General comments

In the manuscript, “Multi-sectorial impacts of Mediterranean snow droughts on mountain socio-ecohydrology,” the authors characterised snow droughts across Italy for about the last decade and analysed the cascade impacts on the mountain landscape, that is, snow-vegetation-streamflow-people. I enjoyed reading the manuscript and think that the approach, which tries to tackle drought as a whole across the mountain system, is extremely valuable and much needed. However, the manuscript's storyline is sometimes unclear, and in some sections, the analyses seem somewhat independent. In addition, different periods and locations are used for each analysis, which also contributes to that slightly confusion. My comments aim to go in this direction: keep an integrated story using the propagation cascade you showed in Fig. 9 as the common thread from the beginning of the paper.

Specific comments

Title

I feel the title is a bit confusing. To me, it is not clear what the cause-and-effect relationship is. That is, snow drought impacts different sectors, and these sectors condition the mountain socio-ecohydrology, or are the different sectors conditioning snow droughts and then impacting mountain socio-ecohydrology? What are these multi-sectoral impacts? Is hydrology one of these sectors? I also think it would be nice to specify in the title that the work is carried out across the Italian mountains as a representative case of the Mediterranean mountains.

Introduction

• Since the Mediterranean mountains are the target area of the study, I suggest adding a paragraph explaining a bit about the particularities of the Mediterranean mountain systems (snow-vegetation-streamflow-people). Among them, I think it is important to mention the roles of snow evaporation and snow sublimation in the water balance.
• I miss a sentence with the main aim of the paper. Line 73 points in this direction; however, it is followed by a dataset description, which masks it. I suggest rewriting this objective, moving the scientific questions (lines 80-83) closer to it, and sorting them according to the previously suggested cascade.

Materials and Methods

• The current headings’ structure is not clear; the use of the word impact in both data and analysis is confusing, at least to me. Maybe an explanatory summary methodological figure would help. Another option, maybe also complementary, would be to keep just three main subheadings: 2.1 Study region, 2.2 Data, and 2.3 Analysis, and to change those under data to the type of data (for instance, meteorological, hydrological, vegetation, and societal) and those under analysis to the analysis carried out following the same structure.
• Figure 1 mixes study site data with results. I would keep only panel (a) from the current figure, and I would add some of the information written in the description of the study site here: meteorological context, land cover distribution and watershed districts. I would also zoom in on the selected catchments and draw their borders.
• Line 161, please add more detail about the BIGBANG dataset, for instance, is it a monthly or daily dataset? Is it a reanalysis product or an interpolated product from ground observations?
• Lines 164-169, please contextualise this paragraph. I do not understand it.
• Table 1, I suggest adding the data's spatiotemporal scales to this table.
• Line 176, please add some uncertainty information for the PML_V2 product.
• Line 250, if I have understood correctly, the paper defines a snow drought on an annual basis, that is, for each hydrological year, just a snow drought can be defined, and in the case this snow drought exists, the year is classified as a snow drought year. Please add a sentence to clarify that.

Results

• I would include in section 3.1 a new figure with Fig 1 panels (b) to (e). In addition, I suggest replacing the probabilistic density function graphs with boxplots, following the same design used in Figs. 4 and 5.
• As stated in the previous section, I suggested splitting snow from streamflow sections.
• 2 and 3, following the previous comment, I think boxplots are a better option for representing differences between snow drought and non-snow drought years.
• Section 3.3, in the analysis at the different catchments, have the authors assessed the possible impact that spring precipitation and temperature could have on these results?
• Lines 371-382, I found this analysis very interesting; however, I proposed to remove it or include it in an Appendix since I see it as a complementary analysis.
• Figure 5, change km to m in the x-thick mark to be consistent with the rest of the figures.

Discussion

• I would emphasise and contextualise the discussion more in the Mediterranean mountain context, since the study is carried out in this type of environment.

Conclusions

• Conclusions are short to have the entity of a proper section. I would elaborate further or merging with section 4. Discussion.

