Summary

In this paper, the authors analyze the scaling properties of lidar-derived snow depth and possible dependencies with topographic and vegetation descriptors in two agro-forested and one coniferous site in eastern Canada. They conduct variogram analyses on snow depth fields to find possible scale break lengths that define regions with self-similar behavior, and develop random forest models to characterize predictor importance. The results show scale breaks spanning 4-7 m in forested sites, and relatively longer values in field areas – up to 18 m in wind exposed fields – in agreement with previous studies. The results also show that wind-related forest edge descriptors mostly explain snow depth variability in agro-forested sites, while canopy characteristics (i.e., forest structure) are more important in the coniferous site.

Overall, the topic, research questions and experimental setup are interesting for the snow hydrology community. The literature review and discussions are quite extensive (maybe more than needed), and the graphics included in the manuscript are very nice. I have three major comments that I think the authors should address before this paper is considered for publication. Additionally, the authors will find a set of minor comments and editorial suggestions that may be helpful to improve the quality of this manuscript.

Major comments

1.    Fractal analysis:

i.    It is not clear from Figure 4 that scale breaks actually exist and, therefore, all the remaining analyses and interpretations remain unsupported, unless the authors demonstrate quantitatively that the snow depth scaling behavior changes. I recommend the authors to revise Mendoza et al. (2020a) as a reference on how to detect scale breaks in variogram analysis.

ii.    The authors need to show quantitatively that variograms hold a power law (which is required to indicate that a spatial pattern is actually fractal). I think that, at the very least, the authors should demonstrate that a linear model in the log-log space holds before and after the scale break, with a high coefficient of determination (e.g., R2  0.9). I also recommend the authors to test whether other geostatistical models are more suitable for this data (e.g., spherical, Gaussian).

iii.    The authors might consider comparing omnidirectional variograms of snow depth (and potential scale breaks) with those obtained from bare earth topography and topography+trees (e.g., Deems et al. 2006; Trujillo et al. 2007). Additionally, the analyses could be enriched by computing directional variograms and associated scaling parameters, in order to establish possible connections with dominant wind directions (e.g., Deems et al. 2006; Schirmer and Lehning 2011; Clemenzi et al. 2018; Mendoza et al. 2020a).

2.    Partial relationships: I think the authors should be more quantitative, since the reasoning provided in section 3.3.3 is subjective and difficult to follow. You can easily improve this section by computing the Spearman rank correlation coefficient, and reporting the p-values. I suggest avoiding statements like ‘strong relationships’, ‘stronger that’, ‘slight decrease with increasing’, etc.; instead, you can show the numbers and let the readers judge.

3.    The authors may consider using the following sequence to display RF results:

i.    Exploratory analyses with scatter plots of snow depth vs. predictors (current Figure 6). In any case, I recommend the authors verifying these results, since it's very odd that there is practically no scatter along the y axis. Are you displaying all points within your domains in each panel?

ii.    RF model performance (i.e., modeled vs. observed snow depth, current Figure 7) for training and prediction periods (a 2x3 panels plot, with the top row for training, and the bottom row for OOB).

iii.    Results for predictor importance (current Figure 5). How different are these compared to those obtained with the training dataset?

Minor comments

4.    L25: Do the authors mean “physically-based models”? Note that all hydrological models (even simple bucket-style models) are, to some extent, process-based (see discussions in Hrachowitz and Clark 2017).

5.    L37: Do you mean vegetation density?

6.    L39-40: You might want to read and cite the work of Deems et al. (2013).

7.    L43: Please clarify what you mean with high-resolution. In L43 you say <100 m, but in the following line you say <10 m. Also, I suggest providing references for micro and meso-scales, and reviewing the study of Tedesche et al. (2017).

8.    L48-49: The authors should include other studies that also reported multiscale behavior in snow depth (Helfricht et al. 2014; Clemenzi et al. 2018; Mendoza et al. 2020b). The latter is particularly relevant for this study (and the discussion in L432-433, L445-447), since the authors found 4-m scale break lengths (similar to what is reported here) at the only Andean vegetated site they examined.

9.    L50: I think the authors want to say “different combinations of processes”. Also, I would precise that you refer to the importance of horizontal resolution, not only for the measurement scale, but also to inform model scales.

10.    L62: Please note that process-based models are assemblages of hypotheses about the functioning of hydrological systems. Accordingly, models might be missing processes (e.g., avalanches, blowing snow) that are relevant in particular locations, and hence not all of them are applicable to all conditions (see discussions in Clark et al. 2011).

11.    Table 1: Was the snow-on flight conducted right after a storm? I think this information is relevant to establish possible connections between your snow depth results and dominant winds.

