The manuscript deals with the an analytical method for stability analysis of rock blocks susceptible to differential erosion at the base and the corresponding application to a case study in China.

The manuscript is relatively well-written and well-organized, but several doubts regarding the novelty, the methodology and the conclusions proposed by the work arise. Here is a list of questions and comments that need to be clarified:

• English language presents some mistakes throughout the paper and needs to be improved
• Figure 8: it is unclear why for case b (three free faces) there is the scheme corresponding to the side view along the x direction (lower and right portion of the figure), since the corresponding face should not exist. Moreover, the upper captions (side view along the x and y directions) should be exchanged, according to this reviewer.
• Line 156: the sentence “rainfall is the main predisposing factor of rockfall” is strongly questionable from a theorical point of view. Rainfall is universally known to be not a predisposing factor.
• The coefficients k in all the equations at pages 11-13 are not introduced at all. Please, check that all the parameters mentioned are clearly defined in the text.
• The Authors state that, according to the results of in situ surveys, mudstone is not subjected to deformations (line 171). If so, why the need to introduce Fos corresponding to compressive strength (Fos_co) and tensile strength (Fos_te). What happens if these strength are reached? What is the effect of stresses exceeding strength in the mudstone? Please, clarify this point, since it represents a central innovative concept proposed in the manuscript, although it is not sufficiently described in detail.
• Related to the previous point, while the text portion corresponding to the 3D sliding and toppling stability analysis is not new and well-known in the literature, what should be the effect of a Fos_co lower than 1.0 from a physical point of view? Is actually important for the block stability? And what about the effect of a Fos_te lower than 1.0? The phenomenological and physical interpretation of these concepts seem to be not sufficiently investigated by the Authors.
• It seems that in eq. 31 and 32 the terms should be exchanged: st_max should refer to FOSte, while scmax refers to FOSco. Again, terms st_max and scmax have not been defined in the text.
• Lines 289-290: if there is uncertainty related to the choice of the mechanical parameters, has been such uncertainty quantified? Why not providing a range of the parameter values to account for such uncertainty, along with the corresponding results in terms of FOS?
• Figure 10: if a large amount of cases provides FOSte lower than 1.0, why have the authors not observed tensile failure in the field?
• Figure 11b does not show rmax, so line 299 is uncorrect. In general, Figure 11b is not adequately explained. Lines 300-301 are uncorrect, since FOSmin is not always lower than 1 for the points lying above the red dashed line (see points with 1.53, 2.95, 1.06).
• The relationship in Figure 11b (red line) cannot be considered to be generalized for block stability analysis, since the block stability is highly affected by the value of mechanical parameters chosen and the driving factors acting on the block (water level height within the joints, seismic actions), which have been assumed as fixed in the analysis presented. If these input data should vary, the corresponding FOS will change.
• Lines 308-315: this part of the text is highly important because it provides a global interpretation of the conceptual model proposed by the Authors, However, it is excessively synthetic, while it should be enlarged and enriched with a clearer description. The Authors should highlight in a clear way that compressive and tensile states within the block foundation do not provide global instability, as sliding and toppling, but could be only considered as preliminary signs of a possible future failure.
• Line 313: English is bad. Please, revise.
• Figure 14: this reviewer again strongly suggest to avoid emphasizing excessively the generalization of the results in terms of threshold value for stability, for the same reason described above.

Based on the aforementioned comments, the manuscript can be accepted for publication, providing that all the comments described above are discussed in detail.

Dear Authors,

Thank you for your paper submission (egusphere-2022-658).

As a general comment, let me say that the manuscript is relatively well-written at a first view. The methodology is clearly presented. The results section is quite compact taking into account that you studied 22 blocks, although the conclusions might be improved.

Some specific comments follow, addressing individual scientific questions and little issues which raised during the review. At the very end, I grouped some minor technical corrections that I propose to you.

