I read with great interest the manuscript by Yang et al. which examines the synchrony between the annual peak in nitrate concentration and the maximum or minimum discharge, and the controls of synchrony. The study contributes to a better understanding of the processes and catchment properties that impact nitrate concentration seasonality. However, I think that some clarifications would be needed on several aspects to get the manuscript ready for publication. I summarise my main comments below:

1. The analysis of the synchrony variability between years was not very clear to me.

- Firstly, it would be good to clarify how Qmax-Synced and Qmin-Synced years are distributed in time in the three catchment categories (Qmax-Synced, Qmin-Synced, and Asynced). In other terms are the Qmax-Synced (Qmin-Synced) years grouped together in time and therefore can we separate a time period with a Qmax-Synced (Qmin-Synced) behaviour? Or are there sparsely distributed in time? This would help to understand whether changes in synchrony are due to possible trends or year-to-year variability in drivers, in particular for Asynced catchments.

- Secondly, I have been a bit confused regarding the analyses presented in Table S11 and the pink polygon of Fig. 6 and I think that their meaning should be clarified in the manuscript. From my understanding, these results refer to differences between catchments and are not explaining the year to year variability of synchrony given the catchment. To me, only the analyses based on precipitation and discharge (L271-286) examine what drives the temporal variability in synchrony.

2. A few methodological points would require clarification regarding the catchment properties used and the time scale of the analysis. Was synchrony determined based on concentration and discharge data at daily time scale or aggregated to monthly time scale? 

3. I think that the background should be expanded in the introduction (see details in the following).

I provide in the following detailed comments below that I hope will be of help to the authors to revise the manuscript.

- P2 L44: this should be nuanced and better discussed, since C-Q relationships can be used for analyses at different temporal scale, as highlighted for instance in Musolff et al. (2021).

- P2 L51-52: what are these studies, what do we learn from them, and why are they not sufficient?

- P2 L55 “data gaps”: I do not understand this, as the annual peak may not be identifiable because of data gaps. This would need to be further explained.

- P2 L62: I think it would be good to discuss previous literature that analysed the drivers of concentration (beyond discharge) to clarify and highlight the contributions of this study.

- Table 1: 

Why was SPI1 adopted for winter months only and not for summer months as well? 

Are the different catchment properties static or time-varying? My guess given the rest of the manuscript is that all properties are static but SPI. This point links to the variability analysis presented in Sect. 3.4: would it be possible to relate the synchrony variability between years to the variability in catchment properties beyond SPI and discharge?

Please add a column for the data source. 

It would be helpful to provide further details (equation) on the hydrological variables (this could be in appendix or supplements). 

- P6 L148: the p-value of which test is this?

- P7 L165: I think that the term “synchrony variability” should be better defined.

- P7 L170-171: I can see that the performance is rather low for some catchments (R2 as low as 0.11), which indicates that the processed data should be used with care. However, in the end, the actual values of the concentration is not the main focus but its synchrony. I am therefore wondering whether another performance metric, that would focus on the temporal pattern, could be relevant to complement the performance analysis (such as Spearman or Pearson correlation).

- P11 L228: how is the change in peak nitrate concentration and discharge calculated? From one year to the next?

- P11 L229-232: From Figure 4, I see that the changes in the timing of discharge are rather small for both Qmax-synced and Qmin-synced catchments (mostly between +1 and -1). Perhaps the only notable difference is that changes in concentration seem to more systematically follow changes in Q for Qmin-synced catchments?              

- Figure 4.d: there is an error in the x-axis, the middle value should be 0 instead of -4.                                              

- P14 L286 “median 0.086 vs 0.068, p=0.007": the difference appears to be rather small and I think that the results should be more nuanced. A low p-value only means that we can distinguish the two values given the sample size, but it does not mean that the difference is actually large and relevant for the analyses.

- P15 L293-302: It was not easy to get around these analyses. I suggest to better guide the reader through the different figures. In particular, I understand that the analyses refer to the pink polygon of Fig. 6 (this should be explained) and the extended results of the correlation analysis in Fig. S11. In addition, the caption of Fig. S11 is not very explicit and should be revised. My understanding is that the correlation is calculated between the catchment properties and their percentage of synchronous years (using one value for each catchment), while the caption suggests that a value for each catchment and each year is used. But maybe I missed something ?

