worth studying.

Weaknesses:

In its current form, this is an incomplete and underpowered study that does little to clarify the complicated relationship that exists between DA and 5-HT in the mammalian brain under physiological conditions or during cocaine use.

We appreciate the reviewer’s thorough evaluation and constructive efforts. We acknowledge that the original manuscript did not meet the expected standards and have therefore undertaken a complete revision. We hope that the revised version addresses the concerns raised and provides a clearer and more rigorous presentation of our findings.

Reviewer #3 (Public review):

The authors suggest that the small release of DA may be due to a release of glutamate from DRN 5-HT neurons to the VTA that stimulates weakly and in a transient fashion the VTA DA neurons, which in the end, produce a transient and small release of DA in the NAc.

Their findings give more information on the previously reported complex and partial known crosstalk between 5-HT and DA in the NAc.

I only have some minor concerns about the manuscript:

(1) In Figure 2F, there is a missing curve for 5-HT in NAc. Besides, the legend shows n=2, making it difficult to perform statistical analysis with that data.

We repeated the experiments and analysis with a new and expanded dataset. We believe this revised dataset now provides sufficient power for robust statistical analysis.

(2) In Figure 3, the use of NBQX/AP5 is shown, but it is not mentioned either in the methodology or in the discussion. What is the meaning of those results?

Based on the reviewers’ suggestions, we have removed this figure entirely from the revised manuscript.

(3) Line 98 compares results from two different places of stimulation. The results are related to stimulation in the VTA, but the comparison indicates that the stimulation was made in the DRN.

The manuscript has been extensively revised, and all relevant sections of the text have been updated accordingly.

(4) If the release of 5-HT in Nac does not occur, it needs to be precise in the abstract that 5-HT is released in the dorsal striatum (DS) but not in the NAc (line 19).

We performed an additional set of experiments and confirmed the presence of 5-HT release in the NAc.

(5) Be consistent with the way you mention the 5-HT neurons. For example, in lines from 106 to 119, SERT neurons are used. Previously, 5-HT neurons were used.

We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

(6) There are several points of confusion when referring to the figures, making the text difficult to follow because the text explains something that is not shown in the figure cited.

We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

Recommendations for the authors:

Reviewing Editor Comments:

Additional comments from the reviewers recommend that the authors increase sample sizes, carry out control experiments to exclude non-specific effects, and modify the title and abstract to reflect the minimal cross-talk observed between dopamine and serotonin. Finally, we note that the text of the manuscript does not meet minimum standards in the field for clarity, interpretability, or reproducibility.

We acquired a new experimental cohort, and performed additional experiments suggested by the reviewer. The manuscript has been revised and reformatted, incorporating all reviewer comments. We hope that this new version now meets the expected standards for clarity, interpretability, and reproducibility in the field.

Reviewer #1 (Recommendations for the authors):

(1) For angled stereotactic injections, the direction of the angle (ML, AP, etc) is not defined.

Added to the revised manuscript.

(2) The manuscript is full of grammatical errors and is very difficult to follow in some places, especially the results section for Figures 2 and 3. The following is an incomplete list of the most obvious errors to give examples of what I mean, but I strongly urge the authors to thoroughly revise the entire text.

(a) There appear to be photometry traces copied and pasted by mistake over the x-axis labels in the bar graph in Figure 1E.

(b) Line 41 states that fiber photometry recordings were used in reference 17, which is a human study that used voltammetry.

(c) Figures are referenced out of order throughout.

(d) Acronyms are used without being defined on the first usage.

(e) Lines 54-56, missing references.

(f) Line 82, the crosstalk reported in this paper is unidirectional, not bidirectional.

(g) Line 92 describes the virus as AAV-dLIGHTX.XX, where presumably the exes are placeholders for numbers that were never replaced.

(h) The text of the results section for Figure 2 in some cases directly contradicts the data it describes, and likely has some mistaken figure panel references.

(i) Line 123 is missing a reference and just has the placeholder REF.

