GENERAL COMMENT

Dear Editor, Dear Authors

I reviewed with interest this manuscript for possible publication in NEHSS journal. The work describes a comprehensive modeling tool to assess shallow landslides initiated by rainfall, in a probabilistic framework. The manuscript provides an interesting contribution in this field, although some aspects are strongly simplified, in contrast with others. The scientific quality is good, the reading is agile although the manuscript is overall a bit long and often dispersive. The literature review can be improved with additional appropriate references of strictly related works. The description of the climate forcing that initiates (or not) the landslide events requires significant improvement.  

To my opinion, the work can be published after some important clarifications and revisions.

SPECIFIC COMMENTS

Please read in the following my specific observations.

1. Literature review (introduction/discussion).

The discussion on the impacts and costs of the natural hazards, from the point of view of insurance institutes, is interesting. However, in general, I found the introduction a bit dispersive, lacking in some aspects. The work of Dietrich and Montgomery, 1994, (SHALSTAB) represents the pioneering work within this approach, and it has been followed by many other deterministic work that gave different contributions in improving the hydrological modeling at support for the shallow landslide, such as the cited Iverson 2000, and, additionally, Rosso et al., 2006; Claessens et al., 2007, Arnone et al., 2011; Lepore et al., 2013; Simoni et al., 2008, Baum et al., 2002 (TRIGRS), Montrasio et al., (2011) (SLIP) (among the others).

With regard to the effect of vegetation, the aspects related to the hydrological effects should be at least discussed, which can sometime be even more significant than the mechanical ones (Feng et al., 2020).

An interesting review are by Chae et al., 2017, Gasser et al., 2019 and the just published by Masi et al., 2021.  (SEE REFERENCES LIST)

2. Definition of the stability problem.

I found the definition of the problem of stability estimation (section 2.2, Figure 2) a bit misleading. It is not clear the definition of the volume of soil to which forces are applied. In the method of the limit equilibrium, under the hypothesis that the width of the landslide is sufficiently large so that the deformations are in the plane parallel to the soil thickness H_soil (i.e. perpendicular to the elliptic landslide in figure 2), forces are assessed by considering a ‘slice’ of soil with unit width (in the direction parallel to the elliptic landslide plane). Figure 2 is confusing and the planes of forces are not well drawn. The limit equilibrium method (and infinite slope model) is based on the hypothesis of large and elongated element with respect to the soil thickness, so that a unit in width element can be considered. Also, P_water is not indicated in the Figure 2. According to the definition in the manuscript, R_lat and F_res apply on different planes. 

I suggest to modify in a 3D perspective the Figure 2 and specify the hypothesis/assumptions.

3. Hydrology and precipitation.

Here is my main comment. The proposed modeling framework addresses shallow landslides that are initiated by rainfall, which is the triggering factor. The approach used (based on TOPMODEL) is extremely simplified because based on steady state conditions, which do not take into account the transient of the hydrological processes (Chae et al., 2017). The authors declare the limitation of the approach used in the discussion section, but this should be clearly stated soon in the methodology. As correctly written by the author, the stationarity is supposed to be reached within the hour of timestep. Clearly, this cannot be largely verified.

That said I arise two more critical issues that are not mentioned by the authors:

• under unsaturated conditions, soil (especially fine and clayey soils) exerts a strong water uptake effect due to suction, which leads to an apparent ‘hydrological’ cohesion. This represent a further limitation of the Montgomery and Dietrich approach that the authors should mention (see, works mentioned in Chae et al., 2017, e.g. Lepore et al., 2013).
• In the description of the model application (section 3.4.2) it is not clear how rainfall initiating events are selected. If I understood well, only events of 1hour duration are selected, whose intensity is identified from the Depth-Duration-Frequency (DDF) curve at different return periods (i.e. from 10 to 100 years). Therefore, I guess 10 events of 1 hours are simulated. Is that correct? If so, it should be explained and justified the reason of analyzing events of only 1 hours, which cannot be ‘critical’ for landslide initiation. Authors should deeply clarify this part in the manuscript, explain the methodology used to define the events, and report the parameters of the DDF curves.

4. Data inventory

The proposed methodology used to characterize the hypothetical landslides (extent) is strictly dependent on the data inventory (section 2.3), as also stated somewhere by the authors. However, it is important that the observed landslides used to characterize the model are of the same type, according to the hypothesis of the stability model used and all triggered by rainfall. Is it so? Please specify.

