Häusler et al. present a study in which they apply two vibration analysis techniques to rock arches which are assumed to provide more detailed and robust results than previously employed methods. The study covers a relevant, timely and sufficiently novel topic, thus providing originality and an appropriate scope regarding the audience of the journal. The manuscript is in general of adequate quality; the language is scientifically correct and appropriate. Tables and figures are of proper quality with the exception of some too short captions (see below). It is good to see that the data is being made available. With some revision, it will make a valuable addition to the journal.

I see a few general concerns that I think need to be addressed, though. First, the study does not provide any benchmark data, but only relies on comparisons of the results of the two new techniques (EFDD and SSI-COV) – either amongst each other or with respect to results by Geimer et al. (2020). Thus, it is not possible to judge the overall quality/correctness of the presented modal information beyond that relative level of comparison. How can we know that the finer resolved results by EFDD and SSI-COV are real, due to the rock structure, and not just artefacts of either the data collection or the utilised methods? Perhaps this standing question can be solved by citing and discussing existing literature examples that provide the theoretical justification in this respect.

Second, the data are not interpreted in a geoscientific way, hence the implications of the identified frequency modes for the landform. Are the discovered values in agreement with what one would expect for these landform geometries, rock types, stress distributions and environmental settings? I suggest the authors spend a few sentences on establishing the context of their analysis and the journal’s main scope: fostering understanding of Earth surface dynamics. This is especially relevant when considering the pitch given in the introduction.

Third, I see some ambiguities and arbitrarities in the presentation of the methods. It is good to see that the authors mention the multitude of model parameters but then, we simply get a reference to a table in the appendix in which the used parameter values are listed. The problem here is that these parameter values need to be introduced and justified. This should include a discussion of expected ranges, for example based on what other researchers have found or used. This may also include a description of the process that lead to the decision on the ultimate parameter values used. Currently, we have to take the parameter combination at face value, which is a fair bit from transparency and reproducibility.

Fourth, there is a mix of methods, results and discussion in each of the respective sections, which should be resolved. I give detailed comments to this issue further below. And I may emphasise that this is not a crucial flaw but one that should simply be resolved to give the manuscript a clear and organised structure.

l.1, The title is very (if not too) long and it also reads very (if not too) technical, with a lot of quite specific jargon, especially when considering the main scope and readership of the journal. I recommend to shorten the title, remove the detailed technical/methodological terms and in exchange to add more emphasis on the environmental context (e.g. “monitoring rock arch material strength evolution”, but this is just a non-ideal example that I give to reveal what I might expect as a reader to see, feel free to adjust as you please).

l. 9-10, you could also consider motivating the study by a geotechnical pitch, instead of or in addition to the hazard one. Especially since you do not discuss the hazard perspective in the interpretation section, at all.

l. 27-29, you need to better motivate this sentence/abstract. There is a break in logic, here. I suggest you first motivate by the needs to monitor the stability of these landforms. Then you briefly mention the classically used techniques and their shortcomings. Then, this gives you the pitch to identify the research gap and thus motivate the seismic approach as complementary solution.

l. 36, “resonant frequencies arise primarily due to changes in rock mass stiffness”. This is true but there are also other important factors that control the frequency. See for example Bottelin et al. (2013) or the full story told by Lévy et al. (2010). These other important aspects should be mentioned, as well.

l. 41, “more invasive monitoring techniques”, mention these other techniques, perhaps in relation to my comment above (l. 28-29).

l. 81, can you explain why this refers to overlapping modes? Is this specific to the method?

l. 84, “picked manually”, here some information must be given on the criteria used to define these manual picks.

l. 92, please define “output-only technique”, this seems quite generic to me.

l. 99, You need to tell why each of the parameter values was chosen. Currently this is just arbitrary. It seems that the paremeter combinations determine to a significant extent the output of the technique, so this is a crucial part that deserves clear description and rigour. Have you tested different combinations and optimised them manually/iteratively? Have you used values published by other authors? Did you set the parameters just arbitrary?

l. 103-105, this would actually be much better suited for the introduction when you motivate the two techniques and want to convice the reader of their appropriateness. I suggest to move this to the introduction. It certainly does not match here in the results section.

l. 107 “modelled with a low number of modes”, “the maximum number”, please mention what a low number is and what the concrete maximal numbers were, and more important give a justification for these numbers.

l. 111, “user-defined accuracy criteria”, what are these criteria? Please describe and justify them.

l. 116, actually I would like to see the “raw” data, in this case the spectrograms or spectra, if just to be convinced that from these raw products one cannot already see the same frequency modes as in the advanced analysis.

