We appreciate reviewer 1’s thoughtful comments. In general, we found all of these comments helpful and believed that they would improve the presentation of the work. We have already prepared a revised manuscript that addresses nearly all of these comments, but will go through and briefly respond to each of reviewer 1’s points. 

We agreed with Reviewer 1’s point point regarding Figure 1 and the potential for misinterpretation. We will modify Figure 1 now so that each arc is initialized at a random angle (constrained so that it is fully contained within the range of the inner arc) and include text to safeguard against this misinterpretation. We are aware that direction of spread can influence the amount of area burned and that some portions of the fire will spread faster than others (e.g. headfire versus flank). However, modeling this in our difference equation would pose at least two challenges. Firstly, it would require estimating the (partial) perimeter of an ellipse, for which there is no closed-form equation for. Of course this is certainly possible to do this numerically or by using an approximation, but we believe that the closed-form difference equation solution can be more readily used in future applications and serves as a natural starting point for these kind of future work. Secondly, and I don’t think reviewer 1 would disagree with this point, it is worth mentioning that the solution of the elliptical version of this fire growth model would be dependent on which section of the fire was first extinguished. That is, the duration and size of the fire would be less if the head fire were extinguished on the first day than if the flank were extinguished on the first day. A model of growth that assumes circular fire growth side steps this problem. All models are simplifications of reality, and we believe that (incorrectly) assuming circular fire growth buys (1) an intuitive parameterization of fire growth dynamics and (2) an easy to implement mathematical model that does not require computationally intensive numeric analysis. 

As suggested by reviewer 1, we will include the closed-form solution of the difference equation at the end of section 2 separate from the mathematics that were used to arrive at the solution.  

With regard to the problems associated with land cover changes over time, these are certainly valid. A pixel that was classified as forest land in 2009 could be classified as pasture in 2019, and alternatively an unforested pixel in 2009 may succeed into a forested pixel by 2019. We were unaware of any alternatives to GlobCover when we originally did this analysis and assumed it would adequately, in most cases, characterize the general vegetation class of the burned area, even with the time delay. We maintain that this is a reasonable assumption. Even if a forested pixel became unforested or vice-versa, there should be a fair degree of spatial autocorrelation so that landscape keeps the same general distribution of land classes. Forested landscapes will likely still be forested after a decade, even if certain portions of the landscape become unforested. However, as mentioned earlier these criticisms are valid and we will raise them in the discussion section. Furthermore, as suggested by reviewer 1, we will provide a better description of GlobCover and the nature conservancy data. With respect to forested-unforested simplification that was made, this was mostly made as a convenience since multiple ecoregions were compared that may have different “kinds” of forest. This too will be addressed in the discussion as it is a fair point. 

Similarly, forest structure/composition is certainly important. Eucalyptus plantations and native forest may both be “forest”, but the former is populated by a very-flammable tree species and is likely to produce fire’s that spread at much different rates than the latter. We will discuss this limitation in the discussion and mention this in the introduction when discussing the effects of land cover on fire spread. 

The gamma distribution was selected specifically because it provided a better statistical description of the model parameters than the log-normal (as evidenced by the qq-plots). As I have done in past papers, rather than include the log-normal qq-plots in the article, which will already likely run a bit long once the additional analyses suggested by other reviewers are included, we can provide a footnote letting readers know that we will provide them by request. The choice of inverse-link was made because it was the canonical link-function for the gamma, although other link’s could have been used instead. We felt that attempting to optimize the choice of link function was beyond the scope of this article and would have made the model uncertainty figures (Figure 6) even more difficult to visualize than they already are. We will leave this as an area for future research and discuss this point in the discussion section. 

The suggestions regarding the structure/organization of the paper will be fixed in the revised version. Indeed, the combination of model description and results in one section was a mistake. 

Although possibly a concern if other methods were used, we do not think the correlation of spread rates and extinguish rates will lead to any flawed conclusions from the methods used in this analysis. For example, relative humidity and temperature are highly correlated, but it would not be wrong to build a model that predicted one or the other. We do however understand why, as it is written, this section would be concerning to readers and agree that it can be rewritten with more details explaining why the correlation arises. The statistical correlation is but one factor to consider, and some careful thinking about the mathematical model itself can provide some intuition as to why these two parameters covary. 

