the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 19 Feb 2024
The influence of burn severity on dissolved organic carbon concentrations across a stream network differs based on seasonal wetness conditions post-fire
Abstract. Large, high severity wildfires in many regions across the globe have increased concerns about their impacts on carbon cycling in watersheds. Altered sources of carbon and changes in catchment hydrology after wildfire can lead to shifts in dissolved organic carbon concentrations (DOC) in streams, which can have negative impacts on aquatic ecosystem health and downstream drinking water treatment. Despite its importance, post-fire DOC responses remain relatively unconstrained in the literature, and we lack critical knowledge of how burn severity, landscape elements, and climate interact to affect DOC concentrations. To improve our understanding of the impact of burn severity on DOC concentrations, we measured DOC at ~100 sites across a stream network extending upstream, within, and downstream of a large, high severity wildfire in Oregon, USA. We collected samples across the study sub-basin during four distinct seasonal wetness conditions. We used our high spatial resolution data to develop spatial stream network (SSN) models to predict DOC across the stream network and to improve our understanding of the controls on DOC concentrations. Spatially, we found no obvious wildfire signal—instead we observed a pattern of increasing DOC concentrations from the high elevation headwaters to the sub-basin outlet, while the mainstem maintained consistently low DOC concentrations. This suggests that effects from large wildfires may be “averaged” out at higher stream orders and larger spatial scales. With our DOC measurements grouped by burn severity group, we observed a significant decrease in the variability of DOC concentrations in the moderate and high burn severity sub-catchments. However, our SSN models were able to predict decreases in DOC concentrations with increases in burn severity across the stream network. Decreases in DOC concentrations were also highly variable across seasonal wetness conditions, with the greatest (-1.40 to -1.64 mg L-1) decrease in the high severity group during the wetting season. Additionally, our models indicated that in all seasons, baseflow index was more influential in predicting DOC concentrations than burn severity, indicating that groundwater discharge can obscure the impacts of wildfire in a stream network. Overall, our results suggest that landscape characteristics can regulate the DOC response to wildfire. Moreover, our results also indicate that the seasonal timing of sampling can influence the observed response of DOC concentrations to wildfire.
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Notice on discussion status
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Preprint
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The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Journal article(s) based on this preprint
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2024-273', Anonymous Referee #1, 20 Mar 2024
General comments
This well-written and well-considered manuscript set out to explore the variability of stream DOC in both burned and unburned parts of a sub-catchment. The paper builds on a large dataset of streamflow DOC and uses satellite-derived burn severity to explore how burn severity impacts stream DOC at seasonal scales. The main weakness of the paper is that data collection was delayed by > 2 years post-fire. Greater consideration is needed for the delayed onset of sampling, and how this may have altered results. The main strength is that the dataset is extensive (129 sites, repeated collection), allowing for interesting and useful statistics. The paper was an enjoyable read, and I look forward to seeing the revised version.
Ordinarily, I would have reviewed the code, but I saw too late that it was available to the reviewers on the same page were reviewer comments are posted. My apologies that I did not see it in time, and cannot comment on it here.
Specific comments
Without any pre-fire data, some statements become tenuous: e.g. Line 382: Wildfires are known to impact organic matter availability on burned hillslopes and shift hydrologic flow paths… we expected DOC concentrations would be influence…” but you are analysing a post-fire system, in which DOC is already low and buffered by the streamflow. So perhaps you’re too late for the post-fire DOC signal/it is too subtle/it is being confounded by the upstream-downstream gradient?
Is the burn severity in the model a mean burn severity for the whole fire, or the associated burn severity for each collection point? Since the heterogeneity was likely higher than what is resolveable by the satellite products, you could stress-test how you select burn severity, by using different mean burn severities within different radii of each collection point.
The discussion refers to hypotheses (Line 473) which is not clearly stated in the introduction. Please make sure to clearly state any hypotheses in the introduction, or just refer to your clearly defined research questions. This section continues to say that “Hydrologic flow paths would shift to more shallow pathways” during the wet season – is this an over-simplification? Would it instead be that during the wet season the proportion of hydrological flow from more shallow pathways is greater, due to surface runoff and lag in infiltration? Shift implies to me that the contribution from groundwater declines. Suggest rewording to make this clearer.
Line 245: “contrary to expectations, we did not observe…” The fire was in September 2020 but the first sampling happened in November 2022. How long would you expect a signal to persist? The introduction needs to refer to the literature on the persistence of post-fire changes in DOC, so we can understand the potential for the post-fire DOC signal to persist in the landscape.
The consideration of drinking water feels tacked on in the conclusion. As you did not do any characterisation of which compounds make up your DOC, talking about effects on DOC if more recalcitrant types of DOC are formed comes out of nowhere. The discussion does not mention impacts on drinking water at all, and it is only a minor part of the introduction. If this is included to set up further work, it should either be presented more concisely, or the discussion should be expanded to include drinking water and how your results relate to drinking water.
Technical corrections
Line 15: just state the number of sites rather than ~
Line 141: how was severity classified (briefly)?
Figure 1: data sources should be cited within the caption.
Figure 2: define the water year (i.e. from which bracketing months?). The USGS data should have a reference. What synoptic sampling, there are no precipitation data presented? Either here on in an extended figure in the supplement, you should show precip and hydrographs for the 2021 and 2022 water years (with the timing of the fire shown).
Line 167: move the lines from 172 about need to freeze samples for DOC up to line 166, as justification for why samples weren’t frozen.
Line 173: Change ‘doesn’t’ do ‘does not’
Line 201: states seasonal models used same variables as mean models, but line 215 says season was not included in the seasonal models (which is sensible, but need to be clear about what independent variables are used where).
Line 206: since you only used a tail-up model, is this necessary?
Line 215: suggest rewording “checked for model issues” to something like “ensure that the assumptions of linearity, normality, and homoscedasticity were met” (if that is correct)
Line 220: What is the reference for thresholds? Common source of thresholds is Key and Benson (2006), who describe different threshold values to those used here.
Line 266 – how were CIs calculated?
Line 295: define ‘nugget.’ It is used in the text before it is defined in the caption for Table 3.
Line 298 – a caveat should be added in here somewhere about the large standard error of the coefficient values for dNBR, AI, and pH, noting overlap with most other variables.
