the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 09 Aug 2021
Evidence for iceberg fertilization of the NW Atlantic
Abstract. Icebergs are known to have a significant fertilizing impact on primary productivity in the Southern Ocean, but this link is yet to be investigated in the Northern Hemisphere. This study combines sightings of icebergs with satellite-derived ocean colour data from 1998 to 2015, to seek such a relationship in the NW Atlantic. Despite the obscuring coincidence of the seasonal iceberg flux with the spring bloom of chlorophyll, it is shown that there is a large-scale, one-month-lagged regional correlation between iceberg flux and chlorophyll levels. In addition, a spatial time-lag analysis is consistent with the main cause for the iceberg-chlorophyll relationship being through advection of the nutrients entrained in iceberg meltwater. This leads to a delayed fertilization response of 2–4 weeks. There are a range of possible sources for the nutrients likely leading to this delayed response. The Northern Hemisphere impact of iceberg meltwater on primary production is much less pronounced than in the Southern Ocean, but it is discernible.
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RC1: 'Review os-2021-61', Anonymous Referee #1, 30 Aug 2021
Bigg et al., present an analysis of iceberg distribution and chlorophyll analysis in the North Atlantic, investigating the links between iceberg distribution and primary production. The authors use satellite derived chlorophyll a, a historical record of the number of icebergs transported past 48 degrees south ‘I48N’, and a database of iceberg locations on a 1 degree grid resolution. By contrasting the dynamics of chla and iceberg density in a region of interest, and a control region, the authors investigate the role of N Atlantic icebergs in ocean fertilization. The statistical method used to do this, partial correlations, is novel in this context and is argued to show a weak but statistically significant positive effect of icebergs on chlorophyll a with a month time lag between iceberg presence and chlorophyll change. The conclusion of this paper rests heavily on the application of this technique and whether it not it is capable of distinguishing chlorophyll changes driven by iceberg passage from other ‘background’ changes.
I am a chemical oceanographer and thus whilst I’m familiar with the literature on icebergs and the use of satellite derived a, some of the statistical techniques herein are unfamiliar. With editorial consent, I did consult with a colleague concerning these aspects of the manuscript in an oceanographic context.
There are existing iceberg-chlorophyll tracking papers which explicitly show in detail (and test) appropriate statistical methods for assessing whether or not iceberg passage is associated with changes in chlorophyll, (Schwarz and Schodlok, 2009; Wu and Hou, 2017). Both of these works cited contain careful critical assessments of the methods used that robustly test whether or not the presence of an iceberg itself, rather than some coincident factor, is responsible for any associated change in chlorophyll, and whether or not any associated change in chlorophyll is different from background changes in the same region with the same timing. This work is not quite so careful, two obvious points could be raised with the method as described. First, given the technique is completely novel, why not test it in an area where icebergs are thought to have a strong influence based on existing work to see if the technique functions similarly? A different control factor would be required, but if the technique works, it should be possible to apply it to a box in a region where other studies have identified strong relationships between iceberg abundances and chla. The results of such a test would then justify the use of the technique to look for an iceberg influence somewhere more challenging where it would be more difficult to apply well tested techniques. Secondly, concerning the control parameter -the NAO index- used to account for variability due to other causes. It is not really clear to me why the NAO index used as a control parameter? Does this fully account for differences in wind driven mixing, is it completely independent of iceberg density or iceberg arrival within the region of interest? Have other control parameters been tested? Seasonal cycles can, and often do, cause artificially inflated correlations in datasets, so it’s very hard to account for this when making correlations between two seasonally variable parameters. To make a convincing case, as has been done in prior work, I think more testing of this is required, the authors could for example select some completely unrelated, but strongly seasonal, monthly time series around the N Atlantic/Greenland and attempt to do the same analysis. The authors’ case would be more convincing if they could robustly show that the weak correlation the paper hinges on is not spurious. The same comment can be made concerning a comparison between one region of interest and one control region- a comparison to multiple control regions would be more convincing, and I have some concerns about the choice of control region used.
There are also other specific problems with the statistics which I think preclude any conclusions supporting the authors’ hypothesis, particularly concerning a month ‘lag’ effect between iceberg arrival and fertilization. Such an effect is very difficult to explain using the known mechanisms via which icebergs could affect fertilization in this region and its appearance may relate to factors such as a difference in latitude and spring bloom commencement contrasting the control and ROI boxes rather than anything to do with icebergs in the ROI. More obviously, unless I’m mistaken, the control and the ROI boxes appear to be different sizes, thus statements comparing the two in terms of the number of points within each following application of any technique are not mathematically valid. What is the specific rationale for the size and location of the control box? As above, given the novelty of the technique it would have been better to pick multiple control regions, and to specifically find a control region with bloom dynamics the same as the ROI. The authors comment that the mean monthly chla in the control region is not distinguishable from the ROI, but I am not sure exactly what this means as chla data clearly shows that the spring bloom commences and peaks much earlier in the control region than it does in the ROI.
Main points
- I found the manuscript very hard to read, whilst some of the statistics are described in detail, other points (which could be tested statistically) are made as unsupported qualitative statements. For example, it’s not actually clear from reading the text where icebergs are within the ROI, or what the main area receiving iceberg tracks is. The authors refer to this ‘iceberg alley’ several times, so an obvious question is why not define this region and then we can see if there are/aren’t strong correlations specifically for this area of high iceberg tracks? Is the main ‘iceberg alley’ a subregion with the region of interest? Does this correspond to the patch of significant correlation highlighted within the ROI in several figures?