The title will be changed to “Estimating the effects of land cover and meteorology on fire growth in Peru using a novel difference equation model” to address reviewer 1’s final point. 

All of the technical comments, where possible, will be addressed in the revised version.

General comments:

1. The manuscript is well written and clearly discusses the materials.
2. The method and calculations are well explained.
3. As constructed, the validity of the approach is uncertain since no validation was attempted.

Thank you for comment 1 and 2. As I wrote for reviewer 3, although we were initially not planning on doing a validation since we envisioned the model fitting exercise as attempting to identify which meteorological/landscape covariates coincided with fire growth, we now see that this would be a prudent idea given the concerns you are raising here. We will include a cross validation section in the revised manuscript.  

4.  Be careful in discerning where your model is giving you insights into fire behavior as opposed to where results are artifacts of the model constraints or assumptions.

This distinction was probably overlooked in the original writing of the manuscript. When revisiting the discussion section we will carefully consider whether the predicted fire behavior is a reflection of real-world relationships or whether it is due to the structure imposed by the difference equation model.    

Specific comments:

The model makes two simplifying assumptions, namely that fire spreads at a constant rate from an ignition point, and that a constant length of the fire’s perimeter is extinguished after the first time step. This is an understandable expediency but how and when these assumptions might lead to erroneous results should be discussed. Basically, what sort of fire behavior or conditions would tend to ‘break’ this model?

This is a good point that will be discussed in the revised manuscript. The simplifying assumption has at least two benefits, (1) it reduces fire growth dynamics into two easily understood parameters and (2) it is mathematically convenient, allowing us to produce a closed-form solution to the difference equation model (this would not have been possible if even just a little more complexity was included in the form of an elliptical spread model). However, these benefits are certainly at the expense of realism (an elliptical fire growth model would clearly be superior and even that is a oversimplification of the growth dynamics of multi-day fires). As state earlier, we will be sure to elaborate about the limitations of these assumptions in the revised manuscript. 

Provide more detail on the burned area product being used. The GlobFire data is derived from a 500m MODIS burned area product.

This will be elaborated upon in the revised manuscript. 

Many fires over many years were used to derive the specific ecoregion models, which is good, but effectively what is developed are average values for each fire. Since daily spread is not examined, it would seem that basically, the final Area (km2) and Duration (days) are used to solve for an average spread rate (r) and fixed amount of perimeter being extinguished. The lack of daily progressions is clearly discussed in the Discussion section but more could be done to 1) support the approach, and 2) explain why it may not work so well for some ecoregions.

1. 1. Why were all the fires used in the parameterization? Generally it would be expected to break into training and validation datasets. This division could be done and analyzed in a number of ways to better understand how well the model(s) are performing. Equally well across fire danger levels? Equally well for each year?
   2. How was the fire danger that was used calculated? From the text, it states that the value on the date and location of the reported ignition was used? Did you look at how much daily variability there was over at least a selection of the fires in each ecoregion? Given the approach, the median or average value for the duration would seem more likely to prove significant. This may be part of the reason why the model fit drops as the duration (and hence area) grows.
   3. It should be noted that the model did fabulously in the Amazon (n = 663), reasonably in the Andean (n=252) and marginally/poorly in the Xeric and Dry Forest (n = 38 and 50). Could performance be sample size driven? That may not be the driving issue but it could be tested to bound the matter.

@1. We will do just that in the revised version. In our response to the general comments, you see what our original thought process was and that your comments led us to evolve on that perspective. 