Figure 3: predicted error is not resolvable at this scale. Suggest plotting the predicted error elsewhere and moving to the supp mat. I don’t think a diverging colour palette is the right choice for this dataset.
Line 363: introducing ‘burn severity thresholds determined by MTBS’ here sounds like a different burn severity index than the dNBR used earlier in the manuscript. From the methods, it looks like there is only one product used? Please clarify.
Figure 7: if possible, could you rearrange either figure 7 or figure 4 so that they match (e.g. colour = burn severity, x axis has antecedent conditions, or vice versa) to allow for better comparison between model and obs.
Line 434: suggest using ‘found’ rather than ‘measured’
Line 436: missing word? Following a wildfire in Alberta?
Line 441: refs should be together in parentheses.
Line 491: Please clarify, increased contributions of DOC from groundwater, or greater contribution of groundwater flow?
Line 492: please rephrase, the ‘while’ sounds like the second clause will disagree, but the second clause supports your statement.
Line 763: Ref should state that this is a preprint.
Line 807: Add URL.
Citation: https://doi.org/10.5194/egusphere-2024-273-RC1 -
AC1: 'Reply on RC1', Katie Wampler, 15 Apr 2024
Thank you for taking the time to provide thoughtful and helpful comments to improve our manuscript. Please find our responses below.
General comments
This well-written and well-considered manuscript set out to explore the variability of stream DOC in both burned and unburned parts of a sub-catchment. The paper builds on a large dataset of streamflow DOC and uses satellite-derived burn severity to explore how burn severity impacts stream DOC at seasonal scales. The main weakness of the paper is that data collection was delayed by > 2 years post-fire. Greater consideration is needed for the delayed onset of sampling, and how this may have altered results. The main strength is that the dataset is extensive (129 sites, repeated collection), allowing for interesting and useful statistics. The paper was an enjoyable read, and I look forward to seeing the revised version.
- Thank you for your comment. It is fairly typical of post-fire research to have delayed sampling, often due to limitations to site access. We agree with the reviewer that greater consideration for the fact that we sampled two years post-fire is an area that could be further explored in terms of potential limitations or influence on the results in the manuscript. We have seen evidence from past research (i.e., Rhoades et al. 2019; Emelko et al., 2016; Niemeyer et al. 2020) that wildfire effects on hydrology and water quality can persist for more than a decade. Additionally, several meta-analyses have found that DOC impacts lasted at least 5 years (Cavaiani et al. 2024; Raoelison et al., 2023; Hampton et al., 2022; Rust et al., 2018)--thus, it was our expectation that the effects from the high severity wildfire in our study would result in substantial long-term effects on water quality. We will include this in our introduction.
- We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Ordinarily, I would have reviewed the code, but I saw too late that it was available to the reviewers on the same page were reviewer comments are posted. My apologies that I did not see it in time, and cannot comment on it here.
Specific comments
Without any pre-fire data, some statements become tenuous: e.g. Line 382: Wildfires are known to impact organic matter availability on burned hillslopes and shift hydrologic flow paths… we expected DOC concentrations would be influence…” but you are analysing a post-fire system, in which DOC is already low and buffered by the streamflow. So perhaps you’re too late for the post-fire DOC signal/it is too subtle/it is being confounded by the upstream-downstream gradient?
- After examining the initial spatial patterns, we used the spatial stream network models to investigate if the signal was too subtle to be observed spatially and if it was being confounded by landscape factors (Figures 6 & 7). In terms of a lack of pre-fire data, while we don’t have pre-fire data, we do have 65 unburned reference control sites across the basin which help us isolate the impact of the wildfire.
- In terms of being too late for the post-fire DOC signal, it is possible that we were too late to observe the post-fire signal, however current wildfire recovery literature suggests that impacts last 5+ years (Cavaiani et al. 2024). We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Is the burn severity in the model a mean burn severity for the whole fire, or the associated burn severity for each collection point? Since the heterogeneity was likely higher than what is resolveable by the satellite products, you could stress-test how you select burn severity, by using different mean burn severities within different radii of each collection point.
- Thank you for catching this, we did not explain how we determined burn severity very clearly. It was determined as the average burn severity (determined by dNBR) across the upstream area for each sampling point. We will clarify this in revision. We did try other methods (i.e,. using the average dNBR for a 100m buffer on either side of the stream, the percentage burned a high severity) but these did not notably influence the results.
The discussion refers to hypotheses (Line 473) which is not clearly stated in the introduction. Please make sure to clearly state any hypotheses in the introduction, or just refer to your clearly defined research questions. This section continues to say that “Hydrologic flow paths would shift to more shallow pathways” during the wet season – is this an over-simplification? Would it instead be that during the wet season the proportion of hydrological flow from more shallow pathways is greater, due to surface runoff and lag in infiltration? Shift implies to me that the contribution from groundwater declines. Suggest rewording to make this clearer.
- As you stated, we would expect that a greater overall proportion of streamflow would come from lateral flow during the wet season (our basins have extremely limited surface runoff). You make a good point that the use of the word “shift” is misleading, we will adjust the wording to remove reference to hypotheses and link to our existing research questions defined in the introduction.
Line 245: “contrary to expectations, we did not observe…” The fire was in September 2020 but the first sampling happened in November 2022. How long would you expect a signal to persist? The introduction needs to refer to the literature on the persistence of post-fire changes in DOC, so we can understand the potential for the post-fire DOC signal to persist in the landscape.
- We agree that this is an area we could further explore and in revision we will include more discussion on post-fire recovery. Past work (i.e. Rhoades et al. 2019) measured fire impacts 14 years post-fire in Colorado while a recent meta analysis found that DOC impacts lasted at least 5 years across North America (Cavaiani et al. 2024). Emelko et al., (2011) quantified elevated DOC >10 years after wildfire in the Rocky Mountains. Niemeyer et al. (2020) was able to identify elevated streamflow >30 years after a wildfire. These are only a few examples–there is evidence that wildfires are a substantial perturbation to the system, which can create effects that persist for decades. As such, it is our expectation that we would observe an effect of wildfire just two years after.
