Review of: Quantifying Contribution of Atmospheric Circulation to Precipitation Variability and Changes in the U.S. Great Plains and Southwest Using Self Organizing Map – Analogue

OVERALL COMMENTS:

This is a really interesting paper. I think this is a valuable contribution. I am a big proponent of the use of classification techniques (and SOMs) in helping to analyze and visualize the complex relationships between atmosphere and surface impacts – and this is an excellent example. However, I have some semi-major and minor comments that I detail below, that I would like the authors to address and consider, prior to publication. Also, this manuscript might need some slight language editing.

MAJOR COMMENTS:

I think the dynamic vs. thermodynamic dichotomy is a bit misleading. This is because z500 and IVT are going to have thermally-related variability inherent to them, right? While you only explicitly include z500 heights and IVT on each day into the classification, that does not necessarily mean that many/all other environmental variables (e.g. 2m temperature, 850t, 2m dew points, 925winds, SLP, and everything else) are not also ‘indirectly’ playing a role in classifying a day’s weather. That is to say, classification is implicitly wholistic – it categorizes the *wholistic/synergistic* environment over a particular time period (herein, a day). While this is not an issue in most research using classification (and is arguably a benefit of using classification in applied research), herein, when you are trying to use classification to de-couple the dynamics portion from thermodynamics, I think it is problematic. I just cannot de-couple this in this manner… To me, what you are actually calculating here is not dynamic vs. thermodynamic contributions, but rather the variability that can be accounted for using this categorization (i.e. this SOMA-based model) and the residual variability that cannot – and both the SOM and the residual contain both dynamic and thermodynamic contributions within them. That is, you do not have P’_dyn vs. P’_the, but rather more like P’_SOMA vs. P’_residual. In this sense, there is nothing inherently wrong with what you did, just the way you interpreted it, and the dynamic vs. thermodynamic is a misnomer. But, perhaps I can be convinced otherwise.

INDIVIDUAL COMMENTS:

Line 100-102: Need a bit of clarity here… the daily standardized anomaly is applied to the pentad moving average filter? Or the opposite? Or are these two things done separately?

Line 102:; Why 1950 to 1999 for the climo? Why not the entire period, or the most recent 30-year climate normal period? Or a period that ends in the present (2021)?

Line 131: The way this is written is still slightly confusing in terms of how many dimensions you actually have here. It is a 2-dimensional data matrix with a size of 3782-by-26,280 (with perhaps a few leap-days in there), correct?

Line 160: While I am fine with the way you did this, just as a note, if trained using a batch process, then slightly different input vectors might be used and thus, result in different final clustering solutions, even with all the other ‘settings’ the same. So, you might want to run each node number multiple (10-20) times, and then average their QE, TE and CE.

Figure 2: It would be nice if you could incorporate the seasonality of frequency of each atmospheric pattern into this graphic instead of having a separate figure 3.

Figure 3: I think the y-axis on these should be identical, so we can tell which ones are more/less frequent overall.

Figure 4: Again, I think the y-axis on these should all be identical.

Line 226 and Figure 5: I rarely see CAPE and CIN in standardized values, but rather in their more-traditional units. I think you need to be careful here, as for example, a lower than average CAPE for a location that has pretty high average CAPE normally, might still mean that the atmosphere is pretty unstable. Also, are these values deseasonalized?

Line 230: D1 is perhaps suppressing convective development, but convective *initiation* (i.e. the ‘triggering lifting mechanism’) is as somewhat separate ingredient.

Line 235: the soil moisture thing comes out of no-where…. I don’t disagree, but, I do suggest a citation for this.

Line 274-275: I think you need to be careful with how this sentence is worded. I agree that the dynamic factors are likely the major contributors, but that statement is predicated upon how you specifically defined “dynamics” herein (with z500 and IVT SOMs). If you had chosen different variables to represent “dynamics” (e.g. SLP) would this statement still hold? Would the statement be weaker? Would it be stronger?

Figure 8: Very interesting figure! I like it. However, why are the types color-coded the way they are? Is there a reason? It looks roughly like wet is green, and dry is red/orange/yellow, but is there a specific method for this?

Figure 9: Again, these subplots should have the same y-axis.

Line 314: “… larger or smaller than 90%...” - wouldn’t that be ALL of them?

Line 316: yes, but this is partly because PDO is not as often >0.5 or <-0.5 during these months, and thus, less sample size, right? And why the +/- 0.5 thresholds… why not 1.0, or 0.25??

Line 321: Perhaps I am missing something here, but, just because these nodes have been found to be related to PDO, doesn’t necessarily mean that this represents the “PDO-related dynamic contribution” to P’ … moreover the way that you have constructed this, makes it impossible for PDO to contribute MORE than the SOM-based dynamic component. That is, it could very well be that PDO is a more-dominant factor (more dominant than the SOM patterns), but this methodology would not allow for that. I think there is a better way to tease out how PDO is contributing to P’ in these areas. At best, perhaps you can say that this is showing the combined contribution of the SOM-patterns that have been found to be most influenced by the PDO.

Also, who is to say that this represents PDO-only related contributions to P’? What if you did this for AMO and AMO phases?? Or the IPO? In many ways, the SOM patterns you define are simply the regional-scale manifestation of hemispheric- to global-scale variability in the multiple internal climate oscillations occurring simultaneously (PDO/AMO/IPO/ENSO and that of all other teleconnections/oscillations at various periodicities).

GENERAL COMMENTS:

Overall, this paper can be great contribution to our science community. The authors come up with the novel approach for quantifying the contribution of atmospheric circulation to the recent precipitation variability in US. They combine two statistical techniques - Self Organizing Map (SOM) and circulation analogue - to effectively visualizing circulation pattern as in SOM and quantifying the dynamical contribution as exact as in circulation analogue. Using this new SOM-Analogue (SOMA) approach, they investigate the link between circulation patterns and daily precipitation anomalies in different seasons and PDO phases. The results provide the valuable insight how the specific circulation pattern leads to the regional precipitation anomalies in US. However, I think there are some major issues in the development of new SOMA approach and the analysis regarding PDO-related contributions. I would suggest the authors to address below major/minor comments before the publication.

MAJOR (SPECIFIC) COMMENTS:

Decomposition of dynamic and thermodynamic contribution

The variables Z500 and IVT are used for elucidating the dynamic contribution to the precipitation anomalies. However, IVT is multiplication of wind vector (dynamic variable) and moisture (thermodynamic variable), so the SOMA from IVT would also contain the thermodynamic contribution. To decompose the dynamic and thermodynamic contribution, I think dynamic variables (e.g., velocity potential) has to be used instead of IVT. Or, rather than focusing on the decomposition of dynamic/thermodynamic contribution, the authors can express the same results as the contribution from the moist circulation and the residual. In my opinion, the interesting science in this study is to characterize the circulation pattern responsible for the regional precipitation anomalies, and the exact decomposition of thermodynamic and dynamic contribution is kind of secondary interest compared to that.

If the authors want to decompose the thermodynamic/dynamic contribution, then I think new variable should be used for SOMA instead of IVT. Or, authors can express the same results as the contribution from the moist circulation and residual, with revising rest of the manuscript accordingly. 

Issues regarding the data and SOMA approach

First, is the observational data used for SOMA detrended or high-pass filtered? In previous studies using circulation analogue (Deser et al. 2016; Lehner et al. 2018), the dynamic contribution is found after the observational data is detrended or high-pass filtered. This is for eliminating the forced thermodynamic contribution in the timeseries and to focus on the dynamic contribution. In this manuscript, it seems there are no mentioning about such data processing. I think the detrend is needed if it is not done, and it should be mentioned if it is done. Or, you may show that such data processing doesn’t matter to your results.

