Data quality: The data from Jakolof Bay in April are clearly bad. The values of these data are well beyond what is typically seen in nearshore settings in Alaska and other areas along the NE Pacific coast. The authors could have instilled a lot more confidence in these data by showing how the discrete measurements compare. This could be done by simply plotting the discrete pCO2 values with the pCO2 time series in Figure 4. The fact that the fluxes estimated for this region exceeded 200 mmol m^-2 ^d-1 (Figure 5), yet the fluxes from the discrete samples from April 23 were ~4 mmol m^-2 d^-1 is a big hint the pCO2 is wildly different between the two measures. The authors seemed to miss this when they say on Line 275 that “mooring values fell below the range measured discretely at the farm”. The figures show the opposite. Clearly both the inside and outside moorings were fouled at this site (indicated by the photo in the appendix) and, given how important the results are from this site for the conclusions of the paper, I feel the authors need to either make a much stronger argument for the validity of the data or remove the bad data from the analysis and re-evaluate their conclusions.

Given the consensus between the two reviewers, we have decided to remove all mention of Jakolof Bay and only include the other two sites in the manuscript.

Computing fluxes: On Line 390 the authors state how important wind speed is in dominating sea-air exchange rates (and clearly this is not the case given the above statement about Jakolof Bay – the very high deltapCO2 there – and the resulting extreme fluxes) yet there are no wind data presented in the paper. The authors claim to have used NDBC buoy data but I’m not sure there are buoys in each of these areas. Was it one buoy that was used? Multiple? Can the NDBC buoys be indicated on the maps in Figure 1? If the authors are using the MacIntyre relationship, then they should be clearer about that maybe refer to the fluxes as “synthetic fluxes” and qualify that these estimates are meant to give a sense of the exchange rates and are not actual estimates of the flux (which would include local winds).

We have added to the methods the IDs for the buoys used and the distance from the farms. We have also added wording to the methods describing that we cannot use local winds and therefore it gives a sense of the exchange rate instead on lines 105-109.

Calculation of “net” flux: I don’t think differencing the instantaneous flux (hourly) from inside and outside the farm site and calling that a “net flux” makes sense. The flux is kind of a net parameter to begin with since it uses the sea-air gradient in the computation. A clearer way to do this computation might be to integrate the flux from inside and outside the farm site, and then difference the integrated values to report a flux difference between the inside and outside of the farm. I assume the start of the “transition time” would be when you would start the integration, but this part wasn’t clear in the manuscript.

Whether we integrate before or after differencing the inside and outside, we get the same final number. But we maintain that the net calculation prior to integration is still useful because it allows for a visualization of short-term differences between the inside and outside moorings that cannot be seen when seasonally-integrating the timeseries. However, we had previously used the entire timeseries and when we shortened the integration window to start at the transition time, Windy Bay turned from a source of CO₂ to a sink. We have gone over these values again and noticed a conversion issue with days and hours which overestimated previous calculations. This has been resolved along with the resulting carbon credit estimations.

Integrated signals: As a community providing mooring CO2 system measurements from settings like this, I think we need to be very careful to recognize that pH or pCO2 measurement we are making and reporting on integrate signals reflecting all the processes encompassed in the decomposition they present. Authors attempt to do this but nowhere did I see mention of the local phytoplankton community potentially contributing to the deltaDIC change and the resulting pCO2 values driving the fluxes. This study cannot discount the role of phytoplankton within and around kelp beds, so I suggest the authors re-examine how they are presenting the “role of kelp”. Kelp are part of the autotrophic community growing during spring and driving changes in the CO2 system.

We recognize our lack of acknowledging phytoplankton in its role in affecting carbonate chemistry. We have gone through and ensured that when we are discussing the biological effect on carbonate chemistry, we use the general term biological processes and not specifically kelp. Further, we emphasize this with line 462 in the discussion.

Some minor comments:

Intro – consider some statements of the potential negatives and unknown consequences of using kelp for mCDR. Should reference the National Academies report.

A sentence for the potential consequences of mCDR has been added to the introduction on lines 47-50 and referenced the National Academies report.

