the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
A Norwegian Approach to Downscaling
Rasmus E. Benestad
Abstract. A description of a comprehensive geoscientific downscaling model strategy is presented outlining an approach that has evolved over the last 20 years, together with an explanation for its development, its technical aspects, and evaluation scheme. This effort has resulted in an opensource and free Rbased tool, 'esd', for the benefit of sharing and improving the reproducibility of the downscaling results. Furthermore, a set of new metrics was developed as an integral part of the downscaling approach which assesses model performance with an emphasis on regional information for society (RifS). These metrics involve novel ways of comparing model results with observational data and have been developed for downscaling large multimodel global climate model ensembles. A literature search suggests that this comprehensive downscaling strategy and evaluation scheme are not widely used within the downscaling community. In addition, a new convention for storing large datasets of ensemble results that provides fast access to information and drastically saves data volume is explained.
Rasmus E. Benestad
Status: closed

RC1: 'Comment on gmd2021176', Anonymous Referee #1, 18 Oct 2021
Summary: The manuscript is a review of the statistical downscaling strategies followed by the author over the past decades, highlighting the differences to other mainstream approaches . This review also includes some related questions, such as strategies to archive data from ensemble of simulations that can be retrieved more efficiently.
Recommendation: I am rather sceptical about the added value of the manuscript. It is clearly a review  it does not contain original model or methodological descriptions  but being a review it focuses almost exclusively on the work done by the author. Even then, many of the descriptions/conclusions refer to a list of previous papers without offering deeper insight. Also, the reasoning concerning a few technical aspects is dubious. All in all, the manuscript to me rather reads like a project report or a report of a laboratory for an external evaluation  seasoned with a generous portion of selfpraise than a proper scientific paper . I provide more detailed justifications for this opinion in the following
1) Title: The title actually provides a good example of my concerns on the paper. It is clearly not informative about the contents  what should a reader interpret from 'Norwegian approach' ? I do not think that is a descriptive scientific term to inform the reader.
2) The abstract is also uninformative: on what is the downscaling method based? is it statistical or dynamical ? to what extent is it different or better ? is is applied to mean climate or to extremes ? The reader decides after reading the abstract whether the manuscript is useful for them, but this abstract does not provide any information towards that decision.
3) ' Long experience with both downscaling, and working with impacts and society, has shaped the typical Norwegian strategy for downscaling.'
Is that different from other approaches ? Other groups have also long experience and deal with impacts and society. .
4) 'The description of this experience serves as a stocktaking on where the science stands on downscaling in Norway,'
It seems that the work by the author is representative for whole Norway. I do not know if that is the case but is this relevant in a scientific paper ?
5) 'The latter take on downscaling also highlights the difference between downscaling and biasadjustment,'
This whole paragraph on biasadjustment is misplaced. Why focus precisely out of the blue on biasadjustment ? It is debatable whether biasadjustment is a type of downscaling.
6) The paragraph on common EOFs is, in my opinion, very weird:
' In spite of the success with utilising common EOFs, a Google scholar search on ’"common EOFs" downscaling’ only had 63 hits (of which about 40 referred to our own work), despite more than 20 years since they first were introduced in ESD and the widespread need for climate change adaptation and downscaled results. This surprising results suggests that they are not appreciated, and this is supported by the fact that common EOFs are not mentioned in text books such as Maraun and Widmann (2018).'
In my interpretation, the author assumes that common EOFs is a superior technique. It was presented by the author already in 2001, and used by the author and collaborators in following papers. However, the authors seems surprised that the scientific community as a whole has not applied his approach more often. I guess that a valid hypothesis to explain this discrepancy is that the scientific community does not share the author's opinion about the superiority of common EOFs.
7) ' It turns out that statistical properties are surprisingly predictable, are oftenstrongly connected to single predictor variables, and that predicting statistical properties tends to be more robust than predicting individual outcomes (Benestad and Mezghani, 2015;'
what does 'individual outcomes' mean in this context? climate downscaling is never about the prediction of individual events, but actually changes in the statistical properties, i.e. climate changes.
8) 'we tend to use multiple regression because parameters aggregated over seasonal scales tend to approximately follow the normal distribution according to the central limit theorem'
This is not true in general. The estimator of some statistical parameters are normally distributed, but not for others. For instance, the estimator of a variance cannot be normally distributed, and in a bayesian setting the prior for variance are other types of nonnormal distributions.
