GENERAL COMMENTS - overall quality of the preprint

This paper re-addresses the long standing and still interesting question of the role of phyllosilicates in controlling pressure solution and multiscale transport in rock materials. It does so by means of micro-CT imaging of uniaxially compaction tests performed on brine-saturated NaCl aggregates containing biotite rich layers - in two different configurations and using one pure NaCl control sample.  The results obtained for this rock analogue system demonstrate that the biotite-rich layers compact at a similar average  (?) rate to the adjacent pure salt layers but that the porosity of the biotite-bearing layers decreases faster due to preferential precipitation of NaCl in the biotite layers.  This is a nice, observational  demonstration of transport on the length scale of the layer thickness as opposed to the grain scale, as put forward in previous work, such as that by Merino et al. (1983).  The experimental approach is largely sound (some questions can be raised) and the results are mostly clearly and pleasingly presented. However, the discussion appears to contain several inconsistencies and non-sequiturs in reasoning, as well as some conflicts with previous literature and established understanding.  These may be the result of mixed terminology and/or unfortunate expression or use of English, but the effect is confusing for the reader, undermining the strength and value of the conclusions drawn.  In particular, given that there were no major differences in compaction strain in the different layers, it is not clear WHY there was diffusive transport from the NaCl layers to NaCl/biotite layers beyond a phenomenological similarity to the effect put forward by Merino et al.  The proposed driving force for transport requires at least initially preferred compaction (grain contact area increase) throughout the biotite-bearing layers, which is not very clearly demonstrated or perhaps lost in the discussion of the uniform compaction observed in the samples. I am also left wondering what the imaging results add to the earlier work of Macente et al (2018) on the same system, beyond technical and methodological refinements. Nonetheless, the paper contains good observational work which deserves to be published if the improvements vs. Macente et al (2018) can be clarified, if aspects of the compaction experiments can be clarified,  and if the discussion can be sharpened and the Merino hypothesis tested a bit more rigorously.  On this basis, I am recommending major revisions, which ideally should contain some additional experiments.   My specific comments are listed below.

SCIENTIFIC COMMENTS

Scientific points that require attention are as follows:

1) Title : I find the title misleading as it suggests that the observed effect is caused specifically by biotite.  However, the authors seem to argue that it is not specifically the biotite that causes the observed effect but initially (?) reduced porosity in the biotite-bearing layers.  If they are right, then a biotite-free but denser salt layer in the sample would show the same layer-scale mass transport phenomenon reported here and described by Merino et al.  I would recommend a title more along the lines of “CT imaging demonstrates interlayer mass transport in layered halite-biotite aggregates undergoing dissolution-precipitation creep”.

2) Abstract, lines 5-6 read: “We used time-resolved (4D) microtomographicdata to capture the dynamic evolution of the transport properties in layered NaCl-NaCl/biotite samples”.  This is not true.  No attempt was made to calculate transport properties (or measure them).  Only porosity evolution was studied.  Best correct to porosity rather than “transport properties” – throughout the ms.

3) Abstract, lines 12-14 reads: “We propose that, in our experiments, the diffusive transport processes invoked in classical theoretical models of DPC are superseded by chemo-mechanical feedbacks that arise on longer length scales.”  This cannot be said if in the main text it is claimed that the sample scale compaction behaviour is consistent with compaction experiments on pure NaCl.  The effect of interlayer transport in the present experiments is argued not to influence overall compaction strain, so it does not dominate over pressure solution as a deformation mechanism, it merely contributes and dominates porosity reduction in the bi0tite-bearing layers.

4) Introduction, lines 29-30 read: “Phyllosilicates have been recognised to have a reinforcing effect on the dissolution process ..”.  Yes, a but others have notes that pressure solution (compaction) can be inhibited or unaffected by phyllosilicates, e.g. Niemeijer & Spiers (2002). The enhancement effect comes mainly from observations on natural rocks where advective mass removal along phyllo-rich layers cannot be eliminated as playing a role.

