My comments are as follows:

1.      The paper is interesting and well written, and it is relevant to the water management of a vital area of China: Xiongan New District.

2.      There are two major issues that require a much more careful analysis, and I hope the authors can revise their paper accordingly. The first is the description of denitrification. In this manuscript, the authors used a two-step reduction to simplify the process. This is OK, but requires a much more careful and detailed analysis to justify its correctness. It is well known that denitrification is a complex process controlled by many factors. So, the authors should carefully justify why such a two-step reduction treatment is acceptable for this site!

3.      The second issue is related to Eq. 5. The author stated that “ For example, according to the redox gradient theory, sulfate reduction may be inhibited by oxygen, nitrate, and trivalent iron dissolved in groundwater. These effects are modeled using an inhibition term in equation (5)”. This is not sufficient. I would like the authors to explain what “inhibition term in Eq. (5)” is used and why. In one sentence: more elaboration is needed here!

4.      L60, there should be a question mark “?” after the two questions mentioned there.

5.      L65, when NCP is mentioned for the first time, the full name of NCP must be provided.

I will recommend moderate revision.

This manuscript presents a regional-scale assessment of MAR impacts on groundwater level recovery and nitrate dynamics in the Xiong'an New Area using a three-dimensional coupled flow and reactive transport model. The topic is relevant for managing groundwater depletion and nitrate pollution in intensively cultivated regions. The integration of MAR hydraulics with nitrate biogeochemistry is an important contribution, and the authors provide clear insights into how dilution, denitrification, and geological heterogeneity jointly shape water-quality outcomes. The discussion is generally well-structured and highlights both the strengths and limitations of MAR. However, several aspects require clarification and improvement before the manuscript can be considered for publication. The model structure, boundary conditions, and parameterization of reactive processes need more transparency, particularly regarding organic carbon availability, redox controls, and the justification for simplifying nitrogen pathways. Some interpretations appear to overstate the certainty of denitrification estimates given the strong assumptions applied. While the authors have mentioned the influence of spatial resolution, recharge configuration, and heterogeneity, this part would benefit from more rigorous sensitivity analyses. The discussion could also more explicitly connect findings to broader MAR design principles and regional management implications. Furthermore, I suggest the authors discuss how their exclusion of other nitrogen transformation reactions might affect the conclusions regarding denitrification's minor role. 

Overall, the study has clear potential, but refinements in methodological justification, uncertainty communication, and the contextualization of results will substantially strengthen the manuscript. Therefore, I recommend minor revisions.

Specific comments:

1. Line 16: The abstract states that “regional-scale hydrological and geochemical impacts remain insufficiently understood,” but several recent MAR modeling papers at regional scales exist. It is unclear what is truly new: the model structure? the scale of the simulation? integrating heterogeneity? long-term simulation horizon? nitrate processes? 

2. Line 13-24: Currently the abstract provides interpretation but no numbers, making the conclusions feel generic. Consider adding a sentence on the role of heterogeneity in shaping nitrate reduction patterns.

3. Line 33: “become as”

4. Line 113: The rate expression multiplies terms for electron donor (ED), terminal electron acceptor (TEA) and inhibition. However, there is no mention of an explicit microbial biomass pool (or active biomass concentration). Denitrification in aquifers is often biomass-mediated and can be substrate-limited and biomass-limited; excluding biomass (or at least an active biomass term) risks mischaracterizing dynamics, especially under long-term MAR where biomass may grow or be flushed.

5. Line 117: The Introduction criticizes prior studies for omitting microbial OM degradation and C–N coupling, but the method section does not convincingly demonstrate that these processes are represented.

6. Line 123: The manuscript specifies that the model domain is discretized using 100 m horizontal grid spacing but does not provide justification for this choice. Given the scale of the study area (tens of kilometers) and the strong emphasis on preferential flow paths, MAR-induced infiltration fronts, and heterogeneity, did the authors perform mesh and time-step sensitivity analyses (e.g., Courant number assessment or grid refinement tests) to ensure numerical stability and accuracy of both flow and reactive transport simulations?

7. Line 129: Only four lithofacies are represented based on 14 boreholes. This is a very sparse conditioning dataset for a 3D domain of this size. The uncertainty introduced by such limited conditioning should be acknowledged.

8. Line 203: How sensitive are these values to recharge rates or hydraulic conductivity? The results repeatedly attribute attenuation to “distance and connectivity,” but this remains qualitative. A clearer linkage between MAR response zones and the permeability map is needed.

9. Line 215: The concept of comparing points with different distances and permeabilities is good, but the interpretation mixes permeability effects and distance effects. For example, line 220 states that “their amplitudes diverge with permeability: Point1 rises by ~4–7 m, while Point2 increases by ~3–5 m across the projection horizon”. But figure 5b clearly shows a larger amplitude than 5a, which means MAR posed a higher effect on Point2. Also, no lag time between Point1&2 is surprising.

10. Line 255-256: Be cautious with statements such as “strongest decreases” when the absolute reductions remain quite small (10^-5 mol/L is extremely minor relative to typical groundwater nitrate levels). You may want to discuss ecological significance, not just the mathematical magnitude.

11. Line 278: Obviously, denitrification is effectively negligible in this system. How reliable this result is? Plus, it is surprising that the spatial pattern is nearly uniform, given strong variability in residence time, electron donor availability, and organic carbon distribution in real systems.

12. Line 353: You highlight the differing effects of heterogeneity on dilution vs. denitrification but do not clearly link these insights to the broader literature on preferential flow and residence-time control on reactive transport. Adding comparison to previous heterogeneity–redox studies would position your results more convincingly.

13. Line 362: “he”

14. Line 373: While you note that the recharge scheme assumed constant conditions, you do not discuss how sensitive the nitrate response is to recharge timing, distribution, or water chemistry. Without acknowledging potential model sensitivity, the management implications may appear overstated.