The consideration of drinking water feels tacked on in the conclusion. As you did not do any characterisation of which compounds make up your DOC, talking about effects on DOC if more recalcitrant types of DOC are formed comes out of nowhere. The discussion does not mention impacts on drinking water at all, and it is only a minor part of the introduction. If this is included to set up further work, it should either be presented more concisely, or the discussion should be expanded to include drinking water and how your results relate to drinking water.
- Our aim is to set up future work on DOM character with the conclusion. However, we agree it could be presented more concisely. We will retain mention that wildfire can affect DOM character, impacting its fate (Lines 513-515) and that work in this area can help improve our understanding of post-fire DOM mechanics (Lines 518-520). We will remove additional detail and references to drinking water quality and methods that could be used to investigate this (Lines 515-518, 520-527).
Technical corrections
Line 15: just state the number of sites rather than ~
- We will update the manuscript with the total number of sites sampled (129) instead of using an estimated number in the abstract.
Line 141: how was severity classified (briefly)?
- Burn severity is determined by finding the satellite derived difference in normalized burn ratio (dNBR) from the pre to post-fire period. Burn severity classes are determined by examining thresholds in the data. We will add these details into the manuscript upon revision.
Figure 1: data sources should be cited within the caption.
- Data sources are NLCD 2019, MTBS, and NHD, we will add these to the caption.
Figure 2: define the water year (i.e. from which bracketing months?). The USGS data should have a reference. What synoptic sampling, there are no precipitation data presented? Either here on in an extended figure in the supplement, you should show precip and hydrographs for the 2021 and 2022 water years (with the timing of the fire shown).
- We will replace the words water year with streamflow from Oct. 2022 to Oct. 2023 to be more clear. We will add a reference of the USGS data to the figure caption. We were confused about your comments that “ there are no precipitation data presented”, as precipitation is shown in Figure 2a. We will make sure that the precipitation data is presented as clearly as possible in the figure caption to avoid confusion.
- The synoptic sampling refers to the four sampling campaigns; we will ensure these are clearly presented and the description of the sampling campaigns is clear in the caption.
- We feel that Including an extended figure of precipitation and the hydrographs is outside the scope of our study since we don’t deal with those time periods at all.
Line 167: move the lines from 172 about need to freeze samples for DOC up to line 166, as justification for why samples weren’t frozen.
- We agree the movement of those lines makes more sense as suggested, we will move it up.
Line 173: Change ‘doesn’t’ do ‘does not’
- We will change this word to remove the contraction.
Line 201: states seasonal models used same variables as mean models, but line 215 says season was not included in the seasonal models (which is sensible, but need to be clear about what independent variables are used where).
- Thanks for pointing this out, the seasonal models did not include season. We will alter the text in line 201 to be correct.
Line 206: since you only used a tail-up model, is this necessary?
- We think including explanations of the other types of models is necessary since, while we ended up just using a tail-up model, we tested all three types so it provides context for our results.
Line 215: suggest rewording “checked for model issues” to something like “ensure that the assumptions of linearity, normality, and homoscedasticity were met” (if that is correct)
- Thank you for your suggestion, we agree we could be more clear. We checked our models by examining the residuals and performing leave one out cross validation to ensure that the assumptions of linearity, normality, and homoscedasticity were met. We will add this additional text in the methods section.
Line 220: What is the reference for thresholds? Common source of thresholds is Key and Benson (2006), who describe different threshold values to those used here.
- On line 219 we state the thresholds used were “based on the dNBR thresholds monitoring trends in burn severity used in classifying the burn severity for the Holiday Farm Fire (MTBS Project, 2021).”
- We will edit this sentence to increase clarity that we used the specific thresholds as determined by MTBS for the Holiday Farm wildfire specifically.
Line 266 – how were CIs calculated?
- CI were calculated using the standard errors from the GLMM model. We will edit the methods section to include a more thorough description.
Line 295: define ‘nugget.’ It is used in the text before it is defined in the caption for Table 3.
- You are correct, thank you for catching that, we will include a definition of the nugget (the unexplained variance in the SSN model) where it is first used.
Line 298 – a caveat should be added in here somewhere about the large standard error of the coefficient values for dNBR, AI, and pH, noting overlap with most other variables.
- You make a good point, we will add in text to emphasize the overlapping confidence intervals by adding the text: “However, the confidence intervals for these variables overlap, suggesting uncertainty in the exact order of importance for these variables.”
Figure 3: predicted error is not resolvable at this scale. Suggest plotting the predicted error elsewhere and moving to the supp mat. I don’t think a diverging colour palette is the right choice for this dataset.
- We tried a number of different color palettes for this dataset, the one used was the only one we could find that was colorblind friendly and still allowed for interpretation of the results accurately. If you have specific color palette suggestions we’d happily try them.
- We will remove the predicted error and show the points using a uniform size. As suggested we will create a supplemental figure where the size differences between the points is larger to be more easily interpretable for the standard error.
Line 363: introducing ‘burn severity thresholds determined by MTBS’ here sounds like a different burn severity index than the dNBR used earlier in the manuscript. From the methods, it looks like there is only one product used? Please clarify.
- They are the same, we will edit the text to clarify.
Figure 7: if possible, could you rearrange either figure 7 or figure 4 so that they match (e.g. colour = burn severity, x axis has antecedent conditions, or vice versa) to allow for better comparison between model and obs.
- We can rearrange Figure 7 and match the colors/axis. However, to clarify, these two figures shouldn’t necessarily be compared, they are not presenting the same thing. Figure 4 is the overall DOC across season and severity levels. Figure 7 is presenting the predicted change in DOC only due to wildfire (removing other confounding factors). We will ensure the text/caption makes this clear.
Line 434: suggest using ‘found’ rather than ‘measured’
- We accept this change in word choice from the reviewer.
Line 436: missing word? Following a wildfire in Alberta?
- Thank you for catching that, the reviewer’s suggestion is correct, there was some text missing in that sentence which we will add in during revision.
Line 441: refs should be together in parentheses.
- Thank you for catching that, those references should be together. We will fix it during revision.
Line 491: Please clarify, increased contributions of DOC from groundwater, or greater contribution of groundwater flow?
- Thanks for noting this, that is unclear. They noted increased contributions of groundwater to overall streamflow. We will rephrase this sentence to clarify.