@2. This is similar to a comment that was raised by reviewer 3. Although we agree that looking at temporal averages may be a superior approach for predicting historical data, we envision at least two practical reasons why we prefer using the ignition date in these models. Firstly, we would prefer to continue to use the fire danger (i.e. ERC, BI, FWI, KBDI, SC) on the ignition date because it is the quantity that can be readily derived for prediction in future applications. That is, in using these models to predict fire danger in say 2024 with new data, we would struggle to use temporal averages over a fire’s lifetime to make predictions from these models because (1) we would not know in advance the duration of a fire and by extension how far into the future forecasted fire danger values would be needed for any given fire, and (2) whether forecasted values would even be feasible and/or reliable over the relevant forecast horizon (although an extreme example, we are unlikely to reliably predict what the 40 day average of the SC might be as would apparently be required in Amazon if temporal aggregates were used). In most cases, fire duration will be fairly short and most fire growth is early in the fire’s lifetime, so fire danger information on the ignition date will be close to when most active growth occurs. Moreover, temporal autocorrelation should be reasonably high. A cursory look at the ACF of the fire danger variables showed that the SC had the weakest temporal autocorrelation, but even that could have detectable/statistically significant autocorrelation 40 days out. A simple analysis showing this temporal autocorrelation could be included as supplementary material. Moreover, if the goodness-of-fit between the model including SC and another that uses or ERC, BI, KBDI, FWI is not too large (as would be estimated from a cross validation procedure) than the robustness of latter models to the uncertainty in the model inputs might justify using them instead.

@3 Extreme values are certainly more likely to occur in smaller data sets (law of small numbers), and this could in part explain why the dry forest and xeric regions had the best/worst performance. This is certainly worth mentioning in the discussion to safeguard against hasty interpretations. 

Given the methods, I understand why single day fires were excluded but where does the 405 hectare limit come from? Is it reasonable to have it be the same in all ecoregions?

The 405 hectare threshold is somewhat arbitrary, other than we wanted to lessen issues regarding detection probabilities. A small fire that would be detected in unforested vegetation might not also be detected in forested vegetation, whereas a large fire is likely to be detected in either forested/unforested vegetation. The 405 threshold itself corresponds to what the Monitoring trends in burn severity project  uses in its data products. Given that reviewer 3 also raised this point, I propose rerunning the analysis twice (once with the 405 threshold once without) to assess the sensitivity of these results to the choice of threshold. I do not envision including this as an additional section of the manuscript, but as a sentence in the discussion where it is mentioned whether this modeling choice does/or doesn’t have an influence on the results. 

Line 162 - “The spread rate and extinguish rate were highly correlated with one another”: Given that they were both calculated from the total area burned and duration of burning, is this a finding or a necessity from the calculations?

We suspect the latter. We found this comment particularly insightful, as we have at times, struggled to explain things like why the extinguish rate would increase with increasing spread rates, when one would think that they should be independent.

Do the median RMSE values for the ecoregions have any independent comparative value? Shouldn’t they be normalized by the median spread rate or fire size for each ecoregion? It is unclear if 0.5 km2 is a large or small error, for example.

This is a good point. Additional, scaled, performance measures should be explored here. (S)MAPE seems like a reasonable choice given relative errors are a concern. Relative performance measures can be included in the revised manuscript. 

Figure 5 (Time – Days) – this looks like the error term is an exponential term. The long term rise in errors would drive the larger error for large fires and ecoregions typified by them. Then again it may be a sample size issue….

As mentioned above, we will explore relative performance measures in the revised manuscript. We agree that it is reasonable to expect larger errors in larger fires upon further reflection. 

Line 191 – “Changes in fire weather and land cover were predicted to have no effects on fire growth in the dry forest regions.”- Really? I think this is misstated or fundamentally miscomprehended. What was shown here is that neither fire weather nor land cover had statistically significant predictive value for fire growth in these forests. Why is the question? Is it because there were no other land cover types encountered? Was it because fire growth was more strongly determined by a variable that wasn’t included (e.g. topography)? Was it because of the relatively small sample size, especially since the data were skewed by at least one very large fire?

“neither fire weather nor land cover had statistically significant predictive value for fire growth in these forests” This is a much more precise and accurate way of stating this result that avoids any misinterpretation. As you allude to later in the comments, I think part of this can be explained by the small sample size of the dry forests, which would not allow for particularly complex models to be fit. Of course, fire weather conditions and land cover SHOULD have an impact on fire growth, but they may not be detectable. One other point is that, per reviewer 3’s comments, we will be including an additional land cover category in the revised manuscript. 

Line 209 – additional parameters or covariates could be included” – such as what? How would they help?

