Review of Watson-Parris et al (2024)

The years 2023 and 2024 have seen exceptional levels of global warming, and climate scientists are still trying to attribute this warming to different causes. Watson-Parris et al. add to the growing body of literature assessing the impact of IMO shipping regulations on near-term warming. 

They not only present a new set of simulations which is broadly in agreement with previous work on this topic, but also try to reconcile different climate model results which seemingly came to different conclusions. Their discussion on methodology and framing is very valuable. I think this is an excellent piece of work, and would like to see it published after the authors consider the minor comments below.

Comments

Title : Avoid having a subjective assessment of the strength of the IMO effect in the title (“Weak”). Maybe saying “within internal variability” is enough and more objective.

Assuming the radiative forcing is 0.1W/m2 or more, that corresponds to ~1/10th of the aerosol ERF which is not insignificant. How that translates to surface temperature change may be considered a different question. There could be competing effects: it takes time for the surface to warm and hence for the signal to emerge, and the background scenario also has declining shipping emissions so the difference between control and perturbation scenarios gets smaller after 2030. This probably explains why the temperature change maximises around 2030 in various models as discussed around L.288.

Have you compared your TOA SW and LW radiation to observations as in Quaglia & Visioni? Their figure 1 shows a very large increase in ASR at the TOA in 2023 which is not captured by the models (with and without shipping regulations, though they do help). Of course this increase can come from other aerosol changes or natural variability. Maybe the observed changes are within the variability of your larger ensemble? If it isn’t, does that say something about the ability of CESM2 to capture observed changes (especially given large uncertainties around aerosol ERF)? I recognise this may be a lot of extra work and would be happy to see this work published without it.

L.64-5 What’s the reference for the 0.5W/m2 value? Diamond (2023) gives a value of order 1 W/m2.

L.92 What Quaglia & Visioni call a radiative forcing is in fact a change in TOA radiation between 2 sets of coupled simulations, rather than being a ERF calculation which assumes fixed SSTs to remove the effect of feedbacks. So change “ERF” in L. 92.

L.283 the p=0.18 is for 2020-40 I imagine?

Make the figures higher resolution (plt.savefig('filename.png', dpi=300) for ex in matplotlib).

Review of Watson-Parris et al. (2024)

In this paper, the authors use a 18-members ensemble of CESM simulations to investigate the potential impacts of the changes in shipping emissions in 2020.  The paper has a rather comprehensive review of recent papers on the same subject, and is definitely well written. I agree with the first reviewer about the value of their discussion and the importance of this study. I also agree with the first reviewer on the framing problem: “weak” is a personal characterization of the results, and one that I’m not sure is very informative here. It is clear, as the authors also note, that this signal is not so easy to detect, and different investigation methods yielding different results speaks volumes to that. However, the authors also say that “IMO regulations may contribute up to at 0.16 ℃” (note the at typo in the abstract) for individual years, and I think it’s hard to reconcile this presumpt “weakness” with the relevance that that might have to, for instance, intensifying heatwaves or fire weather over specific regions.

Differences in conclusions are particularly interesting when considering that, using a very similar set-up (with the only difference being the magnitude of the SO₂ reduction, 80% and 90%, and the size of the ensemble, 18 and 10), their results are strikingly different from those in Quaglia and Visioni (2024) (Q&V), in review for ESD. In these results, I wasn’t able to find any mention of what size of ensemble the authors here use for the baseline simulations: do you use the whole 50 (considering only the smbb runs) or 100 CESM-LE, or only the same ensemble members you spun-up from? I think this could be useful to understand why (acknowledging they might be using slightly different methodologies) they find no significance in Fig. 3 while Q&V find statistically significant differences both in TOA fluxes and in detrended monthly temperatures, as well as the maps in their Fig. 3. Could it be that a 10% further reduction contributes to the significant/not-significant threshold? Maybe the two teams can find a way to compare their results, either here or in the future.

One possible curiosity would be to check if all the simulations were run on the same cluster as the original CESM-LE runs: in the Acknowledgments here, it looks like these simulations might have been ran on another one? If there is no bit-by-bit reproducibility in the branch, this might influence such a delicate assessment.

I also think the maps here in Fig. 3 pick two specific cases in which the results will look less significant by design: for the 2020-2025 period, by including a at least 12 months period in which the “termination shock” (to quote from the Yuan et al. (2024) paper) hasn’t manifested yet, while for the 2020-2040 period, by including years in which the scenarios somewhat reconcile in terms of shipping emissions.

I want to stress that I’m not trying to imply that one study is wrong and the other right: I think that the fundamental differences in answer come from differences in methodology and perspectives: this study takes a more “climatological” approach and find that, especially when considering the underlying global warming trend, the signal is hard to detect over decadal timescales, whereas Q&V take a more “detection and attribution” approach and ask if, for a specific year, close enough to the termination effect, it is possible to make a probabilistic determination of how even a “minor’ effect might have contributed to pushing  even further a year that is now almost universally recognized as highly anomalous. Indeed, I think in the abstract itself, as I pointed above, the authors acknowledge that they can’t exclude that IMO changes have produced a significant change in the specific year under question. So I strongly suggest the reviewers reconsider some of their language in light of this.

Minor quibbles and comments:

Sometimes the authors use ºC, sometimes they use K, even in the same phrase (see line 77). I suggest to reconcile that.

Note the "at" added to line 33 of the Abstract.

Fig. 4: are these results implying that during a positive ENSO phase, in 2023-2034 one would have expected a cooling contribution from the change? I think this is also rather different from the Q&V analyses, and very counter-intuitive…

Fig. 5: There seems to be a very weird ensemble member that starts at 1.5 and cools down to 0.9 by 2025. That sounds highly anomalous.