the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 31 Jul 2026
Trends in geo-hydrological risk to the population of Italy
Abstract. Geo-hydrological hazards, including floods and landslides, are among the most widespread hazards and a major cause of human loss worldwide. Their impacts are shaped by meteorological forcing and by long-term changes in exposure, vulnerability, and settlement patterns. Yet robust assessments of long-term fatality trends are rare because sufficiently long, accurate, and homogeneous records of damaging events are lacking. A key unresolved question is whether the human toll of geo-hydrological events has changed structurally through time, and which climatic, socio-economic, or policy factors best explain that change. Here we show, using a unique 1950–2024 catalogue of fatal events in Italy, that geo-hydrological risk underwent a marked transition, with fatalities and fatal days declining sharply until about 1970 and then stabilising at much lower levels. This decline was driven mainly by landslides, whereas flood-related losses showed weaker long-term change. The decline was not explained by specific risk policies or management programmes, as most of it preceded their implementation. Instead, precipitation was the main climatic driver of the remaining interannual variability, particularly for floods and days with fatal events. By contrast, population and gross domestic product did not account for the long-term trends once shared temporal changes were considered. Fatal days were less overdispersed and more predictable than fatalities, suggesting that meteorological factors control more directly the occurrence of dangerous conditions than the final death toll. Fatalities, instead, depend strongly on exposure, vulnerability, timing, location, and other event-specific circumstances. Together, these findings indicate that broad socio-economic dynamics can reduce geo-hydrological mortality even as hazardous processes persist, whereas meteo-climatic conditions continue to shape year-to-year risk.
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Status: final response (author comments only)
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RC1: 'Comment on egusphere-2026-4342', Milad Basirifard, 01 Aug 2026
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AC1: 'Reply on RC1', Fausto Guzzetti, 16 Oct 2026
We thank the referee for the careful assessment of our manuscript and for identifying weaknesses in its interpretation and statistical analyses. The three main comments have prompted substantial revisions to clarify what the available data and methods can support. In the responses below, we explain how we have reframed fatalities and fatal days as complementary measures of lethal outcomes, reconsidered the predictor and policy analyses in light of confounding and multiple testing, and reassessed the predictability comparison and interpretation of trend extrapolations. These changes place the emphasis on describing the observed temporal patterns while acknowledging the limitations of causal attribution and forecasting.
Comment 1
The use of fatal days is conceptually flawed. A fatal day is still defined by the occurrence of a death. It therefore depends on exposure, vulnerability, warnings, and chance. It does not represent all days with hazardous conditions. Days with serious floods or landslides but no fatalities are completely excluded. Thus, comparing fatalities with fatal days cannot separate hazard occurrence from human consequences. This claim is repeated throughout the manuscript but is not supported by the data. Independent records of both fatal and non-fatal events are needed.
We thank the reviewer for this important clarification. Our catalogue records fatal events and days with at least one fatal event; it does not provide an independent record of floods and landslides that caused no fatalities. A day therefore enters the fatal-days series only when at least one death occurred. In the revised manuscript we make this clear.
Reframing fatalities and fatal days
The manuscript already presented fatalities and fatal days as distinct measures, and this was the reason for analysing them separately. Separate models were fitted to each series; neither series was used as a predictor of, or control for, the other. Fatal days measure the number of calendar days on which at least one fatal event occurred, whereas fatalities measure the total number of people who died or were reported missing. The two series therefore describe different aspects of lethal outcomes. We agree, however, that some passages extended this distinction beyond what the data support. Because both series are conditioned on the occurrence of at least one death, considering their results together cannot separate the occurrence of hazardous events from their human consequences. In the revised manuscript, we continue to model the two series separately, but we avoid presenting fatal days as a measure of dangerous conditions or suggesting that the two series distinguish hazard occurrence from human impacts.
Consequences for interpretation
Fatality counts have a wider range and a heavier upper tail because a single day can contribute many fatalities, whereas it contributes only one fatal day. This explains the distributional difference between the series, but it does not show that hazardous conditions are more regular or that fatal days are more predictable. As reported in our response to Comment 3, forecast scores normalized against a separate negative-binomial reference model for each of the six series show no consistent predictability advantage for fatal days. We have revised the Abstract, Results, Discussion, and Conclusions to remove the previous predictability claim.
