General considerations:
In this manuscript, Milosavljević et al. characterized a transgenic mouse model overexpressing the human CYP2C19 and CYP2C18 genes (“CYP2C19 mice”) for exploration of this as an animal model for cerebellar ataxia, based on previous evidence revealing that these mice exhibited neurodevelopmental impairments associated with locomotion. The authors started by characterizing mouse motor function using a battery of behavioral tests, where they observed impaired locomotion and gait. Next, they analyzed the dopaminergic system integrity in neuropathological studies, using immunohistochemistry, chromatographic neurochemical quantification of the whole-brain and neuroimaging techniques. As CYP2C19 mice revealed hyperdopaminergism, the authors then treated the animals with dopamine antagonists to try to ameliorate the observed phenotype, which was not achieved.
While the study is relevant and presents a pertinent contribution for the field of neurobiology, adding new information about the phenotype of a previously described animal model, and from a language standpoint, the paper is well written and easy to comprehend, the figures are clear and easy to interpret, and the statistical analysis was exhaustive and thoroughly described, the article has, nevertheless, important logical flaws and missing pieces of information. Its main shortcoming is the lack of fluidity and logical connection between parts. Also, some aspects of the research work are lacking explanation, such as the choice of ages of the animals, the rationale for looking at specific brain areas and neurotransmitters (not often linked to ataxia) and not others, and the choice to measure oxidative enzyme activity and not other pathways, for example. The article reads like three separate works put together without a clear logical thread. The conclusions are in some cases overstated and, sometimes, not fully supported by the results. The authors should carefully revise these aspects of the manuscript. Importantly, given the scope of this journal, further neuropathological exploration of the model should be done, considering different timepoints, additional neuronal subtypes and neurotransmitter systems, and other brain regions, in order to provide a clearer idea of the nature of the neurodevelopmental perturbation and its evolution during the lifetime of the animal. Also, authors should provide more theoretical background to some of the analyses made, discuss more thoroughly the data and interconnect it further. Although ultimately the article fails to provide a solid validation of the model presented here as a model for preclinical studies cerebellar ataxia, at this stage, it encompasses a relevant amount of work and experimental results and gives important information regarding the model itself. A deeper study of the pathology and an improved organization of the writing could make it relevant for the field.

Section by section considerations:

ABSTRACT
The abstract is concise and clear. It summarizes well the objective and methods of this research work, although the aims are not clear, and most of all the interconnection between them not at all logical.
Minor issues:
-The authors shouldn’t include statistics in the abstract.

INTRODUCTION
The authors start the introduction by characterizing cerebellar ataxia and highlighting the impact of the lack of understanding of this condition, setting the tone to introduce the relevance of animal models to better comprehend ataxia pathophysiology as well as the need to find better models. Then, from lines 36 to 58 (page 2) the authors elegantly and thoroughly describe what is already known about the CYP2C19 mice model.
Major issues:
-The authors did not explain in detail the function of this gene, the pathways it is involved in and its biological relevance. It is known that this gene produces an enzyme that is involved in the processing and metabolizing of some prescribed drugs. Here, the link between this gene and ataxia is missing: its expression in the cerebellum, substantia nigra and other important areas, as well as in the timepoints analysed; the molecular mechanism that might involve this gene and its relationship with the dopaminergic system (the study focus) as well as with the cell apoptosis, that authors consider in the discussion but do not further elucidate.
-The link between paragraphs is not clear, and, most importantly, the links between the subjects to be addressed in the article are not established. This should be provided in this section. For instance, the association of CYP2C19 with essential tremor should be mentioned. Also, what are their (or the field's) hypotheses regarding potential substrates and products of CYP2C19 of relevance to the neurological phenotypes?
-From line 3 to 20, page 3, the authors state the hypothesis and aims of the study. Some of the aims of the study (3 and 5) appear as a surprise to the reader, as neither the abstract nor the introduction clarify the relation of the nigrostriatal dopaminergic system nor the involvement of oxidative stress and neuromelanin with the ataxia phenotype, or why they are focusing on these to characterize the model. This is important to elucidate the originality of the research aims so the reader could understand the relevance of the investigation in this topic.

Minor issues:
-In lines 47 to 49, the authors write “Therefore, this mutant is the best attainable tool to study the role of CYP2C19 in the developing brain in vivo.”. However, they do not present any evidence or comparison with other models that can sustain this statement, and they do not discuss the potential confounding effect of having a second gene also overexpressed in this strain. This might be relevant to understand the importance of this model.
Overall, the introduction is missing key information regarding the neuropathology of the disease and what is known about the brain pathology of the CYP2C19 model, in order to better comprehend the procedures performed next.

