General comments

Marine phytoplankton pigments determined via HPLC analysis have been extensively used to develop and validate remote sensing algorithms for determining the specific abundance of phytoplankton groups, becoming a reference metric. The study under review aims to compare phytoplankton pigments with measurements of DNA-based metabarcoding and mRNA abundances via metatranscriptomics. This study seeks to determine to what extent existing datasets of DNA metabarcoding and marine mRNA can be used to develop models of phytoplankton group distributions, supporting the next generation of hyperspectral satellites.

The manuscript appears well-structured and written. The abstract and title reflect the content accurately, and the references are appropriate. This is interesting work by comparing the significant number of samples. Even though such comparisons has been done previously, this cover different geographical locations and explored quantitative methods that express both 18S rDNA and total mRNA as concentrations. This work merits to be published after a series of minor weaknesses that are reported here will have to be addressed. These involve the following:

• The scientific methods and assumptions are clearly outlined regarding DNA, mRNA techniques, primary productivity, and flow cytometry. However, there is a notable lack of detailed description of the HPLC pigment analysis methods, and the relevance of flow cytometry in the context of the presented work is not well explained.
• The results are sufficient to support the interpretations and conclusions, and the description of experiments and calculations is sufficiently complete and precise. However, the discussion and conclusion sections lack a connection to the potential satellite applications of the results presented.

Specific comments

Introduction:

The Introduction is well-structured, and the database is adequately described and appropriate in terms of its representativeness for the study presented.

Materials and Methods:

In the Methods section, substantial attention is devoted to describing the DNA metabarcoding and mRNA methods and analyzing their results. The cytometry method is adequately described. However, the HPLC method is not described at all: the analytical procedure applied, the pigments measured, and the sample pre-treatment method are not mentioned. Additionally, there is no discussion of the uncertainty associated with the pigment measurements. It is unclear how the composition of pigments, such as chlorophyll a, is calculated. Furthermore, diagnostic pigments are only briefly mentioned in line 315. The abbreviation for the pigments are not clarified (i.e., Total Chlorophyll a) and uniformly used and need to be revised through all the text.

The description of the HPLC method references the Phytoclass (line 165), but its relevance to the article is no further discussed except using for the fig. 4 and fig. S4. On the other hand, at line 329 the text, there’s a reference to CHEMTAX (but no link with the phytoclass). There is also no rationale provided for limiting the analysis to diagnostic pigments alone.

Another point to clarify is when cytometry data is used: an explanation of the added value of this information should be included (e.g., why cytometry is important for the Prochlorococcus; lines 305 and 408 but not elsewhere).

The seasonal variation is presented but not further discussed in the follow session

Results and Discussion:

Finally, both the abstract and introduction mention the potential use of this study to support the development and validation of remote sensing products. However, additional explanation on how could be realized should be added. Specifically, potential models of pigment concentrations for remote sensing of harmful algal blooms or phytoplankton community structure are not adequately explored.

Conclusion:

This conclusion is comprehensive, presenting the study's findings effectively and connecting them to broader ecological and methodological implications. However, the text could be improved for clarity, conciseness, and better flow (i.e., moving between themes like biases, PDRs, HABs, and remote sensing lack sometimes of clear transitions)Some ideas, such as the limitations of 18S rRNA gene copy number variability and the importance of quantitative approaches, are repeated multiple times, making the text unnecessarily long. jumping between themes like biases, PDRs, HABs, and remote sensing without clear transitions

Technical corrections

Line 115-120: capture/capturing used 3 times in few sentences: consider to use synonym

Line 160. The HPLC acronym was already introduced in line 57

Line 315 the Fuco, Perid, etc… acronyms were introduced already at line 285

Line 321 “correlation”, consider to specify Pearson correlation

Line 364 “example, reduced light availability may lead to cellular increases in accessory pigments” please specify if this included accessory pigments used in the present study.

fig 4. Total Chl a in A and D is different from and Chl a of E-J ?

General comments:

This is a valuable and timely contribution for the PACE era. The use of quantitative omics is very much a step in the right direction, in my opinion, and the strong and improved correlations observed between quantitative omics and pigment data are reassuring.

Overall, I found the writing and presentation to be of a high standard and the collection of data over multiple years and seasons is a commendable feat.

The authors have done a good job considering environmental gradients and seasonal change, but it feels like an opportunity was missed by not doing a more granular analysis of surface vs. deep communities if the data are in hand.

I found the ecological application ‘case studies’ to be a mixed bag. On the one hand, Section 3.2.1 that considers ecological assessments shows a lot of promise of combining omics and pigment data to improve understanding of ecological processes. On the other hand, I’m not persuaded by the suggestion of Section 3.2.2 that quantitative omics, as presented in this manuscript, can improve the monitoring and forecasting of harmful algal blooms. But, I hope the authors can change my mind about this. Finally, Section 3.2.3 suggests that quantitative omics may lead to better biogeochemical and metabolic rate estimates. I think this section could be improved by considering further the substantial caveats and current limitations to this potential application.

Finally, the Methods section is missing important details in places, which are described in the Specific comments below.

Specific comments:

Fig. 1 Figure caption; L129-130: Consider adding “regions” after (18S-V9 (blue)”

Methods:

L137-140: I understand what the authors are trying to say, but this is an awkwardly worded sentence. Perhaps along the lines of “These data represent only a subset of the on-going NOAA-CalCOFI Ocean Genomics (NCOG) time series and are restricted to samples where quantitative approaches for DNA and RNA were employed concurrently with phytoplankton pigments samples (no DNA samples from 2017 and only RNA samples from 2017-2020; James et al., 2022).”

LN150-158: The primary productivity section is sparse and could benefit from additional details.

How were the sampling depths determined? Was there a bio-optics CTD cast to determine the light extinction coefficient prior to sampling for ¹⁴-C incubations, and the sampling depths were then chosen to match the degree of attenuation of the neutral-density screens used for the deckboard incubation?

What was the specific activity, concentration of radioactivity added to the sample bottles, and supplier of the NaH¹⁴CO₃ used?

I believe ‘HA’ is a Millipore-specific designation for filter type. I suggest mentioning the material of the filter (i.e., mixed cellulose esters (MCE) membrane) for those reader who are not familiar with them.

Was the incubation time a constant between seasons? Multiplying by 1.8 to obtain 24 h productivity implies that the incubation time was ~ 13.3 h, but you state also that incubations were performed between local noon and civil twilight, which presumably varies seasonally.

How closely did the collection depths of productivity and DNA samples match? “Closest” is vague.

L160-165: Analytical details of the HPLC pigment analyses are entirely missing – you skip directly from sample collection to Phytoclass taxonomic analyses. I suggest adding a citation to the analytical method at the very least.

L255: Flow cytometery. It appears that the only flow cytometry data that is presented is for cell abundances for Prochlorococcus and Synechococcus in Fig. S2. As such, you may wish to consider moving this portion of the methods to the supplementary information. I suggest also that you tailor the description of the methods to explain how Prochlorococcus and Synechococcus were differentiated and gated.

L264-266: I’m confused about the use of side- versus forward-scatter. Were forward and size-scatter signatures used to estimate the size of Prochlorococcus and Synechococcus?

Results and Discussion

LN286: As you’re discussing the range here, I suggest reporting the range for Fuco, rather than the maximum concentration, as you don’t specify in the previous sentence what pigments were measured at the lowest concentrations (and the log scale used in Fig. 1E makes this difficult to discern by eye).

L364-372: The authors state that samples were collected from both the near-surface and SCML. It’s reasonable to assume that the two communities may differ systematically in terms of both community composition and photophysiology, as the authors discuss. Were samples from these two depths pooled for all analyses? If so, how did the sample numbers differ between the two depths, potentially skewing the aggregated results?

The authors have done a good job considering environmental gradients and seasonal change, but it seems like a missed opportunity to not extend these analyses to surface vs. deep communities if the data are in hand. Have the authors performed the regressions shown in Fig. 2 on low- vs high-light binned samples? Even if they are do not differ from each other, this is useful information and could be included in the supplementary information.

Section 3.2.1 This was a useful illustrative example of how to combine the strengths of ‘classical’ HPLC data and DNA-based approaches to better understand phytoplankton ecology. I enjoyed reading it.

