The authors did a valuable work to clarify several aspects of their analysis and to improve the readability of the manuscript. Further, they provided detailed and convincing answers to the reviewers’ comments supporting their thoughts.
However, a couple of points (point 2 and 4of their response letter) of the previous review still need to be addressed accurately and are source of concerns before the manuscript can be accepted for publication.
Regarding point 2 of the response letter.
L10P196-215: the description of the deconvolution needs further explanation. The answer provided by the authors is not satisfactory.
To my understanding of this section, the authors computed 4 timeseries of pH by using: the true observations of T and the climatological monthly means of the other three variables; the true observations of S and the climatological monthly means of the other three variables, and so on for DIC and ALK. Then, the linear regression analysis is performed on these 4 pH timeseries, and the estimated slopes are reported in Table 3.
Therefore, I think that this is not the methodology proposed by Garzia-Ibanes et al., (2016). Indeed, the sensitivity of the pH to the four drivers (i.e. the changes of pH caused by the changes in the drivers ( ) as prescribed in Garzia-Ibanes’ method) is not provided in the manuscript. Is it perhaps computed? Then, the different pH contributions are not computed as the multiplication of times the trend of the variables, . Therefore, the equation (1) is not correct with respect to the analysis that is effectively performed, and some of the results and conclusions should be provided in a different way.
I suggest that the analysis presented in the manuscripts can be maintained, however authors should provide the robustness of the underpinning hypothesis (i.e. the overall trend can be decomposed in such a way) and they should provide the sensitivity of the method to the choice of the temporal means of the variables that are kept constant (i.e. how different would be the results if the averages are computed on yearly or over the whole period?). Revise accordingly this section and the results.
P13L272-278: provided that the deconvolution is computed as previously described, these comments should be revised since these numbers are not produced by the multiplication of times (i.e. the trends of T, S, alkalinity and DIC reported in table 2 and the sensitivity of pH to the vars).
L271: why do these results indicate that the deconvolution analyses well represent the observed trend?
Regarding point 4 of the response letter.
At P13L282-284 it is said that the trend of atmospheric CO2 represents the “maximum influence of anthropogenic CO2 forcing at Point B” under the assumption that “increase in atmospheric CO2 causes an equal increase in seawater pCO2”. This assumption is quite questionable. The authors should provide some evidences in support of this assumption.
Then, at P16L345-347, it is argued that the atmospheric pCO2 increase is the remaining part composing the contribution of ΔCT to ΔpCO2, which assumes that the atmospheric ΔpCO2 is the actual contribution and not, as previously hypothesized, the maximum one. As the authors surely understand, the similarity between two numbers does not imply any physical relationship. Therefore, this conclusion seems not supported by the results. Please resolve it.
Further, at L347-349: which is the causal relationship between the influence of atmospheric pCO2 and the significance of monthly CT trends? The increase of atmospheric pCO2 should have an effect throughout the year (in winter and autumn months too). Therefore, results do not show the influence of atmospheric pCO2 to the significance of monthly CT trends.
Finally, L354-356: since it has not been demonstrated that the subtraction of delta AT from delta CT gives the contribution of atmospheric pCO2 (i.e. trends in other processes can have contributed), these sentences appear poorly supported by the results.
Other minor points
Abstract
L2P27-28: CT increase could be driven by the same processes that caused the increase in At not by the increase of At itself.
L2P34-35: the conclusion about rapid warming could be misleading by the fact that the length of the timeseries is very short. As well, also some of the trend values reported in Table 2 appear quite large. I wonder whether the length of the timeseries (only 9 years) could have played any role in overestimating the slopes, since it seems (after a simple visual inspection of Fig. 2) that some timeseries have a maximum in 2012 -2013 and values do not increase more after that period.
I would suggest testing the robustness of the trends by using a bootstrap analysis (or any other re-sampling technique) or testing a regime shift analysis to verify whether it is a trend or a regime shift.
I acknowledge that authors specify that trends (i.e. warming, and acidification) referred to the specific 2007-2015 period in several parts of the manuscript, however, a comment about the reliability of trends computed on very short timeseries should be added somewhere in the manuscript (e.g. at L363-365 and in the conclusion)
P8L140-141: avoid to use the “river signature” of the Mediterranean Sea while the Bay of Villefrance is described.
P8L144: provide the position of rivers in Figure 1
P10L190: Should it be called “climatological monthly means”? Even if the word “climatological” is referred to a temporal average over longer periods than the presently considered 9-year period, the use of “monthly means” can be misleading.
Provide a definition of how anomalies are computed (i.e., at L190, L212 and L215).
P12L243: more than 400 samples.
P12L244: do the authors mean that the trends of all variables are significant both at 1 and 50 m and only Salinity at 1 m is not significant? The sentence is not very clear. Then, avoid writing all trends estimates (and confidence interval and number of points) since they are already shown in Table 2. Provide the number of points in Table 2 along with the unit of the variable trends.
Table 2: Which is the meaning of “Total” in the first column? are you meaning the whole Mediterranean Sea?
P15L311: provide an appropriate symbol for AT and S that indicates that AT and S are monthly means. Then, more importantly, add a new plot to figure 4 reporting the regression between salinity and alkalinity based on the monthly means.
P15L328-329 and Fig. S1: it would be interesting to see some statistical tests on the relationship between diel pHT variability and T and Chl variability. Or just do not mention it. The Figure S1 does not show a clear message.
I acknowledge that the authors have chosen to not further investigate the high frequency pH time-series, however, I suggest adding at least the estimate of the diel variability of pH to be compared with the trend estimate (L268) and the annual range (L263). Providing the different scales of variability of pH (daily, seasonal, interannual) would be of great interest for many readers.
L338-341: the assumption that the increase in AT is due to increases in its carbon constituents deserve a better verification. Since HCO3- and CO32- are computed by SeaCarb, the no-carbonate AT can be easily derived and the regression of no-carbonate AT can be calculated in order to verify the assumption. Otherwise, some of the conclusions that follow (e.g. L350-353) cannot be validated by the results.
L366-370: which is the rationale of the relationship between the temperature increase and climate indexes? Provide any statistical correlation index.
P18L391 and L410-411: provide a short definition of “atmospheric forcing”. Do the authors refer to CO2 exchange, Evaporation minus Precipitation, and warming? This definition should be introduced in the abstract at P2L26.
Plots b, d and e of Figure 7 are never introduced nor commented in the text. Remove them if not needed. |