In this manuscript, the authors attempt to map snow droughts in Italian mountain regions onto a wide range of impacts (hydrological, ecological, sociological). They use a high-resolution Italian snow reanalysis product to calculate basin-wide snow water equivalent for 38 montane catchments, and identify snow droughts as water years in which the basin-wise December-June average SWE falls below the 30th percentile over the WY 2011-2023 period. They then identify how warm-season runoff and runoff efficiency in their catchments differ between snow drought and non-snow drought years; examine differences in vegetation phenology and productivity derived from remote sensing, as well as two in situ flux towers; and characterize societal impacts using reports of water restrictions and surveys of mountain hut managers. They find reduced runoff and runoff efficiency following snow droughts, modest increased gross primary productivity, and water supply impacts.

Overall, I found the manuscript very interesting, as understanding the impacts of snow droughts in a non-stationary climate is important to informing adaptation in snow-dependent regions. The effort to bring together the multifaceted impacts of snow-drought from a variety of different data sources was impressive. I also found the paper generally well-organized and well-written. I do, however, have a couple significant concerns about some of the methods and framing of results that I feel need to be addressed before I would consider the manuscript ready for publication. I detail each of these points below.

Major Comment 1: Choice of snowpack measure 

The authors characterize the winter snowpack by taking the average basin-wide value over the December-June period, including no snow days. My concern is that this measure does not capture just snowpack accumulation, but also aliases the length of the accumulation and melt seasons. For instance, a basin could reach the same peak SWE in year 1 and year 2, but if the snowpack begins accumulating at different points (say 1 December versus 1 January), the measure the authors use would report a very different value, even though the following warm season would likely be very similar hydrologically, at least from a snowpack perspective. Additionally, even if a fixed window were appropriate, the period seems much too wide. Looking at the histograms in Figure 2, the overwhelming majority of basin-years have snow durations, much less than 200 days, except at the highest elevations, which means that this window includes large chunks of time outside the snow season, especially at the lower elevations. I would strongly encourage the authors to use a more commonly, hydrologically-relevant measure such as basin-scale peak SWE to characterize the snow season. At the very least, the authors would need to validate their chosen measure by examining its relationship to warm-season streamflow vis-a-vis other snowpack metrics like peak SWE to justify its use as a hydrologically-relevant variable.

Major Comment 2: Snow drought definition

The authors define snow droughts as years in which their snowpack measure falls below the 30th percentile over the 2011-2023 period. Essentially, this choice imposes a fixed number of snow droughts (4) for each basin. There are numerous ways to define snow droughts, and the choice of method necessarily affects the set of events identified and thus the set of impacts one might ascribe to them (Gottlieb & Mankin, 2022). I would encourage the authors to consider a broader range of methods from the literature for identifying snow droughts and make sure that their results are robust to that analytical choice. 

Major Comment 3: Visualization of distributions and use of statistics

In Figures 1 and 2, it would be far more informative to show the distributions of local basin-year anomalies of temperature, precipitation, streamflow, etc., rather than the absolute values, as the current distributions largely show the differences in climatology across stations rather than the difference between snow drought and non-snow drought years. By calculating the departures from normal (e.g., degrees for temperature and percentages of normal for hydrologic quantities) and plotting those distributions, it would make those differences much more salient and easier to interpret. It would also make for a more appropriate statistical test, as it would compare within-basin anomalies in snow drought versus non-snow drought years, whereas now it also includes between-basin differences in climatology, which doesn’t provide much information about the snow drought effect. Finally, the numbers the authors report about differences between snow drought and non-snow drought years (e.g., -50% length of snow season, -50% summer runoff, etc.) should reflect these local anomalies (if they do not do so already; I cannot tell where those values are coming from), rather than the pooled distribution.

Major Comment 4: Overinterpretation of GPP results

This is somewhat related to the last point, but the authors do not, as far as I can tell, apply any statistical tests to assess whether the vegetation metrics they examine are significantly different between snow drought and non-snow drought years. My guess is that they are not, as the authors show quite a conservative uncertainty range (inter-quartile range in Figures 5 and 6), and the differences between snow drought and non-snow drought years appear quite modest. Even in the cases with the largest departures above 1500m, the median in snow drought years seems to sit at about the 60th percentile of the non-snow drought distribution, which hardly seems like meaningful support for the claim that GPP is higher following snow droughts. This section either needs to be supported by strong statistical evidence if it exists, or the authors need to report this accurately as a null result — to be clear, it would be a very interesting null result! — if that is indeed the case.

