General comments

This manuscript is well written, and the work done appears quite meticulous and informative from a methodological point of view, but I am not fully convinced of the novelty of this manuscript. The manuscript shows that GXAJ-S-SF outperforms GXAJ. It is self-evidently almost certain that a more accurate hydrological partitioning can be achieved when two important physical processes snowmelt and freeze-thaw are included into the model. Thus, it is certainly expected that GXAJ-S-SF will outperform GXAJ in a region that experiences the S and SF processes. Furthermore, since GXAJ consistently underestimates the runoff, and since the physical processes modeled in SF can only increase the runoff but not decrease it, it is a foregone conclusion that upon calibrating SF you will arrive at a better fit for GXAJ-S-SF than GXAJ. As far as I can tell, there are no novel or interesting findings regarding hydrological processes in this manuscript, nor are there meaningful analyses about the utility and information content of the hydrological models used beyond the goodness-of-fit metrics NSE, RBE, RMSE. Therefore, I recommend that after major revisions addressing the concerns I have elaborated below, this manuscript could be suitable for publication as a technical note.

Would it not be more meaningful to compare GXAJ-S-SF to a different hydrological model that also includes snowmelt and seasonal freeze-thaw? For example one of those models you mentioned in L96 – 112. Even if an actual model comparison is not done, it would be useful to discuss the differences and similarities in model processes between GXAJ-S-SF and other similar models with snowmelt and freeze-thaw functions.

It would be more rigorous to re-run the models with different priors. For example, there could be a configuration of GXAJ, with soil property related parameters set at an “annual average effective value” taking into account that the soil is frozen for 9 months of the year. This hypothetical configuration of GXAJ could possibly produce results as good as GXAJ-S-SF, but it is possible that this configuration of GXAJ was not tested because the optimization algorithm was stuck in a local minimum. Given the highly nonlinear processes involved in this model, I think that calibrating from a single set of priors may be insufficient.

L409 – 417: “The accuracy in simulating the initial freeze and initial thaw dates was validated against ground temperature data from meteorological stations within the basin (Fig. S5), indirectly confirming the simulated soil freeze-thaw processes.”

Could you provide citations or a more detailed discussion to support the validity of this point? Since freezing and melting both start from the top, and since the temperature data for verification was measured at the ground surface, simulating the correct initial freeze and initial thaw dates does not help confirm that the model has simulated the freezing depth correctly over the 9 months with frozen soils.

I think that the “modular approach” that you emphasize several times, including in the abstract and conclusion, is reinventing the wheel as it is just another name for loose coupling or one-way coupling, which is a basic hydrological concept.

After reading through the manuscript several times, I recognize that the bulk of the scientific contribution of this manuscript lies in the freeze-thaw process module in section 2.2.2. As shown in the results, it fits well with the measurements. However, I think some parts should be explained more clearly. What is the purpose of using two different representations of the soil layers in one model? Why not use the same layers for the computation of runoff, moisture and ET (Figure S1)? Does this mean that in the simulations, the humus layer could sometimes overlap with both the “upper soil” and part of the “lower soil”? And can the “upper soil” sometimes overlap with both the humus layer and the vadose zone? Does this not then imply that you need to interpolate some effective soil parameter values that may be inappropriate for the actual individual soil layers? How would this affect the runoff and discharge predictions? Furthermore, wouldn’t this mean that the parameter values you calibrate from field data do not have a proper physical meaning? I think that in order to reconcile the two different representations of the soil layers, it is inevitable that the calibrated parameter values are smoothed interpolations of the values that would actually describe each individual soil layer.

Specific comments

L192: Is saturation excess runoff a reliable way to partition snowmelt fluxes, which are fast and may often exceed the infiltration capacity?

L277: If you divide the SFD by the cube root of ASD to get SFD*, then the units of SFD* are [cm]^2/3. What does that physically mean?

L335: Please be consistent with terminology, do not interchangeably use primary parameters and major parameters.

L346 – 349: It would be helpful to mark in Figure 2 which processes in SNOW17 were calibrated with measured data, and which were not.

L349 – 352: I am not sure what this actually means. You definitely need more parameters for GXAJ-S than GXAJ, because you are adding physical processes. Are you saying that just because the -S module is compartmentalized in a module that means that you do not add more parameters to GXAJ? I think that this is a confusing way to describe one-way coupling.

L402 – 404: I think that the evidence of robustness is that the model did not perform worse during the validation period. Performing better during the validation period is not evidence of robustness. Conversely, performing better during the validation period suggests that you made some assumptions about the physical processes hard coded into the model, that were more valid during the validation period. Please discuss this in more detail if possible.