- In several places the statistical analysis and interpretation is flawed. As an example, there are comments related to the number of points within the control and region of interest (ROI), but the ROI is bigger than the control region, so the two cannot be compared directly in terms of number of points. Clustering of points (patchiness) is also described as if it supports the hypothesis, but patchiness is inherent in any random distribution, so the presence or absence of a “coherent area of statistically significant partial correlation” is meaningless in terms of testing the hypothesis unless this cluster corresponds to something quantitatively.
- There is presently a lot of qualitative discussion concerning biogeochemistry, but whilst the authors correctly identify the few known mechanisms that could explain a link between icebergs and primary production (upwelling/mixing or direct nutrient fertilization), they don’t provide any quantitative analysis of existing data to show which is likely to be effective in the North Atlantic. There are a couple of cruises that have iron/macronutrient data for the region and I’m not sure these support the authors’ hypothesis that addition of iceberg-derived-Fe could be increasing primary production. The Fe calculations that are provided seem out of place without commenting on what Fe and nutrient concentrations are in the region of interest and to what extent there could be Fe or nutrient-limitation in the region at the time of year concerned. They also seem circular, the authors summarize that Fe input into the region of interest could be massive compared to dust input (which is generally thought to be the main input by oceanographers), but if this were the case, and the authors’ hypothesis that any iceberg derived nutrients are being mixed in surface waters for a month before driving any increase in chla were correct, surely Fe concentrations across the region would be high and thus small changes in iceberg Fe delivery would not be needed to change primary production (there would be an excess of Fe relative to other nutrients)?
- The timing of the ‘lag’ investigated herein also seems dubious as this is not really consistent with the Fe fertilization discussed. The (Arrigo et al., 2017) reference cited for example shows a rapid effect of meltwater arrival on chla in a specific box off SW Greenland which is interpreted as possibly being Fe fertilization– but this statistic concerns bloom timing not total chla, so the mechanism doesn’t really compare to what the authors discuss herein. Fe cannot be transported long distances at the ocean surface, it is rapidly scavenged and drawn-down by primary producers even in areas where it isn’t considered a limiting nutrient (e.g. see discussion by (Birchill et al., 2017)) so the idea of an Fe plume from icebergs remaining in the ocean during the growth season, having no effect on primary production until one month after it was deposited is implausible. Fe addition experiments usually show a positive fertilization effect after 1-5 days (e.g. see Browning et al., 2019, 2021 in the ROI) consistent with the timing effect suggested off SW Greenland, and similarly where strong Fe fertilization is observed in the Southern Ocean elevated dFe concentrations are only noticeably observed within a few km of icebergs (Lin et al., 2011; Lin and Twining, 2012) with chla changes detected within days (see main comment for papers doing this well).
Line comments:
13-14 This is not really consistent with any known mechanism of iceberg fertilization. If a nutrient required for primary production in the N Atlantic was upwelled or released as the iceberg melted, it would be drawdown much faster than this during the growth season. Fe in particular does not have a long residence time in the ocean surface, especially during the growth season, so it’s not clear to me what this is ‘consistent’ with. It’s quite bizarre and unexpected.
15 By range, I assume the authors mean either upwelling or release from melting ice? So why not just say these two.
33 Do any icebergs from Greenland not enter the North Atlantic? – it would be very useful on some figure to show iceberg tracks, or areas of high iceberg observations as at present it is not clear at all where the icebergs are or where they generally go. Thus it’s very difficult to comment on the validity of the chosen boxes used in all statistics.
40-41 This is not a correct inference. High secondary production, or high abundances of seals/birds/fish etc does not necessarily imply local high primary production. E.g. it’s well documented seals rest on icebergs after sea ice loss, and there is generally a hotspot of feeding activity at glacier termini in the Arctic (Lydersen et al., 2014), but is not because local primary production is high - quite the opposite in this case, these zones have low primary production but the water column disturbances kill /stun prey making convenient hunting grounds. So ‘enriched ecosystem locally’ does not imply iceberg fertilization.
42 The reference cited does not show micronutrient limitation of the Labrador Sea, they suggest Fe limitation could occur in one specific region off SW Greenland, but only at a window between the spring and summer blooms, not across the Labrador Sea during summer as cited. Canadian GEOTRACES data would be better cited here as this shows low-nitrate/low-Fe conditions in summer in the Labrador Sea.
44-45 What iceberg depth / mixed layer depth is being referred to here? Based on the comments on iceberg dimensions herein, I would not expect more than a minority of large icebergs to penetrate the mixed layer depth in the Labrador Sea, only in well stratified coastal regions where the MLD is shallower.
47 Is there data on the nutrient content of icebergs? I would think this was generally very low for more macronutrients but I’m not sure you refer to any data to suggest the contrary. I’m not sure ‘bypasses removal in fjords’ is quote correct. Icebergs are subject to intensive melting in fjords around Greenland, loosing a majority of their volume and sediment, e.g. (Azetsu-Scott and Syvitski, 1999)
51 Raiswell et al,. don’t explicitly show this, I think it is worth asking how much of the iceberg derived sediment is actually exposed to UV light and for how long, a large fraction likely melts and gets deposited in fjords without ever being exposed to sunlight. e.g. above ref shows most of this sediment never enters the ocean surface (Azetsu-Scott and Syvitski, 1999)
52 What mechanism would icebergs promote spring productivity via? There’s no suggestion in the literature, or in this manuscript, of a mechanism via which icebergs could do this in the North Atlantic.
164 I don’t think (Schwarz and Schodlok, 2009) show this, they only test 6 day periods before and after iceberg transit.
176 “little iceberg meltwater” It is not clear to me what this means -melt from icebergs from the point they enter the ocean? Most freshwater from Greenland (which includes most iceberg melt as most of this occurs near-shore largely overlapping with where runoff enters the ocean) is advected counter-clockwise around the Labrador Sea and then follows the Labrador shelf precisely where the authors state there is no impact (?) e.g. see manuscripts modelling this (Luo et al., 2016)
Figure 3. Why are the ocean areas of the control and main regions different? The region of interest looks to be considerably larger than the control region? Several of the comparisons are invalid as there are fewer datapoints in the control region so it is not valid to comment on ‘less/more’ of anything relative to the control region.
