This manuscript presents mechanical results for fine-grained, polymineralic (and wet, 0.2 wt H2O) granitic ultramylonite samples that are deformed at high pressure (1.2 GPa), temperatures of 650 to 725C, and a wide range of strain rates (expressed as equivalent strain rates) in a mixture of shear and pure shear (or shortening) experiments.  Three types of experiments have been done, including: I) highly localized slip/shear experiments where displacements at the experimental conditions occur on initial fractures (Type I), II) more nearly pure shear experiments, in which foliation is inclined to the compression direction but samples are shortened axially (Type II), showing non-coaxial strain only due to the anisotropy of the ultramylonite samples, and III) general shear experiments, in which samples are sheared (almost by simple shear – often characterized as general shear because of the mixed character of strain) between “alumina forcing blocks” (Type III).  These experiments capture a pronounced reduction in strength for conditions when grain size-sensitive deformation mechanisms are favored by fine grain size and the polymineralic nature of the samples.

The arguments for dissolution-reprecipitation mechanisms for this grain size-sensitive creep behavior are convincing, particularly since the samples are very fine-grained and deformation occurs with significant fluids present.  However, I question the quantitative nature of stresses reported for these experiments;  I do not think the experimental methods are characterized sufficiently or stresses determined well enough to report flow law parameters such as stress exponents (n) or grain size exponents (m).  My first concern is that the present manuscript does not describe methods well enough for the reader to understand such figures as Fig 2 and 4, particularly when the experiments involve single-condition vs multiple-condition stepping experiments.  The description of how equivalent strains are determined and used to compare results in general shear and pure shear is well done.  Measurements of grain size are also well done.  However, the underpinning of differential stress measurements is not described sufficiently; that is, how “hit points” (or forces at initiation of deformation) are determined, for single- vs multiple-condition steps, and why stress corrections for the solid salt sample assembly are made in such strange ways.  None of these experiments were done using a molten salt assembly, so why use a calibration for molten salt assemblies? Unfortunately, this leads me to the conclusion that one cannot trust the stress determinations as quantitative measurements, and yet these are necessary to obtain accurate values of n in Figure 6 (this also goes for shear stresses determined from differential stresses).  m values may be more reliable assuming that the stresses are constant, but this is unclear if force measurements are not made correctly.  In addition, precise measurement of m values is intrinsically difficult, as discussed later in the manuscript.

There are interesting and important results here, but the authors owe it to themselves to make the case for their conclusions, based either on 1) accurate microstructural observations, 2) accurate mechanical measurements, or 3) robust, if qualitative, mechanical results.  The first of these approaches is probably the most trustworthy approaches, given that microstructural observations can lead to interpretations of deformation processes without accurate measurements of mechanical properties.  This worked in the early days of high-pressure, solid-medium deformation experiments using talc assemblies., and one remedy to revise this manuscript it to focus on this line of evidence.  At present, though, microstructural observations serve a secondary role to the mechanical results.  Alternatively, I would argue that the third approach is also viable. But, the second approach, which is emphasized in the present manuscript is problematic.  This is frustrating, since I basically believe that the conclusions regarding grain size-sensitive deformation are probably correct.  But there are flaws in the corrections for stress determinations using external measurements of force for solid-medium sample assemblies that are confusing and misleading.

If the conclusion that dissolution-precipitation creep of these polymineralic ultramylonites is to be supported by mechanical data, then it would be better to present the pronounced weakening (which doesn’t require quantitative measurement, but rather the substantial reductions in raw force/uncorrected differential or shear stresses that are obvious) rather than the attempt to compare apparent values of stress exponents (n) and grain size exponents (m) based on accurate strain rate determinations and uncertain stresses.  This third approach (indicated above) could use the current mechanical results as qualitative measures of change in mechanism. Afterall, comparing a strong vs a weak sample (applying the same “correction” for the experimental method) can still be done to come to a conclusion that strength is different. But numerical values reported for n and m require quantitative measurements of stress, strain rate, and grain size.