Second, in L197-199, to apply circulation analogue to each BMU node, the authors regress total precipitation anomalies onto the circulation anomalies (PC values), and multiply that regression coefficients to the circulation anomalies (PC values) to get dynamical precipitation changes. I think this can overemphasize the contribution from the circulation anomalies, and authors may need to come up with another approach for this step. The detail is written below.

 In previous studies for circulation analogue, the linear coefficients or subsamples to estimate the dynamic precipitation anomalies are calculated only using the circulation anomalies, as you wrote in L205-206. However, here, total precipitation anomalies are directly regressed onto the circulation anomalies in same BMU node to get coefficients, and that regression coefficients are used to estimate the dynamic precipitation anomalies. This is like assuming that total precipitation anomalies are similar to anomalies from the moist circulation (or dynamic contribution) even before the decomposition. I think this would artificially overemphasize the dynamic contribution. So, I recommend you to revise step 4 in L197-199. You may use the linear coefficients for reconstructing target-day circulation from analogue-day circulations to getting target-day dynamic precipitation anomalies from the analogue-day precipitation anomalies in same BMU node, following Deser et al. 2016. I think you should avoid to directly link the total precipitation anomalies to the circulation anomalies to get the coefficients for estimating dynamic contribution.

PDO-related analysis

The precipitation anomalies related to PDO is often linked to the large-scale circulation over the North Pacific (retreat of Aluetian Low/ expansion of subtropical high), and it was less linked to the circulation anomalies within the US. This study can further investigate the teleconnection impact of PDO on the circulation anomalies within US, which will be the valuable contribution for regional teleconnection studies. However, the regional circulation and precipitation anomalies related to PDO will probably sensitive to the detailed pattern of tropical SST pattern (as it is known that the teleconnection within US depends on ENSO diversity), and they will be affected by the other variability (e.g., AMO, ENSO) as well. In this situation, the mere difference of positive and negative phase of PDO with relatively short length of observation would not sufficient to convince the PDO impact in this study. These limitation needs to be addressed in the manuscript.

 In spite of above limitations, I think the analysis in this manuscript can be developed further to shed light on understanding the PDO teleconnection impact. The figure 10 is a good starting point where PDO-related local circulation/precipitation anomalies can be hypothesized and analyzed in detail. I suggest the authors to provide the figure for precipitation anomalies corresponding to figure 10, showing the precipitation anomalies linked to each circulation changes between two PDO phase (for three target regions). And then, authors may select the circulation node which shows strong precipitation anomalies, linking the PDO to that circulation and precipitation anomalies. If the PDO-induced teleconnection can explain those circulation pattern with the previously known mechanisms, authors can somewhat convince that their PDO-related precipitation anomalies are indeed PDO-induced. In summary, I think the current analysis/discussion for the PDO impact is not enough, and authors need to investigate the significant circulation pattern in Fig. 10 and try to link those to the PDO-related teleconnections to ensure the PDO impact.

MINOR (TECHNICAL) COMMENTS:

 L60: Is there any need to use the term “surface parameter”? I think you can just directly mention the precipitation instead of “surface parameter such as precipitation”. It would be great if the terminology in this paragraph is adjusted accordingly.

 L60-63: I think it is hard for readers to understand Cassano et al. 2007 (C07) SOM method by reading few sentences here. I suggest you to add and explain the equation 1 and 3 of C07, since they are quite simple. Those equations may be added on the line with simple explanations.

L138: I think it is better to represent the fraction of variances only for the Z500 and IVT combined variability since the EOF analysis is done simultaneously to two variables.

L164: “issmall” to “is small”?

L194-196: Why do you find the analogue day within 91 calendar windows? This might be due to the seasonal dependence of circulation-precipitation relationship, and it is better to mention this somewhere in the text.

L317: “Fig. 9 (1st column) shows the period mean P′ for different seasons and regions” à There are no seasonal information in Fig. 9. You may need to change the text.

L323: “Table2” to “Table1”?