Magma ascent mechanisms in the transition regime from solitary porosity waves to diapirism

Dohmen, Janik; Schmeling, Harro

doi:https://doi.org/10.5194/se-12-1549-2021

Articles | Volume 12, issue 7

https://doi.org/10.5194/se-12-1549-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/se-12-1549-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 12, issue 7

Research article

|

06 Jul 2021

Research article |

| 06 Jul 2021

Magma ascent mechanisms in the transition regime from solitary porosity waves to diapirism

Janik Dohmen and Harro Schmeling

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Final revised paper (published on 06 Jul 2021)
Preprint (discussion started on 31 Jul 2020)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

RC1: 'Review on the manuscript “Magma ascent mechanisms in the transition regime from solitary porosity waves to diapirism” by Janik Dohmen and Harro Schmeling', Anonymous Referee #1, 06 Aug 2020
- AC1: 'Response to anonymous referee #1', Janik Dohmen, 23 Oct 2020
RC2: 'Interactive comment on "Magma ascent mechanisms in the transition regime from solitary porosity waves to diapirism" by Janik Dohmen and Harro Schmeling', Anonymous Referee #2, 09 Sep 2020
- AC2: 'Response to anonymous referee #2', Janik Dohmen, 23 Oct 2020

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Janik Dohmen on behalf of the Authors (23 Oct 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (26 Oct 2020) by Taras Gerya

RR by Anonymous Referee #1 (04 Nov 2020)

RR by Anonymous Referee #2 (18 Nov 2020)

Suggestions for revision or reasons for rejection

The submitted revised manuscript by Dohmen and Schmeling systematically investigates magma ascent dynamics in order to capture the transition from the solitary wave regime to diapirism. The authors explore this transition by varying the relative compaction length of the system - here by changing the model extend while keeping the compaction length constant.

The authors addressed majority of the concerns raised during the first round of revisions. However, the new version of the submitted manuscript still suffers from major design issues, both in the content and form. Rather than "time investment and good enough-ness", focus should be on scientific approach and accuracy. To the point, the main story of the manuscript -channelling- is not receivable as such. The authors motivate their revised study by unveiling apparent channelling mechanism occurring while transitioning from the solitary-wave to the Stokes regime. Their argumentation would only be receivable if following a scientific approach, i.e., including more than wishful thinking.

Simple words for simple things; Assuming there is a not yet discovered channelling mechanisms, natural steps would be following: (1) provide a parameter accounting for it; (2) test and report the influence of this parameter in a systematic study; (3) prove the robustness of the suggested results by providing (numerical) convergence tests (physical results should no longer vary with further increase in numerical resolution - proof of a robust numerical implementation) targeting the configuration of interest. To date none of these steps are successfully implemented.

Now, and unless proven otherwise, the underlying equation do not contain any channelling mechanism as such. Thus, the reported channels may rather be the expression of a lack in numerical resolution. This conclusion still confirms the outcome of previous reviews.

Channelling ultimately requires an asymmetry in compaction versus decompaction regimes, obtained upon nonlinear bulk rheology by mechanisms such as e.g., decompaction weakening (Connolly and Podladchikov, 1998; Räss, 2018; Räss, 2019) or brittle failure (Keller, 2013; Yarushina, 2015). Moreover, including the full shear stress tensor for the mixture velocities and total pressure won't produce extra focussing and asymmetry; neither would porosity dependent and even strain-dependent shear rheology. Both may impact the compaction length which may further influence the relative inclusion size, at most.

Finally, the effort spent in providing further insights into the underlying physics and mathematical model (Section 2.1) is very much appreciated. However, this new section reports inconsistent derivations. Equation (3) reports de analogy of the fluid momentum equations as a generalised Darcy law that contains de gradient of the fluid pressure P minus the buoyant fluid force ρfg. Equation (4) reports the total force or momentum balance, where the viscous stresses and total (mixture) pressure P equilibrate the total buoyancy force ρ̄g. The pressure term in equation (3) represents as such the fluid pressure Pf, while the pressure in equation (4) stands for the total pressure Ptot. Equation (10) and line 96 is thus wrong. Fluid pressure ≠ total pressure (Pf≠Ptot) and CANNOT be eliminated.