- P15 L293: SPR as well, no?

- Figure 6: Which catchments are considered? I can see less than 66 data points. 

- P16 “temporal reorganisation of those same controls”: This is not fully clear to me, since, to me, the temporal variability in land use, geology and drainage infrastructure was not really analysed in the manuscript but only their differences between catchments (see my main comment 1) above. 

- Sect. 4.1.2: This section could be more concise. In particular, legacy is discussed at several locations (L351, 361). I think that points on the same idea should be grouped together.

- Sect. 4.2: With reference to my main comment 1), I understand that this section discusses in part the variability in space that was already discussed in Sect. 4.1. This creates redundancies.

- P20 “stronger and more dynamic anthropogenic pressures”: isn’t this in contradiction with p9 L200 (“stronger hydrological modulation of nitrate variability in these catchments”)? Do urban nitrate sources (such as wastewater effluents) really have strong dynamics?

- P21 L 455 “shaped by catchment size”: where is this results shown?

- P21 L457-459 and L463-465: would you have sufficient data to test this in the manuscript? or could you discuss what you would need?

References

Musolff, A., Zhan, Q., Dupas, R., Minaudo, C., Fleckenstein, J. H., Rode, M., et al. (2021). Spatial and temporal variability in concentrationdischarge relationships at the event scale. Water Resources Research, 57, e2020WR029442. https://doi.org/10.1029/2020WR029442   

• The current analyses using descriptive statistics and RF model are finding correlations and associations between catchment feature and synchrony class. Throughout the manuscript and in the title, "drivers" is used which implies a mechanistic association. I think it would be more accurate to use "associations" or "correlations" in place of "drivers". 
• Please clarify there was any pre-processing and outlier detection of the water quality data. For example, NW-88004024 with R² = 0.11 appears to be influenced by a single extreme outlier (~16 mg/L when all other observations are <4 mg/L). Is this observation is reliable? Additionally, was there any gap filling of flow in the cases where flow data was missing? Was there a screening for catchments based on proportion of high flow events that had sampled N data?
• Station NW-88003442 exhibits markedly higher concentration variability before ~2004 compared to after, suggesting a potential shift in catchment or monitoring conditions. WRTDS assumes gradual evolution of concentration-discharge relationships and may not perform well when abrupt changes occur (Hirsch et al., 2010). The authors should investigate whether a known change (e.g., dam construction, wastewater treatment upgrades, monitoring protocol change) occurred around this time, and discuss whether modeling this site as a single continuous record is appropriate or whether the pre- and post-2004 periods should be treated separately. While model performance statistics suggest WRTDS handled this transition adequately, if the catchment underwent a structural change, the extracted β₂ coefficients and synchrony classification for this site may reflect a blend of two distinct periods rather than a coherent long-term signal?
• Lines 190-194, 225-226: The finding that concentration magnitudes across Qmax and Qmin classes do not differ is surprising given that arable land, and thus I assume nitrogen inputs, is significantly higher in QMax-Synced catchments. This is not a typical pattern I've seen across other catchments. Some discussion of why in these catchments higher agricultural inputs don't translate to higher concentrations would strengthen the interpretation.
• The interpretation of QMin-Synced catchments as uniformly "urban-dominated" may oversimplify what appears to be a mechanistically heterogeneous group. I understand that you are looking at dominant behavior and broad stroke patterns, however, I think attributing QMin-Synced catchment behavior exclusively to urban dynamics leads to missing important nuance. For instance, while arable land is significantly higher in QMax-Synced catchments on average, Figure 5 shows that approximately 25% of QMin-Synced catchments have >20% arable land cover. Depending on agricultural intensity, proximity to the watershed outlet, etc., this fraction could meaningfully contribute to nitrate dynamics. The possibility that a subset of QMin catchments reflects agricultural legacy contributions, particularly in catchments with lower drainage density, deserves consideration before concluding that QMin synchrony is exclusively urban-driven. Consider stratifying QMin-Synced catchments by WWTP density to distinguish (1) High-WWTP catchments, high urban land use, and high population density where urban point sources likely dominate, and low-WWTP catchments where other mechanisms (legacy groundwater, forested catchment dynamics, or non-WWTP urban sources) may drive QMin behavior.
• The manuscript states that higher CV_C/CV_Q in QMin catchments signals "stronger and more dynamic anthropogenic pressures." and "increased urbanisation and population density are likely the main drivers of QMin-Synchrony, reflecting the dominance of continuous anthropogenic nitrate inputs." The first sentence is vague and overall I'm not sure if this interpretation is well-supported:
  • WWTP effluent loads are typically constant, which would produce dilution-driven concentration variability (high CVc) but wouldn't necessarily indicate "dynamic" pressures because it would indicate consistent point-source loading being diluted by variable flow. Are the authors referring to other urban pressures? If so, the specific pressures are nebulous, which weakens the argument. 
  • The wide distribution of CV_C/CV_Q values within QMin-Synced (Figure S9) that overlaps with QMax-Synced suggests this class may contain distinct subgroups operating under different mechanisms.
  • High CVc/CVq can also occur in natural forested catchments (Ehrhardt et al. 2019). Given that woodland percentage appears higher in QMin than QMax catchments (Figure 5), could some of this variability reflect natural catchment dynamics rather than urban watershed dynamics?

