General comments:

Thank you for this opportunity to review this manuscript. This study details a remote sensing and field-based approach to understanding how post-wildfire debris flow susceptibility changes through time and is subject to seasonal variations following fire in five headwater basins burned in the Lake Fire (2020) located in the Transverse Ranges of southern California, USA. The authors combine information from field visits four years following fire where the authors were able obtain only outlet grain size measurements immediately following the fire (Year 0) and then also obtain grain size and soil hydraulic properties in two visits four years following the fire. In intervening time periods between Year 0 and Year 4, the authors were able to estimate dNDVI using higher-resolution spatiotemporal data from PlanetScope data to assist with estimating vegetation recovery at seasonal timescales and possible surface property changes related to sediment deposits. These data and some assumptions based on similar previous datasets collected in the region (particularly for Year 0 where field data was limited to only grain size) were then used to calibrate a process-based debris-flow likelihood model. From the authors’ modeling approaches their main claims are that grain size and seasonally-variable recovery of hydraulic conductivity were greater controls on debris flow susceptibility than vegetation recovery.

I have many concerns with this study stemming from issues related to basic information on the data presented, likely flawed assumptions, and whether model results (which run contrary to established conceptual understanding of post-fire hazards) can be trusted given a lack of information on presence or absence of debris flows to validate model outputs given the overall low number of ground-based observations (only three observation campaigns over a four-year period). Therefore, I do not believe that this manuscript is ready for publication and opt for a recommendation to reject it in its present form. Below I provide my reasoning based on the information presented in the manuscript and in the event the authors revise for a future resubmission, I also provide additional detailed line comments.

Specific comments:

Potential flaw #1: Unclear if data presented are reliable and possible flawed assumptions

The authors were able to visit the field site a total of three times, in Year 0 immediately following fire and Year 4 in the wet and dry seasons. For each visit, no information is provided about how and what number of sediment samples were taken (i.e. multiple samples, a composite of outlet sediments, landform position?). Also, because soil infiltration properties are extremely variable, it is also important to describe the study design of mini-disk measurements – what is the sample size and spatial coverage of measurements (authors seem to indicate it may be higher up in the watershed given accessibility concerns in Year 0?). For hydraulic conductivity (I’ll herein refer to as Ks – as the authors should also in line with previous literature they cite) – what value is eventually used as an input to the model (e.g., median, mean) and how variable are these values? A mountain of evidence provides information on just how variable this can be (see McGuire et al., 2018 and Ebel, 2022 for some examples). From the standpoint of Ks this becomes important given the finding of its importance in model outputs for these basins from sensitivity testing. Scientific reporting should always include this set of basic information (e.g. summary statistics).

Additionally, there are some assumptions that are potentially flawed: Let’s begin with Year 0, where grain size values were measured at the outlet of the watershed under a shaky assumption that grain size measurements taken at an outlet should be representative of the full distribution of grain sizes from colluvial sources located upstream and reference a study (Santi et al., 2008) that I do not believe makes this claim. Firstly, there is a lot of dry ravel as indicated in Google Earth historical imagery of the site and Figure 2 – Panel A that are common to the Transverse Ranges (see Lamb et al., 2011). Given that field sampling occurred following very limited rainfall and associated runoff (Figure S2) it is very unlikely that a grab sample at the outlet is representative. Runoff events such as a debris flow could act to mix these sources of sediment sources but this did not appear to be the case here (and a judgment of the representativeness of such sampling is also hampered by a lack of information on sample collections indicated above). There is less concern for this particular issue in Year 4 samples following runoff, however, even in the event of a debris flow, there can be large variations in grain size that can occur depending on where sampling takes place – such as very coarse clast-supported deposits such as boulder trains or levees versus more fine-grained poorly-sorted matrix-supported portions of a debris deposit. Also, debris flow deposits can also be reworked by subsequent runoff so this evidence is perishable. Therefore, measurements should account for this depositional variability which is presently not clear in the methods. Other studies have gone beyond this assumption to ensure that d50 measurements are representative through intensive sampling in the watershed (see Tang et al., 2019) but this does not appear to the be case in the present manuscript.

Lastly, the vegetation cover approach also remains concerning to me. Were ground measurements using approaches such as point-intercept surveys ever used to validate satellite-based dNDVI approaches? Given that the original parametrization of the dimensionless-discharge model used ground cover data taken in the field, it might be important to be sure that satellite data can adequately represent this parameter through ground-truthing.