12.    L182-183: If your aim is to analyze wind effects on snow redistribution, you should filter your data considering (i) wind speeds above a threshold (e.g., 4 m s−1) and (ii) air temperature below 0°C when snow transport by wind is most likely to occur (e.g., Trujillo et al. 2007). I also recommend the authors to revise Li and Pomeroy (1997).

13.    L197-198: I recommend the authors to explain with words what the canopy cover and the gap fraction are, before providing details on how you compute their values.

14.    L205-209: I think this explanation would greatly benefit from a diagram showing what a forest edge is, a hypothetical dominant wind direction, windward, leeward, and the maximum search distance.

15.    L241: How did you define the maximum lag distance for variogram calculations? Note that Sun et al. (2006) recommended setting it to half of the maximum point pairs distance for variogram calculations.

16.    Figure 3: It would be helpful having the site names here, hopefully between the top and the bottom panels. You could also include the maximum snow depth, the coefficient of variation (CV) and the skewness to compare field vs. forest. Even more, the authors might consider merging Figures 1 and 3 into a unique Figure, to make it easier to see the snow accumulation patterns they describe with the various land cover types.

17.    L279-280: This is really hard to visualize. Do we really need this level of detail?

18.    L286-287: Where are those snow depth intervals coming from? They don't seem to reflect the actual ranges.

19.    L295-296: Where are you showing this? I don't see it in Figure 3.

20.    L297: I think what you actually mean is "multi-scaling". Multifractal implies a continuous spectrum of fractal dimensions (Mandelbrot 1988). Also, you should define what a fractal is (perhaps in the methods section).

21.    Section 3.3: there are too many acronyms in this manuscript, making it difficult to follow the reasoning. I suggest deleting some or replacing them for more intuitive ones.

22.    Figure 5: Perhaps it would be easier to understand these results if you linked the different symbols with straight lines.

23.    L357-358: this is not clear from Figure 6. Can you please provide a better explanation?

24.    L383: I think it’s the other way. Figure 7 shows RF model estimates vs. observed snow depth.

25.    L424: ‘more spatially continuous’. What do you mean with this? It seems to contradict the previous sentence.

26.    L444: I think here you should cite Mendoza et al. (2020b) and NOT Mendoza et al. (2020a).

27.    I think section 4.3 could be largely condensed. You may also consider shortening the introduction.

28.    L479: ‘At the combined scale’. I think it is more appropriate to write ‘At the full domain’.

29.    L489: I think that you mean Hydrologic Response Units (HRUs).

30.    L490: ‘successfully modeled’. Can you please provide some numbers demonstrating that the hydrologic modeling was indeed successful?

31.    L518: These results seem quite poor. Did you compare RF performance with multiple linear regression models?

32.    L532-533: I would not even mention those references, since NSE is not a good metric to assess the spatial accuracy of model simulations. There are other performance measures for such purpose (Koch et al. 2018; Demirel et al. 2018; Dembélé et al. 2020).

33.    L558: I would avoid referring to ‘improved accuracy’, since RF model results are quite poor.

34.    L567: ‘forest structure variability’. Do you mean spatial or temporal variability?

Suggested edits

I have provided some editorial suggestions. However, I think that the manuscript would tremendously benefit from a language revision.

35.    L13: ‘for the accurate prediction’ -> ‘for accurate predictions’.

36.    L28: delete ‘problematic’.

37.    L34: ‘on the downstream hydrograph’ -> ‘on downstream hydrographs’.

38.    L56: ‘The knowledge’ -> ‘the estimation’.

39.    L60: delete ‘modeling approaches like’.

40.    L77: ‘that used RF algorithm to express’ -> ‘quantifying’.

41.    Table 1: ‘mm/y’ -> ‘mm/yr’.

42.    L150: ‘were quantified’ -> ‘were obtained’.

43.    L153-155: I suggest writing the sentence between parentheses in a separate sentence.

44.    L162: ‘When taking into account’ -> ‘Considering’. Delete ‘that was typically’.

45.    L163: add a comma after ‘environment’.

46.    L165: ‘to represent’ -> ‘represent’.

47.    L165: ‘As well’: I find this term quite odd. I would replace by ‘Additionally’, ‘Further’, ‘Moreover’, etc. (this comment applies for the entire manuscript).