First of all, I fully agree with reviewer 1 in the doubt about the complete novelty of the methodology you present in the paper. The Limit Equilibrium Method (LEM) has been applied for decades to study the stability of rock columns in the cliffs fronts. The well known ‘limitations’ of the LEM are balanced with its simplicity, which makes the LEM an adequate method in a lot of real cases where the data availability is really scarce.

My main concern is that the basic mechanism that you consider is the simplest case when studying the stability of the subsequent blocks close to the cliffs fronts: a prismatic column of rock, isolated from the rock mass thanks to a set of sub-vertical discontinuities, having two or three free faces, also sub-vertical (Figs 6-8). The sub-vertical discontinuities you consider are 100% persistent, but in principle, they are not open because the water can fill the joints and transmit some horizontal trust to the block. On the other hand, the discontinuities are not “closed” because they do not transmit rock to rock reaction, nor horizontal or in shear. This particular situation happens in nature, but we cannot generalize it. Fortunately for the sake of stability, we use to have rock to rock contact: in some parts of the joints there are normal (compressive) and shear stress transmission, highly dependent of the joint roughness and state; whereas in other parts of the joint we can found “rock bridges” (intact rock or cemented), with complex stress distributions, including tensile stresses. Although it is hard to catch all the details of the unstable blocks in figures 1 and 6, one can estimate that even these examples present some variations in relation with the theoretical model: non parallelepiped volumes, steep but not vertical planes, full contact between both joint sides, stair-like joints and so on.

As an example, in your Fig.11b, block W06 (with a Fos of 0.15, r_x and r_y about 0.44) is completely out of the general trend. The block is still stable in the field because of the analysis limitations, probably because the presence of rock bridges.  

You must recognize the huge simplification of the basic LEM mechanism you use in your approach. As far as I read, you only mention the limited scope of your modelling in the Conclusions, lines 363-369, too late according to this reviewer.

In spite of everything, your method is a good systematization of the calculations for situations where the basic mechanism of the rock block fits your basic assumptions and hypotheses. You highlight the importance of basal erosion, and how the eccentricity of the actions at the base of the block (mudstone layer) are keys to explain the evolution towards failure.

The next issue is not a limitation only of your method but is a general drawback of the LEM: it does not consider the deformations. Reviewer 1 pointed out some contradictions in your writing when mentioning the absence of deformation in the underlying material (Line 171). It is better to rewrite this statement: obviously, if some force is applied to the mudstone, it will register deformation. When approaching the toppling failure (figure 7, right) big strain (deformation) will be present. You should mention that the LEM is essentially a Force/Stress/Momentum approach that do not take into account the deformation. The complete stress-strain behaviour (including stress rotation and failure in the mudstone layer) can only be approached with a Finite Element Method (FEM) analysis, although other drawbacks will arise in this case.

As said before, we must keep in mind that the LEM is a convenient but limited method. Thus, we have to be prudent when examining the results and when deriving conclusions. For instance, in lines 341-342 the authors are discussing some results with four decimal places, perhaps too many figures when considering the actual accuracy of the analysis and the block measurements. On the other hand, some of the results in sections 5.2, 5.3 and 5.4 cannot be generalized as pointed out by reviewer 1. The results are highly dependent by the mechanical parameters chosen for the Sichuan basin. Instead of generalizing, you can restrict the conclusions to the study area. However, I must recognize that the critical value 0.33 for the retreat ratio seems reasonable, and coherent with the theory of structural analysis of beams subjected to compression. Another point arises here: Let’s consider a 4m wide block with a cavity of 1 m, i.e. retreat ratio of 0.25, stable situation. What will happen if we find a new (or previously hidden) vertical discontinuity in the middle of the block? The retreat ratio changes suddenly to 0.5 and the block becomes unstable. This reasoning highlights the difficulty when trying to use the critical retreat ratio to new sites after the field reconnaissance.  

The Conclusions section must be re-elaborated, now is too short.

Finally, let me give you some minor, technical corrections.

* Captions must appear in the same page as the figure. Captions must be slightly separated from the main text body.

* Suggestion: Put all the appearances of Fos in italics.