MATERIAL AND METHODS
The Material and Methods section is well written, using a simple and clear language. The authors start by describing the housing of the animals and the welfare assessments performed. Also, the ethical considerations are clear and well discriminated, in accordance with ARRIVE 2.0 guidelines, and they provide the authorization number of the project attributed by the Ethical Committee on Animal Experimentation of the University of Belgrade. Another key part of this section is the statistics which is thoroughly described, especially in the supplementary material, and seemed adequate for the experiments performed. However, the authors should include the number of animals and/or replicates in the manuscript material and methods section (not only in the figures or supplementary material) for all behavioral tests and techniques performed, as this is essential information to better understand the data as well as to replicate the same experiments in other labs. Also, they should clarify the choice of the different ages of the animals to perform each analysis, as this parameter differs among experiments, limiting the analysis of association and correlations between the different aspects of disease.

Major issues:
- Although the authors give important information regarding animals’ housing, welfare assessment and division of the groups, the number of animals used in each group isn’t discriminated anywhere. This is key information for further replication of the experiment, but also to help understand the robustness of the data.
- Power estimates supporting the definition of the number of animals required for the experiments are not provided.
- Starting in line 44, page 8, the authors describe the behavioral tests used to evaluate mouse motor function. However, besides the footprinting test, they do not indicate the age at which each test was performed. This is very relevant information, as it is the best way to correlate the motor phenotype with the neuropathology observed in the brain.
-In line 11, the authors wrote that the mice “are hemizygous carriers of 12 copies of human CYP2C19 and CYP2C18 genes”. The involvement of CYP2C18 genes was never referred before. Couldn’t it affect the aforementioned (Introduction, lines 47-49) quality of the animal model to specifically study the CYP2C19 gene involvement in the developing brain?
-In lines 51 to 53, the authors write “Next, the maximal height of hindpaw elevation while walking was derived from the video footage of the footprinting test.”. However, the analysis was performed manually, raising some concerns on how precise and trustable this measure is, as it depends on the observer, the position of the camera and the quality of the video.
-In lines 29 to 33, page 9, the authors state that dopamine concentration was measured using HPLC-MS/MS in the brain hemispheres of 3 months-old mice. However, they do not explain why they chose this age for this analysis. Considering that the phenotype was more severe in younger animals, and one of the goals of this study was to correlate the motor deficits observed in this model with the brain pathology, wouldn’t it make more sense to use younger animals to perform this analysis, or to use different ages and see the progression of this aspect of the phenotype?
-In lines 41 to 54, page 9, the authors describe the use of a selective D1 antagonist, ecopipam hydrobromide, and a D2 antagonist, raclopride. However, they do not explain what made them choose these specific drugs and dosages. This could be relevant to understand how they might achieve their objectives. Also, they don’t clarify the administration route, the duration of the treatment or at what age the treatment was initiated. This is key information.
-In lines 9 to 11, page 10, the authors state that the immunohistochemical analysis was performed in 6- and 15-month-old animals. Authors should clarify why they chose these ages, as the animals used for the motor behavioral analysis were younger. This raises some concerns regarding the correlation of the motor phenotype with the brain neuropathology, considering that the behavioral assessment was performed in young and adult animals, while the neuropathology was performed in older animals. As so, there is no way to correlate the neuropathological data with the motor phenotype found, not achieving a key objective of this paper. The same applies to the assessment of the presence of neuromelanin, as it was analysed in 15-month-old mouse brain sections (lines 19 to 21, page 10).
-In the supplementary material, from line 42 to line 48, page 32, the authors explain that they placed a strong light source in the starting point on the runway where the animals perform the footprinting test, so they would escape from the stress-induced stimulus. This raises some concerns regarding the stress induced in the animals, especially in TG mice, which have emotional impairment and are more sensitive to stress as described in the introduction. The same applies to the beam walking test (lines 13 to 20, page 34). Authors should comment on this.
Minor issues:
-In line 41, page 9, the authors write “To test the effects of dopaminergic receptor agonists” but later they state they used antagonists. Most likely, this sentence should be corrected “To test the effects of dopaminergic receptor antagonists”.
-From line 34, page 10, to line 26, page 11, the authors described the Gd-enhanced neuroimaging technique. Although all the steps of the procedures, the parameters and statistical analysis were clearly explained, the authors missed to point out the number of animals used in each group as well as their ages. This information is extremely relevant for further replication of the experiments as well as for the understanding of the robustness of the data.

