RC1 comments repeated here , authors' replies in bold.

The paper deals with limits of predictability associated with uncertainties in simulated diabatic heating over the Indian ocean during the MJO. This is investigated by re-running a set of 60-day long ensemble forecasts assuming perfect initial conditions. In other words, the study addresses a component of predictability associated with applied model errors. The error was simulated by stochastic perturbations of the tendencies due to physics geographically limited to the Indian Ocean region 50E-120E and 20N-20S.  Their effects on predictability are studied in the ensemble spread of the vertically integrated diabatic heating, of Rossby wave source, of the heat flux and of the vorticity field at 200 hPa.  The authors report predictability limits, defined as 0.5 of the saturation value of the ensemble variance, to be between 2 and 3 weeks.

Response: Our interpretation is not that our study addresses the component of predictability due to model errors, but that it addresses that component due to intrinsic variability in the model (“internal error”). The stochastic parameterization scheme which is used (SPPT) is considered an integral part of the IFS, and other research (i.e. Selz, 2019) supports the notion that the use of such schemes gives more realistic estimates of intrinsic predictability. The novelty of our experiments is that we suppress SPPT outside the Indo-Pacific region, and that is the only change we make. The ensemble spread is thus due entirely to processes internal in the model.

Summary:

The authors address an important problem but the paper in its current shape does not provide significant new insights  on the teleconnections associated with the MJO or associated predictability limits. 

Response: We may not have emphasized the role of the Rossby wave source in the paper enough: the rate of spread of the Rossby wave source gives an indication of how the spread of the tropical heating is translated into the uncertainty in the mid-latitude response. We agree that more diagnostics concerning the rate of growth of the Rossby wave source (and other measures of the mid-latitude error) will be useful and we intend to provide them.

One way to revise the paper would be to compare the results with the operational seasonal forecasts which sample uncertainties in both initial conditions and  model errors.

Detailed comments:

1. Assumptions

The authors argue (Lines 55-56) that they apply the "perfect model" assumption in their study of (Lines 46-47) "uncertainties in MJO heating, as witnessed by the variability in the details of heating among different episodes of a given phase."  The statement should be re-written in line with what has been done (perfect initial-conditions and simulated model error). Please  discuss what is meant by "variability in the details of MJO heating" and provide references.

            We plan to discuss, both in the revised Introduction and the Results sections, previous work which the reviewer is correct to point out. These include studies of predictability focusing on the roles of: (a) the size of the initial error (Zhang et al., 2019), (b) the role of domain (polar, mid-latitude, tropical) in which the errors are introduced (Judt, 2020), and (c) specific to the MJO, the spatial and temporal variability of Indo-Pacific heating, as seen in low-resolution models (e.g. Lin and Brunet, 2018) and intermediate resolution models (Kosovelj et al. 2019).

             By “variability in the details of the MJO heating” we mean the differences in the evolution of the magnitude and spatial of the heating between ensemble members that are initialized identically. This spread is an indication of the variation of heating in the real atmosphere among episodes that are characterized by one phase of the MJO.

1. Methodology
2. a) Lines 59-61: "the stochastic parametrization scheme (SPPT) described in Leutbecher et al. (2017) has been altered so that perturbations which affect (directly or indirectly) diabatic heating tendencies are confined to the tropical Indian Ocean region".  Some details would be useful here, such as the amplitude of perturbations compared to the signal. Different wording on what parts of the model physics have been perturbed is provided at different places in the paper, and it should be clarified.
3. b) The computation of the divergent horizontal wind in Eq. (1) should be explained. 

The horizontal winds (u,v) on the Gaussian grid were used to compute vorticity and divergent in spectral space (i.e. the coefficient of the spherical harmonics) using standard methods. The vorticity and divergence were truncated to T42. Setting the vorticity spectral components to zero, we transformed back to (u,v). This will be amplified in an appendix.

1. c) What is the sensitivity of the results to the choice of the latitude belt used to compute S?

This will be included in the revised version of the paper.

1. d) Why is the integrated diabatic heating a good measure of the MJO predictability as compared for example with precipitation?

The atmosphere is forced by diabatic heating, which includes latent, radiative and turbulent heating, each of which has its own vertical structure. The precipitation is the vertical integral of only one component (latent heating). While we have not discussed the effects of the vertical structure of heating, this is an area we plan to explore in the future.