* Line 92: “absence of inventory data”… too sharp to say “absence”. Even in your paper, you have some inventory data… I suggest saying “lack of complete inventory data”.

* Line 100: I guess is “Fig.2c” instead of 2b.

* Figure 2a, inset in the graph, “Sagaseta” instead of “Saganseta”.

* Figure 2, caption: “dimensions b x h”, consider using italics for b x h.

* Figure 2, caption: “dimensions b x h”, consider adding “ and weight W”.

* Figure 2, caption: “N is regarded as…”, consider adding T and W.

* L.110: “to applied” -> to be applied

* Fig 3 caption: wording “tectonic sketch profile of A-A’ “

* Fig.3 caption: “serial numbers”: I think it is not correct. Same in Table 1 columns header.

*Table 1. E5 has 232000 m3… this is not a rockfall!

*Table 1. E5 has  a location (K1741) not matching with its position in the map

*L. 144: “which” Do you refer to the slopes or to the blocks ?

*L. 144: “which are consists”  wording.

* L.80: As is the first appearance of “Eccentric effect”, you must define/explain it.

* L.156, consider using triggering instead of predisposing.

*Fig.5: lower or upper hemisphere?

* Which is the location of the data? E1 to E5 show quite different BP dip/dip direction…

* L.170 “forces” -> “stresses”

* L170-171: “…doesn’t present def.”: See reviewer 1&2 comments”

*L174: “partially”-> partial

*L174: force -> stress

* Fig 6 caption: “dominated” -> dominating

* L183: consider deleting “The predisposing factor’s s of”. And start the statement: “Rainfall and earthquake …

*Fig 8: “x direction” must swap with “y direction”. “along” is a little ambiguous.

Attention: the “z” axis can fall outside the drawings.

*Fig 8 caption: “three free surfaces” -> “three free vertical surfaces”

* L189: “Distributed force”… You mean “Stress distribution at the block base”?

*L194: Are you sure of writing “bending moments”? This is not a beam, better saying “non symmetric stress distribution”

*page 11: most of the lines before the equations finish with a comma (,), better delete it.

* Eq. 8 &9: define the factors K1 to k3.

*L229: “underlying” sandstone? Rewrite all the line, please

*L235: J1? perhaps you refer to F1

*L236: “is not exists”? wording

* L 258: “aggregate”  -> “consider simultaneously”

* L.264: “…blocks is” -> “blocks was”

* L266: are ->were

*L268:Consider rewriting “ are abundantly recorded in the investigation reports and published literatures in this area.”

*Table 2: Wording “obtained from the analytical method in section 3”

* Table 2: consider drawing vertical lines between columns 12 and 13, 17 and 18, and 21 and 22, in order to group the Fos by scenarios.

* Table 2 note: “is not existing” sounds weird to me.

* Table 2 note: Consider moving “ NS-Natural scenarios, RS- Rainfall scenarios, ES-Earthquake scenarios” to the columns header

* L280: Can you improve the section title?

*L296: [0,8º]

* L297: the statement “The shade of the points does not change significantly in the 𝑥𝑥-axis direction,

which indicates that the dip of contact surface has little correlation with rockfall stability in this area” seems to me too audacious.

*L299: shown -> shows

* L300: the statement: “𝐹os min of the points in the upper part are all lower than the critical state (𝐹os=1) “ is false.

*FIG 11 caption: wording

* L312: What does it mean “near”? (the vertical axis is Log)

*L313: Wording: “…well agrees with the field insight, that is most rock blocks… “

* L313: “is higher” -> are higher

*L327: “shown” -> “show”

*L351: ConclusionS.

* L352: Damage only if there are vulnerable elements at risk (people, buildings, cars, roads etc).

* Conclusions section: as stated in the general comments, more stuff must be derived from the study.

*L356: in place -> instead of

*L367: The phrase “However, the natural failure surface may be formed along the

cleavages in the mudstone, which will lead to the changes in mechanical parameters of stability analysis” is not a conclusion derived from the study itself.