Overall, this manuscript presents a substantial amount of analysis on snowmelt runoff characteristics across a large sample of basins and multiple models/products, and the overall writing and presentation are generally clear. The topic is relevant and the study has clear value for large-scale model evaluation in cold-region hydrology. In particular, the authors made considerable efforts in constructing the intercomparison framework and diagnosing runoff volume, peak, and timing during snowmelt periods. However, several issues remain insufficiently addressed, especially regarding the parameter calibration and the formulation and interpretation of the newly proposed RI metric. My detailed comments are as below.

Major comments:

1. A major concern is the issue of parameter calibration. It is well accepted in hydrological modeling that calibration can strongly affect model performance, especially that hydrological models typically involve many empirical assumptions, conceptual runoff generation schemes, or regionally variable parameterizations. In practice, model performance may differ substantially before and after calibration, and parameter values can also vary greatly across climatic and physiographic conditions. However, the models included in this study do not appear to have a consistent calibration status: some are calibrated, some are uncalibrated, and some may be only partially calibrated. This compromises the comparability of the intercomparison and makes it difficult to attribute performance differences purely to model structure or process representation. This problem seems inevitable since the study uses existing model outputs rather than builds its own modeling frameworks. However, this problem should be emphasized in the manuscript (in many places) and its impact on the results should be thoroughly discussed.
2. The explanation of the proposed RI in Section 2.2.4 should be strengthened. First, the manuscript does not clearly define the “complexity level/group” used in the RI calculation, including how basins were grouped along the CI gradient and how the corresponding CI values for each group were assigned. Second, the rationale for combining normalized SMAB and normalized slope into a single Euclidean-distance-based metric is not sufficiently justified. At present, it remains unclear how reliable RI is as an integrated measure of model robustness, and whether it can meaningfully balance overall bias against sensitivity to increasing basin complexity. Since RI appears to be a newly proposed metric in this study, the manuscript should provide stronger justification of its formulation, interpretation, and practical usefulness.
3. I recommend that the authors moderate the novelty claims related to the evaluation framework. The volume/peak/timing analysis adopted here is useful and appropriate for process-based diagnosis, and I do not object to its use in this study. However, similar types of diagnostics have already been widely used in hydrological model evaluation, including in snow-related runoff studies. Therefore, some statements currently appear overstated. For example, the conclusion states that “This framework advances model intercomparison by moving beyond average bias evaluation,” but many previous studies have gone well beyond average bias and have used multiple performance metrics and more process-oriented diagnostics. I suggest rephrasing such statements to avoid overstating methodological novelty. More generally, the manuscript would benefit from another careful round of language revision, as several statements appear stronger than the evidence supports.
4. I also suggest revising the title of Part I. At present, the emphasis on “robustness” seems somewhat overstated, as the current emphasis on robustness may not fully reflect the primary contribution of the manuscript. The paper is fundamentally a global-scale evaluation of snowmelt runoff performance across large-scale hydrological models, and the title would be more accurate if it reflected this primary focus more directly.

Other:

1. In the abstract, “little is known about their SMR performance” appears overstated. In addition, “ISIMIP3a and ISIMIP2a” are mentioned without sufficient explanation, and I suggest simplifying or removing these terms in the abstract.
2. In the second paragraph of the Introduction, the statement that SMR-related simulations remain unsatisfactory should be qualified more carefully. Snow-related runoff can in some cases be easier to simulate because of its strong seasonality and regular hydrological response, whereas runoff simulation in arid regions is often more difficult.
3. Since the gridded runoff is at 0.5° resolution while the MERIT basins are much finer, the manuscript should discuss the possible impact of this scale mismatch on routing and the resulting evaluation.
4. The residual water-balance estimate is acceptable as a pragmatic screening proxy for identifying snowmelt-dominated basins, but it should not be interpreted as a rigorous quantification of snowmelt runoff contribution, because changes in catchment storage, delayed groundwater release, and rainfall–snowmelt interactions are not explicitly accounted for.
5. ERA5 SWE is used to define snow periods, but the manuscript should discuss the reliability and possible limitations of ERA5 SWE for this purpose, especially in complex terrain.
6. The description of the observed discharge data source needs clarification. The manuscript states that discharge data are obtained from GSHA, but it is not clear whether GSHA directly provides the daily discharge time series used here. Please clarify this point.

This study presents a large-scale evaluation of snowmelt runoff (SMR) simulation across 15 global hydrological models and runoff products using 1,513 snow-dominated basins worldwide. The authors evaluate three key hydrograph characteristics: total runoff (Qsum), peak flow (Qmax), and centroid timing (CTQ), and introduces a new robustness index to quantify how model performance degrades with increasing basin complexity. The results show that most models underestimate runoff magnitude and predict earlier snowmelt timing, and that model performance degrades as basin complexity increases. Overall, the manuscript is well written and provides a valuable large sample diagnostic of model performance. The concept of evaluating model robustness across environmental complexity gradients is particularly interesting and could offer useful insights for model development. However, several issues need clarification before the manuscript is suitable for publication.

Major comments:

1. The robustness metric is central to the manuscript but requires further justification and interpretation. The index combines the Stratified Mean Absolute Bias (SMAB) and the slope of bias vs. complexity into a Euclidean distance metric. Why was Euclidean distance selected as the combination method? Though the authors mentioned it was done in prior studies, it would be more helpful for readers if some justification can be added here. Also, is the robustness index comparable across different runoff metrics (Qsum, Qmax, CTQ)?
2. The basin complexity index is defined as the sum of normalized DEM, DEMstd, LAI, and PFTh. While this approach is straightforward, the four variables may not contribute equally to hydrological complexity. Some factors, like elevation and topographic variability, may already be strongly correlated. It would be better if the authors can discuss why these four metrics are selected and whether dependencies among these variables influence the analysis.
3. In this study, all runoff outputs are routed using RAPID to ensure comparability. However, the manuscript assumes that routing effects are minimal because long-term mean metrics are used. This assumption needs more justification because routing parameters can influence peak flow magnitude and CTQ. The authors should either provide a short sensitivity analysis, or cite studies showing that routing effects are negligible at the spatial scale considered.
4. Page 19, lines 340: what’s the potential reason that ISIMIP 3a outperforms ISIMIP 2a in simulating Qsum and Qmax, is it because of the forcing data?
5. The manuscript concludes that GHMs outperform LSMs for Qsum and Qmax, while LSMs perform better for CTQ. This is an interesting finding, but the discussion remains somewhat speculative. The authors attribute the differences to energy-balance representations and runoff parameterizations, but more concrete explanations or references would strengthen this argument. In addition, some differences could result from calibration, forcing datasets, and resolution differences. These factors should be discussed more carefully.

Minor comments:

1. The snowmelt period is defined as the interval between maximum SWE and when SWE falls below 1 mm. This definition may not capture multi-peak melt seasons or rain-on-snow events. A brief discussion of limitations would be helpful.
2. ERA5 SWE is used to define snowmelt timing. However, ERA5 has known biases in mountainous regions. The manuscript should briefly discuss how this may affect the analysis.
3. “Stern conditions” is not commonly used in scientific literature, especially in hydrology or Earth system science papers. It’s a bit awkward in this context. Do you mean “challenging conditions” or “complex environmental conditions”?
4. Page 18, in the title of Figure 6, change “blue circles denote GHMs, yellow squares denote LSMs, green triangles denote DGVMS, and grey diamonds denote data products.” to “circle denote GHMs, squares denote LSMs, triangles denote DGVMS, and diamonds denote data products.” Because shapes represent model types and colors shows the robustness.