Review of Xue et al, “Southern Ocean phytoplankton under climate change: shifting balance of bottom up control”

Summary:

In this manuscript, the authors use a multi-model ensemble (MME) to understand how phytoplankton biomass and production is changing with climate change in the Southern Ocean. They use multi-model means and an emergent constraint approach to show that phytoplankton could become more concentrated in a shallower mixed layer, improving light conditions for photosynthesis but also making them more accessible to zooplankton grazing. Therefore, top down controls from grazing compensates for improved light conditions, resulting in little change to phytoplankton biomass as a result of climate change. They use emergent relationships between observed seasonal cycles of chlorophyll and mixed layer depth to constrain the projections.

Overall comments:

I found this manuscript interesting and generally well written. The methods are quite clear and the figures are of good quality. I appreciate their emergent constraint approach. I think this paper should be published eventually because the approach is novel and their hypothesis about phytoplankton change in the Southern Ocean is intriguing. However, there are three main points that I would like to see addressed before publication.

• I think the authors need to tone down their definitive language; as it is written now it comes off as hubris. The authors should use more speculative or conditional language to convey the points they are making. Attributing such specific mechanisms of change in phytoplankton using such a diverse set of models is problematic because the models could potentially have different processes that are controlling productivity/biomass in the Southern Ocean. Multi-model ensembles are useful in that they average out biases in individual models, but such specific attribution of mechanisms can really only be done with certainty by looking at the equations of individual models. Otherwise, it is just speculation about what’s going to happen. The story that the authors describe is compelling but it does not necessarily mean that this is what’s happening in every model. For example, the subantarctic region of the SO could become cloudier with climate change (see Fig 1f in Leung et al 2005), leading to an increase in Chl/C ratios of phytoplankton that could lead to increasing surface chlorophyll trend shown in Fig 6. I’m not suggesting that the authors are incorrect with their hypothesis, but they need to be more modest about how they attribute the drivers of change.
• Relating to the first point - the authors are very dismissive about the impacts of changing iron availability for phytoplankton (despite the well documented importance of iron in controlling production in the Southern Ocean; e.g., see section 3.5 and refs therein of Petrou et al., 2016). They also do not address the potentially big impact of increasing temperature. As phytoplankton growth rates, zooplankton grazing rates, and phytoplankton/zooplankton loss rates are highly sensitive to temperature in most models, I think this deserves some discussion and perhaps additional analysis. How do temperature and iron conditions change in the Southern Ocean upper mixed layer in this MME? How do these changes project onto the hypothesis that the authors present?
• Their argument appears to be somewhat circular – The authors say that a shallower MLD leads to more concentrated phytoplankton at the surface (this is not shown) and that leads to more grazing efficiency which reduces the phytoplankton concentration (which would, in turn, reduce the grazing efficiency). So, I suggest they add more plots to show that phytoplankton biomass really is more concentrated nearer to the surface. The integrated plots that are shown in Figure 5 for example should be broken down by depth to support the hypothesis they are making. They show surface chlorophyll trends in Figure 6, but with most models having variable Chl/C ratios, this is not definitely showing what they claim. The authors repeatedly say that phytoplankton concentrations in a shallower MLD increase so this needs to be demonstrated.

Minor comments/edits:

Line 22: Rather than “poorly simulated”, perhaps say “simplistic”

Line 32/33: This sentence is awkward in that the words “climate change” are used twice. Reword to something like this: “ These factors are all projected to change with climate change so phytoplankton will likely be impacted from changing bottom up processes”

Line 40: light conditions in high latitude regions may also improve due to decreasing sea ice cover

Line 52: perhaps remove the word “current” since Tagliabue et al (2016) is about CMIP5 models

Figure 2 caption and throughout the Figures/captions: rather than “relative variation” could you say “relative change” or “normalized changes”… Variation implies you’re looking at the variability and I find it confusing.

Figure 3 caption. Boxes denoted by dashed lines mark the focus area (reword that sentence of caption)

Figure 3: are these maps means of Figures 1 and 2? If so, could you explicitly state that in the caption?

Line 97/99: I don’t think you should call out figures before you have introduced them in the Results section.

Line 150-160: this is where the logic sounds very circular – you need to show that phytoplankton concentrations actually increases in the mixed layer, or reword.

Line 158/159: Figure 7 is not very convincing towards this point. Much of the negative relationship results from one model (CanESM).. or am I missing something?