RESULTS
The authors describe the results with a simple language, explaining with detail what they did, for what purpose and the results obtained. Although the statistics are well presented in the figure legends, the authors should include the tests performed in each result and also the legend for the values considered for the p (For example: “ *Statistical significance p<0.05).
Major issues:
-In lines 33 to 38, page 13, the authors write “Several animals were excluded from the motoric tests, since they were unmotivated to complete the tasks or the training; similar number of exclusions occurred in TGs and WTs.”. Considering that this TG animal model has some emotional impairment associated with increased susceptibility to stress, one can understand the lack of motivation/interest in the tests, but this statement raises questions as to why WT animals would be unmotivated to complete the motor behavior tests. Can it be due to the use of a strong light source in some of the tests? This means, that this light is interfering with the test itself, increasing the stress and anxiety in the animals, which might have an impact on the results. Also, it would be relevant to specify the observations that made the authors conclude that the animals were not motivated to perform the tests.
-Authors state that animals showing abnormal behavior were excluded from the analysis. This being a behavioral study, it is important to be much more specific about the definition of abnormal behaviors and criteria for exclusion.
-Was there any difference in motor learning? This is an important function of the cerebellum.
Minor issues:
- Figure 2C is missing the scale bar.

DISCUSSION
The discussion of the results is not fluid and is missing some key information, especially supporting data from the literature, as well as some interconnection between all the data. Everything seems diffuse and without a link.

Major issues:
-In lines 20 to 22, page 16, the authors write “Hyperdopaminergism observed in the TG mice is most likely not the cause of the observed motoric phenotype, but rather a compensatory phenotype…”. The authors should consider including some literature supporting this conclusion, as their data per se cannot do it. .
-The information presented in lines 33 to 40, page 16, is quite confusing and difficult to read. The authors should consider to rephrase it. Perhaps it should read “Even though neuromelanin aggregates are not normally detectable in rodents due to their relatively short lifespans compared to the long process of neuromelanin production (24), a few animal models with altered dopaminergic nigro-striatal pathway have been described to exhibit detectable neuromelanin levels (24,25)”?
-In lines 47-48, page 16, the authors state that “Cerebellar atrophy was observed along with ataxia-like phenotype in TG mice…”. Were the MRI studies performed in animals of the same age as the ones where a motor phenotype was described? The authors do not provide this information anywhere, and this conclusion can only be possible if there is a match in the ages, otherwise it is not supported by the data.
-In lines 49 to 53, page 16, the authors suggest cerebellar atrophy as the most probable cause of motor phenotype in TG mice, however they do not explore the cellular basis of this atrophy – is it a reduction in the number of cells or an atrophy of the dendritic branching, leading to a more compacted structure of the cerebellum? What cerebellar cell types are more affected? Which lobules? Which inputs and outputs?
-The different motor-related findings should be discussed and related to the neuropathology patterns. For instance, the abnormal hindpaw elevation, or the presence of the limb clasping in the TG mice. The authors should associate these findings to circuits of the brain and even correlate these behavioral findings to the neuropathological ones described already in the literature, to enrich this characterization. One could question why the BWT had positive results but not the rotarod test? What does this tell us about the differential involvement of brain regions and circuits? Should more behavioral tests be performed to confirm the hypothesis raised by these results, and, if so, which ones?
-In lines 9 to 14, page 17, the authors present their conclusions about the antioxidant enzymes activity, however they do not relate this data with the rest of the manuscript, explain the rationale of these experiments or explain the relevance of looking at these specific parameters.
-From line 60, page 17, to line 8, page 18, the authors conclude that the present model show an ataxia-like phenotype and is a suitable model for preclinical research. The authors should re-consider this conclusion as, from this reviewer's point of view, they don’t provide enough data to support it. Also, the model presented here does not mimic what is observed in the clinics, as it shows a strong motor phenotype at young ages that stays unaltered or improves with age, while in most cerebellar ataxia patients the symptoms worsen with age. This is a lack of face validity, to add to the lack of concept validity, as genetic variants in the CYP2C19 gene have not been described to cause ataxia.

Minor issues:
-In lines 23 to 26, page 16, the authors write “… but rather a compensatory response, since antidopaminergic drugs failed to ameliorate motoric impairments of TG mice and since hyperdopaminergism…”. The authors should consider rephrasing this sentence as the word “since” is repeated. Instead, they could write “… but rather a compensatory response, as antidopaminergic drugs failed to ameliorate motoric impairments of TG mice and hyperdopaminergism…”.
-In line 41, page 16, where it is written “… in 15-month TG mice” it should be “… in 15 months-old TG mice”.
-In lines 47 to 49, page 17, where it is written “(1) the TG mice either stagnate of spontaneously improve phenotypic characteristics…” it should be “(1) the TG mice either stagnate or spontaneously improve phenotypic characteristics…”
-In line 53, page 17, where it is written “… in the both sides of the body…” it should be “… in both sides of the body…”;