General Comments

The manuscript presents a thorough investigation of the effects of climate warming on rain-on-snow events in the Pyrenees. The manuscript is well-structured, includes a comprehensive state-of-the-art literature review, and an extensive discussion of the results. The methodology is sound, but a bit outdated with regard to the scenario approach used (delta-change method). The results show that an increase of rain-on-snow events has to be expected in mid-winter and at higher altitudes, and a decrease elsewhere. These results are innovative and relevant for various sectors, as discussed in the manuscript.  The manuscript is therefore suggested for publication with minor revisions, as indicated below.

Specific Comments

Abstract, line 11: What do you mean with “When air temperature is increased from 1ºC to 4ºC…”? Since your study is based on spatially and temporally varying weather data from reanalysis, there is no fixed 1°C base temperature that you could raise to 4°C. Please reformulate to clarify, that 1°C is not the baseline, but already an additive constant used in the delta change approach.

Section 3.4: Could you please motivate the value of change-factors you selected for the delta change approach? It is important to relate them at least qualitatively to more elaborated climate scenarios. E.g., how do these levels of warming relate to the +2 degree goal? Is +4K a worst case scenario, or an intermediate one? Is +/- 10% precipitation adequately spanning the expected range of change? To answer such questions would strongly increase the general impact of the study, since it could be better related to the general climate change debate going on in our society. There is very limited information on this topic in Section 5, but this needs to be extended and maybe shifted to section 3.4, where the scenario concept of this study is introduced.

Section 3.4: Please clearly discuss the limitations coming along with the delta-change approach. Such a discussion is completely missing so far. E.g. a more realistic simulation of climate change would most probably include a distinct seasonality of precipitation change, which is absent in the delta change approach.

Section 3.5.: The representation of the results in “change per 1K” is great, since it makes the results easily comparable to other regions/seasons/scenarios.

Editorial/Technical

Title: Please consider rephrasing the title. The expression “Rain-on-snow response to a warmer Pyrenees” is semantically very vague (and grammatically incorrect: Pyrenees is in plural). You describe the response of the characteristics of ROS events to warming and precipitation change in the Pyrenees in your manuscript. Something along these lines would be a much clearer title for the article manuscript.

Abstract: Avoid using abbreviations without introducing them in advance (line 8; “ROS fr”).

Line 470: wrong usage of singular/plural (vegetation branches intercepts)

Generally: Some additional proofreading is advisable to remove some remaining minor language mistakes.

Review of « Rain-on-snow response to a warmer Pyrenees » by Bonsoms et al.

The manuscript entitled « Rain-on-snow response to a warmer Pyrenees », by Bonsoms et al., is a sensitivity study about the frequency and magnitude of rain-on-snow events in the Pyrenees, under various local temperature change values. The topic is relevant and new knowledge is interesting to have, to better assess the evolution of related risks under climate change. Overall, I did not detect major flaws in the work carried out, however I have some reservations about the novelty and clarity of the methods used and results obtained in this study. I am not convinced that simple « delta change » methods remain an appropriate choice, at a time where regional climate simulations are readily available, especially in European areas. Combined with a lack of connection to a scenario analysis (i.e., under which circumstances a local warming of 1 to 4°C could/would occur in the Pyrenees, compared to the baseline period 1980-2019 ?), this manuscrips lacks some key elements such as an analysis of the uncertainty induced by the approach developed here, compared to alternative approaches. I also find that the graphical representation of the results could be made clearer and more compact, including, for example, results at the scale of the entire mountain range rather than focusing only on 4 subregions. Also, I find that this study quotes a very large number of references (I counted 100 references), and that it would be preferable, I think, to select a subset of targeted references to support the positioning and the discussion of the results, rather than this very long list of references. Ways forward includ, for example quoting the still recent IPCC SROCC « High mountain areas » chapter (Hock et al., 2019), which includes an analysis of the state of knowledge about climate change and rain on snow events (section 2.3.2.1.3 on Floods). It is indicated there that :

« In summary, evidence since AR5 suggests that rain-on snow events have increased over the last decades at high elevations, particularly during transition periods from autumn to winter and winter to spring (medium confidence). The occurrence of rain-on-snow events has decreased over the last decade in low-elevation or low-latitude areas due to a decreasing duration of the snowpack, except for the coldest months of the year (medium confidence). »

And, for future projections :

« In summary, evidence since AR5 suggests that the frequency of rain-on-snow events is projected to increase and occur earlier in spring and later in autumn at higher elevation and to decrease at lower elevation (high confidence). »

While a few studies were published since that time and expend the available body of literature, I think the introduction (and the long list of references quoted there) could be substantially shortened by refering to this critical assessment of the state of knowledge, and positioning the scope and objectives of the current study on this basis. This scientific study targets a scientific audience, I think it is perfectly appropriate to quickly introduce the context and state-of-the-art in this topic and then introduce very early in the manuscript how the challenges are addressed in the study. I think this could save quite a lot of space and avoid quoting an unecessarily large number of references.

