The paper aimed at using real data assimilation to assess how much the streamflow supply prediction can be improved by assimilating additional snowpack information. The performance of directly assimilating streamflow (Q), fractional snow cover (FSC) and cosmic ray snow sensor data (CRS) and their combination are assessed in three basins with first Sobol sensitivity analysis and then real streamflow data. The authors found that Q assimilation notably improves streamflow estimations during both reanalysis and forecast period, while additional combination of CRS and FSC data to the assimilation further ameliorates the A48 prediction in two of the three basins. Overall, the topic is of interests to operational streamflow forecasting for snow-dominated areas. The data and methods are reliable, and the results are supporting what’s concluded. However, I have some major frustrations with the writing, the main figures, and some moderate concerns with the methodology, as shown below. This should warrant at least major revision.

Major:

1. The Introduction will benefit from a re-structuring. For example, Line 28-30 and Line 63-65 present research questions and objectives of this study, which can be combined. Also, the authors seem to have mixed their results with the Introduction (see Line 35 and Line 75 for examples of unnecessary results), which are usually presented in the conclusion or discussion part. I suggest authors to overhaul their Introduction to give clearer outlines.
2. I think there are major issues with many figures. Fig. 1: Resolution is too low, and subscripts are not recognizable. Using figures from past studies is okay, but needs better caption to describe each individual term appearing in the figure (e.g., what is AEP, what is PET? Seems Potential ET is used as a forcing but not described in your model description part). Fig. 2 lacks description about the shading. Please add a legend. Figs. 5-7 lack the description about the variables plotted (there are need to describe them both in the caption and the main texts). This type of figure presentation is difficult to be accepted by the academic community. Suggest authors to re-draw many figures.
3. Lack of variable descriptions in Figs. 5-7 is preventing readers from clearly getting your methodology: which ones are the most sensitive? (see comments above)
4. I think in the Method section, it is lacking the spatial plots for the FSC and CRS measurements locations. These are key information (how much? Where are they located?)
5. About Methods: the DA framework/perturbation and the model are relatively better presented. But how about the measurements? How are the FSC and CRS obtained? What about their uncertainty? How about their available number and spatial distribute (this is asked above)? I see some information is presented in Intro, but measurements uncertainty is the most important, and should receive a much more balanced writing and description in a specific Method section.
6. Line 181: not sure how is the 900-member ensemble determined? Usually, we use much less ensemble members than this in DA studies. I understand the computation demand may be low for your hydrologic model, but scientifically why is this large number needed? Any justification and supporting evidence on how this satisfies your research goal? If there’s a need for inflating the uncertainty, this should be clearly clarified. It may be tested results to maximize performance in Figs. 9-10, but I think understanding the uncertainties (as denoted by the spread of your ensemble) is more crucial to DA rather than to maximize performance.

Moderate concerns:

1. For the Sobol indices equation, it would be better if the authors can provide detailed explanations of the variables in the cases of temperature and precipitation forcing. Also, the equation takes the presumption that the variables are independent and has known probability distributions. However, in geographical analysis it is often hard to determine whether a variable is completely independent. It would be more convincing if the authors can provide some assumptions and preconditions.
2. What is the resolution of the reanalysis data used in the paper? When assimilating observation data, will the resolution differences cause uncertainty and what is the solution used by the authors?

Minor ones:

1. Line 6. ‘Lead to’ mis-spelled as ‘leed to’.
2. Line 10. ‘A series of’ not ‘a serie of’
3. Line 35: ‘play a role in’ not ‘on’
4. The subtitles like “Hydrological system” do not exactly match the content.
5. Line 311. Is the “prediction time” the same as the forecast period mentioned in line 72? How could the prediction time be lengthened?
6. 9 and 10: to improve readability for the readers, please add the legend directly to the plots.
7. What exactly does A48 represent? In line 2 it seems to men “between April and August”, while in line 20 it seems to stand for seasonal streamflow supply. This type of writing will confuse readers.

The manuscript ‘Snow data assimilation for seasonal streamflow supply prediction in mountainous basins’ by Metref et al. provides an interesting study regarding the big challenge of improving streamflow predictions in mountainous, snow-dominated regions. The authors investigate the additional value of directly assimilating streamflow, fractional snow cover (FSC) and SWE measurements (taken by cosmic ray sensors (CS)) and their combinations in terms of improving seasonal forecast in three French basins (one in the Pyrenees and two in the Alps) applying a conceptual semi-distributed hydrological model (MORDOR-SD) as basis. They test their results during reanalysis (assimilation) and forecast periods and found that (not surprisingly) the assimilation with streamflow improved the estimates during both, reanalysis and prediction. Including CRS and FSC to the assimilation process could further improve the seasonal prediction in two of the three catchments.

