the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Modelling nonstationary flood frequency in England and Wales using physical covariates
Duncan S. Faulkner
Sean Longfield
Sarah Warren
Jonathan A. Tawn
Abstract. Nonstationary methods of flood frequency analysis are widespread in research but rarely implemented by practitioners who manage flood risk. One reason for this may be that research papers on nonstationary statistical models tend to focus on model fitting rather than extracting the sort of results needed by designers and decision makers. It can be difficult to extract useful results from nonstationary models that include stochastic covariates for which the value in any future year is unknown. Examples of such covariates include rainfall, temperature or indices of fluctuations of atmospheric pressure.
We explore the motivation for including such covariates, whether on their own or in addition to a covariate based on time. We set out a method for expressing the results of nonstationary models, and their uncertainty, as an integrated flow estimate, which removes the dependence on a particular value of the covariates. This can be defined either for a particular year or over a longer period of time. The methods are illustrated by application to a set of 375 river gauges across England and Wales. We find annual rainfall to be a useful covariate at many gauges, sometimes in conjunction with a timebased covariate.
For estimating flood frequency in future conditions, we advocate exploring hybrid approaches that combine the best attributes of nonstationary statistical models and simulation models that can represent the impacts of changes in climate and river catchments.
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Duncan S. Faulkner et al.
Status: closed

RC1: 'Comment on hess2022401', Anonymous Referee #1, 08 Feb 2023
Thank you for the opportunity to review Faulkner et al. Modelling nonstationary flood frequency in England and Wales using physical covariates
The central problem the manuscript seeks to address (that of extracting decisionuseful outputs from nonstationary flood frequency analysis) is compelling problem and I agree with the authors that this issue is often overlooked in the academic literature. The fact that one of the authors is from the Environment Agency of the UK shows that this work is recognized by the appropriate government agency.
That being said, this manuscript is essentially a rewrite of a technical report on the topic of nonstationary flood frequency submitted to the Environment Agency (Faulkner et al., 2020; which is extensively referenced in the manuscript). I did not do an extensive/exhaustive comparison, yet it is clear that some portions of the manuscript are directly copypaste (or nearly so; e.g., compare lines 81105 of the manuscript to pgs. 3435 of the report, lines 119125 of the manuscript to pgs. 3637 of the report, Figure 3 of the manuscript to Figure G9 of the report, and Table 2 of the manuscript to Table 4.7 of the report). I state this (without any judgement) for the purpose of bringing it to the attention of the editor.
Apart from what is noted in the previous paragraph, the science presented in this paper is incremental. Essentially, this is a case study applying nonstationary frequency analysis to flood events in England and Wales. The primary advancement, that of an “integrated flow estimate” which allows for representing the nonstationary results in a decisioncentric way, is essentially an integration of the nonstationary flood frequency estimate over the domain space of the covariates. I think this advancement, while incremental, is useful and should be made know to the academic/practitioner world.
However, it seems it has already been proposed by Eastoe & Tawn (2009). If improvements are needed (lines 127129), then perhaps this additional paper is justified; but, what were the weaknesses? (They are not mentioned) and does this paper address those weaknesses? Here was a missed opportunity to further justify the significance of this paper.
Also, the results associated with this “integrated flow estimate” are fairly minimal (Figures 5 and 6; lines 297 – 322; nothing at all in the discussion and conclusion). Since this is the stated main point of the manuscript, more is needed. You could walk through a hypothetical example of how a decisionmaker or engineer might use Figure 5. You could answer questions such as (and I am sure you can think of additional ones to enrich this portion of the manuscript): What is the implication of a 7x ratio of nonstationary to stationary? Which AEPs are used by UK regulatory standards (and how that does affect the interpretation of these results)? What about the case where the ratio was 0.54 (should we disregard the nonstationary model in that case and use the stationary model since it is more conservative)?
Which brings me to the issue that the discussion and conclusion seem disconnected from rest of paper. They read more like a literature review which is found at the beginning of a work, rather than a reflection on what was done. I do not disagree with what is noted in the discussion and conclusion, but it is not in the right place in the manuscript and is not connected with what was shown in the results. Consequently, the reader misses out on a discussion on the actual results that were presented (e.g., answers to the various questions posed in the previous paragraph).
Some minor comments
Line 79: To my knowledge, I do not think that Francois et al. 2019 use/reference the East Atlantic pattern (East Atlantic is not found when I do a search). Please double check and correct the reference. As a recent review paper on this topic, Francois et al. 2019 is relevant and should probably be referenced in this manuscript, but referenced correctly.
Line 82: AMAX is not defined.