I have a series of comments and suggestions, which I provide below :

Page 1, line 8 : While the term is not introduced, I understrand that « ROS fr » refers to « ROS frequency ». I strongly suggest that the full word is spelled out, as « ROS frequency », throughout the text. This will increase its readability.

Page 1, line 17 : I did not understand what is meant by « slow, and non-changes in ROS ablation ». I suggest this is reformulated.

Page 1, line 26 : These introductory statements could be greatly simplified by referring to assessment reports, such as the IPCC ; this would also reduce citations of rather « old » references.¨

Page 2, line 31 : « leading in some cases to ROS events ». To me this is incorrect. A ROS event occurs when rainfall falls on a a snow-covered ground. Such a definition is lacking from the manuscript until section 4.1, I think this should really be provided earlier. Also, ROS have always occurred in mountain regions, but climate change is modifying their frequency and elevation distribution. Climate change does not « lead » to the existence of ROS in mountains, but modifies their patterns. This needs to be clarified, and I strongly suggest that a definition of what a ROS is should/could be added.

Page 2, line 33 : « Mountain elevation-dependent warming ». I think this deserves some clarifications here. Elevation dependent warming (EDW) refers to the fact that, in some cases, the magnitude of the climate trend is not the same depending on elevation. This is debated and the evidence is not unequivocal. However, there is no need to invoke EDW to state that snow cover changes (including ROS) depend on elevation. Indeed, climate conditions depend on elevation, such as the mean snowfall fraction, so that a similar change in temperature would have different consequences depending on the elevation. This shows that there can be elevation dependent changes without necessarily elevation depending warming. I think this could/should be clarified in the introduction here, as this is a confusion which is often made, and this manuscript could offer an opportunity to clarify this, especially in a context where the « delta change » approach applies a uniform warming level to all elevations considered, i.e. it ignores EDW in its very design.

Page 2, line 43 : I think the various SEB components could/should be more precisely described, rather than quoting previous references. There is a common misconception that rainfall is directly causing snow melt during ROS events, and the introduction does not explicitly allude to the processes responsible for the influence of ROS events. Again, no need to quote dozens of references, but a few clear statements on the physical processes related to ROS events and their consequences would be useful.

Page 3, line 73. I have some questions about the concept « ROS drivers ». But before, I think the manuscript lacks a clear definition of what a ROS is (see above), and how is it computed. A ROS occurs then rainfall occurs over a snow-covered ground, hence it recquires an analysis of the simultaneity between two variables (non zero snow cover and non zero rainfall). What is the threshold (i) in terms of snow depth or SWE and (ii) in terms of rainfall amount (daily ?) used to state whether a given day is a « ROS day » ? This should be quickly introduced here in the introduction, and with more details in the Methods section. In this sens, « snow depth / height of snow » and « snowfall fraction » are not individual drivers of ROS, but ROS stems from their combined time series at daily or subdaily time resolution. The analysis cannot be done independently, or, if so, reasons must be given what this is relevant.

Page 4, line 105 : « February (May) in low (high) elevations ». This is not correct grammatically, and should be rephrased for better clarity. See https://eos.org/opinions/parentheses-are-are-not-for-references-and-clarification-saving-space

Page 4, Figure 1 : « low », « mid » and « high » should be defined in the caption (not defined at this stage in the text, and worth making clear in the caption). Also, the time period used for the analysis should be explicitly stated (1980-2019 ?).

