As indicated by the title, the main aim of this paper is to draw attention to and win support for an artificial ocean iron fertilization (aOIF) experiment called KIFES that the authors wish to carry out in the region of the eastern Bransfield Strait in the vicinity of the South Korean station. If their efforts are successful, KIFES would be the 8th Southern Ocean (SO) aOIF experiment but the first to be planned and carried out within the framework of the internationally binding rules put into place by the London Convention (LC) almost a decade ago. For this latter reason alone, this manuscript takes on a relevance that is much larger than its other goals that include a review of previous experiments and recommendations for the design of future experiments. I particularly applaud the pioneering courage the authors demonstrate in taking up the challenge of applying for permission to carry out an OIF experiment following the guidelines formulated by the LC. This manuscript represents the first step in the application process; hence I would, in principle, like to see such a paper published in order to re-stimulate the discussion on using OIF as an experimental tool for hypothesis-testing in the fields of plankton ecology and ocean biogeochemistry.
However, the current version uses the geoengineering aspects of OIF as the sole justification for carrying out the experiment and judges the success of previous experiments primarily on the criterion of “effectiveness” in sequestering CO2. This is a risky strategy as, from my experience, it will not be well received by scientists working in the Southern Ocean. Although large-scale aOIF as a geoengineering technique has been under discussion for several decades, widespread opposition to such plans is nevertheless still pervasive. That this continues to be the case is indicated by the fact that no other marine scientific institutions are willing to take up the challenge of carrying out new experiments although the scientific rewards would be substantial. Thus, each experiment has provided new results on basic processes pertaining to the relationship between pelagic ecology and biogeochemistry, such as selection of the dominant phytoplankton group or species, the effects of grazing by different zooplankters, interactions within the plankton community and other fundamental issues that came to light during each experiment. OIF experiments also attract a lot of publicity which can be a bonus for funding agencies. However, the reason why no one else has plans to carry out the next aOIF experiment is because of fear of negative publicity.
The reason why OIF experiments have been and continue to be viewed with so much suspicion since the 1990s is because of the potential threat of commercialisation and large-scale damage inflicted on the environment by venture capitalists acting primarily on profit motivation; for them, mitigating the effects of climate change in a global framework would just be a collateral concern. To discourage such entrepreneurs, scientists have high-lighted potential negative side effects ever since the iron hypothesis was proposed by Martin in 1990. These have been broadcast by the media and created anxiety in the public. However, the situation has changed now. The geoengineering threat has since been thwarted by the binding regulations passed by the LC in 2010 which has pronounced a moratorium on large-scale OIF in any international waters. Further, the carbon credit system which was touted in the 1990s and 2000s as the incentive to reduce CO2 emissions but also to remove atmospheric CO2 and which would have provided the funds to finance large-scale OIF, is no longer attractive to the point of being non-functional, particularly for ventures involving OIF. In any case, a verification scheme for making cost/benefit analyses was never in place because there has never been any agreement on the relationship between iron input, CO2 removal and the commercial value of the CO2 removed in this way. I think these points need to be made prominently in this manuscript to allay the fears of scientists regarding the possible consequences of OIF experiments.
The other major impediment faced by KIFES is the intended site in the eastern Bransfield Strait. This region has different ecological and biogeochemical conditions compared to previous experimental sites, hence will provide new information and should as such be scientifically justified. However, convincing arguments as to why the experiment is aimed for that particular region are not provided in the manuscript because of its over-emphasis on geoengineering as the justification for the experiment. This is particularly important because the site lies in the heart of the highly sensitive CCAMLR region and KIFES will definitely be opposed strongly by many biologists and particularly by various NGOs for whom the idea of carrying out an OIF experiment in the heart of the animal-rich Bransfield Strait region would be anathema. A prerequisite would be to gain support from SCAR and CCAMLR, because if these international bodies are opposed to KIFES I think it highly unlikely that the LC will grant permission, because they and their reviewers would expose themselves to attack as well. Therefore, convincing arguments need to be provided in this manuscript that KIFES is not intended to be a prelude for large-scale C-sequestration but instead, is a bona fide scientific experiment testing hypotheses in the fields of plankton ecology and biogeochemistry which also pertain to the role of the Southern Ocean in regulating atmospheric CO2 levels over past climate cycles. In this context it would be necessary to provide more details as to why the eastern Bransfield Strait has been selected as the site for KIFES, other than the logistical explanation of proximity to the S. Korean station. Others will argue that, given the well-known high productivity of the eastern Bransfield Strait and its many iron sources, adding iron to the system here will have little effect. But this assumption would first need to be tested by such an experiment.
Another problem created by excessive reliance on geoengineering as a justification for aOIF is not exploiting the valuable information delivered by aOIF experiments in general. The criterion used for success of the various experiments as exemplified by lines 22 – 24 of the abstract is misleading. Here the authors write that the “effectiveness of aOIF … has been unexpectedly low compared to …. natural blooms” with the exception of EIFEX. This uncertainty is used as a rationale to carry out more experiments. This is a flawed argument because OIF experiments should not be compared with each other as individual entities on equal footing but need to be judged in the context of their duration. Later on in the text the authors explain why deep sinking was observed only in EIFEX because that was the only experiment where conditions for recording a vertical flux event were given: sufficient silicate for a diatom bloom, time to capture its rise and fall and a vertically coherent, stable mesoscale eddy to follow the sinking flux. By declaring this experiment as the only “effective” or “successful” experiment so far, the authors set a bar too high to judge subsequent experiments because the chances of finding such a “perfect, young EIFEX eddy” that was stable for so long again are quite slim. Stable eddies are analogous to weather events in the ocean and one cannot rely on there being a suitable eddy at the right time and place. It should be remembered that each mesoscale eddy has a limited lifetime and that eddies are generated by interaction between topography and meandering of the overlying front. Thus, one would need a degree of luck to find a suitable, young eddy for the experiment that would last long enough. This applies particularly to the Bransfield Strait where, because of the topography and current speed, hydrographical features are likely to be more complex and dynamic than along fronts in the open ACC.
Summing up, it is highly unlikely that the rationale presented in this manuscript will convince international bodies or institutions wary of their reputation to support KIFES, and for the LC reviewers and the LC itself to explain the reasons for giving permission for it to be carried out. Besides, the design suggested by the authors requires about 40 days in a stable eddy which requires a great deal of luck. I cannot support publication of the present version of this manuscript as the chances of KIFES acquiring permission based on the rationale presented here are vanishingly small. I would advise the authors to reconsider the rationale on which they have based KIFES and rewrite the manuscript accordingly.
Suggestions for refocusing the rationale for KIFES
The process of acquiring permission for an aOIF from the LC is a multi-facetted enterprise involving not only ecology, biogeochemistry and climate science (Martin’s iron hypothesis), but also social sciences (ethics and efficacy of climate engineering measures) and ocean governance (international law of the sea and its enforcement). Hence the next experiment will certainly draw a lot of attention from all these fields and, if permission is not granted, might well discourage other groups from trying their luck for some time to come. As someone who has been involved in 3 iron fertilization experiments in the Southern Ocean I am naturally in favour of more experiments being carried out and partial to having this paper published in order to stimulate discussion on this topic. In the following I outline how a major revision of the thrust of the arguments and a broadening of the rationale for justification of KIFES could be made so that the endeavour has a chance of success.
OIF experiments should be portrayed for what they essentially are: classic perturbation experiments that form the basis of almost all sciences. So, it is logical to carry out such experiments because they allow one to study how plankton-based ecosystems work by providing insight into mechanisms operating in real time and under in situ conditions. Although they require about the same amount of logistics and infrastructure as any observational cruise, OIF experiments have not been embraced as wholeheartedly as they deserve to be, given the many hypotheses across virtually all fields of ocean science that could be tested with them. Where observational cruises provide a jumble of snapshots from which the plot of the movie has to be guessed, carrying out an OIF experiment is like watching the movie: one can directly follow the processes triggered by addition of the crucial limiting element, iron. I think this point should be stressed in the new version
There is a broad swathe of hypotheses in the fields of pelagic ecology/biogeochemistry that can be tested with these experiments and Martin´s iron hypothesis for the Southern Ocean is just one of them. It was derived from the correlations between temperature, CO2 concentrations and dust over the past 4 glacial/interglacial cycles on the one hand and bottle experiments showing iron limitation of phytoplankton growth in HNLC regions on the other. The rationale and mechanisms proposed made sense. However, interpretation of sediment core proxies, in particular isotopes and biogenic silica as a proxy for productivity, seemed not to confirm the iron hypothesis. In recent years, model results indicate that the iron supply to the ACC via the biological carbon pump is indeed the major factor determining the upper level of CO2 during interglacials of the past 800,000 years. This is the most recent conclusion from a debate that has been going back and forth for decades: what are the sources and sinks of atmospheric CO2 over past climates cycles? The geoengineering implication of using this mechanism for carbon dioxide removal (CDR) is just a corollary of this more fundamental, overarching question. A brief summary like the one above could form the rationale for carrying out experiments like KIFES.
The current introduction makes the case for the need to research geoengineering options to combat climate change and that OIF is one of them. As pointed out above, this is exactly the reason why many scientists, I might add most biologists, entertain negative views towards OIF. The views expressed by Strong et al. (2009, Science) regarding this point are still main stream and I have explained above why the chances of getting permission from the LC for KIFES based on this rationale alone are extremely slim. Instead, I strongly recommend structuring the introduction differently by pointing out that aOIF experiments provide insights into the structure and functioning of pelagic ecosystems that cannot be acquired from observational cruises alone. The issues pertaining to carbon sequestration are a part of the bigger picture which provides the framework for a better understanding of the “effectiveness” of OIF and the C/Fe sequestration ratio (to name just one aspect). The developments in governance and political views on aOIF have been mentioned in this manuscript in a rather low-key way on pages 21-22. I would suggest putting these developments up front, also mentioning them in the Introduction, and pointing out that since a legal framework has been put in place to prevent venture capitalists from deploying large-scale OIF that particular threat no longer exists. Indeed, one might argue here that inaction on the part of scientists might be an incentive for others to go ahead with experiments as happened off Canada in 2012. Again, this OIF event is mentioned in the text but would do better in the introduction.
The chapter on the review of previous experiments is dissatisfying because, as mentioned above, it compares results of experiments directly with each other instead of accounting for their length. For instance it is mentioned that SOIREE had very different results compared to the other SO experiments. But SOIREE lasted only about 2 weeks, so it is not surprising that sinking losses were low. Absence of evidence is not evidence of absence. When experiments are compared with each other it is important to ensure that the comparisons are restricted to matching time periods, under consideration of temperature. If the first 2 weeks of SOFEX South, EisenEx and EIFEX are compared, the results would not be very different. The authors do mention later on that one has to consider the entire history of an iron fertilized bloom, but this should be self-understood. What they do not discuss is that the first 2 weeks have a decisive effect on the development and demise of the bloom. So, even if an experiment lasts only for a short while, useful information can be gained anyway from it. This is a critical point for KIFES because it is highly unlikely that the fertilized patch can be followed for much longer in that dynamic region. If spore-forming Chaetoceros dominate the bloom, as in SEEDS 1 and in the nOIF blooms then this would be an important result. If not, the dominant species would be of interest to ecologists and paleoceanographers as well.
This paper gives little consideration to the species-specific level of the organisms involved, because of its geoengineering focus. However, it is well established that, depending on the species of diatom stimulated by the aOIF, the effect on the BCP can be quite different. Indeed, there are now many papers on the importance of Chaetoceros resting spores in sediments underlying plumes from productive areas and the authors themselves mention that the intended study site is characterised by thick deposits of diatom ooze comprising these spores. It has been argued that coastal sediments are seed banks of coastal species that, because of their life cycles, intensify the BCP in contrast to grazer-protected, thickly silicified oceanic species that contribute silica but little carbon to the sediments. These typically oceanic diatoms such as Fragilariopsis kerguelensis and Thalassiothrix tend not to make spores. Biogenic silica was once considered a proxy for productivity but aOIF observations indicate the opposite. OIF experiments will help characterising the dominant species of the SO, including non-diatoms such as Phaeocystis, according to criteria based on the BCP.
Sediments dominated by either of these genera alternate during glacial and interglacial periods in the Atlantic Sector of the SO. During iron-limited interglacials, spore-bearing sediments are restricted to regions proximate to the coast but these extend further out to sea during glacials when iron input is larger. One could conclude that coastal regions provide the “seed banks” for oceanic blooms of the “effective” spore-bearing species when iron supply increases. This hypothesis could be tested with KIFES and, if properly presented, much more likely to convince the permitting authorities regarding what scientific benefit could accrue from an aOIF experiment in the eastern Bransfield Strait. An added advantage of basing arguments at the species level, rather than just POC or chlorophyll, is that even short experiments can provide useful information within regional and seasonal contexts and the structure of the prevailing ecosystem.
Other hypotheses pertain to the role of grazers. The Bransfield Strait is home to the iconic zooplankter krill, of which I could find no mention in the text. What effect will OIF have on krill, will be the first question posed by SCAR and CCAMLR. Having worked in the region and witnessed a krill swarm literally graze down a diatom bloom and then move on, I would not be surprised if such an event also happened to the KIFES bloom. This would be an ideal opportunity to investigate the long-standing debate on the role of zooplankton, particularly euphausiid faecal strings, vs. diatom aggregates in fuelling the biological carbon pump (BCP). Furthermore, krill grazing is likely to have an effect on the species composition of the bloom after the swarm moves on. Grazing could also be due to salps, which have been observed in the region, and would also be worthy of consideration in this paper. Such contingencies should be considered in the manuscript and contrasted with aOIF experiments carried out in regions dominated by copepods.
Another point that needs to be cleared up is the belief prevalent in the public that even experimental aOIF can harm the environment. This was apparent during LOHAFEX and nothing much has changed since then regarding public education. However, even biologists are apprehensive that small-scale experiments can cause harm, for instance, by inducing harmful algal blooms (HABs) that could impact the food chains leading to birds and mammals. This fear also needs to be addressed up front by pointing out that (to the best of my knowledge) no impacts of harmful algal blooms on animal life have ever been reported from the SO, not even under conditions of natural OIF around islands and land masses. Besides, the species that contributed to aOIF blooms have always been local species whenever the species composition was recorded. If OIF were to stimulate domoic acid production by SO Pseudo-nitzschia species, then such blooms should be common place in the productive hot spots of the SO, but this has not been reported to date from the Peninsula region despite investigations going back many decades. Trace gases such as N2O, methane and halogenated hydrocarbons are likely to be a problem only at the very large and long-term scales, implying that the answer to the Objective posed in lines 29-30 of page 29 will be “no”.
The region where the experiment is planned has a dynamic hydrography shaped by topography and the complex frontal systems leading into the Weddell-Scotia Confluence (WSC) along which water masses from the Weddell Sea mix with Bransfield Strait water. Mesoscale eddies are likely to be formed here and have indeed been reported, but, to the best of my knowledge, they are likely to be smaller and shorter lived than the mesoscale eddies formed along the Polar Front used by the 3 experiments EisenEx, EIFEX and LOHAFEX. Because of topography, the Bransfield Strait eddies are also likely to “wobble” more, relative to the sea floor, which will render tracking the sinking and settling diatom aggregates from the aOIF bloom through the deep water column and onto the sediment surface more difficult.
I would suggest that in the pre-experiment investigations the authors select conspicuous natural blooms appearing as chlorophyll patches on satellite images for process studies and use surrounding water as controls whether located within an eddy or not, in addition to monitoring eddies present in that period and place. By studying mature, natural blooms of high chlorophyll concentrations and snapshots of their fate it will be possible to connect diatom species composition with sinking behaviour. |
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