The study from Hu et al. entitled ‘Modelling rock glacier velocity and ice content, Khumbu and Lhotse Valleys, Nepal’ proposes a model to infer rock glacier ice content based on InSAR velocity measurements. The model is calibrated based on the observational data of the Chilean Las Libres rock glaciers and validated using data from four rock glaciers in the Alps, before to be applied in NE Nepal. The objective is to estimate the water storage of the rock glaciers at the regional scale.

The research is very comprehensive, the approach is novel and valuable for future studies in similar mountain permafrost environments. The study’s scope is well suitable for publication in The Cryosphere. I have no major concern regarding the main methodology and results, but the paper could definitively be improved by modifying the structure, clarifying some steps of the procedure and extending the discussion. These main points are further explained thereafter. Detailed comments are listed at the end of the review.

Workflow and structure:

Due to the extensive work of the authors, the complex articulation of the research steps, the multiples datasets and areas used for the model calibration, validation and application, it is sometimes hard to follow the workflow. I believe that some adjustements of structure may easily help the reader to go through the paper and understand the main elements.

In the abstract (l.15-18), at the end of the introduction (l.58-65) and in Fig.2, the workflow follows a logicial order, starting with the model design and finishing with the model application. However, the methods and results sections are upside-down, starting with InSAR data and continuing with the model. Consequently, we go back and forth between the rock glacier sites used at the different steps and the reader gets a bit lost.

For example: 3.2.5. is far after 3.2.1, although the application is based on InSAR. And 4.2 is coming just after the InSAR results in Nepal but the rock glacier velocity mentioned at l.292 is in that case simulated on swiss rock glaciers.

In addition, I think that Fig.4 is a result and should be added in part 4. The extrapolation to whole Nepal may also be considered as a result (as you also somewhat acknoweldge by listing it as a main conclusion at l.478-480).

One suggestion of structure (both for methods and results): model calibration, model validation, sensitivity analysis, model application based on InSAR, regional extrapolation. And then really focus the discussion on the limitations and prospects.

InSAR coherently moving parts:

Something is missing to fully understand your definition of coherently moving parts and why you decided to do so.

At l.109, I don’t understand the point (2). It seems to me that it may tend to exaggerate the rate if artifically discarding low velocity. At l.111-112: partly same question: why only higher than 5 cm/yr in more than half of the periods? I don’t think it falls into the definition of what is coherent or not, at least not from an InSAR point of view. And from a process point-of-view, what about areas that are coherently not moving (or slowly)?

Do you assume that under < 5 cm/yr there is no more activity/ice, and consider the previous inventory outdated? If yes, it makes somewhat sense but it is important to clearly explain it in the methods and better discuss it in Section 5. If not, one consequence on the results is that the covered areas are much smaller than the inititial inventoried landforms (Fig.6, especially for a and b). Did you then extrapolated the ice/water volume to the whole rock glacier, and if not, which potential understimation may it cause, also for the regional extrapolation presented in Section 5.1?

Method justification vs discussion:

Section 5.2 proposes a relevant list of elements (l.372-375) that can be seen as limitations and supposed to be used to discuss the validity of the approach. However, the way most points are discussed is a bit frustrating: it sounds more like justifying the choices (which should be part of the methods) than acknowleging the limitations and putting the results into a larger context.

For example: at l.403-407: ‘we infer that these rock glaciers develop in a warm permafrost environment for the following reasons: …’. This is not really a discussion, rather an explanation for a chosen assumption. In general for 5.2.2: I don’t think the question of the warm permafrost assumption has not been really introduced before.

At l.437: ‘We introduce this concept because it corresponds with the general model setup.’: Saying that it follows the design you chose is not really an explanation, neither a discussion. Overall in 5.2.5: Before justifying it, explain what could be the problems.

In 5.2.6: Ways to tackle the issue are presented (l.451), but the issue itself is not really introduced (saying that the rheology of rock glaciers in Nepal are not necessarily similar than Las Libres).

Additional thinks that could be further discussed in Section 5:

• Elements previously mentioned regarding the coherently moving area definition and the update of the inventory using InSAR-kinematics.
• How to be sure that the velocity you are measuring is really related to rock glacier creep? As single SAR geometries are used, the values are initially along LOS and could f.ex correspond to subsidence due to melting.
• In the model, there is no water at all in the active layer. Is it realistic? Would it change the results if adding a water content as well?