(j) Lines 182-183 are a copy-paste mistake from lines 185-186.

(k) Scalebars in figure legends are in units of micromolar, not micrometers.

The manuscript has been extensively rewritten to address and incorporate the reviewers’ comments.

Reviewer #2 (Recommendations for the authors):

This is one of the least impressive and compelling manuscripts I have ever been asked to review. It reads in many ways like a first draft, not like a document that was meticulously prepared and proofread prior to submission. The data and analyses are shockingly light (with some conclusions supported by an N of 1 or 2) yet frustratingly difficult to interpret. The text and figures are full of typos, inconsistencies, and factual errors in interpretation. Most concerningly, this study does little to clarify the complicated relationship that exists between DA and 5-HT, including providing compelling evidence for their key finding of 'crosstalk' between both modulators or mechanistically implicating glutamate co-release. In fact, it might add to the noise. It is therefore unclear what the value is of this study in its current form.

We thank the reviewer for their detailed and thorough comments, which we saw as an opportunity to substantially improve the manuscript. We have therefore undertaken a comprehensive revision to improve clarity, coherence, and overall quality. As part of these revisions, we have removed the original Figure 3 presenting the in vitro patch-clamp electrophysiology data. We hope that the extensive changes implemented in the revised manuscript adequately address the reviewer’s concerns and significantly strengthen the study.

General comments:

(1) Limited scope: the design of the experiments performed offers very few opportunities for identifying 'crosstalk' between DA and 5-HT:

(a) To most, such cross-talk might best be imagined at the level of cells expressing receptors for both modulators, yet this is not studied. Cross-talk may also manifest in complex circuit-level interactions, downstream of brain areas directly targeted by DA and 5-HT. This is not studied either. Instead, only one type of experiment is performed: optogenetically stimulating cell bodies in the midbrain while monitoring DA/5-HT levels in the striatum. Opportunities for 'cross-talk' in this preparation are exceedingly limited. For example, the only way that optogenetically-evoked DA release may impact 5-HT levels (assuming classical, direct projections from DA neurons to the striatum) is via presynaptic modulation of 5-HT release from axons. Though potentially interesting, it is not exhaustive.

We agree that many types of crosstalk can be investigated; however, we chose to first adopt a broader approach that integrates neuronal circuit-level mechanisms. We believe that an important discrepancy remains in the literature that needs to be addressed. While our findings do not exclude the involvement of other forms of crosstalk, they aim to clarify whether crosstalk already exists at the level of neuronal circuits, which our results support.

(b) Any negative modulation of DA or 5-HT release would require a baseline tone of either modulator within the dynamic range of the sensor, which is not demonstrated. Thus, in both cases, a negative influence cannot be excluded, limiting any finding to 'positive' modulation. This is problematic for a study set on setting the record straight on 'cross-talk' between DA and 5-HT, given that prior studies pointed to antagonistic influences.

Previous studies using the same type of sensor have already demonstrated inhibitory crosstalk. For example, the study “Opponent Control of Reinforcement by Striatal Dopamine and Serotonin” successfully used this approach to reveal opposing interactions between dopaminergic and serotonergic signalling. Therefore, our findings are consistent with the possibility of circuit-level crosstalk and further contribute to resolving this ongoing question.

(c) Only one stimulation paradigm is tested, and its biological (ir)relevance is not discussed.

The stimulation paradigm used in this study has been extensively validated in multiple publications from our laboratory and has consistently been shown to promote reinforcement. Our recent review provides a comprehensive overview of this approach and its established behavioral effects. (Lüscher et al, Neuron, 2026, PMID: 42462721).

(d) Only one brain region is investigated (striatum), with little justification for omitting other regions where both modulators coexist (e.g., amygdala, cortex, DRN).

Not all brain structures can be investigated within the scope of a single study, and we acknowledge this limitation in the Discussion section.

(e) The suitability of the chosen behavior and cocaine administration to reveal interactions is not mentioned.

