Dysfunction of ventrolateral striatal dopamine receptor type 2-expressing medium spiny neurons impairs instrumental motivation

Impaired motivation is present in a variety of neurological disorders, suggesting that decreased motivation is caused by broad dysfunction of the nervous system across a variety of circuits. Based on evidence that impaired motivation is a major symptom in the early stages of Huntington's disease, when dopamine receptor type 2-expressing striatal medium spiny neurons (D2-MSNs) are particularly affected, we hypothesize that degeneration of these neurons would be a key node regulating motivational status. Using a progressive, time-controllable, diphtheria toxin-mediated cell ablation/dysfunction technique, we find that loss-of-function of D2-MSNs within ventrolateral striatum (VLS) is sufficient to reduce goal-directed behaviours without impairing reward preference or spontaneous behaviour. Moreover, optogenetic inhibition and ablation of VLS D2-MSNs causes, respectively, transient and chronic reductions of goal-directed behaviours. Our data demonstrate that the circuitry containing VLS D2-MSNs control motivated behaviours and that VLS D2-MSN loss-of-function is a possible cause of motivation deficits in neurodegenerative diseases.

neurons are hypofunctioning in DOX-off day 7 mice. However, they are recording VP neurons that receive input from hundreds of MSNs. Therefore, it seems equally likely that the DTA-exposed but living D2R-expressing neurons are in fact normal, but there are just fewer of them due to the ablation, hence the weaker inhibitory responses in the VP. I don't see how the authors can dissociate these points via in vivo recordings. To properly evaluate these possibilities the authors should use slice recordings from D2R expressing MSNs. However, I also don't think it's critical to their conclusions that the remaining neurons are hypo-functioning, so they could remain agnostic on this point and report both possibilities.
3. The classification of Phases I, II, and III in the 5-CSRTT seems arbitrary, with each phase containing a different number of days in a way that appears to allow Phase II to capture the days when the data appeared significant. Was a rationale approach used to define these phases that I'm just missing? If not, it would be more appropriate to report which specific days were significant, controlling for multiple comparisons with a Benjamini-Hochberg False Discovery Rate that will protect against false negatives due to the high number of comparisons.
4. The optogenetic ablation experiment is extremely interesting, and a potentially novel and useful application of optogenetics. However, I am not convinced they achieved ablation from the data they report. They show loss of GFP, microglial activation and reductions in D2R mRNA, none of which is directly linked to cell death. I'd be more convinced by NeuN staining showing fewer living neuronal nuclei, or another stain that specifically evaluates cell death.
Minor comments: 1. In several places the authors include discussion and interpretation within the results, and at times I felt it was too much. Most notably, when discussing emotional regulation and anhedonia . While this interpretation is interesting, it should be moved to the discussion due to its speculative nature.
2. Certain behavioral details were missing. In particular, the time of day when experiments were run was not given, and is important given the food-based operant responding that was used as an assay of motivation. In addition, it is unclear whether the mice undergoing the various behavioral tasks in Figure 4 are the same mice or different mice.
3. In Figure 1 the authors show data ruling out non-specific toxicity on ChAT neurons and dopaminergic neurons, but put the data on D1R-expressing neurons into supplemental figure 2. I would put this in the main figure, as it argues against a non-specific toxicity that is difficult to evaluate from ChaT and dopamine neurons. 4. Figure 2 shows methods that could be placed in a supplemental figure.
Reviewer #3 (Remarks to the Author): In this paper, the authors characterized the functional role of ventrolateral striatal D2 receptorexpressing neurons in goal-directed behavior, and argue that ablation of this specific population of neurons results in an increase in apathy. They generated a new D2-tTA line, which they crossed with a tetO-DTA line, and used this line to show that a progressive destruction of D2 neurons (spreading from ventrolateral striatum to more dorsal regions of the striatum) differentially affects motivated behavior depending on the amount of destruction. Early timepoints following DOX removal (ventrolateral striatum damage) result in an apathetic-like phenotype in goal directed behavior (3 choice serial reaction time task and progressive ratio task). Later timepoints following DOX removal (ventral and some dorsal striatal damage) result in an inability to withhold responding (premature response in the 3 choice serial reaction time task) and an increase in locomotor activity in the open field task. Last, optogenetic inhibition and ablation of ventrolateral striatal D2 neurons leads to deficits in the progressive ratio task. The study is interesting, well controlled, and well written. I have some specific suggestions for improvement: The authors have generated a new mouse line with tTA targeted to D2 neurons. They have characterized this line by crossing it with a tetO-ChR2 line, but the supplementary figures depicting this characterization are currently somewhat unclear. Could the authors provide quantification of both specificity and penetrance in D2 neurons? It is unclear which is depicted.
The central hypothesis is that loss of D2 neurons in ventrolateral striatum leads to apathy (e.g. Fig 4b,  Fig 5b) while the spread of this loss to more dorsal regions of the striatum leads to deficits in inhibiting movements (e.g. Fig 2b, Fig S3). The authors have demonstrated that optogenetic inhibition of D2 neurons in the VLS leads to a reduction in breakpoint in the progressive ratio task. It would be helpful to bolster this claim by optogenetically inhibiting D2 neurons in more dorsal regions to demonstrate (for example) increased premature responding.
The authors have a bigenic D2-tTA::tetO-ChR2 mouse in their lab. What are the effects of optogenetic activation of D2 neurons in ventrolateral and more dorsal striatum?
There are D2-expressing neurons in the cortex, in particular layer 5 neurons in the medial prefrontal cortex. Dopamine in this region is hypothesized to play a role in apathy. It would be straightforward for the authors to provide an anatomical characterization of DTA mRNA and the loss (or not) of D2 neurons in this region as a time series following DOX off as in Figure 1.