L500-509: The use of recycled nutrients (a low f-ratio in the case of nitrogen, a low Fe-ratio in the case or iron) should be included as a general strategy.

Section 3.2.2 This section was not nearly as compelling as the previous one. In effect, you argue that if fucoxanthin is detected then there are likely to be some Pseudo-nitzschia present, some of which mayproduce DA. It’s also quite possible for fucoxanthin concentrations to vary independently of Pseudo-nitzschiaabundance. It’s not clear how this improves the current state of knowledge or improves the monitoring and forecasting of harmful algal blooms, even within an intensively sampled region like the CalCOFI survey site.

Section 3.2.3 I appreciated the ambition and hope of this section. One thing to note about L587-591: the modules or subsystems of genes that predict a reaction rate are likely to be different between species. As such, it would seem to me that to make use of this correlation, not only would you need to know about abundance and expressed metabolism, but you would need to have a comparable degree of knowledge of your target species as we have for baker’s yeast – an extensively studied model organism – to know which gene clusters predict rates. Would this not require intensive lab rate measurements to validate this correlation? Also, the baker’s yeast correlation was achieved under steady-state conditions. Trying to accomplish this in a field study? Yikes.

Technical corrections:

Fig. 2, column B: Y-axis number format is sometimes in scientific format, sometimes not. I suggest keeping this consistent amongst panels.

L481: “The observations of unimodal PDRs have led to hypotheses for the mechanisms that underlying them.” Remove ‘that’ before ‘underlying’.

General comments:

This manuscript addresses how to interface phytoplankton observations across many different lenses (e.g., metabarcoding, metatranscriptomics, HPLC, flow cytometry, biogeochemical rate measurements), a goal that has remained elusive due to differences in absolute quantification of organisms and relative abundances stemming from the compositional nature of molecular datasets. The authors circumvent this by using quantitative techniques, such as with the use of internal standards, to move beyond relative abundances with their molecular efforts. This allows them to complement other approaches like flow cytometry and HPLC used to measure pigment concentrations to reveal significant correlations between different eukaryotic and cyanobacteria phytoplankton groups across these different methodologies. By integrating the different approaches, they have further leveraged these relationships to interpret mechanisms setting the ecological patterns (e.g., productivity-diversity relationships, harmful algal bloom composition) in a dynamic upwelling region across both spatial and temporal dimensions.

Furthermore, since HPLC-measured pigments are routinely used to develop and validate remote sensing observation, including emerging high resolution hyperspectral remote sensing reflectance data, the authors highlight the importance of comparing phytoplankton pigments to alternate metrics, e.g., metabarcoding and metatranscriptomics, of phytoplankton community composition (PCC). The positive correlations between HPLC and molecular based PCC observed in this study are helpful in establishing the usefulness of using molecular data to further help validate global phytoplankton community structure being observed by remote sensing algorithms and developing improvements with Earth system models (ESMs).

In general, I find the authors did a nice job structuring the manuscript, building their arguments, and supporting their findings in context of what has been discussed in literature. The overall content and important take home messages are also clearly articulated. However, I think section 3.2.3 could use a bit more explicit discussion guiding how to interpret the results highlighted here and create a stronger link to how ESMs might use these results (or perhaps we should simply focus on the patterns observed as another validation reference for ESMs?).

Importantly, since so many of the relationships and ecological patterns discussed throughout the paper rely on various statistical analyses, I would strongly urge the authors to update the “Statistics” section in the methods and provide some justification for choosing Pearson correlation instead of Spearman correlations for this study (see more specific comments below for general guidelines that might be helpful). Lastly, there were several different sequencing platforms used for the various libraries prepared for metabarcoding and metatranscriptomics work – please address whether there are any biases or concerns comparing across all the different platforms (e.g., did you use unique dual indexing pooling combinations to minimize index hopping with the NovaSeq 6000 platform).

Specific comments:

Figure 1: Panel D – I’m a little confused by the y-axis scale for nitrate concentrations. I think you are trying to highlight the often very low (<0.5 µM) concentrations on the same range as values as high as 20+ µM but the scaling seems a bit unorthodox. The intervals between values don’t signify the same thing so is there a way to clarify that (perhaps in the figure legend)?