We have now clarified the use of i.p. cocaine injection to study the different temporal dynamics of 5-HT and DA release.

(2) Scarcity of data and questionable analyses and interpretation:

We thank the reviewer for the detailed comments listed below (a-m). In response, we repeated many experiments, increased sample sizes, completed the experimental groups, fully reanalysed the dataset, and removed the patch-clamp electrophysiology data. The manuscript has been extensively rewritten and reformatted based on a largely new dataset. In addition, we now focus specifically on one form of crosstalk and have expanded the discussion to address other potential mechanisms, as suggested by the reviewer. We hope this revised version adequately addresses the concerns raised. Because of the many changes in the text, the concerns listed below were addressed.

(a) Conclusions for Figures 3B and C are based on a N of 1 whole cell recording each.

(b) The relevance of data in Figures 3D and 3E to test the proposed hypothesis is unclear.

(c) Figure 2F is an average of N=2 recordings.

(d) Lines 98-100: Concluding statement not supported by experiment performed.

(e) Apparent contraction: Lines 112-113 indicate that 5-HT neuron stimulation failed to evoke 'any significant change in DA', while lines 117-118 talk about a small but significant increase in DA in response to the same manipulation.

(f) Line 114: conclusion not supported by data; Figure 2E points to DA, not 5-HT, and Figure 2F-H only shows 5-HT in DS, not NAc. Legend specifies that only 2 recordings are averaged in Figure 2F, and n=4 are quantified in Figures G and H, despite the plot containing 5 data points. What is going on?

(g) The key finding of this study is a transient, barely-detectable increase in NAc DA for ~1s during the 10s stimulation of 5-HT neurons in N=4 mice (Figure 2D). It is not clear if a significant increase was observed in all mice tested, or if this increase is significantly different from what is seen in DS. Was this effect seen in multiple testing sessions?

(h) Concerningly, the authors do not exclude the possibility of a 'startle' response to strong light delivery in mice expressing tdTomato-only. This is an essential control that is missing.

(i) Very few details regarding this DA response are offered. How soon does it appear following DRN stimulation? If mediated by glutamate co-release, it ought to appear with the very first light stimulus.

(j) The physiological significance of this stimulation paradigm is not established. Comparing it to cocaine-evoked DA release is not satisfactory, as cocaine elevates DA beyond levels encountered physiologically.

(k) Correlative evidence to implicate glutamate is insufficient. Does co-release depress when driven with the same stimulus train as that applied in vivo? Is it strong enough to drive DA neuron firing? Does it not affect DS-projecting DA neurons? Does this DA 'blip' disappear in mice genetically deficient in glutamate co-release (using SERT-Cre vglut2-floxed mice, which are commercially available)?

(l) The authors don't find evidence for DA stimulation affecting 5-HT release in the striatum. Is this sufficient to exclude any influence of DA on 5-HT? Isn't the fact that cocaine evokes 5-HT release evidence of an interaction? As such, it is unclear if the experiments performed significantly advance our understanding of whether and how DA and 5-HT influence one another.

We respectfully disagree with this statement. Cocaine directly binds to the serotonin transporter (SERT), thereby blocking serotonin reuptake into the presynaptic terminal and increasing extracellular 5-HT levels in the synaptic cleft. Furthermore, dopamine and serotonin release exhibit distinct temporal dynamics, suggesting that their release is mediated through different molecular mechanisms and neural circuit pathways rather than through a single shared process.

(m) The evidence that 5-HT stimulation alters DA release in the striatum is not compelling, but also not sufficient to exclude or support cross-talk between both modulators. The evidence provided is simply insufficient to strongly validate or challenge earlier studies.

(3) Minor:

In this revised manuscript, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised. We believe that this revised version addresses a significant proportion of the reviewers’ concerns and hope that these fundamental improvements are fully recognized during the evaluation.

Because of the many changes in the revised manuscript, the concerns listed below do no longer apply or were addressed.