9) 'The median can only be an integer number (or halfway between two integer numbers), and is not
a pure rational number such as the mean spell length that is needed to represent the parameters of a pdf#
This sentence refers to the distribution of spelllengths. As such, any distribution has to be discrete, and therefore the median has to be an integer or the mean of two integers. What is wrong with that ? The mean is a different parameter, which may be more useful to write down an analytical expression for the pdf, but the median has other advantages, especially for the enduser. I do not really see the point of this paragraph
In addition, the mean of a discrete distribution can be a real number (also irrational), it does not need to be a 'pure rational' number' , whatever this means mathematically.
10) 'The statistics of maxima is often cluttered and involves a high degree of uncertainty, is not a
rational number,'
I do not understand this paragraph. The mean of the spelllength maximum in a sample of size L can be a real number as well . The mean is also a statistics. The author likely means, not the statistics, but one realization, and confounds both terms.
11) 'Strategy for storing large volumes of multimodel ensemble ESD output..'
I fail to see the direct link of this section to the other sections. In principle, the question of efficient archiving of data from ensemble of simulations is independent of 'downscaling', Moreover, this section only provides superficial information about how efficient this system is supposed to be, without explaining how. I think they reader will not gain very much from this section.
12) Hence, their results do strictly not represent the same aspects as those observed. RCMs nevertheless have great value in the context of experiments'
The same could be said of GCMs. GCMs are however considered to be the central tool for climate projections
13) 'Even the traditional EuroCORDEX RCM ensemble is a case of not using the right information in correct way, as all RCMs in the ensemble may have systematic biases with the same sign because of common physical inconsistencies in terms of OLR and common shortcomings in coupling with surface/ocean/lakes or treatment of aerosols'
This is a very sweeping and potentially very assertion, As in the previous point, the same can be said of CMIP5 and CMIP6. Each model have systematic biases, which possibly can be of the same sign, and common physical inconsistencies. Does this mean that the CMIP5 and CMIP6 ensemble is a 'case of not using the right information in a correct way`?.
14) 'These results are robust because they are derived from large multimodel ensembles of GCM simulations '
which is the conceptual difference between ensemble of simulations with GCMs and ensemble of simulations with RCMs ? I am really confused that in previous paragraphs, ensemble of RCMs are criticized because of model biases and inconsistencies, and ensemble of GCMs are considered free of those problems.
Citation: https://doi.org/10.5194/gmd2021176RC1 
AC1: 'Reply on RC1', Rasmus Benestad, 21 Oct 2021
The comment was uploaded in the form of a supplement: https://gmd.copernicus.org/preprints/gmd2021176/gmd2021176AC1supplement.pdf

AC1: 'Reply on RC1', Rasmus Benestad, 21 Oct 2021

RC2: 'Comment on gmd2021176', Anonymous Referee #2, 18 Oct 2021
Review of “A Norwegian Approach to Downscaling”, by R. E. Benestad
This paper summarizes a list of procedures for statistical downscaling of climate variables and advocates their use in the scientific community.
General remarks
This paper is filled with rhetoric and subjective statements, and, surprisingly, does not contain any new scientific advancement (which are left to already published papers). What is called a “Norwegian approach” seems to be exclusively developed and used by the author (as shown by the list of publications). As the author seems to criticize “mainstream approaches” (quotation marks and italics), this implies that the whole scientific community in Norway is tied to the work of one author, which I find rather contradictory and worrisome, with all due respect to my colleagues there. So, why this paper? The oneparagraph introduction does not provide any answer to this elementary question.
The paper tries to explain the divergence of the author’s work to what he calls “mainstream”. But what is mainstream? From what I understand, “mainstream” looks like every paper without Benestad as a coauthor, which might indeed sum up to many papers. This is not very informative. The author suggests that most (if not all) the climate community performs downscaling with regional climate models (RCMs) and is focused on CORDEX experiments. This sounds like a biased statement. CORDEX is a tool among others to provide normalized regional climate simulations. Many countries have their own regional climate simulations with spatial and temporal resolutions that far exceed those of CORDEX.
The fact that the author does not find selected keywords (e.g. “common EOF”) does not prove that there is no reference that use approaches that are similar to his. It suffices that other authors use a different terminology. Hence, the reasoning behind l. 80 is flawed.
The author never gives a precise definition (with equations) of “downscaling”. This implies that most of the statements in Secs. 2.1 – 2.6 are at most qualitative and subjective. If one writes down the mathematical challenge of downscaling, then climate research on this subject would be about outlining options to solve this challenge. I don’t see why there should be a “best” way, as the expectations of the outcome of downscaling might differ on the communities. If one acknowledges this elementary fact, then the rationale for this paper seems rather weak.
I am surprised that the author decides NOT to discuss the precise details of his approach in the paper (for GMD), which hence requires reading many other papers (some of which are not in open access). It is even unclear whether the reported results appear elsewhere. So, what is the purpose of peer review?
What is called the “Norwegian approach” seems to depend heavily on assumptions on the probability distribution of climate variables. The author then does “something” (that is not precisely described in the paper) to rectify the parameters of probability distributions from a large scale to a small scale. Fine. No explanation is provided on the time dependence of those parameters (neither short term or long term), although this should be the crux of a scientific paper. I do not see a discussion on intervariable dependence, which is also a major challenge of climate downscaling. Spatial dependence is not included in the procedure (it is just checked visually a posteriori).
The author does not try to compare his approach with other methods (dynamical or statistical), which is disappointing, as it would have given a concrete example of the advantage of using ‘esd’. One can also wonder whether the Scandinavian example was chosen because the author is satisfied by the results, although his satisfaction of Figure 5 is subjective: the fact that qqplots deviate from the 11 line might not be surprising but it contradicts Sec. 2.6 on extremes.
Specific remarks
The introduction looks like a biased statement of “stateoftheart”. The goal of the paper is not stated. The author lists keywords (dynamical downscaling, empiricalstatistical downscaling…) as if they were the only and exclusive pillars of downscaling.
l. 1214 (“The climatic conditions to which […] hazards”). This sentence is very strange. There is ample literature that show how some human societies have been affected (even collapsed) due to changes in climate features since prehistory. I do not see what kind of “new weatherrelated hazards” the author refers to. I do not think that the SREX (2012) mentions them.
The author mentions several types of downscaling approaches. Is this supposed to be exhaustive? There seems to be a continuum of approaches, that mix several types of data and paradigms. The “Norwegian approach” is one among many others.
Section 2.1: as long as what “mainstream” is NOT defined, sections 2.12.4 are rather obscure.
Section 2.2, l. 47: what does linear algebra here? Is it because you are working on vectors and matrices of numbers? Anybody who deals with vectors or matrices of numbers does linear algebra. This is not very informative.
l. 5055: Playing on words is not very helpful. Please state the mathematical formulas that are involved and how your approach differs. There are too many “ors” to be really rigorous.
I doubt that CORDEX can be considered as “mainstream” for downscaling.
l. 59: “Bias adjustment doesn’t involve the dependency between spatial scales […]”. Bias adjustment is a separate issue from downscaling. And there are bias adjustment methods that consider the dependency between spatial scales. The statement that “some will say that it gives the right answer for the wrong reason” sounds like slandering and dismisses the vast literature on bias correction and verification procedures.
Section 2.4, l. 115125: I understand that a choice is made to model temperature by a Gaussian distribution and precipitation by an exponential distribution. No information is given on the temporal dependence. Are the variables IID? If one is interested in temperature extremes, there is ample literature that shows that it is not Gaussian. The way the parameters of the statistical laws are “downscaled” is nowhere explained or discussed in the manuscript. The strategy of “keeping things simple and elegant (mathematical)” is barely reflected in the manuscript as no precise equation is given, especially for the rules of inferences. Wanting to keep things simple and elegant often leads to “spherical cows in vacuum”. Having a list of nine rather heterogeneous criteria of evaluation (Section 2.7) is neither simple nor elegant.
Section 2.6: If you model temperature with a Gaussian distribution and precipitation with an exponential distribution, it is very unlikely that extremes of temperature and precipitation are correctly inferred. Figure 5 is an elementary counter example of the title of this section.
Section 2.7, l. 192: what are GCM grids? How do “common EOFs” deal with biases in mean values between observations and GCMs?
Section 2.8: What is the point of this section? There is no description of the method to store files, just an unverifiable statement that it is better than netcdf. Figure 6 does not demonstrate anything on the storage method.
Section 3 (conclusion): The threeparagraph conclusion leaves me still confused. What makes the author believe of “silo thinking”.
Citation: https://doi.org/10.5194/gmd2021176RC2 
AC2: 'Reply on RC2', Rasmus Benestad, 21 Oct 2021
The comment was uploaded in the form of a supplement: https://gmd.copernicus.org/preprints/gmd2021176/gmd2021176AC2supplement.pdf

AC2: 'Reply on RC2', Rasmus Benestad, 21 Oct 2021
Status: closed

RC1: 'Comment on gmd2021176', Anonymous Referee #1, 18 Oct 2021
Summary: The manuscript is a review of the statistical downscaling strategies followed by the author over the past decades, highlighting the differences to other mainstream approaches . This review also includes some related questions, such as strategies to archive data from ensemble of simulations that can be retrieved more efficiently.
Recommendation: I am rather sceptical about the added value of the manuscript. It is clearly a review  it does not contain original model or methodological descriptions  but being a review it focuses almost exclusively on the work done by the author. Even then, many of the descriptions/conclusions refer to a list of previous papers without offering deeper insight. Also, the reasoning concerning a few technical aspects is dubious. All in all, the manuscript to me rather reads like a project report or a report of a laboratory for an external evaluation  seasoned with a generous portion of selfpraise than a proper scientific paper . I provide more detailed justifications for this opinion in the following
1) Title: The title actually provides a good example of my concerns on the paper. It is clearly not informative about the contents  what should a reader interpret from 'Norwegian approach' ? I do not think that is a descriptive scientific term to inform the reader.
2) The abstract is also uninformative: on what is the downscaling method based? is it statistical or dynamical ? to what extent is it different or better ? is is applied to mean climate or to extremes ? The reader decides after reading the abstract whether the manuscript is useful for them, but this abstract does not provide any information towards that decision.
3) ' Long experience with both downscaling, and working with impacts and society, has shaped the typical Norwegian strategy for downscaling.'
Is that different from other approaches ? Other groups have also long experience and deal with impacts and society. .
4) 'The description of this experience serves as a stocktaking on where the science stands on downscaling in Norway,'
It seems that the work by the author is representative for whole Norway. I do not know if that is the case but is this relevant in a scientific paper ?
5) 'The latter take on downscaling also highlights the difference between downscaling and biasadjustment,'
This whole paragraph on biasadjustment is misplaced. Why focus precisely out of the blue on biasadjustment ? It is debatable whether biasadjustment is a type of downscaling.
6) The paragraph on common EOFs is, in my opinion, very weird:
' In spite of the success with utilising common EOFs, a Google scholar search on ’"common EOFs" downscaling’ only had 63 hits (of which about 40 referred to our own work), despite more than 20 years since they first were introduced in ESD and the widespread need for climate change adaptation and downscaled results. This surprising results suggests that they are not appreciated, and this is supported by the fact that common EOFs are not mentioned in text books such as Maraun and Widmann (2018).'
In my interpretation, the author assumes that common EOFs is a superior technique. It was presented by the author already in 2001, and used by the author and collaborators in following papers. However, the authors seems surprised that the scientific community as a whole has not applied his approach more often. I guess that a valid hypothesis to explain this discrepancy is that the scientific community does not share the author's opinion about the superiority of common EOFs.
7) ' It turns out that statistical properties are surprisingly predictable, are oftenstrongly connected to single predictor variables, and that predicting statistical properties tends to be more robust than predicting individual outcomes (Benestad and Mezghani, 2015;'
what does 'individual outcomes' mean in this context? climate downscaling is never about the prediction of individual events, but actually changes in the statistical properties, i.e. climate changes.
8) 'we tend to use multiple regression because parameters aggregated over seasonal scales tend to approximately follow the normal distribution according to the central limit theorem'
This is not true in general. The estimator of some statistical parameters are normally distributed, but not for others. For instance, the estimator of a variance cannot be normally distributed, and in a bayesian setting the prior for variance are other types of nonnormal distributions.
9) 'The median can only be an integer number (or halfway between two integer numbers), and is not
a pure rational number such as the mean spell length that is needed to represent the parameters of a pdf#
This sentence refers to the distribution of spelllengths. As such, any distribution has to be discrete, and therefore the median has to be an integer or the mean of two integers. What is wrong with that ? The mean is a different parameter, which may be more useful to write down an analytical expression for the pdf, but the median has other advantages, especially for the enduser. I do not really see the point of this paragraph
In addition, the mean of a discrete distribution can be a real number (also irrational), it does not need to be a 'pure rational' number' , whatever this means mathematically.
10) 'The statistics of maxima is often cluttered and involves a high degree of uncertainty, is not a
rational number,'
I do not understand this paragraph. The mean of the spelllength maximum in a sample of size L can be a real number as well . The mean is also a statistics. The author likely means, not the statistics, but one realization, and confounds both terms.
11) 'Strategy for storing large volumes of multimodel ensemble ESD output..'
I fail to see the direct link of this section to the other sections. In principle, the question of efficient archiving of data from ensemble of simulations is independent of 'downscaling', Moreover, this section only provides superficial information about how efficient this system is supposed to be, without explaining how. I think they reader will not gain very much from this section.
12) Hence, their results do strictly not represent the same aspects as those observed. RCMs nevertheless have great value in the context of experiments'
The same could be said of GCMs. GCMs are however considered to be the central tool for climate projections
13) 'Even the traditional EuroCORDEX RCM ensemble is a case of not using the right information in correct way, as all RCMs in the ensemble may have systematic biases with the same sign because of common physical inconsistencies in terms of OLR and common shortcomings in coupling with surface/ocean/lakes or treatment of aerosols'
This is a very sweeping and potentially very assertion, As in the previous point, the same can be said of CMIP5 and CMIP6. Each model have systematic biases, which possibly can be of the same sign, and common physical inconsistencies. Does this mean that the CMIP5 and CMIP6 ensemble is a 'case of not using the right information in a correct way`?.
14) 'These results are robust because they are derived from large multimodel ensembles of GCM simulations '
which is the conceptual difference between ensemble of simulations with GCMs and ensemble of simulations with RCMs ? I am really confused that in previous paragraphs, ensemble of RCMs are criticized because of model biases and inconsistencies, and ensemble of GCMs are considered free of those problems.
Citation: https://doi.org/10.5194/gmd2021176RC1 
AC1: 'Reply on RC1', Rasmus Benestad, 21 Oct 2021
The comment was uploaded in the form of a supplement: https://gmd.copernicus.org/preprints/gmd2021176/gmd2021176AC1supplement.pdf

AC1: 'Reply on RC1', Rasmus Benestad, 21 Oct 2021

RC2: 'Comment on gmd2021176', Anonymous Referee #2, 18 Oct 2021
Review of “A Norwegian Approach to Downscaling”, by R. E. Benestad
This paper summarizes a list of procedures for statistical downscaling of climate variables and advocates their use in the scientific community.
General remarks
This paper is filled with rhetoric and subjective statements, and, surprisingly, does not contain any new scientific advancement (which are left to already published papers). What is called a “Norwegian approach” seems to be exclusively developed and used by the author (as shown by the list of publications). As the author seems to criticize “mainstream approaches” (quotation marks and italics), this implies that the whole scientific community in Norway is tied to the work of one author, which I find rather contradictory and worrisome, with all due respect to my colleagues there. So, why this paper? The oneparagraph introduction does not provide any answer to this elementary question.
The paper tries to explain the divergence of the author’s work to what he calls “mainstream”. But what is mainstream? From what I understand, “mainstream” looks like every paper without Benestad as a coauthor, which might indeed sum up to many papers. This is not very informative. The author suggests that most (if not all) the climate community performs downscaling with regional climate models (RCMs) and is focused on CORDEX experiments. This sounds like a biased statement. CORDEX is a tool among others to provide normalized regional climate simulations. Many countries have their own regional climate simulations with spatial and temporal resolutions that far exceed those of CORDEX.
The fact that the author does not find selected keywords (e.g. “common EOF”) does not prove that there is no reference that use approaches that are similar to his. It suffices that other authors use a different terminology. Hence, the reasoning behind l. 80 is flawed.
The author never gives a precise definition (with equations) of “downscaling”. This implies that most of the statements in Secs. 2.1 – 2.6 are at most qualitative and subjective. If one writes down the mathematical challenge of downscaling, then climate research on this subject would be about outlining options to solve this challenge. I don’t see why there should be a “best” way, as the expectations of the outcome of downscaling might differ on the communities. If one acknowledges this elementary fact, then the rationale for this paper seems rather weak.
I am surprised that the author decides NOT to discuss the precise details of his approach in the paper (for GMD), which hence requires reading many other papers (some of which are not in open access). It is even unclear whether the reported results appear elsewhere. So, what is the purpose of peer review?