l. 126, Fig. 2, it might help to colour code the singular value lines to indicate which is the first, second, third SV (a legend would be needed in that case, too). Also, this figure should contain the PSDs of the data sets to compare the new outcomes against them. In panels c, f and i, it remains elusive to me when a pole is defined stable and when not. Is there any criterion that was used? For example in c around 2.7 Hz there are many apparently stable values that still are plotted as blue crosses.

l. 133-151, there are many occurences of interpretations in this part. Please separate presentation of results and their intepretation throughout the text. Here is just an example.

l. 141, what means “good agreement”? Please quantify or leave it.

l. 159-163, This approach has not been mentioned in the methods. Please move it to the methods section and also give more context and information on SDOF.

l. 163, “half-power bandwidth technique”, here as well this may be better mentioned in the methods section (or introduction if it is more appropriate there) but in any way, some short explanation of the term and its implication needs to be added, especially in a non-seismologist journal.

l. 176-185, this section is also full of repeated interpretations of results. Please separate these materials into the appropriate sections, “Results” and “Discussion”.

l. 189/Fig. 3, the cation is too short and gives too little context about the presented material of this figure.

l. 206-208, this is repetitive and redundant. Consider removing.

l. 208, what means “well suited”? Can you quantify this? Besides, how do you know the methods a re well suited if there is no independent benchmark data to compare against? Data like rock mechanical model predictions of expected frequencies and their degree of overlap? Ovreall, this will be tricky to show. See my general comment on this issue.

l. 209-211, How can we be sure these are not just artefacts but indeed emerging due to a “better” approach?

l. 216-220, these descriptions are not really an outcome/implication of this study but rather a generic property of the method that should be better mentioned in the introduction (or methods section).

I shall add to the review letter submitted earlier that this letter was based on a different manuscript version (still downloaded from the website just upon being nominated as referee) than the one, which is available, now. However, the main arguments I made in my letter still hold, also for the currently available manuscript version. I can understand if the authors consider some of the detailed comments from the list after the general issues irrelevant, especially if these refer to typos or smaller caveats.

This short communication of Hausler et al. presents the comparison of two classical methodologies currently used for operational modal analysis of engineering structures applied. It is an original and interesting idea to apply both methods to geomorphological features such as rock arches. The objective is clear, the paper can be fluently read and the results are interesting. Nevertheless I have several questions and remarks that I would like to be adressed/discussed by the authors before final publication. 

General remarks

Need to exactly define what is EFDD and SSI-Cov methods. I understand is meant to be a short paper, but this are not current techniques in Geomorphology, so some hints will help readers a lot. Especially, how the damping is estimated by each method ? and what are the main processing steps in both.  

Need to specify and discuss that only two of the four sites have array data. So, for example, what is the advantage to use advanced techniques in single station measurements ?

Specific Remarks

Abstract. 

Line 14-16 "Therefore, we investigate two algorithms well-established in the field of civil engineering through application to a set of natural arches previously characterized using conventional seismological techniques." 

-I would not call "algorithms" but instead "methods" for EFDD and Co-SSI. 

-Please specify what do you mean by "conventional seismological techniques" -> may be the polarization analysis (Lines 17-18) ?

Line 19: the authors state that the proposed advanced techniques have "the capability to resolve closely spaced modes and provide stable damping estimates" and provide "more detailed characterization of dynamic parameters". After reading the whole paper, I'm not convinced that the results presented validate both statements (unless dynamic parameters, the authors mean exclusively modal shapes and frequencies) 

Introduction

Line 71. EFDD is really "well-suited" for distinguish closely spaced modes ? Can the authors underline what enhanced EFDD is compared to FDD ? 

Line 80-85. Sort of repetition of the main capabilities of each proposed advanced technique. Please delete.

Line 84. The authors suddenly include "rock slope instabilities", but they were not studied in the present work. Please clarify or delete.

Methods

Line 85. The methods section begins with the site presentations and instrumentation. Please adapt the section's title. The authors should clearly specify why each site has been chosen for the present study. Different instrumentations have been applied (See my General Remark).

Line 114. Please specify "data residuals" of what ? : Velocities, cross-correlation traces, at which sensor, components, etc. 

Line 117. "Modes (i.e. Poles)" Need a MUCH longer explanation.

Line 120-125. This paragraph fits better in the Introduction part : the fact that the two methods have been previously compared in other context.

Line 130. This paragraph include technical details of the SSI that are not clearly followed by the reader. Please clarify

Results

Line 137-140. The authors state that damping values for the fundamental mode are quite different from the three techniques. By the way, the authors should previously define the "half-power bandwidth method" used by Geimer (2020), with respect to the "mode bell" fitting of EFDD.