While the original study needed some revision, the here submitted revised version addresses none of the early design issues. Instead of providing scientifically robust proofs about potential new transient regimes, it further motivates wishful thinking instead of results.

To accept the claims made by the authors about the existence of an intermediate regime leading to flow channelling while transitioning from solitary waves to diapirism, following steps should be included:
1) identification of a physical and testable parameter accounting for focusing
2) systematically testing and reporting of the influence of this physical parameter
3) numerical convergence test to support the robustness of the numerical results (independent of the chosen numerical implementation)

-- Further detailed comments (line numbers refer to the manuscript version 4):
l.9: Not only size but related to compaction length. Size could be kept constant but change in compaction length may lead to similar results

l.19-22: No channels will form. Results seem to report a lack of resolution here. To form channels, one needs an asymmetry in compaction versus decompaction rheology. This asymmetry one does not get with the shear rheology. Including porosity dependence in bulk and shear rheology may induce a change in compaction length but no asymmetry.

l.45-47: It's the same, as compaction length and radius are interconnected. Changing compaction length using Rt may be the same than changing the bulk to shear viscosity ratio, which will ultimately also impact the compaction length.

l.68-72: Boussinesq approximation. There is no need for abbreviation since you only use "BA" twice. Also, the wording could be improved here as it is not very clear in the current form.

---- Section 2.1
Equations (3) and (4) have a pressure issue. How can the same P both be used in the Darcy flow and in the total momentum balance, once relating to fluid density, once relating to total density? Needs revision, modification and clarification.

Minor notation issue: this section could be enhanced with notation homogenisation. Either adopting the ∇ or ∂/∂x notation. Also, some i,j,k may be missing if including those.

---- Section 2.3
What linear and nonlinear absolute and or relative tolerances are used (criterion to stop iteration and accept the current solution before starting the next physical time step)?

---- Results Section:
l.233-234: What is observed in Fig.1a-d is simply the evidence of the problem's internal length scale, the compaction length. Although the initial melt anomaly becomes larger, flow still re-organises within a blob of characteristic size given by the compaction length.

l.244-245: There is no channelling. You may see focusing of melt from an original distribution into a new circular one, but the channels you refer to are numerical artefacts. A model including at least >10 grid points to resolve the channel width will be needed to validate your statement.

l.245-267: If you can both model Stokes and porosity waves, why do you need analytical velocity formulation for your lines in Fig. 2? Basically, Fig. 2 should be obtained by tracking your results, or at least some of those. How does one know whether your results match the curves on Fig. 2? One does not need to run any numerical model to reach your conclusions if they're based upon evaluating semi-analytical solutions from literature.

l.319-325: Be careful with statement. You still do not resolve the small instabilities and those may just be small blobs if properly resolved.

l.339-341: Receivable statement upon successful proof that those are not numerical artefacts.

---- Numerical issues:
As long as no convergence test neither benchmark (available in e.g., the Appendix of Räss (2019) and Keller (2013)) is provided, the reported results, especially channels, could well be under-resolved and thus numerical artefacts.

4.1 channelling: As long as bulk rheology is linear; no literature reports any growth of instabilities besides splitting of original wave into new size owing to dynamical change in compaction length. Richardson (1998) shows minor impact of external stresses on blob's shape, but no channelling as such is presented.

l.404-405: No channelling here, changes in compaction length will change the characteristic diameter of the spherical wave which needs to be resolved.

l.411-414: Unfounded claims. Connolly & Podladchikov (1998) do not suggest following "this upward weakening might not be strong enough to lead to the focusing needed for the nucleation of dykes".

l.422-428: No channelling. As long as there is no asymmetry in viscous compaction versus decompaction, you won't get channels out of blobs. Taking full stress tensor into account and having porosity dependent viscosity will just impact compaction length, nothing else (Räss, 2019).

l.439: "the velocities fit quite nicely to the observed model velocities" where does one sees this? You report analytical solution from other authors and your analytical solutions, but nowhere your modelled results. Since your model includes the stress tensor and velocities, it would be very interesting to report those to support your statement and make them receivable.

l. 447-448: A mechanism needs a testable physical parameter, and a verification that this parameter delivers robust and resolution independent results.

l. 451: (2) see previous comment.

l. 459-463: Good point. Apply it; re-run the suggested simulations with 10 times higher resolutions and longer travel path to convince the reader that you won't get blobs but some real channels being resolved at least with more than 10 grid points.