Most quantitative mechanical datasets for diffusion creep, grain boundary sliding or Coble-creep-like dissolution-precipitation creep at pressure come from gas apparatus, capable of measuring very small differential stresses accurately.  It is difficult to measure grain size-sensitive creep stresses (and thus flow laws for diffusion creep or dissolution/precipitation creep) by high-pressure solid-medium techniques (Griggs rig with solid confining media) because the differential stresses are generally so small that stress resolution and accuracy are not sufficient.  This difficulty makes stress corrections very important, and the attempts at correcting differential stress in this manuscript are questionable. 

A final alternative that would help remedy this manuscript’s revision might be to apply corrections for stress, which I now feel I have argued about for more than a decade.  Or to do the backup technical work to develop a better stress correction. I’m sure that my digression on calibration of the Griggs solid medium apparatus will not be welcomed by everyone, but the H-K calibration for the solid-salt sample assembly, is based simply on a comparison of Griggs solid medium results and Argon gas apparatus results for the very same metals. This is a time-honored means of calibrating solid-medium results in high-pressure petrology (piston-cylinder) and mineral physics (multi-anvil or other apparatus).  Most researchers view high temperature gas apparatus as a gold standard in achieving truly isostatic stress conditions prior to deformation, and then determining differential stresses by simply measuring departures from the initial isostatic stress state. External force measurements require only a simple (constant) packing pressure correction and internal force measurements do not require correction.

If the authors feel that quantitative measurements of stress and determinations of n and m are required to support the manuscript’s conclusions, then differential stresses simply must be corrected.  If the H-K calibration for the solid salt assembly is not trusted, then a new calibration is required to convince readers of the quantitative nature of the mechanical results.  Some of the text suggests to me that the H-K calibration has not been applied as intended;  I will address hit point determinations, and initial transients and strains where the calibration applies a little later in this review.  As for the claim that the H-K correction overcorrects (reduces differential stresses too much), why not improve on prior calibrations?  Experimentalists in some fields might view a repeat (or improvement) of important calibrations to be a once-every-decade necessity to obtain quantitative results.  The metals deformed in a Heard apparatus in the H-K calibration paper were reported digitally, so repeat or improved experiments in any solid-medium apparatus capable of triaxial compression can be executed.

This manuscript could readily be improved by a more detailed description of methods and revision of corrections (Sections 2.2 and 2.4).  Section 2.2 should describe procedures used in “single-condition” experiments and “multiple-condition” (or stepping) experiments.  Figure 2 and 4 show that some experiments were done at one condition, which simplifies description of methods, but others appear to have had steps in conditions, and even include what look like “stress-relaxation” intervals (the shear stresses appear to decrease with time and strain).  The nature of the experiments and methods must be described in Section 2.2.  In addition, it does not appear that new “hit point” determinations were made after a time of different conditions or load relaxation.  This is a problem since solid medium assemblies show transient viscous effects (as the solids have their own nonlinear viscous responses to changes in stress, strain rate, temperature, and other conditions).  Force-displacement measurements in a triaxial gas apparatus only involve simple corrections for linear elastic response, and thus, force-displacement data can be used to study nonlinear responses of the sample during changes in displacement rate or load relaxation.  However, this is not so simple if the sample assembly changes and the externally measured force changes for multiple reasons.