187-188 This does not prove causation. What factors lead to high iceberg transfer into this region? These factors likely include wind/current forcing which also affects plankton dynamics. If icebergs did have an impact at this time of year, via what mechanism is this plausible? It is not clear to me what factors the NAO does/doesn’t account for.
191-192 This is not robust if the only test is whether or not correlation with chl is higher than one control region based on the fact that the control region has similar environmental forcing (and see my earlier comment concerning the timing of the spring bloom between the two regions). This should really be done compared to multiple iceberg free regions and ideally in regions with similar bloom dynamics rather than significant temporal offsets in the initiation of the bloom. If it is the case that only the main region of interest has a strong iceberg signal, then this basic statistic (that the correlation between chla in this region, and a control region with similar forcing is stronger in low iceberg years and weaker in high iceberg years) would hold generally with a comparison across all of the adjacent cells. The sensitivity of the statistic to the threshold of 100 should also be shown. Looking at Figure 1 for example, it looks like the best possible fit between spring mean chla and spring I48N would be obtained for the ranges I48N >900, or I48N >200 i.e. a correlation may be very sensitive to what threshold is used just because the dataset is small.
Figure 4 This is not particularly convincing without showing sensitivity analysis. For example, why is there also a positive 2 month threshold for the control region? If I understood correctly, what is shown here is the correlation between a list of numbers (I48N) that show a peak building from march, peaking in May, and then shouldering in July, with chla dynamics. The timing of the spring bloom varies by region/latitude and thus in a correctly selected region, the timing of the spring bloom peak and spring I48N peak will coincide creating a better correlation than is possible in a region where the events don’t coincide temporally. Looking at regional Chla, the spring bloom starts earlier in the control region peaking in April (i.e. too early to match the I48N) peak, whereas the bloom starts later in the region of interest and is more intense. So there is a better temporal overlap between the timing of I48N and the spring bloom in the region of interest. If the control region were instead at the same latitude with the same seasonal timing of the spring bloom, it may no longer be the case that there is a difference between the Person correlations shown. As above, multiple control regions around the ROI would be more convincing.
Figure 5 again shows a correlation between a list of numbers, IT, and local chlorophyll anomalies within small grid cells in the control region and region of interest. In looking at whether there are positive or negative correlations here, the number of cells must be considered. Again, if icebergs had no effect, IT could be considered a random list of numbers, in which case the correlation would be random i.e. equal roughly numbers of positive and negative correlation scattered across the regions. With a p value of 0.05 how many boxes within the regions would show a correlation in such a random scenario? Is this more or less than actually show a correlation? For the amount of grid cells and a p value of 0.05, the displayed data does not appear to show any convincing relationship. It’s hard to comment without knowing the number of grid cells, but from what I can see the balance between positive and negative values and the number of cells picked out by a p value of 0.05 seem to show not much difference from a random distribution.
273 Here and elsewhere the authors comment on the patches of statistically significant correlations, but patchiness would be observed in any random distribution. Do these patches actually correspond to anything meaningful, i.e. can you plot the intensity of iceberg distributions onto cells? If not, this discussion is relatively meaningless concerning Figure 5.
288 But (a) the control region is smaller and (b) randomly dispersed patched would be present in a random distribution. Patchiness is inherent in a random distribution, so patchiness doesn’t make any argument more convincing unless it can be shown quantitatively that the patches mean something i.e. do they correspond to areas with the highest iceberg intensity? As noted above, more correlation between chla and iceberg presence could simply reflect latitude as in the area of interest the timing of the spring bloom is better matched to the timing of iceberg arrival. It would be useful to have control regions distributed around the area of interest, not just one SW of it with an earlier bloom dynamic.
Figure 6. Similar comment to the above statistics. I’m not sure what this really shows, there’s a positive lag effect across the N Atlantic including in the ROI, but also in areas that don’t receive any iceberg influence outside the ROI? The region of interest doesn’t appear to show an iceberg ‘hotspot’ that can be delineated from any other effect, (unless as above the authors can specifically highlight the area of highest iceberg intensity) so I’m not sure this adds any evidence to support the authors hypothesis.
References referred to
Arrigo, K. R., van Dijken, G. L., Castelao, R. M., Luo, H., Rennermalm, Å. K., Tedesco, M., Mote, T. L., Oliver, H. and Yager, P. L.: Melting glaciers stimulate large summer phytoplankton blooms in southwest Greenland waters, Geophys. Res. Lett., 44(12), 6278–6285, doi:10.1002/2017GL073583, 2017.
Azetsu-Scott, K. and Syvitski, J. P. M.: Influence of melting icebergs on distribution, characteristics and transport of marine particles in an East Greenland fjord, J. Geophys. Res., 104(C3), 5321, doi:10.1029/1998JC900083, 1999.
Birchill, A. J., Milne, A., Woodward, E. M. S., Harris, C., Annett, A., Rusiecka, D., Achterberg, E. P., Gledhill, M., Ussher, S. J., Worsfold, P. J., Geibert, W. and Lohan, M. C.: Seasonal iron depletion in temperate shelf seas, Geophys. Res. Lett., 44(17), 8987–8996, doi:10.1002/2017GL073881, 2017.