In general, this topic is interesting to the readers of the journal. However, the manuscript in its current state needs major improvements before considering for publication. The authors should add important additional information and clarifications at several points (see comments below) as the paper currently produces several question marks in the eyes of the reader at some points. I agree with the points raised by reviewer 1. In addition, I have further points, which are listed below. English language should be improved.

General comments:

• In your study, you are focusing on snow-dominated catchments where the simulation of snow processes plays an important role. However, the description of the snow module of the MORDOR-SD model is entirely missing here (e.g., I guess it is a simple day-degree approach to describe snow melt). This should at least be described (Section 2) and discussed (Section 5 or 6) carefully.
• In general, assimilation can lead to good results regarding streamflow predictions (as you have shown). However, it should also be discussed in the paper, if adding more physical realism in describing snow cover processes could also lead to improved results regarding streamflow predictions.
• As reviewer 1 already stated, the introduction is difficult to read and a mix of state of the art, presentation of some results, objectives, research questions, outline, and some methods. The Introduction should be carefully improved including a solid state of the art paragraph.
• What is the reason for selecting the three chosen basins Verdon, Naguilhes, and Gui? Are they very different in terms of topography, meteorology, geology, etc. to learn different behaviours regarding catchments response? Do you expect to gain additional information, if you would select further catchments out of the 50 catchments operated by EDF?
• You tried out the settings of assimilating i) Q, ii) Q and FSC, iii) Q and CR, and iv) Q, FSC and CR. Why didn’t you show the results of just assimilating FSC (regarding CR you stated it would deteriorating the system estimation (l.42ff – this however, would fit rather in a discussion section instead of the intro))?
• How well does the MORDOR-SD model perform in general in your catchments regarding calibration and validation periods (e.g., according to objective functions such as Nash Sutcliffe Efficiency)?
• I miss the link of meteorological and snow conditions at certain years in the three catchments and your results (especially in the discussions in Sections 5 and 6). Snow and meteorology conditions can be quite different throughout the years and might affect the quality of your streamflow predictions. What is the impact on e.g. a lot of snow vs. shallow snowpack during single winters in the three catchments?
• In the lines 28-30 you raise three questions on the relevance of using in satellite and situ snow observations to improve seasonal streamflow predictions in mountainous catchments. However, I have the feeling that these questions are not properly answered in the course of the manuscript.

Specific comments (chronologically):

• 86: The paper is actually divided into six parts (including the introduction). -> Better reformulate: ‘The paper is structured as follows:’
• Figure 1 and Section 2.1: At least a basic introduction to the model and its components should be given. Please add information (e.g., as a legend in Figure 1) on the variables and parameters shown in the graph.
• 93: How many metres does one elevation band encompass? Regarding Figures 5-7, this seems to be 250 m for each catchment!?
• 95: What are the orographic gradients (lapse rates) applied in this study for temperature and precipitation?
• 99: What are the 5 state variables (I guess S, G, U, L, Z and N?) and the 2 global variables? Please add this information at least in the the methods descriptions and the legend of Figure 1. In additions, why do you write the span of 10-12 free parameters? How many did you have in your setup?
• 106-111: Not entirely clear; Please improve the descriptions in these lines. / Figure 2: Is this a catchment averaged meteorological data set shown here or is it representative for one elevation band? In general, not sure if Figure 2 is really needed. In addition, the Verdon basin is actually introduced one Section later and the reader might be wondering why you already mention it here.
• Figure 3: This graph just shows the location of the basins in France. The graph misses topographic information as well as important information such as at least the location of its capital and the name of the mountain ranges (Pyrenees, Alps). In addition, I suggest giving a more detailed overview on the three selected basins in the Figure.
• 140f: Please add information on the expected footprint of the CRS as well as limitations of this sensor type.
• 142ff: Please describe in more detail how FSC was derived. Did you look at basin-averaged values or did you consider elevation band based FSC values. I think just taking FSC values for the entire catchments (with elevation ranges of approx. 2000 m) is not sufficient and might not be representative for the application of assimilation data.
• Figures 5-7: Not introducing U, L, Z, S, TST before makes the figures questionable (see comments above). Information regarding elevation bands is missing in the y-axis. The chosen (linear) colour representation is not very meaningful. In addition, I would suggest to add a row in showing the average Sobol indices for the entire time period to get a clearer overall picture. Interpretation why the Sobol indices are higher for some elevation bands as well as distinct years is missing in the text.
• 170-174: Please avoid repetitions – was already introduced before.
• Figures 9 and 10: Please insert for a better readability legends. Why do you show the selected years, assimilation configurations (assim. of Q in Fig. 9, assim. of Q and Q&CRS), and the selected catchment as an example in those Figures as examples? Are other seasons/years similar in their quality?