In Section 2.4, the means of determining equivalent strains and the conversion of differential stress to shear stress (the cos2 correction) are well described.  However, I have a problem with the corrections applied to force records, if differential or shear stress determinations are to be made without correction or incomplete correction.  The so-called “friction” correction, I believe, is the one that was developed at Brown University, based on force measurements while shortening salt samples within salt sample assemblies (a citation to this correction is appropriate).  In those calibration experiments, an increase in force was observed with the advancement of the load piston.  It may be a minor point, but I prefer to think of this as a “frictional slope” correction.  What is sometimes called “friction” or “packing friction” is already subtracted for external force measurements, with the usual hit point force determination, so the “friction” (or really a mix of frictional resistance at the packing and at load/confining piston surfaces, and viscous resistance to deformation of the sample assembly) has already been subtracted from the rest of the force record by a constant force (determined when the piston-sample load column is all in contact).  The “frictional slope” then corrects for the increased sample assembly resistance to piston advancement, and this is apparent in the increasing correction with shear strain in Fig. 2.  This correction is generally valid for simple single-condition experiments, but I am not certain that the monotonic increase of “friction” with piston displacement (increasing stress correction with shear strain, Figure 2) depends on piston displacement alone, or whether it might show viscous relaxations during periods of low strain rate such as during load relaxation steps (again, I am inferring that No 673NN of Fig 2 has two times of stress relaxation). 

The bigger problem, though, is the use of the H-K molten salt correction applied to experiments using solid salt assemblies.  This doesn’t look correct on the face of it.  The statement that the solid salt correction was not applied because it involves a further offset of 48 MPa, which is a constant subtracted from the entire (stress-strain) record, doesn’t make the solid salt assembly behave as a molten salt assembly.  This offset is most likely due to the non-zero viscous strength of the solids used in the solid salt assembly, and the lack of this offset for molten salt assemblies implies that the solid contributing to the 48 MPa offset is the inner salt cylinder of the assembly, rather than lead, pyrophyllite or other solid components.  The fact that stresses determined in Griggs apparatus/solid-salt assembly methods are greater than stresses measured for the same samples at the same conditions in gas apparatus was already reported in Kirby and Kronenberg (1984).  The offset of the H-K calibration of solid salt cells is not the first report of such an effect. The authors claim that the offset in stress must somehow be incorrect because it leads to negative compressional stresses when the sample continues to be compressed. 

I cannot be sure how the H-K correction has been applied, but some criteria for its application are worth reviewing:  typical issues are the following:  1) the correction applies to the original design, dimensions, and materials of a Griggs apparatus, particularly the load and confining pressure pistons and pressure vessel, as described in the H-K calibration paper, 2) the correction applies to solid salt assemblies and load piston packings that are the same (or similar) to those used in the H-K calibration, 3) the correction applies only to larger displacements in a constant strain rate experiment (at shortening strains of 5% or greater), and 4) the correction is applied to force records that have already been corrected for the “hit point” force.  One of the improvements that might be made to a stress correction for solid-medium apparatus would be to determine the transient viscous correction at low finite strains.  At strains less than 5%, the steady-state stress correction indeed overcorrects force measurements.  That is, not only can samples deforming by dislocation processes show transient increases in flow strength (before a steady-state is reached), but solid salt assemblies may show viscous resistance that increases with strain as well (such as transient dislocation creep of solid NaCl).  This may also apply to transient creep during stepping experiments where internal defects and creep strengths change with strain rate, temperature, and stress relaxation steps (during the stress drops of Figs 2 and 4?).  The H-K correction also cannot work if an accurate “hit point” force has not been determined.  Thus, when hit points have not determined in multiple-step experiments, the conditions needed to apply the correction have not been met.  Corrected stresses may appear to be negative because the “hit point” force wasn’t remeasured for the current experimental step.

Finally, it is worth noting that the accuracy of results obtained with the solid salt assembly is +/-30 MPa, so if a sample deforms by diffusion creep at a differential stress of just 4 MPa, for example (not an uncommon value at low strain rate for a near-linear Newtonian flow law), a corrected stress value can easily appear to be negative (as much as -26 MPa in this example).  This does not imply that the sample is extending or that the corrected stress is incorrect.  It simply indicates that the sample flow stress is less than 30 MPa.  This means the sample is too weak to measure with the solid salt assembly.