Line 187: end this sentence after Le Quéré reference. Then start a new sentence with “It is thought to be mainly caused by….”

Figure 8. I think you should be careful about using TTE in this context, as TTE depends on community composition of the plankton. For example if much of the zooplankton are microzooplankton, the energy stays more in the microbial loop, whereas if they are mesozooplankton they can be consumed by higher trophic levels. See, for example, Krumhardt et al., 2022

Line 188 to 190: this is exactly why you can’t definitively attribute mechanisms in the models.

Line 192-195: Have you verified that this is what is happening in each model? Otherwise please be more speculative in this statement..

Line 198: add ‘s’ to ‘exist’

Line 205: rather than “mixed layer, average light” say “mixed layer with higher average light intensity”

Line 215: say “Our results suggest, therefore, that there will be an increase in surface chlorophyll…”

Line 218: you have not shown an increase phytoplankton concentration, so be careful how you word this statement.

Line 226: add “productivity” after “phytoplankton”

Figure 10: could you make the colors more distinguishable? The dark purple and black are so close in tone so it took me awhile to see the difference in color between the two dashed lines on panel b.

Line 231: replace “all” with “some”

Line 236: actually models with iron representation show a much larger spread than those without iron, which is something that should be mentioned.

Lines 244 to 247: this sentence is confusing and long. Please reword. Also, mention the potential influence of different types of predator prey relationships, Holling type II and Holling type III, both of which are used in ESMs.

Line 255: actually, the COPEPOD dataset has pretty good coverage globally, except for the subantarctic Southern Ocean (see Moriarty and O’Brian 2013). Perhaps mention this.

Line 310/311: I don’t think this is true. Many studies have aimed to understand more about the zooplankton component of ESMs. See for example, Heneghan et al (2016 and 2020) & Negrete-Garcia et al (2022).

References cited:

Heneghan, Ryan F., Jason D. Everett, Julia L. Blanchard, and Anthony J. Richardson. "Zooplankton are not fish: improving zooplankton realism in size-spectrum models mediates energy transfer in food webs." Frontiers in Marine Science 3 (2016): 201.

Heneghan, Ryan F., Jason D. Everett, Patrick Sykes, Sonia D. Batten, Martin Edwards, Kunio Takahashi, Iain M. Suthers, Julia L. Blanchard, and Anthony J. Richardson. "A functional size-spectrum model of the global marine ecosystem that resolves zooplankton composition." Ecological Modelling 435 (2020): 109265.

Krumhardt, Kristen M., Matthew C. Long, Zephyr T. Sylvester, and Colleen M. Petrik. "Climate drivers of Southern Ocean phytoplankton community composition and potential impacts on higher trophic levels." Frontiers in Marine Science 9 (2022): 916140.

Moriarty, R., and T. D. O'brien. "Distribution of mesozooplankton biomass in the global ocean." Earth System Science Data 5, no. 1 (2013): 45-55.

Leung, S., A. Cabré, and I. Marinov. "A latitudinally banded phytoplankton response to 21st century climate change in the Southern Ocean across the CMIP5 model suite." Biogeosciences 12, no. 19 (2015): 5715-5734.

Negrete-García, Gabriela, Jessica Y. Luo, Matthew C. Long, Keith Lindsay, Michael Levy, and Andrew D. Barton. "Plankton energy flows using a global size-structured and trait-based model." Progress in Oceanography 209 (2022): 102898.

Petrou, Katherina, Sven A. Kranz, Scarlett Trimborn, Christel S. Hassler, Sonia Blanco Ameijeiras, Olivia Sackett, Peter J. Ralph, and Andrew T. Davidson. "Southern Ocean phytoplankton physiology in a changing climate." Journal of Plant Physiology 203 (2016): 135-150.

Xue et al., “Southern Ocean phytoplankton under climate change: shifting balance of bottom-up and top-down control”

This manuscript is a nice exploration of how the plankton ecosystem in the Southern Ocean will change under a high-emissions climate change scenario. Xue et al., evaluate a set of CMIP6 models for phytoplankton, zooplankton, and mixed layer characteristics, arguing that the shift from bottom-up to top-down control under climate change results in roughly unchanged phytoplankton biomass in the Southern Ocean. Additionally, they find an emergent constraint between models’ representation of the seasonal sensitivity of surface chlorophyll with the shoaling of the mixed layer to a long-term sensitivity of chlorophyll and mixed layer depth. With this emergent constraint they are able to reduce the uncertainty in model projections of chlorophyll change under climate change.