Lines 39-41: Poor wording, please rephrase. Disequilibrium refers to the sea-air pCO2 gradient which can be positive (source) or negative (sink).

We have removed this sentence because the paragraph works well without it and to reduce the discussion around the wind data that created issues in other comments.

Lines 49-57: The authors are referring to the northern Gulf of Alaska but then mention the state economy. Here they are referring to the State of Alaska so perhaps should be clearer and refer to Alaskan state of federal waters in the Gulf of Alaska.

We have now mentioned that once in the paragraph indicated, but we will keep the reference to the NGA as the acronym for simplicity.

Methods – could add caveat that 3m measurements may mis-represent the flux in highly stratified settings. If you believe these settings aren’t highly stratified then make that point clearer in the results.

We have added the caveat to the methods on lines 105-108. During the spatial survey conducted in spring, we also collected three discrete samples in a vertical column at 3m, 2m, 1m, and the surface to determine if it was well-mixed and the pCO₂ values did not differ between those samples. However, now that we are not using Jakolof Bay in the manuscript, we didn’t see fit to include it to aid in supporting our argument.

Line 118: what do you mean SAMI-CO2 was translated up or down relative to the water samples? Show the data with in pCO2 time series figure.

While we are able to perform calibrations for the pH sensors, the SAMI-CO2 sensors are highly proprietary so there is no way to correct the values before they are available as a pCO₂ timeseries. We could not do a thorough calibration like we were able to do for the pH sensors, we translated the SAMI-CO₂ sensors relative to water samples. However, after receiving this comment, we have reviewed published manuscripts that used this instrument and found no mention of doing any calibrations to the data directly given from the instrument so we have decided to undo the translation mentioned. See below for the raw data and the discrete bottle samples overlain. This has caused changes to the results in the manuscript.

Line 154: there is mention of lag time calculations but I don’t see how this was used.

The lag time calculations were used at the end of the first paragraph in the results when we indicated what the cross-correlations were for salinity and temperature between the inside and outside moorings to demonstrate the lag in time between the two locations and possible water mass movement.

Flux units: I believe you are reporting hourly data but the flux units appear to be mmol m^-2 d^-1. If you want to keep hourly data, suggest reporting mmol m^-2 hr^-1, otherwise average to daily for d^-1.

We have converted the data to hourly. We hadn’t averaged the data to make it daily but had taken the hourly data and multiplied by 24 to put it into units comparable to other studies. But we agree with the suggestion made to keep it as hourly. 

Decomposition calculations Line 180, here H is meant to be the depth of the mixed layer and not the sampling depth. This equation is meant to show the change in TCO2 over the mixed layer due to sea-air CO2 exchange. Suggest author’s add a caveat that they are exchanging sampled depth for mixed layer depth which may drive larger deltaDIC in areas/times of weak stratification and high flux. Is there a reason the decomposition was done on monthly averages instead of daily (comment above) or hourly data? With monthly, t2-t1 should be month2-month1 and not days and units should match.

We used sampled depth for H because Garcia-Troche et al. had done it that way and we adapted our equations from them. As we are assuming a well-mixed water column with no stratification, we have changed H to reflect the entire water column, as now described on line 193. As per the comments regarding hourly vs daily vs monthly data, we calculated the decomposition for hourly data.

Results – consider starting out with a statement about the time span, volume of data recovered, number of discrete sample events, etc. Why is the inside mooring record shorter than the outside mooring record?

The inside mooring timeseries ended when the kelp was harvested but the outside mooring continued over the summer for AOP to get a sense of what the system might look like past the harvest time. However, we understand the confusion here and have removed the timeseries for the outside mooring past harvest.

Figure 2 – consider plotting density and maybe spice time series instead of T/S diagrams. It is hard to see any differences with those plots. I do not that Kalsin Bay outside mooring does see a lot more fresh water than inside mooring.

The reason we used the T/S diagrams is that we are trying to compare what masses between the inside and outside moorings.