5. Calibration/sensitivity analysis

With regard to the best set of parameters, my question is: are the found parameters consistent and realistic? For example, I argue the choice of including the precipitation intensity as calibration parameter. As discussed in the previous comment, rainfall represents the triggering forcing and it is a dynamic variable. Ideally, we should know the precipitation intensity associated to each observed landslide. Otherwise, if used as parameter, it seems that the model is tuned ad hoc just to reproduce the past events. If so, which could be its utility?  

Additionally, it would be interesting to see the AUC curves for the calibrated and the best model combinations. The shape of the curve also tells about the model performance.

Then, to my opinion, sensitivity analysis should go before the model calibration. Normally, calibration is done on parameters that are more sensitive. I understand figure 7 and 8, but not sure this is the most efficient way to verify the sensitivity of the parameters. I am curious to see how, for example, the landslide probability varies with the chance of parameters values. This test could be shown with the least and most sensitive parameters.

6. Results

The result of high m_f and low m_c is quite obvious; as the author clearly say in the discussion, and as found by other past works, in the end only few parameters really affect the process: the geometry of the slope (i.e. the soil thickness), the mechanical properties (i.e. friction angle) and the characteristic of the trigger (i.e. precipitation) whose effects are controlled by the soil transmissivity.

With regard to the vegetation: different vegetation scenarios are analyzed (and this is fine). which is the real configuration? Which is the ultimate target of the simulations?

7. General

I suggest to clearly state which is the ultimate main target of the model. Can we use it as forecast tool in an early warning system? If so, in which way? My impression is that it is too constrained to the calibration parameters, which, in some cases, may lose their physical meaning.

TECHNICAL CORRECTIONS

Please see in the following technical observations:

• Abstract: I strongly recommend to reduce the abstract to make it more concise.
• L3: I do not completely agree with this sentence given that there are of works that take into account the effect of vegetation, although from different perspective such as the hydrological one, together with the mechanical one. Please remove this sentence from the abstract, where you do not have room to discuss.
• L72-L80- I suggest to synthesize.
• Figure 1: it is useful and appropriate. However, consider to improve it to make it clearer. Not clear from where to start. “extract mean value for each landslide”: do you mean hypothetical landslide? Emphasize the ‘append’ box where everything converges. Avoid text outside from the box. Also, I suggest to use the symbol used in the section (instead of the description). For example: definition of rho_ls; it would improve the correspondence with, for example, section 2.3.
• Line 417: Not clear which single rainfall event you refer to. I understand that the database include landslide triggered by different storms across the years.
• Lines 378-379: it is not really clear the procedure. Please try to write more clearly.
• Lines 385-386: I understand the reference, but please give an explanation also here, based on your results.
• Section 2.7: how did you define the threshold from daily to hourly??

REFERENCES

Baum, R.L., Savage, W.Z., and Godt, J.W., 2002, TRIGRS – a fortran program for transient rainfall infiltration and grid-based regional slope-stability analysis. U.S. Geological Survey Open-File Report 02-0424. http://pubs.usgs.gov/of/2002/ofr-02-424

Arnone E., D. Caracciolo, L. V. Noto, F. Preti, and R. L. Bras (2016) Modeling the hydrological and mechanical effect of roots on shallow landslides. Water Resources Research, 52 (11), 8590-8612

Chae, BG., Park, HJ., Catani, F. et al. Landslide prediction, monitoring and early warning: a concise review of state-of-the-art. Geosci J 21, 1033–1070 (2017). https://doi.org/10.1007/s12303-017-0034-4

Claessens, L., Schoorl, J. M., and Veldkamp, A.: Modelling the location of shallow landslides and their effects on landscape dynamics in large watersheds: An application for Northern New Zealand, Most, 87, 16–27, 2007.

Feng, H.W. Liu, C.W.W. Ng (2020). Analytical analysis of the mechanical and hydrological effects of vegetation on shallow slope stability. Computers and Geotechnics 118, February 2020, 103335

Gasser, M Schwarz, A Simon, P Perona, C Phillips, J Hübl,  L Dorren. 2019. A review of modeling the effects of vegetation on large wood recruitment processes in mountain catchments. Earth-Science Reviews, 194, July 2019, Pages 350-373.

Gonzalez-Ollauri, C Hudek, SB Mickovski, D Viglietti, N. Ceretto, M. Freppaz (2021). Describing the vertical root distribution of alpine plants with simple climate, soil, and plant attributes Catena, 203, 2021, 105305

Lepore, C., Arnone, E., Noto, L.V., Sivandran, G., Bras, R.L., 2013. Physically based modeling of rainfall-triggered landslides: a case study in the Luquillo forest, Puerto Rico. Hydrol. Earth Syst. Sci. 17, 3371–3387.

