This manuscript investigates the methodology for incorporating biomass burning emissions within the UK Earth System Model due to their importance on radiation, clouds, and climate. A series of modeling experiments investigated the use of no scaling factor, a doubling of emissions, and a scaling based on the dry matter consumption. AOD from these simulations were compared to observations from AERONET and VIIRS. There are a few concerns with the present version that would warrant major revisions prior to publication. Diurnal cycles can be present in emissions and the AOD, which were neglected in the comparisons between the model simulations and the observations. A daily mean was used for the model, but VIIRS will only have a single observation per day and AERONET will only be representative of cloud-free daytime observations. Better care needs to be taken to ensure these are proper comparisons. It could also be made clearer as to why the authors would recommend using the FIRE_DM approach when the case studies demonstrate that it is not necessarily any better. Finally, the manuscript would benefit from better organization and higher quality figures. More detailed comments are below.

-Line 91: Should the California fires be included with in this sentence? Either way, the sentence is missing “and”.

-Line 111: I do not see how you can distinguish radiative forcing based on the imagery, though I would honestly recommend removing figure 2 and its associated text.

-Line 150: If there are two years of model data, why is only one year shown in the results? Even if there are no extreme fires, wouldn’t the additional data be beneficial for evaluating the weaker fires?

-Line 159: change to “a month of spin up”….”for the period of 2019 through the end of 2020”

-Line 161: reanalysis should be singular

-Line 185: Are biomass burning emissions included for other species in the model (like SO2 and NH3) that can contribute to the total AOD? If so, are they scaled in the same manner as carbon?

-Figure 1/Section 1.3: Consider reducing the length of the text and combining the figure into figure 3, making figure 3 have three panels. These sections are related and the reader would then have already the description for GFED.

-Section 3.2: I am a little confused about the emphasis on the California wildfire event in the section title if the figures show all of the US for the entire month of September 2020.

-Figure 4: Do any of the yellow dots have an inverse gradient that are well below 1 such that it would be better to scale down? And likewise for the purple dots for scaling beyond 2?

-Line 318: observation should be plural

-Section 3.2.1: What is the temporal resolution of the model output? The reason I ask is because there is a potential application of imposing a diurnal cycle on the daily emissions, in addition to expanding the number of data points for the statistics as a one-month sample is rather short.

-Line 349: Is this confirmed with the satellite observations?

-Line 352: Another possibility is vertical placement of the emissions is incorrect, which would then alter the dynamical flow.

-Line 386: Does the figure show the straight up monthly mean AOD or was it subsampled for the availability of VIIRS observations. I am guessing it wasn’t subsampled as the other panels have gray shading (I am assuming) for missing data. It is best to show an apples to apples comparison.

-Figure 7: Why no panel for FIRE_1X?

-Figures 8,  9, and 11: It is not appropriate to use daily mean values here. SNPP has a single snapshot each day.

-Line 427: Typo in VIIRS

-Line 510: Could also be anthropogenics

-Line 553: There is no measure of significance here.

-Line 573-574: should be “due to”

-Figures 14 and 15: Can CERES be added here to give a sense of where these simulations lie with respect to observations?

-Line 603: These are not novel results. If this section is going to remain in the paper, it should cite relevant references that have already shown this.

-Paragraph beginning on Line 625: I do not think it was sufficiently demonstrated that this is the case, particularly because there was no measure of statistical significance showing that the FIRE_DM simulation was any better than FIRE_1X. Another important consideration for the conclusions section is to specify that this is specifically for a period that uses MODIS for fire detections. The footprint for VIIRS is smaller, meaning that smaller background fires can be detected and that these results may not be applicable for future versions of GFED. I recognize this work was likely started prior to the beta release of GFED 5, but nevertheless, the implications should be mentioned.

-Throughout: missing spaces in W m^-2 and g m^-2

-Throughout: The quality of the figures could be improved by using bigger and bolder text and thicker lines for the line plots.

-Consider reorganizing the paper such that the global AOD is discussed first, and then you go into more detail for the other regions, ending with California.

The authors present a novel emission-scaling approach based on daily dry matter (DM) burnt thresholds and evaluate it in the context of the 2020 California wildfires using the UKESM1 atmosphere-only model. The proposed daily-resolution emission framework, combined with a DM-based scaling scheme, aims to correct for under-detected or under-represented extreme fires. The study compares multiple scaling scenarios (1×, 2×, and DM-scaling), evaluates results against satellite and ground-based AOD and CO observations, and analyzes differences in instantaneous radiative forcing (IRF).

The topic is timely and relevant, and the modelling framework is well structured. However, several key aspects of the methodology, interpretation, and physical justification remain underexplained. Some assumptions are insufficiently supported, and the generality of the approach beyond the California case is not convincingly demonstrated. Moreover, while the paper contains extensive quantitative descriptions (AOD values, correlation coefficients, forcing magnitudes), many results are presented descriptively without adequate diagnostic evidence, mechanistic interpretation, or uncertainty assessment. Consequently, the manuscript currently reads more as a compilation of results than as an evidence-driven analysis, making it difficult to assess the robustness of the findings.

I recommend that the authors (a) emphasize the underlying physical insights rather than reiterating numerical values, (b) include uncertainty or statistical significance estimates in key comparisons (e.g., standard deviations, RMSE, or confidence intervals), and (c) strengthen the mechanistic reasoning linking the observed differences to relevant processes (emission strength, plume injection, transport, cloud masking).