Side comment here – the outside farm site moorings should be referred to as reference sites and not control sites. These time series aren’t a control of anything but provide some baseline, or reference, to judge the inside farm site time series against. Throughout – remove “control” and replace with “reference” when discussing outside farm moorings.

All mention of “control” has been changed to “reference.”

There are grammatical errors in a number of places throughout the manuscript.

We have done a thorough readthrough of the manuscript and believe to have found the grammatical errors referred to here.

Major points:

Introduction--While many of the salient considerations are introduced here (mCDR, OA, carbon burial rates), the introduction could be streamlined to more clearly state the goals of this project. As currently written, I wasn’t certain whether they were arguing that kelp farming would be a major contributor to mCDR (as implied in the 2^nd paragraph) or ameliorate OA conditions more locally (as paragraph 1 seemed to imply). Some of these details would probably be better suited for the discussion, as they are a bit confusing here (e.g., they mention low natural OC burial rates in coastal sediments, but make no mention of sinking kelp to the deep ocean until much later).

We hesitate to remove all mention of either mCDR or OA from the introduction because both are discussed later in the manuscript and we want to make sure that they are introduced at the beginning. We have removed the sentence describing burial rates, however, to leave that for the discussion.

[[By the way, the comment about seaweed needing to absorb 4 Gt CO2/yr is incorrect—the statement in the paper cited is that that 4 Gt CO2/yr needs to be removed from the atmosphere to achieve net zero by 2050, with seaweed being one major potential contributor if it can be scaled up to Gt scale.]]  

This sentence has been removed for accuracy but also for clarity as the sentence before it already emphasizes the point we wanted to make, that kelp farming would need to upscale dramatically.

1) I wholly agree with Dr. Evans’ comments generally, and specifically about data quality being bad at Jakolof Bay. I concur that a much stronger justification would be needed to keep that site in the published results, otherwise remove that time-series.

We have removed that timeseries from the manuscript.

2) I also agree that given the importance of wind data in many places throughout the manuscript, as well as the seemingly contradictory comments regarding the role of wind (cf. line 375 and line 390-391), it’s confusing that wind data aren’t shown. There are some good discussion points about peak wind season not coinciding with kelp growing season in the discussion. It would be helpful to see the NDBC buoys on the maps and some plots of wind speed. It’s all just alluded to in the text now.

As per reviewer 1, we have now added the ID and distance between the buoys and the farms to the methods on lines 150-151. We have not added it to the figure 1 because it is too close to the farm on the Gulf of Alaska overlay and not in the view on the smaller maps. We have plotted the wind data for you to see here. There is not much information to gain from it so we could move it to the appendix if you believe it is useful.

3) Confusing mix of units in the decomposition calculations (monthly vs daily or hourly values)—needs clarification.

We are changing all the data to hourly to avoid confusion.

TA in decomposition analysis: Normally the influence of photosynthesis and respiration on TA are considered negligible compared to their effects on DIC (e.g. https://www.researchgate.net/figure/Effect-of-various-processes-on-DIC-and-TA-arrows-Solid-and-dashed-lines-indicate_fig2_360026150). In high productivity settings like this, I would expect you might see an effect of production (and respiration) on TA, but I think you may still not need to include TA as part of your decomposition, as the DIC effect is much larger, and they are not independent (unless, maybe, you are making an argument for CO2 vs bicarbonate uptake, in which case this needs to be explained/justified, especially why they would be independent). If you exclude TA, does it change the magnitude of your residuals (down in lines 296-299)?

This is an incredibly valid point. We included TA initially because kelps can draw up bicarbonate, or there may be shifts in TA from nitrate uptake or ammonium release if there is high enough productivity. But when we reran the decomposition without TA, the residuals increased. Please see the figures below, first showing the residuals for Windy Bay inside the farm including TA and then second not including TA. Since we observed the residuals increasing without the inclusion of TA, we have decided to keep TA as part of the decomposition but we included the hourly decomposition in figure 7 instead of monthly as suggested by the reviewer.

