the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 01 Jun 2026
Evaluation of angular resolution of the finite volume method on the predicted accuracy of wildfire thermal radiation
Abstract. Thermal radiation is the dominant heat transfer mechanism in wildfires, governing both flame dynamics and fire spread through radiative preheating of unburned fuels. In physics-based wildfire models, the Finite Volume Method (FVM) is widely used to solve the 3D Radiative Transfer Equation. However, a fundamental contradiction exists between the demand for high-fidelity incident radiation predictions and the associated computational overhead. While previous research has predominantly focused on buoyancy-driven flames, this study systematically evaluates the impact of FVM angular resolution on the accuracy of surface incident radiation for both buoyancy-driven and wind-driven fire scenarios. Results show that low-resolution schemes (e.g., 16 azimuthal and 2 zenith angles) suffer from severe "ray effects"—non-physical numerical oscillations—leading to significant local heat flux errors. In calm atmosphere cases, a high resolution of at least 64–12 angles is required to eliminate artifacts and resolve the incident radiation correctly. In wind-driven scenarios where the flame is attached to the surface, the high-intensity radiation zone near the fire source is more tolerant of lower resolutions (e.g., 32-4), though far-field predictions remain sensitive. This research provides critical selection guidelines for angular discretization in wildfire radiation models.
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Status: open (until 23 Sep 2026)
- RC1: 'Comment on egusphere-2026-1903', Anonymous Referee #1, 02 Jul 2026 reply
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RC2: 'Comment on egusphere-2026-1903', Anonymous Referee #2, 14 Sep 2026
reply
General Comments
This manuscript presents a sensitivity study of angular resolution in the so-called finite volume method for two fire configurations. In recent years, there has been some detailed work related to radiation modelling in fire conditions, such as the work coming out of the MaCFP working group (e.g., 10.1016/j.jqsrt.2024.109177). Therefore, this is a highly relevant work and has value to the research community. A rigorous study of the required angular resolution for fires is important. However, this manuscript needs to be revised significantly before it can be accepted.
The two major concerns I have for this current version of the manuscript are the fact that there are no validated reference data available against which this numerical experiment can be judged, and the authors seem to make a highly generalized claim of required angular resolution of the FVM method based on just two cases and a couple of line plots.
Specific comments1. This work focuses on ray effects, and there have been a significant number of studies on ray effects in various configurations over the past several decades. The manuscript would benefit from a very brief background on this. Additionally, some of the references in the introduction do not really point to an original or comprehensive source. For example, on line 32, there is a reference to Nmira et al., 2020 for the non-grey spectral model. While Nmira et al. discuss the non-grey spectral model, I doubt that it can be considered a comprehensive reference to the generic non-grey models used in radiation. Some review papers or even chapters from Modest and Mazumder or Howell et al's textbooks can serve as a more comprehensive reference here. Similarly, Sun et al. (2022) is not really a comprehensive reference for DOM, FVM, or MCRT. The introductory literature review needs to be revised appropriately.
2. The authors seem to simplify all RTE solution methods to the angular decomposition approach. RTE has both spatial and angular dimensions, and the deterministic methods essentially rely on various strategies to decouple the spatial and angular components. Stochastic methods work completely differently. Therefore, describing everything (including Pn and MC methods) as a form of angular discretization is misleading at best. This needs to be clarified and corrected throughout the text.
3. Line 30: "... it needs to solve by linear algebra solvers over many directions...": This is somewhat an incomplete description. For example, for spherical harmonics methods, you do not really have "directions", and it is unclear why or what role linear algebra solvers play in this assessment.
4. Line 32: "For the angular space of the RTE, four methods..." As already mentioned in #2, Categorizing various RTE solvers as simply methods of angular space discretization is arguably misleading.5. Line 46: "CPU time for radiation solvers scales almost linearly...": This cannot be generalized across all RTE solvers. Even if one considers that the authors are referring only to DOM/FVM, the linear scaling will likely break down in the presence of scattering media and/or reflective surfaces. This should be carefully restated. In fact, in Table 1, the runtime more than doubles between 64-4 and 64-8 cases, meaning computational cost does not scale linearly.
6. Lines 56-58: The authors point to an important point about confusing terminology used: DOM and FVM. And later in line 124, they also point to another confusion regarding FVM. For this purpose, I would recommend that they consider choosing the terminology "Finite Angle Method" or "FAM" as proposed by Modest and Mazumder (Radiative heat transfer, 4th Ed.).7. The authors use the phrase "fire flame" repeatedly. What do they actually mean? What is considered a "fire flame"? How is it different from "fire" or "flame"?
8. On line 77, the authors refer to CO2, H2O, and soot as participating media and mention that radiative properties should be obtained from HITEMP. But soot properties are not available in HITEMP.9. In Sec 2.3, more details are required for the cases. For example, what is the fuel used? What are the boundary conditions? What modelling parameters are used in the original reacting flow simulations (the authors cite Sun et al., 2024, but a very brief description of parameters used in the underlying LES work that produced the flow and composition field will be useful)? Is there soot in the domain? If so, what is the level of soot there? etc.
10. Using frozen fields or snapshots to assess radiation models is a valid approach, and such a strategy has been applied in various other works as well. However, it is important that, for such a numerical experiment, a well-validated result is used as a reference. Are there any radiation-related data - numerical or experimental - available that can be used as a reference for this numerical experiment?
