Rev#1

Thank you for the thoughtful and constructive comments by the reviewer.

This manuscript by Hanna Campen and coauthors considers the production/loss of carbon monoxide in Arctic seawater under different pH and environmental conditions. Overall, the manuscript was well-presented with strong text and clear figures. The Introduction section was very well-researched and referenced, and the authors thoroughly informed the reader about published relevant work.

However, there were a few things about the manuscript that were not clear to me. These are listed below

1, At one site, the background CO was 50 +/- 9 pmol/L. During the dark incubations, CO concentrations decreased from 50 pmol/L to approx 10 pmol/L. These CO values are incredibly low and must have been scraping detection limit. From memory, a working detection limit is approx 0.1 nmol/L so the authors somehow must have improved upon this.

Reply: The detection limit of our measurements of dissolved CO was <0.01 nM (<10 pM) and thus it is comparable to other studies using a similar method (see e.g., Xie et al., Mar. Chem, 77, 98-108, 2002).

2, I didnt see any mention of a blank which could have consisted of deionised water (or MilliQ or sterile freshwater). This would have informed the authors about any production of CO from the bottle. I realize the authors tried to avoid the use of plastic which leaches CO but at low picomolar concentrations even trace contamination could have influenced the field data. For your info, even Niskin bottles made of PVC produce CO which is why previous researchers measuring dissolved CO made Niskin bottles made out of titanium (I think it was Craig Taylor and Oliver Zafirou that did this work).

Reply: Blanks have been measured beforehand in the laboratory. We did not find any significant CO production by the glass bottles used in the incubations. Unfortunately, no titanium sampling bottles were available for our study. The very low initial CO concentrations, however, speak against a significant CO contamination by the Niskin bottles. Please note, that the waters in the Fram Strait have low water temperatures and therefore any CO production/diffusion from the Niskin bottles is expected to be low.

3, It is hard to interpret the data relating to CO production because the light experiments were conducted for 48 h period and therefore cover both light and dark periods. Its not clear to me why the CO production experiments did not run for a 12 h light period.

Reply: The incubations were run north of 76°N during the Arctic summer when there was no dark period (i.e. there was light even during ‘night time’). Therefore, the light incubations were run for 48 h.

4, Can you make box and whisker plots (Figure 3) with triplicate values?

Reply: We tried box and whisker plots. We think however, that the given plot is better suited to illustrate our points. In order to provide additional statistical information, we will add ‘The vertical extent of the bars in a) depicts the spread of triplicate samples and the red line within each bar indicates the average.’ to the figure caption.

5, Did the authors know or test whether the pH values they established for their experiments influence cDOM bioavailability? This is something that could have been done prior to the expedition. If changing the pH does not cause any impact on cDOM bioavailability, then why would any change in production/consumption occur?

Reply: No, we did not test the effect of pH on CDOM prior to the cruise. This sort of experiment would have been strongly biased by the fact that we could not use in-situ produced CDOM from the Fram Strait. In other words, the CDOM used in prior lab experiments would have been different from the CDOM encountered during the cruise.

Indeed, Gao and Zepp (1998) showed that a photochemical breakdown of CDOM is increased at low pH (5.5) thus affects CDOM bioavailability. Moreover, ocean acidification may alter CO production/consumption indirectly via its influence on bacterial and phytoplankton processes which, in turn are also affecting the CDOM pool and its bioavailability. (Gao and Zepp, Environ. Sci. Technol, 32, 2940–2946, 1998.)

6, Do the authors think an acclimation period should have been included for the pH experiments? If the impact of pH on cDOM chemistry and/or microbiology was not immediate, then changes throughout the following 24-48 hrs would be interpretated as biological signal.

Reply: Thank you for pointing to this interesting aspect. An acclimation period, however, might significantly change the setting in the incubation bottles before adjusting the pH. Over the course of the light incubation we did not observe a general trend of the CO concentrations with time, see lines 146-149. Therefore, an acclimation time during the incubations appears to be unlikely.

1. The small paragraph beginning on Line 205 which compares carbon monoxide with carbonyl sulfide is too speculative and should be removed.

Reply: We agree that this idea is very speculative. However, we would like to keep the small paragraph as it seems to be justified by the results presented in Pos et al. (1998). We suggest rephrasing of the last sentence in order to emphasize that it is speculative: ‘Even though based on indirect evidence, we suggest that the trend of decreasing CO photoproduction (GPco) with increasing NO3- concentrations (see above) might be caused by the mechanism suggested by Pos et al. (1998).’

Summary

I support scientific publications where the results do not show significant results, such as this manuscript where two pH manipulations did not impact CO production or oxidation, however, the questions raised above must be fully addressed. I also think the authors should consider whether the Results+Discussion section presents any novel data or perspectives, as its current format seems to be just a comparison with‪ previous work published by Huixiang Xie.

