the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 15 Oct 2025
Seasonal influence on post-fire debris flow likelihood after the 2020 Lake Fire
Abstract. The increasing severity of wildfires in Western North America is widely hypothesized to lead to an increased likelihood of post-fire debris flows (PFDF), specifically those triggered by high-intensity rain. PFDF likelihoods are highest in the first year and tend to decrease over time. However, it is not well understood how seasonal variation affects the PFDFs initiation in the years following a fire. Here, we monitored the changes in PFDF likelihood of the 2020 Lake Fire in Southern California over a span of four years using field and satellite observations, together with numerical modeling for a subset of drainage basins. We found that unsaturated hydraulic conductivity increased by an order of magnitude during the dry season as compared to the wet season, significantly reducing the PFDF likelihood. Our simulations show that vegetation cover has a smaller impact on PFDF likelihood as compared to hydraulic conductivity or grain size. This study helps clarify the impacts of hydraulic conductivity, grain size, and vegetation on PFDF due to seasonal variation in these parameters for four years after the fire. We suggest that field measurements and modeling approaches should consider how different climatic and seasonal patterns could influence PFDF several years after fires.
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- RC1: 'Comment on egusphere-2025-4671', Anonymous Referee #1, 11 Nov 2025 reply
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RC2: 'Comment on egusphere-2025-4671', Anonymous Referee #2, 22 Dec 2025
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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:
- 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
- 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.
- 3.4 Numerical modeling inputs. The model used should be described better.
- 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?
- 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?
- 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.
- Line 266 – highly variable rainfall ID threshold among adjacent basins. I can’t find where this variability is shown or quantified.
- 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.
- Line 315 – This statement should be moved in the result section.
- Line 335- 337 – This statement should be moved in the result section.
Figures
- 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.
- 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.
- Figure 5 – The caption is confusing and should be rewritten for clarity.
- Figure 6 – the variables shown are difficult to interpret. Please describe them more clearly in both figure and caption.
- 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
- Table 1 – Year 0 appears to be missing.
- 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”.
- Table 2 - Please correct in the caption 50 with 5.
- Table 4 – Similar to Figure 6, the variables listed need to be explained.
Supplementary material
- Table S2 is very similar to Table 2, why you don’t merge them? Same for Table S3 and Table 3
Citation: https://doi.org/10.5194/egusphere-2025-4671-RC2
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- 1
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.