As suggested above, a simple observation that fine-grained samples deforming by dissolution-precipitation creep are weaker as this mechanism becomes predominant can be made qualitatively comparing uncorrected external force measurements (if all other factors are the same). However, quantitative determinations of n values depend on accuracy in both strain rate and stress determinations.  While the strain rates are well known, I have reservations about the accuracy of uncorrected stresses (as discussed above), and thus the quantitative nature of n determinations (Fig. 6).  To be sure, m values don’t look as well determined as n values. However, this is not uncommon for many datasets for grain size-sensitive creep laws.  The authors make some credible arguments for why m is so difficult to measure.  Much of this might indeed be related to the size distribution of grains and variations in predominant grain boundary processes for different grain sizes.  If grain size of a starting material were truly uniform, then one might expect that values of m match theoretical model predictions.  However, it is more likely that, in natural fine-grained shear zones and ultramylonites, grain sizes will show a broad distribution (as measured in this study) and spatial variations in grain size could lead to spatial variations in predominant grain boundary deformation mechanisms.

I have a few additional comments and questions that are not as important as those above (ie., they don’t bear on acceptability for publication), but I will add them here in case they are helpful in the revision of this manuscript.

Quantitative determination of activation energy Q also depends on accuracy of differential (or shear) stresses, but this is not a major focus of this study.  I would simply note that activation energies for creep of different feldspars might depend on composition.  It’s fair enough to compare the value of Q reported here and the Q for diffusion creep of fine-grained anorthite of Rybacki and Dresen (2000), but the Q for deformation of intermediate Ab-An composition plagioclases of granitic ultramylonites might not be expected to be the same as for deformation of pure An100.

A question of minor importance is why fine-grained samples show compaction early in the experiments. I might have thought that ultramylonites are very dense, with very low porosities, limiting the amount of deformation by compaction.  Do these samples have microporosity, associated with their fine grain size?

I find Figure 7 difficult to understand and evaluate.  How are we to understand the mechanical results of pure shear and simple shear (or general shear)? Principally, my problem is how to compare stresses and their transients if the horizontal axis is ”not to scale”.  Couldn’t equivalent strains be plotted, so that one can see whether samples in deformed in these different configurations compare well or not at the same equivalent strains?  If equivalent strains are determinable for some but not all of these experiments, maybe it would be easier to understand if the plot just shows those experiments for which equivalent strains are determined.

Finally, I apologize for the length and severity of this review.  I believe that this study has merit, and I expect the conclusions of this manuscript are likely correct.  However, I strongly urge the authors to decide how best to support the likely processes of grain boundary deformation, either by accurate microstructural observations (which do not depend on stress measurements), or by qualitative examination of the more obvious mechanical results (higher vs lower shear stress), or by a serious analysis of mechanical results with appropriate corrections.

Andreas Kronenberg

Nevskaya et al. (2025) explored the bulk rheology of granitic compositions, which is more representative of the continental crust than the rheology of monomineralic quartz or feldspar. The scientific questions addressed in this study are highly timely, and the effort behind exploring these questions is commendable. The journal is also appropriate for the publication of this study.

Although I have not thoroughly checked the companion paper, the microstructural observations and interpretations presented here appear sound. Conducting three different types of experiments within a single study is rare, and this approach provides valuable insights. The authors have an opportunity to further explore whether the results from coaxial and shear experiments are truly comparable under the same deformation conditions and whether the mechanical data can be transferred across different deformation geometries. The observed relative mechanical strength differences between different experimental setups (for a specific deformation geometry) are logically consistent.