As of the current state, major revisions are warmly suggested.

-- References
Connolly, J. A. D., & Podladchikov, Y. Y. (1998). Compaction-driven fluid flow in viscoelastic rock. Geodinamica Acta, 11(2-3), 55-84.
https://www.tandfonline.com/doi/abs/10.1080/09853111.1998.11105311

Räss, L., Simon, N. S., & Podladchikov, Y. Y. (2018). Spontaneous formation of fluid escape pipes from subsurface reservoirs. Scientific reports, 8(1), 1-11.
https://www.nature.com/articles/s41598-018-29485-5

Räss, L., Duretz, T., & Podladchikov, Y. Y. (2019). Resolving hydromechanical coupling in two and three dimensions: spontaneous channelling of porous fluids owing to decompaction weakening. Geophysical Journal International, 218(3), 1591-1616.
https://academic.oup.com/gji/article/216/1/365/5140152?casa_token=ffbIm7VK8EsAAAAA:L7LuROOcMXTBgosYEdylrae-1rhNCS2E_kVvfn9aOpM3-LnRn5RFtmHEvvFOLvpPlCRssxARrVVa4Zg

Keller, T., May, D. A., & Kaus, B. J. (2013). Numerical modelling of magma dynamics coupled to tectonic deformation of lithosphere and crust. Geophysical Journal International, 195(3), 1406-1442.
https://academic.oup.com/gji/article-abstract/195/3/1406/2874184

Yarushina, V. M., & Podladchikov, Y. Y. (2015). (De) compaction of porous viscoelastoplastic media: Model formulation. Journal of Geophysical Research: Solid Earth, 120(6), 4146-4170.
https://agupubs.onlinelibrary.wiley.com/doi/abs/10.1002/2014JB011258

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RR by Anonymous Referee #3 (03 Dec 2020)

Suggestions for revision or reasons for rejection

This study focusses on the interesting and relevant question of the trade-off between compaction waves and melt-rich diapirs in partially molten systems of the upper mantle and crust. The topic has been covered in the literature in the past but perhaps there would still be room for a study to systematically investigate the transition between the two well-accepted end-member regimes. However, in my opinion the manuscript in its revised form still suffers from a number of critical flaws that must be addressed fully before publication of the study is advised. The most important issues to be addressed in my view are the following:

- Ratio of length scales as governing model parameter. Previous literature shows clearly that the ratio between the emergent physical length scale, the compaction length (here, "delta"), to the set system length scale (here, "r") is the crucial control on flow regimes between compaction waves and diapirism. If the compaction length is similar or larger than the system length scale, pore fluid segregation is more or similarly rapid than collective flow of both phases as a mixture. Conversely, if the system is much larger than the compaction wave, segregation becomes less relevant and collective flow becomes dominant. Dimensional analysis shows that the square ratio of length scales R = delta^2/r^2 is a dimensionless parameter arising in the governing equations if the system length scale is used to non-dimensionalise length. The parameter in fact arises from taking the ratio of characteristic Darcy and Stokes speeds driven by the buoyancy-contrast between phases (see the recent discussion in Keller & Suckale, GJI, 2019). As this ratio of length scales is at the heart of this study, it is surprising that the authors choose a different, rather more circuitous route in their dimensional analysis of the governing equations. They first introduce the retention number, Rt, not recognising that it is in fact both the ratio of segregation to diapirism speed as well as the square ratio of length scales. Later, apparently as a mere afterthought, the authors bring up the compaction length without putting it into context with their dimensional analysis. They then seek to explain in rather convoluted language how they are varying Rt to obtain an increase in system length scale compared to compaction length. I would regard it as critical to the clarity of their model description and the entire study to instead use a form of dimensional analysis that introduces the governing ratio of length scales clearly from the start and sidesteps the confusing and unnecessary reference to the retention number.