Detailed comments:

1. Title: As you actually used velocity measurements as input to the model in your study area, a title such as ‘Modelling rock glacier ice content based on InSAR velocity, Khumbu and Lhotse Valleys, Nepal’ would sound more correct to me.

2. l.14 and 16: Repetition ‘model to infer ice content of rock glaciers’ could be avoid.

3. l.21-22: This sentence could be simplified. For ex: ‘Due to the accessibility of the model inputs, the approach is easily applicable to permafrost regions where…, and thus valuable to estimate the water storage…’

4. l.29: ‘The potential hydrological value of rock glaciers, and thus their importance in terms of hydrological research… Corte (1976); despite this, research...’: long sentence, with strange structure and quite some repetitions. Possible to simplify?

5. l.35: ‘triggers’ instead of ‘produces’? / ‘rock slope failure and mountainside collapses’: what the difference?

6. l.38: Could start the sentence directly with 'Jones et al. (2021)…'

7. l.39-40: ‘The relative importance of rock glacier ice content compared to glaciers in the region is 1:25, …'

8. l.42-43: Maybe a personal preference and definitively a detail: Easier to write without ; and making two sentences.

9. l.45: I don’t understand ‘the likelihood of glacier-rock glacier transition’ part and I believe you are anyway not discussing it in this paper. I would suggest: 'However, there is a lack of modelling studies to test these postulations and assess the hydrological impactions of the glacier-rock glacier transition’. But, if the point of it is to potentially use the results of this study as a baseline, with future updates to see the change of ratio (ice content of RG compared to G), you can also add something about it in the discussion (prospect).

10. l.47-48: Contradicts with the previous paragraph where you refer to Jones et al. (2021), who have provided quantitative information concerning ice content. You may consider inverse the paragraph order, and replace “absence of quantitive information” by something like “we have little quantitiative information”.

11. l.63-65: You are not modelling the kinematic response, you are measuring it and modelling the ice content. Rephrase to for ex: ‘We apply the calibrated model for five rok glaciers… and model their ice contents based on remote sensing…’

12. l.67-68: The Khumbu and Lhotse glaciers draining… to remove the unecessary parantheses.

13. l.73: Altitudinal limit of permafrost: missing a reference here.

14. l.78: ‘For the period of 1994–2013, recorded accumulated annual precipitation was 449 mm yr-1, …

15. l.83: You give a reference for the delineated RGs, but not for the DCG.

16. l.85-86: See main comment: here the structure is counter-intuitive (opposite of the introduction).

17. l.93: I guess here you mean ‘We selected the interferograms…’

18. l.97: Missing an information about the final resolution you achieve.

19. l.100: How do you know it is stable? Based on visual interpretation? Good to say it. And rather say: ‘supposed to be stable’.

20. l.101: The water vapour is not delayed, the phase is. The end of sentence is also a bit clumsy I think. Maybe ‘atmospheric and ionospheric effects including phase delay due to water vapour can be effectively removed because they lead to long-wavelength spatial artefacts and...’

21. l.102: ‘because these lead to long-wavelength artefacts across the region’.

22. l.105: ‘projected ... onto the downslope direction’.

23. l.107-108: The start of the sentence is about the criteria to select valid pixels, while point (1) describes which pixels were discarded. Phrasing in (1) could be inversed (> 0.3 are kept).

24. l.109: I don’t understand point (2). It seems to me that it may tend to exaggerate the rate if artifically discarding low velocity. See main comment about InSAR.

25. l.111-112: Partly same question as my point 24: Why that? See main comment.

26. Table 1, caption: List of … interferograms used in the study.

27. Figure 2: As I understood, you just used the coherent part as input to the model, so it may be enough to write ‘InSAR-derived kinematics on coherently moving parts’.

28. l.123: Since you are not assuming shear horizon at depth in the model, it sounds weird to have it mentioned at the second line of the section, without then acknowledging in a way or another the limitation before the discussion.

29. l.134-137: I am struggeling to understand the point of this part. Too detailed or not enough. What is happening when the critical volumetric debris content is reached? What is the implication for this study? If it is important, one would like to know the actual relation betwee the ice-debris mixture strength paramater, and the debris content.

