# Seismic Wave Speeds Derived from Nuclear Resonant Inelastic X-ray Scattering for Comparison with Seismological Observations

*Reviewer 1:*Alexeï A. Bosak

*Reviewer 2:*Anonymous

*Reviewer 3:*Anonymous

**Round 1**

*Reviewer 1 Report*

General comments:

The manuscript presented by B. Delbridge and M. Ishii explores the links between NRIXS-derived values and macroscopic averages relevant for the seismology. Significant part of paper is devoted to approximate semi-analytical calculations.

The most difficult point for me was to rely on the statement that authors show in the unpublished manuscript that the relevant averaging scheme for seismic wave propagation is the Voigt average. I couldn’t follow the arguments of unpublished paper for obvious reasons, and in general I cannot see why constant strain condition is reliable for compact polycrystalline aggregates. Treatment in the Appendix of present paper relies solely on the use of perturbation theory in particular form and has no links with seismological observations.

The values of estimated errors, as well as main statement concerning the upper bound of Debye velocity, are critically dependent on the validity of Voigt average in the context of seismic waves propagation. Idem for the utility of subchapter 2.1.

Generation of large set of constrained elastic tensors is an interesting approach, which allows to reduce the dimensionality of data representations. Constraint of constant averaged speeds is used for different averaging schemes. What remains unknown is the probability distribution in the space of elastic moduli – which can strongly affect the shape of hystograms of Fig. 3.

Fig. 4 could be instructive, but is forced to Voigt averaging and probability distribution can affect the density of points.

Subchapter 3.2 claims that averaging schemes other that Voigt’s underestimate the errors. However, it’s worth reminding that VRH and [36] averaging schemes were experimentally validated for the polycrystalline aggregates.

To conclude, the utility of manuscript critically relies on the validity of unpublished [16] results, which appear to be largely counterintuitive. If, indeed, they are convincing enough, embedding them to the manuscript to some extent is the must. In such a case I would be willing to propose some technical comments given below.

Technical comments:

Page 3. It should be underlined that averaging over the unit sphere < . > is not necessarily uniform and is related to the orientation distribution function.

Page 7. Integration over k can be skipped for transversely isotropic material, as

v_{WD}^{-3} = 2/3 v_{D(equator)}^{-3}+ 1/3 v_{D(axis)}^{-3}_{,} and just two previously calculated extremal values are needed.^{ }

Page 8. Analytically, v_{WD} = v_{D}, precisely. Using approximate analytical calculations to suggest that v_{WD} ~ v_{D} is thus a non-necessary complication.

Typewriting errors:

Page 3. Projected men wave speed

Page 4. Phonon Propogation

Page 8. Resuss

*Author Response*

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Author Response File: Author Response.pdf

*Reviewer 2 Report*

In this paper Delbridge and Ishii discuss the difference between the Debye sound velocity determined from Nuclear Resonant Inelastic X-ray Scattering (NRIXS) experiments performed on polycrystalline samples, Debye sound velocity estimated from material’s elastic properties and the Debye sound velocity derived from seismic wave speed, with specific focus to the case of anisotropic materials. The main conclusion of this interesting analysis is that for anisotropic samples, the sound velocities derived from NRIXS measurements are significantly below the true material’s sound velocities.

I believe the authors hold an important point that deserves to be made clear to the community working on the Earth’s core.

I only have few, but possibly major remarks, which authors have to address before publications, and other comments aiming at improving the paper.

Major points

1) When generating the one million random transversely isotropic elastic tensors were mechanical stability criteria considered? If not they have and, in this case, do these extra constraints on Cij change the results?

2) In many places in the manuscript the authors make reference to a paper under review (ref [16]). I could not access this work. More in general, being this not accepted, it cannot be use to sustain strong statements such as “Voight-Reuss-Hill averages are incompatible with observed seismic wave speed” or “When comparing with seismic wave speed from a model such as PREM, the wave speeds should be calculated using the Voight average” etc. Furthermore the assumed elastic constants for the inner core are from ref [16].

At many levels the discussion and conclusions are based on the work in ref [16]. Unless this paper has been accepted in the meanwhile, the authors should rewrite their discussion and conclusion in a way that is less heavily based on this work.

Other points

1) Abstract. “Unit of anisotropy”. As there is not a unique way to define and quantify elastic anisotropy, this sentence in the abstract is not clear. Only later on reading the paper it becomes clear what the authors refer to as “unit of anisotropy”.

2) While I understand that the authors only want to focus the discussion on NRIXS, there is a wealth of other techniques that have been used to measure sound velocities of materials, including geophysically relevant iron alloys, that have to be at least briefly introduced or mentioned. For a review I invite the author to consider Antonangeli and Ohtani, Progress in Earth and Planetary Science 2:3 (2015) and references there-in.

3) Line 23. I would rather use “Inelastic scattering”, not absorption. I would as well avoid referring to this a “relatively new” technique, as it is now almost 20 years that it is used for iron and iron alloys under high pressure.

4) Line 28. “distribution of energy levels of the excited acoustic phonons”. I do not believe this is correct. Please check and reformulate the sentence.

5) Theory. “This low energy portion of the density of state exhibits linear phonon dispersion with Debye-like behavior”. The sentence might be misleading. Phonon dispersion typically refers to dispersion with the wave-vector q (exchanged momentum). Phonon energy is linear with q (for low q). Phonon density of state is linear with the square of the energy (for low energies). Please clarify.

6) Page 3, after line 58 “projected men wave speed” should be “mean”.

