The reviewed manuscript addresses the evaluation of a high-resolution, spatially distributed hydrological modelling framework designed for mapping pluvial flood hazards in ungauged agricultural catchments. The main objective of the study was to assess the capabilities and limitations of conceptual modelling under conditions of limited calibration data, with particular attention given to the separation of runoff generation and flow routing processes. The Authors compared adjusted SCS-CN formulations, including the Jain method, with two routing algorithms, using data from 39 rainfall-runoff events observed in two nested experimental agricultural catchments.

The topic of the manuscript fits well within the scope of Hydrology and Earth System Sciences, as it addresses important issues related to rainfall-runoff modelling, flood hazard assessment, ungauged catchments, and the practical application of distributed hydrological approaches.

It should be noted, however, that the manuscript presents a modelling approach that is already well known in the literature. Similarly, accounting for the spatial variability of flow paths is a commonly used concept and largely follows ideas presented in the frequently cited study by Grimaldi et al. (2012). Therefore, the manuscript does not show particularly strong methodological novelty.

Nevertheless, the study has considerable practical relevance, as it provides a useful approach to reducing errors in surface runoff simulation in ungauged catchments. The results indicate that the Jain method reduces volumetric bias, and that the distributed approach performs better than lumped modelling. However, model performance remains strongly dependent on rainfall intensity. An important conclusion of the study is also the indication of the limitations of static CN parameterization in representing rapid Hortonian runoff processes, as well as the usefulness of the proposed framework for identifying hydraulic hotspots in ungauged catchments.

Overall, the methods are well described, the results are clearly presented, and the discussion is generally sound and valuable from a practical point of view. I have several comments and suggestions that may help improve the manuscript:

1. Please explain each abbreviation when it is used for the first time in the manuscript.
2. Line 200: Is sheet flow always assumed to occur, for example, in flat forested catchments? In practice, this process is rather rarely observed and usually occurs after heavy rainfall events. Please clarify this assumption.
3. Line 214: What happens if the rainfall duration differs from 24 hours and the return period differs from 2 years? Please explain how the proposed approach can be applied under different rainfall duration and return-period scenarios.
4. Why were only normal antecedent moisture conditions considered? In some cases, especially for low precipitation events, changing the CN value to wet antecedent conditions may generate surface runoff. Why did the Authors not adjust CN according to antecedent precipitation, for example using P5? Such an approach would make the model more realistic.
5. Did the Authors consider adding a subsurface flow component? This could increase simulated runoff during smaller precipitation events and would make the representation of runoff generation processes in agricultural catchments more realistic.

In conclusion, although the manuscript does not provide strong methodological novelty, it addresses a relevant and practically important problem. The paper is generally well prepared and fits the scope of HESS. I recommend that the manuscript be considered for publication after the Authors have addressed the comments listed above.

Major comments

1.  The analysis is based on a single catchment of only 111 ha, with an 84 ha nested sub-catchment. These are not two independent catchments with contrasting characteristics, but two highly dependent evaluation points within essentially the same hydrological system. This severely limits the possibility of assessing transferability across climatic, pedological, topographic, land-use, and catchment-scale conditions.

The very small catchment size may also explain why the two routing approaches provide almost identical results. The reported mean difference in concentration time is approximately seven minutes, which is close to one 5-minute computational time step. A larger or morphologically more complex catchment could produce very different conclusions regarding the relative performance of the routing methods.

The manuscript appropriately acknowledges the single-context limitation near the end, but this reservation is inconsistent with claims elsewhere that the approach constitutes a “transferable blueprint,” is reliable for ungauged agricultural landscapes, or can support vulnerable landscapes globally. These statements should be substantially moderated throughout the Abstract, Results and Discussion, and Conclusions.

In this context, the authors could consider Soulis (2018), which showed that changing watershed conditions following wildfire altered not only runoff and peak discharge but also the apparent SCS-CN response, including a transition from complacent to standard behaviour. This illustrates that SCS-CN behaviour and the relative performance of CN-based approaches can change markedly under different watershed conditions, even within the same catchment. The paper is particularly relevant to the statement that runoff partitioning is sensitive to local conditions and that results from one case cannot be generalized:

Soulis, K.X. (2018). Estimation of SCS Curve Number variation following forest fires. Hydrological Sciences Journal, 63(9), 1332–1346. [https://doi.org/10.1080/02626667.2018.1501482](https://doi.org/10.1080/02626667.2018.1501482)

2.  The performance of the runoff-generation component is far from satisfactory. Even the best configuration produces NSE = 0.17, RRMSE = 133%, and PBIAS of approximately 16%. Similarly, the median KGE values of 0.40 and 0.37 indicate only limited overall hydrograph reproduction, while errors during high-intensity and extreme events are frequently very large.

Against this background, the improvement from the lumped to the distributed Jain implementation is quantitatively small: NSE increases from 0.14 to 0.17, RRMSE decreases from 135% to 133%, and PBIAS changes from 19% to 16%. A statistically significant paired difference does not necessarily represent a hydrologically or operationally meaningful improvement. The authors should report an appropriate effect size and uncertainty intervals and discuss the practical magnitude of the improvement rather than relying mainly on the p-value.