Line 135. For this example of Rainbow Bridge, it may help the reader to recall that here a single station analysis is being used, and that is the reason a single Modal vector is compared.

Line 153. Corona Arch. It seems here two closed modes are found between 5.0 and 5.4, but EFDD and SSI_Cov indicate exactly the same frequency ! So the advanced methodologies were not indicated to separate close modes ? Please rephrase the paragraph to explain this behavior. 

Line 158. The concept of "modal incidence" is not clear at all. Please redefine. In fact, could the authors propose other terminology (for the single station measurements) because it is quite confusing. I would not see an "incidence" angle for a mode. If I understand correctly, the authors would like to compare vector orientations in 3D, it is not better simply "azimuth, dip and rake" ?

Line 160. here again damping values are different. Reasons ? Can the authors advance any uncertainty for each estimation ? 

Line 164. Squint Arch. Mode splitting is proposed here for the two close modes at 11.5-12.5 Hz cause by anisotropy. I do not have access to the work of Geimer et al (2020) but it looks that "homogeneous numerical model" does not reproduce a mode-splitting phenomenon.

First I guess "homogeneous" should be replaced by "isotropic". In fact, it may be the case that heterogeneous (though isotropic) models may present these two modes with quite close frequencies, but completely different modal shapes. In fact, it seems to be the case from the EFDD results of the later experiment with the 6 node stations : the first one seems to be a longitudinal mode, while the second one seems to be bending in the transvere direction. Is that also confirmed by the single station analysis ( azimuth/incidence ) ? This should be discussed in the paper. In fact why looking to anisotropic models (rather complex) when may be a numerical modal analysis could support this two "close" modes ? It may be useful for the readers to get the Figures from Geiger et al (2020) co-author included in the present paper.

I can not see why the full modal analysis with many sensors is not much exploited. For example, there is also the strange phenomenon of mode f3 (near 20 Hz) that completely dissapears in the second campaign. It would be really helpful to compare the recordings from the broadband seismometer (1st campagin) and the node exact (or closely) located node for the 2nd campaign. This would be quite useful for new planned operational modal analysis campaigns with node-type equipment. 

Line 187. Puzzled about this interesting active experiment. More information needed. 

 

Last thing, about Squint Arch. What would be the damping value estimated from the EFDD or SSI of the nodal campaign ? The peaks in the SVD looks quite different from the ones of Figure 2c). It will be useful to compare the two campaigns in light of different instruments, number of sensors, both for frequency and damping characterization. Which is the impact ? 

Lines 210-215. It is rather dissapointing that the experiment with the higher number of sensors (2x16) is not much further discussed (with respect to the other 3 cases, only one paragraph !). For example, two lines were measured: synchronously ? with a reference station ? how much time duration ? Were these the same instruments that the ones in Squint Arch ? Why a twisting mode (torsional mode) is not being identified ? What about the dimensions (especially width, thickness) of the arch ? 

Discussion and Conclusion

Line 227. I'm not fully convinced about the statement that both methods are "well-suited" to determine all dynamic parameters. Please rephrase, the objective of the paper was to look to differences in parameter determination. Anyway, the differences are important and the instruments for data acquisition seem to have much stronger impact than the methodology. Comment on that ?

Lines 235-240. Damping estimation (even with EFDD and SSI-Cov) is always difficult and I'm not convinced that the advanced techniques are more "robust" than the half-power bandwith picking. Is there no "spectral smoothing" in both advanced techniques ? In the EFDD a "mode bell" is fitted to an SVD singular value, then back transformed in time, and measured by logarithmic decay; and in SSI-Cov, as far as I understand, there is also a parameter fitting in the least-square sense. No smoothing and/or regularization at all ? 

In conclusion, I advise the authors to revise this paragraph, specially the statement concluding that more advanced techniques would give more robust estimates of damping. Robustness may only be assessed if a detailed uncertainty analysis is carried out: different time windows, spectral estimation, etc.

Line 239. "determined by the active impulse measurement at Squint Arch." I'm really puzzled about this experience. There is not much information in the manuscript. If an active impulse was used (hammer?) , I could imagine relatively high frequencies involved. How damping at high frequencies can/may be compared with damping at the whole structure scale (freq < 15 Hz) ? I think the authors should give much more information of the active experience in the present paper.  

Line 245-255. On the other hand, I agree with the authors about the capabilities of sensor arrays to better characterize modal shapes of different rock arches or geological structures compared to a single station approach.

      

Line 254. homogeneous "isotropic" models.