Main comment

The authors take a global hydrological model (PCR-GLOBWB 2.0) and apply it over a large Alpine region. They propose several model adjustments to improve the model in order to better capture snow cover and discharge dynamics. I find it a very interesting study on a relevant topic and I see great potential in their work, however, I do not think that the analysis and manuscript at its current state fulfills the journal’s requirements and some clarifications and revisions are required. In my opinion, the strength of the manuscript (i.e. the usage of a large selection of forcing and evaluation data sets and the investigation of several processes) is its weakness at the same time, as it is getting more and more difficult to keep a concise and understandable workflow. Furthermore, I lack the overall justification of applying a global hydrological model to the Alpine regional scale, as there are better suited models available for this task. Why not using models that have the required process implemented already?

Specific comments

Title: Why is it hyper-resolution? If if would be a global application, then a 1km resolution run is termed hyper-resolution, I think. However, I do not understand why a regional application over the Alps in 1km should be termed hyper-resolution. Please clarify. Please be aware that in the snow-hydrological community, snow simulations in 1km are considered very course and not adequate to capture snow processes.

Line 1: I was wondering. Are there actually major rivers that do not originate in mountain regions?

Line 8: Please add in the abstract what is hyper-resolution for you? Please provide numbers.

Line 140: I do not understand ‘calibrating SWE agains a reagional SWE’. Usually one calibrates parameters such as the DDF using measured snow. Please clarify.

Fig. 1: For me this map was a bit misleading, as I was expecting you to simulate the runoff of the large rivers, but as I understood, you do not look at discharge from those rivers. This map shows another area than what you actually analyze and simulate. Please consider to adapt and show the exact modelling domain.

Fig. 2: As far as I understand, the implementation of the snow transport was not part of this study and hence should be part of the benchmark model in my opinion. The presentation and evaluation of the snow transport scheme was done in another study, right? The removal of this step of complexity in the analysis also could make your total analytical set-up more concise.

Line 259: What is the SWE threshold used in this study? Please state and explain how it was derived.

Line 310: You add the snow routing and calibrate it offline. What were the other model parameters of the model calibrated on? If they were calibrated on discharge, do not all parameters have to be re-calibrated again?

Line 313: Please be aware that the SWE data products you use also only are model output and the also these models are (for different reasons) often incorrect.

Line 342: What different climatic regimes are meant here?

Line 370: I am a bit skeptical about the applicability of the WB measure in the Alps to assess the influence of reservoirs. As you mention, it is also strongly impacted, e.g., by the the meteorological data used. In my opinion, your results (e.g. Fig. 7) showing the general deviations of the WB from zero are more an indication of the big uncertainties in precipitation and evapotranspoiration. Hence, the WB is a poor measure for reservoir influence and I am not sure what is then the validity of this measure to stay in the manuscript. To me the calculation of the WB does not provide new insights and only adds an unnecessary level of complexity to the study. Please think again what is the added value of calculating and showing the WB so prominently.

Line 402: In my opinion, the comparison of the meteorological input data sets with regard to the discharge performance (Fig. 4 G,H and I) should be conducted after the model routines have been improved. As seen in Fig. 4, the overall model performance seems fairly low with a median KGE barely above 0. If the models routine is not good enough, also a better precipitation input, for example, cannot improve runoff in a snowmelt-dominated catchment. Please think of moving the evaluation of the different meteorolgical input data sets at the end of you workflow.

Line 411: I do not see a general improvement of discharge. It looks a bit random to me. How do you come to the conclusion that the performance is ‘decent overall’. Please quantify.

Line 426: I am not sure I can see this improvement in the Fig. 5 G and H. Looking at Fig. G and H I do not see any improvement in model performance with increasing complexity of the snow routine.

Line 430: I do not see the evaluation of ‘melt rates’. You calibrate a DDF which is the same for all the area. How are there different melt rates depending on elevation? Please explain.

Line 462: Please explain the performance decrease in the shout-western Switzerland.

Line 491: ‘These changes have similar magnitudes as the changes due to different forcing data’. This is an interesting sentence, as you previously state that the forcing data has a very strong influence. Does this mean also the selection of the evaluation period has a strong influence?