Masi, Segoni and Tofani (2021). Root Reinforcement in Slope Stability Models: A Review. Geosciences (Switzerland) 11(5):212. DOI: 10.3390/geosciences11050212

Montrasio, L., Valentino, R., and Losi, G.L., 2011, Towards a real-time susceptibility assessment of rainfall-induced shallow landslides on a regional scale. Natural Hazards and Earth System Sciences, 11, 1927

Rosso, R., Rulli, M. C., and Vannucchi, G.: A physically based model for the hydrologic control on shallow landsliding, Water Resour. Res., 42, W06410, doi:10.1029/2005WR004369, 2006.

Simoni, S., Zanotti, F., Bertoldi, G., and Rigon, R.: Modelling the probability of occurrence of shallow landslides and channelized debris flows using GEOtop-FS, Hydrol. Process., 22, 532–545, doi:10.1002/hyp.6886, 2008.

GENERAL COMMENTS

The authors describe a probabilistic model called SlideforMap (SfM) which generates a map of shallow landslide probability across an area of interest.  The approach is to randomly simulate “hypothetical landslides” across the landscape.  A factor of safety is calculated for each hypothetical landslide based on limit-equilibrium analysis.  Areas with factors of safety less than 1 are assumed to be unstable.  The final output of the model is the fraction of unstable landslides at a given location.

The model requires a total of 22 parameters, 16 of which are deterministic and 3 of which are drawn from probability distributions (each of which is defined by 2 parameters).  The resisting force is based partially on pore water pressures computed using a variation of TOPMODEL, which is justified by assuming the dominant role of macropore flow in pore pressure development.

The novel feature promoted by the authors is the inclusion of basal and lateral root reinforcement from vegetation into the resisting force.  In their case study, the authors demonstrate how they obtain an inventory of trees from an airborne laser scanning dataset.  The authors also argue that the root reinforcement should explicitly depend on the size and spatial distribution of individual trees.

The authors demonstrate their approach using three study areas in Switzerland, each of which has a landslide inventory that the authors use to calibrate the model against.  The authors conduct a sensitivity analysis where they analyze how the marginal distributions of different parameters are related to model performance and to the fraction of unstable landslides.

The authors include a thorough discussion that explores the limitations of the reference datasets in assessing model performance, the assumptions of several model parameterization choices, and the AUC as a performance metric.  Much of this discussion reflects on the differences in the predicted unstable ratio between one of the study areas, St Antonien, and the other two.

The authors have organized their manuscript well, and they have described a complex workflow in a straightforward way.  They also build a convincing case for the utility and need for a model of this type, and the described case studies illustrate the applications well.

In my opinion, this manuscript should be published in NHESS after some clarifications and revisions.  Most of my criticisms are focused on areas where the authors need to provide additional clarifications, either to adequately explain their approach or to explain how this model could be used by others.