Overall, the authors have done a good job outlining their data acquisition and correction procedures. However, I am not entirely convinced by the data points collected from rate-stepping experiments for measuring n-values. Firstly, which part of the data was used from each step to calculate stress? Highlighting the relevant portion of the mechanical curve would be helpful. Additionally, why are stress values not shown in Table 1? One important factor they should consider is the potential effect of rate-dependent friction and/or viscous drag (from the confining medium interacting with the σ₁ piston at different displacement rates) on their mechanical data. This factor may or may not significantly impact their n-value calculations. I recommend consulting the supplementary materials of Proctor et al. (2016), Okazaki and Hirth (2020), and Ghosh et al. (2022). Based on my own experience conducting coaxial rate-stepping experiments using a conventional rig at higher P-T conditions, the rate correction can range from >15 MPa to as low as 2 MPa, depending on the successive rate steps. However, since this study was conducted at a much lower temperature, I suspect that the correction between steps might not be insignificant. It is possible that applying a systematic correction could lead to a higher n-value than what is currently presented.

My detailed comments can be found in the attached PDF file. Below are a few of the important points:

1. Referencing could be better, as highlighted in the introduction.
2. There are a few factual mistakes that I noticed. Therefore, the paper should be checked thoroughly. E.g., Fukuda et al., (2018), used a Hot-pressed polycrystalline quartz, not novaculites. Hirth et al., (2001) used the experimental results of Gleason and Tullis (1995), who in turn, used BHQ, not Simpson quartzite.
3. Line 170: When converting the shear strain rate to an equivalent strain rate, you are effectively transforming shear data into a coaxial geometry. In that case, shouldn't you also use the equivalent stress (transformed to a coaxial geometry) for calculating the n-value?
4. Line 260: When discussing grain size, are you treating all constituent minerals collectively, without distinguishing between quartz and feldspar? Would it be possible to differentiate between the grain sizes of quartz and feldspar separately in your analysis? Have you checked if the piezometers are providing reasonable stress values for such grain size ranges?
5. Line 285: This value (n = 1.81) is not significantly different from those reported in several recent quartz deformation studies. In addition, those studies also interpreted grain size sensitivity. Given this similarity, why wouldn't the deformation mechanisms interpreted in those studies be applicable here? To clarify the discussion on Ghosh et al. (2022) in Nevskaya et al., (2025a): The study was focused on coarse-grained Tana quartzite and provided insights into deformation behavior that were later expanded in the 2024 study. In is noteworthy, that those authors interpreted their results in terms of Dissolution-Precipitation of silica material along the grain boundaries (~ GBM) as an accommodation mechanism, which is different from the DP“C=creep” mechanism interpreted in the present study (Nevskaya et al., 2025a, b). The observations from the 2022 paper should be considered in the context of the 2024 study.
6. Line 300: This is a personal opinion, as interpretations may vary among researchers. However, I do not think this is a very reliable method for calculating the grain size exponent. Determining the m-value is inherently challenging, and the complexities discussed by the authors further complicate the process. Moreover, the large range of errors associated with only three data points does not inspire confidence in the results. Ideally, repeating these three experiments would increase the number of data points, improving the statistical reliability of the method. Without such additional data, I doubt that these m-values will be widely accepted within the community.
7. Line 305: Only 2 data points do not justify 'limited data" or the calculation of Q-value and A-value. As discussed above, any error in the n-value calculation might affect the Q-value.
8. I might be missing something, but Figure 7 does not make much sense to me. My apprehensions can be found in the pdf file.
9. Line 560: In addition to Figure 9, I would encourage the authors to compare their new data with Rutter and Brodie (2004b), Ghosh et al. (2024), Fukuda et al. (2018), and Richter et al. (2018) studies directly on a single plot. The same practice should also be done using earlier feldspar studies. Preferably, this should be done in a normalized space using the original reported mechanical data rather than comparing it (the new data) with the published flow laws. The latter part is just a suggestion and should not be taken as a compulsion. One of the main reasons for this suggestion is my lack of confidence in the reported flow law (which the authors themselves claimed to be a first-order approximation). However, direct data-to-data comparison should be able to generate more confidence about the claims like “fine-grained polymineralic rocks are deforming up to six orders of magnitude faster than quartz”.
10. Maybe the authors can prepare a small section discussing the limitations of this study.

Good luck with the revision.

Subhajit