5) Intro, lines 30-35: What does the present study actually add to the paper by Macente et al (2018)?  Would be wise to make this clear somewhere, e.g. in lines 46-48.  Just seems like a technical refinement at present.

6) Intro lines 48-49 read: “Our aim was to determine length scales of diffusive transport in a dynamically evolving porosity during DPC”. What about trying to explain them?? 

7) Section 2, line 53. Peach and Spiers 1996 is a study of the percolation threshold in dilating salt, not a study of deformation mechanisms.  A far more relevant reference here and in line 57, would be the study of pressure solution in compaction by Spiers et al 1990, which specifically addresses the creep law for pressure solution in NaCl in 1D compaction and deviatoric creep – and emphasizes the analogue aspect.

8) Section 2, lines 58-59 read: “It is further a material used in geological nuclear waste repositories (Powers et al.,1978), and its deformation behaviour is well-characterised”.  Salt is not a material used in radioactive waste reporitories – it has been and still is widely considered as a HOST ROCK for repositories.  A more recent ref than Powers should be added and refs should be added to underpin “well characterised”. Urai , Schleder, Spiers and Kukla 2008 would be suitable here.

9) Section 2.3 Experimental setup, lines 95-96 reads: “The experiments were run inside a thermally insulated box where the temperature was logged and found to be stable within ± 1.7 °C over the course of the experiments.” This is quite a large range in T for such a soluble material as NaCl (which would certainly cause sample-wide dissolution-precipitation effects) and raises questions regarding temperature GRADIENTS in the sample and their possible effect on convection and advective transport.  Was temperature measured at different points along the length of the sample and if so what was the T profile or gradient? Could this have driven advective transport in the samples? Some calculation is needed to answer this.  Of further interest here is the possible effect of differential heating of the sample during CT-imaging, as a result of x-ray attenuation – e.g. differential heating of biotite-bearing versus pure NaCl layers.  Can effects such as this be eliminated? 

10) A further point related to the above is the issue of radiation damage and its effect on NaCl solubility. Recent measurements that I have witnessed in a similar scanner show heating of NaCl by a few degrees accompanied by significant radiation damage of the salt – it turns yellow or purple at high doses.  So my question to the present authors is: did the samples change colour after CT scanning?  Did they check?  And, if the colour did change, can they eliminate the possibility of damage gradients influencing dissol-precip transfer between layers of different composition hence different damage in the NaCl?  Note that from a theoretical point of view, if the deposited energy due to radiation damage of NaCl is E, the increase in solubility for small E is 100.E/RT %. Could this effect, or the heating due to attenuation,  be significant?

11) Also under Section 2.3, it is mentioned in line 98 that the applied effective stress on the compaction experiments was 6.64 to 10.5 MPa.  That means that local stresses at NaCl and NaCl-biotite grain contacts would have been much higher – in the range 12 to 50 MPa.  These stresses are well inside the regime where salt deforms plastically at room T, leading to a coupling between work-hardening plasticity on the grain scale and dissolution-precipitation transfer, as opposed to classical pressure solution seen in compacting NaCl at stresses below 3 -4 MPa (see Urai et al 2008 above; also Spiers & Brzesowsky. Densification behaviour of wet granular salt: Theory versus experiment. Seventh Symposium on salt 1, 83-92, 1993).   The likleyhood that this plasticity-coupled mechanism played a role in the present experiments, rather than classical pressure solution, should be pointed out, especially as it is a mechanism where pore volume diffusion plays a role as opposed to the grain boundary diffusion process that controls  “normal” pressure solution.