30. l.186 and 190: Little detail: not sure it is necessary to have ‘collected by’/’detailed in’ before references.

31. l.195: ‘… by Arenson and Springman (2005a) who evidenced a parabologic relationship…’

32. l.201-204: Instead of using 4 lines, you could just entitled the equation lines: Scheme 1: u_s = / Scheme 2: u_s = / Scheme 3: u_s =

33. Figure 4: It could be moved to Results. Also, since you numbered the Schemes 1-2-3, it would be good to label the subplots a)-c) accordingly, by adding subtitles to make it easy to understand.

34. l.213-216: Long sentence, hard to understand since it is a double-validation of both the velocity and the ice content. May find a way to rephrase / divide the sentence.

35. l.234: Air density: provide the actual values.

36. l.245: Currently not really understandable: what is the usual value range in reality?

37. Table 3: Necessary information? Could be moved to Supplementary, to shorten a bit the really heavy method section.

38. l.255: ‘Active layer thickness was determined as the mean value over the extent of each rock glacier, based on the 2006–2017 estimate from the…’

39. l.259: Is the estimate of water based on the whole inventoried rock glacier or the coherently moving part? See main comments.

40. l.265: In a way, this table is already a results, as it is based on the coherently moving parts of the rock glaciers, presented later in the paper.

41. l.267-268: It cut the workflow to separate InSAR to the model application. See main comment about structure.

42. l.274: ‘...approximately similar values’

43. l.276: ‘...during the observational periods’. You may also emphasize somewhere what the timseries vary from site to site.

44. l.279: ‘since 2010’: The evidenced acceleration is based on one value also, i.e. the difference between the two last acquisitiond dates, right? Maybe writing ‘between 2010 and 2015 acquisitions’ would be more correct.

45. In 4.1: More references to the Fig.5 subplots would help the reader to make the link.

46. Figure 6: Missing scales.

47. l.293-296: Partly repetition with Methods.

48. l.301: Reference and inference ice content: why not simply saying ‘observed’ vs ‘modelled’?

49. l.301-303: Missing references to Scheme 1/3 graphs (Fig. 7, 9). If you think there are unnecessary, you may consider moving them to Supplementary.

50. l.303-304: ‘However, the above bias is not statistically useful for correcting the modelling results due to the limited amount of validation data.’ Not clear, could be more discussed, here or in Section 5?

51. Figure 7: Is it correct to say that the intersect of the yellow & blue lines correspond here to the 'truth' (observed values / references)? If yes, it would be useful to highlight it better (encircle it for ex).

52. Figure 8/9, captions: Add full captions instead of referring to 7.

53. l.325: ‘The model has higher sensitivity to the surface slope angle...

54. l.327: ‘...the model is mostly sensitive to...’

55. l.334: Interred ice content based on Scheme 2, right?

56. l.336-339: Separate the information related to % and total volume, and add a reference to geometrical information from Table 4 would help making sense of it.

57. Section 5.1: I would say that it is a result. See main comment.

58. l.364-365: Based on which study? Jones or yours? As you refer to previous research just before, it is not fully clear.

59. l.367: ‘… across the entire Himalayas’

60. l.373: ‘(3) absence of shear horizon’ (also at l.408).

61. l.382: ‘… to evaluate the stability…’

62. l.385: You could probably cut ‘This is not surprising’.

63. l.391: ‘creep parameter’ is only mentionned once before and referring to n, not A (l.192). A is described in more general terms at l.128.

64. l.413: ‘This short-term feature of rock glacier kinematics is assumed to be insignificant…’. And it would be more logical to move this statement at the end of 5.2.3.

65. l.421: Add reference to Fig.10.

66. l.428-429: ‘Thus, the uncertainty introduced… is unavoidable.’ I don’t see the causal link with the previous sentence here. It is not because Cicoira et al. (2020) also had accuracies at the same level that it is unavoidable.

67. l.437-438: ‘We introduce this concept because it corresponds with the general model setup.’ That is no explanation… Just saying ‘we did it because we designed it that way’…

68. l.443-445: Without more explanations, this is not understandable.

69. l.451: Which issue? You have not mentioned an issue yet.

70. l.465 and l.481: ‘surface-velocity-constraints’: surface velocity would’nt be enough? To avoid a long word in 3 parts.

71. l.469: ‘emerging’: What does it mean in that case?

I read the manuscript with great interest and anticipation, and I do like to congratulate the authors on their effort of presenting a manuscript that is, editorially, well written and properly developed. However, I do have some fundamental concerns with the approach and assumptions used and I therefore do not recommend that the text is published in The Cryosphere as presented. Unfortunately, this manuscript is following a trend that I have observed in recent years, in particular where authors publish their work without having sufficient field data to support it. I do understand that there are only a few data available on rock glaciers, but that is a fact we must accept, which also means that theoretical approaches that heavily depend on reliable field data for calibration and validation simply should not be published. Therefore, I strongly believe that the approach shall be revisited before the authors submit a revised manuscript. I will address individual aspects below, but the fundamental problem I have with the proposed approach is that following the author’s approach, we would infer that the ground ice contents of the rock glaciers in the Alps, for example, is increasing in response to climate change. Several studies show that the creep velocities of rock glaciers are increasing in the Alps (Note: I specifically do not add many references in this paragraph as I’m sure the authors are well aware of this literature and I would not be able to pay justice to all the authors that have contributed to some of the elementary statements I use). So, if we were to calculate the ice content using today’s surface velocities, and then repeat the calculation again in 10 years it is very likely that an increase in ground ice content would result. This is a fundamental mistake, illustrating that it is impossible to link the parameters used with rock glacier surface velocities in order to estimate ice contents without making huge mistakes. The change in velocity that we are currently monitoring, mainly in the Alps, is related to permafrost degradation in the rock glaciers, specifically the warming of the ice and potential increase in unfrozen water content. Both impacting the creep parameters. While the actual ground ice content may not even change, creep velocities increase in response to warmer conditions, another aspect that was not included in the proposed model where ground temperatures are assumed to be constant. Ground ice melt in rock glaciers in response to climate change is extremely slow because of the latent heat. The higher the ground ice content, which would in tern benefit higher creep velocities, the more latent heat is stored in the ground, requiring more energy (time) in order to melt the ground ice. In other words, there are multiple processes at play that influence the ground ice content, the degradation and the velocity. The simplified approach presented does not consider this complexity, which, as illustrated above, could result in erroneous conclusions.

I do understand that specifically section 5.2 addresses the uncertainties, but if the authors would read those lines carefully, they would probably agree that they are telling the reader that there are so many uncertainties that even the authors are no longer sure if the approach is realistic or not. This is a dangerous approach because on the one hand the manuscript provides a very clear approach on how to calculate ice contents, but at the same time, the paper also says that it may actually all not be correct because of all the simplified assumptions used. For example, I appreciate that the authors indicate the acceleration in one sentence on line 378. However, this does not resolve the major flaw of the paper indicated above. Like many researchers, the authors assume some sort of steady-state behaviour, which is typically an accurate assumption when modelling glacier dynamics. However, rock glacier kinematics responds on different time scales and therefore it is inaccurate to use assumption tailored for quasi steady state conditions on a process (landform) that is constant transition, always lagging behind modern climate conditions.

On line 481 the authors conclude that “This study demonstrates the effectiveness of inferring ice content of rock glaciers by using a surface-velocity-constrained.” However, that is not really what this paper is doing, The proposed approach uses such a correlation, assuming it is accurate, not demonstrating. The is a lack of date that can actually be used to demonstrate that the proposed approach is valid. The authors are therefore turning the initial hypothesis into a conclusion without proofing it.