Line 492: please rephrase, the ‘while’ sounds like the second clause will disagree, but the second clause supports your statement.
- Reviewer is correct, we will rephrase this statement.
Line 763: Ref should state that this is a preprint.
- Yes, that was an oversight, we will update the citation.
Line 807: Add URL.
- We will also include the URL for this citation.
Citation: https://doi.org/10.5194/egusphere-2024-273-AC1
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AC1: 'Reply on RC1', Katie Wampler, 15 Apr 2024
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RC2: 'Comment on egusphere-2024-273', Anonymous Referee #2, 21 Mar 2024
This is a review of “The influence of burn severity on dissolved organic carbon concentrations across a stream network differs based on seasonal wetness conditions post-fire” by Wampler et al.
The manuscript analyzes spatial and temporal dynamics of stream DOC concentration in a watershed impacted by extensive wildfire about two years prior to the sampling campaign. The extensive spatial sampling (about 100 sites) allows the inference of landscape attributes affecting DOC concentration and how they vary with watershed wetness condition. The focus variable of the authors, burn severity, has a minor role in predicting DOC concentration.
Overall, the manuscript is very well written, organized and easy to follow. The methods are clear (excepts for few points detailed below) and sound. My few comments are reported below.
The first one is of general character. One obvious limitation of the study is that it comprises samples taken only after the fire. I think that the introduction would benefit from classifying the existing literature depending on whether before/after data were available. This kind of limitation should also surface in the discussion/conclusion. Another potential issue is related to the time elapsed between the wildfire and the data collection. The literature review should discuss more in details the expected duration of the potential impact.
Lines 195-200. Could you please expand on the rationale for the choice of this variable selection procedure? I think I have intuitively understood it, but I would suggest to be more explicit.
Line 381-387 and 506-510. This is a fair account of the results, but I feel that is not effectively summarized in the title. I can understand that the authors are attached to their initial hypothesis, but maybe they could consider changing it.
Line 448. Maybe it is worth noting here that the theoretical expectation for a uniform stream network is that DOC concentration decreases with drainage area due to instream removal (se e.g. https://doi.org/10.1016/j.advwatres.2017.10.009)
MINOR COMMENTS
Table 1. For most variables, it is explicitly reported that the values consider the whole basin area upstream of the point. For the soil variables and the TWI this is not explicitly stated. Please clarify.
Figure 2. Please report the location of the three outlets in Figure 1.
Line 255 (and other places). I think you can omit “OR” after the first occurrence.
Line 394. Delete “rates of”. Hydraulic conductivity is not a rate.
Citation: https://doi.org/10.5194/egusphere-2024-273-RC2 -
AC2: 'Reply on RC2', Katie Wampler, 15 Apr 2024
This is a review of “The influence of burn severity on dissolved organic carbon concentrations across a stream network differs based on seasonal wetness conditions post-fire” by Wampler et al.
- Thank you for taking the time to provide thoughtful and helpful comments to improve our manuscript. Please find our responses below.
The manuscript analyzes spatial and temporal dynamics of stream DOC concentration in a watershed impacted by extensive wildfire about two years prior to the sampling campaign. The extensive spatial sampling (about 100 sites) allows the inference of landscape attributes affecting DOC concentration and how they vary with watershed wetness condition. The focus variable of the authors, burn severity, has a minor role in predicting DOC concentration.
Overall, the manuscript is very well written, organized and easy to follow. The methods are clear (excepts for few points detailed below) and sound. My few comments are reported below.
The first one is of general character. One obvious limitation of the study is that it comprises samples taken only after the fire. I think that the introduction would benefit from classifying the existing literature depending on whether before/after data were available. This kind of limitation should also surface in the discussion/conclusion. Another potential issue is related to the time elapsed between the wildfire and the data collection. The literature review should discuss more in details the expected duration of the potential impact.
- Thank you for your comment. It is fairly typical of post-fire research to have delayed sampling, often due to limitations to site access. We agree with the reviewer that greater consideration for the fact that we sampled two years post-fire is an area that could be further explored in terms of potential limitations or influence on the results in the manuscript. We have seen evidence from past research (i.e., Rhoades et al. 2019; Emelko et al., 2016; Niemeyer et al. 2020) that wildfire effects on hydrology and water quality can persist for more than a decade. Additionally, several meta-analyses have found that DOC impacts lasted at least 5 years (Cavaiani et al. 2024; Raoelison et al., 2023; Hampton et al., 2022; Rust et al., 2018)--thus, it was our expectation that the effects from the high severity wildfire in our study would result in substantial long-term effects on water quality. We will include this in our introduction.
- We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Lines 195-200. Could you please expand on the rationale for the choice of this variable selection procedure? I think I have intuitively understood it, but I would suggest to be more explicit.
- We chose to use the double selection procedure because it is robust, allows more accurate identification of potential confounding variables. Most importantly, the method prevents inflation of the p-values and standard errors for our variable of interest, burn severity. We will add in a few sentences of this justification into the revised manuscript.
Line 381-387 and 506-510. This is a fair account of the results, but I feel that is not effectively summarized in the title. I can understand that the authors are attached to their initial hypothesis, but maybe they could consider changing it.
- One of the key main points of our paper is that the importance of burn severity isn’t constant, but changes across the seasons. Given this, we feel that the title does convey our results, even if we’re not able to incorporate all our main findings into the title. We do plan to remove the words “post-fire” from the title as this is redundant as we’ve already mentioned burn severity.
Line 448. Maybe it is worth noting here that the theoretical expectation for a uniform stream network is that DOC concentration decreases with drainage area due to instream removal (se e.g. https://doi.org/10.1016/j.advwatres.2017.10.009)
- Indeed, as you pointed out we would expect more instream removal leading to lower DOC concentrations at higher stream orders. We will include a statement of this and add the reference from the reviewer in our discussion.
MINOR COMMENTS
Table 1. For most variables, it is explicitly reported that the values consider the whole basin area upstream of the point. For the soil variables and the TWI this is not explicitly stated. Please clarify.
- Thanks for catching this, soil variables and TWI were averaged over the upstream area. We will update the text to reflect this.
Figure 2. Please report the location of the three outlets in Figure 1.