Potential flaw #2: Lack of true validation of debris flow susceptibility modeling

This major comment stems from the fact that the authors seemed to be unable to make unambiguous measurements of runoff response in their basins. Therefore, even with relatively robust field measurements (which is already called into question above), it is difficult to know if the model is adequately representing basin-scale runoff response without independent data on presence or absence of debris flows (or some similar proxy beyond what seems to be ambiguous satellite indices and sparsely-timed field observations). Part of the issue may arise from the fact that rainfall intensity-duration thresholds were never met at all during the study period so it may be that this monitoring experiment was ill-suited to begin with (this is a challenging aspect of post-fire monitoring work where we have little control over what happens with post-fire weather!). The authors do highlight this possibility (of overall low peak rainfall I15) at least, but it does not help the case here.

Additionally, at face value, the authors’ work seems to show debris flow risk sticking around for up to four years, in fact even increasing due to possible seasonal-scale variability in Ks (where drier soils generally, except for Basin A, resulted in large increases in Ks). These findings seem to be contrary to large databases of post-fire debris that find a preicipitous drop in runoff-generated debris flow occurrence 3+ years out from wildfire (see Graber et al., 2023), particularly as vegetation recovery takes hold. Therefore, a suggestion of possible increases in runoff-generated debris-flow risk with increasing time since fire (as this study seems to indicate, e.g. Figure 5) is contrary to many studies and a general conceptual understanding of time evolution of runoff-related post-fire hazards (for example guidance on the USGS M1 model used for emergency assessments does not advise using rainfall ID thresholds beyond Year 2 following fire). Less ambiguous and more well-supported evidence to validate such modeling approaches would be needed here to make such claims, which is especially salient in post-fire hazard science where this work is used to inform decision-making related to public health and safety concerns.

Here are some specific line comments:

Line 50: Tillery and Rengers, 2020 reference – I don’t think this study supports the idea of post-fire debris flow risk persisting 10 years or more following fire, this study looked at adjacent burned vs unburned debris flow initiation mechanisms. I would opt for Graber et al., 2023 instead for a rich discussion of this in addition to DeGraff et al., 2015.

Lines 218-219: “Similarly, we assumed no runoff generated debris flow occurred during this period due to the lack of high-intensity rainfall from our simulations” is an unfortunate choice in phrasing that implies you are only relying off simulated rainfall for making this assumption. I would think it would be better to say based on the identified rainfall-ID threshold of __mm/hr, we found that it was unlikely debris flows were initiated because rainfall values never exceed this threshold (or something similar – needs to be supported by observations).

Line 266: Related to the idea that basin topography could be an important control on rainfall ID threshold variability acorss basins – this could be easily assessed by looking at basic watershed morphology (listing basin mean slopes or channel slope variation for example).  In fact, I would report these somewhere as is standard practice in many post-fire geomorphic studies.

Line 277: Related to the comment about opening macropore spaces in drying soils - but what about the literature that supports dry soils promoting enhanced soil water repellency? (see Ebel & Moody, 2013)

Line 318-320: I’m glad the authors acknowledge this limitation here and something to consider more, especially for the Year 0 sampling where there did not seem to be evidence of debris-flow deposits being sampled.

Lines 321-330: The guesses here about observed shifts in grain size are interesting but I think a more careful consideration of exactly where deposits were taken could help with this. For example, did the authors see evidence of stratification of where deposits were taken (e.g., fines sitting over coarser material supporting theory #2) or inferences type of flows depositing the sediments based on sedimentary characteristics (e.g., debris flow deposits are generally more poorly sorted versus alluvium which is more well-sorted and normally-graded). If such information was recorded in the field, it could help with constraining this and may also help to elucidate concerns brought up earlier related to representativeness of grain size estimates for susceptibility modeling. If not, this is a learning opportunity for the authors to more carefully plan sampling designs and collect this information in the future (as they indicate in the future work statement at the close of the paragraph).

Line 360-361: Variability in rainfall patterns influencing debris flow triggers: what variability type is being referred to here? Spatial or temporal variability? Not really sure how useful this sentence is.

Lines 368-371: I agree here, I think the inferences made from satellite data without ground validation are too generous from satellite data alone (as outlined in major comments).

Line 381: Typo to fix: “larger to not be affected” should read “large enough to not be affected.”

Lines 423-424: Related to the primary succession of grasses: Does your modeling approach of relying on satellite dNDVI account for the growth of these grasses?