12) Section 3 Results, Figure 3.  The apparently straight portion of the compaction curves shown in this plot is referred to by the authors as steady state creep, whereas the inset in the Fig clearly shows that the strain rate is continuously decreasing within the resolution of the data.  Moreover, the authors actually say that the compaction curves show asymptotic behaviour (e.g. line 271), which in itself means that steady state is not achieved.  In addition, it is quite impossible to reach a steady state compaction rate in a compaction experiment of any kind, as porosity is continuously decreasing and therefore so must the strain rate – regardless of deformation mechanism.  In this study, apparent steady state seen in the compaction curves is an artifact of the few, rather scattered strain-time data (clearly understood from the inset in Fig 3).  Perhaps use of the term “apparent steady state” would be acceptable, but the term steady state creep should be removed throughout and all related points corrected accordingly.

13) Figure 7. Lines 223-224: “Figure 7 shows the vertical displacement rate of the biotite-bearing layer and the bulk sample for different increments of progressing deformation”.  And in Lines 225-226 “At the beginning of the experiment the rate of both bulk samples was elevated compared to the biotite-bearing layers.” OK for the displacement rates, but any meaningful comparison requires normalization with respect to the thickness of the NaCl and NaCl-biotite layers considered , i.e the average strain rates in each zone should be plotted versus compaction stage (time proxy).  This is crucial because of later discussion around the issue of enhanced compaction (lower contact stresses) causing interlayer mass transfer.

14) Section 3.2 Strain analysis.  The usage of the terms volumetric strain (isotropic) , deviatoric strain and compaction strain becomes a bit confused from here on, I feel.  In 1-D, compaction strain is equal to volumetric strain, but not equal to the isotropic strain component of the strain tensor of course. However, the isotropic vol strain does seem to be referred to as compaction at some points in the ms. Somewhere early in the ms, these terms need to be strictly defined and differentiated from each other, and then used consistently.  It is also important to note that deviatoric strain cannot occur during 1D compaction independently of the isotropic component of volume reduction, because the pressure solution process (even when accompanied by plasticity) is serially coupled to intergranular sliding – you cannot have one without the other (in pure NaCl or in NaCl-biotite mixtures).  In isotropic compaction under 3D loading with S1=S2=S3 you can get compaction with little or no intergranular sliding.

15) The above point comes into play in Figs 8-11, where isotropic volumetric strain (called volumetric strain) is used as an indicator of compaction, whereas macroscopically measured compaction is 1-D compaction.  I would strongly advise the authors to present a complete picture in Figs 8-11 by adding contour plots of vertical compaction strain, in addition to the isotropic vol and deviatoric strains.  This would make what is going on clearer with a complete set of all information.

16) Section 3.4 NaCl redistribution, Fig 13 and text referring to it (e.g. lines 254-255). Here, changes in NaCl content within the samples are specified per horizontal slice through the sample. That should be made clearer in the text as it reads as though the mass of the samples is not constant.  That also raises the question as to whether the mass of NaCl in the samples is indeed constant.  Do the changes in NaCl mass/vol fraction seen in individual samples add up to the original NaCl solid mass?  This needs to be clarified.

17) Section 4 Discussion, lines 269-270 read: “The general compaction behaviour we observed  was consistent with previous studies on NaCl compaction”. Well, yes, the data do show increasing compaction with time.  But that is no basis to claim consistency with previous work.  First, no other compaction data on salt show the apparent steady state portion claimed by the authors, so they are not qualitatively consistent. Second, a comparison with the isostatic compaction tests of Schutjens & Spiers is not expected to be consistent because of the different boundary conditions imposed. Third, no evidence is presented that the present amounts and rates of compaction are consistent with previous 1D compaction tests on samples of controlled grain size, such as those reported by Spiers et al (1990 – low applied stresses) or Brzesowsky and Spiers (1993 – stresses similar to the present).  To claim any consistency or detect any interesting differences, a quantitative comparison should be made by adding a few curves from previous 1D compaction studies on salt of the same grain size – or calculating compaction curves for the present conditions from the compaction data or laws given by previous authors.

18) Lines 272-276. The authors claim a change in deformation mode beyond 200 hours here.  But they also argue that their data are continuous and show a continuous asymptotic decrease in strain rate.  The continuous nature of their strain rate data is also apparent from Fig 3 (see point 12 above).  It does not seem justified then to claim a change in deformation mode here, so the point should be removed or weakened.