Reply: We present the very first study of the potential effects of OA on CO cycling. As such, we argue that our results are novel. Given that Huixiang Xie and colleagues have published several studies of CO in Arctic waters, it appeared meaningful to us comparing our new results with theirs. Moreover, we would like to point out that our incubation experiments not only evaluated the role of pH, but also that of temperature and cDOM under the environmental conditions found in Arctic waters. We anticipate the CO production/consumption rates resulting from our experiments to be of wide interest for modelling studies evaluating future changes due to e.g. warming and changes in light availability in high-latitude marine ecosystems.

Rev#2

Thank you for the thoughtful and constructive comments by the reviewer.

Manuscript entitled “Carbon monoxide (CO) cycling in the Fram Strait, Arctic Ocean” studied the cycling of CO in the surface waters of the Fram Strait. The authors measured CO production and consumption rates in various incubation experiments at four sites in summer. They conclude that ocean acidification does not affect CO gross production (GP_CO) and consumption (Æ™_CO) rates. And the combination of high CDOM and low NO₃^- concentration favored high rates of CO production and CO consumption. Therefore, the authors identified both CDOM and NO₃^- as key drivers of CO cycling. This manuscript facilitates a better incorporation of both terms into biogeochemical models, and would improve both CO emission estimates for the Arctic realm, and the assessment of how atmospheric CO emissions will affect the radiative budget and oxidative capacity of the Arctic atmosphere. The Reviewer supports this manuscript for publication in Biogeosciences if the authors could carefully address the following comments.

Specific comments:

1. Page 3 Lines 88-91: The author is requested to clarify the abbreviation meaning of pH in the manuscript. If it represents ocean acidity, why adjust the values to -0.14 and -0.3? And, can the acidity be negative? If the pH represents the concentration of CO₂, how is the pH regulated? Please explain it in detail.

Reply: Thank you for pointing to this issue (of course, a pH is not negative). We will rephrase the sentence. It now reads ‘[…], the pH in pH1 and pH2 was adjusted by lowering the pH by 0.14 and 0.3, respectively, […].’.

The pH does represent the concentration (or the activity) of dissolved protons (H+) and is indirectly linked to dissolved pCO2 via the equilibrium reactions of the carbonate system. In lines 91-94 we explain how the pH was adjusted.

1. Page 3 Line 92: The authors are advised to supplement the total alkalinity (TA) and dissolved inorganic (DIC) concentrations ranges at the four sites collected for this manuscript.

Reply: We will list the TA and DIC data (together with the pH data) in a new Table S2 in the supplementary material.

1. Page 4 Lines 99-100: “All incubators were continuously flushed with ambient seawater to keep bottles at ambient temperature”. Does the ambient seawater flush incubators wash the outside of the tank or circulate inside seawater?

Reply: The incubation bottles were placed inside the incubator devices which were filled with seawater which was pumped through the incubator. We will replace the sentence with ‘The incubation bottles were placed inside the incubators which were filled with ambient seawater which was pumped through the incubator to keep bottles at ambient seawater temperatures.’.

1. Page 5 Lines 136-137: The authors mentioned the seasonal variation of CO in the Arctic surface water, but the four sampling stations were all completed in summer, so please explain it in detail.

Reply: Yes, our data are only from one season. Our statement of the ‘seasonal variability’ thus refers to the comparison with other studies which were conducted during other seasons. The other studies are cited in the following sentences.

1. Page 5 Lines 160-162: What is the range of ocean acidity in terms of lower pH? In addition, how to conclude that the pH has no effect on neither ƙ_CO nor GP_CO significantly during the incubations?

Reply: The term ‘lower pH’ refers to the adjusted (= lowered) pH in the pH1 and pH2 incubations. We will list the pH data (and DIC and TA) in new Table S2 in the supplementary material.

There were no statistically significant differences between the results from pH1/pH2 and the control (ambient incubation). This is also shown in Figure S3.3 of the supplementary material.

1. Figure 2: The points in Figure 2 are too scattered, can they represent good correlations?

Reply: The correlation is significant (see statistical data given in the figure caption).

1. The author mentioned in the manuscript that CO consumption is due to microorganisms and phytoplankton. Would the author consider using some testing methods to analyze the consumption of these microorganisms and phytoplankton to confirm the experimental results?

Reply: Thank you for pointing to this issue. The suggested experiments would be indeed very helpful to confirm the conclusion of our study. However, they were not part of the study presented here.

1. What is the purpose to measure the CO concentration development during dark and light incubations in Section 3.1? The results and discussion section should correspond to the research objectives presented in the introduction section.

Reply: In lines 56-57 of the Introduction we stated ‘[…] the major objectives of our study were (i) to identify the main drivers of CO production and consumption in the Fram Strait and […]’. In order to address this objective, we performed the light and dark incubations as light is one of the main drivers of CO production (via photochemical and biological production). Therefore, we think that the Results and Discussion section corresponds to the objectives raised in the Introduction.

Rev#3 = Rev#2

See our replies to Rev#2.

Rev#4

Thank you for the thoughtful and constructive comments by the reviewer.