Residuals from Windy Bay farm including TA in decomposition:

Residuals from Windy Bay farm NOT including TA in decomposition:

Contradictory(?) quantitative statements:

1) There are a lot of different results presented for each site, and it’s not always 100% clear how they relate to each other across sections. For instance, line 19 says KB is a sink, WB a source (excluding JB as sink due to bad data), but then in L250-251, it says JB is a source and KB and WB are sinks. I get that both things can be true, if, e.g., you are considering different timescales, but a table may help organize and present the information in a way that is easier for readers to follow.

I think the confusion lies in that we are talking about two different things in both locations. In the abstract when we say that KB is a sink and WB a source etc, we are referring to the net integrated flux as in the farm is acting as a sink or a source based on the carbonate chemistry measured at the farm relative to outside of the farm. Later in the manuscript results, when KB and WB are both sinks, that is referring to the air-sea flux at the farm site in spring demonstrating that as photosynthesis increases in spring, the nearshore acts as a sink of carbon. One is a net value comparing inside and outside the farm and the other is the actual air-sea fluxes at the farm.

2) On a similar note, there are contradicting statements about net source/sink status for Alaska’s coastal waters: cf. line 61 and line 37. It may require some reorganization of the topics discussed throughout to clarify how they do or don’t actually (dis)agree with each other. As written now, they are both just stated and not critically compared.

In line 37, we introduced the idea that the nearshore is usually a source of CO₂ because it is heterotrophic and in line 61 we say that the coastal system is generally net heterotrophic which would insinuate that it is a source to the atmosphere. When we mention that the offshore ocean acts as a carbon sink, it is in reference to the continental shelf. Perhaps this is an issue of the definition of “coastal” as we intend the term to not include the continental shelf. We have changed the wording on line 62 to reflect this.

Circulation: Having been the lead carbon assessment scientist on an early seaweed uptake experiment in Washington state (to look at local OA amelioration), I have an understanding of what a critical role circulation plays in the results for these sorts of studies. A few questions:

1) The authors state in L 189-190 “Comparison of water mass movement at the inside and outside moorings confirmed that both sensor arrays detected similar water masses, allowing for a calculation of net air-sea CO2 flux when paired with the inside sensor array.” but they did NOT measure water movement or really describe how they made these inferences. How was this conclusion reached?

We did not deploy current meters at the sites during this study so we did not quantify circulation directly. The statement that is pointed out from line 189-190 was made based on the similarity of the T-S diagrams at the inside and outside moorings (Fig. 2) and the observed coherence of major tidal signals across sites (Fig. 8). This suggests that both moorings were sampling the same regional water mass and the cross correlations demonstrated that the lag time is within an hour or two.

2) Did they correct for the changing direction of advection of water masses into/out of the kelp farms as the tides changed? They simply give 0-1 hour lag times that are a) unclear how they arrived at them and b) unclear whether these may be reversed with the tides.

The lag times were calculated using a cross correlation mentioned in the methods on lines 168-169. We did not explicitly correct for the changing direction of tidal advection, and we acknowledge that ebb and flood tides may alter the direction of water exchange. The short lag times (≤1 h) and the strong tidal forcing in these bays suggest that inside and outside moorings experienced largely coherent tidal signals, but finer-scale reversals could occur that we were unable to resolve with our current sensor configuration. To address this, we have clarified the lag-time methodology in the Methods section and added a note in the Discussion on lines 470-472 acknowledging that tidal reversals may introduce additional uncertainty.

3) Dr. Evans asked about whether the 3 m depth of the kelp and sensors is relevant to air-sea gas exchanged. I have the same question. It’s hard to tell to what extent O2 and pCO2 covary temporally across the figures, as the timescales of the plots are different. If they covary strongly, that may suggest that gas exchange is not having a large effect, as O2 should be exchanged much more rapidly than CO2. The authors state in lines 345-346 that WB and KB had well-mixed water columns, but with sensors at a single depth, I’m not sure how they inferred the well-mixed status of the water columns.