19) Lines 305-306 read: “the upper NaCl layer did develop a pronounced gradient towards the interface with the biotite-bearing layer though, which could be evidence for a diffusive salt redistribution”. Yes agreed.  But it could also be evidence of advective redistribution if there were even small internal T-gradients.  Can this possibility be eliminated?  If not that should be stated.

20) Lines 309-319:  Here it is proposed, quite reasonably, that Merino’s model of diffusion from more porous to denser layers may occur because of a higher solute concentration (supersaturation) in the more porous material than the denser material.  This is consistent with pressure solution theory and fine.  However, appealing to the high supersaturations discussed by Desarnaud et al (2014) or Zimmerman et al (2015) is misplaced here as these are concerned with pre-nucleation supersaturations.  There is no evidence for a nucleation stage in the present experiments as it is quite clear from the grain scale images, and from previous compaction work on NaCl, that precipitation occurs mainly by OVERGROWTH on the pre-existing grain (pore) walls.   If fine grains are nucleated in the pores in the present experiments, that would be new and should be described. Only then should the above nucleation argument can be kept. 

21) Lines 320-322. Here the authors argue that the Merino model may apply because the biotite-bearing layers compacted more than the pure NaCl layers in the early stages of the experiments, so had lower porosity, lower contact stresses and hence a lower supersaturation on NaCl in the pores – giving a driving force for diffusion of dissolved NaCl from the pure to the mixed layers.  For the reader, however, this seems to be a strange statement after so much emphasis has been placed on the lack of evidence for any strain enhancement in the biotite-bearing layers (at many points, but also again in lines 336-337).  The argument seems inconsistent.  Can the authors please clarify this picture – it is most confusing in the present form???? Was strain only uniform in the late stages but not initially? If so, please make this clearer.

22) In relation to the above point, I also wonder if the authors should mention the possibility that the preferential “cementation” of the biotite rich layers that they see could reflect an INSTABILITY caused by the Merino effect progressively reducing grain contact stresses and supersaturation  in the biotite layers faster than in the NaCl layers.

23) Line 331. The authors suggest here that electrochemical effects at the NaCl-biotite interface may enhance dissolution at those sites, following the references cited. However, as far as I recall those refs deal with the effects of micas at mica-quartz interfaces.  I do not think one can then assume that the same enhancement effects will occur at a mica-salt (ionic solid) interface.  Line 331 should read “…..which MAY accelerate dissolution of NaCl.”.

24) Lines 336-334: This explanation of what goes on inside a biotite-bearing layer is reasonable. However, is it not a remarkable coincidence that “the additional NaCl contributes to a load-bearing framework whose compaction rate is in sync with the bulk sample’s”???  Would it not be better (i.e. more accurate) to replace “is in sync with” by “roughly matches” ??  Otherwise there would have to be some strong coupling which is hard to argue.

25) Lines 374-386.  The issue of volumetric strain versus compaction strain versus isotropic strain raises its confusing head here again, further underpinning the need for better definition of these terms at an early stage in the paper, followed by consistent use in a way that distinguishes between physical compaction and the math properties of the isotropic part of the strain tensor – see point 14 above.  MORE INTERESTING though is the issue of what was observed in the glass bead layers in the biotite-bearing samples.  Presumably there was no actual compaction of these layers, beyond some rearrangement effects or possible bead breakage or chipping.  This should be clarified in the Results.  There, it should also be made clear whether there was any precipitation of salt in the bead layers.  If there was at both sample ends, this would support the Merino model, as there would be no stress-induced supersaturation in the brine in the pores between beads. If there was precipitation between beads at one end of the sample but not the other, this would suggest a role of convection and advective transport, or double diffusive convection.  If there was no precipitation at all between the beads, this could be explained by the nucleation barrier at these sites – thus supporting neither the Merino model nor an advective transport model.