Methods

Section 2.4 & 2.5: It doesn’t seem that any mock communities were used in the library prep, is that right? Please address how mock communities could also improve the quantitative assessment of this study (e.g., see conclusions from Lamb et al., 2018 -  https://doi.org/10.1111/mec.14920).

For the use of Parada et al., 2016 primer set, were the 18S sequences discarded and solely the 16S sequences were denoised into ASVs? If yes, perhaps mention this – it seems to tally with your choice of removing all eukaryotic chloroplast and mitochondrial ASVs from the 16S fraction of this data (lines 206 – 207).

Lines 211 – 212: In previous method section (2.3), only the addition of S. pombe is mentioned so please reconcile that before introducing this step of dividing by ratio of an additional internal standard of T. thermophilus.

Section 2.7 Statistics: Please expand upon this section to highlight the different functions and any parameters that were modified from their default setting when using the function to carry out various analyses such as Shannon H’ index, GAMs, Pearson correlations, linear regression on residuals, etc. For instance, “GAMs were fit using the function ‘gam (y~s, method = “REML”)’ from the mgcv package v1.9-1 (Wood, 2017).” Furthermore, the interpretations and discussion rely heavily on Pearson correlations – please add some justification for why this method was chosen over others, i.e., Spearman rank-correlations. For datasets that follow a bivariate normal distribution, Pearson correlations are useful to measure linear relationships (not sure if you have tested for whether your datasets are normally distributed). However, if the datasets are nonnormally distributed or have relevant outliers, you might actually consider using an alternative like Spearman correlation to test for monotonic association. This could provide different interpretations, potentially stronger correlations, than what your current results indicate.

Results and Discussion

Lines 303 – 307: This section discussing the results of the cyanobacteria fraction of the data could be expanded a bit more. For instance, this potential dominance of Prochlorococcus might align with the observed warming influence and advection of oligotrophic offshore waters into the study region as previously observed at the San Pedro Ocean Time-series (SPOT) where this was accompanied by a notable shift from cold-water ecotypes to warm-water ecotypes during 2014-2015 (Yeh and Fuhrman, 2022 - https://doi.org/10.1038/s41467-022-35551-4). Similarly, the 2015-2016 El Niño event also marked an increase in an open ocean ecotype of UCYN-A at SPOT (Fletcher-Hoppe et al., 2023 - https://doi.org/10.1038/s43705-023-00268-y) but it seems its presence and range of coverage was not detected with the cyanobacteria ASVs recovered from the samples collected in this study.

Figure 3: Consider specifying “All Cyanobacteria” on the figure’s panel titles C and D to align with the description in the figure legend. And same thing for Figure S7.

Line 497: “…;however, contrary to predictions” Are there literary references to suggest that diversity and richness should be expected to be low in deep SCML samples – where/why did you have that hypothesis?

Figure 5: Are the samples highlighted in panel F only a subset of the samples from panel E? It is specified that the samples are ordered by the associated fucoxanthin concentrations, but it seems that only samples above a certain dabA expression threshold are included here – maybe clarify this selection criteria.

Technical comments:

Line 48: “Earth systems models” (make it as “system” – singular)

Line 137: Station 81.8 46.9 – are these two separate stations or just a unique nomenclature?

 Line 481: “…for the mechanisms that underlying them.” Awkward phrasing.

Line 535: Adjust to “…shown to produce DA and its production is…” You already introduced the acronym DA to represent domoic acid so you can maintain consistency this way.

Lines 542-544: Consider rephrasing the sentences to streamline the strucutre: “Dinoflagellates, including certain members in the genera Alexandrium, Dinophysis, and Gonyaulax and species Gymnodinium catenatum and Lingulodinium polyedra, may also cause HABs globally and in the region (Anderson et al., 2012, 2021; Trainer et al., 2010; Ternon et al., 2023).”

Lines 545 – 546: “although 39% of V4 and 55% of V9 18S copies…” Wouldn’t referencing Figure S6B better point to these percentages – not sure the reference to Figure S13 here? Also, does blasting those sequences improve the taxonomic resolution to help better assess if there are potentially more HAB species which may currently be unassigned as HABs due to insufficient taxonomic resolution?