Browning, T. J., Al-Hashem, A. A., Hopwood, M. J., Engel, A., Wakefield, E. D. and Achterberg, E. P.: Nutrient regulation of late spring phytoplankton blooms in the midlatitude North Atlantic, Limnol. Oceanogr., 65, 1136–1148, doi:10.1002/lno.11376, 2019.
Browning, T. J., AlâHashem, A. A., Hopwood, M. J., Engel, A., Belkin, I. M., Wakefield, E. D., Fischer, T. and Achterberg, E. P.: Iron regulation of North Atlantic eddy phytoplankton productivity, Geophys. Res. Lett., doi:10.1029/2020gl091403, 2021.
Lin, H. and Twining, B. S.: Chemical speciation of iron in Antarctic waters surrounding free-drifting icebergs, Mar. Chem., 128, 81–91, doi:10.1016/j.marchem.2011.10.005, 2012.
Lin, H., Rauschenberg, S., Hexel, C. R., Shaw, T. J. and Twining, B. S.: Free-drifting icebergs as sources of iron to the Weddell Sea, Deep. Res. Part Ii-Topical Stud. Oceanogr., 58(11–12), 1392–1406, doi:10.1016/j.dsr2.2010.11.020, 2011.
Luo, H., Castelao, R. M., Rennermalm, A. K., Tedesco, M., Bracco, A., Yager, P. L. and Mote, T. L.: Oceanic transport of surface meltwater from the southern Greenland ice sheet, Nat. Geosci., 9(7), 528–532, doi:10.1038/ngeo2708, 2016.
Lydersen, C., Assmy, P., Falk-Petersen, S., Kohler, J., Kovacs, K. M., Reigstad, M., Steen, H., Strøm, H., Sundfjord, A., Varpe, Ø., Walczowski, W., Weslawski, J. M. and Zajaczkowski, M.: The importance of tidewater glaciers for marine mammals and seabirds in Svalbard, Norway, J. Mar. Syst., 129, 452–471, doi:10.1016/j.jmarsys.2013.09.006, 2014.
Schwarz, J. N. and Schodlok, M. P.: Impact of drifting icebergs on surface phytoplankton biomass in the Southern Ocean: Ocean colour remote sensing and in situ iceberg tracking, Deep. Res. Part I Oceanogr. Res. Pap., 56(10), 1727–1741, doi:10.1016/j.dsr.2009.05.003, 2009.
Wu, S.-Y. and Hou, S.: Impact of icebergs on net primary productivity in the Southern Ocean, Cryosph., 11(2), 707–722, doi:10.5194/tc-11-707-2017, 2017.
Citation: https://doi.org/10.5194/os-2021-61-RC1 -
AC1: 'Reply on RC1', Grant Bigg, 20 Oct 2021
Reply to Reviewer 1
We welcome the reviewer’s careful analysis of our paper. However, we believe that they have unconsciously exaggerated the confidence of our findings. We are claiming that despite the complexity of the region and its forcing we think there is sufficient evidence to suggest that icebergs probably do have an influence on production in the NW Atlantic, but that this is difficult to isolate. Our paper is a call for more targeted studies to investigate such a link, to confirm or deny our speculative findings. We would be happy to make it clearer that the purpose of the paper is to provide a first analysis of a complex question.
Previous papers investigated the link between icebergs and production have studied the Southern Ocean, where the icebergs are larger and even casual inspection of images of iceberg motion compared to chlorophyll values provides strong suggestion that there is a signal to find. The various papers quoted by the reviewer do indeed carry out very careful analyses but in a region where the circumstantial evidence is stronger, and the database of the location and size data for icebergs is better than available to this paper. The NW Atlantic is a difficult region in which to seek a signal: the main iceberg flux corresponds with the timing of the spring bloom; the concentration in iceberg science there is for protection of shipping; and the region is one with significant climatic and weather variability. This is why we sought to use the novel technique of partial correlation, which is novel in oceanography but used as a standard statistical technique in other fields, as we note in the paper. Because the technique is not novel per se, and the circumstances of the study region are so unique, we did not consider it worth using the approach elsewhere. This could be done, but we do not agree with the Reviewer that this would strengthen our specific analysis.
The reviewer also questions why we used the NAO index as the control variable. We did explore a number of other possible control variables, as mentioned in the paper, however, we found the NAO, as a well used and acknowledged measure of North Atlantic climate variability, gave the strongest correlations. It is not correlated with iceberg numbers (Hanna et al., 2011; Zhao et al., 2016), if indirectly linked to iceberg calving and survival (e.g. Bigg et al., 2014; Zhao et al., 2016; Bigg et al., 2019). This is already referred to in the paper.
The reviewer also questions our control region choice. There are few other options in the region. We needed an area of a similar latitude, close to the coast, so experiencing similar seasonal river fluxes and climate, but not visited by icebergs. Areas north or east of the core region would not be suitable control analogues as they violate one or more of these conditions. We agree that no region would be a perfect control but argue that the region shown in Figure 3 is the best choice, given our core region. We defend our analysis in the paper showing that the mean chl in the control region is significantly correlated with that in the core area.
Addressing main points:
- The reviewer assumes the quality of the iceberg data is much better than it is in reality. We describe the various ways we have tried to reconstruct iceberg data in the paper, but using the basic number data provided by the International Ice Patrol, which includes all icebergs observed out to 35W, restricts options for a large-scale study. A more focused study could look at individual years and individual tracks but the quality and amount of the available data means that this is a task for a next step, rather than the first attempt to examine the question here. The iceberg tracks are sufficiently variable from year to year that we decided not to seek to define a smaller area. If it would help with assessment of the analysis we could provide a map of iceberg density. As an example, the density map for all icebergs observed in the high iceberg year of 2015 is given below. This shows that icebergs are present over much of our core area.
Figure 1: iceberg density map for icebergs seen in our region during the year 2015.
- We are not aware of discussion about “numbers of points” anywhere in the paper. We usually compare mean quantities of areas, whether chlorophyll a or iceberg number, with 1x1 degree fields. We are aware that our mention of clustering of points is not a statistically robust statement as random numbers will cluster, as the review points out. However, the spatial coherence of significance is at times suggestive and it would be remiss not to point this out to the reader.
- We would be happy to remove any discussion about iron in the Discussion. However, the reviewer has not appreciated that this is a “back of the envelope” approach showing that such fertilization by icebergs is not impossible in the NW Atlantic. We do not claim it is occurring. Further fieldwork would be needed to verify this. However, we stand by the spirit of the qualitative discussion given. This is a field that promotes polarization of viewpoints and we do not attempt to join this but merely explore possibilities.
- The Reviewer questions the one month lag suggested between iceberg presence and productivity maxima. This has previously been found in the Antarctic as possible, both for icebergs (Duprat et al., 2016) and for iron-fertilization experiments (e.g. SOFEX). We do not claim to know what drives this, which was a clear signal in the analysis, but present several possibilities linked to ocean circulation. We are not proposing an iron explanation for this phenomenon. More fieldwork is needed to establish the robustness and cause of this phenomenon. Our analysis is only a first step.
Line Comments:
- 13-14: We agree the abstract sentence is misleading. We suggest it is changed to “In addition, a spatial time-lag analysis is consistent with the main cause for the iceberg-chlorophyll relationship being linked to advection of the nutrients entrained in iceberg meltwater.” We stand by the 2-4 week delay found in the analysis, which is consistent with Southern Ocean work, as suggested above.
- 15: we kept the cause vague deliberately, so as not to miss any currently unknown mechanisms.
- 33: Of course not all Greenland icebergs enter the Labrador Current. Probably only a few per cent reach the area of interest (see Marsh et al., 2019). This comment clearly suggests we should add a map of iceberg density in a final paper version (e.g. like Figure 1 above).
- 40/41 & 42: We are happy to omit the inference from higher trophic levels and alter the reference in l. 42.
- 44-45: Much of the region discussed is coastal or on the Grand Banks and so relatively shallow. We can certainly change the statement to make it clear it is larger icebergs that are referred to in terms of causing vertical mixing.
- 47/51: There isn’t much information available on nutrient levels in icebergs but sufficient evidence just from open ocean pictures that some exists (see figures in chapter 2 of Bigg, 2016). We are not questioning that most icebergs don’t escape fjords, but some clearly do (see l. 33 comment above). We are focusing on those that reach the Newfoundland area.
- 52: The reviewer misreads our statement. We merely say the iceberg peak corresponds to the timing of the spring bloom. Nowhere do we say the latter is caused by icebergs. It is this co-incidence of timing that makes our analysis much more difficult.
- 164: We suggest modifying the line to “Remote sensing analysis in the Southern Ocean also suggests that the impact of fertilization from melting icebergs can have a time lag of some days (Schwarz and Schodlock, 2009) to weeks (Duprat et al., 2016).”
- 176: we are referring to meltwater from nearby icebergs clearly. We suggest changing this sentence to “A nearby coastal area, which will experience many of the same environmental forcings as the main area, but which almost no icebergs reach (see Fig. 13 of Wilton et al., 2015), was also defined as a control area.”
Figure 3: the areas are different in size. However, analysis is in terms of comparisons between means. There is no discussion where point numbers play a role in the analysis. Nevertheless, if desired, we could alter the box sizes to make them comparable. Some of the analysis already only goes to 52N, removing 80 grid boxes and making the areas roughly the same.
- 187-188: causation is not intended. We can change the wording to remove this connotation: “The next step is correlating the monthly mean chlorophyll between the control and iceberg areas for just the months during the peak iceberg season of April-June.”
- 191-192: The argument in this whole paragraph is to suggest that the control and main areas do experience different behaviours when icebergs are present in one. It is not definitive, merely suggestive. We could remove the whole paragraph but feel the reader loses some of the rationale behind our thought processes by doing so.
Figure 4: we agree this is not particularly convincing. It is why the analysis then takes on its novel approach, to try to strengthen the hints Figure 4 provided. The reviewer is being too critical of what is clearly the first step of the analysis. Note that the 2 month control area correlation is not statistically significant and we do address this aspect in the text (l. 264-5).
Figure 5: we agree that this is not strong. This fact is why we then go on to the lag study, as is stated in l. 291. This is a difficult problem and unlike some scientific approaches we here show our steps to arrive at the best answer we could with the data available. Science is not perfect and the process of argument reasoning is often not shown. (l. 273 and 288 are also part of the discussion that ends needing to move to a deeper analysis so we will not directly reply to these points)
Figure 6: we feel the Reviewer had decided against the paper’s theme by this point and was not prepared to examine the evidence in Figure 6 – and most importantly the video – in a positive way. We believe Fig. 6 and the video clearly show an increase and movement of regions of positive correlation. We do not claim to know what causes this but the Discussion attempts to address this question. The answer awaits further work.
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RC2: 'Comment on os-2021-61', Delphine Lannuzel, 23 Sep 2021
Review - Evidence for iceberg fertilization of the NW Atlantic
General comment:
The North Atlantic basin bloom has been widely studied, as far back as 1950s with Sverdrup testing his critical depth theory using Spring bloom data. This initial theory has since be challenged with work from Siegel et al 2002 and Behrenfeld a few years later. Nitrate is generally the main limiting nutrient in the North Atlantic since the Sarahan dust supplies enough Fe to surface waters for it not to be limiting. Iron can however sometimes be found at levels too low to support marine productivity, as shown in papers from Rijkenberg et al 2014 and Achterberg et al., 2018.