7) End of section 2, eq (20) and following line. I invite the authors to find an experimental confirmation of this conclusion on measurements done for hcp Fe (see for instance the already mentioned review paper by Antonangeli and Ohtani).

8) Results and discussion. All the examples are based on calculations (references 19-23). I strongly recommend adding examples with density and Cij from experiments. Many metals have an hcp structure and anisotropy comparable to hcp Fe (e.g. Co, Re) and data are available at ambient conditions and at high-pressure and high-temperature conditions (while not at inner core conditions) obtained by ultrasonic measurements or inelastic x-ray scattering on single crystals (N.B. momentum resolved, not nuclear resonant scattering).

*Author Response*

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Author Response File: Author Response.pdf

*Reviewer 3 Report*

In this manuscript the authors try to show that the Debye velocity extracted from nuclear resonant inelastic X-ray scattering (NRIXS) data for anisotropic material may not represent the its effective seismic wave velocity. In spite of the title of the manuscript no experimental NRIXS data are presented and discussed. Instead the authors concentrate their attention on different mathematical expressions of the Debye velocity which can be obtained for different Fe-alloys using exclusively elasticity data obtained from ab initio calculations. As such the title is misleading, and so are the conclusions.

Any scientist who work with inelastic scattering is well aware of the anisotropic problem. Sturhahn and Jackson (2007) clearly state: “It is important to note that this formulation will only hold approximately for elastically anisotropic materials”. From what I can understand the authors in this manuscript are trying to show how much this “approximately” can be, however I have a major problem (see following paragraph) with the arguments made in the manuscript and I cannot see where the novelty of this study resides.

Hill already in 1952 (Proc. Phys. Soc. A65 349) has shown how an aggregate of anisotropic crystallites show aggregate bulk and shear moduli, and, as a consequence, seismic wave velocities, which lie in between the Reuss and Voigt bounds (this is equivalent to the expression presented as eq. 20 in the manuscript). Since then, the elastic behavior of an anisotropic polycrystalline materials has been approximated using the Reuss-Voigt-Hill average and therefore it is not surprising that the mathematical exercise presented in the manuscript yields a similar result (line 137-139). More surprising is that according to the authors the Reuss-Voigt-Hill average is not compatible with observed seismic wave velocities (lines 140-142). This statement appears to be based on what the same authors have shown in a previous paper, i.e. that the relevant averaging scheme for seismic wave propagation is the Voigt average contrary to what has been considered until now. Since the mentioned paper (Delbridge& Ishii 2019) is actually only submitted, it is difficult for me to ignore 60 years of literature and accept such statement especially when even the authors can show that the Reuss-Voigt-Hill is indeed a good approximation for the Debye velocity of an elastically anisotropic material (Figure 3).

I also found that the paper does not give enough credit to the existent literature. Most of the equations reported have already been discussed in details by other authors (for example the Christoffel solutions reported in appendix can be found in Every Phys Review B, 22, 1746, 1980), moreover I have found some mistakes in the equations reported: for example in eq. 1, 4 and 6 the density is reported twice in the denominator but it should be present only once; in equation (22) the authors seem to imply that the bulk and shear moduli are those corresponding to the Voigt bound, whereas they are the adiabatic moduli. Moreover I cannot reproduce the denominators of the Ruess bulk and shear moduli (A10 and A11).

*Author Response*

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Author Response File: Author Response.pdf

**Round 2**

*Reviewer 1 Report*

The claim of the validity of Voigt average for the seismic wave propagation is based on its proximity to the simple orientational average of sound velocities. It is not precise, but rather true for small deviations from isotropy. However, sound speed in the isotropic polycrystal with anisotropic constituents will approach the orientational average of sound velocities only if the grain size is bigger than the wavelength. This condition is far from being guaranteed. Otherwise, aggregate will behave as a continuum and averaging of the elastic tensor must be evaluated – and in no way it can coincide to the Voigt average for strongly interacting anisotropic particles.

No claims on the validity of any kind of averaging can be based on particular symmetry of constituents (transversely isotropic here) and/or any kind of fitness of PREM constraints with any combinations of elastic moduli, calculated or measured.

The analytic result V_{WD} = V_{D}, applicable for any symmetry, follows from Eq. 5 of the manuscript (alternatively, Eqs. 2 and 3 of [35]), as the trace of rank 2 tensor is its invariant.

*Author Response*

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*Reviewer 2 Report*

After having red the revised version of the paper and the answer by the authors to my previous comments (regrettably only to mine, when it would have been useful and appropriate to have been able to also evaluate the responses to the comments of the other reviewers) I find the paper improved in many aspects but not all.

In particular the second of my major criticisms still holds: even the current version of the paper is heavily based on an unpublished paper by the authors (old ref 16, now ref 17). I do not see where the manuscript has been modified. I red the unpublished work provided by the authors, which is overall sounding, but in regard of which I do have comment and criticisms (but I am only reviewer of the submission to Minerals, not to the other one). As it reads now, the present work does not completely stand alone.

Other than this problem, I reiterate my previous general comment: the mathematical considerations outlined in this work have to be taken into account for a careful interpretation of NRIXS data and a meaningful comparison with seismological models. This clearly does not imply not using anymore such a technique, nor that the actual quantification of possible errors is strictly correct (as based on elastic moduli from calculations and as depending from the employed averaging scheme), but I do consider this paper as a general warning.

I am not familiar with Minerals editorial policy, but I would strongly encourage resubmission of a modified manuscript.

*Author Response*

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Author Response File: Author Response.pdf