11. The authors discuss the temperature and velocity fields of the two cases. The velocity field has no direct relevance to the current study (and the authors sort of allude to that). The velocity field will be relevant for coupled simulations, which is beyond the scope of this work. However, the concentration fields (not just temperature) of participating media are very important, and the authors mention that concentration fields of CO2 and H2O are identical due to the unity Lewis number approximation. I am not convinced that, for a reacting flow, a unity Lewis number means that temperature, CO2, H2O, soot- everything- has the same distribution. This needs to be clarified.12. Are the results based on one single snapshot of the flame? Or are they time-averaged?
13. Lines 174-175: Please mark in Fig. 5 where exactly these three different features (three local maxima?) are seen.14. Lines 176-177: "These three levels of incident radiation correspond to the three levels of vortex structures in Fig. 4." How can the authors be sure that these three levels are related to the three vortex structures?
15. Lines 177-178: "However, this is also physically false and caused by the ray effect in the zenith direction..." How can the authors separate which ray effect is due to zenith angles and which is due to azimuthal angles by looking at the contour on the ground surface?
16. Throughout the results section, for both cases, the authors make their point by looking at the contour plots at the ground surface and two line plots. Any quantitative assessments made on the basis of contour plots should be done with utmost care, as interpretation of colors in contour plots is very subjective. The line plots are better suited for quantitative assessment, but the location of the sampling line can influence the findings strongly. Therefore, the authors need to justify why the two sets of lines were chosen at the locations they indicated as opposed to any other locations. Furthermore, how can the authors make a generalized assessment of the radiation solution just by looking at the incident radiation at these two locations? There is no reference data as to which solution is correct. Additionally, a smooth incident radiation plot at one location does not automatically indicate the correct solution of the radiative source term inside the flame, which can have a critical role in the fire dynamics.
17. Does the spatial resolution of the mesh used in the flow and concentration field not play any role in the ray effect? A discussion on the effect of CFD mesh size on the angular resolution requirement of FVM needs to be presented.18. Fig. 1: Please show the direction of theta and phi
19. Figs. 2-5, 7-9: Please show the coordinate system and spatial scales.
20. Figs. 5 and 9: Please mark the locations where the sampling lines (for Figs. 6 and 10, respectively) are selected.
21. Line 24: What is a "false ray effect"?
22. The discussion related to the computational cost needs to be revised for clarity. First, different cases seem to have been simulated under different parallelization. Therefore, the time presented does not allow for a one-to-one comparison of computational cost. Second, the discussion of memory requirements is confusing, and actual memory usage (in MB, GB, TB, etc.) is needed instead of how many CPUs on each node.
23. There are several typographic and grammatical/editorial mistakes. Please review the entire manuscript to correct those. Below are some examples:
(a) Line 33: There is nothing called "sphere harmonics method" - it is "spherical harmonics method"
(b) Lines 27 and 39 - repeating "However"
(c) Line 44: "... meshes exceeding 2000 rays ..." The authors should be careful about consistent terminology. It seems that they use direction or angles to describe DOM/FVM discretization not rays. The term "ray" is often used in Monte Carlo terminology.
(d) Line 45: "high-resolution accuracy" should be "high accuracy"
(e) Line 106: "chose" should be "chosen".
(f) Line 144: "buoyant driven" should be "buoyancy-driven"
(g) Line 177: "which has not 2 mesh" - this seems like a fragment of a sentence. Please correct this sentence.Please note that this is an incomplete list of such typographic/grammatical/editorial errors. Please review the entire manuscript thoroughly.
Citation: https://doi.org/10.5194/egusphere-2026-1903-RC2
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The manuscript investigates the effect of angular resolution in the finite volume method on predicted surface incident radiation in wildfire radiation modeling. This is a relevant and useful topic, since angular discretization directly affects ray effects, heat-flux accuracy, and computational cost. The authors compare buoyancy-driven and wind-driven fire cases and provide practical recommendations for selecting angular resolution. The objective is clear, and the decoupled radiation-only approach is appropriate for isolating the numerical influence of angular discretization. However, the authors should address following comments before publication:
Major comments:
(1) The manuscript appears to use 64-12 as the reference or converged solution. Please clarify whether this case is truly angular-converged or simply the finest resolution tested. If no finer case was tested, the statement should be softened.
(2) The findings show that buoyancy-driven and wind-driven flames show different sensitivity to angular resolution. The authors should more clearly explain why the attached flame in the wind-driven case is less sensitive near the fire source, whereas the detached and unsteady buoyant flame requires finer angular discretization.
(3) The decoupled approach is reasonable for isolating angular-discretization effects. However, the statement that this strategy does not affect the purpose may be too strong. In fully coupled wildfire spread simulations, radiation can influence fuel preheating, pyrolysis, flame dynamics, and spread rate. This limitation should be stated more carefully.
(4) Tables 1 and 2 provide useful timing and memory information, but the timing trends are not entirely clear. For example, in the windy case, the 48-8 case appears faster than the 40-6 case. The authors should specify whether the reported values are wall-clock time or CPU time, and whether the processor number, decomposition strategy, and solver settings were identical.
Minor comments:
(1) Please define the angular-resolution notation, such as 16-2, 32-4, and 64-12, clearly at first use and in figure captions.
(2) Some conclusions use strong wording such as “ray effects vanish.” Unless a quantitative criterion is provided, it may be better to write “ray effects become visually negligible” or “are substantially reduced.”
(3) The limitation related to non-sooting flames is important and should be mentioned earlier in the methodology, not only in the conclusion.
(4) Several language issues should be corrected, for example: “unburn vegetables” to “unburned vegetation/fuels,” “The chose of numbers” to “The choice of the numbers,” “buoyance driven” to “buoyancy-driven,” and “Keven-Helmholtz” to “Kelvin–Helmholtz.”