48.    L180: ‘which gives’ -> ‘, providing’.

49.    L182: ‘from the hourly’ -> ‘from hourly’.

50.    L250: ‘two thirds… is’ -> ‘two thirds… are’.

51.    L266: delete ‘of a variable’.

52.    L314: delete ‘to allow’.

53.    L321-322: rewrite as ‘…LAI and WFE have the highest (64 %) and least (3 %) impacts, respectively, on snow depth…’

54.    L323: ‘acting in forests and fields’ -> ‘in such environments’.

55.    L407: ‘In our results’ -> ‘our results show that’.

56.    L415: ‘… suggests microtopographic… ’ -> ‘…suggests that microtopographic…’

57.    L458-459: Awkward sentence. Please re-write.

58.    L462: ‘by the preferential’ -> ‘by preferential’.

59.    L470: Delete ‘Whereas’.

60.    L475: ‘and dominates’ -> ‘dominating’.

61.    L487: ‘in the melting’ -> ‘during the melting’.

62.    L488: ‘challenge the’. Delete ‘the’.

63.    L512: ‘could be due to’ -> ‘could be explained by’.

References

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Clemenzi, I., F. Pellicciotti, and P. Burlando, 2018: Snow Depth Structure, Fractal Behavior, and Interannual Consistency Over Haut Glacier d’Arolla, Switzerland. Water Resour. Res., 54, 7929–7945, doi:10.1029/2017WR021606.

Deems, J. S., S. R. Fassnacht, and K. J. Elder, 2006: Fractal Distribution of Snow Depth from Lidar Data. J. Hydrometeorol., 7, 285–297, doi:10.1175/JHM487.1.

——, T. H. Painter, and D. C. Finnegan, 2013: Lidar measurement of snow depth: A review. J. Glaciol., 59, 467–479, doi:10.3189/2013JoG12J154.

Dembélé, M., N. Ceperley, S. J. Zwart, E. Salvadore, G. Mariethoz, and B. Schaefli, 2020: Potential of satellite and reanalysis evaporation datasets for hydrological modelling under various model calibration strategies. Adv. Water Resour., 143, doi:10.1016/j.advwatres.2020.103667.

Demirel, M. C., J. Mai, G. Mendiguren, J. Koch, L. Samaniego, and S. Stisen, 2018: Combining satellite data and appropriate objective functions for improved spatial pattern performance of a distributed hydrologic model. Hydrol. Earth Syst. Sci., 22, 1299–1315, doi:10.5194/hess-22-1299-2018.

Helfricht, K., J. Schöber, K. Schneider, R. Sailer, and M. Kuhn, 2014: Interannual persistence of the seasonal snow cover in a glacierized catchment. J. Glaciol., 60, 889–904, doi:10.3189/2014JoG13J197.

Hrachowitz, M., and M. P. Clark, 2017: HESS Opinions : The complementary merits of competing modelling philosophies in hydrology. Hydrol. Earth Syst. Sci., 21, 3953–3973, doi:10.5194/hess-21-3953-2017.

Koch, J., M. C. Demirel, and S. Stisen, 2018: The SPAtial EFficiency metric (SPAEF): Multiple-component evaluation of spatial patterns for optimization of hydrological models. Geosci. Model Dev., 11, 1873–1886, doi:10.5194/gmd-11-1873-2018.

Li, L., and J. W. Pomeroy, 1997: Estimates of Threshold Wind Speeds for Snow Transport Using Meteorological Data. J. Appl. Meteorol., 36, 205–213, doi:10.1175/1520-0450(1997)036<0205:EOTWSF>2.0.CO;2.

Mandelbrot, B. B., 1988: An introduction to multifractal distribution functions. Random Fluctuations and Pattern Growth: Experiments and Models, Springer, Dordrecht, 279–291.

Mendoza, P. A., K. N. Musselman, J. Revuelto, J. S. Deems, J. I. López‐Moreno, and J. McPhee, 2020a: Interannual and Seasonal Variability of Snow Depth Scaling Behavior in a Subalpine Catchment. Water Resour. Res., 56, doi:10.1029/2020WR027343.

——, T. E. Shaw, J. McPhee, K. N. Musselman, J. Revuelto, and S. MacDonell, 2020b: Spatial Distribution and Scaling Properties of Lidar‐Derived Snow Depth in the Extratropical Andes. Water Resour. Res., 56, doi:10.1029/2020WR028480. https://onlinelibrary.wiley.com/doi/10.1029/2020WR028480.

Schirmer, M., and M. Lehning, 2011: Persistence in intra-annual snow depth distribution: 2. Fractal analysis of snow depth development. Water Resour. Res., 47, 1–14, doi:10.1029/2010WR009429.

Sun, W., G. Xu, P. Gong, and S. Liang, 2006: Fractal analysis of remotely sensed images: A review of methods and applications. Int. J. Remote Sens., 27, 4963–4990, doi:10.1080/01431160600676695.

