The paper presents a well thought-out and intelligent approach to determining the mechanisms behind changes in the strength of the Madden-Julian Oscillation (MJO) teleconnections in future climate simulations. In particular the paper explores the roles of the changes in basic state (including static stability and the basic state winds) as well as future changes in the characteristics of the MJO itself. The results also indicate the degree to which these mechanisms differ in the various CMIP 6 models. The results are fairly convincing. Subject to some revisions, the paper should be published.

There is one relatively major point I would like to bring up, namely the choice of the teleconnection metric. I should first say that I applaud the use of the temporal variance, since in contrast to many other MJO studies, this choice implies the recognition that the MJO forcing (and hence the wave-train response) propagates in a continuous fashion, and does not make the stationary-wave response hypothesis so often invoked. However, I am puzzled by the choice of the low-level v-wind field. The authors stater that: “We use low-level meridional wind in this calculation (instead of other dynamically relevant variables like mid-tropospheric geopotential height, for example), because the MJO primarily drives surface temperature variability across North America via low-level temperature advection …” This is taking a rather limiting point of view, appropriate if the North America T_sfc teleconnection were the main teleconnection of interest. But I think that the authors should (and do) take a wider point of view, for which a teleconnection metric involving perhaps the upper-level (300 hPa) temporal variance of height or v-wind would be more relevant, and would enable the authors to compare their results with the wealth of literature using upper-level fields to gauge the MJO teleconnection. Applying this metric would mean simply re-running the various codes the authors have on a different field, and the comparison between the results for the upper-level and low-level metrics would be quite illuminating.

There are a few conceptual points on which the authors need to expand further (if briefly). As described, the linear baroclinic model is damped enough to prevent the growth of baroclinic waves, which means that the role of the storm-track transient eddy convergences of heat and momentum are not taken into account explicitly. However, since the mean state u-wind configuration is taken from the CMIP6 simulations, the eddy-mean flow feedback is taken into account implicitly. This should  mentioned in the discussion of the LBM. Secondly, Hoskins and Ambrizzi (1993) show that the waveguide is formed in areas near the maximum in K_s as a function of latitude, and has a width that extends between the points of inflection on either side of the maximum (see their Figure 2E). The width of the waveguide may play as large a role as the maximum value of K_s. The discussion of Figure 2 should be modified in this light.

Minor Points:

(1) The paragraph regarding effect of propagation speed (lines 59-64) should refer to Yadav and Straus (2017) who discuss the observed teleconnections from observed fast and slow MJO episodes.

(2) Figure 1 – is the “Heating rate” (y-axis) the heating amplitude A in equation 1?\

(3) The definition of the teleconnection strength is confusing. In lines 183-184: “…calculate the teleconnection strength at each point as the square root of twice the variance of the ensemble mean meridional wind at 850 hPa” Presumably you mean twice the temporal variance (and not the ensemble spread). Also, do you take the ensemble mean first and then take the variance (as indicated in the text above), or take the variance of each run and then take the model mean (as indicated in the caption to Figure 2)?

(4) lines 209 – 213: the eastward extension of the teleconnections near California is not convincing from Figures 2c-2e.

(5) lines 239-241: is the multi-model mean teleconnection strength different from 0 in any meaningful way?

(6) Rossby wave source: equation (2) – what is the definition of the “anomaly” for each model. Is this the difference between future and historical runs?

(7) line 303-305: Figure 5. This figure is not explained well. I am still not sure which is the index in this figure and which is the geographically varying field. I think the index is the area-averaged teleconnection amplitude and the varying field is K_s (albeit smoothed by a running 15 x 15 degree average). This needs to be clarified.

Since the change in K_s between historical and future runs is not shown, how do we interpret the results of Figure 5 in the context of the general statement made in lines 352-353: “Over North America, the change in the mean state alone also leads to decreases in the teleconnection amplitude for most CMIP6 models”?

How does Figure 5 explain (as stated in the conclusions): “For teleconnections to North America in particular, we have identified a region over the eastern Pacific where changes to the winds appear to explain much of the inter-model spread”?

(8) Figure 6a,d : Does a change in fractional area of 1 mean a doubling in size of areas where teleconnections > 0 ?  

(9) line 396: “Overall, over the North Pacific, despite a relatively large range of −21 to 0.6 % K−1…” The rest of the sentence never states what quantity is being referred to.

References:

Yadav, P. and D. M. Straus, 2017: Circulation Response to Fast and Slow MJO Episodes. Mon. Wea. Rev., 145, 1577-1596.