(a) In the intro paragraph, line 19, specify that you are monitoring DA/5-HT in the striatum of mice.

(b) In the results section, indicate the preparation: in vivo, awake, what were the mice doing...

(c) Inconsistent nomenclature: VTA dopamine neurons are referred to as 'VTA DA', while dorsal raphe serotonergic neurons are referred to as 'DRN SERT' or 'DR SERT'. Why the difference? Is there any reason to believe that SERT-Cre mice label non-serotonergic neurons? Please adopt a consistent nomenclature and/or justify your choice. Also, if neurons are optogenetically stimulated, specify the word 'neuron' (e.g., line 118 refers to 'DR SERT stimulation', which could be interpreted to suggest the transporter is being activated).

(d) Line 103 and elsewhere: Confusing terminology referring to VTA DA neurons stimulation as 'modulating' or 'altering' DA release in the striatum. Isn't it directly evoked by the stimulation of DA-releasing neurons? Please change the terminology so as not to make it unnecessarily vague.

(e) Lines 111-112: comparison between DA and 5-HT fluorescence devoid of biological meaning. Relative increases in the fluorescence of 2 sensors that are molecularly distinct and separately-expressed in different cohorts of mice cannot be meaningfully compared.

(f) The timeline in Figure 1A suggests that the optogenetic stimulation protocol is initiated 5 min prior to cocaine injection. Figure 1D (right) plots this 5 min baseline, yet little/no DA release can be seen, despite Figure 1F indicating peak DA ratios of 0.5-1. Please explain. Since both sets of recordings were performed back to back and are directly compared, make sure to show them both on the same graph for direct comparison.

(g) Figure 1E contains 2 misplaced data traces.

(h) Figure 2D. Please repeat for the full stimulation window, not just for the few seconds where a tiny change in DA is seen.

(i) Figure 2E is misleading. It suggests that the peak extracellular DA concentration in NAC following DRN stimulation is approximately half of what cocaine evokes and similar to what VTA DA stim evokes (Figure 1F). But this is simply not true. There must be an error in calculation, and one should wait more than 20 minutes to properly estimate peak DA concentration in cocaine.

(j) What is the value of comparing optogenetically-evoked neuromodulator release to cocaine-evoked release? Can the authors be sure that the DA levels reached in cocaine are not saturating the DA sensor? Wouldn't this be required to permit comparison?

(k) Line 123: Please include a citation. Rephrase the sentence to avoid sounding dismissive.

(l) Line 124: Vague/confusing sentence. What is meant by 'optogenetic projection targeting' and 'parsing the synaptic currents in identified regions'?

(m) Figures 1D, 1G, 2C, 2F: confirm y-axis unit of measure. Are DA transients really only 0.2% in amplitude?

(n) Figure 3B, 3C: number of recordings performed in DA and NAcSh, anterior not specified. Only one trace showed, and no summary plot. Insufficient data presented to draw conclusion.

(o) How does the presence of EPSCs in OFC or NAc help support the author's finding of a brief elevation of DA upon DRN stimulation?

(p) Line 358: Wrong unit.

Reviewer #3 (Recommendations for the authors):

Some minor concerns are the following:

(1) In line 31, define what DS is.

(2) In line 57, the word "neurons" is missing in the phrase ".....decreases 5-HT neuron spontaneous firing in DRN,...".

(3) In line 111, the comparison needs to be between 5-HT release due to optogenetic stimulation with the 5-HT release due to cocaine infusion, not with DA release due to cocaine infusion.

(4) In line 112, it should be Figure 2F.

(5) In line 114, instead of 5-HT, it should be DA. In addition, it is not Figure 2E, but 2C.

(6) In line 123, add the appropriate reference instead of "REF".

(7) In lines 182 and 183, the text is out of context.

(8) In lines 250 - 251, the text is out of context.

(9) Why was Rabit anti-GFP if you do not use GFP in the procedures?

While the manuscript underwent a complete comprehensive revision to improve clarity, coherence, and overall quality, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised.