Dear authors,

Thank you for the revisions. It has significantly improved but the reviewer sees still several issues. The reviewer has made many comments directly in the manuscript which will help you in the revisions. I am in general in line with the reviewer and also think that the paper may become publishable after the comments are addressed. I choose therefore major revisions but in case the issue with the representativness (see below) and the other comments are well adressed I will make a decision without contacting reviewers again.

Major comments:

One issue is still the representativeness and that the authors focus on one glacier only. We have discussed that you cannot extend due to the high workload. But you should make more efforts to show the representativeness or clearly state that this is the mass balance of one glacier. I also want to again emphasize that there are now more and more studies using Hexagon which cover a much larger area and it is not too much effort to generate a DEM using standard photogrammetric software. It may not be so precise but this could then be nicely shown.

Another important issue is that the role of supra glacier lakes/ice cliffs is not clear, as you show that the studies glacier has not experienced large rates of elevation change, but then refer to “high” rates of surface lowering around lakes towards the end of the paper. The discussion of debris-covered vs clean glaciers should also be improved.

Please do not hesitate to contact me in case you have any questions.

Best regards,

Tobias Bolch, Editor TC

Dear Koji, dear authors,

I have now read your revised manuscript and the reply in detail. I understand that you cannot extend your studies glaciers although it would have been very beneficial and has also been pointed out by the reviewer by a personal note to me. Hence, the major focus of the manuscript, the analysis of the characteristics of glacier elevation changes vs. the existence of supraglacial ponds and glacier flow, is the major focus besides the information of the mass balance since 1975.
In this regard the manuscript has still some shortcomings which need to be considered before I can accept it for publication, some of these were already mentioned in my access review but are from my point of view still not adequately addressed. This is also true for some of the reviewers comments. In order to speed up the process I will not send the manuscript to another reviewer but will provide the comments by myself. However, I asked my colleague about his opinion and he was fully in line with me.
My main comments are:

- Hexagon DEM: The Hexagon image has a spatial resolution of 7.6 m, but you chose the resolution resultant DEM of 5 m. Reasonable DEM results are usually achieved by choosing a resolution of twice the image resolution, hence a reasonable resolution would be 15m. This issue needs to be discussed and clarified. In addition, the sentence in the abstract using high resolution DEMs with a resolution of 5m is misleading. In this sense, the methodological description of the the Hexagon DEM generation needs to be improved. This is important as the DEM generation of this data is not straight forward and I cannot really follow the approach (e.g. L. 102/3: Did you reconstruct the image geometry?; L111/2: How dense are the identified matching points? Is it reasonable to resample the DEM to 5m? One can resample all DEMS of high resolution.

- Comparison of the velocity of the period March-December 2010 to the elevation change for the period 1975 and 2010. You may at least mention and discuss shortly that the time periods you compare do not match and velocities might have changed.

- DEM Coverage: I am also confused about the final coverage of the DEMs and the DEM differencing results after outlier filtering. From L. 126/7 the reader gets the impression that 19% of the entire are data gaps but in L. 194 you write that “DEMs are only available for the lower 22, 6 km² section (38% of the entire glaciers). Are really 62% of the glacier area not covered by the DEM differencing? This must clearly be stated and it must also better shown that you can really estimate the mass balance with such low coverage.

- Results and discussion section: This section is still not well written and structured. This was also highlighted by the reviewer and it is still the case after your revision. In my access review, I did not ask to join results and discussion. I think it would have been better to keep than separately. In this way is would be much clearer what your results and the novelty of the results would be.

- Few further comments: Currently too much emphasis is put on characteristics of the surface elevation change which are well known and shown in several studies before (e.g, L. 227: “The velocity … is possibly influenced by the … surface slope”; however the influence of the thickness is however, not so straight forward (the effect is more indirectly).
- L. 247 -254 are also well known facts and do not fit into a results section as it is now.
- L. 266ff: from my point of view it is also clear that the emergence velocity is negligible where the surface velocity is very low.
- L. 196-198 are more or less similar to L. 229-231.
- L. 271: I am also not fully in line with this hypothesis. It might well be that the surface elevation change is higher at lower slopes because the areas with lower slopes are located as lower elevations where the melt is on average higher.
- I do not want to force you to consider the study by Ragettli et al. 2016, TC a bit more in detail in your discussion as I am co-author on this study and I want you to finally judge on this study. However, I want to emphasize that there are strong similarities as both studies investigate surface elevation changes of debris-covered glaciers in the Himalaya using DEM differencing (incl. Hexagon) and relate it to the existence of supraglacial lakes and flow velocity. Hence from my point of view make a more detailed comparison of your results to the results by Ragettli et al. (2016) would make your results stronger as they are in general in line and you can confirm that the findings are also true for other parts of the Himalaya.
- Conclusions: I am not inline to only add a sentence about the shortcoming of the chosen methods (the small coverage due to the time consuming editing) as a reaction of the comments on the small area coverage and the representativeness. Pros and cons should be discussed more in detail as the main results you present could have also been (and where also achieved) by more simpler image matching using Hexagon data. I’d like to highlight that the reviewer wrote in a personal note that he/she find the spatial coverage still very problematic but left the decision up to me to decide whether the small coverage is enough for making it a relevant paper.
- Figure 6b: This figure is misleading: You do not compare the evolution of the surface elevation of the supraglacial ponds but compare the elevation of the ponds which are present in the ALOS image and ALOS DEM to the glacier surface at the same location in the Hexagon DEM where there were most of the time no lakes have been. The elevation of these locations must be significant lower than the average surface of the glacier as it is well known that the surface of the supraglacial ponds is lower than the surrounding.
- Fig. 6a: You need also be careful as dh/dt of the lakes depends also on the condition of the 1975 surface.
- Figure 7: You may consider a log scale, but more important: Include the source of the other studies and clarify why there are different points for the regions. I assume these are for different glaciers but this is not evident from the figure.
- You may also think to adjust the title as it currently does not fully refelct the content of the study.

I ask you to do your best to really improve the writing and structure especially in the results and discussion section and specifically highlight the novelty and importance of your study taking the current literature and knowledge into account. In addition, eliminate the remaining shortcomings. Only then I can accept the manuscript despite the fact that only one glacier is covered in this study and the DEM coverage of this glacier is quite limited. I am happy to grant an extension in case you need more time.

Please do not hesitate to ask in case you have any question.

Best regards,

Tobias Bolch, Editor TC

Dear authors,

Thank you very much for the careful revisions. From my point of view the effort was really worth it as it is now much better and contributes well to the understanding of the evolution of debris-covered glaciers. However, I have some minor comments left which should not be too difficult to address:

L. 31/32: Please do not cite more than 5 paper is a row. I suggest to split into the studies which address Langtang and those which address Khumbu regions.

L. 36: You may think to consider here: Basnett et al., 2013. Influence of debris-cover and glacial lakes on the recession of glaciers in Sikkim Himalaya, India. J. Glaciol. 59 (218), 1035–1046.

L. 171: For density scenario 1 I suggest to use 850 +- 60 kg /m³ which has now been established in many geodetic studies without further density information.

L. 174: Provide a rational for this ELA.

L. 222 – 233: This section contains both methods and results. Move the methods to the method part.

L. 238: These studies are all authored of co-authored by me. I suggest to remove Pellicciotti et al. 2015 (it was updated by Ragettli et al. 2016) and include another study not authored by me.

L. 290: I suggest to remove the “older” studies (Bolch et al., 2011; Nuimura et al., 2012; Gardelle et al., 2013) but include therefor the most recent relevant ones, e.g. Bolch et al. 2017, TC (if you want as it uses also KH-9 data, but I do not force as it is focusses on Karakoram), Brun et al. 2017, Nat. Geosc., Lin et al. 2017, Scientific Reports.

L. 309: I notice that these studies overlap within the uncertainty ranges. Hence, I’d formulate the differences a bit more with caution although the provided explanation based on the hypsometry differences is very reasonable.

L. 317: The explanation that also the smaller debris-covered fraction for Kanchenjunga Glacier yields to a less negative geodetic mass balance compared with Khumbu Glacier is not so obvious. Provide more evidence or formulate with more caution.

L. 331: I am not so convinced that the Kanchenjunga Glacier can be seen as representative for this region. Provide more evidence of formulate with more caution.

L. 337-344: These lines are important but do fit better in the discussion. Here you can highlight better that your results seem to be robust despite the low data coverage and large uncertainties. You could also highlight similar problems with unmeasured accumulation areas (as present in several studies, e.g. Maurer et al., King et al.)

Please do not hesitate to ask in case you have any questions.

Best regards,

Tobias

Dear Damodar, Koji and Akiko,

Thank you for the further imprevement. The coments were adressed weill.
However, I would have still one further suggestion for improvement (Maybe my comment was not really clear...):
For the two density assumptions I'd suggest to use (1) 850 +- 60 (you may cite Huss 2013, TC here) and (2) 900/600. The first assumption includes already the lower density of firn while it can be assumed tha only ice is lost in the ablation region (scenario2). This won't change your results but would be more consistent with the currently applied methods. An interesting paper to read in this regard is also Sapiano et al. 1998, J. Glaciol.

Thank you once again for your efforts and I am looking forward to see this paper published.

Best regards,

Tobias