Equations of State for the Deep Earth: Some Fundamental Considerations

Round 1

Reviewer 1 Report

In a vein that would have been appreciated by Orson Anderson, Prof. Stacey provides a concise discussion of algebraic and fundamental relationships that guide considerations of equation of state parameterizations. The work builds on and summarizes a line of thinking concerning high pressure limiting behavior that informs representations in accessible regimes.  Particularly useful ideas include the observation that the second derivative of 1/K’ as a function of (P/K) must remain positive while K’ remains bounded at infinite pressure.  Additional relationships given in the paper for higher order derivatives of the bulk modulus as well as for the behavior of the Grüneisen parameter will have lasting utility. The author convincingly argues that no one “best” equation of state parameterization can successfully be used for all materials and circumstances.   

The application of reasoning to the inner core is less compelling since the analysis is restricted to properties as given by PREM which is a known-to-be flawed representation of the inner core.  As successful as PREM is in describing many bulk properties of Earth, it's representation of the inner core does not accurately match either body wave or free oscillation observations.  Furthermore, elastic anisotropy and inhomogeneity of the inner core is large (comparable to the jump in properties at the ICB and radial gradients within the inner core).  The “best” recent models for the inner core have discontinuities at the inner core boundary that are substantially different from PREM and gradients of properties within the inner core remain uncertain.  Perhaps the author could argue that both fundamental equation of state reasoning and improved interpretations of better seismic data support the rejection of PREM as an accurate description of the inner core – but this is “beating on a dead horse” and more interesting will be consideration of the newer representations.

As articulated in the “Concluding comments”, the author hopes to see further progress in development of analytic forms of equations of state. Not as well articulated is why such will be needed for the next generation of science. Historically, analytic forms have been convenient for (1) conveying the behavior of data with a small number of “fitting parameters”, (2) providing a means to obtain “reliable” derivatives of measurements (ie. the bulk modulus from density-pressure data), (3) extracting parameters deemed “interpretable” (ie.  intercepts for K and its pressure derivatives), and (4) providing “extrapolation rules” for use in regimes not directly sampled by measurement. 

My personal views (stated perhaps too strongly) are given below to challenge the author to improve an articulation of the future needs.

uses (1) and (2) require no further improvements in existing parameterizations – although more critical assessments of the “quality of fit” need to be enforced on practitioners. (and consumers need better guidance on reliability of uses based both on statistics of the misfits and the behavior of parameterizations) The necessity of extrapolation (4) has receded as reliable measurements (and now first principle theory) has pushed “data” to unprecedented extremes. Regarding use (3), I accept the current premise that the high-pressure limits on K and derivatives provide a plausible fundamentals-based parameterization for extreme conditions, but the idea that forces between atoms can be fully mapped as a function of distance with a handful of heuristically-motivated constants remains improbable. Applications to Earth have plateaued – we are not seeing better radial Earth models – only increased resolution of the 3-D structures. Applications of equation of state parameterizations to the “radial Earth” have provided no strikingly new insight since the pioneering work of Stacey and a number of others.  With Prof. Stacey’s deep knowledge of this field, can the next horizon of ignorance that needs to be overcome be more fully described?

Nit-picking: The three uses of “etc.”  in this manuscript appear easily avoided with small revisions using more concise language.

Author Response

Response to Reviewer 1

It is the second paragraph of this review that calls for significant amendments to the paper, the essential point being that, in relating theory to observations I have concentrated attention on the PREM earth model, which is now known to be flawed in some important ways, and there are later studies with observations that probably relate better to the real earth. My response is a significant rewriting (and expansion) of Section 3 of the paper, Inner Core Problems, (originally lines 152-209). This response is intended to deal also with the Reviewer 2 comment, identified with line 151 of the PDF version, which makes the same point. There are also added references that are now used. As far as conclusions are concerned, there is no dramatic change because observations from the added literature reinforce rather than resolving the problems that are drawn to attention.

The four dot points in this review are identified with queries (1) to (4) in the third paragraph. All four points call for what is essentially the same response, a justification of the analytical parameterisations that I consider. As the reviewer remarks, analytical representations of equations of state are convenient and they can be manipulated mathematically to obtain conclusions about properties that depend on derivatives. But there is a danger in this. A bad formula leads to bad conclusions and these may be difficult to refute because they are obtained from a formula that may have an obscure justification. I am attempting to improve that situation by developing constraints on the formulae that are rigorous and fundamental. To the extent that this is possible, it makes the formulae more reliable and this is particularly clear when it reduces the need for adjustable constants in data fitting. It also draws attention to reported observations that conflict with theory and these are sensitive development points of the subject. A comment to this effect is added to the final paragraph of the conclusion.