Lines 94 – 105: I am not sure that this discussion of Reason 2 for choosing physicallybased covariates correctly captures the intent of many of the authors I have read, and the approach as best implemented. The intent of a physicallybased covariate to is represent mathematically some physical driving mechanism of floods, whether oceanic, atmospheric, or land based. The confusion of correlation for causation will only happen when an analyst somewhat blindly applies this method: that is, coming up with a suite of possible covariates and trying as many possible and choosing the one with the best correlation. As written, I think this section is somewhat misleading (as if it is the fault of the method, when really this is an error in application of the method).
Line 119: The flood frequency estimate is timedependent regardless of the covariates – either directly dependent on time or implicitly dependent on time via a physical covariate. Wording could be improved here.
Line 198: Why were the models just limited to two covariates? In particular, why weren’t the two physically based covariates used in one model – are they too strongly correlated? Need to justify this choice. Based on skimming the report, I suspect your answer might be that it was too many models... perhaps; but the model with the two physical covariates seems important enough to test regardless of the issue of computation.
Line 219: Why include the GLO if the results are not analyzed? My suggestion is to remove it from the paper, or justify its inclusion (and include results).
Figure 6: They yaxis scale is confusing. Is it a logscale? If so please note in the caption. More labels would also be helpful.
Appendix B: Why is this included? It is just a suggestion, without any testing or analysis or use in the manuscript. I suggest to remove it or to more fully incorporated in the manuscript.
Citation: https://doi.org/10.5194/hess2022401RC1  AC1: 'Reply on RC1', Duncan Faulkner, 23 Feb 2023

RC2: 'Comment on hess2022401', Kolbjorn Engeland, 20 Feb 2023
The paper addresses the challenge of nonstationary flood frequency modelling and how to make such models useful for decision makers. In general, the paper is well written and could be published (provided it is different enough from Faulkner et al., 2020).
The paper is rather short, and have a lot of questions after reading the paper. I therefore think there is room for several types of improvements. Below are some suggestions.
1: I think the numbering of sections might be improved. In particular, the heading on line 55 does not belong to the introduction section since the following paragraphs describe the methods applied in this paper. One solution is to create one section ‘Methods’ that contains lines 56 – 176.
2: No results are shown for the GLO distribution, so it is not necessary to include it at all in the paper.
3: I am not completely convinced of the usefulness of Model 3 where detrended physical covariates are included. Firstly, I cannot see how the covariates are detrended: for which period was the trend calculated, and did you use a linear trend? Secondly, how many of the physical covariates had a significant (and substantial trend) where model 3 and 5 were different ? Thirdly, using a detrended covariate indicate that there is an interaction between time and the physical covariate or potentially interactions with other physical covariate that you have not included. Finally, using a detrended covariate will make it difficult to apply the model for a climate in the coming decades.
This choice of using detrended covariate need a better explanation and discussion. I think it might be helpful to add Model 6 and the methods described in Appendix B. An alternative solution to using independent covariates is to use regularization methods similar to Lasso regression.
4: You included trends in both location and scale parameters of the GEV distribution. Did you systematically evaluate all combination of trends in scale and location parameters? Could different physical covariates be selected for the location and scale parameters? Are the results in Figure 2, Figure 3 and Figure 4 based on the best fitting covariate for the location or scale parameters? Some more details are needed.
5: What are the signs of the detected trends (or regression coefficients)?
6: I think more results similar to those shown in Figure 5 could be produced. It could be good to show one more plot where floods for the nonstationary model is smaller than the floods for the stationary model. It could also be interesting to see this plot for a model where time is included as a covariate and a model where time is excluded as a covariate.
7: Could it be useful to see the results in Figure 6 on a map in order to highlight where the ratio is smaller and larger than 1? Have all records the same year as the last year in the records? If not, how much might the results be influenced by the end year of the record?
8: Is it possible to detect more results from the data used to produce Figure 6? In particular, I would like to know for which models or catchments the ratios are far from one. Is it in catchments where the selected models include time as a covariate or are the specific catchment properties or geographical locations that might explain the differences in ratios? Another possibility is that the estimate of the shape parameter are different in the stationary and nonstationary models. The maximum likelihood estimator is know to results in shape parameter estimates that are not robust, in particular for short record lengths. Could the results you get depend on record length? A penalized maximum likelihood estimator is often recommended for the GEV distribution. Alternatively, a Bayesian approach with a prior on the shape parameter could have been used. I think the robustness of the ML estimator should be discussed.