Line 494 and Line 630: ‘Transferability to warmer climate conditions’: I do not think that the analysis at the current stat sufficiently supports this statement. You use an highly empirical approach for snowmelt and calibrate it to a specific time period. I do not see how the comparison of 10-year time slices can prove that the DDFs will be the same end of the century. In my opinion, the discussion of the transferability of DDFs in time also is not the focus of the study. As there are a lot of other interesting aspect to focus on, please consider to shorten/revise/remove this part.

In their manuscript “Hyper-resolution large-scale hydrological modelling benefits from improved process representation in mountain regions” Joren Janzing et al. describe a set of model extensions to PCR-GLOBWB 2.0 in order to make it more suitable for kilometre-scale modelling in mountainous regions. Together with model improvements in representing snow, glaciers, and soil, different forcing datasets are also tested. In essence, they found that the new model is capable of representing relevant processes in mountain hydrology quite well, even though the original model has been developed for large scale analyses with coarser spatial resolution. The manuscript fits well into the scope of Hydrology and Earth System Sciences. I found that the analyses carried out in the manuscript clearly show the added value of the most recent advances even though I think that some points require some more explanations and / or discussions. Apart from that I believe that the manuscript is an important contribution and I am looking forward to reading the final revised manuscript. Please find my comments below.

General comments

1. Structure of experiments / evaluations. The order of single steps is different throughout the manuscript. Abstract: forcing, snow, glaciers, soil; Introduction: snow and glaciers, soil, forcing. Hypotheses: snow and glaciers, “reviewing standard parameterizations” (I think that H2 should be rephrased in order to better reflect what was actually done. Do you mean reviewing and adjusting?), forcing. Methods and later results: Forcing, snow and glaciers, and soil. Conclusions: Snow and glaciers, soil, forcing. I was wondering if it would help the readers to agree on a consistent order of steps throughout the manuscript?

1. Water balance signature in L371 (and also Figure 7): I found the adoption of the Water balance signature not well introduced into the evaluation even though it seems to be a reasonable indicator. Firstly, I would recommend to better explain what positive and negative values mean. From what I could get from the equation (and later by referring to Salwey et al., 2023), it seems to me that a positive value suggests a gain in water, while negative values would indicate a loss of water. Is that true? Please consider adding a short description that could help the readers to better follow your interpretation later. Secondly, I was wondering why you call this water balance signature later in the results section “water gap”? This even more confusing, since positive values seem to be related to additional water rather than a gap. I would suggest to refer to the original term suggested by Salwey et al., 2023.

1. Glaciers in Figure 8: I agree that your modelling approach might be more suitable to regions of glaciers rather than individual ones. However, I really went through hard times reading Figure 8. Panels a) and b) are hard to read. Would be worth to increase the zoom level and to make glacier outlines smaller? Where is Mer de Glace (L447) on the map? I would suggest updating Figure 8 a) to d) in order to improve readability. The larger glaciers seem to have a positive mass balance bias, see panels e) and f), while in panel g) the model seem to have quite good average skill for glaciers with an area of more than 8 square kilometers. Why do we see a dramatic depletion in skill when looking at smaller glaciers? Why is 8 square kilometers chosen here? Is it related to the threshold in the Delta h method, proposed by Huss et al. (2010)? I was wondering if a regional mass balance, similar to e) and f), would better support your findings? Moreover, what remains unclear is whether the mismatch in glacier response time is related to differences in model (structure) or related to different forcings, when compared to Zekollari et al. (2020)?

1. Glacier initialization in 1990. How do initialize glaciers (area, volume) in your model setup when you deviate from the calibration period (which coincides with the data in Farinotti et al., 2019 for the early 2000)?

Specific comments:

L15: What do you mean by unidirectional?

L28: “thanks to heatwave”. In my opinion you should highlight that this was only possible through a very negative mass balance.

L60pp.: I think that there are lots of other references that support your statement here.

L74pp.: Please explain where exactly theses percentage values refer to.

L77pp.: Introducing one-way coupling would also suggest that two-way-coupling exists, too (see Pesci et al., 2023).

L113. I felt some statement is missing here before introducing meteorological forcing.

L135: Please consider rephrasing H2 (as suggested before).

L176: I am not sure whether “to guarantee” is correct in this context.

