Singh et al examine the photophysiological response of phytoplankton communities during autumn in the Southern Ocean via iron addition incubations. No significant differences were observed in Fv/Fm and σ PSII and the authors conclude that there was not iron-limitation at these times and locations. I commend the authors for presenting what some would consider “negative results.” The data are clearly presented and methods are described in detail. Please see my minor comments below.

1. Abstract (Lines 24-26) and Line 399 - The authors state that this study confirms that the phytoplankton communities “were not iron limited and…ambient iron concentrations were sufficient.” I suggest that the authors rephrase these sentences to reduce their high confidence in their assessment that there was no iron limitation although I agree with the authors that these results suggest that Fe was not the sole limiting nutrient. An alternative explanation is that there is Fe-Mn colimitation. Ratios of dMn to dFe relatively close to the study region suggest that Mn limitation or Fe-Mn limitation is possible (Browning et al. Nature Communications 2021 Supplementary Fig 5). As Mn is critical for PSII, the photophysiology results presented here could be influenced by Mn-Fe colimitation. The authors very briefly hint at this at the end of the conclusion (line 430). Also, much of the dFe is < 1 nM (lines 279-287), and only a fraction of dFe is bioavailable, which should also be mentioned in the results/discussion. It may also be useful to report the range in dFe:NO3 (nmol:umol) which appear to be quite high so it is also surprising that Fe did not have an effect. Again, I largely agree with the authors’ conclusions; however, I believe some altered wording and added discussion of potential Fe-Mn colimitation is warranted.
2. Line 424 – The authors state that they observed “high Fv/Fm” although I would consider many values to be relatively low (< 0.3). I suggest changing this sentence.
3. The recent paper in Science by the corresponding author here (Ryan-Keogh et al 2023) seems relevant to include in the Discussion. Specifically, its stated that irradiance normalized NPQ is higher in Spring/Summer compared to Fall/Winter which aligns with the results in these studies.

The study by Singh et al. measure the photophysiological responses of phytoplankton communities following iron addition by looking at Fv/Fm and σ PSII variables. The study was conducted from late summer to mid-autumn in the Antarctic Sea-Ice Zone along the 6°E. Overall, no significant differences were observed between control and treatment (+Fe) and the authors concluded that dFe concentrations were not limiting for phytoplankton growth and thereby does not explain the decline of the bloom. Like reviewer 2, I agree that what could be considered negative outcomes are important, but I don't think there are enough measures or data here. I would recommend that this data set be merged with other data from the same expedition. While these data are worthy of publication, these days it is almost anecdotal to measure Fv/Fm and incubate with Fe addition during an oceanographic cruise and this type of data is usually presented as part of a broad set of metrics or analyses (omics, absorption experiment, cell abundance, etc etc). Moreover, only one depth was sampled at each o few locations (5 in total). I honestly wonder if there is enough data for a full publication.

Still, I suggest minor revisions because the data are well presented, the manuscript is well written and pleasant to read as it is. I prefer to leave the final decision on whether to publish in Biogeosciences to the editor.

More specific comments here below:

Abstract

“To better understand the constraints on productivity”. « constraints » sounds a bit vague.

Iron addition – please specify in the abstract the nature of the addition. Inorganic Fe … 2nM…

Introduction

In general, I think the introduction would gain strength by citing more recent work. While I agree that one should acknowledge the work of the pioneers, one also expects to read a state of the art on the subject.

Line 38-40: more recent findings may be cited too

Line 42: same remark as above – the introduction should be a state of art

Line 66: What about grazing ?

Line 77: Work by Lannuzel ?

I like the way differences between short and long term experiment provide different kind of information. It is rarely explained.

Line 101: please specify what differences in physiology (Fv/Fm?) for this statement

Materials and Methods

Line 115: what and where are the ancillary data? Please specify.

Figure 1 – from 28^th Feb to 10 April “initials conditions” between stations cannot be compared. It would be helpful to see the track of the vessel to visually assess what stations was sampled late summer/early autumn versus mid-autumn (April).

Adding the sea-ice extend limit would also benefit the map.

