“Application of the creeping flow restoration method to an analogue model,” by Melchior Schuh-Senlis, et al. leverages a laboratory scale structural analogue model, which has been imaged through its evolution by a time-series of X-ray tomography images, to validate a novel approach to structural restoration.  The restoration method assumes that deformation may be explained by a viscous rheology modeled using Stokes flow equations, and applies reverse time-stepping to reverse deformation of the structure(s).  Is see this line of research as a critical next step in the development and demonstration of Stokes flow restoration methods. 

However, I have significant concerns about the results that are presented.  Most importantly, the analysis of restoration results and comparison with time-series imaging of the analogue model focuses almost entirely (with the exception of Figure 6) on the first restoration step, corresponding to the final stage (18 minutes?) of the forward model.  This is only a small amount of the total deformation of the model.  The misfit between restoration and forward model at this step is difficult to discern (this is a good thing) but I am sure it becomes greater as the restoration goes further back in time.  The authors do not explain their rationale for focusing only on this final step of the forward model, and it leaves me concerned that an incomplete picture of the study is portrayed in the manuscript. 

Additionally, the pressure (Neumann) boundary condition applied to the right hand side, which is suggested as an enhancement to the model relative to kinematic boundary condition, is not sufficiently justified, from my perspective.  In viscous flow models, deviatoric stress is related to viscosity and strain rate.  How does Poisson’s ratio help to calculate an optimal horizontal traction in this case, and, thus, what makes this boundary condition more physical than the previously applied kinematic condition?

Perhaps it is beyond the scope of this study, but the final results left me feeling somewhat unsatisfied, with no benchmark how the Stokes flow restoration compares to other restoration methods.  I believe that Chauvin, et al. (2018) benchmarked an elastic restoration using the same numerical analog model.  Some comparison of the results could enhance the impact of the manuscript without a lot more work.

Finally, there are many opportunities to improve the organization of the manuscript, as well as clarity and precision of the writing.    I have attempted to identify and assist with examples in the comments below and in the attached, annotated version of the manuscript.

For these reasons, I recommend major revisions before accepting this manuscript for publication.

Specific comments:

The abstract is difficult to follow.  My perspective is that too much focus is placed on general background related to restoration, and too little focus on the background of stokes flow-based restoration.  The last few sentences, focused on the contribution of this work, are vague and worded in such a manner the results and implications are difficult to understand.

The introduction provides a relatively detailed, and helpful, overview of the history of restoration and various methods.  However,

• The detail is imbalanced. Mechanical restoration methods receive quite a lot of focus, whereas kinematic restoration methods are described only very briefly
• Validation of geologic interpretation is an important application of restoration methods, but is never addressed
• The direction that the manuscript is going to take could be made clear earlier in the introduction. The review of restoration methods is good, but left me wondering until many paragraphs into the introduction where the authors are going.  Perhaps the introduction could be shortened and a separate section or subsection added to review kinematic and geomechanical restoration methods.
• The paragraph introducing analogue modeling methods comes out of nowhere. The purpose of the analogue model for this study needs to be introduced first.
• The final paragraphs in which the direction of this manuscript is laid out might be explained more clearly (see annotations)

Section 2.1 (Creeping Flow Restoration) is a good overview of the method.  Though published previously, it is sufficiently important to reiterate in this manuscript.  A few minor suggestions include:

• Describe somewhere the viscosity model you use. I believe you assume a linear viscous fluid with constant viscosity, but this should be clarified
• A brief introduction to the section on what is stokes flow and why it is used here would be helpful.

Section 2.2 (The FAIStokes code) is summarized significantly and references Schuh-Senlis et al (2020) appropriately. 

• Because the numerical method is not the focus of this publication, I wonder if this section could be abbreviated further. Is Figure 2 (flowchart showing numerical implementation) necessary? 
• How is the free surface is implemented and (how) is the material above it is addressed in the numerical scheme.