We have also revised the interpretation of the precipitation associations. An association between precipitation and fatal days could arise because precipitation increases the occurrence of hazardous events, because it increases the probability that an event causes a fatality, or through both processes. The available data cannot distinguish these explanations. We therefore no longer state that precipitation controls the occurrence of hazardous or dangerous conditions.
Manuscript revisions and limitation
We have revised the relevant language in the Abstract, Introduction, distributional results, Discussion, and Conclusions. The central wording now states that fatal days measure the frequency of days with at least one fatal event and fatalities measure the total human toll. Both are conditioned on the occurrence of a death; their comparison therefore concerns the frequency and magnitude of lethal outcomes, not the separation of hazard occurrence from human consequences.
We have also added an explicit limitation: because the catalogue does not include an independent record of non-fatal geo-hydrological events, the analysis cannot separate changes in hazard frequency from changes in the probability that an event becomes lethal. Addressing that question would require an outcome-independent catalogue containing both fatal and non-fatal floods and landslides. We identify the integration of such event inventories as a priority for future work.
Comment 2
The predictor analysis is too coarse to identify drivers. National annual precipitation cannot represent the local and short-duration rainfall extremes that trigger floods and landslides. National GDP and population are also poor measures of local exposure and vulnerability. Moreover, these variables share strong trends with calendar year. Adding a smooth time term creates serious concurvity. Removing the shared trend and then concluding that GDP or population did not explain the decline is circular. The policy analysis is equally weak. It uses 378 models with arbitrary and overlapping windows. There is no adequate correction for multiple testing or credible causal counterfactual. The conclusions about climate, socioeconomic development, and policies go far beyond what these models can show.
We thank the reviewer for this comprehensive critique. We agree that our original written suggested a level of causal attribution that cannot be supported by these models. We have revised the manuscript to soften our conclusions, acknowledging that our analysis investigates broad empirical covariations rather than identifying deterministic causal drivers.
Resolution and rationale of predictors
We agree that national annual precipitation, GDP, and population are coarse proxies that cannot represent local, short-duration meteorological extremes or local vulnerability. However, these national aggregations were the only time series available that consistently covered the entire spatial domain and the full 75-year study period (1950–2024). Our intention was never to identify event-scale mechanisms, but strictly to search for potential macro-signals that might empirically explain the evident regime shift observed in the non-stationary landslide series.
Shared trends and the removal of predictor GAMs
We agree with the reviewer that these predictors share strong trends with the calendar year, creating structural confounding. As we had already observed through preliminary correlation tests, these macroeconomic and climatic variables are highly collinear with the historical development of the country.
To definitively quantify your concern, we computed concurvity diagnostics for these predictors. The results proved a priori that their inclusion in the GAMs is highly problematic: GDP and population remain extremely concurved, acting effectively as latent proxies for time (with worst-case concurvity values reaching 0.999).
Consequently, we have removed the bivariate and multivariate predictor GAMs from the revised manuscript. We concede that removing the temporal trend to conclude that GDP does not explain the decline is a circular argument. Therefore, the issue is not that the GAM framework restricts our assumptions, but rather that the inherent properties of these highly collinear historical variables preclude the advantageous use of GAMs to isolate independent causal effects.
Instead of presenting these models, the revised text now explicitly discusses this methodological limitation, clarifying that the time series available at these spatial and temporal scales do not allow for reliable inferences. Furthermore, we have added a comment highlighting that this underscores the profound difficulty of operating with macroscopic statistical methods at national scales in this context. It serves as a cautionary note to the community that, given the structural confounding in currently available historical data, it is genuinely difficult to draw definitive, causal conclusions regarding the specific drivers of the observed regime shift.
Redesign of the policy analysis
We thank the reviewer for pointing out the weaknesses in the policy analysis design. We have completely redesigned this section to address the overlapping windows and the multiplicity issue:
- We abandoned the 378 arbitrary models and restructured the analysis into four families of 30 models with mutually exclusive prospective periods (short, medium, and long-term post-policy phases) and a pre-policy falsification check.
- Simulation-based residual diagnostics confirmed the absence of systematic temporal autocorrelation (Ljung-Box at lag 5), validating the structural adequacy of the GAMs to capture the temporal dynamics.
- To properly address the multiple testing problem, we applied the False Discovery Rate (FDR) correction. Given the structural dependence among the tests (due to nested policy categories and correlated outcomes), we used the Benjamini-Yekutieli (BY) procedure, which controls the FDR under arbitrary dependence.
Following this correction, the redesigned analysis did not identify any policy-related association that remained statistically significant. We have revised the conclusions to reflect this: while policies may have had a positive impact, the available observational macro-data and statistical methods cannot reliably isolate or prove this effect.
Comment 3
The predictability comparison is not valid. Fatal-day counts have a much narrower distribution than fatality counts. They will naturally have lower negative log predictive scores, even without greater temporal predictability. The authors must compare each model against an appropriate climatological or negative-binomial baseline and report a normalized skill score. The entropy analysis is also unreliable with only 75 annual observations, especially after dividing the data into quantile states and using two lags. Important details are missing, including the number of states, bias correction, and bootstrap procedure. Finally, four evaluation years are not enough to validate the forecasts. Showing that four observations fall within very wide prediction intervals is not evidence of forecasting skill. The projections to 2030 are therefore not convincing.
We thank the reviewer for the constructive suggestions, which have improved our understanding of the models' limits and strengths.
Predictability and entropy analysis
We accept the critique regarding the entropy analysis and the predictability comparison. Originally, establishing whether one series (e.g., fatal days) was inherently more predictable than another was driven by its potential impact on Civil Protection management. However, we acknowledge that our proposed state-based methods are ineffective for a time series of only 75 annual observations divided into 3 quantile states. With such sparse data, it is impossible to determine whether transition matrices with zero cases reflect physical impossibilities or are merely artifacts of the short time series. While we could have reduced the discretization to only two states (e.g., above and below the median) to artificially populate the matrices, we are not convinced that such a binary classification is representative for these events. This would have been a mere mathematical workaround to force the analysis, rather than a sound solution. Consequently, we have removed the attempt to establish predictability prevalence between the series, and we have removed the entropy analysis from the manuscript.
Forecasting vs. trend extrapolation
Regarding the forecast validation and the 2030 projections, we concede that we over-structured the interpretation of our results. As the predictor analysis demonstrated, we do not possess the mechanistic drivers required for true operational forecasting. Our genuine initial objective was purely descriptive: to model the historical time series and project the recent trend. The four-year holdout (2021–2024) was intended merely as a qualitative check to verify if the recent data aligned with the extrapolated trend, assuming the current regime remained unchanged. We agree that treating this as "forecasting skill" was an overstatement.
Advantage of temporal GAMs
Following the reviewer’ suggestion to evaluate the models against a stationary Negative Binomial baseline, we found further justification for our descriptive framework. For the non-stationary time series (such as landslides), the temporal GAMs show a 9–12% improvement in representing the recent data compared to the stationary baseline, and more important, they yield narrower prediction intervals. Interestingly, for series that lack statistically significant temporal trends, this advantage over the baseline is not evident. This confirms that GAMs are effective for dynamically capturing the recent trend. For non-stationary phenomena, the splines successfully intercept the current stabilization phase that followed historical regime shifts, avoiding the overestimation of uncertainty that would result from using a simple historical average.
Manuscript revisions
We thank the reviewer for prompting this deeper evaluation. Although our original intent was to describe and reproduce the temporal evolution rather than to predict it, we recognize that our terminology was misleading. We will thoroughly revise the manuscript to explicitly clarify our descriptive intent, and we will carefully remove any terminology, projections, or claims that overreach beyond historical trend extrapolation.
Citation: https://doi.org/10.5194/egusphere-2026-4342-AC1
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AC1: 'Reply on RC1', Fausto Guzzetti, 16 Oct 2026
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RC2: 'Comment on egusphere-2026-4342', Anonymous Referee #2, 19 Oct 2026
Overall
The paper uses the Italian national catalogue of fatal floods and landslides for 1950–2024 to study long-term changes in deaths and in the number of days with deaths. The catalogue is a real asset: it holds 1,349 fatal events for this period, compared with 57 flood and landslide disasters in EM-DAT (p.8). The main finding is well supported. Deaths from ordinary events fell sharply until about 1970 and have stayed low since, and the fall comes mostly from landslides (Tables 1–2). The problem is that the paper goes further than the data. It attributes the decline to post-war socio-economic change, states that policies do not explain it, and concludes that fatal days are more predictable than deaths. None of these follows from the analyses as they stand. I recommend major revision.
Major comments
- The data show that deaths fell, not why. The paper concludes that the decline reflects Italy's post-war socio-economic transformation: urbanisation, better housing and communications, and less rural living (p.16). Most of these factors are not in the models, and the two that are, GDP and population, show no consistent effect once the shared time trend is accounted for (pp.14, 17). The socio-economic explanation is therefore a hypothesis, not a result. The same applies to policy. The analysis only tests whether policy dates line up with the turning point (p.14), but policies usually act with delays and build up over time, so a mismatch in dates does not show that they had no effect. Both points should be presented as possible explanations, including in the abstract and conclusions.
- The predictability comparison is not like for like. Annual fatal days range from 1 to 32, while annual deaths range from 1 to 371 (Table 1). A series with a narrow range is easier to forecast whatever method is used, so lower predictive surprise for fatal days says little about the process. Each series should be compared with a simple reference forecast of its own, such as the mean of recent years, and the gain over that reference reported. The paper's own measures of intrinsic predictability are weak, with bootstrap intervals that often include zero (p.14).
- The scope of the conclusions should be stated. The Vajont and Stava disasters, excluded from all analyses, account for about 40% of all deaths in the catalogue (2,185 of 5,458; p.8). The reason for excluding them is clear, but the results then describe deaths from ordinary rainfall-triggered events, not the geo-hydrological risk to the population of Italy as a whole. The title, abstract and conclusions should say so. The authors should also explain how changes in the sources and completeness of the catalogue over 75 years could affect the size of the decline.
Citation: https://doi.org/10.5194/egusphere-2026-4342-RC2 -
AC2: 'Reply on RC2', Fausto Guzzetti, 25 Oct 2026
Overall comment
The paper uses the Italian national catalogue of fatal floods and landslides for 1950–2024 to study long-term changes in deaths and in the number of days with deaths. The catalogue is a real asset: it holds 1,349 fatal events for this period, compared with 57 flood and landslide disasters in EM-DAT (p.8). The main finding is well supported. Deaths from ordinary events fell sharply until about 1970 and have stayed low since, and the fall comes mostly from landslides (Tables 1–2). The problem is that the paper goes further than the data. It attributes the decline to post-war socio-economic change, states that policies do not explain it, and concludes that fatal days are more predictable than deaths. None of these follows from the analyses as they stand. I recommend major revision.
We thank the reviewer for the careful and constructive assessment of our manuscript. We appreciate the recognition of the value of the Italian national catalogue and of the robustness of the principal finding: a marked decline in fatalities from floods and landslides until approximately 1970, followed by a prolonged period characterised by substantially lower mortality.
We agree that some of our original interpretations extended beyond what the available data and statistical analyses could support. Similar concerns were raised by Reviewer 1, and the two reviews have prompted a substantial reconsideration of the objectives, methods, and conclusions of the study.
In particular, in the revised manuscript, we expect to (i) change the interpretation of the long-term decline to distinguish observed temporal patterns from possible causal explanations; (ii) remove the predictor GAMs because of the strong confounding between national socio-economic variables and calendar year; (iii) redesign the policy analysis, including a correction for multiple testing; (iv) remove the entropy-based predictability analysis and the claim that fatal days are inherently more predictable than fatalities; and, lastly, (v) clarify that the temporal models describe historical changes and provide conditional trend extrapolations rather than operational forecasts.