Reviewer #4 (Remarks to the Author):
This paper examines the effect of a conditional ablation of D2-MSNs in the ventral striatum on behaviour. They find significant loss of D2 mRNA in the ventral striatum after 10 days of removal of the tet suppression of DtA. They observe a lasting increase in locomotor activity, decrease in effortbased instrumental action, increase in impulsivity and compulsivity and a transient effect on cognition in a 3CSRTT. I think they have developed a very interesting model and their data supports some experimental findings that are previously published. For example, decreased D2 receptor predict increased trait impulsivity (Dalley et al., 2007 Science), Activation of D2 receptor expression induces bradykinesia (Kravitz et al., 2010 Nature), where as deletion of D2 in iMSNs induces hyperlocomotor activity, deficits in spontaneous movement and motor skill performance (Lemos et al., 2016 Neuron). Further viral knockdown of D2Rs increases reward threshold on intra cranial self stimulation (Johnson et al 2010, Nat Neurosci.). Here, they characterize a novel method of conditionally knocking down MSNs expressing D2 receptors in the ventral striatum and attempt bring together some of these ideas in a cohesive hypothesis. However, some of their interpretations may have alternate explanations.
First, the authors propose that ablation of iMSN D2 receptors in the Ventral striatum induces apathy or a state of amotivation. The evidence they sue to support this is that they see a reduction in goal directed behaviour though a decrease in trials and increase in omissions observed 6-7 days after removal of the tet suppression. Similarly the impairment in effort-based instrumental responding (PR) occurred within 3-4 days after removal of tet suppression. At this timepoitn they see expression of DTA mRNA, but no alterations in Drd2 mRNA expression until later (after day 10 of tet off). These timepoints of the behavioral alterations fit within the timeframe of an immunological response (activated microglia), but not necessarily within the timeframe of Drd2 loss. Therefore, I would interpret their alterations in motivated/goal-directed behaviour would be likely due to an inflammatory response rather than loss of D2 receptors.
The behavioural data that fits best with the timeframe of loss of D2 receptors is the increased impulsivity and compulsivity on the 3CSRRT (in the supplemental) along with the alterations in locomotor activity. This also supports previous reports of hyperlocomotor activity (Lemos et al., 2016) and increased impulsivity (Dalley et al., 2007) with loss of D2Rs. However, this does not support their hypothesis that decreased D2Rs result in apathy.
If I understand this experiment correctly, to obtain D2-ArchT biogenic mice, they presumably crossed Drd2-tTA mice with TetO-ArchT-EGFP mice (Additional information on this should be in the methods rather than just a reference to the orexin/hypocretin paper in the results). However, I am unclear how this strategy targets ArchT-EGFP only to the D2R expressed in MSNs and not to all DR2 expressing cells. They indicate that they observed little ArchT-EGFP fluorescence in the VTA dopamine neurons. However, this does not exclude the D2 receptors expressed on glutamatergic inputs or cholinergic inputs to MSNs in the ventral striatum. Presumably inhibition (or light-induced ablation) of these D2expressing inputs would alter goal-directed behaviour. Can they demonstrate (or further explain) how this targets only MSN D2 receptors? Furthermore, could their 3h photostimulation to ablate the D2 expressing cells result in changes in neuroinflammation? Line 304 -they are not really looking at reward value, rather reward preference Fig S3c -for sensitization they need to test if locomotor activity on day 5 is greater than that on Day in both groups. We would like to thank the reviewers for their careful reading of our manuscript and their thoughtful comments. Their suggestions are greatly appreciated and nearly all of them have been incorporated into the revised manuscript. Please find our point-by-point responses to the reviewers below.
The reviewers' comments are numbered, underlined, and in italics. Our revised sentences are in the bold face.

Reviewer #1
Comment #1. The title of the study refers to "ventrolateral striatum". However the ablation mainly affects the ventral striatum (nucleus accumbens) and the dorsomedial striatum, not the dorsolateral. This should be revised in the title and throughout the study.
It is true that DTA-mediated cell dysfunction/ablation area covered the ventral striatum and the dorsomedial striatum eventually. However, our experiments were designed to elucidate the effects of D2-MSNs ablation in the "ventrolateral striatum". We believe the DOX-off and re-start regimen enabled us to (temporarily) confine the cell dysfunction area within the VLS (Fig. 5).
We would like to use the term "ventrolateral" instead of "nucleus accumbens" because DTA-mediated cell dysfunction area was not limited to the rostral part of the striatum (probably including the lateral part of the accumbens core and lateral shell) but located from the rostral to the caudal part of the striatum ( Fig. 2A).
According to above two reasons, we believe (and hope the reviewer agrees) that the term "ventrolateral striatum" more accurately depicts the region related to the main topic of this study. We agree with reviewer's comment. The reviewer is concerned whether Drd2-mRNA positive cholinergic interneurons expressed DTA in D2-DTA mice. To solve this concern, we added the data with double fluorescent in situ hybridization for ChAT (the We examined ArchT-EGFP expression in MSNs in the striatum and found that D2-MSNs specific EGFP expression. We provided the information regarding ArchT-EGFP expression of the cholinergic interneuron and the MSNs in Supplemental Figure S5 and Table S1.
We added the following sentences to describe ArchT-EGFP specific expression in the D2-MSNs in the result section.

