Long-Term Changes, Inter-Annual, and Monthly Variability of Sea Level at the Coasts of the Spanish Mediterranean and the Gulf of Cádiz

Round 1

Reviewer 1 Report

Review of « Long-term changes in inter-annual variability of sea level at the coasts of the Spanish Mediterranean and the Gulf of Cadiz” by Vargas-Yanez et al.

 

The paper investigates the sea level changes from tide gauge records for the Spanish coasts and the Gulf of Cadiz since 1880 at the earliest. As mentioned by the authors, investigating regional sea level changes is more relevant than the global mean sea level rise as people are living near the coasts. The authors investigate the contribution of atmospheric pressure, wind changes and temperature/salinity contributions to local sea level changes based on tide gauge records.

 

The study is promising as the method is original and the results might be useful for the scientific community. However, at the moment, I am not positive about this work as I have the feeling that it has been botched. The paper lacks of clarification on the method section. The result section is too short and the authors have to elaborate significantly this part of the manuscript. For instance, the authors have 1) to describe the individual plots to help the reader to understand, 2) to interpret their results. Right now, this is too implicit.

The discussion and summary part contains also results that are not included in the results’ sections. Overall, the paper is not easy to follow and is not well articulated. The paper lacks of clarity as well. For instance, the authors do not mention the time period considered for computing the seasonal cycle, the correlation coefficients, etc. This is a problem as these parameters are highly dependent of the considered time period.

 

In my opinion, the paper is not ready for possible publication. I encourage, however, the authors to follow my comments for a possible resubmission

 

 

 

Major comments

 

• The red boxes presented in Figure 1 are selected to have T/S profiles. Are you actually getting the real T/S profiles or just the T/S gridded fields from the optimal interpolation from EN4 (good et al., 2013)? As I understand, you are getting the gridded fields. This point is crucial if you are considering the T/S gridded fields, this means that the T/S data you retrieve might be the first guess (seasonal cycle mainly) of your optimal interpolation method instead of real T/S profiles. EN4 dataset provides along with the T/S gridded fields the used profiles. Please, have a look on the T/S profile distribution specially for your red boxes.

 

• The title mentions that the inter-annual and long-term sea level changes are investigating. The method describes tide gauge data reconstruction and steric change at a monthly basis. This means that you are accounting for sub-annual and seasonal sea level changes. You should rewrite the title which is misleading at that time.

 

• The authors consider that the vertical land movements are only due to GIA trends. This is a strong hypothesis as tectonics (or other processes) might be another possible candidate for VLM at the tide gauge stations. Why don’t you compare the TG data with satellite altimetry (since August 1992) to validate that the VLM is only due to GIA? Or, don’t you have any GPS data co-localized at the TG station to remove the entire VLM signal? This should be clarified in the manuscript. Comparing TG and satellite altimetry might give you confidence in your results.

 

• The authors only consider the NCEP data for atmospheric parameters. Why don’t you use ERA interim, MERRA or other dataset to test the sensitivity of your results?

 

• Since 2015-2016, some Argo floats present spurious behavior with the salinity data with a drift towards saltier values. EN4 S gridded fields contain such saltier data (Ponte et al., GRL, 2021; Barnoud et al, GRL, 2021). How confident are you for your results after 2016 regarding this problem?

 

• Figure6 and Figure7 do not show very good agreements from observed and predicted sea level change. What are the explained variance values for Cadiz, Tarif, Alegeciras, Ceuta, Malaga and Alicante out? The quality of all the monthly time series are not good enough for any possible judgement. Please, replot them in another manner.

 

 

Below are some minor comments

 

Abstract: Why don’ t you state the main findings of your study ?

 

L 39-30: The authors probably mean the global mean sea level. This sentence is too implicit, please clarify it.

 

L30-31 : The authors are implicitly talking about regional variability. This should be stated clearly. The 2 sentences are too vague for me.

 

L30 : Please, cite all the factors influencing regional sea level change. You are omitting heat fluxes (solar and long wave radiations), air-sea turbulent fluxes, P-E, etc. The introduction deserves more precision.

 

L37: Add these papers: Llovel et al 2009; Church and White 2006

 

Table 1 is not easy to read/analyze. Please, find an alternative way to present it.

 

L119: how do you remove the annual signal. Please, clarify. And opver which time period ?

 

L139 : “After visual inspection, year 2018 ….”. What do you find for this time series? Please, clarify.

L140-142: Provide some statistics to quantify the validation of the interpolation method.

L176 : Provide the entire time period’ from Jan. 1948 to ….”

L181: “Strait of “ instead of “Starit of …”. Please, correct.

L198: “corrected from land movement”. As I understand you only consider GIA for vertical land movement. How about tectonics? You should compare the TG data to satellite altimetry data to see if the GIA is the only candidate for VLM of your TG stations.

L204: ‘long term mean value for rho surface’ : which period do you consider exactly ?

 

L207-210 : Did you check if steric sea level is equal to thermosteric and halosteric ? Because of the non-linearity of the equation of state of sea water, this might not be the case.

 

L237: is not it ‘1945-2018’ instead of ‘1940-2018’ ?

 

L248-255: This section deserves more details as the methodology might not be known by the readers. Please, clarify.

 

L258-264: Do you have any idea why the SL peaks in Oct-Nov ? as the steric sea level for the annual signal ? See Gill and Nihler 1973 for a possible explanation.

~90% of the seasonal sea level is due to net heat flux (Qnet) and warms the ocean surfaces. Therefore, this is traduced by an increase of steric seasonal sea level. As Qnet is maximum in may-June, you have some delay before the seasonal sea level peaks.

 

L266-269 : and so what ?

 

L452: Explain how you derive the theoretical value for atmospheric pressure.

 

Comments for author File: Comments.pdf

Author Response

Reviewer #1

 

First of all we would like to thank the reviewer for a very exhaustive and constructive review. We have followed most of his/her suggestions and honestly believe that the manuscript has improved considerably.

The reviewer considers in the general comments that the manuscript lacks of clarification in several parts, mainly in the method section which is too short. The periods considered for the calculation of seasonal cycles, trends or correlations are not always included. Results and discussion need clarification.

 

We agree with the reviewer and have tried to follow this suggestion. The methodology used should be explained clearly in such a way that any reader could easily follow the manuscript. Nevertheless, the detailed explanation of the multiple linear regression, the forward stepwise regression, etc. could make the manuscript a heavy reading. To solve this question we have included a "supplementary material" where these statistical techniques are described in detail. The information concerning the calculation of the seasonal cycles and the procedure to de-season the time series is explained in the main text, but we have also included it in the supplementary material.

On the other hand, the information about the period of time used for the calculation of all the correlations and seasonal cycles, or trends has been included in the new version of the manuscript.

 

Major comments.

The reviewer expresses some concerns about the use of the gridded product of EN4.

 

We agree with the reviewer. When data are scarce, the interpolated field is simply the background field or first guess that usually reproduce the climatological or average seasonal cycle. Nevertheless, it should be considered that the time series of thermosteric and halosteric components of sea level have been de-seasoned. If the gridded fields simply express the seasonal cycle, because of the lack of data, the de-seasoned time series will be close to zero and will not be able to explain the variability of the observed sea level. This will decrease the significance of the linear model. If this problem was caused by the data scarcity as several works have already shown, using real TS profiles instead of interpolated products would not solve it. On the other hand, the problem could be caused by the methodology used to obtain the gridded product. For this reason we have also used the gridded product from the NCAR/UCAR, to check if our results were sensitive to the data set used. We found no main differences and therefore we are confident about the use of the EN4 or the NCAR/UCAR products.

Another very interesting question is that probably both data sets have the problem of the data scarcity. But this cannot be solved for the past, although it should considered in order to sustain and improve present observing systems.

The reviewer considers that the title is not appropriate, as the manuscript deals with monthly variability, and this is not reflected in the title.

 

We agree with the reviewer. In fact, the linear model obtained by means of forward stepwise regression relates the monthly variability of sea level with that of the atmospheric variables and the steric contributions. We have followed this suggestions and changed the title to include "monthly variability".

 

The reviewer says that the only land movement considered is GIA. He/she also suggest to use altimetry data for comparison with tide gauge data.

 

The reviewer is right. To our knowledge the tide gauges used are not equipped with GPS. Nevertheless, sea level data have a local reference and possible land movements are supposed to be corrected by means of leveling surveys. Therefore, GIA should be the main problem. The comparison with satellite data is a very good idea, although we think that it could be the subject of a new (near future) manuscript, because, in our opinion, this comparison with local tide gauge data, is not a direct comparison (open sea versus local coastal data). We appreciate the recommendation of the reviewer.

 

The reviewer expresses some concerns about the agreement between the linear model and the observed sea level. He/she also considers the possibility of using other data sets for the calculation of meteorological variables.

 

Certainly, there are periods when the agreement between the model and the observations is not very good. Nevertheless, the multiple correlation coefficient is between 0.57 and 0.72 for the period 1948-2018, and increases for the period 1990-2018. We consider that the model is better as more data are available. We also think that this is the reason why the agreement between model and observations is especially good at L'Estartit for the period 1990-2018 when the correlation coefficient is 0.87. This is an area intensively monitored. The problem of the scarcity of data has already been evidenced by Vargas-Yáñez et al. (2021) and Jordà and Gomis (2013b) which are referenced in the present work, or by Llasses et al. (2015; Climate Res., 63, 1-18) or Vargas-Yáñez et al. (2010; J. Geophys. Res., 115, C04001). Some of these works have already addressed the problem of comparing different data sets or different methodologies. Once again we accept the reviewer's comment. It could be a good idea to continue this work in the direction proposed, but we think that it would be too much information and a very long work if included in the present manuscript.

 

Abstract: Why don’ t you state the main findings of your study ?

 

We have followed this suggestion and re-written the abstract.

 

L 39-30: The authors probably mean the global mean sea level. This sentence is too implicit, please clarify it.

L30-31 : The authors are implicitly talking about regional variability. This should be stated clearly. The 2 sentences are too vague for me.

 

Ok! We have followed these two suggestions and make it clear in the new redaction when we are talking about global mean sea level and when about regional variability.

 

 

L30 : Please, cite all the factors influencing regional sea level change. You are omitting heat fluxes (solar and long wave radiations), air-sea turbulent fluxes, P-E, etc. The introduction deserves more precision.

 

Ok! We have included the heat fluxes as one of the main factors contributing to sea level variability.

 

L37: Add these papers: Llovel et al 2009; Church and White 2006

 

Ok! We have included these two references.

 

Table 1 is not easy to read/analyze. Please, find an alternative way to present it.

 

In this case we have not found a better way to present this information and we have maintain the table 1. Nevertheless this table has been modified because some information about Alicante_out and Alicante_in has also been modified.

 

L119: how do you remove the annual signal. Please, clarify. And opver which time period ?

 

The reviewer is right. This question was not clear enough. As we have already mentioned, the periods used for the calculation of the seasonal or annual signal have been included in the new version and the methodology used is explained in the main text, but also explained in a more detailed way in the supplementary material that has been included in this new version.

L139 : “After visual inspection, year 2018 ….”. What do you find for this time series? Please, clarify.

 

 

The reviewer is right again. We have explained in the new version that the sea level for year 2018 was almost exactly equal to the climatological seasonal cycle, and therefore the residuals were almost zero. Here we include the time series of residuals in L'Estartit from 2010 to 2018.

 

L140-142: Provide some statistics to quantify the validation of the interpolation method.

 

Ok! We have followed this suggestion and detailed statistics about the linear regression are provided in the supplementary material to avoid an excessive length of the manuscript.

 

L176 : Provide the entire time period’ from Jan. 1948 to ….”

 

L181: “Strait of “ instead of “Starit of …”. Please, correct.

 

L198: “corrected from land movement”. As I understand you only consider GIA for vertical land movement. How about tectonics? You should compare the TG data to satellite altimetry data to see if the GIA is the only candidate for VLM of your TG stations.

 

We have corrected all these errors. Concerning "land movements" we have used this expression only when considering other works referenced in the manuscript. When considering our own data we always use GIA.

 

 

L204: ‘long term mean value for rho surface’ : which period do you consider exactly ?

 

Ok!. The period considered is the complete period of the time series. It has been explained in the new manuscript.

 

L207-210 : Did you check if steric sea level is equal to thermosteric and halosteric ? Because of the non-linearity of the equation of state of sea water, this might not be the case.

 

This is a very interesting question. We have compared the steric component obtained from the density values calculated using the complete equation of state, and the sum of the thermosteric and halosteric contributions, which ignores the non-linear terms.

Both quantities are not exactly the same, but the agreement is very good as you can see in the following plots for Cádiz and for the Strait of Gibraltar.

 

 

L237: is not it ‘1945-2018’ instead of ‘1940-2018’ ?

 

EN4 data extend from 1940 to 2018.

 

L248-255: This section deserves more details as the methodology might not be known by the readers. Please, clarify.

 

The reviewer is right. We have explained it in more detailed in the supplementary material. We honestly hope that it is now clearer.

 

L258-264: Do you have any idea why the SL peaks in Oct-Nov ? as the steric sea level for the annual signal ? See Gill and Nihler 1973 for a possible explanation. ~90% of the seasonal sea level is due to net heat flux (Qnet) and warms the ocean surfaces. Therefore, this is traduced by an increase of steric seasonal sea level. As Qnet is maximum in may-June, you have some delay before the seasonal sea level peaks.

 

The reviewer is right. We have included a sentence to explain that this is a consequence of the annual cycle of the heat exchange between the atmosphere and the sea. It can be seen in the following plot where we show the net heat flux close to Málaga. The heat flux is positive (the sea gains heat) until October.

 

 

L266-269 : and so what ?

L452: Explain how you derive the theoretical value for atmospheric pressure.

 

We have to admit that we do not understand these two questions.

Author Response File: Author Response.docx

Reviewer 2 Report

Review of the paper “Long-term changes and inter-annual variability of sea level at the coasts of the Spanish Mediterranean and the Gulf of Cádiz” by Vargas-Yáñez et al.

 

The paper deals with aspects of the ocean variability that are of great interest for the study of climate change.

The overall impression is that the paper does not present really new results or findings. Moreover, there are several problems that make the paper unsuitable for publication in the present form.

 

Major problems

The Abstract does not summarize the work but represents a sort of ‘introduction’. Previous works are not the subject of the paper.

The motivation of this work is unclear: At lines 70-74, it seems to be the analysis of sea level variability, but at line 504 it is the reconstruction. The simple approach used by the authors can justify the analysis, although there is nothing really new in the results. By contrast, it is unlikely that the reconstruction turns out to be more accurate than with complex ocean models (that, for instance, are able to account for the halosteric and thermosteric contributions).

The reconstruction of long time series (Sect. 2.2) has several problems.

1. The procedure of gap filling is questionable and might affect the whole analysis. In particular, the authors should show that using stations far from the one of interest is a better choice than using close stations. In the case of Málaga, there are 20 years (1993-2012) in common for Málaga and Málaga II, so why not taking advantage of this period to reconstruct the 2013-2018 interval? Note that the two Málaga’s not only measure essentially the same thing, but also probably experience very similar vertical land movements, whereas, in general, this is not true for stations far from each other. Note also that the Strait of Gibraltar and the Atlantic are characterized by dynamics that can be rather different from the Mediterranean. Clearly, if Málaga II has some problems, it may not be a good choice, but, in this case, the authors should explain it clearly, and, in any case do not use it for validation. If the approach is to use distant stations, I wonder why the gaps of Alicante (out) were filled using Alicante (in).
2. In some cases, the reconstructed data (in red) represent large parts of the time series, as for Cádiz (fig. 3), Algeciras (fig. 4) and Alicante (fig. 5). This raises the question of how much the reconstruction might affect the analysis. For instance, the authors should take into account the errors associated to the reconstructed values.
3. In the literature there are two papers that describe two time series at stations selected by the authors, that are not even quoted in the paper:

Marcos et al., 2011, The long sea level record at Cadiz (southern Spain) from 1880 to 2009, J. Geophys. Res., 116, C12003, doi:10.1029/2011JC007558.

Marcos et al., 2021, Historical tide gauge sea-level observations in Alicante and Santander (Spain) since the 19th century, Geosc. Data J., 2021;00:1-10, doi:10.1002/gdj3.112.

In particular, the 2011 paper shows a Cádiz time series (fig. 5) which looks rather different from the one shown here in fig, 3. As a consequence, the long-term trend is 0.7+/-0.1 mm/y, while in the present paper it is 1.6+/-0.1 mm/y. Comments on this point are required. I understand that the PSMSL is an authoritative data source, but science evolves and new findings can update their data, so why did the authors neglect the data related to the two Marcos’ papers?

 

Minor problems:

Line 33: Both references are missing from the list.

Line 37: Church et al., 2011, is missing from the list.

Line 38: The reference is missing from the list.

Line 59: The two first references are missing from the list.

Line 78: Here and elsewhere there is a Jordà and Gomis, 2013, that should be 2013a.

Line 97: ‘considered’.

Lines 116-117: Please say which problems affect the ‘001’ time series.

Line 169: Better ‘end’ than ‘finalize’.

Line 171: ‘Pressure’.

Line 220: I would not say ‘usually’ but probably ‘often’. Non-linear variations are also usually taken into account.

Lines 224-227: Causal relationships can only be established by studying the physical processes, by no means can they be deduced from statistics, even using deseasoned and detrended time series.

Table 2, heading of columns 2-3: ‘Sea level’ is generic, please use ‘Relative sea level’.

Table 2: What is ‘0’? If it is an estimate, please use ‘0.00’ for consistence with the other values.

Lines 266-269: Why is L’Estartit peculiar?

Lines 271-279: This piece of text should by moved to the reconstruction section.

Lines 297-298: How can this conclusion can be drawn by simply looking at trends? See my comment to lines 224-227, above.

 

Table 4:

1. In some cases one or more atmospheric variable are missing in the equation, even at the same station in different periods. If their coefficients are small, this should appear from the regression. I do not agree with an ‘a priori’ selection. Please also see my comment to lines 506-507, below, and explain.
2. The fact that some coefficients are very different depending on the period (e.g. b3 in Tarifa and Algeciras) deserves some comments.
3. ‘mm/ms-1’ is confusing, and because ‘ms’ can be mistaken for milliseconds;
4. b0 is never quantified.

 

Lines 363-366, 413-414: The authors adopted a very basic approach, compared to regional modelling, but the reader cannot see if and how the results of this paper are better or can be compared to those obtained with other approaches. The comparison with previous works should be made quantitatively.

Line 353: Jevrejeva et al. is missing from the list.

Lines 451-453: Can the authors explain the large range (10-16 mm/y)?

Line 462: ‘contributions’.

Line 463: What does ‘far from 1’ mean?

Table 5: Please show the periods after the station names, and identify the columns on the caption clearly, i.e. not with numbers but the symbols. What is ‘-------’?

Lines 506-507: The authors say that no ‘a priori’ assumption was made, but in Table 4 some variables are sometimes missing as if they had been excluded ‘a priori’.

Lines 511-512: Why does this happen?

Line 512: I guess that the authors call ‘acceleration’ the larger trends in the recent decades compared to those of the longer periods. It can simply be an expression of decadal variability, also considering that the 1960-1990 period was anomalously stationary in the Mediterranean. The acceleration can be estimated from a quadratic fit.

Finally, although to use the mbar (millibar) is not wrong, I suggest to use the hPa (hectopascal) instead, because the millibar is not a SI unit and whose use is deprecated by several institutions dealing with metrology (not meteorology).

 

Author Response

Answer reviewer 2.

 

The paper deals with aspects of the ocean variability that are of great interest for the study of climate change.

The overall impression is that the paper does not present really new results or findings. Moreover, there are several problems that make the paper unsuitable for publication in the present form.

 

First of all, as in the case of reviewer 1, we want to thank reviewer 2 for a very complete and constructive review. We have tried to follow most of the reviewer's suggestions and we think that the new manuscript is much improved.

 

Major problems

The Abstract does not summarize the work but represents a sort of ‘introduction’. Previous works are not the subject of the paper.

 

The reviewer is right. We have changed the redaction of the abstract and included the main findings of this work.

 

The motivation of this work is unclear: At lines 70-74, it seems to be the analysis of sea level variability, but at line 504 it is the reconstruction. The simple approach used by the authors can justify the analysis, although there is nothing really new in the results. By contrast, it is unlikely that the reconstruction turns out to be more accurate than with complex ocean models (that, for instance, are able to account for the halosteric and thermosteric contributions).

We partially agree with the reviewer. Certainly the reconstruction of time series is not the objective of this work. The reviewer is right because the reader could think that it was the main objective, according to the past redaction of the summary at the end of the manuscript. This has been corrected. In fact, reconstructing sea level time series using cubic splines for short gaps and linear regression on nearby stations has already been done in some of the works referenced. The main objective was to explore the influence of meteorological forcing and halosteric and thermosteric contributions from an statistical point of view. Then, considering the part of the sea level trends not explained by meteorological variables and the steric contribution, we estimate the contribution of mass addition to sea level trends. The reviewer is right, this can also be done (as in many works before) using numerical models. For this reason we state in our manuscript that we use a complementary approach. We do not try to state that this is a better approach than the one used in other works, it simply provides a new approach that could be complementary to previous ones. We hope that this is better explained in the new version.

 

The reconstruction of long time series (Sect. 2.2) has several problems.

1. The procedure of gap filling is questionable and might affect the whole analysis. In particular, the authors should show that using stations far from the one of interest is a better choice than using close stations. In the case of Málaga, there are 20 years (1993-2012) in common for Málaga and Málaga II, so why not taking advantage of this period to reconstruct the 2013-2018 interval? Note that the two Málaga’s not only measure essentially the same thing, but also probably experience very similar vertical land movements, whereas, in general, this is not true for stations far from each other. Note also that the Strait of Gibraltar and the Atlantic are characterized by dynamics that can be rather different from the Mediterranean. Clearly, if Málaga II has some problems, it may not be a good choice, but, in this case, the authors should explain it clearly, and, in any case do not use it for validation. If the approach is to use distant stations, I wonder why the gaps of Alicante (out) were filled using Alicante (in).
2. In some cases, the reconstructed data (in red) represent large parts of the time series, as for Cádiz (fig. 3), Algeciras (fig. 4) and Alicante (fig. 5). This raises the question of how much the reconstruction might affect the analysis. For instance, the authors should take into account the errors associated to the reconstructed values.
3. In the literature there are two papers that describe two time series at stations selected by the authors, that are not even quoted in the paper:

Marcos et al., 2011, The long sea level record at Cadiz (southern Spain) from 1880 to 2009, J. Geophys. Res., 116, C12003, doi:10.1029/2011JC007558.

Marcos et al., 2021, Historical tide gauge sea-level observations in Alicante and Santander (Spain) since the 19th century, Geosc. Data J., 2021;00:1-10, doi:10.1002/gdj3.112.

In particular, the 2011 paper shows a Cádiz time series (fig. 5) which looks rather different from the one shown here in fig, 3. As a consequence, the long-term trend is 0.7+/-0.1 mm/y, while in the present paper it is 1.6+/-0.1 mm/y. Comments on this point are required. I understand that the PSMSL is an authoritative data source, but science evolves and new findings can update their data, so why did the authors neglect the data related to the two Marcos’ papers?

 

We honestly think that this is the major mistake that we made in the preparation of our previous manuscript. It is true that we have considered several papers by Marcos and co-authors, such as Tsimplis, Calafat, etc. because they have made very important contributions in this field and they have a considerable influence on our own work. But certainly we did not find these two works: Marcos et al., 2011; Marcos et al., 2021 which certainly are very relevant for our present work and had to be included. We have tried to correct this mistake, not only referencing them in the bibliography, but also using their results and their data.

In Marcos et al., 2011, the authors found that 37.5 mm should be added to the data for the period 1880-1924. We have considered also this correction. In the case of Alicante, Marcos et al. (2021) have made a very exhaustive work for reconstructing the sea level time series in the inner and the outer harbor. These time series are freely available from the British Oceanographic Data Centre. After considering this work, we have to admit that these time series are more accurate than those we had used from the PSMSL. Therefore we have downloaded the time series reconstructed by Marcos et al. (2021). Obviously we have referenced these two works and the data centre that provided the data. After the correction applied to Cadiz sea level, and the use of the new time series for Alicante, the analyses for these two locations have been repeated. Tables 1, 2, 4 and 5, and figures 2, 3, 5, 6 and 7 have been re-made. As the reviewer stated in her/his review, the trends for Cádiz should be lower. For the complete period, 1880-2018, our trends have decreased from the previous calculations to those in this reviewed manuscript, from 1.6 to 1.24 mm/yr, and for the period 1944-2018, the trends have decreased from 1.0 to 0.85. Notice that Marcos et al. (2011) considered data until 2009, whereas in the present work we have extended the data to 2018, adding 9 years with high sea level values. This could explain the difference with the trends in Marcos et al (2021).

Another question is why, in some cases, we do not reconstruct sea level time series using those obtained at the same location. Let us consider the case of Málaga. We have a gap from 2012 to 2018 and it is true that we have another tide gauge operating from 1993 to 2018 at the same location. If we use this other tide gauge for filling the gap from 2012 to 2018, we could not use it to compare the reconstructed time series with an independent one. On the other hand, this second tide gauge is useful only for reconstructing the period 2012-2018, but not for the other gaps during the 1950s and 1960s. Therefore we prefer to reconstruct Malaga with other tide gauges and leave Malaga II for testing the reconstruction.

In the case of Cádiz, we have followed the reviewer's suggestion and used Cádiz III for reconstructing Cádiz II, instead of our previous procedure, but the linear regression did not improve significantly and therefore we have kept our previous approach.

 

Minor problems:

Line 33: Both references are missing from the list.

Line 37: Church et al., 2011, is missing from the list.

Line 38: The reference is missing from the list.

Line 59: The two first references are missing from the list.

Line 78: Here and elsewhere there is a Jordà and Gomis, 2013, that should be 2013a.

 

We have corrected all these references.

 

Line 97: ‘considered’.

 

Corrected.

 

Lines 116-117: Please say which problems affect the ‘001’ time series.

 

Honestly, we do not know. The web site of the PSMSL informs that the data are flagged with 001 when there is any problem. We have trusted this authority. Nevertheless, this does not make any difference because the number of data flagged with 001 in the time series that we have used is very low.

 

Line 169: Better ‘end’ than ‘finalize’.

 

Ok!, corrected.

 

Line 171: ‘Pressure’.

Ok!, Corrected.

 

Line 220: I would not say ‘usually’ but probably ‘often’. Non-linear variations are also usually taken into account.

 

In this case we prefer the present redaction.

 

Lines 224-227: Causal relationships can only be established by studying the physical processes, by no means can they be deduced from statistics, even using deseasoned and detrended time series.

 

The reviewer is right and this has been corrected in the new redaction. The term "causal" has been suppressed.

 

Table 2, heading of columns 2-3: ‘Sea level’ is generic, please use ‘Relative sea level’.

 

Ok!, we have changed it.

 

Table 2: What is ‘0’? If it is an estimate, please use ‘0.00’ for consistence with the other values.

 

Ok! corrected.

 

Lines 266-269: Why is L’Estartit peculiar?

 

We do not really know why the atmospheric pressure seasonal cycle is different at L'Estartit. We have tried to make clear in the manuscript that we are not interested in the seasonal cycles, and that we simply calculate them because they must be subtracted to the original time series previously to the calculation of the linear regression. Then, we simply described these cycles for the completeness of the work and for providing this information. Maybe, this information could be omitted in the case that the reviewer considers it appropriate.

 

Lines 271-279: This piece of text should by moved to the reconstruction section.

 

It is true that this paragraph could be included in the methods. But this sub-section is titled: Seasonal cycles and time series reconstruction. Therefore it deals with the results obtained during the reconstruction. For the moment we would like to keep it here, but if the reviewer insists we could move it to the method sections.

 

Lines 297-298: How can this conclusion can be drawn by simply looking at trends? See my comment to lines 224-227, above.

 

The numbers of the lines in the version of the manuscript are not exactly the same that those in the version that we submitted. Therefore we are not completely sure which trends the reviewer is talking about. We think that the reviewer is considering our statement: " The negative values of the steric contributions in Alicante and L'Estartit were caused by a strong and negative halosteric contribution for the two periods analysed. The halosteric component was negative for Cádiz, Gibraltar and Málaga for the period 1940-2018, but in these cases it was compensated by the thermosteric contribution". In this case we have to consider one question raised by the reviewer 1. Certainly, although the equation of state for sea water is not linear, the steric contribution is very close to the sum of the thermosteric and halosteric contributions (we checked it following reviewer 1). Hence, if the halosteric component is negative and the thermosteric one is positive, but the absolute value of the halosteric one is larger, then the halosteric effect will dominate. On the other hand, if both quantities have a similar size, they will compensate each other.

Table 4:

1. In some cases one or more atmospheric variable are missing in the equation, even at the same station in different periods. If their coefficients are small, this should appear from the regression. I do not agree with an ‘a priori’ selection. Please also see my comment to lines 506-507, below, and explain.
2. The fact that some coefficients are very different depending on the period (e.g. b3 in Tarifa and Algeciras) deserves some comments.
3. ‘mm/ms-1’ is confusing, and because ‘ms’ can be mistaken for milliseconds;
4. b0 is never quantified.

We have to admit that this table and the forward stepwise linear model was not well explained in the previous version of the manuscript. Reviewer 1 considered that the methods should be better explained. For this reason we have included a supplementary material explaining the details. We think that now it is clear that the model is not selected a priori. The model selects which variable makes a significant contribution for explaining the variance of the observed sea level. For each location and for each period of time, only those variables selected by the forward stepwise regression are included in the model. For this reason, the variables that appear in table 4 are different for each case. It is not a question of including only those coefficients which are larger and neglecting those with small values. The variables, and the coefficients, included are those which are significant from a statistical point of view. Once again we accept that this was not clear and we hope that it is better explained with the inclusion of the supplementary material. b0 is not included because it is simply the interception in the origin and does not provide information with relevant physical meaning. But it could be included if the reviewer considers it appropriate.

Lines 363-366, 413-414: The authors adopted a very basic approach, compared to regional modelling, but the reader cannot see if and how the results of this paper are better or can be compared to those obtained with other approaches. The comparison with previous works should be made quantitatively.

 

We think that this point is very interesting, but certainly could be the subject for another work. In the case we continue this work with this suggestion and some others made by the other reviewer, we would try to contact with Marcos and coauthors to obtain their sea level time series from Cádiz.

 

Line 353: Jevrejeva et al. is missing from the list.

 

Ok! Corrected.

 

Lines 451-453: Can the authors explain the large range (10-16 mm/y)?

 

We have repeated this calculations using the time series of Alicante reconstructed by Marcos et al. (2021), and this range has changed, and now it is 10-14 mm/mbar. We think that there is a misunderstanding. It is not a trend, and the units are not mm/y (millimeters per year). These are the coefficients of the regression and express the response of sea level to changes in pressure. Initially they were expressed in mm/mbar. Following one of the suggestions made by the reviewer we have changed it by mm/hPa.

 

Line 462: ‘contributions’.

 

Corrected!         

 

Line 463: What does ‘far from 1’ mean?

 

We think that this is a very good question. If you estimate the steric contribution using observations of sea density, the observed sea level would be:

observed sea level = atmospheric contribution + steric contribution + mass addition.

Notice that in this equation mass addition is understood as a global contribution caused by melting of glaciers, as the atmospheric contribution also produces a redistribution of mass. In fact, in many works, you can find:

observed sea level (corrected by atmospheric forcing) = steric contribution + mass addition.