- Numerical benchmarking and resolution testing. One of the main results of this study is the apparent third regime at the transition between compaction waves and diapirism, which the authors characterise as "channelling instability" and discuss in context with rheological melt-shear localisation first introduced by Stevenson (1989). However, as matters stand, the reader can have no confidence that the feature in question is in fact a robust model result rather than a numerical artefact. The numerical setup used in this study is critically flawed. To avoid interactions with boundaries, the domain is 20x larger than the radius of initial perturbations, r. The standard resolution is 200 cells in each direction, meaning r is resolved by 10 grid cells. Unfortunately, the authors then proceed to test parameters where r is roughly equal to or much larger than the compaction length, meaning that in most parameter tests, and notably the ones showing the apparent "channeling instability", the compaction length is not resolved even by one grid step. It would be best practice to present benchmarks of the numerical method against known solutions (or reference published literature if the numerical method has been benchmarked elsewhere). As an absolute minimum requirement, the authors would need to provide a resolution test where it is clear that the solution converges towards a well-resolved geometry, where the compaction length is resolved by at least 8 grid cells. Unfortunately, the authors do not provide either. Nor is it, to my understanding, possible to push the resolution to the necessary levels given the present implementation and model setup.

- Discussion of the apparent "channeling instability". Even if the feature in question be confirmed in well-resolved simulations, its discussion in context of rheological melt-shear channeling remains questionable at best. Previous discussions of channelling instabilities demonstrate that it can arise from strong melt-weakening or non-Newtonian stress-weakening of matrix shear viscosity, decompaction weakening or tensile plastic failure. None of these effects are included in the present model. Therefore it is most likely that the feature in question, if sufficiently well resolved, will turn out to be simply a small compaction wave temporarily escaping ahead of the diapir. However, that would not necessarily be the expected outcome, since the diapir rise speed under the relevant conditions should exceed compaction wave speed. Either way, referring to the feature, if it should persist in revised models, as "channelling instability" is highly misleading.

- Quality of language. The use of language and style in this manuscript falls short of expected standards in international journals. Clear and concise language is important to foster unambiguous udnerstanding. It is highly recommended to have the manuscript edited by a native speaker or professional editing service before resubmission.

Some more detailed comments are given as annotations in the attached PDF file.

Referee Report: PDF

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ED: Reconsider after major revisions (01 Feb 2021) by Taras Gerya

AR by Janik Dohmen on behalf of the Authors (31 Mar 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (01 Apr 2021) by Taras Gerya

RR by Tobias Keller (15 Apr 2021)

Suggestions for revision or reasons for rejection

I would like to thank the authors for thoroughly addressing the issues raised in the previous round of revisions. The revised work now clearly demonstrates that the numerical method produces valid and well-resolved results, introduces a more appropriate dimensional analysis to explain the dominant process regimes, and (mostly) avoids interpretations not clearly supported by the model results. As such, the manuscript is now close to a publishable state.

However, a few issues remain to be addressed.

One of the main concern at this stage is the quality and conciseness of language used throughout. I'm afraid, the text is currently of a quality and style of writing not suitable to publication in an international journal. The instances of incorrect grammar, convoluted and repetitive descriptions, and informal or otherwise inappropriate expressions are too many to usefully point out in detail. I strongly urge the authors to apply thorough copy-editing throughout and in places substantial rewriting to the text.

While the early introduction of the concept of compaction versus diapir length scales and segregation versus collective flow speeds is very welcome, I recommend a general rewrite of the Introduction where the broader context and the specific question or hypothesis of the research are more clearly explained, and where the end-member regimes and their contrasting length and speed scales are more systematically introduced and discussed in light of the literature. At present, the text in some places appears incomplete (e.g., no mention that the research is motivated by partial melt transport in the asthenosphere) and in other places disjointed or oddly sequenced.

