Two-Phase Thermal Simulation of Matrix Acidization Using the Non-Isothermal Darcy&ndash;Brinkman&ndash;Forchheimer Model

Wu, Yuanqing; Kou, Jisheng

doi:10.5194/egusphere-2025-4800

Preprints

https://doi.org/10.5194/egusphere-2025-4800

Preprints

13 Nov 2025

| 13 Nov 2025

Two-Phase Thermal Simulation of Matrix Acidization Using the Non-Isothermal Darcy–Brinkman–Forchheimer Model

Yuanqing Wu and Jisheng Kou

Abstract. This study presents a comprehensive two-phase thermal model for simulating matrix acidization in porous media using the non-isothermal Darcy–Brinkman–Forchheimer framework. The model integrates multiphase flow, reactive transport, dynamic porosity evolution, and heat transfer, with temperature-dependent reaction kinetics incorporated through an Arrhenius-type formulation. A series of numerical experiments are conducted to investigate the effects of initial matrix temperature, injected acid temperature, and injection velocity on dissolution behavior and wormhole formation. Results show that the initial matrix temperature has minimal influence due to rapid thermal equilibrium, while high acid temperature significantly enhances reaction rates and promote localized wormhole growth. Verification experiments confirm that increasing acid temperature produces effects similar to decreasing injection velocity, as both shift the dissolution pattern from uniform to ramified and wormhole-dominated regimes. These findings offer valuable insights for optimizing acidizing treatments by balancing thermal and hydrodynamic conditions to improve stimulation efficiency.

Received: 30 Sep 2025 – Discussion started: 13 Nov 2025

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Yuanqing Wu and Jisheng Kou

Status: closed

RC1:
'Comment on egusphere-2025-4800', Anonymous Referee #1, 16 Jan 2026
I read the paper with interest. It presents a two-phase (oil and acidizing aqueous solution) thermal Darcy-Brinkman-Forchheimer (DBF) model for matrix acidization, incorporating temperature-dependent reaction kinetics. The related code is made available by the authors, which I did not try to compile and run myself. Key findings are claimed by the authors based on just seven 40x40 computed models with different initial or boundary conditions: the temperature of acid injection significantly affects dissolution patterns, while initial matrix temperature has minimal influence, and the imposed injection velocity plays also a role in shaping the dissolution pattern of the matrix.
Overall, the approach appears to be formally sound; however, in the present state the paper is seriously lacking some context as well as numerical applicability, and I cannot recommend it for publication without major-major revisions and integrations. I therefore recommend rejection prior to re-submission.
The formulation appears sound and it is adequately described too - in the sense that the assumptions and simplifications are clear and evident for the reader familiar with both reactive transport and with multiphase flow. Philosophycally, however, I have to admit that I would never advise to pursue a "global implicit" ADR model in this context, because no matter how complicated the model is made, it will be a very rough oversimplification in terms of chemistry and reactive transport, which are the controlling physical factors here.

Nothing is said about the implied formation matrix dissolved by acid injection. Is it a pure carbonate reservoir intended? What would change if there would be an inert matrix fraction, resisting to the acidification?

L 261: "rectangular matrix measuring 0.1 m × 0.1 m, discretized into a uniform grid of 40 × 40 cells": why has this particular length scale of 4 m been chosen? Anyhow, these numerical models can be taken as proof of concept for the validity of the formulation and of the numerical solution, but I am not convinced that such grid can be useful to depict real systems or draw meaningful conclusions about sensitivity of the process and the independence of the results from initial assumptions. Also, the images appear to be smoothly interpolated, hence misleading: a 40x40 image should be clearly "pixelated".

Line 266: "Porosity is spatially randomized with an average value of 0.18": how? Is it uniform white noise, or gaussian? Which range, which standard deviation? What happens if porosity is considered initially homogeneous?

Figure 1: I do not see any appreciable difference in the three pictures. I believe it is necessary to find some other way to summarize the results, highlighting the negligible effect of temperature. Maybe just picture their differences?

Figure 2-6: Same for Figure 1. At this point, figures 3 to 6 are redundant and the whole 4.1 section can be reduced to 1 figure for the lowest and highest temperatures, a mere proof of the negligible influence of the initial matrix temperature.

Figure 7: things start to be interesting, some effects are visible, but again only qualitatively and not quantitatively. However, from here on basically all color scales for the justaxposed images are not comparable anymore, which is not good scientific practice.

Overall, sections 4.2 and 4.3 stretch the results of two and three different model runs respectively, without any quantification which can be assumed to be transferable (thing such as scale invariance, transferability of results to higher temperature...) or usable otherwise. Moreover, most figures do not actually add anything meaningful to the paper. This is the case for example for figures 10 and 11 (only one among 4 would suffice), but also figures 12 and 14, are they not just the expected consequences of the imposed boundaries?