L239: DDF in general depend on land use. For the large-scale model it’s clear that working with an “average” DDF makes sense. However, I remember from own research that DDF shows a quite different behavior in forests. Given the increased resolution and the relevance of forests in the water balance in mountainous areas, I think it is at least worth to discuss this later.

L261p: I do not understand that snow is transported to glaciers, given that transport is only considered to non-glaciated cells. Could you please explain this please?

L271: Do you mean lower albedo?

L294: If glaciers can only grow to its original extent, how do you realize to initialize the glaciers with a larger extent in the past?

L311: I am sorry if I missed this important detail but for me it’s not clear if you calibrate a single parameter (e.g., DDFmin) for the entire domain or catchment-wise. From the table in supplement, it seems to me that it’s a single value only which is valid for the entire domain after calibration.

L378: Why is snow calibrated only in Switzerland (I hope that I understood it correctly)? Here you focus on both Switzerland and Austria?

L383: How do you evaluate glacier geometry evolution? Later you explain that this was only done visually.

L442p: Her, I think it would be interesting to provide a few more details what we see, e.g., the values around zero for small snow fractions. By the way: Is snow fraction the percentage of precipitation that is solid or how is it defined?

L491pp: When comparing the drop in median for the different periods, it would be relevant to mention them in the text. Given the very good representation of SWE in the warmer period, is there any observation regarding the glaciers?

Figure 12: Adding KGE or some other score would be helpful. Why does the full model compute a very high peak for Massa. Given that it is a 10 yrs. average, it seems to be a quite high event.

Technical comments:

Figure 4: Unfortunately, the legend hides important details of the distribution. Would it be possible to make its background transparent? See also Figure 5, 6, 11

Figure 10: KGE refers to the upper row A-C, while KGESS to the bottom row (D-F)?

References

Farinotti, D., Huss, M., Fürst, J.J., Landmann, J., Machguth, H., Maussion, F., Pandit, A., 2019. A consensus estimate for the ice thickness distribution of all glaciers on Earth. Nature Geoscience. https://doi.org/10.1038/s41561-019-0300-3

Huss, M., Jouvet, G., Farinotti, D., Bauder, A., 2010. Future high-mountain hydrology: a new parameterization of glacier retreat. Hydrology and Earth System Sciences 14, 815–829. https://doi.org/10.5194/hess-14-815-2010

Pesci, M.H., Overberg, P.S., Bosshard, T., Förster, K., 2023. From global glacier modeling to catchment hydrology: bridging the gap with the WaSiM-OGGM coupling scheme. Frontiers in Water 5, 1296344. https://doi.org/10.3389/frwa.2023.1296344

Salwey, S., Coxon, G., Pianosi, F., Singer, M.B., Hutton, C., 2023. National‐Scale Detection of Reservoir Impacts Through Hydrological Signatures. Water Resources Research 59, e2022WR033893. https://doi.org/10.1029/2022WR033893

Zekollari, H., Huss, M., Farinotti, D., 2020. On the Imbalance and Response Time of Glaciers in the European Alps. Geophysical Research Letters 47, e2019GL085578. https://doi.org/10.1029/2019GL085578

This study describes the implementation of several modifications to an existing Large Hydrological model and evaluates the effects of implementing those changes stepwise. Specifically, it evaluates the implementation of a snow transport scheme, an altered snow model parametrization, improvements related to calibration of that snow model, a new glacier model, and altered soil parameters. The authors also evaluate model differences related to meteorological forcing uncertainty. 

General comments:

Overall this is a well-organized paper that clearly tracks the series of implemented changes. The authors justify their choices of evaluation data and techniques, and provide sufficient evidence for most conclusions. However given the complexity of the study, there are a few places where further clarification, justification, or tempered conclusions are needed.

The only substantial piece of additional justification pertains to Figure 7 and your conclusions of performance in non-regulated versus regulated catchments. While the correlation of performance with water gap sign is quite clear for the second and third row, I’m not totally convinced how well the value of the water gap fraction works in identifying natural vs regulated catchments (to my eye both improvements and deterioration of performance are pretty evenly split between those with and without reservoirs marked as + and o). This is important because you later equate locations with performance improvements to natural catchments and locations with deterioration to regulated catchments (Table 3 and around line 565 and 606). Can you provide any additional justification for this association over your domain? Since the Salwey study was over Great Britian it may not transfer well to more inland mountainous locations. How do you know that another variable isn’t controlling the relationship between WB and performance improvement? For example, maybe improvements in the model occur at locations that correspond to thin soil in the real world and where the hydrological response is flashier (since you effectively biased your model to better performance at such locations). Such locations might have limited capacity to store water longer term which would correlate with WB and could appear as a signal in non-regulated catchments.