The revisions may narrow the scope of our conclusions but preserve what we consider the principal contribution of the study: a quantitative characterisation of the long-term evolution of fatalities and fatal days associated with floods, landslides, and their combination in Italy for a 75-year period.
Comment 1
The data show that deaths fell, not why. The paper concludes that the decline reflects Italy's post-war socio-economic transformation: urbanisation, better housing and communications, and less rural living (p.16). Most of these factors are not in the models, and the two that are, GDP and population, show no consistent effect once the shared time trend is accounted for (pp.14, 17). The socio-economic explanation is therefore a hypothesis, not a result. The same applies to policy. The analysis only tests whether policy dates line up with the turning point (p.14), but policies usually act with delays and build up over time, so a mismatch in dates does not show that they had no effect. Both points should be presented as possible explanations, including in the abstract and conclusions..
We agree that the observed decline in fatalities cannot, by itself, establish the causes of that decline. Our original discussion attributed excessive explanatory weight to Italy's post-war socio-economic transformation, although several of the mechanisms invoked, including urbanisation, changes in housing conditions, infrastructure development, and improvements in communication, were not directly represented in the statistical models. In the revised manuscript, we expect to change the interpretation of the long-term decline. The Socio-economic transformation will be presented as a plausible historical explanation, rather than as a causal result established by our analyses. We expect to o revise the Abstract, Discussion, and Conclusions to distinguish more clearly between the observed changes in mortality and the possible processes that contributed to them.
Socio-economic predictors and confounding
The reviewer's observation concerning GDP and population is particularly relevant. These variables exhibit strong long-term trends and are therefore structurally confounded with calendar year. As also noted by Reviewer 1, including a smooth temporal term in the GAMs makes it difficult to distinguish their independent contributions from the historical evolution represented by time. To investigate this limitation, we have calculated concurvity diagnostics. These confirmed severe confounding, particularly for GDP and population, with worst-case concurvity values reaching 0.999. Consequently, we expect to remove the bivariate and multivariable predictor GAMs from the revised manuscript. We no longer interpret the absence of independent statistical effects after adjustment for time as evidence that GDP or population did not contribute to the historical decline. Instead, we explicitly acknowledge that the available national annual series do not permit a reliable separation of the effects of socio-economic development, climatic variability, and other processes evolving over the same period. We consider this an important methodological limitation of the study, particularly for attempts to identify the causes of long-term changes in geo-hydrological mortality using highly aggregated historical data.
Policy analysis
We agree that differences between policy implementation dates and the timing of the observed decline cannot establish that policies were ineffective. Policy measures may operate through delayed, cumulative, or indirect mechanisms, and their effects may overlap with broader socio-economic and institutional changes. In response to this concern, and to the related criticism raised by Reviewer 1, we have redesigned the policy analysis. The original set of 378 models has been replaced by four families of 30 models, examining post-policy phases, cumulative policy exposure, policy-enactment years, and pre-policy falsification periods. The post-policy analysis distinguishes mutually exclusive short-, medium-, and long-term periods, allowing for potential delayed associations. We have also addressed the multiplicity of statistical tests by applying the Benjamini–Yekutieli false discovery rate correction, which accommodates dependence among tests. After this correction, none of the policy-related associations remained statistically significant. Importantly, we shall not interpret this result as evidence that policies had no effect. Rather, the revised analysis indicates that the available national annual data do not provide sufficiently robust statistical evidence to isolate policy-related changes from the broader historical trend. We acknowledge that the absence of statistically significant associations is not equivalent to the absence of policy benefits. We expect to change the text in the Abstract, Discussion, and Conclusions accordingly. In the revised manuscript we present socio-economic transformation and risk-management policies as possible, potentially interacting explanations for the observed decline, while acknowledging that their relative contributions cannot be established from the available data.