In my opinion, most of chapter 4 can be removed, hence highlighting the poorness of the presented results.

Generally speaking, the authors completely neglect the abundant literature about the use of Péclet and Damkohler numbers to describe these class of models and the interacting boundary and initial conditions. This is scientifically unacceptable in my opinion. Properly familiarizing with this well known literature - a good starting point would be the Golfier paper, cited by the authors, and following other works referencing it - will also inevitably lead to more convincing design of experiment for the paper. As the manuscript currently is, these are merely nice pictures without real usability.

The Kozeny-Carman relationships should be probably somehow bounded for very small porosity values.

I can go on and list further deficiencies of the present manuscript. Just to name a few which I would have expected:

1. lack of true control simulations, e.g. with initial homogeneous porosity;

2. lack of code efficiency evaluation, things such as required CPU-time for the seven simulation; scaling of the computations with more CPUs (the code is claimed to be parallel) and so on.

These aspects are in my opinion fundamental for the GMD journal and must be properly addressed for consideration

I stress the fact that the posed model - in the sense of equations and possibly their numerical implementation - could really be interesting and worth of publication, but at the moment I see no convincing results.
Citation: https://doi.org/10.5194/egusphere-2025-4800-RC1
- AC1: 'Reply on RC1', Yuanqing Wu, 27 Jan 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC1
RC2:
'Comment on egusphere-2025-4800', Anonymous Referee #2, 29 Apr 2026
The topic is relevant, and the attempt to combine two-phase flow, thermal effects, and DBF momentum balance in one acidizing model is potentially valuable. The manuscript also addresses an important practical issue: how thermal and hydrodynamic conditions influence wormhole formation. However, in its present form, the paper does not yet provide sufficient methodological rigor or numerical evidence to support its claims at the publication level. The most serious issues are the lack of proper verification/validation, insufficient numerical detail, limited quantitative analysis, and several places where the claims are stronger than the presented evidence. For these reasons, I recommend major revision.
Major comments:
1. The manuscript contains a section titled “Verification experiments,” but this does not constitute verification in the numerical sense. Instead, it presents an additional parametric study on the effect of injection velocity. It does not validate the solver against analytical solutions, benchmark problems, experimental data, or previously validated numerical results. I recommend adding a proper verification section after the methodology and before the numerical experiments. This section should demonstrate the validity of the model—either as a whole or for its individual components—by comparison with existing benchmarks or, at a minimum, previously published numerical models.
2. A central weakness of the paper is that the solution procedure is not described with sufficient clarity for reproducibility. The current presentation makes it difficult for readers to understand how the coupled problem is actually solved. This section should explicitly clarify:
whether the coupling strategy is fully implicit (monolithic), sequential implicit, or loosely coupled. From the current description, it appears that a staggered approach is used, which does not fully enforce coupling between the primary variables;

whether any inner (within–time step) iterations are performed;

the convergence criteria adopted;

how nonlinear residuals are defined and monitored;

how boundary conditions are imposed for pressure, saturation, concentration, and temperature;

how stability is influenced by the treatment of thermal source/transport terms (Eq. 8), particularly given the use of explicit discretization, and the rationale for this choice;

the justification for and implementation of upwind discretization for edge saturations and acid concentration.

I also recommend including the fully discretized form of the governing equations (as it appears a finite difference method is employed), along with a clear flowchart of the solution algorithm, to ensure transparency and reproducibility.
3. The paper states that the model can simulate complex field phenomena “with high fidelity” and bridge the gap to practical field applications. This is too strong for a 2D lab-scale numerical demonstration without validation. Similarly, the conclusion section moves quickly toward future field-scale, surrogate-model, and optimization applications, but the present manuscript has not yet demonstrated the reliability required for such extensions. The authors should moderate these claims and more clearly position the work as a methodological step rather than a validated predictive tool.
4. The discussion relies heavily on visual comparisons of porosity, saturation, concentration, streamlines, and temperature fields. The results section would be significantly stronger with quantitative metrics such as the following:
breakthrough time and PVBT versus injection temperature and velocity,

reacted mineral volume,

acid utilization efficiency,

wormhole length, width, branching density, or localization index

At present, the conclusions are plausible, but not quantified to a level expected for a strong modeling paper.
Minor comments
1. The parameter table is informative, but it would benefit from the addition of a column describing the physical meaning of each parameter, as well as references to literature sources or notes on calibration.
2. The section titled “Verification experiments” should be revised. It does not represent verification in the conventional computational science sense; a more appropriate title would be “Additional parametric study” or similar.
3. While the conclusions clearly summarize the results, they should more carefully distinguish between findings that are directly supported by the simulations and those that remain speculative or interpretive.
4. The quality of the figures should be improved to ensure high-resolution output. In addition, some figure titles appear to be inaccurate and should be corrected for clarity and consistency.
Citation: https://doi.org/10.5194/egusphere-2025-4800-RC2
- AC1: 'Reply on RC1', Yuanqing Wu, 27 Jan 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC1
- AC2: 'Reply on RC2', Yuanqing Wu, 09 May 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC2