In Section 3 (Presentation of the Analogue model), I have made quite a few suggestions and posed several questions to the authors.  To summarize,

• The model could be explained better. Specifically, what is the right-hand-side boundary of the model? How are the layers deposited through time? How do the material properties of the silicon, sand, and pyrex scale in both space and time to geologic materials and structures?  See annotations for additional detail.
• The description of X-ray tomography and how it is used may not be clear to an unfamiliar reader. Need to specify that it is an imaging method.
• The header title “Available data” is vague and unclear. I would suggest  merging this section with the analogue model description in the prior paragraph and relabeling the section something like “Analogue Model Description.”
• Section 3.2 (Creation of the Numerical Model): Please clarify what is meant by “numerical model.” This section refers specifically to the geometry to be restored and its discretization on the mesh.  Stokes flow and the implementation in the FAIStokes code is another numerical model not addressed here.
• In section 3.2, please address the mesh resolution and particle density per cell, in addition to the swarm.
• The final paragraph addressing the use of X-ray tomography images to determine the height of the topography after the deposition of each layer seems out of place. Boundary conditions are not otherwise addressed in this section, and the time-series of tomography images has not been adequately introduced.

Section 4 (Boundary condition analysis)

• It might help to put this section in the context of how boundary conditions have been dealt with in previous applications of Stokes flow restoration, especially the 2020 paper by the same authors. I tried to read this manuscript in the context of that prior work and was left wondering because I think that this study begins with a different approach (this may be fine, but I found it confusing).
• I have made several suggestions to clarify wording in the annotated manuscript

Section 4.1 (Restoration using kinematic boundary conditions)

• Please specify if gravity is applied in this model
• The paragraph beginning line 223 seems primarily relevant to the numerical implementation, and I’m concerned it will be a diversion to the average geologist reading the manuscript (it took me some effort to understand). Perhaps it could be moved to the numerical implementation section, or explained in a more intuitive manner?
• Figure 6 is a nice time series of the restoration model, but only (b) is compared to the tomography reference image. Why?  Also, why is this the only time-series of restoration results?  I would like to see a similar time series and comparison to tomography images for the preferred model described in section 5 also.  The absence of this rigorous comparison leaves me feeling like the analysis presented in this manuscript is incomplete.
• I have made several suggestions to clarify the captions of figures 7 and 8
• In figure 8, is d_reference(x) always positive? Or does it represent an absolute value? I cannot see in figure

Section 4.2 (Upgrading the kinematic conditions to natural boundaries)

• At the start of section 4.2.1, please explain more completely the restoration model to be performed. In particular, what is the boundary condition applied to the top of the model in this case?  I had to read on some way for this to be clear.
• It is unclear to me how the pressure boundary condition applied to the right side of the model relates to the forward analogue model. In viscous deformation, deviatoric stress relates to strain rate.  Why is Poisson’s ratio used here?  What makes this boundary condition more physically realistic than the kinematic boundary condition applied previously?
• Building on this, it is unclear to me (and not addressed sufficiently in the paragraph beginning line 273) what might be the implications for model precision.
• In figure 11, it would be helpful to include the topography before restoration as an additional reference, beside the expected flat topography.
• The legend of figure 11 is unclear, because (a) and (b) refer to the right hand side boundary condition, but this is not specified. Reading the text, it says that the top surface is treated as free in fig. 11.
• The caption of Table 6 could be shortened by referencing Table 5 (similar to what is done with Figures 8 & 10
• The last sentence of this section makes a broad statement that is, so far, unjustified. This should be presented as a hypothesis or it should be specified that this will be demonstrated in the next section.