26) The issue of the glass beads does raise the question of why the authors did not do an additional  control compaction experiment with a layer of denser NaCl instead of a layer containing biotite?  This would more rigorously test whether the Merino model may apply, i.e. whether diffusive transport is caused by porosity hence supersaturation differences,  as opposed to some special effect of biotite.  This would be a worthwhile addition to the paper, if time and money allow - as would an experiment substituting calcium fluoride cleavage flakes for biotite flakes.  That would be useful because the diffusive properties of NaCl-CaF2 interfaces have been directly measured during active pressure solution of the NaCl by De Meer et al (2002 EPSL 200).

TECHNICAL ISSUES (language, typographics etc)

Overall the paper is well written and in good English.  Nonetheless a few small improvements can be made as follows:

1. i) an asterisk * is not a mathematical symbol. Proper multiplication and scalar, vector or tensor product symbols should be used.
2. ii) Figures 8-11 would benefit from an explicit indication of which sample is being displayed.

P.S. The references cited above but not listed in the ms can be easily found in an online search from the information I have given.  I checked this. 

The paper by Schwichtenberg et al describes a set of 3 long-term compaction experiments on pure NaCl, a layered sample of pure NaCl and a mixed NaCl/biotite layer, and a layered sample of pure NaCl, mixed NaCl/biotite and pure NaCl. It addresses the question of the role of biotite in pressure solution creep, which is a process relevant to the understanding of deformation processes in the Earth crust. It is not exactly clear how this paper differs in approach and conclusions from earlier work done by Macente et al in 2017 and 2018. The paper concludes that with the type of biotite used, the earlier indicated reinforcing effect of phyllosilicates on pressure solution creep has not been found. The methods and assumptions are valid, and results are probably sufficient to support interpretations and conclusions, provided the two major comments are fixed. Otherwise, the organization of the paper and details of the manuscript are mostly of appropriately high quality, though some edits (see specific and technical comments) are needed to fix what is currently not clear.

Apart from the apparent similarity to Macente et al 2017 and 2018, I have two major comments concerning the potential validity of this study.

Major comment 1 is related to the technical capacity of the DVC. How well can automatic processing, such as DVC cope, with material literally moving, or jumping, from one place to another? it is written for small amounts of lateral deformation and shape change of particles, so if material moves from one place to another, which the 2D analyses indicate, is DVC then capable of picking it up? The main part of the argument in paragraph 4.3.3 seems to be based on the fact that the code ran and indicated no massive problems, and therefore the answers are correct. This is not necessarily the case. A smaller part of the argument is that the interiors of the grains don’t change. But what if new grains are created with a similar shape and size? And what if grains are completely dissolved? In the latter case, a correlation can be made with the neighboring NaCl grain, which looks otherwise quite similar, due to similar initial grain size.

The second major comment is related to the starting porosity, a critical element for compaction experiments, and a notoriously difficult one to control. The initial compaction was 9 to 18%, but the starting porosity of the samples is quite different (Figure 12). In the mixed samples this porosity is not homogenously distributed. Since pressure solution is heavily affected by porosity, how does this affect the rates and results you indicate? and on this note, the term steady state compaction is misleading, since the compaction rate should continuously decrease (see references in the manuscript). It is also not entirely clear how porosity is determined: is this like Macente et al from a 400^3 voxel subvolume in the CT scan? If so, include in the method section. Is the determination of the 2D porosity and 2D presence of NaCl per slice, but for the full sample, and for the 3D volumetrics on subvolumes only?

Specific comments:

Line 15: this is the only place where the length scale is actually quantified, whereas it would make sense to include it in the discussion paragraph 4.1.

Line 73: please add a clarification on the different aspect ratio of the biotite flakes. Which dimension is 200-500 microns?

Line 76: dry NaCl?

Line 80: simple insertion of the piston, or already with a specific applied force?

Line 86-91: out of curiosity, why is there a difference between SBS and SB samples in the design of the pumping system? Is there a different brine used? Or is it just one of those things that happens when experiments progress?