Also for some of the figures: I would recommend changing the scale bar to be more legible (i.e. add a white background) as they can be a bit hard to read. 

References cited in this review beyond those cited in study:

Ebel, B. A., & Moody, J. A. (2013). Rethinking infiltration in wildfire-affected soils. Hydrological Processes, 27(10), 1510-1514.

Ebel, B. A. (2022). The statistical power of post-fire soil-hydraulic property studies: Are we collecting sufficient infiltration measurements after wildland fires?. Journal of Hydrology, 612, 128019.

Graber, A. P., Thomas, M. A., & Kean, J. W. (2023). How long do runoff‐generated debris‐flow hazards persist after wildfire?. Geophysical Research Letters, 50(19), e2023GL105101.

Lamb, M. P., Scheingross, J. S., Amidon, W. H., Swanson, E., & Limaye, A. (2011). A model for fire‐induced sediment yield by dry ravel in steep landscapes. Journal of Geophysical Research: Earth Surface, 116(F3).

McGuire, L. A., Rengers, F. K., Kean, J. W., Staley, D. M., & Mirus, B. B. (2018). Incorporating spatially heterogeneous infiltration capacity into hydrologic models with applications for simulating post‐wildfire debris flow initiation. Hydrological Processes, 32(9), 1173-1187.

The study "Seasonal influence on post-fire debris flow likelihood after 2020 Lake Fire" is relevant and interesting, and I support its publication after major revisions, primarily aimed to improve how the information is presented to the reader. I agree that incorporating seasonality in predicting PFDF initiation is important. However, I don’t see this idea developed as it should along this manuscript. In addition, the method section needs to be more descriptive and the results need to be better developed and clearly separated from the discussion. Several results currently appear only in the discussion, and some methodological steps are not clearly explained. The description provided of the model is particularly poor, which prevents me to give a proper assessment of the robustness of the applied methodology.

Below I provide some detailed comments:

1. 3.2 Precipitation records – since the manuscript focuses on how seasonality will improve PFDF prediction, I recommend a better characterization of the precipitation regime for each season. This can include cumulative precipitation, average – max rainfall intensity. In addition, I will clearly define what you mean for wet and dry season
2. 3.3 Differenced Normalized Difference Vegetation Index (NDVI). At line 145, dNDVI is presented as the difference between post and pre. While Table 1 clarifies that pre-images are from the previous year of interest, this may be confusing for the reader. I suggest rephrasing this section to better describe the timing of pre- and post- imagery.
3. 3.4 Numerical modeling inputs. The model used should be described better.
4. Line 179 - You assumed a fractional vegetation cover of 0 immediately after the fire (Year 0). Why not use dNDVI to estimate the vegetation cover for this year as well?
5. Line 249 – it is not clear how these results were obtained. The method section focuses heavily on dNDVI but provides little detail on precipitation intensity analysis. Thus these results are without sufficient methodological context. Is PFDF initiation based only on the intensity? What about rainfall duration? Is seasonality affecting these thresholds?
6. Line 266 – I₁₅ of 80 mm hr^-1 needed to trigger PFDF in the dry season. This value is presented for the first time in the discussion, it should be moved in the result section.
7. Line 266 – highly variable rainfall ID threshold among adjacent basins. I can’t find where this variability is shown or quantified.
8. Line 296-304 - A sensitivity analysis is discussed, but not introduced in the methods or presented in the results section. This makes it difficult to understand how it was performed and which variables are analyzed. All analyses should be described in the methods section and presented in the results sections before introducing them in the discussion.
9. Line 315 – This statement should be moved in the result section.
10. Line 335- 337 – This statement should be moved in the result section.

Figures

1. Figure 3 – I suggest removing the date boxes and instead including the dates directly in each panel title. If you choose to keep the boxes, please clearly explain which dates correspond to pre- and post-fire conditions. Since “pre” and “post” are commonly used to indicate pre- and post-fire periods, alternative wording may reduce confusion. Also, the date box is missing in Figure 3d.
2. Figure 4 – I don’t understand what the small numbers near to watershed outlets represent. Are these median grain sizes? Table 3, referenced in the caption, does not appear to include grain-size information.
3. Figure 5 – The caption is confusing and should be rewritten for clarity.
4. Figure 6 – the variables shown are difficult to interpret. Please describe them more clearly in both figure and caption.
5. Figure 7 – is this figure necessary? It is introduced only in the discussion and appears to be connected with future research rather than this study.