Tedesche, M. E., S. R. Fassnacht, and P. J. Meiman, 2017: Scales of snow depth variability in high elevation rangeland sagebrush. Front. Earth Sci., 11, 469–481, doi:10.1007/s11707-017-0662-z.

Trujillo, E., J. A. Ramírez, and K. J. Elder, 2007: Topographic, meteorologic, and canopy controls on the scaling characteristics of the spatial distribution of snow depth fields. Water Resour. Res., 43, doi:10.1029/2006WR005317.

The study by Dharmadasa et al. explores snow depth distribution at three Canadian sites (agro-forested and boreal forest) based on snow depth maps derived from UAV-LiDAR. Scaling behavior is investigated, and random forest models are used to assess the importance of various topographic and vegetation controls on these snow depth distributions. The topic of the study is of interest to the community, and in general, the manuscript is neatly organized, and the figures are well made. However, I have some methodological concerns that need to be addressed before this manuscript can be considered for publication. A major issue is certainly that the data at hand may not be sufficient to reach the conclusions drawn in the study – in the current state, the key findings and novelties of the study as well as the potential impacts of these findings are not highlighted well enough. Please find my major and minor comments detailed below, as well as some suggestions that I believe would make the study more novel and convincing.

Major comments:

1. In the methods, the authors should state more explicitly that the datasets are published already. Some redundancy with their article published earlier this year is unavoidable but should be kept to a limit. There are instances where the text could be shortened and simply refer to Dharmadasa et al. 2022, I have pointed these out in the minor comments. Watch out for self-plagiarism - Figure 1 and Table 1 are almost identical to Dharmadasa et al. 2022, and need to include a proper reference (e.g. ‘adapted from’).
2. I am not convinced by the choice of aggregating the variables to different resolutions (10-20m) for the RF modelling and related analysis, in my opinion this raises some problematic questions:

• Firstly, I don’t understand why the aggregation of the vegetation parameters is needed at all (L200ff). ‘Canopy height’ and ‘Tree height’ is not necessarily the same thing, and I see no problem with computing canopy height if the pixel size is smaller than the tree crown. Doing so would actually allow extracting the small canopy gaps that have been shown to be the main source of forest snow variability in some other studies (cited in this manuscript), while these gaps are averaged out if the pixels are aggregated to 10-20m resolution. This averaging is likely masking some dependency of snow depth distribution on forest structure.
• Likewise, averaging topographic variables will average out most of the micro-topographic variability that I understood to be the focus of the study. Again, some dependency between snow depth and these variables may be masked by this aggregation. It should be clarified whether the authors are trying to quantify micro-topography or topography.
• I find it particularly problematic to use an aggregation that is larger than the scale break identified in Section 3.2. Doesn’t this mean that the variability that you are trying to explain is averaged out?
• Finally, aggregating leaves you with a rather small sample size, as the surveyed areas are quite small. Especially in the case of Montmorency, the field landcover type covers a very limited area only.
• I would find the analysis more convincing if it was conducted at the 1.4 m resolution, I suggest doing that in view of a resubmission.

3. Some parts of the results chapters require more detail / explanation, and the discussion needs to be more convincing. Some examples:

• Section 3.1: The large overlap of forest and field histogram makes me wonder whether the difference between the two distributions is statistically significant – testing this would be appropriate (see e.g. Currier et al. 2018 for examples of such tests). The inter-site comparison is problematic because data acquisition did occur in different years.
• Section 3.2: It is unclear how the scale breaks were identified.
• Section 3.3.1: You need to better justify why you computed so many topographic and vegetation variables if most of these remain unused in the analysis / RF model. You also need to explain why you used the same predictors at all sites – for instance, NFE and WFE are homogeneous across the forested area in Montmorency forest so it is not surprising that they have no predictive power.
• Section 3.3.3: This section is a bit lengthy, and the key messages don’t quite come through. Maybe it would be better to show fewer subpanels in Figure 6 and focus on the variables that actually exhibit interesting relationships to snow depth.
• In the discussion, you need to comment on the actual benefit of such an RF approach. The model performance shown in 3.3.4 is pretty poor, and it’s not straightforward to extract the interesting information from the plots in Figure 6. In fact, I felt like the most insightful Figure to grasp the snow depth variability was Fig 3, where increased accumulation in sheltered locations is visible by eye.

4. Given that the datasets have already been presented and used in an earlier study by the same work, the added value of the analysis presented in this manuscript seems a bit limited and the novelty of the study is not emphasized enough. What are the key findings, and where will they be useful? I realize that it’s not easy to get more out of such a limited amount of data, but I tried to make sume suggestions that the authors could consider in view of a re-submission.