This study examines the uncertainty in MJO teleconnection amplitude changes in North Pacific and North America in January based on results from the linear baroclinic model (LBM). The model is forced with the CMIP6 mean state and an idealized MJO heating with multiple sensitivity runs to test the relative contributions of different MJO and mean state characteristics to the uncertainty in MJO teleconnection amplitude changes. The results indicate that future changes in the mean state wind largely lead to uncertainty in the teleconnection amplitude over both the North Pacific and North America regions. Changes in the MJO propagation speed also contributes to the teleconnection uncertainty. Although some comprehensive simulations are run, the analysis approach in this study may need justification/improvement. Some results are not convincing as they are based only on the LBM and lack other scientific support. I, therefore, recommend this manuscript go through a major revision based on comments below.  

Major comments:

Some analysis method needs justification/modification. For example:

1. L91-93. In terms of the mechanisms related to teleconnection amplitude, the LBM could be TOO simple. Teleconnection amplitude is largely influenced by nonlinearity (Lin and Brunet 2018). Some relationships that may not found in full GCMs such as weaker MJO circulation leads to weaker teleconnection amplitude (Zhou et al. 2020) can be found in the LBM because the LBM is linear. This will make some results unrealistic/less convincing. Therefore, the authors may need to compare their results from the LBM with CMIP6 to discuss which relationships may be due to the linear setting, and which are not. Another way to address this issue is that the LBM package also has a nonlinear version (used in Henderson et al. 2018) which may be better for the investigation of the teleconnection amplitude changes.
2. The authors investigated changes in the MJO propagation speed, zonal extent, intensity, and mean state dry static stability and winds. It is not clear why only these changes are examined. Are the authors choosing them randomly or based on some studies that these are the most robust and significant changes in the MJO and basic state?
3. The authors force the LBM using only the January condition. The authors may need to provide a strong reason why they are not using the entire winter season mean.
4. The authors only use one ensemble member from the CMIP6. However, there can be very large uncertainty coming from different ensemble members. Also, these ensembles may not be the ensembles that produce the most realistic MJO teleconnections in their historical runs. Is there a reason why the authors are not using the ensemble mean?
5. When deciding the lower and upper bounds of the MJO changes, the authors used the estimate from CMIP5 models from previous studies. It makes the analysis inconsistent in this study. It would be better to estimate the MJO changes based on the CMIP6 models. CMIP6 produces a much more realistic MJO propagation (Ahn et al. 2020), the authors would need to discuss if there are any sensitivity of the results. Also, the authors did not show evidence why they choose to extend the MJO to 20° eastward.
6. The amplitude metric in this study may not be clean enough to represent the amplitude only. The metric can also be influenced by changes in the location of MJO teleconnections. Is there a reason why the authors not just simply calculate the spatial variance of MJO teleconnections as in Wang et al. (2020)?
7. The authors investigated the 850hPa meridional wind because they indicate that low-level circulation will be more important to regulate near-surface weather. However, the main purpose of this study is not to examine the MJO impacts on near-surface weather. Then it would be better to use either middle or upper tropospheric wind given that MJO teleconnections have larger amplitude over the middle to the upper troposphere and the results could be used to compare with previous studies.
8. L232-234. Are these supported by CMIP6 projections? Here, it would be nice if the authors can compare their results with the CMIP6 projections.
9. Teleconnection changes are analyzed at the lower troposphere, whereas mechanisms (RWS and Ks) are analyzed at the upper troposphere. This can lead to inconsistency of the results. The authors may want to confirm their results by looking at teleconnection changes in the upper troposphere.
10. The authors analyze the amplitude changes by separating the North Pacific and North America regions. Please provide a reason for looking into different regions.
11. Eq (3): Here, the stationary wavenumber is for the barotropic model and mean wind with no zonal variation and no meridional wind. That being said, this equation is not fully consistent with the basic state they used for the calculation. If the authors are using the full basic state, they would need to use the more complete format of stationary wavenumber (Li et al. 2015). The authors may need to justify why they neglect the zonal asymmetry and meridional wind in Eq (3).
12. Fig. 3. The larger spread of MJO teleconnection amplitude could be due to the larger spread of mean state wind projection by CMIP6s. The authors may need to show 1) whether the wind projection is more uncertain in CMIP6 models than DSE. If this is the case, it is very easy to interpret Fig. 3 that the larger uncertainty in teleconnection amplitude is due to larger uncertainty in future mean wind projection, which is important to look at. 2) However if the projection uncertainty is similar between wind and DSE in CMIP6s, the authors may need to discuss why changes in the wind would lead to larger uncertainty in teleconnection amplitude than changes in DSE.

Some figures that need to be improved or questions regarding the figures:

1. It would be quiet useful if the authors could provide the spatial pattern of MJO corresponding to their perturbed cases. Only the upper bound case would be sufficient to visualize the MJO pattern to facilitate understanding.
2. Fig. 2a. Is this location arbitrary? Why are the authors not showing the multi-model mean of the CMIP6 which may be more useful?
3. Please be very clear here that Fig. 2b is based on LBM response not based on real multi-model mean CMIP6.
4. Fig. 2b. very hard to see the strengthening (highlight of the contour). The authors did not provide the longitude of this eastern boundary to quantify the eastward extension. Also, it may be useful if the authors could provide the difference map with the control runs to help interpret the changes.
5. Fig. 3. 1) No changes in DSE is shown, then how the authors know there is an increase in dry static stability? Is it based on previous studies? Some CMIP6 may project different changes in DSE. The authors may need to show how each CMIP6 model project DSE change and how that relates to teleconnection change. That being said, Fig.3 can be separated into 8 figures. In one figure, one axis represents DSE change in the CMIP6 models, one represents teleconnection amplitude change (either absolute change or fractional area). The same to the wind. By doing this, the authors could see how DSE or wind influences teleconnection amplitude. 2) Also, the authors have never shown how DSE and wind are changing in CMIP6. 3) Very hard to separate the models with these markers here. Using numbers may be better to separate.
6. Fig. 5b and c. Still not clear how these maps are calculated? What region is used for the average of the 15°x15° box? Also, the authors may want to only focus on the regions that have a high correlation coefficient. That means the authors can draw plots only with significant correlation in Fig. 5.
7. Fig. 6. Very hard to imagine why the spread can be this large over the North America region for Fig. 6e. The MJO is changing with the same propagation speed, and the mean state is not changing between the two runs. It may be helpful if the authors could provide the spatial maps of the two runs (historical MJO value and future MJO value) for these 10 models.

Some mechanisms that need more discussion:

1. L300-305. Better to show if this can be found in any CMIP6 model. Also, it is not clear why an increase in the number of Rossby waves can lead to stronger MJO teleconnections?
2. L329-331. What is the underlying mechanism? The more eastward extent leading to larger teleconnection amplitude has been found in Adames and Wallace (2014).

Minor comments:

1. The title is too misleading. Firstly, this paper discusses mainly the amplitude or strength of the MJO teleconnections which should be pointed out in the title. Secondly, the paper runs the simple model using the CMIP6 mean state but the results are not based on the CMIP6 projections, and the MJO heating is even idealized. So the authors may need to change the title to the numerical study of the mechanisms driving MJO teleconnection amplitude changes, etc. Also, this paper is more focused on the important factors contributing to the teleconnection amplitude changes rather than the mechanisms. Most mechanisms discussed in this study are based on findings in previous studies.
2. L5-6. For example? The more eastward extension seems to be a robust change in most models (Zhou et al. 2020).
3. This study is focused on which season? How MJO teleconnections are characterized? These would need to be mentioned in the abstract.
4. L9-10. This is found in Wolding et al. (2016), which would need to be mentioned here.
5. L11-12. Also found in Wang et al. (2020), which would need to be mentioned here.
6. L12-13. Briefly explain more here about the mechanism.
7. L14-16. May be better to put it right after L11.
8. L16-17. This may not be a good argument. The reduction is implied by the LBM experiment forced by the CMIP6 mean state rather than in the majority of CMIP6 models.
9. L23-25. It is not clear how MJO teleconnections would be impacted by these factors. Since these are largely discussed in this study, a much more detailed introduction is needed to emphasize the motivation.
10. L26. How do the authors come to this conclusion? No references are discussed and cited here.
11. L26-27. Why only these two factors are mentioned among very many factors that influencing the MJO simulations? The authors may want to point out that MJO simulation is relatively poor in some CMIP5 models as that is the main focus in Ahn et al. (2017).
12. L28-29. Zhou et al. (2020) already provided some very good analysis of the teleconnection changes. The authors may want to discuss a bit about their results and what remains unknown. This sentence is not their main conclusion. Also, what is the relationship between this and the previous sentence?
13. L30. “MJO teleconnection strength” over which region?
14. L31. L35-36. Need references.
15. L36-37. Discuss how “MJO precipitation intensity or cloud optical properties” would change
16. L39-41. Do the authors mean the large spread in circulation projection is because of the spread in the projection of precipitation?
17. L41-43. what are the relationships between these two studies? One is talking about static stability, one is circulation change? Better to make consistency here although they may be coupled.
18. L57-58. What changes in mean wind and what changes in teleconnections the authors believe would be important to look at? Is there any evidence from previous work which could serve as motivation?
19. L64-65. Is this found in CMIP6 projections? any reference? Or just the authors' hypothesis?
20. L70-71. References or hypothesis? There are many other changes in MJO, such as frequency of events, the authors may want to point out why they are focused only on propagation speed and extent. Is it because these are the most robust changes? If so, please provide references.
21. L73. Please clarify what the authors mean by "MJO teleconnection change". It has been quite confusing throughout the text. How the authors quantify the uncertainty? Please briefly specify here.
22. L79-81. It is better to have the main motivation to fill the gap of previous studies which authors should discuss more rather than from the prediction perspective which is too operational oriented.
23. L81-83. This could sound like a big problem here. The authors may need to prove that this would not be an issue such as the authors are using an idealized MJO.
24. L84. Please clearly describe here what analysis will use CMIP6 model output and what will use LBM. This is quite confusing in the introduction.
25. L85-86. Why the authors hypothesize the uncertainty in projections is large? I did not see this point in the previous paragraphs, only a bit was discussed in Zhou et al. (2020). But this cannot be considered as the authors' hypothesis. The authors may need to provide more evidence to support this hypothesis.
26. L86. “various mechanisms” such as...? Please also briefly describe how to quantify the contribution?
27. Fig. 1. Any references that used similar idealized MJO heating?
28. Please make the discussion consistent. Only use "amplitude" or only use "strength". Now is a bit confusing.
29. L217. Are the authors changing both the zonal and meridional mean winds in LBM?
30. L222. How fractional area is calculated?
31. L244. Can only say “changes in dry static stability”. The authors did not show how DSE is changing in CMIP6s.
32. The finding that RWS is not the key role in changing the teleconnection amplitude is also implied in Wang et al. (2020). They found that changes in the amplitude of RWS does not necessarily lead to the same changes in the amplitude of teleconnections.
33. L290. What sizes of the boxes have the authors tried?
34. I am not sure why the experiments of the MJO intensity are necessary? It is very obvious that with a linear model the teleconnections would change as to how heating intensity changes.
35. L315-316. Is this arbitrary? How the authors chose the models?
36. L326-329. Impacts of propagation speed on the teleconnection amplitude have been found in many previous studies already (e.g., Yadav and Straus 2017; Goss and Feldstein 2018; Zheng and Chang 2019; Wang et al. 2020). 
37. L333. “uncertainty in changes to the MJO”. I do not understand why there is uncertainty in the MJO? Isn't the MJO difference the same between different models? The MJO used in the forcing is just an idealized MJO which is certain. “uncertainty in the mean state”. Why there is uncertainty in the mean state? Isn't the mean state just used the historical value? Is here the uncertainty mainly comes from the model difference of their mean state?
38. L350-351. Be careful to make this conclusion as this is only a finding in the LBM.

References:

Lin, H., and G. Brunet, 2018: Extratropical response to the MJO: Nonlinearity and sensitivity to the initial state. J. Atmos. Sci., 75, 219–234.

Henderson, S.A. and Maloney, E.D., 2018. The impact of the Madden–Julian oscillation on high-latitude winter blocking during El Niño–Southern Oscillation events. Journal of Climate, 31(13), pp.5293-5318.

Ahn, M.S., Kim, D., Kang, D., Lee, J., Sperber, K.R., Gleckler, P.J., Jiang, X., Ham, Y.G. and Kim, H., 2020. MJO propagation across the Maritime Continent: Are CMIP6 models better than CMIP5 models?. Geophysical Research Letters, 47(11), p.e2020GL087250.

Wang, J., H. M. Kim, D. Kim, S. A. Henderson, C. Stan, and E. D. Maloney, 2020: MJO teleconnections over the PNA region in climate models. Part I: Performance- and process-based skill metrics. J. Climate, 33, 1051–1067.

Li, Y., Li, J., Jin, F.F. and Zhao, S., 2015. Interhemispheric propagation of stationary Rossby waves in a horizontally nonuniform background flow. Journal of the Atmospheric Sciences, 72(8), pp.3233-3256.