Tables

1. Table 1 – Year 0 appears to be missing.
2. Table 2 – Please clarify whether D50 represent an average? Consider to add “Wet” and “Dry” after the month and year in column “Months since fire”.
3. Table 2 - Please correct in the caption 50 with 5.
4. Table 4 – Similar to Figure 6, the variables listed need to be explained.

Supplementary material

1. Table S2 is very similar to Table 2, why you don’t merge them? Same for Table S3 and Table 3

Seasonal influence on Post-Fire Debris Flow likelihood after the 2020 Lake Fire

EGUsphere (2025-4671)

Authors

Jeng-Hann Chong, Adit Ghosh, Brandon T. Page, Gregory Jesmok, Denise V. Berg, Marlene Lopez, Deepshikha Upadhyay, David J. Stone, Scott C. Hauswirth, Eric O. Lindsey, Louis A. Scuderi

Reviewer Comments

Overall, the manuscript is well written and easy to comprehend. 

The authors apply a hydrologic model to calculate discharge and then convert it into a dimensionless unit discharge.  The dimensionless discharge is then compared to a 15-min dimensionless-discharge rainfall ID threshold.  Input parameters used in the hydrologic model included the use of mini disk infiltrometer data to estimate hydraulic properties of soil, remote-sensed metrics such as NDVI and dNDVI to estimate changes in vegetative cover, and sediment grain size to estimate roughness and control critical Shields number/shear stress used in developing model-derived ID thresholds.  Two main findings reported by the authors include 1) unsaturated hydraulic conductivity increased by an order of magnitude between the wet and dry season four years post fire, suggesting unsaturated hydraulic conductivity is a significant factor in post fire debris flow (PFDF) occurrence, and 2) vegetative cover and grain size provided less influence compared to hydraulic conductivity in controlling PFDF occurrence.

Although the results of this study do show some similarities with other studies, the methods applied lack scientific rigor with the use of only a few data collected in the field to fully test influences of hydraulic conductivity and changes in vegetative cover.  For example, the finding that seasonal variability in unsaturated hydraulic conductivity is a significant factor appears to be based on mini disk infiltrometer measurements taken at the outlet of four basins, with three of the four basins showing an increase in hydraulic conductivity from the wet to dry period.  Mini disk infiltrometer measurements are known to exhibit large variability between measurements at the same location and typically vary spatially across the landscape.  Therefore, relying on just a few values of hydraulic conductivity measured at the outlet of basins is not advised and additional data would be required. 

Moreover, the authors rely on dNDVI to approximate changes in vegetative cover.  NDVI is known to be sensitive to seasonal variations in vegetative cover, largely as a function of vegetive health and the natural cycle of plant growth.  For example, plants actively growing in the spring will have NDVI values approaching 1 compared to the same plants that go dormant and dry out during the late summer.  Thus, NDVI as a sole predictor of vegetative cover is not recommended.  Instead, use of a combination of indices including NDVI, LAI, and vegetative water content has been demonstrated to provide better predictors of vegetative cover, particularly when used to inform hydrologic models (Lahmer et al, 2025; Thomas et al, 2021; Nourani et al., 2017).  Regardless of the remote-sense metrics used, it is important to validate measured values against in-field observations, including vegetative type, density, height, and ground cover.

Based on the limitations and findings contained within this study, it is difficult to except it for publication unless substantially changed.

Please see comments below for additonal context.

Lines 90-102:  The authors describe making field measurements at the outlet of five basins that include taking samples for grain size analyses and performing mini disk infiltrometer measurements.  In reading the text, it appears the sediment samples were taken from the channel and represent sediment that was transported from source areas above.  It also appears the mini disk measurements were performed in the channel adjacent to where the soil samples were collected.  If this is the case, then the mini disk measurements were made on deposits of transported material (e.g. alluvium/colluvium within the channel) and may not be representative of in-situ soils across the basin that would control infiltration and runoff.  A more acceptable approach would have been to conduct far more and spatially dispersed measurements across the basin. 

Additional information on the method applied to perform the grain-size analyses is needed.  For example, were the samples run in the lab using an established method such as ASTM D422?  If so, please state the standard method that was applied. The grain size listed in Table 2 and Figures 3 and 4, suggest grain size with a D50 as low as 0.08mm.  It implies that hydrometer tests were performed to quantify the grain size distribution.  Grain sizes equivalent to silt and clay are not frequently encountered in channels where fluvial process occur.  Such fine grains would dramatically influence the dimensionless discharge and the critical dimensionless discharge used to set the ID rainfall threshold.  Please elaborate.