SPECIFIC COMMENTS

1. The authors say that their model demonstrates the importance of root reinforcement on shallow landslides, but the authors need to define what “shallow” means so that it is clear where their conclusions apply.
2. The authors are persuasive about the importance of root reinforcement in modeling landslide hazards, but they do not provide much discussion of how this model compares to other previously published models, including both related models (such as SOSlope or SlideForNET) or other models that compute landslide susceptibility on a regional scale. Some additional discussion of where this model fits within the context of other landslide susceptibility models generally would be helpful for prospective users.
3. In describing the methodology, the authors are not always clear about which values are assumed for their own case study, and which values are fixed in the model. For example, at a number of places in the methodology section, the authors assign values and limits on parameters (e.g., maximum HL surface area, mean tree density, precipitation intensity threshold, etc.) based on data from Switzerland (where the case study is located), but it is not clear whether a given user would have the freedom to change these values.
4. The structure of the model requires that soil depth, soil cohesion, and the angle of internal friction be modeled as random variables with normal distributions, but the other 16 parameters are assumed to be deterministic. The authors need to explain why these three parameters specifically were chosen to be random variables.  For instance, variables can be randomized when the uncertainty in their values is either shown or assumed to have the most significant effects on the results.  This is suggested somewhat by the sensitivity analysis for the case of soil cohesion and soil depth, but this choice is not explained explicitly.
5. The authors make use of two datasets, a tree inventory and a landslide inventory, in their analysis. However, they do not spend much time explaining how a prospective user would apply this model if they were lacking these datasets.  It seems that users could still apply this model without these datasets, either by creating synthetic datasets or assuming specific values for the parameters that would be derived from these datasets.  Providing some more guidance on applying the model without these datasets this would make the model more accessible to users.
6. The sensitivity analysis is interesting but not entirely convincing. If strong parameter correlation is at play, as the authors suggest, then how would we know which parameters are truly important? 
7. In a couple of places within the text (L49-52; L169-170) the authors conflate deterministic models with spatial homogeneity. This is misleading, as it is possible to have deterministic models that account for spatial heterogeneity, and probabilistic models that are spatially homogeneous.  I would suggest that the explanation the authors are after is that the spatially heterogeneous values themselves are uncertain, and this is the motivation for using a probabilistic approach.
8. Is it valid to compare the globally uniform vegetation scenario to the other three scenarios if the globally uniform scenario was used to calibrate the parameters?
9. It appears that the authors used the same landslide inventory to both calibrate the dataset and to validate the performance of the model against different vegetation scenarios. Did the authors consider using any portion of the landslide inventory as an independent validation dataset?
10. L44-45.  The authors need to give some additional definition of a deterministic approach and why SHALSTAB is an example of this approach.
11. L128-130.  It seems that the unstable ratio is a very limited metric, particularly if the landslide density is already very low.  Shouldn’t the landslide density be relevant in addition to the unstable ratio?  If there is an explicit requirement that the number of HLs be large enough to compute the unstable ratio with a large denominator, does this effectively put a lower bound on the landslide density for this model?
12. L152-153.  I am surprised that the landslides are generated using a spatially uniform distribution, as this may result in landslides being simulated in areas that are not landslide prone.  What is the rationale behind this?  Shouldn’t they follow a spatially distributed density, or at least be restricted to susceptible areas?
13. L278.  A 2km buffer seems extremely large, especially if topographic wetness is computed over multiple small catchments.  How was this value chosen, and is it adequate for other studies?
14. L407-408.  What does this mean if the unstable ratio decreases when single tree detection is used?  Does this indicate that heterogeneity is important for slope stability, or does it simply mean that the uniform vegetation scenarios are not realistic?

15. Table 7.  Why are the AUC and Unstable ratio values different for the globally uniform vegetation scenario compared to the results with the optimal parameters (Table 6)?  Is this due to the difference in the landslide density?

16. L471-473.  Does this high unstable ratio match with long term observations about landslide occurrence in StA?  In other words, is the unstable ratio realistic?

17. L480.  This suggests that AUC is a poor choice of performance metric for comparing the three study areas.  Are there other metrics which would be better?

TECHNICAL CORRECTIONS

• L14.  This should be “ratio” instead of “fraction.”
• L121.  Does SfM generate a raster image of probability values?
• L134.  Do the authors mean “greater than 1.0”?
• L163.  What does “distance of 10” refer to?
• L 271-273.  What resolution is the unstable ratio computed at?   This is not made explicit here in the paper.
• L300-307.  What is the spatial format of the landslide inventory?  If they are polygons, how are they compared to the unstable ratio map so that the AUC can be computed?  Does the landslide inventory need to be converted or rasterized at a specific resolution?
• L309.  The format for the numbers a,b, and c looks unusual.  Please verify that the values and formats are correct.
• L312-313.  Why are these 11 parameters fixed while the others are varied?
• L332.  What is n?
• L336-337.  Please explain why weighting is being used and how this weighting is calculated.
• L343.  Please explain why the parameter range is using intensity values from different return periods.
• Table 5.  The value for vegetation weight, Wveg, uses a different name and different units than the rhotree in Table 1 (tonne per square meter vs. kg per cubic meter).  Is there a reason for this difference?
• L348.  Is 1000 an adequate size to represent the sample space over the 12 parameters used in the sensitivity analysis?
• L360-361.  Does this model assume that root reinforcement comes only from trees, and not from shrubs, grasses, or other vegetation types?  Is the single-tree detection scenario using the same trees as the tree inventory cited in 3.2?
• L363.  Please verify that the exponent is correct in the expression for landslide density.
• Fig. 8.  How is “x% best” defined for the unstable ratio?
• L403.  Do the model runs assume randomization of the three parameters (as in the original model setup)?
• L508.  Are the 12 parameters all included in the 22 original parameters?