Additional comments

The title is a bit awkwardly worded. I would drop the “Multisectorial impacts of” part, as mountain socio-ecohydrology already captures the fact that the authors are looking at a diverse set of impacts. 

l. 107-108: It would be useful context to provide the snowfall fractions of your mountain catchments, or report values from the literature.

l. 154-155: Are these error values for peak SWE/snow depth? They seem quite large. More detail would be useful here. What are those errors as a percentage of average? How do they vary across elevations?

l. 159: A bit more information about the BIGBANG dataset would be useful. Is it a reanalysis? Interpolated station data?

l. 240: I believe the Hatchett and McEvoy citation is incorrect. In that paper, they identify warm snow droughts based upon 1 April accumulated P > 100% and SWE < 100% of normal and dry snow droughts using 1 April accumulated P < 100% and SWE < 100% of normal. This is a very different snow drought definition than the one the authors use.

l. 341. It is unclear where the number of  a ~100% increase in melt-out events comes from, given that the increase at each individual elevation band is <100%. 

ll. 348-349: It is also possible that warmer summertime temperatures in snow drought years (to which the snow drought itself may or may not causally contribute) drive increased evapotranspiration and thus lower streamflow and runoff efficiency (Goulden & Bales, 2014)

Figures 5 and 6: shading the interquartile range (i.e., the middle 50% of the data, or 6-7 years) is an overly narrow portrayal of the variability in these measures that makes differences appear significant, even when they may not be. I would encourage the authors to either show all 13 individual years (thin and light) with the median heavier and darker, or more of the full range of the data. This would put the snow drought vs. non-snow drought differences in their fully context of the range of variability. 

Figure 7: I don’t believe a boxplot of elevations is appropriate here. Isn’t the number of restrictions more relevant? A clustered or stacked bar plot showing the number of restrictions in different elevation bands would be more appropriate. 

Figure 9: Again, I am not convinced that the results support the GPP/growing season length conclusions. 

ll. 437-438: Your findings run counter to the Trujillo et al. (2012) paper, which finds increased vegetation productivity after snowier winters. Overall, this discussion section could better position your findings in the context of the literature and attempt to explain possible discrepancies between them. 

l. 441 Zhao et al., (2022) also show widespread increases in ET during droughts

l. 445: Pulliainen et al., (2017) also show that early snowmelt advances spring green-up across the northern hemisphere and enhances springtime carbon uptake, which feels like an important part of the literature to cite. 

ll. 456-464: Much of the difference between the grassland and forested site likely has to do with the fact that soil moisture was measured at 30cm, while trees typically have much, much deeper rooting depths that allow them to access deeper soil water and/or groundwater or water in fractured bedrock, which respond more slowly to hydroclimatic variability (Baldocchi et al., 2021; McCormick et al., 2021)

Review references

Baldocchi, D., Ma, S., & Verfaillie, J. (2021). On the inter- and intra-annual variability of ecosystem evapotranspiration and water use efficiency of an oak savanna and annual grassland subjected to booms and busts in rainfall. Global Change Biology, 27(2), 359–375. https://doi.org/10.1111/gcb.15414 

Gottlieb, A. R., & Mankin, J. S. (2022). Observing, Measuring, and Assessing the Consequences of Snow Drought. Bulletin of the American Meteorological Society, 103(4), E1041–E1060. https://doi.org/10.1175/BAMS-D-20-0243.1 

Goulden, M. L., & Bales, R. C. (2014). Mountain runoff vulnerability to increased evapotranspiration with vegetation expansion. Proceedings of the National Academy of Sciences, 111(39), 14071–14075. https://doi.org/10.1073/pnas.1319316111 

McCormick, E. L., Dralle, D. N., Hahm, W. J., Tune, A. K., Schmidt, L. M., Chadwick, K. D., & Rempe, D. M. (2021). Widespread woody plant use of water stored in bedrock. Nature, 597(7875), 225–229. https://doi.org/10.1038/s41586-021-03761-3 

Pulliainen, J., Aurela, M., Laurila, T., Aalto, T., Takala, M., Salminen, M., et al. (2017). Early snowmelt significantly enhances boreal springtime carbon uptake. Proceedings of the National Academy of Sciences, 114(42), 11081–11086. https://doi.org/10.1073/pnas.1707889114 

Zhao, M., A, G., Liu, Y., & Konings, A. G. (2022). Evapotranspiration frequently increases during droughts. Nature Climate Change, 12(11), 1024–1030. https://doi.org/10.1038/s41558-022-01505-3