« Underway measurements are shown with surface CTD data for (b-g) along with the initial incubation values » unclear

Table 1: Legend – “mean initial parameters for the photophysiology” mean of how many replicates? Please specify. “associated ancillary data” which are?

« Materials and methods » : remove Uppercase at Materials or harmonize

“±” precedes standard deviation : how many replicates ?

Cumulative photon dose : not clear – what depth ? what integration? within the MLD? Within 24h?

Sea Surface Temperature : I would suggest to write Sea Surface Temperature (SST) in legend and SST only in the Table. Or harmonize the spelling (uppercase)

Community Structure – if only dominant species are cited please specify. Structure or phytoplankton composition ?

Materials and Methods

Line 143: in situ in italic

Line 147: 20-30 m depth is not surface anymore.

Line 155: “bottles were filled unscreened” why not ? it should be at such depth to reproduce light attenuation.

Line 158: “spiked with 2.0 nM iron (III) chloride (FeCl3 TraceCERT®; Sigma Aldrich) prepared in 2‰ HCl (30% suprapur HCl; Merck)” – can the authors discuss the amount of Fe they think remained in solution (as dFe and therefore expected to be available to phytoplankton) after mixing with seawater?

Line 171: I am surprised there was only 43% of PAR with no screen.

Line 172: remove “experiment was terminated”

Line 178: what the authors consider relevant versus ancillary data?

2.4 misleading title as FRRf is not the acronym for Phytoplankton photosynthetic photophysiology. Remove FRRf and include Fast Repetition Rate Fluorometry in the text below.

2.5 rename title as “Chlorophyll a (Chl a)”

Line 204: “250 μL of chloroform » percentage ? at saturation ?

Line 204 : « the samples were kept cold » cold is a subjective word. In the fridge at 4°C ?

Results

Line 260: If the authors are not citing their own results in Chla concentration, I suppose they cite average value for the MLD from Kauko et al. 2021? Please specify.

Line 267: I found excessive by the authors to say they “characterize two regions” with only one to two station in each of them but more importantly only one sample depth.

Line 270: I don’t see differences in Fv/Fm between the two regions considering SD.

Line 280: same remark for silicate concentrations…they are similar.

Line 290: not the same location, therefore it is not a time-series. Using the word “drop” is therefore confusing.

Line 311: I don’t find Fv/Fm of 0.2 “particularly low”. Lower than the others only.

Line 320: Change cholorophyll for Chl-a

Figure 3: I would recommend to add on the top right of each panel the location of the stations to ease the reading. I would also add the ratio Fe/control to effectively compare the experiments together.

Table 2: ratio between Fe/control would be helpful here as well. I recommend to add the consumption (delta between initial conditions and end of incubation) in macronutrients for each experiment.

Discussion

First paragraph (line 354-368): I would suggest to delete it as it sounds like a repetition of the introduction.

Line 372: I am surprised by this statement. A large body of works on Fe uptake experiments in the Southern Ocean are conducted within 24h (ex. work by Strzepek and/or Fourquez). If the authors wish to keep this sentence please cite references to support this statement.

Line 379: I suggest the authors add more references here. Photophysiology is not a new topic, and has been extensively studied in phytoplankton of the southern ocean.

Line 382-384: The temperature in incubation in these studies was similar or warmer? This could be part of a discussion rather than a statement.

Line 386: this is the start of a discussion to me

Line 393-395: a bit vague. What percentage of each group?

Line 403-405: The authors state Fe is not the limiting factor but discuss the importance of upwelling of iron-rich deep water together with a list of other unrelated factors in curtailing the bloom? Please rephrase or delete this paragraph as it does not add anything to the discussion.

Line 405: Can the authors add something about they could have assessed the grazing pressure? Did they not see increase in Chla during the experiments?

Line 410: add references on Fe remineralization by bacteria here (e.g. Boyd, Bressac, Tagliablue).

Line 410: “Relatively high bacterial abundance”. Relative to? Please justify. It seems very average to me (see Fourquez et al. 2015 or Christaki et al. 2021 for comparison at different stages of bloom development).