Page 4, line 117 : While I have no problem with using FSM2, I wonder what the Crocus model results, driven by SAFRAN, where not used at least to compare with the FSM2 results. These simulations are also provided on the AERIS data portal. Also, there are climate projections available for all the massifs in the Pyrenees using the adjustment method ADAMONT applied to an ensemble of EURO-CORDEX regional climate models driven by several CMIP5 GCMs, with the same geometry as the SAFRAN reanalysis. The method and type of results is described in Verfaillie et al. (2018, The Cryosphere), and the dataset (atmospheric and snow cover) dataset for climate projections is freely available on the Drias climate data portal (https://www.drias-climat.fr/accompagnement/sections/215). It is thus suprising that a simple delta change method has been applied here, without any comparison to other approaches and using other snow cover simulations. Combining the results obtained here would enhance the robustness of the analysis, by adding several ways to explore and quantify the uncertainty related to changes in ROS frequency and characteristics under climate change.

Page 5, line 140 : I suggest referring to « flat terrain »

Page 5, line 143 : « homogenized » is to be deleted.

Page 5, line 144 to 146 : this part of the sentence is not accurate and is misleading. Indeed, there are two implementations of SAFRAN in France : the original configuration of SAFRAN operates in mountain areas (Durand et al., Vernay et al.), and an another implementation was developed for the entire country, and referred to as « SAFRAN-France », providing results on a 8kmx8km grid. I think it is better to not mix references to these two systems. In this sense, the references to SAFRAN-France implementations (Habets et al., 2008, Quintana-Segui et al., 2008), would be better left out.

Page 5, line 161 : The elevation bands chosen are 1500, 1800 and 2400. It is not clear why these bands were chosen, and in particular whay there are not equally spaced. In this context, I suggest that throughout the manuscript the elevations are explicitly provided instead of « low », « mid » and « high » elevation, to avoid misunderstanding or overinterpreting trends at these three elevations.

Page 6, line 179 : I think that it would be appropriate to explain how the LWin was increased according to changes in temperature (I noticed the last sentence of the paragraph on the topic, better combine at the same place and provide more information such as an equation and/or a reference to the method employed).

Page 6, line 184 : « Delta-change » is a method that was developed and primarily employed a time when regional climate projections were not available or not usable, or for locations where this is still the case. While I understand that such approach may bear some relevance for sensitivity analyses, I think it should be stated clearly that such methods undersample some climate change effects, such as changes in the variability of meteorological conditions, which only climate modelling methods can approach. I think this should be clearly stated here and also recalled in the dicussion and conclusion. Also, I would strongly suggest to provide some context about the values used for the local warming level (1° to 4°C), i.e. how do they connect to global warming levels and/or climate change scenarios. Otherwise, the results here stand disconnected from the analysis of climate change impacts relevant to stakeholders and policy-makers, and other scientific studies based on scenarios and climate models.

Page 6, line 187 : The reference time period should be clearly stated here. Is it 1980-2019 ?

Page 6, line 195 : I don’t understand why there is no reference to the change according to the change in precipitation amount (+ or – 10%) but only temperature. Could this be clarifier ?

Page 6, line 196 : Here is the much needed information about the definition for a ROS day and a number of other terms used in the manuscript but not introduced before, unfortunately. This should be clarified much earlier in the manuscript.

Page 6, line 198 : What is the motivation for defining ROS ablation based on the change in snow depth/height of snow : SWE is a much more appropriate variable to infer changes in snow quantity, because changes in snow depth/height of snow can be due to compaction. I’m certain that FSM2 can provide SWE output. More information should be given about the motivation for such a choice, and, if possible focus rather on SWE than snow depth/height of snow.

Page 7, line 213 : I’m not convinced by the term « ROS drivers », mostly because these are not independent drivers and that ROS compounds the state of the snow cover with the occurrence of rainfall. I would be more comfortable with simply stating that this is an analysis of the change in mean seasonal/monthly snow depth/height of snow and snowfall fraction.

Page 7, line 214 : I think at least one figure showing the influence of the change in precipitation should be provided in the main manuscript and not only ion the Supplement. That temperature plays a much stronger role than precipitation change was found as early as in the 1990s (also using delta change approaches, see Martin et al., 1994, Annales Geophysicae).

Page 8, line 232. « baseline climate » should be provided explicitly in each figure caption. Also, we don’t find the reference to the warming level in the legend of the figure, which is further unclear because the changes are indicated as % per °C. The content of the figure needs to be clarified, perhaps it is simply too complicated. As indicated above, « low », « mid » and « high » needs to be explained in the caption, especially in a context where the corresponding elevation bands are not equally spaced.

Page 8, line 247 : I think it would be good to always state that the values provided are for a given time period (1980-2019 ?) and also provide some information about the variation about the mean (standard deviation ? quantiles ?).