Page 8 line 33:
Drd2-positive cholinergic interneurons were not labeled with GFP ( Figure S5C). The pyramidal neurons are known to express Drd2 mRNA, and their axon terminals project to the striatum; however, neurons in the medial prefrontal cortex and IC were not labeled with GFP ( Figure S5E). Together with these data, ArchT expression within the striatum was specific to the D2-MSNs (Table S1). Fig. 1G shows in situ for ChAT and Drd2 (not D2R, please fix) mRNA but it seems like they do not correspond to same section and thus colocalization can be not quantified. It is important to add the quantification of the colocalization experiments between ChAT and DTA mRNA as it will strengthen the evidence that the interneurons are spare in this manipulation.

Comment #3. On this same issue,
We displayed the confocal images in the previous Fig. 1G (now Figures 1H and 1I). To clarify this, we added the method information in the Figures 1H and 1I legends in our revised manuscript (page 28, line 35, and page 29, line 3).
We conducted double fluorescent in situ hybridization for ChAT and DTA mRNA at DOX off day 10 and found that none of ChAT positive cells expressed DTA mRNA (please see comment #1). We described this histological data in the result section (page 4, line 25) and added the quantification in Figure 1I legend (page 29, line 4).

Comment #4. Also, the current quantification corresponds to density of
ChAT-positive neurons. Please express the density of neurons as cell/area of tissue, not per section as it can vary from section to section.
We described the density of ChAT-positive neurons as cell/area in our revised manuscript ( Figure 1G) as follows. According to reviewer's advice, we conducted electrophysiological analysis by using D2-DTA with DOX on regimen and obtained comparable data with previous experiment using WT mice. We replaced the data in our revised manuscript (Figure 3 and Table 1).
The recording sites were reconstructed in all cases by the probe track, which was visualized with DiI. The depth of the recorded neurons was evaluated with the distance from the dura. Responsive neurons were found in the same region, and each response pattern was randomly obtained in the VP of ON, OFF7 and OFF20. We included the random distribution of responded neurons in the method section as follows. Although the precise mechanism is unknown, this result is consistent with the previous report with immunotoxin-mediated D2-MSNs ablation study (Sano et al., 2013, ref 35).
We now include this information in the method section. As the reviewer pointed out, the ratio of eex-inh pattern at OFF20 increased compared with that at OFF7 although the degree of MSN dysfunction was comparable. One plausible explanation is that D1-MSNs in the VLS-VP pathway compensate the inhibition at OFF20. However, this explanation does not account for the same response patterns including late excitation (eex-inh-lex and eex-lex), which corresponds to VLS-VP-STN-VP pathway.
It is difficult to solve this specific concern (why does the frequency of eex-inh pattern goes up with the treatment?), but we believe that we convince the readers that DOX-off treatment (both OFF7 and OFF20) resulted in the decreased responses containing inhibition phase according to this population histogram.
Regarding the behavioral consequence at OFF20, the effects from extended area (VMS and DMS) should be added to that from the VLS. Thus it is difficult to address the later concern (this increase inhibition from VLS could also account for the behavioral changes observed or lack of). Please consider these limitations. To clarify what GFP positive cells were in the midbrain, we conducted a double immunohistochemistry with GFP and TH (the marker of dopamine neurons) (2 D2-ArchT mice, 4 sections). We found that GFP-immunopositive midbrain neurons were TH-positive dopamine neurons in the VTA; 90% of GFP-positive cells (n= 7.0 ± 2.3) were labeled with TH and 7% of TH-positive cells (n=76.8 ± 8.6) were labeled with GFP. We added these in Supplemental Figure S5C.
Regarding the assumption of ArchT functional expression in DA neurons, we rephrased the term per the reviewer's comment.

Before:
Immunohistochemistry detected a few GFP-positive cells at dopamine neurons, however, the level of GFP was too low to observe direct fluorescence (data not shown), indicating that optogenetic inhibition should not work in dopamine neurons due to the low level of ArchT expression.
After (page 8, line 30): Immunohistochemistry detected a few GFP-positive dopamine neurons (Supplementary Figure S5C), however, the level of GFP was too low to observe direct fluorescence (data not shown), suggesting that optogenetic inhibition should not work in dopamine neurons due to the low level of ArchT expression. Comment #9. The authors used the term bigenic and monogenic. Are they referring to homozygote and heterozygote? Is there a good reason why not to use those terms?
The Tet system is a bipartite system; the system requires two distinct lines, tTA and tetO lines. Therefore, the researchers use bigenic (double transgenic) and monogenic (single transgenic) instead of hetero-and homozygote.

Comment #10. Please add a reference for the statement of long-term ArchT activation leading to cell death.
To our knowledge, there is no previous report describing the opto-ablation. Fig S4 to  We moved the data to Figure 5F as the reviewer suggested. We examined the differences of the Drd2 mRNA expression level within the striatum by in situ hybridization. ISH is not a qualitative method, however, it can qualitatively address mRNA level in the single cell level. Especially, at the beginning of the color development, cells with higher mRNA were labeled weakly and those with lower mRNA was not. As shown in below pictures (a: low magnification, Drd2 ISH, 30 min development, without nuclear fast red stain, b: dorsolateral, c: ventrolateral), there was no regional difference of Drd2 mRNA level. We think that the regional difference of Drd2 mRNA level is unlikely the cause of the preferential targeting of VLS in our system.