Please state or reference the standards that were applied in performing the mini disk infiltrometer tests.  If you followed the manufacture’s standards, please state so and include a reference.  Also, please state the suction head applied and if you used a thin layer of silica bedding sand to ensure good contact with the mini disk.   

As discussed, it does not appear more than one measurement was performed at each of the basin outlets for each sampling period.  If this is incorrect, please indicate the number of tests performed and show the results of each test in the supplement.  

Year 0 mini disk measurements were not conducted.  Instead, Year 0 results were assumed by extrapolating results obtained on the Fish Fire.  Additional information justifying the use of values obtained on the Fish Fire should be done.  For example, bedrock type, soil type, slope aspect, slope gradient, pre-fire vegetation, and post-fire soil burn severity should all be shone to be relatively similar to apply the Fish Fire results to the Lake Fire study area. 

Lines 110-113: It is unclear what “15-minute duration threshold” is being referred to here.  Is it the fire-wide USGS I15 threshold of 24mm/hr used to estimate debris flow likelihood?  Or is it basin specific thresholds derived by the USGS assuming a probability of occurrence of 50%.   Or is it basin specific derived using the critical dimensionless discharge model?   If the “threshold” being referred to is associated with the USGS model, then it would only apply for years 0-1, since the USGS model does not predict thresholds after year 1. Also, Table S7 and Figure S2 don’t refer to “thresholds” in the sense of triggering thresholds.  Table S7 simply shows the dates that rainfall exceeded 15mm/hr in 15 minutes and Figure S2 shows peak I15 rainfall events that exceed 20mm/hr.

Section 3.4, starting on Line 158: Additional information is needed to explain the hydrologic model used.  It is understood that the authors applied the Green-Ampt formula for infiltration and Kinematic Wave formula for routing using the program KWAVE (Renger et al., 2016), yet there is a lack of detail on how the models were parameterized.  For example, additional information is needed to explain how saturated hydraulic conductivity, sorptivity, soil porosity, initial soil moisture, infiltration depth, and Mannings # were obtained and used in the hydrologic model.  The list of parameters summarized in Table 2 is insufficient, and the broad generalization of assumed values applied and discussed on lines 190-192 are poorly justified.  See methods section in Tang et al., 2019, and McGurie and Youberg, 2020, for examples how to explain the model and parameterize it.

Lines 190-192: The authors suggest the use of dNDVI to assess vegetative cover and post-storm response, including sediment transport and deposition associated with debris flows.  It is understood that dNDVI can show the location of vegetative-free areas, but to infer flow response, such as flood flow or debris flow, in areas using dNDVI would require field verification.

Results 4.0, starting on Line 194:  It is difficult to understand why the modeled dimensionless discharge have bell-shaped curves with peak discharge occurring at slope angels of about 35 degrees.  Typical plots of dimensionless discharge start low at high slope angles and increase at lower slope angles.  These results are suspect and difficult to rationalize.  Further explanation is needed.

Figure 2: The riparian zone shown in the Dec 2020 photos following fire suggest low burn severity due the lack of consumption and observed intact organic mat on the ground surface in padel (a).  The coarse resolution of the BARC map used by the BAER team likely didn't capture the low burn severity in the mainstem channel and within the lower elevations of the basins.  Because field observations and data were collected only at the basin outlets, near their intersection with the main channel, it is possible the data is biased towards areas of low fire severity and not indicative of conditions located upslope within the basins.  

Figure 3:  In looking at the shades of blue and red in areas outside the burn scar, it appears that seasonal changes in vegetative cover may not have been accounted for and may mislead the interpretation of vegetative recover inside the burn scar using dNDVI.   For example, areas outside the burn perimeter in panel a show no change with the color being light grey to white.  This is expected.  However, panels b, c, d, and e all show some level of change occurring within the unburned areas due to seasonal variations that are likely due to soil/vegetation moisture content or vegetation health.  To correct this, the average observed dNDVI values in unburned areas should be subtracted from the values inside the burned areas. 

Panel d appears to be missing the inset indicating the dates of images used in the differencing analysis.

Please provide units for the D50 grain size. 

