Dear editor,

This paper investigates the crystal orientation fabric of the Dome Fuji Station ice core using a novel methodology as the dielectric anisotropy (from the dielectric permittivity tensor). Dielectric anisotropy is revealed as a good indicator of the vertical clustering of the crystal orientation fabric, also exhibiting a correlation with the concentration of chloride ions and with the amount of dust particles in the ice core. From the results, the authors conclude that the COF clustering is therefore affected by the presence of chloride irons, which increase the dislocation density, promote dislocation creep and enhance the COF clustering, while the presence of dust impedes it. The results show a COF layering in the upper 80% of the ice sheet, where the COF contrast amplitude increases at deeper layers. The conclusion is sound regarding the lowest 20% of the ice sheet, as layers will behave differently under stress depending on the COF cluster strength.

This well-written and well-organised manuscript presents a very useful methodology to be further evaluated in the future. We could obtain the COF contrast from the permittivity contrast obtained in VHF/UHF radar sounding. This will allow comparing deep COF layers avoiding areas with layers with heterogeneous thickness. This heterogeneity can lead to layer disturbances and folding due simple shear close to the bedrock.

The detailed description of the presence of soluble impurities and particles and its correlation with the COF is very useful for the understanding on the effect of them on ice rheology, which is currently unknown.

The manuscript is relevant for The Cryosphere and thus can be a valuable contribution once some important issues are addressed. Thus, I recommend that the paper is accepted after minor revisions.

Suggestions for improvement:

Line 50: this statement “It has been suggested that the finer grain size in glacial ice results from high concentrations of impurities such as dust particles or soluble substances 50 that restrict grain growth via pinning and drag at the grain boundaries” requires a reference.

Line 80: I would give details of the physicochemical properties obtained.

Table 1: Could you explain in the text why the thickness at the EDC samples (Durand) are not indicated?

Line 110: the authors do not explain why this study focuses on the upper 80% and not in the whole ice core. What are the difficulties to apply it in the bottom 20%? A discussion on this aspect will be useful.

Figure 2. Colouring in red and blue the lines is not necessary as they do not provide extra information.

Line 150: the detrended Ae value is a key parameter used in this work. It is mathematically defined in the text, but it would be very useful for readers to be able to see an explanation of what it value means, in practical terms.

Line 186. has the value of 0.0334 for the single ice crystal been determined in this study or does it come from the literature? In this case, a citation would be needed.

Line 213. Would it be possible to briefly explain the relationship between the permittivity value and the normalized eigenvalues? (here or in the caption of figure 6). I find the reference to Saruya et al. 2021 not enough, as this data is relevant for the conclusions.

Figures 4 and 5: I suggest including the references at the legend, as in figure 7.

In general: please, check the graphics in all figures. Box and axis markers do not match (as in figure 7). 

Line 384: the reason why the presence of HCl has a stronger effect on dislocation migration than NaCl is explained later, in line 387. I suggest moving line 384 there to make the paragraph more understandable.

Line 444: In general: It should be explained with a bit more detail, what the positive or negative feedback mechanism referred to Azuma (1994) does mean (Relationship between CPO and deformation conditions).

Line 499: Regarding the alteration of layers in the deep parts in ice sheets, here I miss some discussion with observations already done in ice cores (as in Faria et al., 2010; Jansen et al., 2016, etc…).

Conclusion and chapter 4.5 Implications for the deformation regime in ice sheets: both texts are very similar. I would modify the conclusion part in bullet points or in a more synthetised way, because as it is now it reads as a repetition of the explanation given in the previous section 4.5.

General comments

This contribution provides an excellent methodology for exploring the chemical and mechanical heterogeneity of ice, with a likelihood of inferring crystallographic fabric from permittivity anisotropy. The approach is valuable for the community and the data appear robust. I have no concerns about the data acquisition. The comparisons with with the nearby cores and with the Dome Fuji 1 core chemistry make good sense, including using the orientation tensor as a metric. This is a large dataset that will serve a purpose for many years to come.

I have a few significant concerns about the interpretations. Some of these can be addressed with additional explanation, and some may require reevaluating the text.

Specific comments

1a. Crystal orientation fabric (COF) is not the only factor that affects permittivity or permittivity anisotropy. Dust, salts, or other impurities that are layered in the ice core, even at a fine scale, can cause permittivity anisotropy. I suggest that the paper review the potential impact of these factors on anisotropy and evaluate whether they can robustly related the permittivity data to COF.

1b. If this investigation cannot rule out impurities as factors, then I suggest that the interpretations, including the discussion and conclusion, focus more on reporting the permittivity anisotropy and its correlation with the other features in Fig. 9 and less on COF. I recognize that several sections in the discussion consider how the impurities affect COF, all of which appear to be valid and substantive ideas. At the same time, the lack of a consistent relationship between permittivity anisotropy and, e.g., Cl and dust, indicates that the mechanisms are quite incompletely understood. I do not feel that the data and reasoning support the interpretation (line 400) "Consequently, we propose that the relative strength of COF clustering is mainly determined by a balance between the levels of Cl- ions and dust particles."

2. I was not able to understand the data collection methods from the text, in particular the geometry of the sampling. A figure that shows the spatial relationship between the core, the samples, and the measurement and motor directions would be extremely useful.

3. The text does not include an explanation of the source of uncertainty. It appears that the reported standard deviation is the result of some form of averaging, and it is not clear whether any systematic uncertainty is factored it. I suggest the manuscript add a clear method for calculating uncertainty.

3. On the topic of choosing which technique to use to analyze a core, lines 209-210 state that the "statistical validity of the thin-section-based method is inferior to that of the thick-section-based method." I don't find that statement accurate. The thick section data unquestionably average over a larger volume, but that doesn't mean that they are more statistically valid. I do think that representing the larger volume will provide a better relationship to rheology than the potentially high-frequency variations recorded in thin section data, but that is not the claim currently made. Additionally, as implied by my comment #1, the relationship between COF and permittivity anisotropy is not necessarily straightforward.

4. Much of the discussion focuses on the detrended data. The manuscript mentions the method only briefly in the caption to Figure 3 and on Line 151. More description of the method, including physical and statistical rationale for the choice and comparison with other methods, would provide more confidence in the value of the detrended data.

5. I suggest that a revised manuscript include more statistical exploration of the data comparisons stemming from Fig. 9. I noticed two locations with reported correlation coefficients (lines 355 and 390), which seem to be for timeseries pairs (e.g., delta-e and HCl). I feel that a more systematic, potentially multivariate approach would have more value. Part of this request is to add more reliability to the interpretations: at present, the mixed signals of whether dust or Cl or something else will affect delta-e (e.g., Type A and Type B relationships) does not provide a pathway to predict the effect.

This paper has the potential to make a significant impact in the field. I appreciate the authors considering these comments as ways to strengthen the paper and improve its impact.