Reviewer #2
Comment #1. I did not find the description of their behavioral effects as "apathy" helpful. Apathy is a conscious state in humans that seems very difficult to model in mice. More commonly, the behaviors they tested are described as tests of "motivation", and defined operationally. Is there a reason why the author's don't see their experiments as testing motivation?
We realize that modeling apathy in animals is controversial, however, we continue to feel that our use of the term is justified. First, our finding that striatal neurons mediate decreased motivation in mice is true. The etiology (striatal lesion) and resultant decreased motivation provide construct and face validity for a model of human apathy.
Second, apathy is a pervasive clinical phenomenon that deserves more attention at the translational and pre-clinical levels. Our hope is that our findings will help generate interest in understanding how animal studies of motivation can shed light on the human phenomenon. We would be very happy if reviewer #2 can now accept our link between apathy and decreased motivation in mice. Figure 3 conclude that remaining living D2R-expressing neurons are hypofunctioning in DOX-off day 7 mice. However, they are recording VP neurons that receive input from hundreds of MSNs. Therefore, it seems equally likely that the DTA-exposed but living The reviewer raised possibility that the net effect observed in the electrophysiology in early time points of DOX off regimen (e.g. DOX off days 7) was mediated via cell ablation (dead cells). However, we did not detect any dead cells in the VLS at DOX off days 7 ( Figure 1F), indicating that the net effect was unlikely to be mediated via dead cells. We think that it is reasonable to interpret that altered in vivo electrophysiology results was mediated via hypofunctioning viable DTA-exposed cells.

Comment #2. The electrophysiological experiments in
To clarify that D2-MSNs did not die at this time point, we added the phrase as follows.
Page 5, line 13: Our histological analysis revealed that cell death and apparent loss of Drd2 mRNA occurred after DOX-off day 10. However, prior to cell death, DTA mRNA was expressed at earlier times (DOX off for 3-7 days) ( Figures 1B and 1F). As the reviewer #2 pointed out, we did not clearly explain the rationale of our classification. We classified the periods based on the results of histological analysis: the phase before loss-of-function manipulation is classified as Phase I, the phase from the timing of DTA mRNA appearance in the VLS (DOX off days 3) to the timing of cell death appearance (DOX off days 10) as Phase II, and the phase after the cell death expansion to the whole VS (DOX off days 14～) as Phase III.
After (page 6, line 25): Following DOX-off conditions for 3 days, D2-DTA bigenic mice displayed a decreased total number of trials in 60 min of testing (phase from days 3 to 10: F 2, 15 = 9.102, P = 0.004; phase × group interaction: F 2, 20 = 4.832, P = 0.022, Figure 4B) compared to monogenic controls (total trial: t 10 = 2.422, P = 0.045, Figure 4B). D2-DTA bigenic mice at DOX off day 10 showed normal locomotor activity (Figure 2A We also re-analyzed the behavioral data of PR experiment in accordance with the new classification ( Figure 5) and obtained similar results as previous. We revised the result section as follows.
Page 7, line 30: D2-DTA bigenic mice started to display a behavioral reduction after DOX was off for 3 days and this reduction further deteriorated day-by-day according to decreased break points (phase × group interaction: F 2, 40 = 5.782, P = 0.021, Figure 5B) and prolonged time spent to complete the PR task (phase × group interaction: F 2, 40 = 7.344, P = 0.003, Figure 5C). These observations were not evident in controls (break point: t 20 = 13.211, P = 0.005, time spent to complete the PR: t 20 = 15.899, P = 0.002, Figures 5B and 5C).
After the DOX restart, the behavioral reduction remained (break point, post hoc analysis between groups at phase III: t 20 = 17.377, P = 0.004, Figure 5B; time spent to complete the PR, post hoc analysis between groups at phase III: t 20 = 21.093, P = 0.002, Figure   5C). Associative learning and appetite were unaffected ( Figures 5D and 5E) as seen in the 3-CSRTT ( Figures 4D and 4E), suggesting that cognitive and emotional dimensions were spared. fiber. We believe that added data solve the reviewer's concern. We added this data in Supplemental Figure S6 and revised the sentence as follows.  Figure 6K and Figure S6).

Comment #5.
In several places the authors include discussion and interpretation within the results, and at times I felt it was too much. Most notably, when discussing emotional regulation and anhedonia . While this interpretation is interesting, it should be moved to the discussion due to its speculative nature.
Considering this comment and the comment from another reviewer (Reviewer #4, comment #5), we moved figures presenting emotional regulation and food preference/consumption (previous Figure 4F-H) to Supplemental Figure S3C-E.
According to the change, we removed the corresponding paragraph from the result, but we keep the data with food preference/intake in the result section because this data should be provided in food-incentive instrumental tasks. We have made a change as follows. Before: …… We included 3-CSRTT, EPM, FST, Food preference test, Food consumption test in previous Figure 4. Among these, we used three cohorts; 1) 3-CSRTT, 2) EPM and FST, 3) Food preference and Food consumption.
As the reviewer #4 recommended, we now move data of EPM, FST, Food preference test, and Food consumption test to supplementary Figure S3. We described the information if the same mice were used in the different tests (supplementary, page 14).
In relation to this comment, we realized that we did not describe the method for food preference/consumption tests. We now include it in supplementary page 14.
Comment #7. In Figure 1 the authors show data ruling out non-specific toxicity on ChAT neurons and dopaminergic neurons, but put the data on