Expressions such as “robust,” “reliable,” “acceptable runoff predictions,” “structurally robust,” and “critical operational value” are not supported by these performance levels. The text should distinguish more carefully between: 1) a technically functioning modelling workflow; 2) a statistically detectable difference between configurations; and 3) predictive performance sufficient for practical flood-risk decisions.

The current results primarily support the first of these.

3. The improvement obtained by calculating runoff separately for spatial units rather than using an area-weighted composite CN is an important result. However, it is already well established that, because of the nonlinear form of the SCS-CN equation, runoff calculated from a composite CN can differ substantially from the area-weighted runoff calculated for heterogeneous subareas.

The Introduction should explain this issue explicitly and engage with literature that investigates the effect of watershed heterogeneity on CN estimation and runoff prediction. Two particularly relevant studies are:

Soulis, K.X. and Valiantzas, J.D. (2012). SCS-CN parameter determination using rainfall-runoff data in heterogeneous watersheds – the two-CN system approach. Hydrology and Earth System Sciences, 16, 1001–1015. [https://doi.org/10.5194/hess-16-1001-2012](https://doi.org/10.5194/hess-16-1001-2012)

Palli-Gravani, S., Soulis, K.X. and Wałęga, A. (2026). Simplified approach to considering watershed heterogeneity in direct runoff estimation using SCS-CN model. Hydrological Sciences Journal. [https://doi.org/10.1080/02626667.2026.2628736](https://doi.org/10.1080/02626667.2026.2628736)

The first study explains theoretically and empirically how spatial variability affects the CN–rainfall relationship and why a single composite CN can generate important errors. The second provides a recent multi-catchment and synthetic-data assessment of how explicitly representing the spatial distribution of runoff-producing areas improves CN estimation. These studies would strengthen both the Introduction and the interpretation of the distributed-versus-lumped comparison. The present improvement should be presented in relation to this existing understanding rather than as an isolated finding.

4. I am not convinced that all components of the modelling framework are physically meaningful at a 1 m resolution. The DEM has metre-scale information, but several other inputs, including hydrologic soil groups, CN values, crop classes, Manning coefficients, and channel parameters, are derived from much broader classifications or coarser datasets. Running the model on a 1 m grid does not necessarily imply that runoff generation and hydraulic properties are known at that scale.

The manuscript needs a systematic resolution-sensitivity analysis. Results should be compared at several resolutions, for example 1, 2, 5, and 10 m, considering for instance : delineated flow paths; concentration and travel times; peak discharge; hydrograph performance; computational time and memory requirements; and sensitivity to the imposed minimum slope.

At present, the argument for selecting 1 m is based largely on literature and qualitative reasoning. Appendix A appears to examine the effect of resolution on local velocity classifications, but it does not demonstrate that 1 m provides superior observed hydrograph or peak-flow predictions in this catchment.

The authors should also quantify the error introduced by rounding CN and travel-time values to integers for the grouped convolution procedure.

5. The claim that the approach can be applied without calibration requires reconsideration. Several parts of the routing framework appear to involve catchment-specific adjustment:

- the stepwise relationship between contributing area and flow depth is explicitly described as site-specific and calibrated using field observations;

- the minimum slope of 0.005 m m⁻¹ was selected because it produced concentration times consistent with observed values and another empirical equation;

- the adjustment of travel times for extreme events was evaluated using preliminary sensitivity tests in this catchment, but the results are not shown;

- the transition thresholds between hydraulic regimes are empirical.

These choices may be reasonable for the experimental catchment, but they contradict repeated statements that the framework is uncalibrated and directly transferable to ungauged catchments. The authors should clearly separate:

1. parameters taken unchanged from published sources;

2. parameters inferred from local field observations;

3. parameters selected or tuned against the observed hydrographs; and

4. parameters used without any evaluation.

Ideally, calibration and validation events should be separated, or a leave-one-event-out or split-sample analysis should be undertaken. Otherwise, the method should be described as locally parameterized or partially calibrated rather than uncalibrated.

6. The concentrated flow paths shown over the background imagery require validation. This is especially important in the northern cultivated part of the catchment, where crop rows, tractor tracks, wheel ruts, tillage direction, field boundaries, temporary ditches, roads, and agricultural operations may redirect runoff independently of the bare-earth DEM.

The mapped paths appear relatively natural and topographically controlled, but the agricultural fields are heavily managed and their surface configuration changes over time. Were field surveys undertaken to confirm the location of concentrated flow, ephemeral gullies, muddy-flow traces, or erosion features? Were any mapped pathways compared with UAV imagery, event photographs, observed erosion patterns, or farmer reports?

Without independent spatial validation, good or moderate agreement at one or two outlets does not demonstrate that the internal drainage pathways or mapped hotspots are correct. This is a central issue because the main claimed added value of the study is the spatial identification of critical locations.

7. The manuscript repeatedly refers to “flood hazard maps,” although the main output is peak discharge along predefined concentrated flow paths. Flood hazard normally involves some combination of inundation extent, water depth, velocity, duration, probability, and potentially consequences for exposed receptors.