In the following I will provide some more specific comments I have on the manuscript:

• The authors must be much more careful with the wording and make sure to avoid blank statements, such as "... is important" without specifying important in what respect, and providing a reference or demonstrate the importance as par of the contribution.
• Line 10: Unfortunately, the authors copy misleading statements others have made regarding using rock glaciers as freshwater resources. It is important to understand that a rock glacier is not a special type of a glacier. There is no exchange in ice, and there is no annual runoff from a glacier as we know it exists from a glacier. The hydrological behaviour of a rock glacier is completely different, and therefore it cannot be compared with a glacier when it comes to how runoff from a rock glacier should be seen as a source of freshwater. In fact, when one does calculate how much ground ice from a rock glacier is melting during a summer, even under an extremely hot summer, te authors would realise that a) the amount is extremely low, and in fact, often much lower than the potential evaporation. Specifically, in arid areas. In other words, water that is released from a ground ice melt is most likely not available as freshwater. The current wording is therefore creating potential anticipation that simply does not exist.
• Line 19: The thickness of a rock glacier is a fundamental parameter. Can the authors please clearly define what they mean by the thickness of a rock glacier? As a first step, it would be helpful to define the bottom of a rock glacier, is it defined by the base of the permafrost, the depth to bedrock, or the interface between the original terrain and the material of the rock glacier that had been transported there?
• Line 21: Please provide clear definitions for terms such as reservoir and resource, and explain the differences in how they are used in the manuscript.
• Line 21 ff. When presenting results, it is a) critical that the error range is provided, and b) that the number of significant digits reflects the accuracy. It is not appropriate to present a result to the 10^th of a percent, when the error is in the 10^th of percent.
• Line 26: Please provide references for that statement, also, it is worth noting that this is only true for intact rock glaciers. Rock glaciers are geomorphic landforms and you can’t simply ignore relist rock glaciers, for example. As mentioned above, a rock glacier is not a special type of a glacier and as such this periglacial landform must be considered differently when writing about them.
• Line 28: With regard to Azócar and Brenning, 2010, I encourage the authors to carefully read the comment by Arenson and Jakob on that paper.
• Line 29: What exactly is a “hydrological value”?
• Line 39: I'm not clear what the “ratio of importance” is. Do you simply mean the ratio? If so, then the word "important" doesn't have a meaning.
• Line 42: See my earlier comment regarding water supply. In order to demonstrate that this statement is accurate, please provide a thermal analysis that shows how much melt you will get and then compare it with potential evaporation and infiltration.
• Line 43: Please provide reference and definition of an ice-cored rock glacier.
• Line 44: You write ” However, there lacks modelling studies to test these postulations and to assess the likelihood of glacier- rock glacier transition and the hydrological implications of this process.” I agree with this statement, but I feel that you do not keep this in mind while wording some of your text. Many of the wording is written as if it was a fact, but in essence it isn’t, such as freshwater from rock glaciers.
• Line 54: what exactly is “extremely”? Such qualifying words must not be used in a scientific publication unless clearly quantifiable.
• Line 57: Please clarify that Arenson and Springman (you can find details in Arenson 2002), emphasize that the deformation is not related to an "average" ground ice content, because such an average does not really exist, but rock glaciers do show quite complex internal structures. The deformations are often limited to a shear horizon (Arenson et al., 2002), where the ground ice content is high. Concluding from the ground ice content in the share zone to the ground ice content of the whole rock glacier is something that has not yet been confirmed and is associated with significant errors (orders of magnitude).
• Line 74: Discontinuous permafrost has no altitudinal boundary. The whole concept of continuous and discontinuous permafrost, which has been developed for polar regions, should not be used in mountainous environments. That's why the term Mountain permafrost had originally been coined.
• Figure 1: What is the year of the image? What was the scale used for mapping?
• Line 91: Are you using Ascending and/or descending imagery?
• Line 93: What exactly is high? Can you be quantitative as this is another relative term.
• Line 99: Please provide more details on the analysis methodology used for the InSAR assessment. E.g. did you use PS or any other method? There are many aspects unclear on the InSAR assessment.
• Line 100: relative term, what do you mean by "near"?
• Line 101: what was the landform coverage? How much topographic shade did you experience for the landforms?
• Line 105: I assume that this was done using SRTM topography and not by combining ascending and descending stacks. This can result in significant errors in deformation due to the significant differences in the resolution between SRTM and InSAR imagery. How much are the errors in your evaluation?
• Line 108: you mean less than half? Is this still representative? Can you quantify that using only 40% of the area is representative for the assessment presented? Also, you probably are biased towards the flatter sections of a rock glacier where there is less topography, but where you likely would have more compressive flow.
  