D1R-expressing neurons into supplemental figure 2. I would put this in the main figure, as it argues against a non-specific toxicity that is difficult to evaluate from
ChaT and dopamine neurons.
We added the data showing that D1-MSNs were spared in D2-DTA mice in Figure 1K and added the description as follows: Page 4, line 29: The number of dopamine receptor type 1-expressing medium spiny neurons (D1-MSNs) in the VLS did not change after DOX removal ( Figure 1K).
Comment #8. Figure 2 shows methods that could be placed in a supplemental figure.
We would like to keep this figure in the main figure. It is very important information that the ablation in not limited to the rostral part, which is related to the reply to the comment #1 from the reviewer #1. We provide the supplementary table summarizing the specificity of tTA expression and the penetrance of tTA-mediated gene induction in both D2-DTA and D2-ArchT mice.

Reviewer
We believe that this table helps readers to understand Drd2-tTA mediated targeting.

Comment #2. The central hypothesis is that loss of D2 neurons in ventrolateral
striatum leads to apathy (e.g. Fig 4b, Fig 5b) while the spread of this loss to more dorsal regions of the striatum leads to deficits in inhibiting movements (e.g. Fig   2b, Fig S3).

The authors have demonstrated that optogenetic inhibition of D2 neurons in the VLS leads to a reduction in breakpoint in the progressive ratio task. It would be helpful to bolster this claim by optogenetically inhibiting D2
neurons in more dorsal regions to demonstrate (for example) increased premature responding.
We have data demonstraing that the dorsal D2-MSN-optogenetic inhibition resulted in an increase of locomotor activity (please see Figures A and B with legends below), which may account for the idea that the spreading of ablation to more dorsal regions leads to deficits in inhibiting movements. However, we do not want to include these data in revised manuscript because the expolaration of the striatal region involving the control of behavioral inhibition is not a major question, and the striatal encoding of such behavior would not be simple. We would like to emphase again that our major purpose is to demonstrate the role of VLS-D2-MSNs in motivated behaviors. We would like not to open these data to our revised manuscript because 1) optogenetics-mediated gain-of-function study does not directly supplement the answer to our main question, and 2) we plan to use these data in another paper describing the temporal activities of MSNs during motivated behavior. We hope the reviewer understand our intention. As we replied to the comment #1 from reviewer #3, we summarized the penetrance of DTA induction in D2-DTA mice in Table S1. We did not detect DTA mRNA in mPFC or IC (Figure S1F).
We revised the data as reviewer indicated ( Figure  Therefore, I would interpret their alterations in motivated/goal-directed behaviour would be likely due to an inflammatory response rather than loss of D2 receptors. As the reviewer #4 pointed out, "the impairment in effort-based instrumental responding (PR) occurred within 3-4 days after removal of tet suppression". In this time point, we did not observe activated microglia in the striatum (Fig. 1F), suggesting that alterations in motivated behavior would be unlikely due to an inflammatory response.
Around DOX-off days 7, we have to consider the inflammatory response as a confound factor. As we described in the 6 th paragraph of Discussion, we evaluated the effect of inflammatory response on motivated behaviors. To strengthen our evaluation, we added the data showing the alleviation of microglial activation after DOX-restart ( Figure S7). We would be happy if the reviewer #4 agreed with our thought.
Page 11, line 26 in the 6 th paragraph of Discussion: We also employed DOX-off and restart regimen ( Figure 5) in which only a subset of D2-MSNs was ablated and the resultant glial activation was alleviated ( Figure S7). It is natural that our data with cell dysfunction/ablation study does not fit previous reports with decreased D2 receptor expression.
If not the case, we need to explicitly describe that Drd2 mRNA disappearance coincided with DTA-mediated cell death. We revised the corresponding sentence as follows.
Page 4, line 21: In summary, DTA-expressing (DTA mRNA-positive) cells were viable for several days, and then cell death occurred (Drd2 mRNA signal disappearance coincided).

Comment #3. If I understand this experiment correctly, to obtain D2-ArchT biogenic mice, they presumably crossed Drd2-tTA mice with TetO-ArchT-EGFP mice (Additional information on this should be in the methods rather than just a reference to the orexin/hypocretin paper in the results).
As the reviewer expected, we obtained D2-ArchT mice with crossing D2-tTA mice and tetO-ArchT-EGFP mice. To clarify it, we added the term "bigenic" in the method and result sections as follows: Page 13, line 22 in the method section: Drd2-tTA::tetO-ArchT-EGFP bigenic mice were fed with normal chow (CE-2, CLEA).
Please also see our replies on the comment #2 from the reviewer #1 and the comment #1 from the reviewer #3.

Comment #5. Furthermore, could their 3h photostimulation to ablate the D2 expressing cells result in changes in neuroinflammation?
Immediately after opto-ablation of D2-MSNs, massive neuroinflammation occurred but the inflammation alleviated by the behavioral test. Please see our comment #1 and the 6 th paragraph of Discussion.

