This piece of work applies a new methodology to look at the decadal variability to understand the response across an ensemble of idealised paleoclimate simulations.  I do not see anything incorrect in the work. But I’m not sure that the current layout will result in many citations. This is because the manuscript jumps between trying to describe two things simultaneously: a new method and some scientific results. As the manuscript is submitted to GMD, I presume that the authors consider the new method to be the primary innovation and will address my comments and recommendations accordingly.

I see that there are three important facets of the methodology that are outside of the standard approach. Firstly, there is the fact that the EOFs are computed by looking across the whole ensemble – rather than separately within each single model. This is a nice touch and should be made clearer within the text (currently this is mentioned briefly on L123, but not stressed as key aspect of the methodology). I happen to have adopted this approach myself before (Chandler et al, 2024, https://doi.org/10.1175/JCLI-D-23-0089.1) to look at regional models. However, we were looking at the mean climate, not variability, and the primary modes were detected between the models. I was therefore surprised that your approach does not pick up any inter-model variations. I guess that this comes from the application of the decadal filtering, which is in effect removing the mean climate from the individual models. You ought to explain in more detail what kind of filter is being applied, and its implications. I suspect that you are using a band-pass filter, and that if you instead used a low-pass filter you find fundamentally different EOF patterns (more akin to the EPP, we describe in Chandler et al). The labelling of Fig 1 and 2 implies that they show EC-Earth’s EOF patterns – rather than full ensemble patterns. Only the PCs, directed graph and transition timeseries relate to the particular EC-Earth simulation.

Your second innovation is the introduction of the directed diagrams. I confess that I find these hard to interpret, but I can see that they are important. Can you please spend a bit more time describing them? Perhaps thinking of them in a reduced dimension set would help; say by using the 2 ENSO modes of Ren & Jin (2011, https://doi.org/10.1029/2010GL046031) at then you can place the phase along the x and y axes. Can you also create some possible directed graphs for a system in which all the PCs are truly independent, through building a simple statistical model ? These would then provide a suitable null-hypothesis and allow some statistical testing to be undertaken.

Your third innovation involves the use of Shannon’s entropy. You provide an equation for this and then describe some of its properties in the methods section. However, when showing the results, all the values are approximately 3. I didn’t get why that should be so. I guess it’s related to either the fact there are 3 EOFs or the fact that each PC is divided into 3 states, but I don’t know which and you didn’t explain.

I have 3 other substantive comments:

1. Both the AMM and AZM/AEM are more often defined by SST indices, rather than through principal components. It would be informative to compare your new method against this style of definition.
2. There is no comparison to observations contained within your analysis. Can you project the resultant EOFs onto a reanalysis dataset and look at the real world?
3. You have chosen a case study (idealised green Sahara experiments during the mid-Holocene) that is not readily accessible to the general reader, and therefore requires a substantial amount of additional introduction and methods that get in the way of the methodological innovations you are trying to explain.

Other comments:

• You need to label each panel of a figure rather than collect them together (so Fig 1 has panel a-h, not just a-b).
• Can you make the system-state classification centre around the neutral state of the 3 modes? This is the most intuitive way of thinking of thinking about them, but I don’t see where that state is - presumably it is the most common mode in the directed-graph (but not necessarily).

The presented study has many strengths. First and foremost, it introduces an innovative approach that is rarely seen in the literature and aligns with established methodologies for assessing climate variability. The use of Shannon entropy to analyze climate variability based on trajectories in phase space is a novel method that goes beyond traditional metrics. Constructing a phase space using the first three principal components (PCs) of SST and precipitation, derived from PCA, is consistent with physically justified modes of variability (AEM, AMM, SASD). The comparative value of the study is enhanced by the use of four different models (EC-Earth, GISS, iCESM, CCSM-Toronto) and multiple scenarios (PI, MHPMIP, MHGS, etc.). Analyzing SST and precipitation separately enables the identification of potential decoupling in their response to different forcings. The application of a bootstrap approach to estimate confidence intervals for entropy is methodologically sound.

However, the study is not without flaws. One contradiction lies in the implicit assumption that high entropy equates to high physical variability. Shannon entropy measures the diversity of system states, but not necessarily the amplitude of fluctuations. A simulation with low-amplitude variability but frequent state changes may yield high entropy, despite low physical variability.

Another notable shortcoming is the lack of validation against observational data, even though the authors acknowledge that such a comparison would be possible. This is a critical point — without observational benchmarks, we cannot determine whether the models’ entropy values are realistic or merely reflect internal simulation dynamics.

A further difficulty is the inconsistency in model parametrization. The models differ in terms of the factors they include (e.g., vegetation, dust, lakes), making comparisons challenging. The study lacks an attempt to isolate partial effects — for example, what specifically causes changes in entropy: dust, vegetation cover, or their combination?

Moreover, the study does not quantitatively separate different sources of uncertainty. Although three types are mentioned — internal variability, discretization, and scenario-based uncertainty — their individual contributions to total variability are not assessed.

While the selection of three principal components may be reasonable, the study does not examine the sensitivity of results to the inclusion of additional components.

The use of maximum entropy for each simulation as a reference point is statistically understandable but may lead to non-comparable thresholds and obscure differences stemming from less dynamic models. This approach might favor models that “artificially” gain entropy through threshold adjustments.

Lastly, the graphical representation of results as directed graphs is visually complex and difficult to interpret.

One final comment, offered with all due respect and goodwill: a common PCA analysis should be performed for all models and for each variable (SST and precipitation) using a merged dataset from all models and experiments. This would ensure a shared phase space and resolve the issue of cross-model comparability.

2025-12-26