Dear authors,

I invite you to submit a revised version of your manuscript based on your response to the reviewers' comments, taking into account all the points raised. Both reviewers have been rather critical, thus please be meticulous.

Specifically, I encourage you to consider showing (maybe in a supplement) bacteria abundance data and any other supporting material for the claim that the initial filtered seawater did not contain bacteria but the added bacterial community (from the phytoplankton cultures) was then taken over by a natural one (through air-sea exchange and/or other contamination) by day four. Given the sheer volume of the mesocosm enclosures of 4 cubic meters, the amount of bacteria added by the phytoplankton culture inoculation and the relatively short time frame of four days, there appear to be some lose ends. Also, from an experimental point of view, to tease out potential treatment differences would require the 'contamination' to be equal in all mesocosms (see also my comment on variability at the end).

Furthermore, could you please explain the continuous rise in pCO2 until day 4-6 which implies considerable amounts of DIC added to the system on the order of 100 umol/kg (or removal of alkalinity by some means). Additionally, as the enclosures were aerated at pCO2 target levels of 400 and 1000 uatm, this substantial alkalinity removal or DIC addition is unlikely to be biologically mediated (given the relatively low initial biomass). So, what could be an explanation for your observation? On that note, carbonate chemistry measurements and calculations should be explained in more detail.

Finally, a discussion on how big potential treatment changes would have had to be in order to pick them up, considering the variability among replicates, could be helpful.

Yours, sincerely
Kai Schulz

Dear authors,

your response to the initial round of reviews and your revised manuscript has now been evaluated by two referees. Although one of the reviewers was satisfied with your revisions, I tend to agree with the other (see further down below for details) that there are still major unresolved issues, especially concerning experimental design, and that the revisions which have been made are rather cosmetic. Nevertheless and most importantly both reviewers score your manuscript in terms of scientific significance and quality, and presentation only between fair and poor.

I was particularly disappointed that none of the comments and suggestions in my initial decision was picked up by the authors. As I wrote there are many loose ends, for instance concerning the significant production of DIC during the first days of the experiment (although the water is being aerated at target pCO2!) at very low phytoplankton standing stocks (and that would assume that the phytoplankton community is for some reasons net heterotrophic). One explanation could be extremely high bacterial biomass in the inoculum, but to judge the authors have to show bacterial abundance data. But then, how can randomly introduced bacteria from the outside of the mesocosms out-compete this initial high density community (which should also be highly adapted to the phytoplankton community they have been inoculated with) in just four days? As is stands, this just does not add up.

I will give you the opportunity to submit a revised version of your manuscript. However, it will have to fully resolve all the issues mentioned, and I do mean fully and all.

Sincerely,
Kai Schulz


REVIEWER COMMENTS
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Lin et al. have verbosely responded to my and my coreviewer’s concerns and have rephrased several paragraphs of the paper. However, the ecological question that they set out to study remains unanswered. My main critique: the experimental setup is not sufficient to answer the question how a (distinct) bacterial community responds to elevated CO2. How can the authors differ between continuous foundexsr effects and possible CO2 effects in the study?


The authors mention that “natural bacterioplankton were undoubtedly introduced into the mesocosm system through sampling and air-sea exchange” resulting in the bacterial community composition (BCC). Sampling procedures should in general NOT introduce additional bacterial numbers or taxa into any microbial study! Especially not continuously during the study. This way new bacteria are introduced to the setup and may refresh the initial community, so the authors cannot test how a BCC responds to elevated CO2 over time.
The inoculum issue: I understand that air/sea exchange and aeration will add bacteria to the system. It would be interesting to know how many and which bacteria are added to 4000l-mesocosm bags this way and how that amount of bacteria can outcompete the (I guess high numbers of) phytoplankton associated community within 4 days. Those bacteria have to be very competitive and fast growing to outcompete bacteria already adapted to the model phytoplankton species. What is the natural BCC of the surface water in the Bay during winter, does it resemble the resulting BCC in the mesocosms?

Chapter 3.3. now mentions differences between phytoplankton culture BCC and d4 mesocosms. The authors also mention “The important point is that each mesocosm has the same BCC, as in previous mesocosm studies.” However, they cannot provide evidence for this, and the first BCC data differ between mesocosm bags (Fig2, D4.1, D4.6 and D4.7) therefore I could not be convinced that the early BCC was indeed the same among all mesocosms. Additionally, mesocosm bag 8 was later contaminated with dinoflagellates, resulting in changes in BCC (p.17, l.12). If air/sea exchange and airing can randomly contaminate the phytoplankton community, how can the authors conclude that BCC was ‘evenly contaminated’ by the surrounding waters and that the bacteria were not continuously refreshed?

Additionally, I was disappointed to see that the authors were not willing to re-consider the organization of their data. The bacteria counts which would be most helpful to understand the bacterial dynamics remain inaccessible and were only mentioned as an average for the initial day 2 and 4 in the method section of the paper (the authors refer in their comments to another study currently in review, and did not find it appropriate to redraw the data). Therefore, it is hard for me to follow the argumentation of the entire manuscript.
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Dear authors,

thank you for resubmitting your manuscript. What is still missing is an estimate on the ratio of bacteria being continuously introduced to actual standing stocks in the mesocosms. This is critical as only a low ratio would allow to detect potential CO2 effects.

To do this you could us maximum growth rates reported in the literature for the most abundant groups and then estimate how many you would have needed to introduce after one day of aeration on day 1 to reach the numbers you have measured on day 2.

And such type of analysis would need to be thoroughly discussed in your manuscript.

Sincerely,
Kai Schulz

Dear authors,

thank you for your reply. I am, however, not convinced by your calculations. Given the unproportional influence of a growth rate estimate on the number of bacteria that would have been introduced on day one, a more conservative approach should have been taken.

For instance, simply assuming growth rates to be half of those maximum ones you have chosen to use, I calculate a daily bacteria influx from outside the mesocosms of about 825.000 cells/ml (in comparison to about 100!). Although this should still not pose a problem to your experimental setup, the growth rate of 0.75 h-1 taken from Adave et al. (2008) for Pseudomonas aeruginosa appears to be the maximum growth rate at a pH of 7 at 35 degrees Celsius, which is far from the conditions during your incubations.

Furthermore, it appears that growth rates for marine bacteria are typically rather on the order of per day than per hour (compare for instance Kirchman 2016). This in turn would mean that the contamination of the system with bacteria from the outside would have been substantial, potentially compromising your data and its interpretation.

As it stands, I have unfortunately no choice but to reject your manuscript, unless you can provide convincing evidence or reference for such high growth rates in your bacterial community (e.g.bacterial production rate measurements).

Sincerely,
Kai Schulz

D. Kirchman, Growth rates of microbes in the Oceans, Annual Review of Marine Science, 8:4.1-4.25 (2016).

Dear authors,

thank you for your reply. I am satisfied with your revision but may I encourage you to build your line of evidence in a slightly different manner. Instead of choosing a more or less arbitrary growth rate, I would suggest to calculate the minimum growth rate necessary for introducing, for instance, less than 1 permil of the standing stock. Then you could argue that this growth rate is reasonable in comparison to observed rates in oligotrophic communities, especially in the absence of significant grazing pressure.

Finally, could you please thoroughly check the manuscript for grammar.

Sincerely,
Kai Schulz

Dear authors,

thank you for resubmitting your revisions, addressing the remaining concerns raised by the reviewers.

Sincerely,
Kai Schulz