Peak discharge is certainly a useful hydrological indicator, but it is not by itself a complete representation of flood hazard. The authors should either: reframe the output as spatial peak-discharge or concentrated-flow screening; or couple it with a hydraulic or terrain-based procedure that estimates water depth, velocity, or inundated area.

The practical relevance of flood hazard in this specific 111 ha agricultural basin should also be better demonstrated. 

8. A central justification for the work is its potential application in ungauged regions. However, no evidence is provided that a 1 m iterative implementation is computationally feasible beyond this exceptionally small catchment.

The manuscript should report: the hardware used; preprocessing and simulation times; memory requirements; the number of active pixels and temporary outlets; the reduction achieved by grouping identical CN–travel-time combinations; and how runtime scales with catchment area and drainage-network length.

An application or benchmark for a larger area would considerably strengthen the study. Without such evidence, statements about wider operational use remain speculative.

9. The authors correctly state that the 25- and 100-year simulations are exploratory scenarios rather than validated predictions. This qualification should be maintained consistently throughout the manuscript. Statements that the model “demonstrates” the expansion of the active flow network or identifies nonlinear synchronization under extreme events are stronger than warranted, because these patterns are generated by the assumed model structure and travel-time adjustment rather than independently observed. The reported increase of more than 90% along the main thalweg should be described as a modelled scenario outcome, not as an empirically established hydrodynamic response.

10. The manuscript states that the Jain initial abstraction formulation depends on rainfall intensity. However, the presented equation depends on total rainfall depth, P, and potential retention, S, not on rainfall intensity or the temporal distribution of rainfall. This distinction is important because the manuscript subsequently identifies rainfall intensity as the principal unresolved driver of model error.

The terminology should be corrected throughout. The Jain formulation may make initial abstraction dependent on storm depth, but it does not resolve within-event rainfall intensity. Similarly, the statement that the SCS-CN framework was “empirically calibrated for 24-hour events” should be carefully checked and qualified. The fundamental problem here is that the method is an event-total runoff equation without an explicit infiltration-rate or within-storm intensity representation.

11. The discussion of antecedent conditions should be strengthened and better supported by the relevant literature. The finding that model errors are not significantly correlated with 5-day antecedent rainfall is consistent with a growing body of research showing that antecedent rainfall is often a poor surrogate for the actual watershed conditions controlling runoff generation and that the traditional use of antecedent moisture classes may not necessarily improve SCS-CN applications.

The authors should therefore place their results in the context of previous studies that have questioned the effectiveness of antecedent rainfall indices as predictors of runoff response. In particular, the papers by Soulis and Valiantzas (2012), Soulis (2018), and Palli-Gravani et al. (2026) provide useful evidence that watershed heterogeneity and changing watershed conditions can exert a stronger influence on runoff estimation than simple antecedent-rainfall classifications. These studies also illustrate that runoff response cannot always be adequately represented through conventional antecedent-moisture adjustments.

Rather than interpreting the lack of correlation with P5 as an isolated result, the authors should discuss whether their findings support the broader view that antecedent rainfall is not necessarily an appropriate indicator for adjusting CN values in event-based applications. Such a discussion would place the results within the existing literature and provide a stronger justification for the modelling choices adopted in the manuscript.

12. There is considerable repetition between the Introduction, methodological overview, and detailed method description. The manuscript could be shortened and made more focused by reducing repeated explanations of Hidropixel, the two modelling phases, and the limitations of static CN methods.

More importantly, the conclusions should remain closely aligned with the evidence. The study demonstrates a technically interesting implementation and identifies important limitations of the production model. It does not yet demonstrate a generally reliable or transferable flood-hazard tool. Statements such as “valuable tool for risk-informed land management,” “successfully captured,” “structurally robust,” and “critical to support proactive land management globally” should be revised to reflect the proof-of-concept nature of the analysis.

Minor comments

- The event-selection sentence stating that events were retained “only if they met this rainfall depth” appears incomplete. The rainfall threshold should be specified.

- Please state clearly how many events were available at each monitoring point. Events from the nested outlets should not be treated as independent observations in statistical analyses.

- The smoothing procedure and numerical implementation used to identify the hydrograph inflection point should be fully described. The uncertainty of the observed concentration time should also be quantified where possible.

- The statement that the distributed model “consistently outperforms” the lumped model should be reconsidered because the numerical improvements are very small.

- The reference given as “Baert et al., 2026: currently being published” should be replaced by a published article, a citable preprint, or removed.

- The manuscript requires careful language editing. There are repeated typographical errors, missing spaces, duplicated words, and awkward expressions.

In conclusion, the manuscript contains a useful dataset and a technically interesting distributed modelling exercise. However, the present form overstates model performance and transferability. A major revision should focus on reframing the contribution as a local proof-of-concept, clarifying the extent of calibration, validating or qualifying the spatial flow-path results, evaluating scale and computational requirements, and aligning all conclusions with the modest predictive performance and the single-catchment evidence.