Then the coefficient of the steric contribution should be 1. But these works also consider that it is not clear that the change of the steric sea level observed at the open sea, would be the same observed at a coastal station. On the other hand, using different reference levels for the calculation of the steric component could yield different results. For this reason we prefer to estimate the coefficient from the statistical analysis of the data, and we find that the coefficient is far from 1.

 

Table 5: Please show the periods after the station names, and identify the columns on the caption clearly, i.e. not with numbers but the symbols. What is ‘-------’?

 

The reviewer is right. This was not explained. We have included it in the legend of the table. The meaning of ----- It is simply that the variable does not contribute to the linear trend of sea level. We have tried to include the two periods: 1949-2018 and 1990-2018 in the table, but the result is not good. Therefore this is explained in the legend of the table.

 

Lines 506-507: The authors say that no ‘a priori’ assumption was made, but in Table 4 some variables are sometimes missing as if they had been excluded ‘a priori’.

 

We have explained in the previous question that this was not decided a priori. Instead, the linear model selected the variables with a significant contribution, and the others were excluded. As we already said, this is better explained with the inclusion of the new supplementary material.

 

Lines 511-512: Why does this happen?

 

Does the reviewer refers to the better behavior of the model for the period 1990-2018? We think that this is because more TS data are available and the steric contribution is better estimated.

 

Line 512: I guess that the authors call ‘acceleration’ the larger trends in the recent decades compared to those of the longer periods. It can simply be an expression of decadal variability, also considering that the 1960-1990 period was anomalously stationary in the Mediterranean. The acceleration can be estimated from a quadratic fit.

 

The reviewer is right. The term acceleration is not used anymore in this work.

 

Finally, although to use the mbar (millibar) is not wrong, I suggest to use the hPa (hectopascal) instead, because the millibar is not a SI unit and whose use is deprecated by several institutions dealing with metrology (not meteorology).

Ok!, we have changed mbar by hPa

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

The authors have answered all my previous comments and questions.

Adding the supplementary part to the manuscript is a good idea. The reader can refer to this part if the methodology is not known.

 

 

 

 

 

Author Response

We appreciate the reviewer's comments!

Thanks!

Reviewer 2 Report

Although improvements were made with respect to the first version, the overall impression is that the paper is still not well focussed. Moreover, some issues were not addressed properly. As a consequence, I think that the paper is not suitable for publication.

 

Here follow my comments in bold (REV:) after the authors’ responses and to a few minor points related to the revised version. The points that were satisfactorily addressed by the authors are not covered.

 

 

Major problems

 

 

The reconstruction of long time series (Sect. 2.2) has several problems.

1. The procedure of gap filling is questionable and might affect the whole analysis. In particular, the authors should show that using stations far from the one of interest is a better choice than using close stations. In the case of Málaga, there are 20 years (1993-2012) in common for Málaga and Málaga II, so why not taking advantage of this period to reconstruct the 2013-2018 interval? Note that the two Málaga’s not only measure essentially the same thing, but also probably experience very similar vertical land movements, whereas, in general, this is not true for stations far from each other. Note also that the Strait of Gibraltar and the Atlantic are characterized by dynamics that can be rather different from the Mediterranean. Clearly, if Málaga II has some problems, it may not be a good choice, but, in this case, the authors should explain it clearly, and, in any case do not use it for validation. If the approach is to use distant stations, I wonder why the gaps of Alicante (out) were filled using Alicante (in).
2. In some cases, the reconstructed data (in red) represent large parts of the time series, as for Cádiz (fig. 3), Algeciras (fig. 4) and Alicante (fig. 5). This raises the question of how much the reconstruction might affect the analysis. For instance, the authors should take into account the errors associated to the reconstructed values.
3. In the literature there are two papers that describe two time series at stations selected by the authors, that are not even quoted in the paper:

Marcos et al., 2011, The long sea level record at Cadiz (southern Spain) from 1880 to 2009, J. Geophys. Res., 116, C12003, doi:10.1029/2011JC007558.

Marcos et al., 2021, Historical tide gauge sea-level observations in Alicante and Santander (Spain) since the 19th century, Geosc. Data J., 2021;00:1-10, doi:10.1002/gdj3.112.

In particular, the 2011 paper shows a Cádiz time series (fig. 5) which looks rather different from the one shown here in fig, 3. As a consequence, the long-term trend is 0.7+/-0.1 mm/y, while in the present paper it is 1.6+/-0.1 mm/y. Comments on this point are required. I understand that the PSMSL is an authoritative data source, but science evolves and new findings can update their data, so why did the authors neglect the data related to the two Marcos’ papers?

We honestly think that this is the major mistake that we made in the preparation of our previous manuscript. It is true that we have considered several papers by Marcos and co-authors, such as Tsimplis, Calafat, etc. because they have made very important contributions in this field and they have a considerable influence on our own work. But certainly we did not find these two works: Marcos et al., 2011; Marcos et al., 2021 which certainly are very relevant for our present work and had to be included. We have tried to correct this mistake, not only referencing them in the bibliography, but also using their results and their data.

In Marcos et al., 2011, the authors found that 37.5 mm should be added to the data for the period 1880-1924. We have considered also this correction. In the case of Alicante, Marcos et al. (2021) have made a very exhaustive work for reconstructing the sea level time series in the inner and the outer harbor. These time series are freely available from the British Oceanographic Data Centre. After considering this work, we have to admit that these time series are more accurate than those we had used from the PSMSL. Therefore we have downloaded the time series reconstructed by Marcos et al. (2021). Obviously we have referenced these two works and the data centre that provided the data. After the correction applied to Cadiz sea level, and the use of the new time series for Alicante, the analyses for these two locations have been repeated. Tables 1, 2, 4 and 5, and figures 2, 3, 5, 6 and 7 have been re-made. As the reviewer stated in her/his review, the trends for Cádiz should be lower. For the complete period, 1880-2018, our trends have decreased from the previous calculations to those in this reviewed manuscript, from 1.6 to 1.24 mm/yr, and for the period 1944-2018, the trends have decreased from 1.0 to 0.85. Notice that Marcos et al. (2011) considered data until 2009, whereas in the present work we have extended the data to 2018, adding 9 years with high sea level values. This could explain the difference with the trends in Marcos et al (2021).

Another question is why, in some cases, we do not reconstruct sea level time series using those obtained at the same location. Let us consider the case of Málaga. We have a gap from 2012 to 2018 and it is true that we have another tide gauge operating from 1993 to 2018 at the same location. If we use this other tide gauge for filling the gap from 2012 to 2018, we could not use it to compare the reconstructed time series with an independent one. On the other hand, this second tide gauge is useful only for reconstructing the period 2012-2018, but not for the other gaps during the 1950s and 1960s. Therefore we prefer to reconstruct Malaga with other tide gauges and leave Malaga II for testing the reconstruction.

In the case of Cádiz, we have followed the reviewer's suggestion and used Cádiz III for reconstructing Cádiz II, instead of our previous procedure, but the linear regression did not improve significantly and therefore we have kept our previous approach.

REV:

1) If the authors want to reconstruct a gap in station A with station B, A and B must not be independent of each other, otherwise the regression does not give useful results. In this case it works because also distant stations are not independent of one another, as part of the sea level variations are common to all of them.

It is also very confusing to see that some time series were reconstructed using distant stations even when close stations were available, but Alicante out was reconstructed with Alicante in (Lines 150 ff). Moreover, in some cases a ‘validation’ was made and in others it was not.

As regards to Cadiz, I am lost. The authors wrote a long response to my previous remark, but in the paper I can see only few things. Because the reconstruction is an important part of the work, it is important for the reader to know what the authors did with the available data sets and why they made certain choices, particularly in the presence of different options.

I understand that the authors did not adopt Marcos et al. (2011) data but they did adopt the +37.5 mm correction to the data of 1880-1924. Is there a reason for not using the newer data? This question is important because the authors adopted the newer time series for Alicante.

Going back to Cadiz, first, it is hard to believe that the sole addition of the 2010-2018 data can justify a 0.5 mm/y difference in the long-term trend between this work and Marcos’ 2011 paper; in fact, it is easy to see that the two time series are completely different. Moreover, I cannot accept that ‘This could explain …’ (in the response) when the authors can simply compute the trend until 2009 and make the comparison.

Secondly, why has the 1944-2018 trend changed if the correction ends in 1924?

2) The authors did not respond to point 2.

3) Ok.

 

Minor problems:

REV: Line 119: ‘bodc’.

 

REV: Line 132: ‘missing monthly values’.

 

REV: Table 1 is confusing. First, according to the caption a data lack exists from 1925 to 1942, but in the table Alicante out has data in 1927-1938. Secondly, the horizontal grey bands after 1924 and before 1943 have almost the same colour as the shaded boxes. Finally, 1943 is void of data. Please make it more clear.

 

Lines 136-137 (previously 116-117): Please say which problems affect the ‘001’ time series.

Honestly, we do  not know. The web site of the PSMSL informs that the data are flagged with 001 when there is any problem. We have trusted this authority. Nevertheless, this does not make any difference because the number of data flagged with 001 in the time series that we have used is very low.

REV:

As it does not make any difference, I suggest to say that you used data that the PSMSL considers reliable, without technical details.

 

REV: Lines 139, 140: please choose either ‘seasonal’ or ‘annual’, they are the same thing.

 

REV: Line 223: December

 

Lines 291-292 (previously 266-269): Why is L’Estartit peculiar?

We do not really know why the atmospheric pressure seasonal cycle is different at L'Estartit. We have tried to make clear in the manuscript that we are not interested in the seasonal cycles, and that we simply calculate them because they must be subtracted to the original time series previously to the calculation of the linear regression. Then, we simply described these cycles for the completeness of the work and for providing this information. Maybe, this information could be omitted in the case that the reviewer considers it appropriate.

REV:

Ok, but I suggest not to introduce concepts that you cannot explain, particularly when they raise questions. You might say that in general the seasonal cycle is characterized by etc.

 

Lines 296-305 (previously 271-279): This piece of text should by moved to the reconstruction section.

It is true that this paragraph could be included in the methods. But this sub-section is titled: Seasonal cycles and time series reconstruction. Therefore it deals with the results obtained during the reconstruction. For the moment we would like to keep it here, but if the reviewer insists we could move it to the method sections.

REV:

At lines 75 ff. the authors describe their main goal. The time series reconstruction is made to obtain longer time series for the analysis but it is not a goal. In fact, they are shown in fig. 3-5, which are mentioned in sect. 2.2. In my opinion, all the comments on the reconstruction should be placed in sect. 2.2, not in the ‘results’ section. Anyway, I do not insist.

 

Lines 297-298: How can this conclusion can be drawn by simply looking at trends? See my comment to lines 224-227, above.

 The numbers of the lines in the version of the manuscript are not exactly the same that those in the version that we submitted. Therefore we are not completely sure which trends the reviewer is talking about. We think that the reviewer is considering our statement: " The negative values of the steric contributions in Alicante and L'Estartit were caused by a strong and negative halosteric contribution for the two periods analysed. The halosteric component was negative for Cádiz, Gibraltar and Málaga for the period 1940-2018, but in these cases it was compensated by the thermosteric contribution". In this case we have to consider one question raised by the reviewer 1. Certainly, although the equation of state for sea water is not linear, the steric contribution is very close to the sum of the thermosteric and halosteric contributions (we checked it following reviewer 1). Hence, if the halosteric component is negative and the thermosteric one is positive, but the absolute value of the halosteric one is larger, then the halosteric effect will dominate. On the other hand, if both quantities have a similar size, they will compensate each other.

REV:

The line numbers 297-298 were correct (now they are 323-324). The relevant text looks like this:

lysed. This result indicates that the atmospheric variability is one of the factors that     297

modulate the sea level decadal variability.                                                                       298

I wanted to point out that linear trends are not enough to draw that conclusion.

 

Table 4:

1. In some cases one or more atmospheric variable are missing in the equation, even at the same station in different periods. If their coefficients are small, this should appear from the regression. I do not agree with an ‘a priori’ selection. Please also see my comment to lines 506-507, below, and explain.
2. The fact that some coefficients are very different depending on the period (e.g. b3 in Tarifa and Algeciras) deserves some comments.
3. ‘mm/ms-1’ is confusing, and because ‘ms’ can be mistaken for milliseconds;
4. b0 is never quantified.