The Ice Sheets have been recognised as important sources of trace elements to the polar seas, with potentially a significant contribution to the global carbon sequestration. In the Southern Ocean the fertilization effect from large icebergs on local surface productivity can be seen from satellites recording ocean colour. In the North Atlantic, some work by Smith et al 2013 and others suggests that icebergs from the Greenland ice sheet may well play a role in boosting local productivity and this is the hypothesis that the authors are aiming to test here.
I think that topic is extremely interesting, whether the hypothesis is proven right or wrong. However I find the manuscript hard to follow and the execution not very convincing, which is unfortunate. I suggest below some different ways to appraoch the work and I hope you find some of my comments useful.
Introduction:
The introduction is needs to be approached differently. I would instead use the following structure: 1/ Known drivers are of the NA bloom. you can go as far back as Sverdrup 1953, then Siegel et al 2002, then Berehnfeld. Here what is important is a critical assessment of the role of the wind mixed layer depths and light in initiation of the blooms. The Siegel et al 2002 is especially key since it covers the area of interest that this paper focuses. Do note that 71 - 87% of Fe in NA comes from dust (from Sahara). 2/a section on macronutrients and Fe limitation in the NA, referring to the RijkenBerg work, then 3/ your hypothesis: icebergs may supply additional Fe to a localised region of the NA.
Note that lines 53-61 are already results/discussion and need to be removed.
Figure 1 needs work: a)we need lat/long and main landmarks. It would also be good to see the limits of the study area for satellite derived ocean color analysis, as well as detailed bathymetry. Here for exemple it looks like the enhanced Chla areas match shallow bathymetry, which makes sense. ie. coastal waters being more productive than offshore waters (from upwelling and/or local eddies). b) is confusing. The reader is not quite sure what they’re looking at. I would remove it
Methods:
The Methods are confusing as they currently stand. The way I would approach the study is by comparing the climatology of Chla vs frequency of icebergs transiting through the study area. ie. in years that we have higher occurence of icebergs passing through the study area, do we see anomalies in Chla records? You could stick to the bloom period, ie. April-May. and secondly are these positively and significantly correlated? I would set the scene that way lines 74-80, then explain how the Chla and icebergs data were obtained. One point to emphasize is that the data does not report size, which I think is key. ie. small icebergs are unlikely to alter the area of interest as much as a giant iceberg would.
I would move lines 75-80 to the "iceberg data" subsection, and 80-83 to the Chla subsection.
Line 82: Also it would be worth mentioning that polar areas are quite tricky with ocean colour - clouds decrease data coverage and large solar zenith angles can lead to an underestimation of the in situ chlâa - see Sirjacobs et al., 2011.
Line 88: Please define the box/area of study as xx–xx°N and xxx–xxx°W - we need the same spatial limits for Chla and icebergs analysis otherwise we're comparing apples and pears
Line 92-94: Before applying the standardisation did you test the difference between MODISâAqua and SeaWiFS values in the area when co-located data are available. ie. what is the mean difference between the 2 products for your study area, and is this different statistically?
Line 101-103: Here instead you should record the flux of icebergs transiting through the defined study area from any direction - ie. why 48N? and where it that relative to the study area? We really need lat/long on Figure 1.
Line 163: this is a Southern Ocean reference
Line 165: is it really a time lag, or that the fertilisation effect can last for weeks? in the case of Fe, there is no way that this Fe would stay in surface waters for that long. Nitrate might (not that I have any references to support this statement), but not Fe. This idea is carried through the whole manuscript yet I cannot wrap my head around such a long Fe residence time.
Line 175-177: I am not fond of this approach. Region A is influenced by coastal processes, which is not the case for the "iceberg" region. What I would do instead is simply run a climatology of the iceberg area as I suggested above. ie. do you see enhanced (above average) Chla the years that more icebergs transit through the area? noting that other processes (large scale weather forcings like NAO, eddies) may explain any anomalies in surface Chla
Figure 3: Again here, if you superpose bathymetry I think that you will see that the control area and iceberg area have completely different bathymetry, therefore physical and chemical settings.
Line 181-192: The drivers of the blooms will be different, even though you may have a similar end results. To really nail this down, you would need to run a climatology of bloom start, bloom end and bloom amplitude (and max) in both regions (see Arctic and Antarctic phytoplankton bloom phenology studies). Check e.g., / bathymetry, 2/wind mixed layer depths, 3/Sea surface height (i.e do you have eddies?), or as studied later the NAO.
If results are exactly the same then maybe yes you can say the 2 areas undergo similar environmental conditions (before adding icebergs influence to the mix). But at the moment, the approach is not rigorous enough.
Line 199-204- remove this text
Line 207: I am struggling with this section - I don't think that this approach holds particularly well - Why would you expect a temporal decoupling between icebergs passing and the Chla anomaly? Please explain, set the scene for the reader.
Results & Discussion:
Given the lack of rigorous approach to the study I have to admit that I did not particularly trust the results and discussion sections, nor spent considerable time on them, simply because they are not well founded.
In Figure 4 for exemple the signals are very patchy and it's difficult to say that weak correlations translate into direct causation. There are a lot of studies on the NA spring bloom that should be cited/explained before suggesting that icebergs drove these trends.
The section on fertilization is also weak - when you say fertilization, is it Fe? or is it that the icebergs create local mixing that may bring NO3 up? Please explain. One thing to also highlight here is that not all Fe is bio-available. Plus you need enough Fe binding ligands in seawater to keep this Fe in surface waters. This is where the lag time is a really tricky concept to grasp.
Line 375-376: Is there any obvious trends in that flux? I would have imagined that maybe the flux of icebergs may have significantly increased since 1958. If that’s the case, then this work could become really interesting from a climate change angle, ie. as the polar ice sheet continue to lose mass.