• If the authors have the opportunity to acquire more data in the upcoming winter, the authors should consider postponing the final analysis to after the upcoming season. Repeated flights over the same site would allow for a much more insightful analysis. It is very difficult to draw conclusions on individual processes based on snow distribution data from one acquisition only, which I think is part of the reason why the discussion does not seem very conclusive. For instance, it could be interesting to see if the snow depth maxima at the forest edges are a recurring feature, and if their effect persists throughout ablation (that’s just an idea, but one could do much more). It would also be good to survey all sites in the same year to allow a more convincing comparison between sites.
• Since the authors analyzed many more terrain and vegetation variables than they ended up using in the RF model, it could be interesting to dedicate a section on the physiographic variables themselves, attempting to identify a set of variables useful to characterize this sort of landscape. Maybe in comparison to variables that have been related to snow distribution in other studies. For example: Elevation has been found to exert a main control on snow depth in complex terrain in other studies, but it is not a really ‘useful’ predictor at the sites used in this study – is this a consequence of the site choice, or is this site representative of the terrain found in the whole ecoregion?
• Exploring the relationships between snow and physiographic variables at different spatial aggregation levels could be interesting.
• Applying additional modelling approaches (statistical, or even physically based) to compare with the RF model could be insightful, especially to draw conclusion on the utility of these findings for later work or practical applications.
• Adding an application of the model results would be a nice addition – e.g. suggest tiling approaches, extend to larger area or entire watershed, etc.

Minor comments (including wording/language suggestions)

L37 ‘topography and vegetation type, and density’ -> you mean vegetation density? Sentence doesn’t read very well, consider rephrasing

L46: a very nice and comprehensive paper on the topic: https://doi.org/10.1029/2011WR010745 - I suggest including this reference

L51 ‘a short scale break is reflected by interception’ -> I would say it’s the other way round?

L62: You should refer to much more recent developments of process-based models, as some of these models now actually do resolve small-scale variability due to heterogeneous canopy structure. See Broxton et al. 2015 (already cited elsewhere) and Mazzotti et al. (https://doi.org/10.1029/2019WR026129 and https://doi.org/10.1029/2020WR027572).

L93: ‘one of the earliest results […]’. I think this is not a very fair ‘selling argument’ for this study, since the data used for the analysis has already been presented in another paper.

L108: incomplete sentence (WMO’s station network?)

Table 1: Winter season -> snow cover period?

L136 is this vertical or horizontal accuracy, or both?

L164: what do you mean by ‘multipath effect’?

L165: you just said the accuracy is comparable to previous studies, so what is the improvement? I would omit the entire end of the paragraph from 162 onward and just refer to Dharmadasa 2022.

Section 2.2.2-2.2.4: Please specify that maps of the variables are found in the supplementary material, I was missing those maps here and found them only much later. Note that the figures in the supplement should include the units for all variables.

L197-199 Is GC = 1-CC? and at what resolution are these metrics calculated, also 1.4m?

L201: How did you estimate crown diameter?

L224: This approach seems a combination of Currier & Lundquist and the DCE presented by Mazzotti et al 2019  (which however has no notion of search distance contrary to your method). Maybe worth noting?

L256: It is not very clear how you define the variable ‘Site’, or at least it wasn’t to me when looking at the descriptor maps in the supplementary material and comparing with the other vegetation metrics. I think this is quite crucial for understanding the edge metrics, hence I more detail is needed here.

L264 Tenses are inconsistent

L266: Variable importance of a variable? Consider rephrasing

Figure 3: specify whether you used the binary variable or the land cover classification to create the histograms.

L308: how did you come to this conclusion?

L310 ‘collinearity analysis suggested discarding GF and CH in favor of LAI at the two agro-forested sites, while LAI was instead flagged as colinear instead of GF and CH in the coniferous site’. Please rephrase – ‘LAI was flagged as colinear’ is unclear (colinear to what?)

Figure 6: Y-axis label missing (snow depth)

L445-446: Unloading through branches should reduce spatial variability, no?

L511-513: The counterintuitive […] stations at the site. -> I don’t understand what you are trying to say here.

L565ff: this section needs to acknlowledge hyper resolution process based (physically based) models (see earlier comment). There are ways to account for fine scale canopy structure, while I would say that the terrain roughness still represents a major difficulty.

L483: I think this should be ‘Hydrologic response units’

Section 4.3: The work from Safa et al. (https://doi.org/10.1029/2020WR027522) needs to be included in this discussion – they applied RF models as well.

Please see attached file for comments.