What is called the “Norwegian approach” seems to depend heavily on assumptions on the probability distribution of climate variables. The author then does “something” (that is not precisely described in the paper) to rectify the parameters of probability distributions from a large scale to a small scale. Fine. No explanation is provided on the time dependence of those parameters (neither short term or long term), although this should be the crux of a scientific paper. I do not see a discussion on intervariable dependence, which is also a major challenge of climate downscaling. Spatial dependence is not included in the procedure (it is just checked visually a posteriori).
The author does not try to compare his approach with other methods (dynamical or statistical), which is disappointing, as it would have given a concrete example of the advantage of using ‘esd’. One can also wonder whether the Scandinavian example was chosen because the author is satisfied by the results, although his satisfaction of Figure 5 is subjective: the fact that qqplots deviate from the 11 line might not be surprising but it contradicts Sec. 2.6 on extremes.
Specific remarks
The introduction looks like a biased statement of “stateoftheart”. The goal of the paper is not stated. The author lists keywords (dynamical downscaling, empiricalstatistical downscaling…) as if they were the only and exclusive pillars of downscaling.
l. 1214 (“The climatic conditions to which […] hazards”). This sentence is very strange. There is ample literature that show how some human societies have been affected (even collapsed) due to changes in climate features since prehistory. I do not see what kind of “new weatherrelated hazards” the author refers to. I do not think that the SREX (2012) mentions them.
The author mentions several types of downscaling approaches. Is this supposed to be exhaustive? There seems to be a continuum of approaches, that mix several types of data and paradigms. The “Norwegian approach” is one among many others.
Section 2.1: as long as what “mainstream” is NOT defined, sections 2.12.4 are rather obscure.
Section 2.2, l. 47: what does linear algebra here? Is it because you are working on vectors and matrices of numbers? Anybody who deals with vectors or matrices of numbers does linear algebra. This is not very informative.
l. 5055: Playing on words is not very helpful. Please state the mathematical formulas that are involved and how your approach differs. There are too many “ors” to be really rigorous.
I doubt that CORDEX can be considered as “mainstream” for downscaling.
l. 59: “Bias adjustment doesn’t involve the dependency between spatial scales […]”. Bias adjustment is a separate issue from downscaling. And there are bias adjustment methods that consider the dependency between spatial scales. The statement that “some will say that it gives the right answer for the wrong reason” sounds like slandering and dismisses the vast literature on bias correction and verification procedures.
Section 2.4, l. 115125: I understand that a choice is made to model temperature by a Gaussian distribution and precipitation by an exponential distribution. No information is given on the temporal dependence. Are the variables IID? If one is interested in temperature extremes, there is ample literature that shows that it is not Gaussian. The way the parameters of the statistical laws are “downscaled” is nowhere explained or discussed in the manuscript. The strategy of “keeping things simple and elegant (mathematical)” is barely reflected in the manuscript as no precise equation is given, especially for the rules of inferences. Wanting to keep things simple and elegant often leads to “spherical cows in vacuum”. Having a list of nine rather heterogeneous criteria of evaluation (Section 2.7) is neither simple nor elegant.
Section 2.6: If you model temperature with a Gaussian distribution and precipitation with an exponential distribution, it is very unlikely that extremes of temperature and precipitation are correctly inferred. Figure 5 is an elementary counter example of the title of this section.
Section 2.7, l. 192: what are GCM grids? How do “common EOFs” deal with biases in mean values between observations and GCMs?
Section 2.8: What is the point of this section? There is no description of the method to store files, just an unverifiable statement that it is better than netcdf. Figure 6 does not demonstrate anything on the storage method.
Section 3 (conclusion): The threeparagraph conclusion leaves me still confused. What makes the author believe of “silo thinking”.
Citation: https://doi.org/10.5194/gmd2021176RC2 
AC2: 'Reply on RC2', Rasmus Benestad, 21 Oct 2021
The comment was uploaded in the form of a supplement: https://gmd.copernicus.org/preprints/gmd2021176/gmd2021176AC2supplement.pdf

AC2: 'Reply on RC2', Rasmus Benestad, 21 Oct 2021
Rasmus E. Benestad
Data sets
A Norwegian approach to downscaling Rasmus Benestad https://doi.org/10.6084/m9.figshare.14922837.v1
Model code and software
A Norwegian approach to downscaling Rasmus Benestad https://doi.org/10.6084/m9.figshare.14922837.v1
Video supplement
A comprehensive downscaling strategy for climate change adaptation Rasmus Benestad https://youtu.be/yEtyU37Zvj4
Rasmus E. Benestad
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