I recommend the authors consider condensing some of the lengthy and at times repetitive descriptions and discussion of the results. In a number of instances, the authors repetitively point out features that are clearly visible in the figures without adding more information to the discourse. The clarity of characterisation of regimes between compaction wave- and diapir-dominated is obfuscated by repetitive discussion and unclear or inconsistent terminology. Similar arguments are stated multiple times in different contexts, but no clear and consistent terminology is introduced to characterise the regimes or the main metrics used to characterise them. For example, in one instance the authors refer to the diapirism regime as "the solitary wave composed diapiric uprise regime". I believe it should be possible to rewrite the Results section to condense and clarify the observed model behaviour and the following regime classification using concise descriptions and clear and consistent terminology. It would allow the interesting results to be understood more clearly.

Finally, in the Discussion the authors attempt to argue that larger diapirs will generally break up into trains of smaller compaction waves, and that these could be expressed in pulsating volcanic activity. I'm afraid I find this line of argumentation as it is currently stands entirely implausible. Firstly, the authors fail to clearly discuss that their analysis only applies to porous flow of melt within generally partially molten domains at low melt fraction. Previous work has shown that considering more realistic rheologies (e.g., exponential melt-weakening, non-Newtonian or visco-plastic matrix viscosity, decompaction weakening) all lead to substantial modification of melt transport such that the classical picture of compaction waves versus melt diapirs might not apply at all, or at least not everywhere in the partially molten mantle. These limitations should be clearly pointed out and taken into account when discussing implications. Secondly, there are a number of complex processes at play in transferring melt arriving from mantle melt source into the lower lithosphere to volcanic centres at the surface. The ones that come to my mind are subject to their own time and length scales which will likely buffer out or entirely overprint any periodicity of melt transport in the mantle. In my view it is therefore not plausible that the model results presented here have a direct bearing on observed volcanism at the surface. They may still be relevant for some partially molten domains in the mantle or ductile crust, and that is where I would see the main contribution of this work to our present understanding.

I further point out a number of minor suggested clarifications and corrections in the annotated manuscript attached to this report.

Tobias Keller (Tobias.Keller@glasgow.ac.uk)

Referee Report: PDF

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RR by Anonymous Referee #2 (20 Apr 2021)

Suggestions for revision or reasons for rejection

The submitted revised version of the revised manuscript by Dohmen and Schmeling systematically investigates magma ascent dynamics in order to capture the transition from the solitary wave regime to diapirism. The authors explore this transition by varying the relative compaction length of the system - here by changing the model extent while keeping the compaction length constant.

In this latest revision the authors finally address the study's major early design issue. The current version is scientifically sound and brings some insight on the transition without extensively reporting numerical artefacts.

The current manuscript lacks however in quality regarding the writing style which significantly affects readability. You'll find hereafter some ideas on how to improve it. Another solution would be to get the manuscript revised for language by a professional language service or get some advice from a native speaker.

The author should clarify the pressure issue and elimination discussed between equations (3)-(10). I agree it is not the scope of the paper to sort out the confusion and extra complexity introduced by McKenzie (1984), but the current explanation is not consistent. It would be of great help to the reader to have well defined concepts with clear names referring to that are kept constant throughout the entire manuscript. To this end, it would be appreciated to have a clear definition of what is the melt, the fluid, the effective properties, the mixture and other quantities introduced on a non-systematic basis throughout the paper. Then, once this framework and naming conventions are set, define the pressure as it should. I suspect in the current form the pressure called fluid pressure (and missing the subscript f) may not be the pressure of the pore-fluid but a composite fluid pressure defined by McKenzie.

Based on these considerations, I would recommend this draft for publication after extensive minor revisions (more than just fixing the detailed comments below).

# General comments
Hereafter some ideas and suggestions on how to enhance the writing style applicable to the entire manuscript. Sentences should be kept short and as concise as possible. One way of achieving this is to switch to the active voice wherever it is possible.

Action verbs may also help getting straight to the point; consider using more precise verbs rather than "doing".

The text is populated with too much useless linking words. One possibility to fix this would be to remove all parasite linking words, read through the text, and add them back in places where having them missing would seriously alter the meaning or the logical reasoning.

The text currently includes a lot of familiar "spoken" jargon. Consider removing these or replacing them with more scientific and precise concepts.

Regarding the layout and style, it is considered good practice to have inline equations in the text, preferring horizontal fraction expressions to / for better readability. Also, referring to figures and equations in a passive fashion (e.g. "Our results confirm A (Fig.X)" instead of "Figure X shows that our results confirm A."") may often help to increase flow and readability.