The final point: The ‘etc’s are deleted.  

Reviewer 2 Report

This paper reviews the author's previous work on high pressure equations of state, and especially the infinite pressure relationships between P/K_T, K_T' and the volumetric grueneisen parameter. Many of the points made in the manuscript are of interest to those of us working in high pressure geophysics/petrology.

In my opinion, the manuscript requires some modifications to maximise its value, especially given the overlap with Stacey and Hodgkinson (2019). If I understand correctly, the manuscript aims to provide constraints that should be used/understood by seismologists and petrologists. If that is correct, then I would like to see:

A self-contained summary of the necessary theory, with more citations. A consistent separation of thermodynamic identity from approximation (with explicit mention of the assumptions required to generate the approximations). More rigorous use of subscripts. Figures demonstrating the proposed thermodynamic constraints, preferably including equations of state that fail, and available high pressure, high temperature data. Some discussion of the temperature dependence of γ.

With respect to Point 1, understanding any significant part of the manuscript currently requires frequent reference to the authors' previous works, including: Falzone and Stacey (1981), Stacey and Davis (2004) and Stacey and Hodgkinson (2019). I would prefer to see a more detailed summary in the current manuscript - with reference to previous works for derivations.

For Point 2, one salient example is Equation (2), where the first equality is an identity, while the second is an approximation based on free volume theory. The text makes no mention of what free volume theory is, and the citation given (Vashchenko and Zubarev) is not easily accessed. I know that much of the theory is given in the references above, but many readers will not appreciate where the theory has come from without a bit more guidance.

For Point 3, I agree that in many cases the difference between K_T and K_S can be ignored, but in much of the manuscript you're discussing theoretical infinite pressure limits, and it isn't clear to me that K_S - K_T (= γ² Cv T / V) can be neglected when making the kinds of arguments made in the manuscript.

Point 4 is a particularly important one for me. I liked the MgO figure in Stacey and Hodgkinson (2019; Figure 4), and would like to see more figures supporting your arguments, both for K'(P) and for γ(P). Stixrude and Lithgow-Bertelloni (2005) published several figures supporting their proposed equation of state (BM3+Taylor expanded mode frequencies), and I would like to see similar presented here. One useful figure might use the Brillouin-derived elastic constants presented by Kurnosov et al. (2017). Their results produce a concave-up curve on a 1/K' vs P/K plot that, if extrapolated, would argue for a value of K'_inf << 5/3. It would therefore be interesting to hear whether you believe that d(1/K')/d(P/K) should monotonically increase with pressure. I've actually played about with trying to find a single functional form that satisfies the requirements in Stacey and Davis; the best I've found is based on an Einstein function (see attached).

As for Point 5, I think the reason why the free volume theory (in any of its guises) has not been more heavily used is that expressing γ in terms of P, T dependent parameters does not lend itself to efforts to create fully self-consistent P-T-V equations of state. It would be extremely interesting to hear how/whether a full PVT EoS could be developed using the theory/models outlined here.

Line comments can be found at the bottom of this message.

I think that with some changes, this would be a very welcome contribution to the literature.

Best wishes,

 