Other Specific comments (generally minor):



Line 37: “regional to local-scale” can be interpreted differently. Please be more explicit.

Figure 1: The range of colors on the map doesn’t look like it fully matches those on the color bar (which doesn’t seem to have the darker greens and bluer greens). Is there some sort of transparent overlay of other colors on the map?

Line 160: Since the precipitation isn't downscaled to the resolution of your model, it might be clearer to specify “(3) CERRA-CHELSA, a mixed dataset with temperature from the Copernicus European Regional ReAnalysis (CERRA) further downscaled using the CHELSA algorithm and precipitation data directly from CERRA-Land.”

Line 180-221: This section needs some clean-up to help clarify details. You mix in both data required for evaluation and ancillary data required to run the model (e.g. RGI) or produce metrics (e.g. snowfall fraction, PET). It’s hard to sort out what is what, especially at a first read. In some cases, datasets mentioned don’t appear in the Table (e.g. RGI, GLAMOS) and in others they appear in the table but aren’t discussed here (Farinotti glacier volumes). You might try splitting up the discussion of strictly evaluation data versus ancillary data needed to run the model or compute metrics.

Lines 237-251: What values were chosen for m_m and m_p? Do these not alter the calibration? - at line 320 you state that you only calibrate the two DFF values.

Lines 255-270: Please reword to clarify the interactions between snow and glaciers regarding both lateral transport, accumulation from snowfall, and melt. Including an arrow for lateral transport in Figure 3 may help. In particular I think it would help to more explicitly describe how the model treats the three possible cases: transport “onto” glaciers (i.e. non-glacier to glacier; I think this is what you have implemented and focus on), transport “off” glaciers (i.e. glacier to non-glacier;  maybe this is what you restrict from occurring?), but also clarify whether lateral transport still occurs from non-glacier to non-glacier cell. On glaciers, is the laterally transferred snow considered as a separate source from the snow accumulation from snowfall? For example, is laterally transferred snow converted to glacier ice based on its mass but the snow accumulated from snowfall sits “on top” of the glacier and must melt off? (“the glacier only melts when it is not covered by snow”). Or are the two sources of snow put into the same reservoir which can only convert to glacier ice on sept 1? (in which case I guess there’s no glacier melt that season)

Line 268: “The glacier ice reservoir only decreases when…”

Line 288-295: This is also confusing and needs clarification. Is the Huss et al relationship applied to the distribution of elevations from combining all the rasterized glacier cells across the domain? Or do you group individual rasterized glacier cells as belonging to specific real-world glaciers based on where they are located? And then you use the distribution of model elevations associated with those real-life groupings? Otherwise wouldn’t each rasterized glacier cell have an elevation change in direct correspondence to its mass balance change?

Line 303-308: I would describe this as a sensitivity experiment. Do both the thickness of the upper soil layer and the total soil thickness vary spatially in the model? When you state that your sensitivity test is to halve the upper layer thickness it sounds like it varies over the region, but then when you state the maximum upper layer thickness it sounds like it is spatially uniform.

Lines 369: afterwards this is referred to as the “water gap”, so please put this in parenthesis somewhere here.

Line 414-417: Check references to figures and forcings. I think there is a mistake here where either Figure 4H should read 4I or one of the references to the forcings should read CHELSA instead of CERRA-CHELSA.

Lines ~425/Figure 5: It might be helpful to explicitly state that the large amount of SWE present during the summer in the benchmark (at high elevations) and ERA5 data (at middle and high elevations) is due to the presence of snow towers and that the inclusion of snow transport (present in the runs labelled "transport", "uncalibrated", and "full run") removes this unphysical effect. Also, please discuss the differences in SWE magnitude between the LHM model versions and the CERRA-Land analysis – does it also have snow build up in some cells, but resets to near-zero every year?