The whole section of Fe fluxes to the area needs tightening. Go source by source, using data from the literature to report possible Fe flux to the study area, ideally reported in umol Fe/m2/d. Please check the units and the conversions carefully.
Conclusions:
The conclusions are not really supported by the results. The authors are so keen to draw a line between icebergs and phytoplankton bloom, that they dismiss other possible drivers. This needs rewriting.
Citation: https://doi.org/10.5194/os-2021-61-RC2 -
AC2: 'Reply on RC2', Grant Bigg, 20 Oct 2021
Reply to Reviewer 2
We welcome the reviewer’s careful reading of our paper. However, as with Reviewer 1, we believe that they have unconsciously exaggerated the confidence of our findings. We are claiming that despite the complexity of the region and its forcing we think there is sufficient evidence to suggest that icebergs probably do have an influence on production in the NW Atlantic, but that this is difficult to isolate. In other words, chlorophyll peaks have a range of causes, as the Reviewer rightly points out in their overview of the subject at the beginning of the review, but we are only proposing that an iceberg influence is discernible, rather than dominant, or even important. Our paper is more a call for targeted studies to investigate such a link, to confirm or deny our speculative findings. We would be happy to make it clearer that the purpose of the paper is to provide a first analysis of a complex question.
The introduction is needs to be approached differently. I would instead use the following structure: 1/ Known drivers are of the NA bloom. you can go as far back as Sverdrup 1953, then Siegel et al 2002, then Berehnfeld. Here what is important is a critical assessment of the role of the wind mixed layer depths and light in initiation of the blooms. The Siegel et al 2002 is especially key since it covers the area of interest that this paper focuses. Do note that 71 - 87% of Fe in NA comes from dust (from Sahara). 2/a section on macronutrients and Fe limitation in the NA, referring to the RijkenBerg work, then 3/ your hypothesis: icebergs may supply additional Fe to a localised region of the NA.
We would be happy to rewrite the Introduction towards the approach suggested, however, it does change the purpose of the paper to be explicitly about what explains chlorophyll behaviour in the NW Atlantic. This is changing the intention beyond what the paper is trying to do, which is see whether there is any evidence for icebergs to influence productivity in the North Atlantic as it is known to do in the Southern Ocean.
Note that lines 53-61 are already results/discussion and need to be removed.
These lines are helping to set the scene for the discussion in the paper and so pertinent to the Introduction. We think the focus of the paper would be lost by removing this text.
Figure 1 needs work: a)we need lat/long and main landmarks. It would also be good to see the limits of the study area for satellite derived ocean color analysis, as well as detailed bathymetry. Here for exemple it looks like the enhanced Chla areas match shallow bathymetry, which makes sense. ie. coastal waters being more productive than offshore waters (from upwelling and/or local eddies). b) is confusing. The reader is not quite sure what they’re looking at. I would remove it
Figure 1 could be improved by adding bathymetry and more labelling. Part b is not confusing – it shows very clearly that there is no strong link between the established measure of iceberg numbers in the region and chlorophyll levels during the peak iceberg season. It clearly shows that icebergs are not the dominant cause of variability in chlorophyll and that we need to look deeper to seek what influence they do have.
Methods:
The Methods are confusing as they currently stand. The way I would approach the study is by comparing the climatology of Chla vs frequency of icebergs transiting through the study area. ie. in years that we have higher occurence of icebergs passing through the study area, do we see anomalies in Chla records? You could stick to the bloom period, ie. April-May. and secondly are these positively and significantly correlated? I would set the scene that way lines 74-80, then explain how the Chla and icebergs data were obtained. One point to emphasize is that the data does not report size, which I think is key. ie. small icebergs are unlikely to alter the area of interest as much as a giant iceberg would.
The Reviewer is recommending we swap the initial results to become a motivator for the methods used. While we can see this argument, isn’t that what Fig. 1b has already done? We prefer to leave the order of the methods as it is.
I would move lines 75-80 to the "iceberg data" subsection, and 80-83 to the Chla subsection.
We were trying to say there were issues with both main data sources for our analysis. The respective texts could be moved as suggested.
Line 82: Also it would be worth mentioning that polar areas are quite tricky with ocean colour - clouds decrease data coverage and large solar zenith angles can lead to an underestimation of the in situ chlâa - see Sirjacobs et al., 2011.
This is a helpful suggestion and can be added in a revision.
Line 88: Please define the box/area of study as xx–xx°N and xxx–xxx°W - we need the same spatial limits for Chla and icebergs analysis otherwise we're comparing apples and pears
This can be added, although note that we obtained much more of the North Atlantic surface with the chlorophyll data than icebergs, to be able to compare within iceberg-influence areas from non-iceberg areas.
Line 92-94: Before applying the standardisation did you test the difference between MODISâAqua and SeaWiFS values in the area when co-located data are available. ie. what is the mean difference between the 2 products for your study area, and is this different statistically?
We did look at the difference and found it small but non-zero. We can give values in a revision.
Line 101-103: Here instead you should record the flux of icebergs transiting through the defined study area from any direction - ie. why 48N? and where it that relative to the study area? We really need lat/long on Figure 1.
We agree we should show 48N on Figure 1 – it is level with the southern coast of Newfoundland approximately. Icebergs are largely taken through the study area by the Labrador Current along the western shore of the Atlantic basin, so an east-west line is most sensible for this analysis (and has been the standard used by the International Ice Patrol for over 100 years). A map of iceberg density could be shown, as was also suggested by reviewer 1 (please see Figure 1 from the reply to this reviewer).