l.39 - which eoses do not? Perhaps a good opportunity to rehash the figure from Stacey and Davis?
l.48 - It's probably a good idea to mention early that just because a functional form satisfies the infinite pressure constraints, it may do a bad job at low pressures. Also that many thermal EoSes require the isothermal EoS to go to negative pressures. This precludes the use of several isothermal equations of state, for which K' very rapidly increases at negative pressures.
l.53 Use two separately numbered equations here. Use the identity symbol for thermodynamic identities.
l.55-74 Limiting myself to this manuscript, I get little from this section. Where does the expression in (2) come from? Is it an identity? A finite strain expansion at low pressure? Is it valid at any temperature (for K_T)? Any entropy (for K_S)? or only static conditions? Is f a function of T? Does it depend on K_T or mu?
l.58 Please keep the subscripts!
l.61 A plot would be good here.
l.77-l.78 are identities...
l.80 why does it vanish? Citation needed?
l.83 first inf symbol needs to go outside the square brackets
l.85 You say that Eq. (3) and Eq. (6) are identities, but it isn't clear why in this manuscript. The form of Eq. 3 is from free volume theory, soI think there needs to be a justificantion for why this is a universally valid approximation at infinite pressure.
l.89-92 How are these derived?
l.95 indeterminate, not indeterminant. This appears again on l.102
l.97 How much do these high derivatives tell us about the finite pressure regions that we're interested in? How smoothly do you expect the curves to vary as a function of P/K at high P?
l.147 citations needed
l.151 There have been numerous purported PKJKP observations (early papers by Wookey, Deuss, Cao, Romanowicz, ...). These should definitely be cited!!
l.171 There needs to be a figure here.
l.184 Is the source of error in these theories clear?
l.194 Observational citations needed.
l.196 What are other explanations? Why are they not convincing?
l.199 I think there needs to be a definition of "best" here. Over what pressure range? Are we including temperature? Should the EoS provide a closed form for the thermodynamic potentials (Gibbs/Helmholtz/Enthalpy/Internal energy)? What about a closed form for volume (or pressure)? Should the EoS work well for all materials at extreme pressure, or just HCP phases? Should there be an expression for mu as well as K_S?
Much of the discussion here deals with very high pressures, but at what pressures do other equations of state start to fail? Is a BM3 EoS good enough for the mantle? And if not, why not - what kinds of errors do we have to contend with if we stick with the Stixrude and Lithgow-Bertelloni thermal EoS, for example?
l.222 Why not? Is this based on extrapolation by eye? Perhaps a figure would be good here.
l.221-233 This is just for the lower mantle, right? Different values of x would apply to different substances? I agree that there should probably be a good single EoS for the inner core, but I'm not yet convinced that a single EoS could work for a 1D "average" of the lower mantle, which is a heterogeneous multiphase (per/bdg/cpv/ppv/stv/seif/...) composite undergoing numerous reactions and spin transitions.
l.241 which other tests?
l.244 For the benefit of other readers, I think Rydberg/Vinet is clearer (with citations to the Rydberg and Vinet papers, rather than Stacey et al., 1981.
l.285 The manuscript would benefit greatly from this graph!
l.299 This assumes that the gradient of 1/K' is monotonically increasing w.r.t P/K. This certainly isn't the case for liquids like SiO2, nor is it likely to be true for most minerals with structural flexibiity. Do you have a good argument for its veracity in high density structures?

 

Comments for author File: Comments.pdf

Author Response

Response to Reviewer 2

I have found it difficult to write a sensible reply to this review. In some places I am left to guess just what the reviewer’s intentions are and my responses are responses to my guesses. The second and third paragraphs of the review refer to points numbered 1 to 5, implying that they are listed in the first paragraph, but that is not so and my responses, based on inferences from the remarks in the second and third paragraphs, are numbered (1) to (5) below. For a couple of the line numbers comments appear not to be identifiable with the specified lines and in these cases I give in square brackets the lines that appear relevant to the comments.

Point 1. The reviewer objects to my use of the results of derivations and analyses in two review papers, Stacey and Davis, 2004, and Stacey and Hodgkinson, 2019, asserting that this material should be repeated in the present paper. That would convert it to another major review, with a duplication of material that I see as inappropriate. The review also calls for a large number of new analyses and figures which, if I were able to provide, would require an estimated two years and result in a document hundreds of pages in length. The review is not so much an assessment of what I have written but a statement of what the reviewer would like to see. I have had to restrict my consideration to comments that bear directly on the fundamental questions that my paper addresses and avoid distraction by requests for material that could, instead, be a new and comprehensive review or book by the reviewer.

Point 2. The reviewer has a different interpretation of the word ‘identity’, as applied to mathematical expressions, from the one I use. In Eq. (2) the first expression is a definition, not an identity. To avoid possible confusion with the definition of the lattice mode gamma, I now refer to ‘thermodynamic definition’. The distinction is important to the use of Eq. (2) to derive Eq. (3). Although the second expression in Eq. (2) cannot be an identity while the parameter f is the subject of alternative interpretations, it does not matter what value or P-T variations f has, because when we apply Eq. (1) to Eq. (2) f is cancelled out. It does not vanish or become zero, it simply does not appear in Eq. (3). Therefore Eq. (2) could be regarded as an identity by using f as a completely arbitrary function and then it does not matter what that function is because it does not appear when Eq. (1) is applied. That makes Eq. (3) an identity. Concerning the generalised free volume formula in the final expression of Eq. (2), I see no justification for a discourse on free volume theory. That theory was used by Vashchenko and Zubarev to derive a version of Eq. (2) with f = 2. No one else has used this theory and, as we now know, the f = 2 result is wrong anyway and free volume theory does not lead to corrected (generalised) version of the formula. There are other, quite different derivations, but since history says that a formula of this type first appeared in the free volume paper by V and Z, the name has stuck, but no useful information is conveyed by the expression ‘free volume formula’.