Section 5 (Model parameters analysis)

• The section header I believe refers specifically to material properties… please say so.
• In line 305 a statement is made regarding the ratio of viscosity between overburden and silicone. Please explain this better.  Where does this ratio come from?
• I like figure 13! It’s a good visual display of the DOE study.
• In line 325, I do not follow what are the “computational instabilities” shown in Section 4.2.2.
• In the sequence of figures 14-16, the authors focus on results at the final time step of each simulation. However, as a geologist, I am most interested in the optimal time step (i.e. the results when each curve in Fig. 14 is minimized).  Could the same analysis be completed on the optimal time step (i.e. show it in Fig. 15) or could an explanation be provided why the final time step is better?
• Line 345 presents a hypothesis which has thus far not been demonstrated as fact. Please present it as a hypothesis or with the caveat that this will be demonstrated in the following section.
• At the start of section 5.2, please specify (in addition to the parameters) which experiment number (from prior section) is selected as optimal.
• Line 353 says a range of multipliers from 0.75 to 3 are used, but Table 7 shows multipliers ranging from 0.75 to 7. Please reconcile.
• Does figure 17 need to be its own figure? It’s just adding one curve to figure 14.
• Table 8 includes the exact same information as Tables 5 & 6, plus a new row. Please consider if tables 5 & 6 need to be included as stand-alone tables.
• In figure 18, the difference between restored geometry and reference target (image) is difficult to discern. As discussed previously, please add restoration steps with more deformation or address why only the first restoration step (in which deviation is presumably smallest) is chosen for comparison.

Section 6: discussion

• Table 8, row 3, column 1: the use of “Kinematic restoration” confuses kinematic restoration methods with kinematic boundary conditions in a mechanical (stokes flow) restoration. Please clarify.
• Line 377: I believe this references silicone viscosity, not actually salt.
• Please clarify the caption for Table 8 as requested in annotated manuscript.
• Line 379: please specify what you mean by times scales ranging from seconds to hours. The experiment was 4 hours long.
• The paragraph beginning line 384 overlooks the fact that the last case (optimized material properties) produced the best restoration results. This is key to conclusions and should be highlighted here.
• Paragraph beginning line 390 seems a bit of an aside to the point of the manuscript. It’s relevant, but maybe could be moved later in the discussion.
• Line 401: The sentence beginning “It poses…” touches on questions around the magnitude of traction applied to the right boundary. I would like to see this addressed more thoroughly (in relation to comment on section 4.2)
• The numerical improvement from the first case to the last is relatively small (see total of first two rows in Table 8). I would like to see more discussion of if it’s worth the (large) additional effort of to optimize the model. 

Throughout the manuscript, wording is frequently awkward and/or imprecise.  I have tried to identify and assist with the more significant examples in the attached, annotated version of the manuscript.

Review of the manuscript entitled “Application of the creeping flow restoration method to an analogue model” by Schuh-Senlis et al. submitted to EGU Solid Earth

Schuh-Senlis et al. present a meticulous study aimed at determining the optimal method for restoring an analogue experiment that represents a geological event. This is achieved through the application of an inversion scheme utilising Stokes' equations, with velocities inverted to facilitate backward stepping in time (restoration).

The study draws attention to the impact of velocity and pressure boundary conditions on the success rate of inverting a numerical model. The numerical model, derived from the initial conditions of a late stage analogue experiment, demonstrates that while pressure boundary conditions, despite their greater realism, do not yield significantly superior results, they underscore the importance of material properties, such as viscosities along individual faults.

As a reader, the expectation was to find a robust solution to the problem. Towards the end, however, there is a sense of frustration at the need to delve into material properties individually through a parameterisation study. Nonetheless, this meticulous approach is considered positive, as it necessitates a detailed exploration to establish a constitutive relationship capable of inverting a broad spectrum of geological events. Yet, achieving such a relationship appears incomplete, demanding further studies that may involve more sophisticated tools, such as machine learning. Conversely, the authors could opt for a simpler model, if the analogue part exists, involving one or two faults with varying properties. Then, the authors would increase the complexity of the problem in subsequent chapters.

Before proceeding with publication, I advise considering the following points:

1. In your inversion model, it is noted that the heat transport equation is not solved. Could you elaborate on the potential impact of this factor on your results?

2. On line 35, clarification is sought regarding why the aforementioned methods are particularly limited in capturing the dynamics of salt basins. Is it related to layering or other characteristics of salt basins?

3. Have you assessed whether the resolution of your model may significantly impact the results?

4. Would you consider exploring periodic boundary conditions on the side walls? It is presumed that faults may restore as the model equilibrates.