Page 9, line 259. There is a problem with the graphics, which shows spurious « wider » bars for panels with less bars. This should be fixed so that bars all have the same width, and the graphical processing account for the lack of value (or 0 values ?). I also suggest that some information about the variation around the mean is provided, especially because the rounding seems to have quite a large influence on the display of the results (in fact, why are the results rounded to the nearest integer ? In fact, I see no reason for this, there is no problem to refer to the mean number of days with ROS as non-integer value. My suggestion would be to remove this rounding, and include a representation of the variability around the mean (standard deviation ? quantiles ?). I also think that such figure would benefit from an overall graph showing the entire mountain range, with a sub-regional focus for a more in-depth analysis, given that many results seem rather comparable depending on the subregion.

Page 10, line 278. Figure 4 : the color palette is inadequate. It uses a diverging color palette although continuous, increasing values are shown. Maybe the baseline could be provided using a continuous/increasing color palette, and then the change compared to the reference could be displayed as a deviation from the reference (using a diverging palette, then).

Page 11, line 292, Figure 5 : same general comments for Figure 5 as for Figure 3.

Page 12, line 306, Figure 6 : same general comments for Figure 6 as for Figure 4.

Page 14, line 339, Figure 8 : same general comments for Figure 8 as for Figure 3.

Page 15, line 344, Figure 9 : same general comments for Figure 9 as for Figure 4.

Page 16, line 356 : The sentence on climate projections is largely insufficient. More information should be provided here on the scenario consideres, and the reference period used from which temperature and precipitation changes are reported. Here the statement on the temperature increase could be provided in a way that makes it possible to contextualize the temperature increase values (since 1980-2019 ?) used in this study.

Page 16, line 365 : « The contradiction between rainfall ratio increase and snowpack reductions ». I see no contradiction here at all, both the rainfall ratio (note that the manuscript refers rather to the snowfall fraction) and snow cover decrease are driven by the temperature increase in a consistent way. I suggest that this is reformulated, because, indeed, the increase in rainfall ratio and the decrease on snow depth, induce potentially divergent effects on ROS days.

Page 16, line 368 : « elevation dependent snow sensitivity to temperature change ». This is not a new result, there are multiple reports or publications addressing this issue (e.g. Hock et al., 2019, and Kotlarski et al., 2022, for the European Alps). In fact, this also shows that there is no need for an elevation dependent warming to see elevation dependent changes in snow conditions, as discussed earlier in this review.

Page 16, line 360 : A Discussion section generally introduces a discussion of the limitations of the method used for the study. This is currently lacking from the Discussion section, and I think this should be addressed. Examples of topics for discussion include the relevance of the delta change method, compared to methods directly using climate change projections from regional climate model experiments (again, the corresponding data has been made available for the Pyrenees on the Drias climate data portal, see above). The discussion could also refer to the influence of the snow cover model used for the analysis.

Page 19, line 463 : The section on ROS socio-environmental impacts and hazards provided interesting context, but does not discuss the results of this specific study. I suggest providing this information in a condensed way, rather in the Introduction, because it provides context and motivation for the study, than in the Discussion, because it does not build on the results of this particular study.

Page 20, line 501 : Again, please indicate what « low », « mid » and « high » elevation refer to.

Page 20, line 509 : I don’t see any counterintuitive factor in the study. It is quite obvious, as indicated above, that rainfall fraction and snow cover evolve in different directions, and it is relevant to assess changes in ROS, which is indeed a compound of snow cover state and rainfall. But this is not counterintuitive. Here some of the results are provided in general terms for the entire mountain range, which supports the suggestion before that some results could also be provided for the entire mountain range, in addition to the sub-regional analysis.

Page 20, line 518 : It should be discussed here that the increase in ROS rainfall amount (I suggest, btw, changing ROS rain to ROS rainfall amount, this will be clearer) is not due to any change in climate conditions such as Clausius-Clapeyron effect on precipitation amount, but is only a direct consequence of the influence of temperature on the precipitation phase (what is the threshold used, btw ?), which leads to more cases of rainfall corresponding to previous cases of snowfall under a colder (reference) climate, at potentially different periods of the year. This is another point, which could be discussed in the Discussion section, as it is a limitation of the delta change approach with respect to the topic addressed in this study.

Typos : I noticed some typos in the text, they can be identified by running a proofreading software through the text.