We have to admit that this table and the forward stepwise linear model was not well explained in the previous version of the manuscript. Reviewer 1 considered that the methods should be better explained. For this reason we have included a supplementary material explaining the details. We think that now it is clear that the model is not selected a priori. The model selects which variable makes a significant contribution for explaining the variance of the observed sea level. For each location and for each period of time, only those variables selected by the forward stepwise regression are included in the model. For this reason, the variables that appear in table 4 are different for each case. It is not a question of including only those coefficients which are larger and neglecting those with small values. The variables, and the coefficients, included are those which are significant from a statistical point of view. Once again we accept that this was not clear and we hope that it is better explained with the inclusion of the supplementary material. b0 is not included because it is simply the interception in the origin and does not provide information with relevant physical meaning. But it could be included if the reviewer considers it appropriate.

REV:

1, 2, 4) Ok, more clear.

3) It is still there and confusing. Also in Table 2, for example we have ‘mm’, ‘mbar’ (but wasn’it corrected to ‘hPa’?) and ‘ms-1’. Please use ‘m s-1’.

 

Line 491 (previously 463): What does ‘far from 1’ mean?

We think that this is a very good question. If you estimate the steric contribution using observations of sea density, the observed sea level would be:

observed sea level = atmospheric contribution + steric contribution + mass addition.

Notice that in this equation mass addition is understood as a global contribution caused by melting of glaciers, as the atmospheric contribution also produces a redistribution of mass. In fact, in many works, you can find:

observed sea level (corrected by atmospheric forcing) = steric contribution + mass addition.

Then the coefficient of the steric contribution should be 1. But these works also consider that it is not clear that the change of the steric sea level observed at the open sea, would be the same observed at a coastal station. On the other hand, using different reference levels for the calculation of the steric component could yield different results. For this reason we prefer to estimate the coefficient from the statistical analysis of the data, and we find that the coefficient is far from 1.

REV:

The concept was clear, but ‘far from’ is not a mathematical expression. Please replace it with ‘much less/smaller than’ and refer to table 4.

 

Lines 511-512: Why does this happen?

Does the reviewer refers to the better behavior of the model for the period 1990-2018? We think that this is because more TS data are available and the steric contribution is better estimated.

REV:

Yes. A considerable improvement deserves some comments (in the text not in the response to the reviewer).

 

Line 527: Linear

 

 

Supplementary material

 

REV:

REV:

1) There are no references. Please make it clear what was taken from the literature and what was devised by the authors.

2) Page 5: The last sentence of the first section (‘Some period …’) is unclear. Does it mean that gaps of the same time series were filled using different sets of predictors?

 

Author Response

We sincerely thank the reviewer for a very complete and exhaustive review. We have followed almost all of the reviewer's suggestions and we hope that the manuscript is much improved. Please, find detailed answers to all the comments in the attached document.

Author Response File: Author Response.docx

Round 3

Reviewer 2 Report

In this revision my comments are in italics+bold (REV 08/09/21:) after the authors’ responses. The points that were satisfactorily addressed by the authors are not covered.

 

Although the paper was improved, there is something still to be done.

After the corrections the paper can be considered for publication.

 

 

Besides all the questions posed by the reviewer, we have found an important error: The significant figures in trends and coefficients of the linear regression were not correctly presented. We have followed the usual criterion to use two significant figures for the errors. If these two figures are less or equal than 25, we keep two figures. If they are larger than 25 we keep one figure (after rounding it).

REV 08/09/21: Do they mean ‘decimal’ rather than ‘significant’? In the previous version of Table 4 the errors were given with 1 to 3 significant digits: e.g., for Ceuta 1990-2018, b₄ = 0.09+/-0.06 (1 digit, it is equivalent to 6 10^-2), and b₁ = -12.36+/-1.59 mm/hPa (3 digits). However, I think that it is an unnecessary complication.

 

Major problems

The reconstruction of long time series (Sect. 2.2) has several problems.

(…)

Going back to Cadiz, first, it is hard to believe that the sole addition of the 2010-2018 data can justify a 0.5 mm/y difference in the long-term trend between this work and Marcos’ 2011 paper; in fact, it is easy to see that the two time series are completely different. Moreover, I cannot accept that ‘This could explain …’ (in the response) when the authors can simply compute the trend until 2009 and make the comparison.

The reviewer is right. We made this test and certainly the trends are not the same. The reason seems to be that filling of gaps from the early 1940s to 1961 has an obvious influence. Another explanation is that certainly we are using different time series: Those obtained from the PSMSL with the only correction of the addition of 37.5 mm to the initial part of the series (until 1924). If we estimate the linear trend for the Cádiz II data set from the PSMSL, with the 37.5 mm correction for the period previous to 1924, we obtain the value 0.98 ± 0.16 which, considering the uncertainties, is not far from 0.7 ± 0.1 obtained by Marcos et al., 2011. But we have to admit that Cádiz II extends only from 1880 to 1990 with a large gap between 1924 and 1976. Therefore it is clear that the way the gaps are filled has an important influence. We have presented our own results in the "results" section, but in the "discussion" section we have explained clearly the differences between the results obtained with our time series (those from PSMSL) and those from Marcos et al. , 2011 and let the reader know that our results from Cádiz should be taken with caution. We hope that this is better explained now.

REV 08/09/21: Ok, but the sentence at lines 391-392 about Alicante is redundant.

 

Secondly, why has the 1944-2018 trend changed if the correction ends in 1924?

In the first version the trends were estimated for the period 1948-2018. In the first review we used all the available period for the reconstructed time series: 1943-2018. If the trends are computed over the same period, obviously there is no change. Anyway, the changes are not significant considering the uncertainty of the trends.

REV 08/09/21: Ok, sorry, I did not realize that the period was different (by the way, it was 1944 not 1943). It is difficult to spot these things if the authors do not provide a detailed list of changes.

 

 

Minor problems:

REV: Table 1 is confusing. First, according to the caption a data lack exists from 1925 to 1942, but in the table Alicante out has data in 1927-1938.

Ok! The legend has been corrected.

REV 08/09/21: … except that it reads ‘lack of data from 1937 to 1943’ and Alicante does have data in 1937-1938.

 

Table 4:

REV:

3) It is still there and confusing. Also in Table 2, for example we have ‘mm’, ‘mbar’ (but wasn’it corrected to ‘hPa’?) and ‘ms-1’. Please use ‘m s-1’.

 Ok!, we have changed mbar by hPa and ms-1 by m s-1 in this table and in other places along the work.

REV 08/09/21: I did not suggest to make a simple text replacement: b₃ represents a length over speed, therefore it must be measured in mm/(m s^-1) not mm/m s^-1 !!! This comment is valid throughout the paper.

 

 

Author Response

Please, find the answers to all the reviewer's comments in the attached word document.

Author Response File: Author Response.docx