Comment 2
The predictability comparison is not like for like. Annual fatal days range from 1 to 32, while annual deaths range from 1 to 371 (Table 1). A series with a narrow range is easier to forecast whatever method is used, so lower predictive surprise for fatal days says little about the process. Each series should be compared with a simple reference forecast of its own, such as the mean of recent years, and the gain over that reference reported. The paper's own measures of intrinsic predictability are weak, with bootstrap intervals that often include zero (p.14).
We agree that the original comparison of predictive surprise between fatalities and fatal days was not appropriate. The two series have markedly different distributions, ranges, and degrees of overdispersion. Consequently, lower negative log predictive scores for fatal days cannot be interpreted directly as evidence of greater intrinsic predictability. The issue was also identified by Reviewer 1 and drives a substantial revision of our analysis and interpretation.
Removal of the intrinsic predictability analysis
We have reconsidered the information-theoretic approach used to estimate intrinsic predictability. The analysis relied on 75 yearly observations, discretised into three empirical-quantile states. With such a limited sample, particularly when considering two preceding states, the estimated transition probabilities become highly sensitive to sparse observations and sampling variability. We agree that the resulting estimates do not provide a sufficiently reliable basis for comparing the intrinsic predictability of fatalities and fatal days. Rather than retaining an analysis whose results depend strongly on discretisation choices, we expect to remove the entropy-based predictability analysis from the revised manuscript.
Comparison with reference models
We have reconsidered the interpretation of the rolling predictive scores. As the reviewer correctly observes, comparisons of raw predictive surprise between series with different distributions are not sufficient to establish relative forecasting skill. Following the recommendations of both reviewers, we evaluated the temporal GAMs against separate stationary negative-binomial reference models for the individual series. This comparison indicates that, for the series exhibiting marked non-stationarity, particularly those associated with landslides, the temporal GAMs provide improvements of approximately 9–12% in representing the recent observations relative to the stationary reference models. For series without statistically significant temporal trends, this improvement is not evident. The results support the usefulness of temporal GAMs for describing and extrapolating the historical evolution of non-stationary count series. They do not, however, demonstrate that fatal days are intrinsically more predictable than fatalities. We expect to remove the conclusion that fatal days are generally more predictable than fatalities.
Interpretation of temporal extrapolations
We have reconsidered the purpose and interpretation of the temporal models. Our original objective was to characterise the long-term evolution of the annual series and examine the continuation of their recent trends, rather than to develop operational forecasting systems. We acknowledge that the four-year evaluation period (2021–2024) is insufficient to establish robust out-of-sample forecasting skill. The agreement between the observations and the model prediction intervals should be regarded as a limited consistency check, not as evidence of operational predictability. We expect to revise the text to distinguish historical trend modelling and conditional extrapolation from forecasting skill. The extrapolations to 2030 are now interpreted as model-dependent representations of what might be expected if the recent statistical regime persists, with the associated uncertainty, rather than as forecasts of future mortality. We believe the changes will address the reviewer's concern and will provide a more defensible interpretation of our temporal modelling results.
Comment 3
The scope of the conclusions should be stated. The Vajont and Stava disasters, excluded from all analyses, account for about 40% of all deaths in the catalogue (2,185 of 5,458; p.8). The reason for excluding them is clear, but the results then describe deaths from ordinary rainfall-triggered events, not the geo-hydrological risk to the population of Italy as a whole. The title, abstract and conclusions should say so. The authors should also explain how changes in the sources and completeness of the catalogue over 75 years could affect the size of the decline.
We thank the reviewer for raising these important issues concerning the scope and representativeness of the analysis.