1. e) Why is vorticity a good measure of the forecast error growth in the tropics (Figures 8-9)?

It is not the only measure; we will examine other measures.

1. f) How is the estimated predictability limit sensitive to different choices of predictability time (Line 211) taken to be 50% of the saturation error?

We will present results for the predictability limit as a function of spatial scale and threshold.

1. g) How is the wavenumber analysis performed, is it spherical harmonics space?

The zonal wavenumber analysis is performed on latitude circles (i.e. as a function of longitude only) after the fields have been transformed back to the Gaussian grid using a T42 truncation in spherical harmonics.

1. h) The ENSO events are introduced in 2.2  and Figures 1-2, but little mentioned after 3.1.
2. Relation to previous work

Many studies addressed the response of tropical and extratropical circulation to MJO-like heating perturbations. I disagree with the authors' statement that (Lines 47-49) "the wealth of MJO teleconnection research discussed above has relied almost exclusively on the Wheeler-Hendon multivariate empirical orthogonal function framework (Wheeler and Hendon, 2004)." See for example https://doi.org/10.1175/JAS-D-18-0203.1 and references herein. Similarly, there is a wealth of research in predictability associated with MJO that is missing in the introduction and discussion of the results.

We plan to discuss, both in the revised Introduction and the Results sections, recent previous work which the reviewer is correct to point out. These include studies of predictability focusing on the roles of: (a) the size of the initial error (Zhang et al., 2019), (b) the role of domain (polar, mid-latitude, tropical) in which the errors are introduced (Judt, 2020), and (c) specific to the MJO, the roles of spatial and temporal variability of Indo-Pacific heating on MJO predictability, as seen in low-resolution models (e.g. Lin and Brunet, 2018) and intermediate resolution models (Kosovelj et al. 2019).

1. Results

This paper, like several earlier studies of predictability, finds a predictability scale of 2-3 weeks and that longer scale have longer predictability. In the present study, the predictability limit is due to perturbations in model physics. Previous studies such as https://doi.org/10.1175/JAS-D-19-0116.1 find similar intrinsic predictability to be due to small perturbation in initial conditions (perfect model assumption). I wish the authors discussion their predictability results in comparison to other studies of predictability in the tropics and globally. 

How does the growth of spread in selected variables compare with the scale-dependent circulation response to heating perturbations in  https://doi.org/10.1175/JAS-D-18-0203.1 (their figures 7-8)?

A number of previous papers show the growth of errors as a function of spatial scale (characterized by zonal wavenumber) for different variables and pressure levels. In the revised paper we will compare our results to those in a similar format.

Overall it is unclear why the ensemble spread of diabatic heating is a good measure of predictability limits, rather than prognostic variables of circulation and/or precipitation.  For example, how is the amplitude of the ensemble spread in diabatic heating related to the predictability of precipitation? Could the results be coupled with the precipitation validation in the ECMWF model forecasts (e.g. https://doi.org/10.1029/2020GL091022)?

In the tropics, the spread of diabatic heating is presented to document just how variable heating is, and to show the forcing for the extra-tropical spread in circulation. Whether the tropical precipitation in this model is realistic is a different question: it is the total heating that is coupled to the atmospheric circulation. Heating in mid-latitudes is a good indicator of activity in the storm tracks, as much of the heating arises from the warm conveyor belts in extra-tropical cyclones. We will clarify this in the revised paper.

Comments from Reviewer 2 are in regular font – responses in bold small font

R2 Major Comments:

1. While it is true that only the model physics over the Indian Ocean are perturbed, the effect of chaos seeding (Ancell et al. 2018) quickly spreads the error over the whole globe in non-physical ways. This likely means that the results are indistinguishable from results that would have been obtained if SPPT perturbations were added to the entire tropical belt or to another location that is convectively active, such as the Amazon. I suggest testing this out.

This is a valid point – any perturbation will rapidly spread due to variety of reasons, some numerical and some intrinsic to the system. We want to point out that the stochastic parameterization scheme which is used (SPPT) is considered an integral part of the IFS, and other research (i.e. Selz, 2019) supports the notion that the use of such schemes gives more realistic estimates of intrinsic predictability. Thus the effects of restricting the SPPT to the tropical Indo-Pacific region may be confined to the early growth of errors.  This may be worth testing in a future project. [The simulations done for this paper were quite computer-intensive.] We thank the reviewer for this interesting reference and will include a discussion of this in the revised paper.