Line 92: what was the fluid pressure? Was this the same for all three experiments?

Line 98: why is there a difference between the constant effective load for SBS (6.64 MPa) for SB + S1 (10.5 MPa)? What is the load during the experiments? Please add here.

Line 142: is for this type of microtomograph the gray scale belonging to 100% NaCl density always the same, regardless of scanning conditions? Because in some CT scanners the grey signal “floats”, and in some scanners it is fixed. How is that for this scanner?

Line 155-157: I do not understand the size of the 3^rd dimension for the 3D NaCl subvolume.

Line 176: How do SPAM and TomoWarp deal with grains which change shape themselves? They do not only rotate and rearrange, but can also change shape due to dissolution and precipitation (major comment 1).

Line 186-187: all samples were under a constant and similar effective vertical load during this compaction time? This doesn’t become clear from the preceding sections. What is the starting porosity of the sample? Is it homogeneous throughout the sample? Does each sample have the same starting porosity? (major comment 2)

Figure 3 and line 198-206: why the smooth connection between datapoints in Figure 3a? What is the highest resolution in vertical strain rate you can obtain with your measurement method? The fact that a plateau is reached can also mean you have reached the measurement capacity of the setup. In principle, in a pressure solution type of process, based on theory (citations in the manuscript), one would expect a continuously decrease in strain rate with porosity. In other words, it is a steady state in the length of the experiment, but if you could measure indefinitely, the rate would continue to decrease. So is it really a 2 stage process, or is it actually a visual artefact caused by measurement resolution and experiment duration?

Line 225/Figure 7: as Figure 3 and line 198-206: is it caused by steady state or measurement resolution?

Figure 7: this is z-displacement rate. In the NaCl-biotite-NaCl sample both NaCl layers have a different thickness than the mixed layer, where in the NaCl-biotite sample they are of similar thickness. If you would plot strain rate instead of z-displacement rate, would the trend then change?

Figure 8-9-10: why did you not do the DVC for all time steps? How certain are you that the time steps shown are representative?

Line 229-245: please be more precise in your description, and in labeling if you are looking at compactive or dilative strain maximum in this paragraph. In Figure 8 (SBS), I see deviatoric strain maxima in the center of the sample, correlating with positive volumetric strain (dilatation), and overall more activity in the bottom half of the sample. In Figure 9 (SB) I see similar high deviatoric strain in the center, but more activity in the top half of the sample. There is barely any dilatation. In Figure 10 (S1), there are high deviatoric strains in the center, and both dilation and compaction, with more activity in the bottom half of the sample. Moreover, what would be the minimum strain needed to be measurable? The samples overall do look blue, but how blue does it need to be to be sufficiently away from zero?

Table 2: in all three figures, there are three plots for the DVC, but only two data entries for each sample in this table.

Line 236: I would consider the use of the word “trend” with only two data-points per sample too strong.

Line 243: “deviatoric strain maxima corresponded to the location of biotite grains as well as open pore space and pure NaCl clusters” – in other words, there is no correlation between the location of the deviaotric strain maxima?

Line 247: the correlation is not absolute: the maximum loss of porosity in the SB sample (1932 hr) is from slice 500-925 or so, and the biotite layer ends at slice 1000. For the SBS sample, the maximum loss (1932 hr) is from slice 800 to slice 1550, and the biotite layer is from slice 750 to 1350. How does the location of the maxima compare to the data from the DVC?

Figure 12: the starting porosity is quite different for the samples. How would this affect the average compaction curves of Figure 3?

Line 254-259: how did you determine the NaCl distribution? 100% minus porosity minus biotite? Or did you also segment the NaCl grains individually? What is part of the NaCl remains in solution as supersaturation, as indicated in the discussion as a potential part of the process?

Line 260-264: Unclear phrasing: if the assumption is made that biotite is an insoluble internal standard (line 261), it makes sense that the analyses show the biotite content to be standard… And can you show somewhere in a Figure where the subvolume is taken (this would also solve line 155-157)?