Comment #6. Fig S2c -numbers in the table are way too small to see
We revised the manuscript as the reviewer pointed out (Supplemental Figure S2C). We moved data in 4F, G, H to the supplemental (now Figure S4A-C). We would like not to combine Figs 3 and 4 because topics are different.

Comment #8. Line 304 -they are not really looking at reward value, rather reward preference
We rephrased it per the reviewer's comment (page 10, line 7).

Comment #9. Fig S3c -for sensitization they need to test if locomotor activity on day 5 is greater than that on Day in both groups.
We re-analyzed the MAP sensitization data. Two-way repeated ANOVA revealed that there was no Day × Group interaction (F 1, 21 =0.190, P=0.677). We then conducted One-way repeated ANOVA and detected main effects of Drug for control group (F 1, 21 =5.572, P<0.01) and for DOX off group (F 1, 21 =6.976, P<0.01). The multiple comparisons with Bonferroni method followed and revealed significant increases (P<0.05) of locomotor activity between Day 1 and Day 5 for both groups. We described these precise statistical results in our revised supplementary information (Figure S3F).
Comment #10. Fig. S4d. They should label the units for the preference score on the y axis.
The authors have done a decent job responding the questions and comments I had. The revised manuscript includes more controls and additional data that improves the manuscript and facilitate the interpretation of the results.
My only additional request is that the result section includes a brief statement defining the concept of the ventrolateral striatum to include the lateral part of the nucleus accumbens. Also, a mention that over time the manipulation also causes dell death in the ventral part of the dorsal striatum All other experiments and answers were already incorporated.
Reviewer #2 (Remarks to the Author): I thank the authors for their revisions. The new data showing cell death from the optical ablation is convincing.
With respect to my prior points, I'm still stuck on two: 1) The authors responded to my concern that cell death may be an equally viable explanation for their altered ephys responses at day 7 by referencing a schematic ( Figure 1F) saying there is no cell death at this point. Can they provide something quantitative on this point? Or write the section in a manner that leaves open this possibility? They conclude that "loss-of-function occurred prior to DTA-mediated cell death," but don't show evidence that there was no cell death at the time of their recordings.
2) I still cannot fully accept the rationale for using the term apathy, and found the authors use of this term at times speculative. For instance, the conclusion sentence of the abstract ends, "thus implicating this circuit in apathy associated with neurodegenerative diseases." No data in their study relates to neurodegenerative diseases, so this type of speculation seems out of place for a conclusion sentence.
In the introduction, the authors cite Levy and Dubois' definition of apathy as a "quantitative reduction of voluntary, goal-directed behaviors", which the authors suggest makes it amenable to study in animals. However, not all reductions in voluntary behavior in humans are caused by, or should be defined as, apathy. Levy and Dubois go on to note that the mechanisms underlying apathy have multiple emotional and psychological sources. I remain unconvinced that mice experience apathy, or that the behavioral tests in this study (which have a long history in the motivation literature) should be described as evidence of apathy.
However, to not get caught in semantics, I would suggest the authors change the term to "apathy-like behavior" and give some description of what exactly they mean by this (reductions in voluntary motor behavior?) if they are set on using this term. Either way, the speculation in the abstract should be kept to a minimum.
Reviewer #3 (Remarks to the Author): I thank the authors for their response, but note that some concerns were not fully addressed, detailed below: 1) The penetrance and specificity quantification data for the newly generated Drd2-tTA mouse are still lacking, and are required to interpret these results. Figure S1C is unclear: is this specificity (% of YFP cells that express Drd1 or Drd2) or penetrance (% of Drd1 or Drd2 cells that express YFP)? Both quantities should be depicted. If the presented data is, in fact, specificity, 60% is lower than what is usually accepted for genetic targeting -90% is a typical minimum percentage. What is the identity of the other 40% of cells, and how do you know they are not responsible for the behavioral effect? The same holds true for Figure S5B.
2) Figure S1F is not sufficiently high resolution to determine whether or not there is DTA mRNA in mPFC or IC. This is a critical question, since the majority of the work in this paper relies on a transgenic approach rather than a spatially restricted viral vector approach. If it is to be believed that the degeneration of VLS D2 neurons leads to apathy, it needs to be shown that D2 neurons elsewhere in the brain are intact. Therefore, it is absolutely essential that 1) the authors provide high-resolution images of mPFC and IC with Drd2 neurons clearly labeled; 2) the authors show, quantitatively, that there has not been a reduction in this population after DOX-off at several time points up to 20 days; and 3) there is no DTA mRNA in mPFC or IC when assayed at high resolution. Even this is not ideal -D2 neurons elsewhere in the brain could still be mediating the effect (hippocampus, other cortical areas, etc). The cleanest approach would be to use a cre-dependent DTA vector (which exists) in a Drd2-cre mouse -this would control for expression everywhere else in the brain. It is difficult to accept a unique role for VLS in apathy without specifically demonstrating that the approach used in this paper does not affect the activity of ALL other Drd2 cell groups.
3) The authors use a brief 2-second inhibition that starts when the lever is presented, but this inhibition is temporally dissociated from the time during which the behavior is modified. This raises some questions that need to be answered. a) First, and most important: it is known that periods of optogenetic inhibition can be followed by rebound excitation, and the amount and duration of this rebound excitation may depend on cell type. The authors have shown that a brief 100 ms pulse in a whole cell voltage recording leads to transient inhibition, but they have not demonstrated the effect of this 2-second inhibition on cellular physiology in vivo. It is entirely possible that the net effect of this manipulation is enhanced excitability during the bulk of the progressive ratio task, which would muddle the relatively straightforward interpretation presented here.
b) Is there something special about 2 seconds that leads to this behavioral effect? The more obvious experiment would be to turn the laser on at lever presentation and turn it off when the animal has successfully pressed the lever the last time for that trial, or after 5 minutes has passed with no lever press. The results of this kind of experiment would be far easier and more straightforward to interpret, and would be a direct demonstration of the critical role for this cell population in apathy.