We can elaborate upon this in the revised manuscript, but forest structure/composition could be a useful covariate (per reviewer 3’s comments). Firefighting effort/resource strain might also play a role as a suppressed fire would seemingly have lower average spread rates than an unsuppressed one. Similarly, we were unable to differentiate between planned versus out-of-control wildfires, but if we were able to label the events as such, a difference in fire growth would be expected. Topographic influences will clearly influence fire spread (hilly versus flat terrain). Additional parameters could be included in the difference equation model that could improve model fit. Although this would throw out the benefits of the circular growth approach, an elliptical fire growth model could be assume that had a head and flank growth rate (this would result in the loss of a closed-form solution to the difference equation but it could be fit numerically. There would also be a problem of deciding “where” the fire was being extinguished, as extinguishing the head fire would result in smaller/shorter fires than extinguishing the flank, although interval estimates of daily growth could instead be produced using these two scenarios). The rate at which fires were extinguished could be nonstationary, so that extinguishment is high in the early/intermediate stages of the fire’s lifetime, reflecting a situation where firefighting effort is ramped up as a threat is identified and drawn down as the threat passes. 

Figure 7 – Wettest 2% of day? If that were true no fire spread would be expected. I suspect this is the wettest 2% of days when fire spread was observed.

These are model predictions conditional on being in the lowest 2nd-percentile of the relevant FDI. As you are alluding to here, this is extrapolating beyond the bounds of the data (no fire was ever reported to have ignited and spread when in the 2nd FDI percentile) and we can choose a more realistic lower-bound (informed by the data) for a “low-fire danger” scenario in the revised manuscript. It appears the lowest FDI percentile where a large, multi-day fire (LMDF) event occurred was at approximately the 6th percentile and that the revised lower-threshold should be no lower than that, and the 10th and 90th percentile might then be good choices. On the other han, a case could also be made for the 25th and 75th percentile if we want the max-min observed percentile at which LMDF were observed (i.e. a LMDF may have occurred at the 6th percentile in the rainforest, but in the dry forests a LMDF never occurred in Q1 at all).  

Line 228 – How would the spread tool identify when/where fire occurrence is possible since it is not spatial? It might help identify conditions when fire spread is possible that could perhaps be used in this way.

A more precise way of stating what we were attempting to communicate was that a spread tool could identify a location in which a fire could spread given an ignition, which is essentially what is being said in the second sentence here. This will be corrected in the revised manuscript. 

Lines 244-245 – “relatively sparse human habitation” – perhaps but in the case of the Amazon forests most if not all of those ignitions are tied to those areas of sparse human habitation. The fires rarely if ever happen in remote forests.

Excellent point. We will make sure that this point is included in the revised manuscript. 

Lines 256-257 “This implies that the spread  rate is proportional to the extinguish rate, with a harmonic number as the scaler” – see comment 5 above.

Same response as above. We again appreciate this insight. It was very helpful and we will address it in the revised manuscript.

Line 269 – “additional covariates” – such as?

These were described in our response to comment 9. This will be further elaborated upon in the revised manuscript. 

Line 274 – “ENSO-related effects on fire spread” – perhaps better stated as – “ENSO-related effects on weather conditions that affect fire spread”.

Agreed. ENSO itself doesn’t influence fire, it influences the weather which influences fire. What you have written is more accurate/precise. 

Line 305 – “increased fire danger increased extinguish rates” seems nonsensical physically. It could arise from the model structure for fires that either were extinguished because they spread more rapidly to where landcover or features prevented further fire spread or when sudden events (e.g. rain) extinguished a fire that started during high fire danger conditions.

This is why we greatly appreciated your comment about the model form. We now believe this strange relationship is largely an artifact of the constraints created by the model and NOT something that exists in the real-world. Real-world extinguish rates and spread rates should be either largely independent or perhaps instead negatively correlated. This is a topic that was a bugbear during the drafting of the original manuscript and it will be carefully addressed in the revised manuscript. 

The methods in Section 3 should be improved and clarified. Any reader not expert on fire behaviour will probably not be able to understand what the different FDIs are, which is the difference between them, the variables used to calculate them, and why they were selected amongst the different NFDRS components. Although some of this information is commented in the discussion, that is not the section to explain how the FDIs are calculated. 

The revised version will include a brief description of the FDIs in introductory materials, and will in general make sure that the methods are accessible to those without background in fire science.