Status: closed

RC1:
'Comment on egusphere-2025-4800', Anonymous Referee #1, 16 Jan 2026
I read the paper with interest. It presents a two-phase (oil and acidizing aqueous solution) thermal Darcy-Brinkman-Forchheimer (DBF) model for matrix acidization, incorporating temperature-dependent reaction kinetics. The related code is made available by the authors, which I did not try to compile and run myself. Key findings are claimed by the authors based on just seven 40x40 computed models with different initial or boundary conditions: the temperature of acid injection significantly affects dissolution patterns, while initial matrix temperature has minimal influence, and the imposed injection velocity plays also a role in shaping the dissolution pattern of the matrix.
Overall, the approach appears to be formally sound; however, in the present state the paper is seriously lacking some context as well as numerical applicability, and I cannot recommend it for publication without major-major revisions and integrations. I therefore recommend rejection prior to re-submission.
The formulation appears sound and it is adequately described too - in the sense that the assumptions and simplifications are clear and evident for the reader familiar with both reactive transport and with multiphase flow. Philosophycally, however, I have to admit that I would never advise to pursue a "global implicit" ADR model in this context, because no matter how complicated the model is made, it will be a very rough oversimplification in terms of chemistry and reactive transport, which are the controlling physical factors here.

Nothing is said about the implied formation matrix dissolved by acid injection. Is it a pure carbonate reservoir intended? What would change if there would be an inert matrix fraction, resisting to the acidification?

L 261: "rectangular matrix measuring 0.1 m × 0.1 m, discretized into a uniform grid of 40 × 40 cells": why has this particular length scale of 4 m been chosen? Anyhow, these numerical models can be taken as proof of concept for the validity of the formulation and of the numerical solution, but I am not convinced that such grid can be useful to depict real systems or draw meaningful conclusions about sensitivity of the process and the independence of the results from initial assumptions. Also, the images appear to be smoothly interpolated, hence misleading: a 40x40 image should be clearly "pixelated".

Line 266: "Porosity is spatially randomized with an average value of 0.18": how? Is it uniform white noise, or gaussian? Which range, which standard deviation? What happens if porosity is considered initially homogeneous?

Figure 1: I do not see any appreciable difference in the three pictures. I believe it is necessary to find some other way to summarize the results, highlighting the negligible effect of temperature. Maybe just picture their differences?

Figure 2-6: Same for Figure 1. At this point, figures 3 to 6 are redundant and the whole 4.1 section can be reduced to 1 figure for the lowest and highest temperatures, a mere proof of the negligible influence of the initial matrix temperature.

Figure 7: things start to be interesting, some effects are visible, but again only qualitatively and not quantitatively. However, from here on basically all color scales for the justaxposed images are not comparable anymore, which is not good scientific practice.

Overall, sections 4.2 and 4.3 stretch the results of two and three different model runs respectively, without any quantification which can be assumed to be transferable (thing such as scale invariance, transferability of results to higher temperature...) or usable otherwise. Moreover, most figures do not actually add anything meaningful to the paper. This is the case for example for figures 10 and 11 (only one among 4 would suffice), but also figures 12 and 14, are they not just the expected consequences of the imposed boundaries?

In my opinion, most of chapter 4 can be removed, hence highlighting the poorness of the presented results.

Generally speaking, the authors completely neglect the abundant literature about the use of Péclet and Damkohler numbers to describe these class of models and the interacting boundary and initial conditions. This is scientifically unacceptable in my opinion. Properly familiarizing with this well known literature - a good starting point would be the Golfier paper, cited by the authors, and following other works referencing it - will also inevitably lead to more convincing design of experiment for the paper. As the manuscript currently is, these are merely nice pictures without real usability.

The Kozeny-Carman relationships should be probably somehow bounded for very small porosity values.

I can go on and list further deficiencies of the present manuscript. Just to name a few which I would have expected:

1. lack of true control simulations, e.g. with initial homogeneous porosity;

2. lack of code efficiency evaluation, things such as required CPU-time for the seven simulation; scaling of the computations with more CPUs (the code is claimed to be parallel) and so on.