- Thanks for the suggestion, that’s a great idea. We will edit Figure 1 as you suggested.
Line 255 (and other places). I think you can omit “OR” after the first occurrence.
- Thanks for the suggestion, we added it in so that if someone is just scanning through the paper and hasn’t read the methods section they have the information needed to interpret the figure.
Line 394. Delete “rates of”. Hydraulic conductivity is not a rate.
Saturated hydraulic conductivity, Ksat, describes water movement through saturated media, and its units are distance/time. Therefore, we believe our sentence is scientifically correct. However, we recognize that there are many different similar concepts related to Ksat that might cause confusion for readers. Therefore, we will include Ksat into the sentence to increase clarity on what specific parameter the hydraulic conductivity is referencing in this sentence.
Citation: https://doi.org/10.5194/egusphere-2024-273-AC2
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AC2: 'Reply on RC2', Katie Wampler, 15 Apr 2024
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2024-273', Anonymous Referee #1, 20 Mar 2024
General comments
This well-written and well-considered manuscript set out to explore the variability of stream DOC in both burned and unburned parts of a sub-catchment. The paper builds on a large dataset of streamflow DOC and uses satellite-derived burn severity to explore how burn severity impacts stream DOC at seasonal scales. The main weakness of the paper is that data collection was delayed by > 2 years post-fire. Greater consideration is needed for the delayed onset of sampling, and how this may have altered results. The main strength is that the dataset is extensive (129 sites, repeated collection), allowing for interesting and useful statistics. The paper was an enjoyable read, and I look forward to seeing the revised version.
Ordinarily, I would have reviewed the code, but I saw too late that it was available to the reviewers on the same page were reviewer comments are posted. My apologies that I did not see it in time, and cannot comment on it here.
Specific comments
Without any pre-fire data, some statements become tenuous: e.g. Line 382: Wildfires are known to impact organic matter availability on burned hillslopes and shift hydrologic flow paths… we expected DOC concentrations would be influence…” but you are analysing a post-fire system, in which DOC is already low and buffered by the streamflow. So perhaps you’re too late for the post-fire DOC signal/it is too subtle/it is being confounded by the upstream-downstream gradient?
Is the burn severity in the model a mean burn severity for the whole fire, or the associated burn severity for each collection point? Since the heterogeneity was likely higher than what is resolveable by the satellite products, you could stress-test how you select burn severity, by using different mean burn severities within different radii of each collection point.
The discussion refers to hypotheses (Line 473) which is not clearly stated in the introduction. Please make sure to clearly state any hypotheses in the introduction, or just refer to your clearly defined research questions. This section continues to say that “Hydrologic flow paths would shift to more shallow pathways” during the wet season – is this an over-simplification? Would it instead be that during the wet season the proportion of hydrological flow from more shallow pathways is greater, due to surface runoff and lag in infiltration? Shift implies to me that the contribution from groundwater declines. Suggest rewording to make this clearer.
Line 245: “contrary to expectations, we did not observe…” The fire was in September 2020 but the first sampling happened in November 2022. How long would you expect a signal to persist? The introduction needs to refer to the literature on the persistence of post-fire changes in DOC, so we can understand the potential for the post-fire DOC signal to persist in the landscape.
The consideration of drinking water feels tacked on in the conclusion. As you did not do any characterisation of which compounds make up your DOC, talking about effects on DOC if more recalcitrant types of DOC are formed comes out of nowhere. The discussion does not mention impacts on drinking water at all, and it is only a minor part of the introduction. If this is included to set up further work, it should either be presented more concisely, or the discussion should be expanded to include drinking water and how your results relate to drinking water.
Technical corrections
Line 15: just state the number of sites rather than ~
Line 141: how was severity classified (briefly)?
Figure 1: data sources should be cited within the caption.
Figure 2: define the water year (i.e. from which bracketing months?). The USGS data should have a reference. What synoptic sampling, there are no precipitation data presented? Either here on in an extended figure in the supplement, you should show precip and hydrographs for the 2021 and 2022 water years (with the timing of the fire shown).
Line 167: move the lines from 172 about need to freeze samples for DOC up to line 166, as justification for why samples weren’t frozen.
Line 173: Change ‘doesn’t’ do ‘does not’
Line 201: states seasonal models used same variables as mean models, but line 215 says season was not included in the seasonal models (which is sensible, but need to be clear about what independent variables are used where).
Line 206: since you only used a tail-up model, is this necessary?
Line 215: suggest rewording “checked for model issues” to something like “ensure that the assumptions of linearity, normality, and homoscedasticity were met” (if that is correct)
Line 220: What is the reference for thresholds? Common source of thresholds is Key and Benson (2006), who describe different threshold values to those used here.
Line 266 – how were CIs calculated?
Line 295: define ‘nugget.’ It is used in the text before it is defined in the caption for Table 3.
Line 298 – a caveat should be added in here somewhere about the large standard error of the coefficient values for dNBR, AI, and pH, noting overlap with most other variables.
Figure 3: predicted error is not resolvable at this scale. Suggest plotting the predicted error elsewhere and moving to the supp mat. I don’t think a diverging colour palette is the right choice for this dataset.
Line 363: introducing ‘burn severity thresholds determined by MTBS’ here sounds like a different burn severity index than the dNBR used earlier in the manuscript. From the methods, it looks like there is only one product used? Please clarify.
Figure 7: if possible, could you rearrange either figure 7 or figure 4 so that they match (e.g. colour = burn severity, x axis has antecedent conditions, or vice versa) to allow for better comparison between model and obs.
Line 434: suggest using ‘found’ rather than ‘measured’
Line 436: missing word? Following a wildfire in Alberta?
Line 441: refs should be together in parentheses.
Line 491: Please clarify, increased contributions of DOC from groundwater, or greater contribution of groundwater flow?
Line 492: please rephrase, the ‘while’ sounds like the second clause will disagree, but the second clause supports your statement.
Line 763: Ref should state that this is a preprint.
Line 807: Add URL.
Citation: https://doi.org/10.5194/egusphere-2024-273-RC1 -
AC1: 'Reply on RC1', Katie Wampler, 15 Apr 2024
Thank you for taking the time to provide thoughtful and helpful comments to improve our manuscript. Please find our responses below.
General comments
This well-written and well-considered manuscript set out to explore the variability of stream DOC in both burned and unburned parts of a sub-catchment. The paper builds on a large dataset of streamflow DOC and uses satellite-derived burn severity to explore how burn severity impacts stream DOC at seasonal scales. The main weakness of the paper is that data collection was delayed by > 2 years post-fire. Greater consideration is needed for the delayed onset of sampling, and how this may have altered results. The main strength is that the dataset is extensive (129 sites, repeated collection), allowing for interesting and useful statistics. The paper was an enjoyable read, and I look forward to seeing the revised version.
- Thank you for your comment. It is fairly typical of post-fire research to have delayed sampling, often due to limitations to site access. We agree with the reviewer that greater consideration for the fact that we sampled two years post-fire is an area that could be further explored in terms of potential limitations or influence on the results in the manuscript. We have seen evidence from past research (i.e., Rhoades et al. 2019; Emelko et al., 2016; Niemeyer et al. 2020) that wildfire effects on hydrology and water quality can persist for more than a decade. Additionally, several meta-analyses have found that DOC impacts lasted at least 5 years (Cavaiani et al. 2024; Raoelison et al., 2023; Hampton et al., 2022; Rust et al., 2018)--thus, it was our expectation that the effects from the high severity wildfire in our study would result in substantial long-term effects on water quality. We will include this in our introduction.
- We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Ordinarily, I would have reviewed the code, but I saw too late that it was available to the reviewers on the same page were reviewer comments are posted. My apologies that I did not see it in time, and cannot comment on it here.
Specific comments
Without any pre-fire data, some statements become tenuous: e.g. Line 382: Wildfires are known to impact organic matter availability on burned hillslopes and shift hydrologic flow paths… we expected DOC concentrations would be influence…” but you are analysing a post-fire system, in which DOC is already low and buffered by the streamflow. So perhaps you’re too late for the post-fire DOC signal/it is too subtle/it is being confounded by the upstream-downstream gradient?
- After examining the initial spatial patterns, we used the spatial stream network models to investigate if the signal was too subtle to be observed spatially and if it was being confounded by landscape factors (Figures 6 & 7). In terms of a lack of pre-fire data, while we don’t have pre-fire data, we do have 65 unburned reference control sites across the basin which help us isolate the impact of the wildfire.
- In terms of being too late for the post-fire DOC signal, it is possible that we were too late to observe the post-fire signal, however current wildfire recovery literature suggests that impacts last 5+ years (Cavaiani et al. 2024). We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Is the burn severity in the model a mean burn severity for the whole fire, or the associated burn severity for each collection point? Since the heterogeneity was likely higher than what is resolveable by the satellite products, you could stress-test how you select burn severity, by using different mean burn severities within different radii of each collection point.
- Thank you for catching this, we did not explain how we determined burn severity very clearly. It was determined as the average burn severity (determined by dNBR) across the upstream area for each sampling point. We will clarify this in revision. We did try other methods (i.e,. using the average dNBR for a 100m buffer on either side of the stream, the percentage burned a high severity) but these did not notably influence the results.
The discussion refers to hypotheses (Line 473) which is not clearly stated in the introduction. Please make sure to clearly state any hypotheses in the introduction, or just refer to your clearly defined research questions. This section continues to say that “Hydrologic flow paths would shift to more shallow pathways” during the wet season – is this an over-simplification? Would it instead be that during the wet season the proportion of hydrological flow from more shallow pathways is greater, due to surface runoff and lag in infiltration? Shift implies to me that the contribution from groundwater declines. Suggest rewording to make this clearer.
- As you stated, we would expect that a greater overall proportion of streamflow would come from lateral flow during the wet season (our basins have extremely limited surface runoff). You make a good point that the use of the word “shift” is misleading, we will adjust the wording to remove reference to hypotheses and link to our existing research questions defined in the introduction.
Line 245: “contrary to expectations, we did not observe…” The fire was in September 2020 but the first sampling happened in November 2022. How long would you expect a signal to persist? The introduction needs to refer to the literature on the persistence of post-fire changes in DOC, so we can understand the potential for the post-fire DOC signal to persist in the landscape.
- We agree that this is an area we could further explore and in revision we will include more discussion on post-fire recovery. Past work (i.e. Rhoades et al. 2019) measured fire impacts 14 years post-fire in Colorado while a recent meta analysis found that DOC impacts lasted at least 5 years across North America (Cavaiani et al. 2024). Emelko et al., (2011) quantified elevated DOC >10 years after wildfire in the Rocky Mountains. Niemeyer et al. (2020) was able to identify elevated streamflow >30 years after a wildfire. These are only a few examples–there is evidence that wildfires are a substantial perturbation to the system, which can create effects that persist for decades. As such, it is our expectation that we would observe an effect of wildfire just two years after.
The consideration of drinking water feels tacked on in the conclusion. As you did not do any characterisation of which compounds make up your DOC, talking about effects on DOC if more recalcitrant types of DOC are formed comes out of nowhere. The discussion does not mention impacts on drinking water at all, and it is only a minor part of the introduction. If this is included to set up further work, it should either be presented more concisely, or the discussion should be expanded to include drinking water and how your results relate to drinking water.
- Our aim is to set up future work on DOM character with the conclusion. However, we agree it could be presented more concisely. We will retain mention that wildfire can affect DOM character, impacting its fate (Lines 513-515) and that work in this area can help improve our understanding of post-fire DOM mechanics (Lines 518-520). We will remove additional detail and references to drinking water quality and methods that could be used to investigate this (Lines 515-518, 520-527).
Technical corrections
Line 15: just state the number of sites rather than ~
- We will update the manuscript with the total number of sites sampled (129) instead of using an estimated number in the abstract.
Line 141: how was severity classified (briefly)?
- Burn severity is determined by finding the satellite derived difference in normalized burn ratio (dNBR) from the pre to post-fire period. Burn severity classes are determined by examining thresholds in the data. We will add these details into the manuscript upon revision.
Figure 1: data sources should be cited within the caption.
- Data sources are NLCD 2019, MTBS, and NHD, we will add these to the caption.
Figure 2: define the water year (i.e. from which bracketing months?). The USGS data should have a reference. What synoptic sampling, there are no precipitation data presented? Either here on in an extended figure in the supplement, you should show precip and hydrographs for the 2021 and 2022 water years (with the timing of the fire shown).
- We will replace the words water year with streamflow from Oct. 2022 to Oct. 2023 to be more clear. We will add a reference of the USGS data to the figure caption. We were confused about your comments that “ there are no precipitation data presented”, as precipitation is shown in Figure 2a. We will make sure that the precipitation data is presented as clearly as possible in the figure caption to avoid confusion.
- The synoptic sampling refers to the four sampling campaigns; we will ensure these are clearly presented and the description of the sampling campaigns is clear in the caption.
- We feel that Including an extended figure of precipitation and the hydrographs is outside the scope of our study since we don’t deal with those time periods at all.
Line 167: move the lines from 172 about need to freeze samples for DOC up to line 166, as justification for why samples weren’t frozen.
- We agree the movement of those lines makes more sense as suggested, we will move it up.
Line 173: Change ‘doesn’t’ do ‘does not’
- We will change this word to remove the contraction.
Line 201: states seasonal models used same variables as mean models, but line 215 says season was not included in the seasonal models (which is sensible, but need to be clear about what independent variables are used where).
- Thanks for pointing this out, the seasonal models did not include season. We will alter the text in line 201 to be correct.
Line 206: since you only used a tail-up model, is this necessary?
- We think including explanations of the other types of models is necessary since, while we ended up just using a tail-up model, we tested all three types so it provides context for our results.
Line 215: suggest rewording “checked for model issues” to something like “ensure that the assumptions of linearity, normality, and homoscedasticity were met” (if that is correct)
- Thank you for your suggestion, we agree we could be more clear. We checked our models by examining the residuals and performing leave one out cross validation to ensure that the assumptions of linearity, normality, and homoscedasticity were met. We will add this additional text in the methods section.
Line 220: What is the reference for thresholds? Common source of thresholds is Key and Benson (2006), who describe different threshold values to those used here.
- On line 219 we state the thresholds used were “based on the dNBR thresholds monitoring trends in burn severity used in classifying the burn severity for the Holiday Farm Fire (MTBS Project, 2021).”
- We will edit this sentence to increase clarity that we used the specific thresholds as determined by MTBS for the Holiday Farm wildfire specifically.
Line 266 – how were CIs calculated?
- CI were calculated using the standard errors from the GLMM model. We will edit the methods section to include a more thorough description.
Line 295: define ‘nugget.’ It is used in the text before it is defined in the caption for Table 3.
- You are correct, thank you for catching that, we will include a definition of the nugget (the unexplained variance in the SSN model) where it is first used.
Line 298 – a caveat should be added in here somewhere about the large standard error of the coefficient values for dNBR, AI, and pH, noting overlap with most other variables.
- You make a good point, we will add in text to emphasize the overlapping confidence intervals by adding the text: “However, the confidence intervals for these variables overlap, suggesting uncertainty in the exact order of importance for these variables.”
Figure 3: predicted error is not resolvable at this scale. Suggest plotting the predicted error elsewhere and moving to the supp mat. I don’t think a diverging colour palette is the right choice for this dataset.
- We tried a number of different color palettes for this dataset, the one used was the only one we could find that was colorblind friendly and still allowed for interpretation of the results accurately. If you have specific color palette suggestions we’d happily try them.
- We will remove the predicted error and show the points using a uniform size. As suggested we will create a supplemental figure where the size differences between the points is larger to be more easily interpretable for the standard error.
Line 363: introducing ‘burn severity thresholds determined by MTBS’ here sounds like a different burn severity index than the dNBR used earlier in the manuscript. From the methods, it looks like there is only one product used? Please clarify.
- They are the same, we will edit the text to clarify.
Figure 7: if possible, could you rearrange either figure 7 or figure 4 so that they match (e.g. colour = burn severity, x axis has antecedent conditions, or vice versa) to allow for better comparison between model and obs.
- We can rearrange Figure 7 and match the colors/axis. However, to clarify, these two figures shouldn’t necessarily be compared, they are not presenting the same thing. Figure 4 is the overall DOC across season and severity levels. Figure 7 is presenting the predicted change in DOC only due to wildfire (removing other confounding factors). We will ensure the text/caption makes this clear.
Line 434: suggest using ‘found’ rather than ‘measured’
- We accept this change in word choice from the reviewer.
Line 436: missing word? Following a wildfire in Alberta?
- Thank you for catching that, the reviewer’s suggestion is correct, there was some text missing in that sentence which we will add in during revision.
Line 441: refs should be together in parentheses.
- Thank you for catching that, those references should be together. We will fix it during revision.
Line 491: Please clarify, increased contributions of DOC from groundwater, or greater contribution of groundwater flow?
- Thanks for noting this, that is unclear. They noted increased contributions of groundwater to overall streamflow. We will rephrase this sentence to clarify.
Line 492: please rephrase, the ‘while’ sounds like the second clause will disagree, but the second clause supports your statement.
- Reviewer is correct, we will rephrase this statement.
Line 763: Ref should state that this is a preprint.
- Yes, that was an oversight, we will update the citation.
Line 807: Add URL.
- We will also include the URL for this citation.
Citation: https://doi.org/10.5194/egusphere-2024-273-AC1
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AC1: 'Reply on RC1', Katie Wampler, 15 Apr 2024
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RC2: 'Comment on egusphere-2024-273', Anonymous Referee #2, 21 Mar 2024
This is a review of “The influence of burn severity on dissolved organic carbon concentrations across a stream network differs based on seasonal wetness conditions post-fire” by Wampler et al.
The manuscript analyzes spatial and temporal dynamics of stream DOC concentration in a watershed impacted by extensive wildfire about two years prior to the sampling campaign. The extensive spatial sampling (about 100 sites) allows the inference of landscape attributes affecting DOC concentration and how they vary with watershed wetness condition. The focus variable of the authors, burn severity, has a minor role in predicting DOC concentration.
Overall, the manuscript is very well written, organized and easy to follow. The methods are clear (excepts for few points detailed below) and sound. My few comments are reported below.