I therefore recommend substantial modification before the paper can be considered for publication. Strengthening the physical reasoning behind the emission-scaling scheme, clarifying the interpretation of radiative forcing, and reducing purely descriptive content will greatly enhance the clarity, robustness, and broader scientific relevance of the work.

Major comments:

1. The 2020 California wildfires produced an unusually thick smoke layer, under which MODIS active-fire detection (used in GFED4.1s) can fail to identify ongoing fires. Please clarify whether GFED includes any correction or retrospective burned-area adjustment to account for such obscured fires. If not, this limitation should be acknowledged, as it could partly explain the need for emission-scaling and influence the interpretation of the results.
2. The threshold values for DM (< 50 g m⁻² d⁻¹ scaled by 2×; > 200 g m⁻² d⁻¹ no scaling; linear ramp in between) appear somewhat arbitrary. The authors mention testing other bounds (10–100 and 100–500), but the reasons for selecting 50 and 200 remain vague. I suggest including a sensitivity analysis or at least more transparent rationale (with reference to fire size, detectability, satellite burn‐scar miss‐rate literature) to support threshold choice.
3. The study should discuss whether and how the DM-scaling scheme applies to different fire environments (e.g., savannah, small-patch, or boreal fires) where the relationship between dry-matter burnt and satellite detectability may differ. Clarifying this would help define the scope and limitations of the proposed approach.
4. While the California 2020 case is compelling, especially in the title, the manuscript proposes broader applicability (“global” fire extremes) yet the evaluation across other regions is relatively limited (five regions listed). The performance metrics (e.g., r² ~0.48 for western US) suggest substantial unexplained variance. I recommend adding a table summarizing performance metrics (bias, MAE, correlation) for all regions, and discussing where the method succeeds versus where it struggles. This will help readers assess transferability.
5. The purpose and main conclusion of Section 3.4 are unclear. What is the key message of this section? Are the authors aiming to demonstrate a net cooling or warming effect associated with different emission‐scaling schemes? If so, this needs to be explicitly stated and quantified. Currently, the section reads largely descriptive; a more conclusive statement about whether the DM‐scaling leads to systematically stronger or weaker shortwave (and potentially total) forcing compared to the 1× or 2× runs would clarify its scientific contribution.
6. Throughout Sections 3.2–3.5, the manuscript presents numerous quantitative values (e.g., AOD differences, correlation coefficients, radiative forcing magnitudes) in a largely descriptive manner, without providing sufficient diagnostic or statistical evidence to support the inferred conclusions. For instance, several paragraphs simply report value ranges (“the AOD increases by x%,” “the forcing reaches –2 W m⁻²,” etc.) without explaining the underlying processes, assessing statistical significance, or connecting the numerical differences to physical interpretation.
7. The model uses prescribed vertical injection rather than explicit plume‐rise modeling. For extreme fires, injection height critically impacts aerosol dispersion, lifetime, cloud interactions, and radiative forcing. While the manuscript does not discuss this impact, especially the relative contribution compared to emission scaling. The manuscript would benefit from a sensitivity discussion or diagnostic showing how injection height uncertainties might affect AOD, transport and forcing in the extreme‐fire context. At minimum, this limitation needs to be emphasized in the conclusions with implications for interpretation.
8. The atmosphere‐only modeling framework (fixed SST/sea‐ice) is a limitation for assessing climate‐feedbacks; this should be clearly noted and discussed in the implications.

Specific comments:

1. Abstract: Quantify phrases such as “little overall bias” in AOD to provide a clearer, evidence-based summary.
2. Section 1.3: Define “extreme” or “megafire” explicitly (e.g., > 10 000 ha or > 100 000 ha) and discuss how definitions vary across ecosystems.
3. Figures 5 and 7 (AERONET vs VIIRS): At the Catalina site, all three experiments miss high daily AOD (> 1), yet the monthly bias map shows near-zero bias. This discrepancy could be a color-scaling artifact (~0.4 intervals). Including VIIRS AOD in the Figure 5 time series and adding RMSE/mean-bias metrics to the scatter plots would help clarify consistency between datasets.
4. Figure 5: Explicitly discuss sites with poor model–observation agreement (e.g., negative r²) rather than highlighting only successes.
5. Figure 6: Caption text for panel (c) appears incorrect and should be checked.
6. Figure 7: Consider adding an AOD₁× – AOD_VIIRS difference panel for consistency with Figure 6.
7. Figure 8: Clarify why the FIRE_1× run performs best and what physical explanation underlies this result.
8. Figure 13: The description of surface versus atmospheric components is inaccurate and should be revised.
9. Section 3.5 and Figure 14: The terms “all-sky” and “clear-sky” are used without definition. Please clarify that “all-sky” IRF includes the effects of clouds (both cloudy and clear regions), while “clear-sky” IRF represents forcing under cloud-free conditions only. This clarification will help readers interpret why clear-sky forcing shows stronger cooling.
10. Units and consistency: Ensure units are consistent (e.g., g m⁻² d⁻¹ for dry-matter burnt).
11. Grammar and formatting: Review for minor typographical issues (e.g., “smoke injections” rather than “smoke ejections”) and maintain consistent reference formatting.