The same applies to the methods applied to estimate the model parameters and perform the statistical modelling. Further explanation should be provided to help the interpretation of the results. For example, I do not see a clear relation between the parameters “relative decay rate” and “normalizing factor” in Section 2, and the methods explained in Section 3.

Although we are confident that the mathematics are sound, after reviewing the manuscript we can understand why some might find the description of the mathematics and the justification for the models/parameters lacking. We will make sure that the explanations are more clearly presented in the revised manuscript.

I have some concerns regarding the analysis performed:

• There is a group of land covers not considered in the analysis, corresponding to the shrubland and grassland land covers. I believe that it is an important omission. It would be expected that in the Andean region (which actual biome name is “Montane Grassland and Shrublands) fires would be influenced by these land covers, but that is not reflected in the paper.
• It is difficult to accept that any good model trying to characterize fire behaviour would be independent from fuel characteristics and meteorological conditions.
• It is a very risky assumption to use the FDIs calculated at one point in time (on fire start), and with a very coarse resolution, as characteristic of a fire event that had a size of several km2, and spread during days or weeks. Although the authors mention it in the discussion, I believe that as is, the model is very limited in this respect.

We agree that the presence of shrub/grass landcover types may also influence fire behavior, particularly in the Andean, dry forest, and xeric regions, and when we originally did this analysis we treated this land cover class as the default. That is, if a pixel was not forested and not agriculture, then with only a few edge cases (namely water and ice) then the pixel could be assumed to be some form of grassland/shrubland. Hence, a positive effect of grassland/shrubland on fire spread could be captured by the models with a negative effect of forested pixels. We will include this land cover class in the revised version, although our expectation is that it will be fairly correlated with the other two land cover classes. 

Although we are sympathetic to the concerns regarding holdover fires, the decision to use of FDIs on the ignition date was motivated by (1) the fact that the duration of a fire is generally unknown until they are extinguished, so models based on temporal aggregates (as opposed to conditions on ignition day) will be difficult to apply in the future, and (2) that FDI values should be fairly temporally autocorrelated over the typical duration of fires (between 1-2 weeks). To point (2), a cursory analysis showed that although the weakest temporal autocorrelation was seen in the spread component, the autocorrelation was significant for more than 40 days. Perhaps the FDI values during the largest run of the fire would be more useful and provide better risk estimates than information on the ignition date, but like temporal aggregates, this time/date is generally unknown. The point raised here is fair, and we will make sure to discuss this limitation in the discussion section, but we would prefer to continue to use the conditions at ignition date so that the models can be easily applied in the future to predict fire risk. 

Although the authors state that estimates of spread and extinguish rate could be calculated from environmental data, Tables 3-4 suggest the opposite for the biomes where FDIs are not included in the linear models.

Although certainly other environmental covariates not explored in this analysis could be included that “might” be useful for predicting these parameters, this point was overlooked by the author when writing this passage. We understand how this might be confusing and we will carefully rewrite the passage to be more precise regarding the effect of the environment on fire spread/extinguishment. 

From the reading of the paper I understand that all the Peruvian fires that complied with the size and time length distribution were used to calibrate the models. I would have liked to see some events left out to be used as validation of the model, in order to evaluate its applicability to other fire events.

We initially had envisioned this analysis as being descriptive in nature, with the goal being to describe what covariates had historically coincided with fire spread/extinguishment. This would not require any cross validation methodology. However, after reading comments regarding this point from reviewer 2 and 3, and further consideration, we agree that there is value in performing a cross validation analysis. Indeed, we hope that these models could one day inform fire-related decision makers in South America of the risk of rapidly spreading fire events, in which case it would be prudent to quantify the model performance/predictive ability. Moreover, such an analysis would validate the posited theories between the environment and fire spread. 

I agree with the authors in their statement that more focus should be given to extreme weather conditions, since they are the ones that probably caused the large fire events used in the paper.

Yes. This is certainly an area that is deserving of further attention, but, for practical reasons, will have to be left to another future analysis.

Several of the points in the specific comments were also raised by reviewer 1 and 2. Many of them were also addressed in my responses to this reviewers “General Comments”. All specific comments will be addressed in the revised manuscript.