The manuscript is well written and the topic relevant to this journal. The source data is adequate to the needs. Overall, I find the study needs some revisions before it is considered for publication. Please see below my main comments. Should I have misinterpreted some points, I will be happy to discuss them further with the authors.

Kind regards,

Francesco Marra

Main points:

1. Underlying assumptions.
   
   - The authors seem to start from the assumption that increasing DDF with area are “implausible” (e.g. see the introduction or line 242: “as the area increases the areal precipitation depth must decrease”). While this is generally what one expects from a statistical perspective, it strictly holds only under spatial stationarity. There exist situations in which this can be not the case - e.g. see Mélèse et al. 2019 (https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2018WR024368). Results in fig. 8 do not show any pattern, but I think some words on this aspect would be useful.
   
   - The second assumption seems to be that the crossings are mainly due to sampling issues. This seems however in contradiction with some of the results: in lines 288-289, it is observed that “in summer the number of locations with crossings is smaller than in winter”. Spatial sampling issues are expected to be more important for events with small space-time scales, such as summer events that are more often convective in nature, rather than winter events. How is this reconciled with the second assumption above?
   
   - In lines 80-081, it is claimed that “we investigate the spatial order relation problems, appearing as crossings in ADDF curves, which lead to missing information in areal rainfall extreme value analysis and underestimation of design storms”. This sentence seems to assume that missing a storm leads to underestimation of the statistics. From a population perspective, “missing” a particular storm is part of the local climatology (the event did not hit the place of interest). The problem arises when the sample at hand is limited and the missing may be considered a statistical outlier. This leads to the question: how much is the problem related to use of a the block maxima approach and how much is it general?
2. Sampling methods.
   
   I had some concerns with the MLES and SLES sampling methods, in which a maximum in space of maxima in time is extracted, because of the different sample size at different durations. Intuitively, this would lead to higher chances of having a large value in the small scales (more samples). I am proven wrong by figure 13, at least for the MLES sampling method. I’d be happy to see some discussion on this aspect.
3. Quantitative accuracy. 
   
   Comparing fig 5 with fig 9, 10, and 11 shows huge differences between the quantities estimated in several locations. For example, in loc26, the 1 km2 scale at 5 minutes changes from 10 mmm to 30 mm in the MLS and SLES (3x more). This is even larger (~4x more) in loc92 and even more for the MLES method in fig 10 (almost 6x more).  How can all these estimate make sense? Which ones make more sense from a quantitative perspective? The answer to these questions is only provided in the discussion (section 5.3). In my view, this should be the first comparison to be shown across the different sampling methods (in the results and before figures 9—11. For the same reasons, I suggest to include KOSTRA estimates in Fig 14a (1 km2).
4. Uncertainty.
   
   - Figure 13 shows that MLES seems the optimal sampling method on average, although a very large variability in the results is observed. This could be due to a larger uncertainty related to this method.
   
   - There is no quantification of estimation uncertainty with any of the methods. This is an essential component of DDF and ADDF curves and should accompany the design values that are provided.
   
   - Uncertainty could be one of the reasons behind the observed crossings. For example, it could be that several of the crossing lines are within each other’s uncertainty, thereby indicating that in some occasions, crossing may just be due to uncertainty (e.g. loc26 in figure 9 could well be the case). This for example was shown by Rosin et al. 2024 (cited in the manuscript). This option would be supported by the absence of clear patterns in Fig 8.
   
   - Should this be part of the reasons behind the crossings, it would be natural to ask in what proportion this may be related to the used method (here, Koutsoyiannis 1998). Could another method that already prescribes no-crossings be preferred? There are several used in ARF estimation that can be extended to the duration-area problem - e.g., De Michele et al 2001 (https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2001WR000346)
5. Previous literature.
   
   - Line 85: “To our knowledge, there are no studies investigating the spatial order problem in detail and offering new sampling methods.” I believe something is out there, for example Goudenhoofdt et al. 2017 (https://doi.org/10.5194/hess-21-5385-2017) and Poschmann et al 2021 (https://nhess.copernicus.org/articles/21/1195/2021/). I invite the authors to discuss their method in comparison to the ones proposed here.
   
   - Some parts of the manuscript (fig 6 and lines 297-303) reminded me of a paper by Peleg et al. 2018 (http://doi.org/10.1016/j.jhydrol.2016.05.033) in which small scale variability of extremes was quantified and compared in terms of the resulting areal estimate. The discussion in said paper may be relevant to the interpretation of this study.
6. Codes availability.
   
   Given HESS policy on the matter, I encourage the authors to submit the codes to an open repository for public use. A final opinion on the matter is left to the editor.

Minor points:

• Lines 120-121: traditionally, Marshall-Palmer is used to indicate a power law relation in which the parameters are 200 and 1.6 (e.g. see Uijlenhoet, 2001, https://doi.org/10.5194/hess-5-615-2001). I suggest to use a term such as “power-law” relation or similar.
• Line 125: some additional details on the merging would be helpful. What data is used? How is the merging handled in ungauged locations? The reference is there but some basic details are needed - especially since you later provide the validation, which makes me think this operation is done on this data by this study and not in the reference.
• Figure 2:
  
  - what return level is shown in the figures? The caption does not say it. Is this behaviour consistent with across return levels?
  
  - Caption: These are technically DDF (not IDF) as the displayed value is rainfall depth
  
  - The two examples shown in the figure display an overestimation of the radar values. This is different from what reported by several studies and in agreement with some other (e.g. see the references in Marra et al 2019, https://doi.org/10.1016/j.jhydrol.2019.04.081). I think a comment on the potential sources of this overestimation should be provided.
• Equations 2: it seems a division by n_gauge is missing (I guess this wants to be the average?)
• Equation 3: it seems a division by n_gauge is missing from inside the square root and from the denominator. If not, I believe the metric is not actually what one expects as a normalised RMSE
• Figure 3: it would be interesting to check whether there is any systematic deviation of RMSE and Bias with return period. The boxplots now merge all the probabilities and do not allow for these interpretations
• Lines 143-144: I suggest to explain the meaning of these metrics (e.g. RMSE is 20% of the estimtated value and percent bias shows ~6% underestimation)
• Line 161-162: please refer to section 3.1 where the method is presented.
• Line 163-164: I am not sure the plotting is part of the ADDF computation procedure. Perhaps this part should not be a numerated item.
• Lines 170-179: it seems the subscript a in i_a,d is lost somewhere between eq 8 and 9. Is each area treated independently and Koutsoyianis method is used only for handling multiple durations? A reader not familiar with this method would probably get lost here.
• Lines 186-186: this is indeed the advantage of such an approach. I guess this also comes with some limitations as annual maxima from many durations are highly correlated, so the actual information contained in the data is less than what it would be in case of independence. This is likely enhanced by the inclusion of the areal averaging. I believe a comment could be useful here.
• Lines 187-188: please explain why the method of the L-moments is used. Usually it is preferred in the case of limited data samples, but after the Koutsoyiannis normalisation the sample becomes relatively large. Is it a matter of computation costs with respect to maximum likelihood, or is it still a matter of sample numerosity?