Line 273-275: it is not clear to me why this is interpreted a change in deformation mode, instead of it being a continuous log-linear decrease in rate (same comment as in the description of the results).

Line 278: This needs more careful phrasing, since even the current description of results indicates that strain maxima occurred mainly within the biotite part of the sample (line 233).

Line 294: unless one takes it that the patterns of Fig 8, 9 and 10 do show there is more strain localization in the biotite… Or that the DVC actually doesn’t cope very well with the material transport (major comment 1).

Line 329: This wasn’t clear to me in the results on the DVC, though the concentration of deformation was mentioned in Figure 12 and 13. Perhaps it would help to add arrows or boundaries to Figs 8-9?

Line 333: I do not understand how figure 5 demonstrates the efficiency of this process

Line 334: ah, that’s what the Lambert plots did (technical comment line 180)! But if there is no significant rotation, then why is the deviatoric strain so high in the biotite layers? Another reason could be that many of them are already fairly horizontal, so that might also be why there is no strong realignment.

Line 345: can you add here that Macente reported a first order effect (i.e. why would you expect a first order effect), and which observations showed there is no first order effect?

Line 367: why/how does Figure 11 show that local maxima correspond to sites of precipitation?

Technical comments

Line 62: “which are described in Macente (2017)”: Since the description is actually below, this phrasing is slightly misleading

Line 105: for clarity, it would be nice to add if the samples were compacting in the same building (I assume so), or if they were transported by car throughout Edinburgh or the UK or even from France (looking at the affiliations of the authors). Given the composition of the author team I imagine the transport between CT scans and compaction location was done carefully, but the explicit mention of the location of the tomography instrument somehow gives the impression that the scans were done somewhere far, far away… Which would have consequences for their validity.

Line 106-107: how many scans and compaction time for the S1 sample?

Section 2.5: this section would be easier to read if there was a flow diagram that briefly labels all the steps and different softwares

Line 136: please mention your figures in order of appearance. Fig 12 now follows Fig 2. Fig. 12 doesn’t contain the error, though that is suggested by this part of the text. Idem for Fig 13 and Fig 14

Line 159: given the name (digital *volume* correlation) I assume this approach is only valid for the 3D volumes, correct? Please add.

Line 160: can you indicate in 1-2 lines which operations or calculations are performed by SPAM and which by TomoWarp2?

Line 180: this is my own ignorance: how does one read a Lambert projection? As the reader, what would it tell me? Can you add a reference here so the non-knowledgeable reader can read up on the importance of these plots?

Figures 4 and 5: why did you choose this specific vertical slice? Where is it located in the 3D sample? Would we see the same if you choose any other slice?

Figure 5: can you add the red markers to all 5 panels? It would help guide the eye. The lower biotie grain seems to also change curvature between the panels, or is that simply due to the unfocused visualization?

Figure 5: Why do you not have panels also to show if similar things happen in the SB and SI samples?

Figure 6: to my non-Lambert-trained eye, figures a and b look very similar… Why could you measure so much more grains for a versus b? Is that because there were more grains in b to keep the layers of equal thickness?

Line 229-234: For readability, please treat the descriptions in the same order as the figures are shown for clarity, and in Figure 8 9 and 10 please add the sample name in the caption or in the figure. This could be improved throughout the paper: sometimes the pure salt sample is described first, and sometimes the salt-biotite-salt sample.

Figure 8 9 10: compaction in rock mechanics experiments is often denoted positive, whereas here the negative values are compaction (line 234/second-last line of caption).  

Figure 9: typo: “cumulative”

Paragraph 4.1: the title of the paragraph, combined with the question of the introduction, gives the reader the impression the length scale will be quantified, whereas this is actually a more qualitative interpretation.

Line 374 – 388: OK, but how can you then be sure for the rest of your sample that the values are correct? You probably can I’m sure, but I don’t see it straight away. What am I missing?

Given the length of appendix A2 and how crucial the terms are, I suggest to move this definition to the method section.