This is overall a nice, well-written manuscript. I found the emergent constraint portion of the manuscript to be the most interesting, however, it seemed at times disconnected from the rest of the manuscript (even though the shoaling of the ML leading to phytoplankton blooms is a key bottom-up mechanism driving phytoplankton biomass) – as if it were somehow tacked on to the manuscript at the end of the writing process rather than fully integrated from the beginning. This is evident from the fact that no mention of the emergent constraint is in the abstract or introduction, even though it makes for quite a key result.

While the EC result is quite interesting, I also found it to be insufficiently explored both in its own sake and also within the context of “shifting balance of bottom-up and top-down control.” A few points for the authors to consider for their revision:

• It’s nice that we are able to now use this new model analysis framework of the emergent constraint to reduce uncertainty in future projections, but what does this analysis REALLY tell you about bottom-up vs. top-down control in the Southern Ocean, in terms of drivers and mechanisms? In the conclusions, you state “we further employ the approach of the emergent constraint to increase our confidence in the increasing trend of phytoplankton concentration … which is the underlying mechanism that contributes to the intensified top-down processes under climate change.” (lines 297-298) but first, phytoplankton concentration (biomass) does not really increase under climate change, and second, chlorophyll as a proxy appears to be a mix of biomass and productivity. All that the EC analysis appears to really be used for is to reduce uncertainty in future projections of chlorophyll (not phytoplankton biomass). The reader is left wondering what the actual connection really is between the EC and the mechanisms of top-down vs. bottom-up control.
• I understand that the methodology of the EC utilizes a linear relationship between the models within the multi-model ensemble to constrain future projects. However, is there an extent to which the models (in the historical period) are sufficiently far away from the observations that they can be excluded? There are 2-3 models with a negative relationship between shoaling of the ML and chlorophyll concentration (S_seas > 0 or S_clim > 0) – what is causing this different relationship in those models? Should they be excluded, or the results interrogated further in some way?
• Along these veins, I noticed that many of the models clustered around the S_seas=0 line (e, i, f, n, h) all have skillful representations of mesozooplankton (Petrik et al. 2022) – and likely have put work into their modelled zooplankton such that they are not “treated stemotherly as a mere closure term.” The one exception is model (c – CanESM CanOE) which is far away from the S_seas = 0 line but not particularly skillful in its representation of mesozooplankton. Have the authors thought about why this might be and what may be driving this clustering of these particular models (CMCC, UKESM, CNRM, IPSL, GFDL)?
• Regarding the observational constraint – it was quite striking to me that the uncertainty around the observed chlorophyll values were so much lower than observed MLD values (Fig 9). When constructing your observed S_seas values (with uncertainties) are you comparing like to like in the MLD and surface chlorophyll fields? E.g., would it be a better comparison if you were to resample the Globcolour chlorophyll field for the 1-degree grids where Argo MLD data are available?

A few minor comments:

• I believe CMCC-ESM2 phytoplankton and zooplankton biomass fields are provided on the CMIP6 ESGF archive. I did a quick search today (Jan 17) and found phydiat, phymisc, zmeso, and zmicro on the archive with monthly outputs. (I did not check for ACCESS-ESM1-5).
• Figure 8a – there is no green shading to indicate the variability in phytoplankton biomass, only orange shading for the zooplankton. If you are intending for the reader to compare the orange shading in Fig. 8a with Fig. 5a then please indicate so. (Also, make your y-axis labels consistent between those two plots)
• It really was not clear to me what Fig. 7 was supposed to show. The text where Fig. 7 is referenced was not particularly informative – can you please expand on it (particularly for readers not familiar with Xue et al. 2022a), and if it’s not essential to the main text, then perhaps remove it or place it in the supplemental?
• Again, there’s no mention of the emergent constraint in the abstract or introduction. It would be great to introduce the concept of emergent constraint earlier than in the methods.
• Also, the first time that chlorophyll is mentioned as a proxy for phytoplankton biomass is in section 2.4 (methods). I think that if there is space, it should be mentioned in the introduction – but also with the caveat that given variations in chl:c ratios due to photoacclimation and phytoplankton type, it is quite an imperfect proxy for phytoplankton biomass. (Though I personally think that chlorophyll is instead a proxy for a combination of phytoplankton biomass and productivity.)

I hope that these comments are helpful and not burdensome to address. This is indeed a nicely written paper and interesting study.