Reviewer #4 (Remarks to the Author):
Apathy is lack of interest or lack of an emotional state. In this paper they really did not explore if the mice experienced a lack of emotional state or an indifference to stimuli of positive or negative valence, they only assessed performance on behavioral tasks addressing cognitive responses (attention, impulsive action) and motivation. While lack of self-generated motivational behaviour is a symptom of apathy, they really don't assess whether there is emotional blunting in these animals. On the tasks that they did perform, ie forced swim test and elevated plus-maze, there was not difference in performance between genotypes. The references they offer to support that their definition is 'well accepted' are studies of human Parkinson's patients that also experience pour verbal memory, emotional blunting, less interest in social activities etc. Furthermore some of their results do not necessarily fit with their definition of apathy (ie increased impulsive action and preservative responding). Therefore, I tend to agree with Reviewer 2 on this point that apathy is a human condition -and if it was possible to model it in mice, they have not done it well here. I am saddened by this current push in today's science to spin results into an anthropomorphic framework for the sake of snappy headlines (ie mice experience loneliness, etc).
With this stated, I think the results of this study are interesting in that they provide a new experimental model testing the contribution of VLS D2-MSNs in behaviour, rigorous, and well controlled and should be published in this journal. However, I really think the 'spin' on apathy is not necessary. I think that it is important that they keep these finding within the context of rodent behaviour. Perhaps in the last paragraph of the discussion they could speculate that these results may fit with certain symptoms of a clinical definition for human apathy, but I really think it is a stretch for the whole paper (introduction and discussion) to be framed around this concept.
My other previous concerns have been addressed.
Below we describe our point-by-point responses to the latest reviewer concerns. The current reviewer comments are shown in italic, and our new responses are shown in blue (our previous responses are shown in regular black text). Revisions in the main text are shown in red.

Reviewer 1
My only additional request is that the result section includes a brief statement defining the concept of the ventrolateral striatum to include the lateral part of the nucleus accumbens.
We added the description that VLS includes the lateral part of the nucleus accumbens.
Page 4, line 35 DTA mRNA expression initiated in the VLS was not limited to the rostral part of the striatum, which included the lateral part of the nucleus accumbens, but spread from the rostral to the caudal part of the striatum