• Section 2.2: WRTDS is a complex model, and given that the authors use its model parameters directly, the manuscript would benefit from subtle but important clarification on the model methods. For instance, "fitted through regression at each time point" is ambiguous. The readers might not understand that coefficients are estimated for each modeled day, meaning each station has thousands of β₂ values. Additionally, there is no mention of the time, season, and discharge window widths used, which affect how rapidly the estimated C-Q relationship can change over time. Did you choose default window sizes or select each catchment window them based on model fit?
• Line 169-172: Confidence in the models could be strengthened through more detailed model assessment. While observed vs. modeled concentration plots are provided in supplementary material, the main text should clarify whether any sites were excluded based on fit criteria and whether poor model performance at certain sites affects interpretation of results. Additionally, RMSE is difficult to evaluate without knowing mean concentrations at each site. Using a normalized metric such as KGE, NSE, or PBIAS would aid interpretation in the manuscript.
• Line 117: Was distinct unimodal pattern determined visually? Did any sites not have unimodal pattern at all sites and were therefore removed from the dataset? Or were these part of the Asynced class?
• Section 2.4: Clarification on the RF model would strengthen the analysis. First, was there any hyperparameter tuning done or were default parameters used? Second, it is unclear whether the permutation importance rankings were averaged across the k-fold cross validation, or whether k-fold cross validation was used only to assess model performance and a single final model fit to all data used to generate permutation importance rankings.
• Section 3.4: This section is challenging to understand. In general, ternary plots are challenging to parse, and the current presentation does not provide sufficient guidance for interpretation. I suggest either providing more detailed guidance in the text walking the reader more carefully through the interpretation, and/or supplementing the plots with  simpler plots to isolate the key relationships. Additionally, Figure S11 caption is not clear and should be expanded upon to help readers understand. 

• QMax-Synched and QMax-Synced are both used throughout the manuscript. 
• Line 84: Fix table and citation parentheses.
• Line 84: Please make sure the catchment features used are outlined more clearly. For example, looking at the NRFA citation, I find two BFI variables but the manuscript does not state which one is being used.
• Line 94: citation missing for WWTP data
• Line 112: Subscript 2 in model coefficient
• Line 113: missing period
• Line 305: spelling error in figure caption "(d) Population density Density of WWTPs" should be Density of WWTPs
• Line 354:  "In our study, random forest analysis identified urban area as the strongest explanatory variable in these catchments." This sentence is misleading. The random forest ranked urban LU highest in variable importance for the classification. It the predictor helps most with prediction accuracy, but it does not provide explanatory inference. The significant differences between synchrony classes were shown in the Wilcoxon results, not by the RF. I’d recommend revising the phrasing to reflect this.