These aspects are in my opinion fundamental for the GMD journal and must be properly addressed for consideration

I stress the fact that the posed model - in the sense of equations and possibly their numerical implementation - could really be interesting and worth of publication, but at the moment I see no convincing results.
Citation: https://doi.org/10.5194/egusphere-2025-4800-RC1
- AC1: 'Reply on RC1', Yuanqing Wu, 27 Jan 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC1
RC2:
'Comment on egusphere-2025-4800', Anonymous Referee #2, 29 Apr 2026
The topic is relevant, and the attempt to combine two-phase flow, thermal effects, and DBF momentum balance in one acidizing model is potentially valuable. The manuscript also addresses an important practical issue: how thermal and hydrodynamic conditions influence wormhole formation. However, in its present form, the paper does not yet provide sufficient methodological rigor or numerical evidence to support its claims at the publication level. The most serious issues are the lack of proper verification/validation, insufficient numerical detail, limited quantitative analysis, and several places where the claims are stronger than the presented evidence. For these reasons, I recommend major revision.
Major comments:
1. The manuscript contains a section titled “Verification experiments,” but this does not constitute verification in the numerical sense. Instead, it presents an additional parametric study on the effect of injection velocity. It does not validate the solver against analytical solutions, benchmark problems, experimental data, or previously validated numerical results. I recommend adding a proper verification section after the methodology and before the numerical experiments. This section should demonstrate the validity of the model—either as a whole or for its individual components—by comparison with existing benchmarks or, at a minimum, previously published numerical models.
2. A central weakness of the paper is that the solution procedure is not described with sufficient clarity for reproducibility. The current presentation makes it difficult for readers to understand how the coupled problem is actually solved. This section should explicitly clarify:
whether the coupling strategy is fully implicit (monolithic), sequential implicit, or loosely coupled. From the current description, it appears that a staggered approach is used, which does not fully enforce coupling between the primary variables;

whether any inner (within–time step) iterations are performed;

the convergence criteria adopted;

how nonlinear residuals are defined and monitored;

how boundary conditions are imposed for pressure, saturation, concentration, and temperature;

how stability is influenced by the treatment of thermal source/transport terms (Eq. 8), particularly given the use of explicit discretization, and the rationale for this choice;

the justification for and implementation of upwind discretization for edge saturations and acid concentration.

I also recommend including the fully discretized form of the governing equations (as it appears a finite difference method is employed), along with a clear flowchart of the solution algorithm, to ensure transparency and reproducibility.
3. The paper states that the model can simulate complex field phenomena “with high fidelity” and bridge the gap to practical field applications. This is too strong for a 2D lab-scale numerical demonstration without validation. Similarly, the conclusion section moves quickly toward future field-scale, surrogate-model, and optimization applications, but the present manuscript has not yet demonstrated the reliability required for such extensions. The authors should moderate these claims and more clearly position the work as a methodological step rather than a validated predictive tool.
4. The discussion relies heavily on visual comparisons of porosity, saturation, concentration, streamlines, and temperature fields. The results section would be significantly stronger with quantitative metrics such as the following:
breakthrough time and PVBT versus injection temperature and velocity,

reacted mineral volume,

acid utilization efficiency,

wormhole length, width, branching density, or localization index

At present, the conclusions are plausible, but not quantified to a level expected for a strong modeling paper.
Minor comments
1. The parameter table is informative, but it would benefit from the addition of a column describing the physical meaning of each parameter, as well as references to literature sources or notes on calibration.
2. The section titled “Verification experiments” should be revised. It does not represent verification in the conventional computational science sense; a more appropriate title would be “Additional parametric study” or similar.
3. While the conclusions clearly summarize the results, they should more carefully distinguish between findings that are directly supported by the simulations and those that remain speculative or interpretive.
4. The quality of the figures should be improved to ensure high-resolution output. In addition, some figure titles appear to be inaccurate and should be corrected for clarity and consistency.
Citation: https://doi.org/10.5194/egusphere-2025-4800-RC2
- AC1: 'Reply on RC1', Yuanqing Wu, 27 Jan 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC1
- AC2: 'Reply on RC2', Yuanqing Wu, 09 May 2026
  
  Please see the attachment.
  
  Citation: https://doi.org/10.5194/egusphere-2025-4800-AC2

Yuanqing Wu and Jisheng Kou

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Short summary

Our study shows how heating up acid used in oil recovery can dramatically change the way it dissolves rock underground. While the natural temperature of the rock hardly matters, hotter acid speeds up reactions and carves more efficient flow channels. Interestingly, this has the same effect as slowing down the injection speed. These insights could help the energy industry design smarter treatments to boost oil production while using less acid.


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