The following is a review of the manuscript "Carbon monoxide (CO) cycling in the Fram Strait, Arctic Ocean " (Manuscript bg-2022-201) submitted to Biogeosciences by Hanna Campen and coauthors.  The manuscript reports results from extensive incubation experiments in the Fram Strait, Arctic Ocean.  A great deal of data was obtained and the authors attempt to use it to “better understand the changes of CO in the ocean.” I support this manuscript for publication in Biogeosciences if the authors could carefully address the following comments.

Specific issues:

• Part 15 “Both production and consumption of CO will likely increase in the future,” This is your result? I did not find this conclusion in the text.

Reply: This sentence refers to line 220-225 of the Conclusion section, where we state ‘This has the implication that predicted changes in terrestrial-derived and marine CDOM (e.g. Lannuzel et al., 2020), as well as dissolved NO3- inputs (Tuerena et al., 2022) could affect future CO production and consumption in the region. Both trends might lead to higher CO gross production as well as higher CO consumption.’.

• Part 20 Please delete “see” “e.g.”

Reply: We will delete ‘see e.g.’ in line 24.

• Part 65 Please delete “see”

Reply: We will delete ‘see’ in line 68.

• Part 145 “thermal CO production” Maybe you can provide the site temperature.

Reply: The initial water temperatures are given in Table S1. We do not see a need to state the water temperature in context of the sentence in line 45 (because it is not relevant to explain the result).

• Part 150 I am very skeptical about this result “Since there was no obvious relationship between the timing of the sampling, CO concentrations and preceeding light intensities (Fig. 3), this indicates that photochemical CO production did not exceed CO consumption.” Unless I am mistaken, you observed that CO concentration increased in incubations in natural sunlight in Fig. 3

Reply: There seem to be a misunderstanding. In lines 147-149 we state ‘CO concentrations in the light incubations showed no uniform trend with time. Only during the incubations NT6A and D5 a significant increase of CO concentrations over 48 h was observed.’ So, there was no general trend of CO concentrations with time. The timing of our sampling indeed showed no correlation with light. In other words, we expected to see enhanced CO concentrations when light intensities were high (and vice versa) because of the photochemical production of CO. This was obviously not the case.

• Part 155 “The kCO computed from our experiments (Table 1) are comparable to previously published findings from Arctic waters.” Higher or lower? And what is the main reason? Please describe in detail how, where, when to collect samples. Some readers are concerned of the final results and discussion.

Reply: As stated, kCO are listed in Table 1 and range from -0.038 to -0.006 hr-1. They are neither higher nor lower as the kCO reported in the literature (see line 156).

It is unclear what is meant by ‘Please describe in detail how, where, when to collect samples. Some readers are concerned of the final results and discussion.’ The sampling of our study is described in detail in the Methods section. We state the oceanic regions where kCO have been determined by the colleagues (see lines 157-158). For the details of sampling the readers are referred to the cited references.

Please delete “(Please note that kCO are given as positive values in Xie et al. (2005)).”

Reply: We are citing kCO from the literature as negative values. However, they are given as positive values in the references although they describe negative slopes as well. To this end, we think that the statement should not be deleted.

Please delete “(see Introduction)”, and add a reference.

Reply: Line 180: We will replace ‘(see introduction’) with ‘(see e.g., Ossola et al., 2022)’.

• Part 200 “The fact that we still measured oxidation rates in waters with very low CO concentrations might indicate that the dominant community is rather heterotrophic, which in turn could help explaining the poor correlation with Chl a.” Maybe you can provide the bacterioplankton data?

Reply: We are sorry, but bacterioplankton data are not available.

• Part 205 please delete “see above”

Reply: We will delete ‘see above’.

This last paragraph does not look like a conclusion, maybe you need to simplify this paragraph.

Reply: We are sorry, but we disagree. We think that the Conclusion is simple enough and should not be simplified any further.

• Part 210 please delete “(representing future scenarios of ocean acidification)”

“lower pH” replaced by “ocean acidification”

Reply: We modified the sentence. It reads now ‘We conclude that that ocean acidification may not affect CO gross production (GPCO) and consumption (kCO) rates.’

This sentence looks like illogical “ We observed a tight coupling of CO production and consumption. Hence, the produced CO is not necessarily emitted to the atmosphere as the dissolved CO seems to be rapidly consumed before its atmospheric release.”

Reply: In order to clarify our statement, we modified it. It reads now ‘We observed a tight coupling of CO production and consumption. Thus, CO produced in surface waters could be rapidly consumed before being emitted to the atmosphere. In consequence, CO production at these depths does not necessarily result in outgassing towards the atmosphere.’

• Part 220 (e.g. Lannuzel et al., 2020) (Tuerena et al., 2022) (Cherkasheva et al., 2014)

(10) The conclusion should not contain too many references.

Reply: We think that citing three references in the Conclusion section is not a case of ‘overciting’. Moreover, the cited references are all necessary to justify our conclusions.

Please delete (as observed in our study)

Reply: We will delete ‘(as observed in our study)’.