The authors present a study titled "Integrating flood-induced population movements into future flood damage estimates in Japan." The manuscript introduces a novel framework for quantifying and predicting population relocation in response to flood events, incorporating climate change effects, to evaluate future population distribution and flood risk in Japan. Overall, I find the study to be well-constructed and the manuscript clearly written. The integration of statistical causal inference with long-term land-use and population projections offers a valuable contribution to socio-hydrological modeling. However, I have identified several critical areas regarding spatial resolution, flood typology, and the modeling of relocation "pull" factors that warrant further attention. I am recommending major revisions to address these methodological limitations and scope concerns. Pending these revisions, I believe the manuscript would be a strong candidate for publication in Natural Hazards and Earth System Sciences (NHESS).

1. Methodological Detail (Line 295): The authors cite Yanagihara et al. (2024) for the fluvial flood damage model. However, the current manuscript lacks sufficient detail regarding this model’s internal mechanics. Please include a concise summary of the model’s core equations or assumptions to ensure the reader can follow the assessment without referring exclusively to prior work.
2. Flood Typology and Title: The study focuses exclusively on fluvial flooding. Given the significance of pluvial and coastal flooding in Japan, the title should be more specific. In the title, I suggest changing "future flood damage" to "future fluvial flood damage" with corresponding adjustments in the Abstract and throughout the text to avoid over-generalization.
3. Spatial Resolution: The use of a 250 m flood grid is relatively coarse for a national-scale study seeking municipal-level precision. This resolution likely misses localized flood risks and micro-topographical features that influence individual relocation decisions. This should be addressed as a limitation in Section 6.3.
4. Multimodal Flooding Impacts: The observational dataset used to quantify FIPMs includes residents affected by various water-related disasters (pluvial, coastal, etc.), yet the predictive model only simulates fluvial events. The authors should discuss the net effect of this discrepancy near Line 375 and in the limitations. Specifically, how does the exclusion of pluvial and coastal flood projections affect the estimated impact of FIPMs the results of the study?
5. "Pull" Factors and Relocation Dynamics: The current framework assumes that populations relocate proportionally to existing density. In reality, migration is driven by specific "pull" factors such as employment hubs and family networks—as seen in historical precedents like Hurricane Katrina in the USA, where displacement from New Orleans was highly concentrated in specific regions (e.g., Houston) rather than dispersed uniformly. This simplification should be explicitly noted as a limitation in Section 6.3.
6. Temporal Resolution and Validation Discrepancy: Since the model relies on 5-year census data, it inherently captures long-term permanent displacement while overlooking short-term movements. This temporal mismatch may explain the significant discrepancy between the model’s 2020 estimate (~16,000 movements) and the IDMC data (~212,000 movements). This distinction between "forced displacement" and "permanent migration" needs a more thorough treatment in the Discussion.
7. Code and Data Availability: The current statements stating "available upon request" do not appear to meet the journal's submission guidelines (https://www.natural-hazards-and-earth-system-sciences.net/submission.html). The authors must deposit the underlying research data and code in a public repository or provide a formal explanation as to why it cannot be made publicly accessible.

Thank you for the opportunity to review this manuscript. The study aims to estimate the impact of two flood events on population movements in Japan, with the goal of assessing the effectiveness of flood mitigation strategies. Overall, the manuscript is well written and addresses an interesting and relevant research question. The empirical approach is generally sound, but I do have some concerns and suggestions for improvement.

Below I provide several comments that could improve the paper. These points are presented in no particular order.

1. My main concern relates to the timing of the analysis. The flood events occurred in 2019 and 2020, while population data are observed from 2005 to 2020 in five-year intervals. As a result, the study can only capture very short-term population movements in response to the floods. Since migration and population adjustments often occur gradually, it would be more informative to examine longer-term effects, for example by including population data for the period after 2020 (e.g., 2020–2025) if such data become available. As it stands, the analysis likely captures only immediate or short-run effects. This limitation also raises some concerns about the usefulness of conducting projections over several decades based on these short-term responses.
2. The Introduction is well written and clearly outlines the research problem. However, the empirical strategy, namely the use of a difference-in-differences (DiD) approach, is not sufficiently introduced or motivated. It would be helpful if the authors explained why they chose a DiD framework and whether alternative empirical approaches could have been used. Placing the chosen method more explicitly within the existing literature would improve the paper.
3. It would be useful to clarify earlier in the Introduction that the analysis focuses on only two flood events. When reading the Introduction, I initially expected a broader analysis of the effects of floods on population movements across Japan, whereas the study is in fact closer to a case study. In addition, a map showing the locations of the flood events would be helpful. Then we could also see whether the affected areas overlap because I was wondering this when reading the manuscript.
4. A large part of the methodology is devoted to explaining the variables, coefficients and fixed effects, which makes the paper somewhat difficult to follow. I would encourage the authors to have another look at the equations and see where they can simplify the notation. For example, \delta_{bf}^{mun} R_{i’, t’, g’}^{bf} is not very readable. The equations might become clearer if the authors use simpler notation for coefficients, such as \beta_{0}, \beta_{1} and \beta_{2}, and call the variables BF, AF and CD, for example. Reducing the number of subscripts and superscripts would likely improve readability. Another suggestion would be to present the variables, coefficients, and fixed effects in a table or in a bullet-point list, so that the reader has a more clear overview.
5. In Equations (1) and (2), the authors include a time trend for each cross-sectional unit (grid cells in Equation 1 and municipalities in Equation 2). At the same time, the paper emphasizes the importance of satisfying the parallel trends assumption so that the estimated effect can be attributed to the flood rather than to other factors. The manuscript presents evidence suggesting that the parallel trends assumption holds. Given this, it is unclear why unit-specific time trends are still included in the regression. While the supplementary information cites one study that adopts a similar specification, this alone does not justify the modeling choice. I would like to see a clearer rationale for including these trends, or even better, a robustness check presenting results without the unit-specific time trends, especially since time fixed effects are already included.
6. Equations (3), (4), and (5) are also somewhat difficult to follow. The notation b,c = {1,2,3,4,5} is not immediately clear. It might be simpler and more transparent to refer directly to the corresponding years instead of using index notation.