Exclusion of the Vajont and Stava disasters
We agree with the reviewer that excluding the Vajont (1963) and Stava (1985) engineering related disasters has important implications for the interpretation of the results. Together, these two events account for 2,185 fatalities, approximately 40% of the 5,458 fatalities recorded during 1950–2024. The decision to exclude these disasters was based on their exceptional characteristics and their close association with major engineering works. They differ substantially from the other fatal floods and landslides considered in the study, both in their triggering circumstances and in the magnitude of their consequences. Including the two events would introduce two exceptionally large mortality observations into the annual series, strongly influencing the distributional properties, trend estimates, and temporal models. Their exclusion allows us to investigate more consistently the long-term evolution of mortality associated with the other recorded fatal landslide and geo-hydrological events. Nevertheless, we agree that the resulting analysis does not represent the complete mortality burden from all landslides and geo-hydrological disasters in Italy during the study period. We shall clarify this in the revised manuscript, as well as the scope of the study. We expect to distinguish between the complete catalogue, which includes Vajont and Stava, and the subset used for the statistical analyses. We further acknowledge that the term "ordinary" requires care. The events retained in the analysis include severe and occasionally catastrophic natural floods and landslides. Their defining distinction from Vajont and Stava is not necessarily their magnitude, but the absence of the exceptional engineering-related circumstances that motivated the exclusion of those two disasters. Our conclusions are therefore restricted to the analysed subset of fatal flood and landslide events and should not be interpreted as describing the complete spectrum of landslide, flood, and geo-hydrological mortality in Italy.
Historical sources and catalogue completeness
We agree that the temporal consistency and completeness of a historical catalogue are important considerations when interpreting long-term trends. Our Italian catalogue has been compiled from historical documentary sources and systematically updated over time. Nevertheless, the availability, accessibility, and characteristics of documentary evidence have changed during the 75-year study period. Improvements in communication, the development of digital archives, and changes in reporting practices may have affected the probability that individual events were identified and recorded. These changes could influence the observed temporal distribution of fatal events, fatalities, and fatal days, particularly for events involving small numbers of deaths.
We acknowledge that the statistical analyses do not explicitly model time-varying catalogue completeness or changes in reporting probability. Consequently, we cannot quantify precisely how much of the observed decline might be affected by historical differences in documentation. We will strengthen the argument of this limitation. In the revised manuscript we shall recognise that the observed decline reflects the recorded mortality series and that its estimated magnitude may be influenced, to an unknown extent, by changes in historical reporting and catalogue completeness. At the same time, we shall consider the magnitude and temporal consistency of the decline, particularly in the landslide series, to be an important empirical finding. The statistical evidence supports a marked change in the recorded mortality regime, although its exact magnitude and underlying causes require cautious interpretation. A quantitative assessment of temporal completeness would require independent documentary sources or other evidence capable of estimating changes in the probability of recording fatal events through time, which are not available to us. We identify this as a useful direction for future research.
Citation: https://doi.org/10.5194/egusphere-2026-4342-AC2
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1. The use of fatal days is conceptually flawed. A fatal day is still defined by the occurrence of a death. It therefore depends on exposure, vulnerability, warnings, and chance. It does not represent all days with hazardous conditions. Days with serious floods or landslides but no fatalities are completely excluded. Thus, comparing fatalities with fatal days cannot separate hazard occurrence from human consequences. This claim is repeated throughout the manuscript but is not supported by the data. Independent records of both fatal and non-fatal events are needed.
2. The predictor analysis is too coarse to identify drivers. National annual precipitation cannot represent the local and short-duration rainfall extremes that trigger floods and landslides. National GDP and population are also poor measures of local exposure and vulnerability. Moreover, these variables share strong trends with calendar year. Adding a smooth time term creates serious concurvity. Removing the shared trend and then concluding that GDP or population did not explain the decline is circular. The policy analysis is equally weak. It uses 378 models with arbitrary and overlapping windows. There is no adequate correction for multiple testing or credible causal counterfactual. The conclusions about climate, socioeconomic development, and policies go far beyond what these models can show.
3. The predictability comparison is not valid. Fatal-day counts have a much narrower distribution than fatality counts. They will naturally have lower negative log predictive scores, even without greater temporal predictability. The authors must compare each model against an appropriate climatological or negative-binomial baseline and report a normalized skill score. The entropy analysis is also unreliable with only 75 annual observations, especially after dividing the data into quantile states and using two lags. Important details are missing, including the number of states, bias correction, and bootstrap procedure. Finally, four evaluation years are not enough to validate the forecasts. Showing that four observations fall within very wide prediction intervals is not evidence of forecasting skill. The projections to 2030 are therefore not convincing.