Figure 5: This is a really small point but your vertical axis starts a zero in plots a and d but below zero in plots b,c,e,f.

Line 431: There is no calibrated snow run labelled in the figure. Are you using the Full run as a proxy for it?

Line 442-443: I don't think I agree with this conclusion. Based on Fig 7a there doesn't seem to be much correlation with water gap sign and I don't see a pattern of KGESS associated with either + or o in plots b,c. I do see a correlation of increased (decreased) KGE skill at locations with higher (lower) snowfall fraction with perhaps a weak dependence on glacier fraction. (The connection between performance and water gap sign for the snow/glacier modules and soil change are much more apparent).

Figure 6: This is a useful figure and tracks the progression of alterations nicely. Based on this, I'd suggest moving the KGE plot below plots a-f so that the full figure can take up more width on the page.

Figure 7: I suggest labelling snow fraction as “snowfall fraction”.

Figure 8: I don’t find plot 8i helpful/insightful as currently presented and discussed. It would be fine to remove, retain the stated numbers in the text regarding the equilibrium experiment and just leave the model-obs comparisons as shown in plots 8g,h.

Figure 8: The glacier outlines really obscure the elevation change results. Is it possible to improve on these maps? Perhaps it's possible to use grey in all four maps to represent non-glaciated regions and to use a color palette for the elevation change that goes through white at zero instead of grey?

Figure 8: I suggest removing the sentence “Finally, the response of glaciers to continuous forcing with the mean mass balance from 1990–2018 (see Section 2.4).” from the caption.

Line 461: You subsequently define rainfall-dominated catchments to be Ps/P < 30% and improvements in Fig 7e are all for snowfall fractions higher than this value.

Line 491: Are the KGESS color bars the same in Fig 11 and 4? If so the changes in skill between non-calibrated and calibrated periods appear smaller on average than the effect of different forcing data (although the spread in values they cover at the extremes is close)

Figure 11: It's hard to distinguish the blue and black colors used, particularly in the legend. Try a more differentiated color choice.

Line 505: Your conclusion that “The representation of soil moisture … needs to be improved in LHMs”: This might be true but I would argue your results also suggest there is a need to compare observed estimates of soil moisture and simulated values in a more representative manner. (I don’t think you need to do this yourself in this paper.)

Figure 12: I suggest removing the label ‘B.’ from the first plot as it looks like a location you will refer to afterwards. Instead specify in the caption:  Swiss canton of Grisons (inset shown in plot A)

Line 618: It might be worth specifying that these improvements apply even without calibration.

Lines 630: I think this claim would require additional testing. You only test about 0.5 degrees away from your calibration period temperature (local increase) but for a climate change study you’d probably want to model a global mean temperature increase of another 2 degrees (and more locally). This would push your model quite a bit further than you’ve tested.

Line 656: I don’t think it’s fair to consider the CERRA-CHELSA forcing dynamically downscaled for the given model setup since the precip (likely the most important control) is taken as is from CERRA-Land at 5.5km and this is substantially coarser than your model at ~1km. Whereas the other products were downscaled (statistically) to 30”. The way it is currently worded it sounds like the expectation was dynamical downscaling should yield improvements over statistical downscaling but I don’t think you tested this hypothesis fairly (at similar resolutions) in your setup. I think you can still conclude that the choice of precip forcing did not make as large a difference on the resulting discharge accuracy as one might naively expect given the higher correlation and lower bias of the CERRA-CHELSA precip with observations). I think the conclusions as worded at lines 598-601 are more consistent with your experiments.

663-664: The final sentence is really vaguely worded. Omit or add some more specificity on the types of questions you think the model is ideally suited for.

Line 701: 50 meters? Specify that E_max and E_min are measured in meters.

Line 710: What is lower-case m? the units of total glacier mass loss specified in units of meters? To me, writing (m) reads like “is a function of the variable m”. I suggest rewriting to avoid this with something along the lines of: “This is done by means of a scaling factor f_S. This scaling factor is the ratio between the total mass loss over the glacier ΔM (units of m. water equivalent) and the integrated normalized change in surface elevation, …) The units of all the subsequent variables should be clear from specifying those of ΔM.

Technical edits:

Line 136: downscaled

Line 554: “than that of our LHM” or “than the resolution simulated here”