The first one is of general character. One obvious limitation of the study is that it comprises samples taken only after the fire. I think that the introduction would benefit from classifying the existing literature depending on whether before/after data were available. This kind of limitation should also surface in the discussion/conclusion. Another potential issue is related to the time elapsed between the wildfire and the data collection. The literature review should discuss more in details the expected duration of the potential impact.
Lines 195-200. Could you please expand on the rationale for the choice of this variable selection procedure? I think I have intuitively understood it, but I would suggest to be more explicit.
Line 381-387 and 506-510. This is a fair account of the results, but I feel that is not effectively summarized in the title. I can understand that the authors are attached to their initial hypothesis, but maybe they could consider changing it.
Line 448. Maybe it is worth noting here that the theoretical expectation for a uniform stream network is that DOC concentration decreases with drainage area due to instream removal (se e.g. https://doi.org/10.1016/j.advwatres.2017.10.009)
MINOR COMMENTS
Table 1. For most variables, it is explicitly reported that the values consider the whole basin area upstream of the point. For the soil variables and the TWI this is not explicitly stated. Please clarify.
Figure 2. Please report the location of the three outlets in Figure 1.
Line 255 (and other places). I think you can omit “OR” after the first occurrence.
Line 394. Delete “rates of”. Hydraulic conductivity is not a rate.
Citation: https://doi.org/10.5194/egusphere-2024-273-RC2 -
AC2: 'Reply on RC2', Katie Wampler, 15 Apr 2024
This is a review of “The influence of burn severity on dissolved organic carbon concentrations across a stream network differs based on seasonal wetness conditions post-fire” by Wampler et al.
- Thank you for taking the time to provide thoughtful and helpful comments to improve our manuscript. Please find our responses below.
The manuscript analyzes spatial and temporal dynamics of stream DOC concentration in a watershed impacted by extensive wildfire about two years prior to the sampling campaign. The extensive spatial sampling (about 100 sites) allows the inference of landscape attributes affecting DOC concentration and how they vary with watershed wetness condition. The focus variable of the authors, burn severity, has a minor role in predicting DOC concentration.
Overall, the manuscript is very well written, organized and easy to follow. The methods are clear (excepts for few points detailed below) and sound. My few comments are reported below.
The first one is of general character. One obvious limitation of the study is that it comprises samples taken only after the fire. I think that the introduction would benefit from classifying the existing literature depending on whether before/after data were available. This kind of limitation should also surface in the discussion/conclusion. Another potential issue is related to the time elapsed between the wildfire and the data collection. The literature review should discuss more in details the expected duration of the potential impact.
- Thank you for your comment. It is fairly typical of post-fire research to have delayed sampling, often due to limitations to site access. We agree with the reviewer that greater consideration for the fact that we sampled two years post-fire is an area that could be further explored in terms of potential limitations or influence on the results in the manuscript. We have seen evidence from past research (i.e., Rhoades et al. 2019; Emelko et al., 2016; Niemeyer et al. 2020) that wildfire effects on hydrology and water quality can persist for more than a decade. Additionally, several meta-analyses have found that DOC impacts lasted at least 5 years (Cavaiani et al. 2024; Raoelison et al., 2023; Hampton et al., 2022; Rust et al., 2018)--thus, it was our expectation that the effects from the high severity wildfire in our study would result in substantial long-term effects on water quality. We will include this in our introduction.
- We will also include discussion of this in the first paragraph of the discussion where we discuss a lack of obvious wildfire impact across the stream network. In addition to the other possible explanations for a lack of signal, we will include that it could also be that we missed any major wildfire response due to the delayed sampling. However, as mentioned above, several studies have found that wildfire effects on DOC exist long past 2 years.
Lines 195-200. Could you please expand on the rationale for the choice of this variable selection procedure? I think I have intuitively understood it, but I would suggest to be more explicit.
- We chose to use the double selection procedure because it is robust, allows more accurate identification of potential confounding variables. Most importantly, the method prevents inflation of the p-values and standard errors for our variable of interest, burn severity. We will add in a few sentences of this justification into the revised manuscript.
Line 381-387 and 506-510. This is a fair account of the results, but I feel that is not effectively summarized in the title. I can understand that the authors are attached to their initial hypothesis, but maybe they could consider changing it.
- One of the key main points of our paper is that the importance of burn severity isn’t constant, but changes across the seasons. Given this, we feel that the title does convey our results, even if we’re not able to incorporate all our main findings into the title. We do plan to remove the words “post-fire” from the title as this is redundant as we’ve already mentioned burn severity.
Line 448. Maybe it is worth noting here that the theoretical expectation for a uniform stream network is that DOC concentration decreases with drainage area due to instream removal (se e.g. https://doi.org/10.1016/j.advwatres.2017.10.009)
- Indeed, as you pointed out we would expect more instream removal leading to lower DOC concentrations at higher stream orders. We will include a statement of this and add the reference from the reviewer in our discussion.
MINOR COMMENTS
Table 1. For most variables, it is explicitly reported that the values consider the whole basin area upstream of the point. For the soil variables and the TWI this is not explicitly stated. Please clarify.
- Thanks for catching this, soil variables and TWI were averaged over the upstream area. We will update the text to reflect this.
Figure 2. Please report the location of the three outlets in Figure 1.
- Thanks for the suggestion, that’s a great idea. We will edit Figure 1 as you suggested.
Line 255 (and other places). I think you can omit “OR” after the first occurrence.
- Thanks for the suggestion, we added it in so that if someone is just scanning through the paper and hasn’t read the methods section they have the information needed to interpret the figure.
Line 394. Delete “rates of”. Hydraulic conductivity is not a rate.
Saturated hydraulic conductivity, Ksat, describes water movement through saturated media, and its units are distance/time. Therefore, we believe our sentence is scientifically correct. However, we recognize that there are many different similar concepts related to Ksat that might cause confusion for readers. Therefore, we will include Ksat into the sentence to increase clarity on what specific parameter the hydraulic conductivity is referencing in this sentence.
Citation: https://doi.org/10.5194/egusphere-2024-273-AC2
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AC2: 'Reply on RC2', Katie Wampler, 15 Apr 2024
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Katie A. Wampler
Kevin D. Bladon
Allison N. Myers-Pigg
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