1. It would be interesting to see how different the result would be when “butterfly seeding”were used, i.e., tiny initial perturbations of the initial conditions everywhere on the globe, as in Judt (2018) or Zhang et al (2019). I recommend running an additional ensemble with this kind of perturbation and comparing the results with the ones obtained so far (this additional experiment would also be more in line with intrinsic predictability, whichusually addresses predictability limits arising due to miniscule initial condition uncertainty).

While we agree that this would be an interesting comparison, there is an arbitrariness in perturbing initial conditions. In fact the whole purpose of the cited paper of Zhang et al. is to compare the error growth due to current, operational uncertainty in the initial conditions (taken from multiple reanalyses) to a hypothetical “perfect” scenario that is implemented by arbitrarily reducing the initial condition uncertainties by a factor of 100. Such a study could be implemented in the ECMWF modeling system since there is in place a procedure to perturb the initial conditions (although we did not use this in the simulations). As above, this computer-intensive proposal is a goal for a future project. Again the Discussion section of the paper will be augmented by a discussion of this alternate approach to estimating “intrinsic” predictability.

1. Is it necessary to discuss the Nov and Jan initialization experiments separately? In my opinion no, as the differences between Nov and Jan events are not large enough to warrant the extra work for the reader to keep track of two sets of results. I therefore recommend combining all experiments into one “grand experiment”. This shouldn’t affect the conclusions.

This is a valid point for most of the diagnostics. It is only for the figures relating to the role of the stratosphere  that we have reasons to discriminate the Jan. and Nov. initial conditions. This is because the polar vortex may not be fully formed in November, so that the “stratospheric pathway” towards uncertainty growth will have a different time scale for the Nov and Jan runs. But we will try to combine the results from all the runs for the other diagnostics.

1. It looks like Fig. 3 is not referenced in the text. Furthermore, I am not sure why the “Rossby wave source” is analyzed at all. I suggest removing this analysis or better motivating it.

This is simply a mistakeo on our part – there was discussion of the Rossby Wave Source in our first draft which inadvertently got omitted. The Rossby Wave Source is one dynamical indicator of how the tropical heating affects the extra-tropical circulation, and we will motivate it more fully in the revised version.

1. Section 3.4 seems to be lacking a conclusion, or at least I’m left with this impression.

Minor Comments:

1. L.45: How does the presence of baroclinic instability limit the predictability of MJ teleconnections? Through error growth associated with baroclinic instability? Yes- this will be mentioned.

1. Figs. 1-3 and 6-9 imply that the runs are 30 days long, while the other figures show the entire 60 day time period. Why are only the first 30 days shown in the Hovmöller plots? Maybe nothing interesting happens after 30 days, but then it should be indicated somewhere so the reader doesn’t end up confused whether or not the experiments are 30 or 60 days long.The experiments are 60 days long, but for some diagnostics it is only the first 30 days that are interesting.  This will be clarified in the text.

1. L.102: Just curious, why are you not using ERA5 to initialize the ensembles? The model configuration is that used by ECMWF for its monthly forecasts, and the system is set up to use ERA-Interim for initial conditions.

1. L. 155-177: I don’t think the description of the figures is necessarily wrong, but I do see a

lot of noise in the Hovmöllers and not so much of the described

We will look at this carefully.

1. Fig. 1 (and Fig. 2): The evolution of the standard deviation in panels (d) shows very little propagation with the maximum being anchored between 70 and 100 deg E, unlike the heating amplitude . Is this because of the continuous perturbation in this region? Yes you are correct. This will be mentioned in the text

1. L. 188: “In the Indian Ocean the two fields are comparable.” I disagree, there seems to be more red in Fig. 1d than in Fig. A1 over the Indian Ocean.  Our point was only that the SPPT induced noise in the Indian ocean heating that has a the same order of magnitude as uncertainty that can be estimated from reanalyses, not that the two fields are nearly identical. This will be clarified.

1. L. 211: Where does the 0.5 threshold come from? It seems arbitrary. In response to another reviewer, we will show the predictability times as a function of threshold.

1. L. 298: “small scales” is relative, wavenumber 21 is “large scale" from the view of a synoptic/mesoscale meteorologist. Yes that was a bad choice of wording; we will correct.