# Specific comments
l.6 Consider capitalising the "Earth" throughout the text

l.8 solitary porosity waves -> Solitary waves of porosity

l.10-11 a mechanism could be dominant, not really a wave or a diapir. Consider a more accurate formulation.

l.16 For enhanced readability I would suggest a full stop after "flux" and starting a new sentence for the melt.

l.37-38 "However, ..." consider simplifying the sentence making it straight to the point.

l.43 "On the other hand" suggests "on the one hand" to appear first. Consider removing unnecessary linking words for enhanced clarity.

l.48 Consider being more precise than "transition looks like" which does not sound very scientific. What interests you in the transition regime ?

l.51 Consider being more factual in this last sentence switching subject from authors to end-member scenarios.

l.54 please refine or clarify the concept of "partially molten scenario".

l.56 "and look especially [at] what happens" doesn't sound very scientific. Consider being more precise and avoid using familiar jargon in a scientific publication.

l.62 Be more specific about "more viscous" -> I suspect you mean feature larger viscosity values, e.g.

l.64-65 "Based on ..." sentence's construction is suboptimal making it hard to get the point. Consider revision for more clarity.

l.66 Consider adding "single phase" to "the Stokes equations" ?

l.72-74 "In the present Boussinesq ..." please rephrase this sentence making the comparison clear.

Section 2.1 Revise usage of fluid and melt. The terminology is mixed up and maybe miss-used in some places in this section, giving the reader hard time to follow the mathematical model formulation.

l.84 If P is the fluid pressure, consider adding the subscript f to it for consistency.

l.85 It is unclear how P, being apparently Pf, would actually include a lithostatic component.

l.86 What is P in the Stokes equation for the mixture, Pf or another pressure ? If P stands for Pf here, it is confusing as this would mean fluid pressure balances the mixture buoyancy forces and shear stresses.

l.88 Eq. (5) is known as Kozeny-Carman relation. Consider stating it and referring to e.g. Costa 2006: Costa, A., 2006. Permeability-porosity relationship: a reexamination of the Kozeny-Carman equation based on a fractal pore-space geometry assumption, Geophys. Res. Lett., 33(2), L02318.

l.88 power-law "n" definition seems missing

l.89 ηf, g and ρ refer to Eq.(4), consider moving these definitions right after the equation they appear in.

l.90 τij is the mixture, solid, total, melt stress tensor ? Please be more precise.

l.94 "simple" does not provide any further information - consider removing it.

l.119-121 Be consistent with the comparison 1 Pa.s - 1e14 Pa.s and then you switch 1e20 Pa.s - 1e16 Pa.s; consider choosing increasing or decreasing values for both.

l.155 Consider rephrasing this sentence to the active voice for more clarity.

l.157 "We can now compare..."

l.157-159 Long and complicated sentence to state something trivial. Consider revising for enhanced clarity.

l.159 Consider replacing familiar expressions with more accurate terms. E.g. "this can be done" -> "we compare the characteristics..."

l.168 Why to have italic text here. Consider clearing formatting or implementing corresponding format to the "diapir limit" text.

l.174 Complete "equ" word

l.190 Consider replacing big by large and spell out what you mean with "the other way around". This sentence could be formulated as a dual comparison in a concise manner.

l.194 Is "Gaussian wave" the most suited terminology for describing your initial condition ? Consider revising it, maybe a "Gaussian profile" or distribution ?

l.199-200 What do you refer to as "model series" ? What do you refer to as "parameter range towards the diapiric regime" ?

l.200-201 what unit is your 201 x 201 model resolution? I suspect it is the number of grid points. Please add it. What does a "high length-scale ratio" stand for ? Consider being more precise.

l.203 "at the top and the bottom" of what ? What about "At the top and bottom domain boundaries we ..."

l.203-205 Be more specific and scientific in the description. Simply state what boundary conditions you implement and for which reason in an active voice.

l.208-209 What does the reader get as add-on value knowing that the lateral BCs are "mirroring" ? Why don't you just state "We enforce no flux horizontal boundary conditions." ?