Point 3. The reviewer’s assertion about the difference between K_S and K_T is wrong. These quantities converge with increasing pressure and, in the infinite pressure extrapolation they are equal.

Point 4. The request for figures and analyses of proposed equations does not appear to contribute to the discussion of fundamental principles that are the subject of this paper. The reviewer’s doubt about whether 1/K’ increases monotonically with P/K and the possibility of a conflict with the thermodynamic K’_∞ > 5/3 arise from the problem that these thermodynamic arguments assume a constant stable phase. This does not apply to liquids very close to the melting point or to open crystal structures close to conditions of instability. It is particularly clear that there is no difficulty under the high pressure conditions that give close packing, in both solids and liquids.

Point 5. The Grüneisen parameter alone cannot, in principle, lead to the sort of equation of state that is contemplated. This is illustrated by Eq. (6), showing a connection between derivatives of γ and K. It means that γ can be used to modify or constrain the form of an equation, but not originate a new one. This point is made explicitly in Stacey and Hodgkinson (2019) and extended in Section 2 of the present paper.

 

Line 39: The only proposed equations that do not satisfy Eq. (1) are unphysical nonsense, requiring P or K to vanish at finite compression.

Line 48: Negative pressures are irrelevant because they would make any material unstable. It must break apart when (or before) the atomic force function holding it together reaches a point of inflection. High negative pressures cannot exist in a solid and I see little point in discussion of the properties of material that assume them.

Line 53: see point (2).

Lines 55-74: see point (2).

Line 58: see point (3).

Line 61: a plot of what? I cannot see what is requested.

Lines 77-78 [80-82]: see note (2), definitions, not identities.

Line 80: This is just standard mathematics. If γ remains finite when V vanishes, so that lnV becomes minus infinity, then dγ/dlnV becomes zero. This and a corollary dealing with the slightly trickier situation when a parameter becomes infinite rather than zero are referred to in Section 5 of Stacey and Hodgkinson (2019), now referenced.

Line 83 [87]: Yes, now corrected.

Line 85: It is derived directly from Eq. (2), with f cancelled. See Point (2), above.

Lines 89-91: Eq. (7) is the same as Eq. (6) with the square bracketed factor as subject of the equation. Eqs. (8) and(9) are derivatives of it.

Line 95, also 102: Yes, now corrected.

Line 97: Individually these derivatives can tell us nothing. They must be used in pairs because it is ratios of derivatives that constrain an EOS, as in Section 5 of [6].

Lines 147, 151: The queries here arise also in Review 1 and are answered in the response to that review.

Line 171: A figure from reference [15] is now cited.

Line 184: Data from observations, not theory. Data fitting used for error estimates, which are clear.

Line 194: hcp iron is anisotropic but bcc iron is not. This is now stated.

Line 196: The only other explanation of IC anisotropy that have heard advanced (decades ago), that it is magnetic alignment, failed by so many orders of magnitude that it did not survive the meeting at which it was suggested.

Line 199: The intended meaning of ‘best’ is discussed in Section 4. There can be no simple answer, but mu is not under consideration. It is covered by Eq. (15). The question also refers to the BM3 EOS but, fitted to lower mantle data, it extrapolates to negative P and K at higher pressures, making implausible derivatives even in the observed range.

Line 222: The range is restricted by the amplitude of thermal vibration. I do not see what figure would be relevant.

Lines 221-233: This is a general argument, not specific to core or mantle.

Line 241: The K’_∞ test, is discussed in Section 1, and the λ_∞ test, is discussed in this section.

Line 244: Vinet was a late starter, who failed to acknowledge that ‘his’ equation had a long history, involving Zharkov and myself as well as Rydberg. It is inappropriate to attribute it to him simply because he exaggerated it significance.

Line 285: The suggestion of a graph here would be duplication of a graph in [6], which the subject of a favourable reviewer comment in the second sentence of his Point 4. Arguably, it might be appropriate for a comprehensive review article or book but not the present paper.

Line 299: This is discussed in Point 4, above. I argue that 1/K’ increases monotonically with P/K for any material (solid or liquid) that is stable and not very close to a phase transition. The phase structure of silica near to its melting point is complicated and the P-T variations of the properties of solid and liquid are sufficiently different to doubt whether liquid SiO₂ is really a single phase in the conventional sense. There is certainly no difficulty in the liquid outer core.

 

Round 2

Reviewer 2 Report

Firstly, let me apologise to you for your difficulty in reading my original review. During submission, the formatting of the review was lost, including the bullet pointed comments in the third paragraph. I'm avoiding bullet points in this review.