  How did you address differences between compressive and extensive flow sections in rock glaciers? Are you implying that the ice content in the compressive areas are representative?
• Line 109: The values presented are averaged over the Dec. 2007 to Feb 2020 stack, is that correct? And I assume it is based on the 40% area coverage.
• Table 1: How come you only have one interferogram? What is your level of confidence to use just that one interferogram in your assessment?
• Line 144: 1. you assume that the base of the rock glacier equals the base of the permafrost, correct? 2. You assume homogeneous conditions, which I haven’t seen in any rock glacier, i.e. this is a huge simplification. I'm not saying there is no value in doing this, but you must be aware of what the consequences of such a simplification are when you draw your conclusions.
• Line 145: Talus derived rock glacier show very variable thickness. Potential generalization that may lead to misleading results / conclusions.
• Line 146: You also assume constant temperature conditions within the permafrost body, which is often not the case. Again, a rock glacier is not a special type of a glacier and can’t be compared to a temperate glacier.
• Line 184: I am very surprised that the simgle most important parameter, the temperature, is simply ignored.
• Line 187: What is the error range? Geophysics w/o calibration may have significant errors.
• Line 220: This correlation should simply not be used (See Arenson and Jakob, 2010). Using such a simplified correlation does not account for the complex geomorphic background of why a rock glacier exists. Hence, utilizing a glaciological, mass balance inspired approach to describe a periglacial, topo-geologically driven process will not provide accurate results.
• Line 224: SRTM resolution is not 30 m, but varies geographically as it is in arc degrees.
• Table 4: These active layer thicknesses are extremely thin. Please look at some of the rock glacier active layer thicknesses in the Alps (e.g. PERMOS reports) where you eill find that rock glacier active layer thicknesses are often several meters thick. Hence the major thermal protection and the lack of contribution to any runoff, even as the permafrost degrades. The energy available for ground ice thaw below a active layer thickness of several meters, is low.
• Line 358: Rock glaciers do not show a uniform creep. Most rock glaciers have an area that is faster and another that is slower. For example, large rock glacier may no longer advance because the lower part lost too much ice to allow creep. However, the upper part is still creeping, Your approach will completely overestimate the ice content as it does not take the actual rock glacier kinematics into consideration.
• Line 367: importance relative to what?
• Line 378: You state “This premise indicates that our method is applicable to rock glaciers currently moving at a relatively stable rate.” For one, based on data rom the Alps, we know that this is likely not the case, and more importantly, you use date from rock glaciers that do not show stable deformation to develop your model, which should then be only valid for stable deformation? This does not sound logical to me.
• Lien 385: Call the “clean” (what ever that actually means) as an uncovered or covered glacier. Or simply call it glacier because rock glaciers are not special glaciers, as I’ve been mentioning severel times already.
• Line 419: You are citing Cicoira et al. (2020) to support your statement. Are you sure, since the publication of Cicoira et al. (2020) had a completely different objective and it seems to me that your referencing is taking out of the appropriate context.
• Line 424: I suggest that you read Arenson and Jakob (2010) and revisit your statement.
• Line 426: I am not at all surprised by the large bias that you found, however, I do not see this bias be further developed, for example using error propagation theories, to illustrate what that means for your end result.
• Table 7: What is Tref?
• Table &: How confident are you that these 5 (!) rock glaciers, which all have very specific features, are representative so that a correlation, such as the one you present, can be developed and reasonably be applied for hundreds of rock glaciers in very different settings?
• Line 459: Based on my review I do not support this statement and it is my very strong impression that this approach is not yet ready and specifically I would not call the uncertainties “well-quantified”. In fact, the uncertainties are unknown.
• Line 460: I completely agree wit the final statement and encourage the authors to put their effort in getting more field data so that can provide a better estimate for rock glacier thicknesses.
• Line 468: The authors indicate that they are measuring active layer from remote sensing. First, they have not discussed this aspect in the paper, which means that this should not just pop-up in the conclusion, and secondly, I am not aware of a method on how to measure rock glacier active layer thicknesses from space. Or maybe the authors mean geophysics, which has its on challenges for block rock glaciers.
• Line 472: Level of accuracy implied is unrealistic.

In summary, this manuscript is not ready for publication and I strongly encourage the authors to re-evaluate their scientific basis and if there is even any merit in the approach presented considering the significant uncertainties that exists because of the assumptions used.