In the present paper, the authors propose, test and apply a novel methodology to estimate changes in the global hydrological cycle (fresh water fluxes) from trends in ocean salinity. The method based on linear response theory and takes into account regional changes.  The authors test their method utilizing ensemble simulation from a climate model (the Community Earth System Model; CESM) and apply it to estimate trends of the hydrological cycle from observations (temperature and salinity from the Institute of Atmospheric Physics). Applying the method to CESM data, show that the proposed methodology can reasonably recover the true freshwater flux of the ensemble mean. The generation of artificial ensembles allow for recovering also changes of individual realizations, i.e. indicate the applicability to observations. However, in this case additional significance criteria for the trend must to be met. Finally, the application to observations give results comparable to previous studies.

As the authors state, estimating the changes in the hydrological cycle as accurately as possible is important and a major challenge. Despite its limitations, response theory can provide an additional method to further improve the estimates.

Overall, I think this is an interesting and valuable study and provides sufficient new and significant information to warrant published.  The manuscript is well written and structured and provides a (almost, see below) clear description of the methodology and the results. However, I have a few comments/questions (in random order) the authors may like to consider:

1) Surface temperature as an additional constraint: In lines 121/122 the authors state that they use surface temperature as an additional constraint. I'm wondering what effect this constraint has. How much would the results change with salinity only?

2) Response functions: From Figure 4 (and 5) the salinity responses of the three forcing experiments show some differences. Thus, the response functions (R) obtained from the individual simulations may have different properties as well. How are the actual Rs used for this study are related to the individual once (but, perhaps I missed or overlooked something)? In addition: As stated by the authors, the sixth mixture for the HadOM3 model seem to indicate a non-linear response. Are these data nevertheless contribute to the final Rs?

3) GMM regions and response functions: As far as I understand, the response functions are derived for the individual GMM regions based on CESM salinity (section 2.2.2). For the observations new GMM regions are defined (Figure 3). However, It seems that the response functions remain the same (based on CESM salinity). Is this the case? If so, how different would be the result when using response functions computed for the observation regions?

4) Significance criteria: The authors need to apply additional significance criteria for the trends to capture the true response for individual CESM ensemble members. Unfortunately, the criteria (in my view) are quite subjective (or, better, are fitted to obtain the correct outcome for the given data set). Fortunately(?), the observations met the criteria for all regions. Beside that I'm surprised by this (which, in my view, may indicate important differences between observations and CESM data), I'm wondering how one would proceed in the case where not all regions met the criteria. Or: How large is the contribution of each GMM region to the total response?

5) Effect of the heat flux:  a) It seems that the authors relate changes in heat flux to changes in circulation/transport (e.g. L195) and therefore claim that their method also captures those changes (e.g. L. 332 & abstract). In general this may be true. However, since the heat flux (via the surface temperature) also directly affects evaporation and thus the hydrological cycle, it is not clear to me to what extent the effect of transport changes are really captured (using linear response). The authors may comment on this. In addition, evaporation also enters the heat flux (via the latent heat flux) and I'm wondering whether this matters for the derived (linear) response of salinity to heat fluxes (in particular for regions where evaporation dominates).

6) Figure 2: The authors may indicate the direction of the flux perturbation (does positive mean into the ocean?)

In this work, the authors present a means to predict the amplification of the hydrological cycle using observed surface salinity data while accounting for local circulation changes which may obscure the ‘true’ E-P signal on the ocean’s surface. This work represents an important evolution in studies that attempt to infer global water cycle change from ocean salinity observations. Past research has identified an impact of sub-surface ocean warming on ocean circulation, which limits our ability to infer hydrological cycle change from surface properties alone. Three-dimensional analyses, on the other hand, are hampered by the significant uncertainty associated with deep ocean salinity measurements. The authors combine unsupervised learning, idealised FAFMIP experiments, an ensemble of CESM historical simulations and IAP ocean observations, and quantify the regional contribution of ocean circulation changes to salinity change. This estimate thus allows for the production of a new surface salinity-derived estimate of water cycle change which accounts for regional circulation changes.

Linear response theory is the unifying method which draws together these lines of evidence and hinges on two fundamental assumptions – that changes to ocean tracers are a linear sum of freshwater fluxes, heat fluxes and wind stress changes, and that the response of surface tracers to surface forcing is linear. The study does a good job of acknowledging, and where possible, quantifying, the caveats associated with these assumptions.

Overall, I commend the authors on an inspired analytical framework that represents a real step forward in the field. I believe the results are important and should be published. I have some comments, however, on the methodology, which should be addressed prior to publication:

Comments:

• The choice of input data for the GMM clustering:

It isn’t clear to me why the authors used the time-mean salinity distribution in defining the geographical locations of the clusters. Wouldn’t it be better to calculate the GMM clusters for each year, then sum them together to get a ‘fuzzy’ set of boundaries that account for both the probability (which comes out of the GMM method), and the spatio-temporal variability of the salinity field? Perhaps the choice made by the authors wouldn’t have a big effect up to 2019 – but surely in the RCP case they would see large changes in the spatial extent of the GMM clusters year-on-year?

• Choice of number of GMM clusters:

AIC and BIC have different equations, with BIC penalising a larger number of clusters (i.e., a more complex model) more. I found it surprising, then, that BIC and AIC have almost identical profiles in figure S1 for the input data. Can the authors comment on this?

Also, typically, the local minimum in AIC/BIC is used as the ‘optimal’ number of clusters. Where there isn’t a local minimum, I would have expected the authors to reach for other quality metrics like the Silhouette Score or the elbow method. This wasn’t explored in this work but may give some more insight into the number of clusters chosen. Additionally, where statistical measures like AIC/BIC fail, the authors could have assessed things like RMSE/variance of salinity in each cluster for a variety of cluster numbers, or other physically relevant parameters. Overall, I found the choice of 6 clusters somewhat subjective and would appreciate some more quantitative assessment to back this choice up.

• Plot results on GMM cluster maps

I felt that the results in Figures 4 and 5 were unclear – there is no guarantee that the cluster numbers align with the geographical locations in Figure 3b and d, other than the fact that the mean salinity of each cluster is similar. I think the presentation of these results could be improved by plotting the change in salinity for the FAFMIP experiments onto the cluster locations in lat-lon space. Note that because each cluster has an associated probability, the results won’t have the same sharp boundaries as the more deterministic plots in Figure 3.

In the Abstract, the authors make the point that the sub-tropics host the largest amount of induced ocean circulation change. This is a very important point and represents the first time (in my view) that such a distinction between ‘surface flux-induced and ‘transport-induced’ surface salinity change has been made at the regional scale. I believe the authors could emphasise this distinction more in the Discussion/Conclusions and in Figures 4 and 5, once they have plotted the results onto the clusters in geographical space.

• Location-based input in GMM

Still on the subject of the GMM clustering, I found it interesting that some clusters (e.g. Cluster 3) cover parts of the Weddell Sea, Labrador Sea, and parts of the sub-tropical gyres in the Pacific. The overall circulation dynamics in these regions is quite different, so it casts some doubt on the ability of the method to distinguish circulation changes in each cluster distinct from surface flux induced salinity changes. It may be, for instance, that temperature-induced circulation changes cancel each other out in all the clusters except cluster 6. Of course, this doesn’t negate the global amplification estimate produced, which integrates over all clusters anyway, but I think a major innovation here is the development of regional estimates. I would recommend that the authors try to add location (latitude/longitude) to the GMM input data (properly weighted so as not to overwhelm the salinity input), such that the clusters are less geographically disparate. This will allow for more concrete statements about the regions experiencing circulation change, as well as a qualitative assessment of the processes that may be contributing to this circulation change.

• Linear assumption of transient response theory

In Figure 5, I found it somewhat concerning that the cluster where temperature-induced salinity change is greatest (Cluster 6) is also where the linear assumption of the theory breaks down in HadOM3, and qualitatively it looks like the faf-all and linear sum are most different in MITgcm. Is it the case that the greater the temperature-induced circulation change the less we may assume this linear relationship holds? One way to test this could be to make use of a more strongly forced case where all clusters experience significant circulation as well as surface flux-induced change and see if (and for how long) the linear relationship holds. This could be an important result, signalling the validity of this method in the future.

• L222: I notice that the authors take the difference between the first and final 5 years as their change estimate. I would recommend the authors instead take a linear trend over the entire time period and multiply the slope of the trend by the number of years they are interested in to get a change. This would avoid issues associated with aliasing if they catch the model in different phases of decadal (or longer timescale) variability.

• Paragraph beginning L245: Like Reviewer 1, I found the significance criteria here very subjective. This reduces the applicability of the method to other data sets, which may not meet these criteria (though IAP does). Why not use a single signal-to-noise ratio as the cut-off for all clusters/regions?

• L275: Can you clarify which particular choices the estimate is insensitive to in this sentence? There are a lot of free parameters in the study (I have focussed mostly on GMM), so it would be good to summarise which parameters you have tested sensitivity to.