Figure 4: What are the dashed lines?

Figure 5: What is the dashed line?

L427: You earlier defined an RBE, but not an RE.

L539 – 534: I think that the formation of a saturated layer above ground under these circumstances is possible only for very coarse soils that are inefficient at soil water redistribution. This is unlikely to be a general behavior. If you are referring to a specific soil type, please describe it. If you are claiming this as a general behavior, please provide references.

L540: If matric potential is the primary driver of moisture movement, then how does gravity cause a saturated layer to emerge at the frozen interface?

L548 – 549: Which processes are you referring to, and what impacts? Are the processes you study not already naturally part of the local hydrological cycle and ecosystem?

L580 – L590: I feel that this is self-evident. It is a rehash of the widely known problem that data-calibrated hydrological models are often ‘right for the wrong reasons’. It is a nice discussion that fits the work done, but does not contribute new knowledge.

L600 – 602: This argument is valid only if the modeled processes are linear. The processes you have modeled are potentially too nonlinear and have too many interactions for this argument to hold.

L603 – 604: I agree that remote sensing errors would probably not affected the core conclusions of this manuscript, but not for the reasons you provide in L600 – 602. As I explained in my general comments, I think your conclusions are mostly self-evident.

L606 – 615: The benchmark model GXAJ you refer to is not a different model, but it is just GXAJ-S-SF without the snow and freezing capacities. This discussion is not meaningful because it is self-evident.

L615 – 617: What is the modular approach being contrasted against? What results did you show that support this statement?

L630 – 634: This is a great point, and could be expanded to make the discussion more interesting.

The authors present a modeling study on the hydrological impacts of snow and frozen ground dynamics in a topographically complex basin. The topic of cryospheric changes and their impacts on hydrology is both significant and timely. However, the authors should address several key issues in the current manuscript to enhance its quality before it can be considered further.

I think the novelty of this study is not sufficiently distinctive or well-highlighted. There have already been numerous modeling studies on snow and frozen ground dynamics in the Tibetan Plateau region, both the basin-scale and regional-scale studies are conducted. Moreover, the models employed in previous studies provided more advanced representations of snow and frozen ground processes, particularly in terms of frozen ground dynamics, compared to the model used in this study. Therefore, the authors need to consider how to better emphasize the unique contributions of this study in comparison to prior research. Here are some detailed comments:

1. In Figure 3c, it is evident that a significant portion of the study area is covered by permafrost. However, the Stefan model mentioned in the methodology is designed to model seasonal frozen ground. Did the authors separately account for the dynamics of permafrost in their study? If not, this could be a critical limitation that needs to be addressed or clarified.
2. Line 272-275: How was this threshold 30cm determined? Was a sensitivity analysis conducted to assess the impact of this threshold on the results? Providing such an analysis would help evaluate the robustness of the study's findings.
3. In Table 3, the authors utilized several data products from other studies. However, the accuracy of these datasets, particularly the snow depth data, which is critical for this study, has not been clarified.
4. Line 309-404: In points with high snow depth, there are significant discrepancies between the model results and the remote sensing data. The authors should investigate the underlying causes of these differences.
5. Line 412:415: For the simulation of frozen ground processes, verifying only the accuracy of the initial freeze and initial thaw dates is far from sufficient. It is also essential to validate the simulated soil temperature and soil moisture (including liquid water content and soil ice content). These variables are key to understanding how freeze-thaw processes influence basin hydrology. Therefore, the authors should provide validation results for these variables to demonstrate the reliability of the study's findings.
6. The ‘Results’ section is too brief and lacks depth in describing the characteristics of snow and frozen ground changes and their hydrological effects. For instance, there is insufficient discussion on how frozen ground processes alter soil temperature and moisture conditions, thereby influencing hydrological processes, as well as how snow changes directly impact runoff. Additionally, the manuscript does not adequately address how snow affects frozen ground processes and thereby indirectly impacts hydrology. Moreover, compared to the analysis of the differences in runoff simulations using various modules, I believe it would be more meaningful to explore how the synergistic changes in snow and frozen ground under climate change influence runoff in the study area during the past decades.
7. In the ‘Discussion’ section, the authors should focus on how their findings represent an advancement over previous research and then call back to the research questions outlined in the Introduction. Rather than including an extensive literature review, the discussion should emphasize the novel contributions of this study and its implications for the field.