l.209 The power-law exponent should be defined in Section 2.1 and n=3 could potentially show up there already if it is constant throughout the study.

l.210-214 You implement a moving frame. Could you be more precise or drop the shifting information ? Once ϕmax reaches L/2+dz you shift the entire model down from one dz. But then you repeat this for every next dz travelled by ϕmax ?

l.217-218 What about "We discretise the non-dimensional set of equations (xx-yy) using finite-differences on a staggered? regular? grid and solve the system using the FDCON code (Schmeling et al., 2019)"?

l.250-254 It is motivating to read that benchmarking was carried out. It would be highly appreciated if the statements could be supported by one or two figures in e.g. an Appendix.

l.257-259 This explanation is very helpful to remind the reader about the experiment design.

l.267 I would reformulate the sentence making such as "We compare the observed solitary wave velocities (Fig3b-e) to equivalent Stokes velocities for a diapir based on eq. (15)". Making more concise sentences without decoration words will strengthen your sayings and clarify the text a lot.

l.273-274 "fits quite nicely". Either it fits, or not. If it fits not exactly, select a precise word instead of "quite nice".

l.274-275 Here and in some other paragraphs, avoid using "can". It reads you are not trusting your results or awaiting the reader to approve your claims. It does not read well.

l.315-317 Consider switching this sentence to the active voice and making a linear construct, subject, action verb, complement. Also consider assessing whether "Just in the case" is really needed.

l.345 Consider switching to the active and affirmative voice. Report what you did and not what you think you may have done, e.g. "A quantitative analysis of ...".

l.349-351 "soli" and "dia" not being variables, consider a non-italic font style.

l.369 Scott isn't himself "in the two-phase flow regime". His results suggest it. Consider modifying here and other places in the text where you refer to authors instead of author's results.

l.400 "that rise diapiric as a swarm" -> "that rise as a diapiric swarm".

l.410-415 The work of Keller 2013 may provide some references to you claims

l.416-421 Unclear formulation and complicated sentence construct. Consider revising and simplifying.

l.436 Consider changing the title "Other issues" to "Model limitations" or another positively relevant item. "Other issues" sounds like previous material is already an issue which is not the case.

l.449 Although solitary waves may be observed on non-resolved resolutions, their properties such as velocity would be non accurate.

l.464 What does a and b stand for or refer to ? Please add precision there.

l.472-473 "might be no longer resolved properly" -> "may not be under-resolved to allow for ..."

---

Figure captions:

Fig.2:
"The six panels depict..."
"resolutions" -> "numerical (grid) resolution"

Fig.3:
A general statement of what the figure is about is missing, e.g. "Melt ascent morphology as function of compaction length".
"a) Initial conditions of the model valid for all cases apart of the change in compaction length".
"b-j) Melt fraction distribution after ... for length scale ratios varying between 2.4 and 48."
"k) Diapiric rise resulting from a compaction length of zero."
"l) Models' transition time as function of length scale ratios varying between 1.8 and 120. ..."

Fig.4:
Consider replacing "show" by "refer to"

Fig.5:
"The upper row panels depict..."
"... from left to right, respectively"
"The bottom row panels depict the corresponding ..."

Fig.6:
A general statement of what the figure is about is missing.
"a) Solitary wave (blue) and ..."
"The dashed lines highlight the transition in the regimes."
"b) Ratio of maximum... in the entire model."

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ED: Publish subject to minor revisions (review by editor) (20 Apr 2021) by Taras Gerya

AR by Janik Dohmen on behalf of the Authors (03 May 2021) Author's response Author's tracked changes Manuscript

ED: Publish as is (04 May 2021) by Taras Gerya

ED: Publish as is (06 May 2021) by Susanne Buiter (Executive editor)

AR by Janik Dohmen on behalf of the Authors (06 May 2021)

Short summary

In partially molten regions within the Earth, the melt is able to move separately from the surrounding rocks. This allows for the emergence of so-called solitary porosity waves, driven by compaction and decompaction due to the melt with higher buoyancy. Our numerical models can predict whether a partially molten region will ascend dominated by solitary waves or diapirism. Even in diapiris-dominated regions, solitary waves will build up and ascend as a swarm when the ascend time is long enough.