The work of Kalin and collaborators is an important effort to characterize the specific functional role of NR4A2a and NR4A2b paralogs of the transcription factor NR4A2 in zebrafish. There is progress in the data presented. However, several caveats should be addressed before publication.

1.- Figure 2 is a quantitative analysis of the number of GFP-positive cells (indicative of dopaminergic neurons) in brain regions of the nr4a2a and nr4a2b KOs compared to WT. The statistical analysis shows no significant differences, except the decrease in GFP-positive cells in the PTN in the nr4a2a KO. However, the authors wrongly conclude that the KO of each paralog has similar global effects on DAnergic neurons in the adult zebrafish brain. The authors should eliminate this conclusion since the data do not support it. I recommend that the authors compare and discuss the similarities and differences found with previous work using morpholinos.

2.- In the same Figure 2, two quadrants are highlighted (letters C, G, and K), but enlarged images of only one highlighted quadrant are shown. They should eliminate the quadrants that do not have an enlarged image.

3.- line 49, change Fig. 5.2 by Fig. 2.

4.- In the next step, the authors exposed zebrafish larvae to the MPTP toxin to characterize dopamine neuron regeneration. They evaluated the expression of several genes and locomotor activity. Interestingly, the effect of MPTP is transient, and the larvae recover control values in all the parameters analyzed by 5dpt (except for average velocity).

The authors claim that MPTP treatment is a Dopamine neurodegeneration-regeneration protocol. However, such a statement cannot be made without measuring neuronal damage or death. On the other hand, they found that DAT expression did not change significantly, albeit the th1 expression fell significantly by 0dpt and increased significantly at 3dpt. Since there is no match between DAT and th1, other possibilities than DA neuron degeneration are possible. TH is common to other neurochemical phenotypes, such as norepinephrine cells. Certainly, the fact that DAT did not change indicates that there is no dopamine neuron degeneration.

On the other hand, the authors highlight a similar expression profile change between shha and nr4a2a. However, the comparison is inappropriate since the variations observed in both genes are not statistically significant. Therefore, the following phrases in the abstract and discussion must be removed:

Abstract: “In a pharmacological model of DAnergic neuron regeneration, we found nr4a2a to drive the differentiation of regenerated DAnergic neurons with an expression pattern resembling sonic hedgehog a (shha). Interestingly, we found increases in notch1, th1 and nestin prior to the largest increase in shha transcription. This may suggest Notch1a is the first or: an early driver of proliferating DAnergic neurons with a shift to Shha signaling during cell-specific differentiation.”
Discussion: “Our findings support the hypothesis of nr4a2 involvement in DAnergic regeneration following MPTP-induced neurodegeneration. Changes in the expression of nr4a2a, but not nr4a2b, followed the same directions as those observed for shha (Fig. 3). The initial reduction and, possibly, a subsequent increase in transcript levels may be explained by an initial inhibition in cell fate differentiation, assuming that hedgehog signaling retains its role described in mouse neurogenesis (Roussa and Krieglstein 2004; Carballo et al. 2018). In the affirmative, the gradual increases observed at 3- and 5dpt could potentially be correlated to the induction of the differentiation stage of neurogenesis, particularly for DAnergic cells.”

In summary, this part of the work needs adequate justification and depth to understand what was sought. The data show no correlation between the expression of the nr4a2 paralogs and the genes analyzed. Indeed, nr4a2a and nr4a2b did not change after MPTP treatment. This part does not contribute to characterizing the effect of the lack of nr4a2 paralogs in zebrafish. I suggest removing it from the manuscript.

5.- In the next part of the work, the authors characterize the effect of KO of each nr4a2 paralog on the expression of several genes, including neurotrophic factors. The number of independent measurements needs to be higher for these experiments. Statistical analysis cannot be performed with n = 2-3 (as indicated in the legend in Figure 4). I suggest increasing the n of data. Furthermore, authors should consider only statistically significant differences to generate conclusions.

6.- Regarding the effect on locomotor activity, only the nr4a2a mutant shows decreased total distance and increased inactivity time in adulthood compared to WT. The authors must limit their conclusions to the statistically significant differences between each mutant and the WT.

These phrases have no evidence to support them: “There was a large variance without a distinct pattern observed at 5dpf, but this did not persist into adulthood where 3mpf nr4a2a mutants consistently swam with a mild hyperactive phenotype. We only observed a slight change in locomotor parameters following the loss of nr4a2b function (Fig. 6A-C). The nr4a2b mutant adults displayed reduced freezing bouts (Fig. 6A-C)” page 20, lines 15-22. I suggest erasing them from the manuscript.

Regarding Figure 7, the axis names in the graphs are not clear. In the figure legend, it is described that letters B and E indicate mean active duration. However, in the graph, the axis indicates mean Inactivedur.

I suggest the authors limit the description and conclusion to significant changes. Please erase this sentence: “whereas nr4a2b mutants showed a trend for lesser activity that was apparent in darkness (Fig. 7D-F)” since the evidence does not support it.

7.- Finally, the discussion should be limited to those significant findings; all comments and conclusions based on "trends" should be eliminated.
The work has very interesting data that must be better integrated and contrasted with what is already reported. A shorter, less speculative discussion would be appropriate.

The authors have substantially improved the manuscript. In particular, they have considered criticisms regarding sticking to statistically significant differences to highlight potential functions of NR4A2 paralogs in zebrafish.
This work constitutes an advance in the knowledge of the function of this transcription factor in dopaminergic neurons in this model.