9: Uncertainties in the estimates are not discussed. I think this is important since the inflation in uncertainty is a drawback of nonstationary modelling. Figure 5 shows that he uncertainty in the nonstationary model is high, and even if the difference in integrated flow estimate is substantial, the difference is not necessarily significant. Figure 6 shows that a large par of the ratios are close to 1. Is it possible to use the results from all 375 flow records to summarize in how many cases the nonstationary integrated flow estimates are outside the confidence intervals for the stationary model?
10: The implications for practical applications could be discussed more. Would you recommend to always use the nonstationary model? What are the recommendations if the nonstationary model results ins smaller design floods or in substantially higher design floods (up to 5 times higher than for a stationary model.) ?
Citation: https://doi.org/10.5194/hess2022401RC2  AC2: 'Reply on RC2', Duncan Faulkner, 23 Mar 2023
Status: closed

RC1: 'Comment on hess2022401', Anonymous Referee #1, 08 Feb 2023
Thank you for the opportunity to review Faulkner et al. Modelling nonstationary flood frequency in England and Wales using physical covariates
The central problem the manuscript seeks to address (that of extracting decisionuseful outputs from nonstationary flood frequency analysis) is compelling problem and I agree with the authors that this issue is often overlooked in the academic literature. The fact that one of the authors is from the Environment Agency of the UK shows that this work is recognized by the appropriate government agency.
That being said, this manuscript is essentially a rewrite of a technical report on the topic of nonstationary flood frequency submitted to the Environment Agency (Faulkner et al., 2020; which is extensively referenced in the manuscript). I did not do an extensive/exhaustive comparison, yet it is clear that some portions of the manuscript are directly copypaste (or nearly so; e.g., compare lines 81105 of the manuscript to pgs. 3435 of the report, lines 119125 of the manuscript to pgs. 3637 of the report, Figure 3 of the manuscript to Figure G9 of the report, and Table 2 of the manuscript to Table 4.7 of the report). I state this (without any judgement) for the purpose of bringing it to the attention of the editor.
Apart from what is noted in the previous paragraph, the science presented in this paper is incremental. Essentially, this is a case study applying nonstationary frequency analysis to flood events in England and Wales. The primary advancement, that of an “integrated flow estimate” which allows for representing the nonstationary results in a decisioncentric way, is essentially an integration of the nonstationary flood frequency estimate over the domain space of the covariates. I think this advancement, while incremental, is useful and should be made know to the academic/practitioner world.
However, it seems it has already been proposed by Eastoe & Tawn (2009). If improvements are needed (lines 127129), then perhaps this additional paper is justified; but, what were the weaknesses? (They are not mentioned) and does this paper address those weaknesses? Here was a missed opportunity to further justify the significance of this paper.
Also, the results associated with this “integrated flow estimate” are fairly minimal (Figures 5 and 6; lines 297 – 322; nothing at all in the discussion and conclusion). Since this is the stated main point of the manuscript, more is needed. You could walk through a hypothetical example of how a decisionmaker or engineer might use Figure 5. You could answer questions such as (and I am sure you can think of additional ones to enrich this portion of the manuscript): What is the implication of a 7x ratio of nonstationary to stationary? Which AEPs are used by UK regulatory standards (and how that does affect the interpretation of these results)? What about the case where the ratio was 0.54 (should we disregard the nonstationary model in that case and use the stationary model since it is more conservative)?
Which brings me to the issue that the discussion and conclusion seem disconnected from rest of paper. They read more like a literature review which is found at the beginning of a work, rather than a reflection on what was done. I do not disagree with what is noted in the discussion and conclusion, but it is not in the right place in the manuscript and is not connected with what was shown in the results. Consequently, the reader misses out on a discussion on the actual results that were presented (e.g., answers to the various questions posed in the previous paragraph).
Some minor comments
Line 79: To my knowledge, I do not think that Francois et al. 2019 use/reference the East Atlantic pattern (East Atlantic is not found when I do a search). Please double check and correct the reference. As a recent review paper on this topic, Francois et al. 2019 is relevant and should probably be referenced in this manuscript, but referenced correctly.
Line 82: AMAX is not defined.
Lines 94 – 105: I am not sure that this discussion of Reason 2 for choosing physicallybased covariates correctly captures the intent of many of the authors I have read, and the approach as best implemented. The intent of a physicallybased covariate to is represent mathematically some physical driving mechanism of floods, whether oceanic, atmospheric, or land based. The confusion of correlation for causation will only happen when an analyst somewhat blindly applies this method: that is, coming up with a suite of possible covariates and trying as many possible and choosing the one with the best correlation. As written, I think this section is somewhat misleading (as if it is the fault of the method, when really this is an error in application of the method).
Line 119: The flood frequency estimate is timedependent regardless of the covariates – either directly dependent on time or implicitly dependent on time via a physical covariate. Wording could be improved here.