Adames, Á. F., and J. M. Wallace, 2014: Three-dimensional structure and evolution of the MJO and its relation to the mean flow. J. Atmos. Sci., 71, 2007–2026.

Yadav, P., and D. M. Straus, 2017: Circulation response to fast and slow MJO episodes. Mon. Wea. Rev., 145, 1577–1596.

Goss, M., and S. B. Feldstein, 2018: Testing the sensitivity of the extratropical response to the location, amplitude, and propagation speed of tropical convection. J. Atmos. Sci., 75, 639–655.

Zheng, C., and E. K. M. Chang, 2019: The role of MJO propagation, lifetime, and intensity on modulating the temporal evolution of the MJO extratropical response. J. Geophys. Res. Atmos., 124, 5352–5378

 Review of " Mechanisms driving MJO teleconnection changes with warming in CMIP6”

By Jenney et al

The paper presents a diagnosis of changes in the strength of the Madden-Julian Oscillation (MJO) teleconnections in future climate simulations. The paper compares changes associated with an altered basic state (including static stability and the basic state winds) with those associated with a few selected characteristics of the MJO. The results also quantify the degree to which these factors differ in the various CMIP 6 models. The results are mostly convincing and merit publication. However the authors don’t do a very good job of discussing the limitations and caveats of their study, but this should be relatively simple to fix.

General comments:

1. The authors mainly examine two aspects of how changes in the MJO itself might lead to an altered extratropical response, namely the propagation speed and eastward extent. Given the relatively poor simulation of the MJO in many previous models, it is not clear to me whether these are the only two possible changes that may occur. (I tend to have little faith in the future projections of the MJO in CMIP5 - maybe CMIP6 will be better – and most of the estimates of future behavior in the MJO seem to come from papers that analyze on the order of 10 CMIP5 models)

a. The authors use a very idealized heating perturbation in their equation 1, which clearly will not capture inter-model variability in how well the MJO is represented in the present climate, let alone the future climate. This caveat needs to be mentioned in the discussion.

b. The authors rightly note that their linear model is poorly suited for understanding whether a change in the magnitude of the MJO circulation might lead to a change in teleconnection, but it is conceivable that a stronger MJO circulation might lead to disproportionately stronger (or weaker) teleconnections if nonlinearities were allowed. While this is mentioned near line 320, this caveat needs to be mentioned more clearly both in the discussion and methods as well.

c. The authors are relying on some previously published work on changes in the MJO, but other possible changes might occur in the MJO besides changes in amplitude, propagation speed, and eastward extent. If for example, the meridional extent of the MJO were to become broader as tropical GMS changes its structure under climate change, then the subtropical RWS could change its entire character. Whether this might occur is hard to know given the poor state of MJO’s in CMIP models (at least CMIP5), but tropical GMS is indeed projected to change its structure and I tend to believe projections of, say, large scale GMS than of the MJO itself. The key point is that our current understanding of how the MJO itself is projected to change is incomplete.

d. Another limitation is you only examine January mean state changes. The January Ks should feature more of a barrier in the West Pacific as compared to the shoulder months as the East Asian subtropical is strongest in January. It is conceivable that changes in the mean wind will matter less if you look at e.g. November or March. This limitation also isn’t mentioned in the discussion.

More generally, the authors need to acknowledge in the discussion that they examine only a subset of the possible changes in the MJO that may actually occur. The current statement on lines 407-409 is very much overstated at present and needs to be deleted. I don’t think the authors need to actually perform additional analysis to satisfy these point, rather add a paragraph or so that more fully discusses limitations.

2. Rossby wave source and Ks are both more clearly related to upper level metrics of the flow than lower level metrics. It is important to confirm that results are generally unchanged if some metric of the upper level flow is examined.

3. Figure 5a: This climatology of Ks doesn’t look very much like that of Hoskins and Ambrizzi, their figure 3, especially in the subtropical East Pacific. If you plot Ks of reanalysis data, does the correspondence improve?

Minor changes

Line 12 : I would replace “Rossy wave excitation” with “Rossby wave source”, to be more precise

Line 87-88 this sentence is missing a few words

Line 226 panel b hasn’t been discussed yet

Line 324 “models’ mean-state” shouldn’t this be amplitude of the MJO related heating?

Line 326: “linearly sensitive to the mean state” – this was confusing to me

Line 322-323  “to changes to the MJO itself” I found these words confusing and unnecessary