I am hesitant to use CO2 and O2 comparisons to infer gas exchange. While there should theoretically be a 1:1 conversion between the two for respiration, many of the photosynthesizers in Alaska (kelps and phytoplankton) can also utilize bicarbonate which would decouple that signal. While we cannot prove using data we collected that the water column is fully mixed, these are shallow, tidally energetic systems that have been shown in the past to be well-mixed, especially due to the elevated tidal height in the region (Archer 2013, Haag et al. 2023). Additionally, the consistency between the inside and outside moorings at a site suggest that the bulk water mass was well mixed so without a strong freshwater input, we believe that the water column would be homogenous. We have added this caveat to the methods on lines 106-108 to caution our results.

Minor points:

-In Fig 1, would help to make the land a different shade than water so the reader doesn’t have to spend time figuring out which is which, especially in the site-specific panels.

I have shaded the land darker as per the suggestion.

--Methods: Unclear what company makes the DIC analyzer used with just a model #

We have added Apollo SciTech next to the model #.

--L 116-117: implies T measured on discrete bottle samples, correct?

We measured temperature in the lab when using it to calculate the pH and DIC from the spectrophotometer readings and doing the conversion for DIC from μmol/L to μmol/kg.

--Fig 2 caption: not sure what the parenthetical statement at the end is meant to say…typo?

It is meant to denote that we are plotting the density anomaly and not the density.

--Fig 4: the log scale used for Jakolof Bay pCO2 data is unusual—would not suggest using it because it obscures the values.  If they keep the log scale, they definitely need to specify the base; when converted to linear scale, the pCO2 values range from ~630,000 to 100,000,000 (log10(pCO2) of 5.8 to 8), which is clearly bogus. I’m assuming they meant log(e)*, which would translate to more like 300-3000. Plausible, but I’d still question the upper end of this for AK waters. The comment about the “astronomical rise” in FCO2 at JB definitely sounds like a strong sign of flawed data quality onset. (* FWIW, I was taught 10 is the default base for log, and ln is for base e, so this may vary across readers.)

We have removed Jakolof Bay data from the manuscript.

--Line 221: do you really mean “uncertainties” or variability? If uncertainties, those numbers do not instill confidence in the results. As variability numbers, these seem more reasonable.

They were conservative uncertainties that include any error associated with differences between sensor readings and calibration bottles, uncertainty in the laboratory seawater analyses, etc.

--Fig 5 colors don’t match legend? Or I think you just can’t see the green? Put the green on top? And put legend with the panels it goes with?

The legend colors is only for the lefthand panel which has green in it but the overlap is so great that it can be difficult to see. We have remade the figure to reduce confusion.

--L 264: Do the net FCO2 values correlate to the biomass grown at the sites?

Net FCO2 values only reflect the subtraction of inside versus outside mooring air-sea flux data, no inclusion of biomass. 

--Lines 269-277: Really need to see the discrete samples overlaid on the mooring data! Also I would disagree that there’s homogeneity of FCO2 anywhere but Windy Bay, and the statement at the end of this section implies it’s at all sites (or maybe just not clearly worded to indicate it’s only about WB?).

We have changed the spatial survey figure to show a histogram to better see the clustering of the discrete samples relative to the mooring data. We do imply that there is homogeneity for both Windy Bay and Kalsin Bay because the air-sea flux values at the inside mooring tended to be similar relative to the outside mooring. We chose not to display the discrete samples over the mooring data because there is already so much data on this plot and the new histogram can clearly compare the two.

--Fig 6: several different font sizes, panels are not the same width

The edits have been made to Fig. 6.

--Fig 8: the inside and outside mooring plots appear to be identical for KB…mistake or real?

I have rerun the analysis and there might have been a mistake because they do look slightly different but the inside and outside plots still look really similar so that won’t have an effect on the results.

L309-311: I mean, sure, there’s MORE kelp around the inside mooring at JB than the outside mooring, but the outside mooring has higher pCO2, yes? So that could suggest more respiration there, in contradiction to this statement? Also, on the plots with both inside and outside mooring data, it’s often very hard to confirm the authors’ interpretation in the text because the data overlap so much. Maybe the authors could put a delta plot panel in the O2 and CO2 figures (figs 3-5, also fig 9) so that readers can see the patterns the authors describe more clearly? It could be a single plot at the bottom with both sites’ (WB, KB) delta(inside-outside) values shown in it.