Figure 4:  It is relatively apparent that the dNDVI method is a good metric of evaluating vegetative health, but it may not be a good metric to indicate the overall vegetative density and cover present within the basins.  Additional field methods evaluating type and density of vegetative cover present on the hillslopes would be needed to better interpret the dNDVI data. 

Please provide units for the D50 grain size. 

Please refer to Table 2, rather than Table 3, for median grain size.

Figure 5:  Again, the bell-shaped curves depicted in the dimensionless discharge plots against slope are odd and difficult to interpret.  Please provide additional discussion explaining the reason for the shape.   

The red line that represents the modeled critical dimensionless discharge separating flood flow from debris flow does not appear to differ between basins and as recovery occurs.  Is this the case, and if so, can it be explained?  It is expected the critical dimensionless discharge used to set the ID threshold would vary between basins and increase as recovery occurs.

Table 2:  It is difficult to understand why the vegetation cover fraction drops significantly from the wet to dry season.  I suspect this is due to change in soil/vegetation moisture content, suggesting a near complete reduction in vegetative cover between April and September 2024.  This appears unrealistic.  There is likely similar vegetative cover between these reported periods, but the vegetation has gone dormant and dried out in September compared to the earlier April period.  Again, additional field data would be necessary to identify the type and density of vegetative cover in the basins and help interpret the remote-sensed NDVI products.

References Cited not already included in manuscript

Lahmers, T. M., Kumar, S. V., Ahmad, S.K., Holmes, T., Getirana, A., Orland, E.,et al. (2025). An observation‐driven framework for modeling post‐fire hydrologic response: Evaluation for two central California case studies. Water Resources Research, 61, e2023WR036582. https://doi.org/10.1029/2023WR036582

Nourani, V; Fard, AF; Gupta, HV; Goodrich, DC; Niazi, F (2017). Hydrological model parameterization using NDVI values to account for the effects of land cover change on the rainfall-runoff response. HYDROLOGY RESEARCH, 48(6), 1455-1473.

This manuscript addresses an important and interesting aspect of post-fire debris flow (PFDF) science: the seasonal variability of soil hydraulic properties several years after a wildfire. Your finding that hydraulic conductivity can vary by an order of magnitude between wet and dry seasons in the fourth year. The authors are to be commended for generating a rare multi-year field dataset that provides critical quantitative evidence challenging the traditional assumption of monotonic hydrological recovery in post-fire environments.

The central premise of the paper is to track the evolution of debris flow likelihood from Year 0 to Year 4. However, the manuscript explicitly states that for Year 0 and Year 1, the authors did not measure hydraulic conductivity or grain size in situ. Instead, they assumed a constant of 10 mm/hr based on the nearby Fish Fire.

The "Year 0" condition is the most critical and variable baseline. K values immediately post-fire can vary by orders of magnitude depending on burn severity, soil texture, and ash clogging. By assuming the starting point, the entire "recovery trajectory" (the slope of the curve from Year 0 to Year 4) is synthetic. If the true Year 0 K was 20mm/h or 5mm/hr (instead of 10), the conclusions about the rate of recovery would be different.

The modeling results for the Year 4 Wet Season indicate a high likelihood of debris flow initiation. Specifically, the model predicts that Basins A, B, and E would trigger at I15 = 30mm/hr, and Basin D would trigger at just 20mm/hr. The authors note that actual rainfall events did reach intensities matching these thresholds. Crucially, the authors do not explicitly state whether debris flows actually occurred during these Year 4 events. If the model predicted failure at 20mm/hr (Basin D) and rain hit 20mm/h, but no debris flow occurred, this is a Type I error (False Positive).

The study uses dNDVI as a direct proxy for vegetation cover in the model. The authors conclude that vegetation has a minimal influence on PFDF likelihood compared to hydraulic conductivity. The authors need to clarify how dNDVI was converted to the hydraulic parameters in the model.

Your discussion currently relies almost exclusively on examples from the Western United States. This may limit the applicability of your findings. You are suggested to compare your results with recent major PFDF events and studies worldwide, particularly in Southwest China, focusing on the Xichang and Yajiang fires. Your study site is Mediterranean. In contrast, Southwest China (e.g., Hengduan Mountains) experiences a monsoon climate where vegetation recovery is often faster, yet PFDF likelihood remains high due to extreme rainfall intensity. How does your seasonal K variation hypothesis change in a region where soil moisture fluctuations are even more extreme?