Also, a mention that over time the manipulation also causes cell death in the ventral part of the dorsal striatum
We mentioned above in page 4 line 17 in the previous version: Drd2 mRNA-negative areas had expanded concentrically by DOX-off day 14 (VLS, ventromedial striatum [VMS], and ventral part of the dorsomedial striatum) (Figures 1C,  1D, and S2) when numerous dead cells were detected.
Reviewer 2 1) The authors responded to my concern that cell death may be an equally viable explanation for their altered ephys responses at day 7 by referencing a schematic ( Figure 1F)  Please see attached figures labeling ssDNA (cell death marker). We did not detect ssDNA-positive cells in the VLS at DOX-off days 7 (n=3 brains).
We just add the phrases in the main text. Before: The number of DTA mRNA-positive cells was increased at DOX-off day 7, but with no apparent loss of Drd2 mRNA signal in the corresponding region.
After revision (page 4, line 13): The number of DTA mRNA-positive cells was increased at DOX-off day 7, but with no apparent loss of Drd2 mRNA signal and with no cell death in the corresponding region.
2) I still cannot fully accept the rationale for using the term apathy, and found the authors use of this term at times speculative. For instance, the conclusion sentence of the abstract ends, "thus implicating this circuit in apathy associated with neurodegenerative diseases." No data in their study relates to neurodegenerative diseases, so this type of speculation seems out of place for a conclusion sentence. We agree with your concern. We remove the term apathy from the title. We carefully edit the abstract, the introduction, and the last paragraph of the discussion.
Reviewer 3 1) The penetrance and specificity quantification data for the newly generated Drd2-tTA mouse are still lacking, and are required to interpret these results. Figure S1C is unclear: is this specificity (% of YFP cells that express Drd1 or Drd2) or penetrance (% of Drd1 or Drd2 cells that express YFP)? Both quantities should be depicted.
We will add the information in the Figure S1 and S5 legends and revise y-axis label ( Figures S1F and S5B).
If the presented data is, in fact, specificity, 60% is lower than what is usually accepted for genetic targeting -90% is a typical minimum percentage.
In case of tetracycline-controllable gene induction system, 60% is high. What is the identity of the other 40% of cells, and how do you know they are not responsible for the behavioral effect? The same holds true for Figure S5B.
The supplemental figure shows penetrance, not specificity (as this comment seems to assume). The other 40% of cells are GFP-negative/D2-positive cells. GFP-positive/D1positive cell are rare (less than 3%, FigureS1C and Figure S5B), which is unlikely to affect the main effect.
2) Figure S1F is not sufficiently high resolution to determine whether or not there is DTA mRNA in mPFC or IC. This is a critical question, since the majority of the work in this paper relies on a transgenic approach rather than a spatially restricted viral vector approach. If it is to be believed that the degeneration of VLS D2 neurons leads to apathy, it needs to be shown that D2 neurons elsewhere in the brain are intact. Therefore, it is absolutely essential that: (1) the authors provide high-resolution images of mPFC and IC with Drd2 neurons clearly labeled; We provided high-resolution images of mPFC and IC with Drd2 neurons in Figure S3B.
(2) the authors show, quantitatively, that there has not been a reduction in this population after DOX-off at several time points up to 20 days We provided the cell number for both cortices below. This seems to be meaningless because we never find DTA mRNA in mPFC or IC. We think that it is not necessary to provide this information even in the supplementary figure.
(3) there is no DTA mRNA in mPFC or IC when assayed at high resolution.
We provided high-resolution images of DTA mRNA ISH in Figure S3A.
Even this is not ideal -D2 neurons elsewhere in the brain could still be mediating the effect (hippocampus, other cortical areas, etc). The cleanest approach would be to use a cre-dependent DTA vector (which exists) in a Drd2-cre mouse -this would control for expression everywhere else in the brain. It is difficult to accept a unique role for VLS in apathy without specifically demonstrating that the approach used in this paper does not affect the activity of ALL other Drd2 cell groups.
One of our key points is that the optogenetic ablation and silencing experiments both target only VLS, and these studies confirm a unique role for VLS (Fig 6). The viral approach suggested by the reviewer could have been used to accomplish the same objective. However, we believe the optogenetic approach is preferable because it demonstrates that the same phenotype can be produced via both silencing and ablation. The virus experiment would not provide any additional information beyond what was provided by the optogenetic experiments.
3) The authors use a brief 2-second inhibition that starts when the lever is presented, but this inhibition is temporally dissociated from the time during which the behavior is modified. This raises some questions that need to be answered. a) First, and most important: it is known that periods of optogenetic inhibition can be followed by rebound excitation, and the amount and duration of this rebound excitation may depend on cell type. The authors have shown that a brief 100 ms pulse in a whole cell voltage recording leads to transient inhibition, but they have not demonstrated the effect of this 2-second inhibition on cellular physiology in vivo. It is entirely possible that the net effect of this manipulation is enhanced excitability during the bulk of the progressive ratio task, which would muddle the relatively straightforward interpretation presented here.
We believe our comment #3 from the previous response should have addressed this concern. It is possible that 2-second ArchT opening caused enhanced excitability. However, as we showed in the previous response, ChR2-mediated activation of VLS D2-MSNs produces a behavioral effect that is totally different from the effect of ArchTmediated silencing. This means that the net effect of ArchT is unlikely to be excitation. Furthermore, the effects of ArchT inhibition are identical to the effects of D2-MSN ablation ( Figure 6), also suggesting that the predominant effect of ArchT is neural silencing.
b) Is there something special about 2 seconds that leads to this behavioral effect? The more obvious experiment would be to turn the laser on at lever presentation and turn it off when the animal has successfully pressed the lever the last time for that trial, or after 5 minutes has passed with no lever press. The results of this kind of experiment would be far easier and more straightforward to interpret, and would be a direct demonstration of the critical role for this cell population in apathy.
We measured the VLS D2-MSNs population activity by using fiber photometry, and identified that VLS D2-MSN activity showed the Ca ++ surge for about 2 seconds immediately after the trial start cue. We will show these data below, but we prefer not to include these data in the manuscript as they are part of another paper. Apathy is lack of interest or lack of an emotional state. In this paper they really did not explore if the mice experienced a lack of emotional state or an indifference to stimuli of positive or negative valence, they only assessed performance on behavioral tasks addressing cognitive responses (attention, impulsive action) and motivation. While lack of self-generated motivational behaviour is a symptom of apathy, they really don't assess whether there is emotional blunting in these animals. On the tasks that they did perform, ie forced swim test and elevated plus-maze, there was not difference in performance between genotypes. The references they offer to support that their definition is 'well accepted' are studies of human Parkinson's patients that also experience pour verbal memory, emotional blunting, less interest in social activities etc. Furthermore some of their results do not necessarily fit with their definition of apathy (ie increased impulsive action and preservative responding). Therefore, I tend to agree with Reviewer 2 on this point that apathy is a human condition -and if it was possible to model it in mice, they have not done it well here. I am saddened by this current push in today's science to spin results into an anthropomorphic framework for the sake of snappy headlines (ie mice experience loneliness, etc).
With this stated, I think the results of this study are interesting in that they provide a new experimental model testing the contribution of VLS D2-MSNs in behaviour, rigorous, and well controlled and should be published in this journal. However, I really think the 'spin' on apathy is not necessary. I think that it is important that they keep these finding within the context of rodent behaviour. Perhaps in the last paragraph of the discussion they could speculate that these results may fit with certain symptoms of a clinical definition for human apathy, but I really think it is a stretch for the whole paper (introduction and discussion) to be framed around this concept.
We agree with this concern. We keep our finding within the context of rodent behavior and carefully edit the abstract, the introduction, and the last paragraph of the discussion.