We have removed Jakolof Bay from the manuscript, but yes, there might have been some confusion around the language associated with the pCO₂ at the moorings.

--Citing figures 8 and 9 on lines 375-376--seems like the figure #s are wrong.

They were the wrong figure #s when there used to be an additional figure that was removed. I have changed the figure #s and checked throughout the manuscript for additional figure # issues.

--Section 4.3, first paragraph: Would the loss of the fixed nutrients from coastal/nearshore areas be a detriment to these ecosystems if kelp was grown “at scale” in this region and subsequently sunk to the seafloor?

Yes, that is a good point. I have added a sentence to lines 442 to 444 to that effect.

L412 and later on: normally expressed as “at saturation” (vs. under or supersaturated) rather than in equilibrium (which can refer to a less fixed value, such as atmospheric, vs. the “saturation” value, which takes changes in T and S into account intrinsically)

We have changed the wording from at equilibrium to at saturation with respect to aragonite saturation.

L415: may be better to word as “may decrease exposure to conditions favoring dissolution”

Wording changed.

L416-417: Important point!!!

L419: Unless you are discussing specific species, technically dissolution shouldn’t be a major issue when aragsat is > 1 as it is everywhere/every time when not under significant biofouling conditions.

Following this comment, we have decided not to stray too far into discussing the effects of aragonite saturation state other than suggesting that under future OA conditions when the aragonite saturation dips to lower values, kelp farms may or may not actually increase the value. See lines 425-434 for changes.

Fig A1: The Evans et al. 2015 relationship does not seem appropriate for these sites, in that the line is substantially below all but two of the measurements from this study; thus, using salinity as a proxy will underestimate TA systematically, assuming their discrete samples were representative. You could look at the effect that the magnitude of difference you saw between measured and estimated values would have on your results (Fassbender et al 2017 did something similar: https://link.springer.com/article/10.1007/s12237-016-0168-z).

As suggested, we computed a sensitivity analysis similar to Fassbender et al. 2017. We used the Evans et al. 2015 salinity-temperature relationship to predict the TA for the discrete spatial survey samples that we had measured in the lab for TA already. The residuals for that can be seen in the table below. Then, we estimated pCO₂ using the predicted TA and measured TA with the package seacarb in R to quantify the sensitivity to that variable (see table). We can conclude from this that the Evans equation works well in Windy Bay for predicting TA in that the sensitivity in pCO₂ is low, but the same is not the case for Kalsin Bay. This is perhaps not surprising given Fig. A1.

Therefore, we created a new linear relationship using the discrete spatial survey samples for Kalsin Bay only. While we would have wished for a larger training set, we used 6 of the 9 samples to create the equation and the last three to perform the same exercise as above to confirm its accuracy.

In Kalsin Bay, CO₂ sensors were calibrated using discrete TA bottle samples, so the site-specific TA relationship was not required for estimating the CO₂ timeseries or the later air-sea flux estimate. In contrast, for Windy Bay, where only pH sensors were deployed, the Evans et al. (2015) relationship was necessary to estimate TA from salinity in order to estimate pCO₂, and it appears from the sensitivity analysis above that the Evans relationship is a good proxy. We do, however, need to use the Kalsin Bay-specific relationship for the decomposition analysis. We have explained this new method in lines 139-144 and in a new Appendix section.  

Fig A3: Not sure why the inside/outside values were divided rather than subtracted for FCO2 values (was not explained on p. 11 either).

This figure is meant to represent the ratio between the inside and outside moorings to highlight the multiplicative changes in air-sea CO₂ exchange at the kelp farm. We wanted to demonstrate that the difference between the inside and outside farm increases during spring, especially as the system enters net autotrophy. We do see the value in subtracting the values, which is why that is how we calculated the net FCO2. We have added to the results on line 273 the reasoning for this to increase clarity.