Peer review of: A direct coupled electrochemical system for capture and conversion of CO2 from oceanwater (2020)

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
The authors have addressed all my concerns and those of the other reviewers very thoroughly and to 
my satisfaction, and I recommend publication in Nature Communications. Before publication, I ask the 
authors to consider two additional comments: 
 
1. It appears that you are flowing seawater through the BPMED system, but you do not mention 
scaling on the membranes due to divalent cations (Ca++ and Mg++) in the seawater. I would be very 
surprised if you do not see scaling on the membranes. If you do not, it may only be because you have 
operated it for a short time. Please add a discussion of this to the manuscript. The way to avoid this is 
shown in the Eisaman et al. work published in IJGGC – you take a small (1% of the volume you 
actually decarbonize) volume of seawater, filter out the divalent cations, and run this pure brine (NaCl 
(aq)) through the BPMED unit to generate acid and base. You then use this acid and base to dose a 
much larger (100x the volume of the sample used to make the acid and base) of seawater and 
perform the desired pH shifts. This has the advantage of reducing your pumping energy requirements 
because only this small seawater volume needs to be flowed through the pressure drop of the BPMED 
unit. In fact, if the pH shifts were performed directly in the ocean (imagine the BPMED unit on a ship 
or offshore platform with an expandable net excluding marine life temporarily from the region where 
the pH shifts would occur), the only seawater you would need to pump at all would be that 1% used to 
make the acid and base. If indeed your experiments did flow seawater through the BPMED unit, I 
suggest you: (1) explain whether or not you observed scaling from precipitation of divalent cations; 
(2) discuss how in a deployed system, you would instead just process a small volume as discussed 
above; and (3) include in your energy and cost analysis, what the pumping energy and cost would be 
in in-situ ocean case where you only need to pump this smaller volume. 
 
2. In the supplementary information when referring to Eqs. 58 and 59, there appears to be some mix 
up with the numbering. 
 
SIGNED: Matthew Eisaman 
 
 
 
Reviewer #2: 
Remarks to the Author: 
Reviewer Comments for Manuscript Number: NCOMMS-20-20054-T: “Electrochemical Extraction and 
Conversion of CO2 from Seawater” 
 
I appreciate the article revisions made by Digdaya et al. in their article combining CO2 capture and 
conversion from seawater. They have extended the impact of the work from my perspective, and 
made the conclusions broader than a purely experimental demonstration from the initial submission. I 
feel that after further modifications of their new content into broader conclusions for the prospects of 
CO2 capture and conversion from seawater, this work could be published in Nature Communications. 
 
The primary aspect missing for me, especially given the additional TEA work, is a strong conclusion on 
whether or not the authors feel this line of study is an energy or cost viable alternative to DAC. The 
data which has been presented indicates to this reviewer that even in the best of scenarios, a BPMED 
seawater extraction will likely not be energetically or cost favourable to the DAC process. The phrasing 
of the article, however, would seem to give the opposite opinion. This is particularly true in the first 
paragraph of the intro. While I understand the need to motivate the reason for performing the work, I 
feel the main conclusions in the TEA analysis are somewhat at odds with these initial motivations. 
 
My additional comments for the manuscript based upon the revisions and comments by the other 
reviewers are below: 
1. The authors address the energy penalties of the system in the new Supplementary Note 7. Here 
they find that the estimated energy cost of a co-located BPMED CO2 capture system is 1.29 kWh kg^-
1 CO2, of which 1.22 kWh kg^-1 CO2 comes from the BPMED itself assuming a current density of 200 
mA/cm^2. This is then lower than the range of 1.53-2.45 kWh kg^-1 CO2 for direct air capture. I 
have some questions and comments related to this: 
 
a) Looking at the manuscript and SI, I’m confused about the author’s assertion that the cell voltage in 
the case of 200 mA/cm^2 would be only 1.316 V, leading to an energy cost of 1.22 kWh kg-1 CO2 (SI 
page 22). In their experiments, for example, the cell voltage was shown to be 1.9 V at only 10 
mA/cm^2. The authors note they use the calculated values in Figure S15, but this is only the BPM 
voltage, rather than the cell voltage. The latter of which is much higher due to necessary ohmic drops 
in the electrolyte. 
 
Can the authors show examples in literature where the voltage is as low as described, or give rational 
why the assumed cell voltage can be so low? I would be curious how this would impact the TEA 
numbers as well. 
 
b) From the authors’ revision, it appears that without co-location of a CO2 extraction process with a 
desalination plant, the BPMED extraction process is likely not viable from a cost or energy perspective 
vs. DAC. In this case it would then be nice at the end of the article to discuss some limitations of the 
approach as a CO2 utilization technology. One option, for example, is to reference the maximum CO2 
reduction potential of a desalination co-located approach. 
 
e.g. Given a current global desalination capacity of 120x10^6 m3/day (43.8x10^9 m3/year), and an 
assumed ten-fold increase in the coming years, then 0.0043x10^9 tons CO2/year (0.012% of annual 
global emissions) could be removed from indirect ocean capture co-located with desalination plants. 
 
2. I feel the title could be less-generalized. I would rather have the specific technologies which were 
used be specified in the title. As phrased, the title seems at first more like a review, than a new 
research article. 
 
3. I noticed that the authors gave a cost and energy comparison of all three technology options in 
their rebuttal to reviewer 1. Can this be added to the SI as well? 
 
 
 
Reviewer #3: 
Remarks to the Author: 
I still do not believe that this article is of sufficient merit to be published in a high impact factor paper 
such as Nature Comms. The process described is from my perspective, still beyond the bounds of 
something that would realistically ever be deployed. 
 
Based on my original comments, the authors have confirmed that the costs of this process in a stand 
alone arrangement are simply not viable. They now indicate that the process can work if it is co-
located with a desalination plant. This allows them to ignore the SWIPP costs, substantially reducing 
the capex and opex. However, even then there are issues: 
a) A desalination plant run entirely on renewable energy needs to be found and be willing to provide 
the land footprint for this installation. 
 
b) This desalination plant needs to be willing to take the seawater downstream of the CO2 extraction 
process, as the SWIPP costs need to be re-couped through the production of fresh water. However, 
this stream is now at pH of ~10.7. Can the materials of construction in a desalination plant withstand 
such a high pH, given the concurrent high salt concentration? I would be particularly concerned about 
the materials in the pump that increases the pressure to 50Bar. 
 
c) There could actually be some advantages in running the desalination RO process at such a high pH, 
as this will limit boron transfer to the fresh water stream. However, the fresh water permeate will now 
be at an even higher pH (hydroxide ions will cross the membranes in preference to any other anion). 
This means that the fresh water, for human consumption, needs to be pH adjusted. This eliminates 
the driving force for the overall process. That is, the water is not being returned to the ocean at a high 
pH to accept more CO2. The pH adjustment could be made using CO2, but this would require further 
capex and opex costs, either to generate a pure CO2 stream or to process this water through a very 
large packed or bubble column to transfer this CO2 from air (i.e. direct air capture). 
 
d)I do not think it will be feasible to return the remaining brine (retentate from the RO membranes) to 
the ocean with elevated pH, as the localised impact on biota will be too extreme. Desalination plants 
are already required to put in place extensive diffusion systems to reduce the impact of the elevated 
salt levels in the brine on ocean biota and I would not think that coupling this with high pH would ever 
be acceptable from an environmental perspective. It would again be necessary to add an additional 
step to reduce this pH, by contact with a CO2 rich stream within a bubble or packed column. This step 
will again add additional capital cost as well as energy costs to move the water and the gas. 
 
e) The manuscript now states that ‘An ion exchange unit may be added prior to the BPMED to remove 
or replace the Mg2+ and Ca2+ in the seawater.” It is simply not that easy to soften a stream 
containing as much NaCl as seawater. The addition of the ion exchange unit adds further costs and an 
additional disposal problem, as a concentrated brine or basic solution (more concentrated than 
seawater) would need to be used for ion exchange regeneration. 
 
f) Even before considering these additional costs, the article predicts a levalised cost of 0.5 to 0.54 $ 
kg−1 CO2 which is significantly above that for direct air capture (between 0.1 and 0.23 $ kg−1 CO2). 
The authors may argue that more R&D may bring these costs down, but this is also true for Direct Air 
capture. It will be very difficult to make up this much ground.