Line 198: Why were the models just limited to two covariates? In particular, why weren’t the two physically based covariates used in one model – are they too strongly correlated? Need to justify this choice. Based on skimming the report, I suspect your answer might be that it was too many models... perhaps; but the model with the two physical covariates seems important enough to test regardless of the issue of computation.
Line 219: Why include the GLO if the results are not analyzed? My suggestion is to remove it from the paper, or justify its inclusion (and include results).
Figure 6: They yaxis scale is confusing. Is it a logscale? If so please note in the caption. More labels would also be helpful.
Appendix B: Why is this included? It is just a suggestion, without any testing or analysis or use in the manuscript. I suggest to remove it or to more fully incorporated in the manuscript.
Citation: https://doi.org/10.5194/hess2022401RC1  AC1: 'Reply on RC1', Duncan Faulkner, 23 Feb 2023

RC2: 'Comment on hess2022401', Kolbjorn Engeland, 20 Feb 2023
The paper addresses the challenge of nonstationary flood frequency modelling and how to make such models useful for decision makers. In general, the paper is well written and could be published (provided it is different enough from Faulkner et al., 2020).
The paper is rather short, and have a lot of questions after reading the paper. I therefore think there is room for several types of improvements. Below are some suggestions.
1: I think the numbering of sections might be improved. In particular, the heading on line 55 does not belong to the introduction section since the following paragraphs describe the methods applied in this paper. One solution is to create one section ‘Methods’ that contains lines 56 – 176.
2: No results are shown for the GLO distribution, so it is not necessary to include it at all in the paper.
3: I am not completely convinced of the usefulness of Model 3 where detrended physical covariates are included. Firstly, I cannot see how the covariates are detrended: for which period was the trend calculated, and did you use a linear trend? Secondly, how many of the physical covariates had a significant (and substantial trend) where model 3 and 5 were different ? Thirdly, using a detrended covariate indicate that there is an interaction between time and the physical covariate or potentially interactions with other physical covariate that you have not included. Finally, using a detrended covariate will make it difficult to apply the model for a climate in the coming decades.
This choice of using detrended covariate need a better explanation and discussion. I think it might be helpful to add Model 6 and the methods described in Appendix B. An alternative solution to using independent covariates is to use regularization methods similar to Lasso regression.
4: You included trends in both location and scale parameters of the GEV distribution. Did you systematically evaluate all combination of trends in scale and location parameters? Could different physical covariates be selected for the location and scale parameters? Are the results in Figure 2, Figure 3 and Figure 4 based on the best fitting covariate for the location or scale parameters? Some more details are needed.
5: What are the signs of the detected trends (or regression coefficients)?
6: I think more results similar to those shown in Figure 5 could be produced. It could be good to show one more plot where floods for the nonstationary model is smaller than the floods for the stationary model. It could also be interesting to see this plot for a model where time is included as a covariate and a model where time is excluded as a covariate.
7: Could it be useful to see the results in Figure 6 on a map in order to highlight where the ratio is smaller and larger than 1? Have all records the same year as the last year in the records? If not, how much might the results be influenced by the end year of the record?
8: Is it possible to detect more results from the data used to produce Figure 6? In particular, I would like to know for which models or catchments the ratios are far from one. Is it in catchments where the selected models include time as a covariate or are the specific catchment properties or geographical locations that might explain the differences in ratios? Another possibility is that the estimate of the shape parameter are different in the stationary and nonstationary models. The maximum likelihood estimator is know to results in shape parameter estimates that are not robust, in particular for short record lengths. Could the results you get depend on record length? A penalized maximum likelihood estimator is often recommended for the GEV distribution. Alternatively, a Bayesian approach with a prior on the shape parameter could have been used. I think the robustness of the ML estimator should be discussed.
9: Uncertainties in the estimates are not discussed. I think this is important since the inflation in uncertainty is a drawback of nonstationary modelling. Figure 5 shows that he uncertainty in the nonstationary model is high, and even if the difference in integrated flow estimate is substantial, the difference is not necessarily significant. Figure 6 shows that a large par of the ratios are close to 1. Is it possible to use the results from all 375 flow records to summarize in how many cases the nonstationary integrated flow estimates are outside the confidence intervals for the stationary model?
10: The implications for practical applications could be discussed more. Would you recommend to always use the nonstationary model? What are the recommendations if the nonstationary model results ins smaller design floods or in substantially higher design floods (up to 5 times higher than for a stationary model.) ?
Citation: https://doi.org/10.5194/hess2022401RC2  AC2: 'Reply on RC2', Duncan Faulkner, 23 Mar 2023
Duncan S. Faulkner et al.
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