Secondly, my review suggestions were intended to be fairly minor - maybe about two days work to summarise (not duplicate) key points from previous papers, and plot a few EoS curves with available experimental data (perhaps Kurnosov and a couple of others). Certainly I had no intention for the paper to become a major review, take two years or run to hundreds of pages! I'm only Reviewer 2, not the devil incarnate...

In the following, I will drop many of my original comments - most of them were intended to make the article more readable/understandable, and were not a reflection on the arguments made in the paper. For example, I think figures are useful, but I won't insist on them.

 

However, I will restate a few comments. Bear with me.

1) In response to my objection to dropping subscripts, it was never my intention to dispute that K_T=K_S at infinite pressure (although my original comment does read that way. Mea culpa). Rather, I question its use as an approximation for the deep Earth at finite pressure.

Perhaps there aren't any places in the manuscript where the distinction matters - if you think this is the case, one alternative would be to explicitly state (around l.64, or at the beginning of the main text) that wherever "K" is written, it could equally apply to K_T or K_S. I'd prefer that to saying that the two "differ too little" to be important, because the difference is fundamental to many properties of the deep Earth (C_V is definitely not negligible!).

2) You write "The reviewer's doubts about whether 1/K’ increases monotonically with P/K and the possibility of a conflict with the thermodynamic K’_∞ > 5/3 arise from the problem that these thermodynamic arguments assume a constant stable phase." In fact, my concern arises from my own plotting of the Kurnosov et al. (2017) experimental data on Mg-silicate perovskite at 25--40 GPa. This is already quite high pressure and perovskite was a constant stable phase during the analysis. I'm happy to be convinced that that particular DAC-Brillouin study had issues, and that d(1/K')/d(P/K) does increase monotonically, but it would be good to know how robust this assumption is under lower mantle pressures. Can I point at your paper and say that Kurnosov's experiments must have had problems, for example?

3) Regarding negative pressures (my comment on line 48). I realise that large negative pressures are unphysical; again, it wasn't my intention to state the blindingly obvious. But moderate negative effective pressures (>~ -K_0/K'_0) are required by a large number of thermal equations of state to model HT-LP behaviour via a Mie-Grueneisen thermal pressure term. To repeat my original comment: "It's probably a good idea to mention early that just because a functional form satisfies the infinite pressure constraints, it may do a bad job at low pressures. Also that many thermal EoSes require the isothermal EoS to go to negative pressures. This precludes the use of several isothermal equations of state, for which K' very rapidly increases at negative pressures."

The reason I mention this is that the reciprocal K-prime equation of state falls apart particularly quickly when extrapolated to HT-LP conditions using a MGD term, because the internal energy reaches a point of inflection at a significantly smaller negative pressure than it does using a BM3 EoS.

4) Regarding Equation 2. I would still like to see a reference to papers other than V+Z, 1963. I have little understanding of how Equation 2 is derived, what are the underlying assumptions, or what the parameter "f" means in any of the relevant theories. Presumably the "other, quite different derivations" that you mention in your response to my original review contain this information, so it would be great to cite them here. I don't require an "extended discourse on Free Volume Theory" - just some papers that I can actually access.

5) l.61 A suitable figure would be a plot of the Grueneisen parameter as a function of pressure (or P/K_T, I guess), as predicted from one or two functional forms for K_T(P), and perhaps also with some experimental data. It was just a suggestion to help visualise what the form of Equation 2 implies, and why a constant value of f is reasonable. It's not necessary to address this if you are averse to the idea.

6) Original question: "l.97 How much do these high derivatives tell us about the finite pressure regions that we're interested in? How smoothly do you expect the curves to vary as a function of P/K at high P?"

Your response: "Line 97: Individually these derivatives can tell us nothing. They must be used in pairs because it is ratios of derivatives that constrain an EOS, as in Section 5 of [6]."

Sure, I understand that. To rephrase slightly: How much do the ratios of these high derivatives tell us about the finite pressure regions that we're interested in? How smoothly do observed curves vary as a function of P/K at high P?

7) l.270 "which has been favoured by some shock wave theories (e. g. [23])." ... You responded to this in your original reply, but the manuscript text remains unchanged. Based on your response, would "which has been favoured by some experimental shock wave observations (e. g. [23])." be better?

Ok, I think that's enough. I have other souls to torment!

Author Response

Dear Editor,

My response to Reviewer 2's second report is provided in the attached document.

Minor revisions to the manuscript are included in Track Changes.

Regards,

Frank

 

 

Author Response File: Author Response.pdf