Line 163: this is a Southern Ocean reference
Wording here can be altered to make it clear we are seeking information from a Southern Ocean source. This is where the vast majority of iceberg analysis has originated.
Line 165: is it really a time lag, or that the fertilisation effect can last for weeks? in the case of Fe, there is no way that this Fe would stay in surface waters for that long. Nitrate might (not that I have any references to support this statement), but not Fe. This idea is carried through the whole manuscript yet I cannot wrap my head around such a long Fe residence time.
There have been few in-situ observations so the answer to this question is unknown. However, it is well established that fertilization effects after iceberg passage in the Southern Ocean are visible for up to several weeks. There may be a range of causes: direct input of nutrients/trace nutrients from melting icebergs; enhanced vertical mixing of nutrients from below the surface in meltwater plumes; slow mixing of initial localised concentrations to larger areas; a requirement for time to pass for the conjunction of light, nutrients, currents and chlorophyll growth to occur. It is not the aim or purpose of this paper to explain the time delay, but to present it. See l. 354-359 for a discussion of this point.
Line 175-177: I am not fond of this approach. Region A is influenced by coastal processes, which is not the case for the "iceberg" region. What I would do instead is simply run a climatology of the iceberg area as I suggested above. ie. do you see enhanced (above average) Chla the years that more icebergs transit through the area? noting that other processes (large scale weather forcings like NAO, eddies) may explain any anomalies in surface Chla
The suggested approach was already presented in Figure 1b – this is not enough to demonstrate any link that might occur between iceberg numbers and chlorophyll
Figure 3: Again here, if you superpose bathymetry I think that you will see that the control area and iceberg area have completely different bathymetry, therefore physical and chemical settings.
No control area is perfect. However, both areas have significant coastal regions, areas with significant riverine fluxes and also areas of deep water. Both also cross the Gulf Stream, so contain some polar-source water and sub-tropical source water. The reader also needs to note this approach begins the analysis but does not drive it beyond the starting analysis.
Line 181-192: The drivers of the blooms will be different, even though you may have a similar end results. To really nail this down, you would need to run a climatology of bloom start, bloom end and bloom amplitude (and max) in both regions (see Arctic and Antarctic phytoplankton bloom phenology studies). Check e.g., / bathymetry, 2/wind mixed layer depths, 3/Sea surface height (i.e do you have eddies?), or as studied later the NAO.
We agree with the reviewer about the diversity of causes of blooms. However, the paper is not about untangling this question in the NW Atlantic but about trying to see whether icebergs are a non-trivial factor that has previously been neglected.
If results are exactly the same then maybe yes you can say the 2 areas undergo similar environmental conditions (before adding icebergs influence to the mix). But at the moment, the approach is not rigorous enough.
This is just the first step of the analysis, and the approach suggested would distort the direction of the paper’s argument.
Line 199-204- remove this text
We do not understand this comment. Surely we need to show the novel approach of partial correlations used here is an established technique in the wider fields of science?
Line 207: I am struggling with this section – I don’t think that this approach holds particularly well – Why would you expect a temporal decoupling between icebergs passing and the Chla anomaly? Please explain, set the scene for the reader.
We explain above why there might be a time lag. This is a well established observed fact in the Southern Ocean.
Results & Discussion:
Given the lack of rigorous approach to the study I have to admit that I did not particularly trust the results and discussion sections, nor spent considerable time on them, simply because they are not well founded.
In Figure 4 for exemple the signals are very patchy and it's difficult to say that weak correlations translate into direct causation. There are a lot of studies on the NA spring bloom that should be cited/explained before suggesting that icebergs drove these trends.
This is a first attempt at addressing a problem that has been mentioned in the literature (Smith et al. 2013), but never approached before. The whole point of Figure 4 is that it suggests a weak, but statistically significant, link between icebergs and chlorophyll. We are not suggesting this is a causal relationship, but merely that the results merit deeper investigation that we then go onto.
The section on fertilization is also weak - when you say fertilization, is it Fe? or is it that the icebergs create local mixing that may bring NO3 up? Please explain. One thing to also highlight here is that not all Fe is bio-available. Plus you need enough Fe binding ligands in seawater to keep this Fe in surface waters. This is where the lag time is a really tricky concept to grasp.
We have already addressed these issues in replies above. We are aware of the bio-availability question – iron is not necessarily the answer to what aspect of an iceberg’s melting assists production and we stress this throughout.
Line 375-376: Is there any obvious trends in that flux? I would have imagined that maybe the flux of icebergs may have significantly increased since 1958. If that’s the case, then this work could become really interesting from a climate change angle, ie. as the polar ice sheet continue to lose mass.
Please see Bigg et al. (2014) for more discussion of the long-term variability of iceberg flux in the NW Atlantic. During the time during which remote sensing data has been available, however, fluxes are highly variable but do not show any clear trend.
The whole section of Fe fluxes to the area needs tightening. Go source by source, using data from the literature to report possible Fe flux to the study area, ideally reported in umol Fe/m2/d. Please check the units and the conversions carefully.
We can be more careful about units. However, please note the intention of the Discussion is to show that Fe might be important from iceberg sources, not to prove it is. More fieldwork and modelling would be required for the latter. This is beyond the scope of our exploratory analysis.
Conclusions:
The conclusions are not really supported by the results. The authors are so keen to draw a line between icebergs and phytoplankton bloom, that they dismiss other possible drivers. This needs rewriting.
The reviewer exaggerates what we are claiming here. As we close by saying: “Smith et al. (2013) speculated that this iceberg effect was likely to exist in the North Atlantic and here we have moved towards confirming its presence. The analysis has also shown that it is possible that it is iceberg-delivered Fe that contributes to this enhanced productivity.” Neither of these statements are decisive and they do not exclude other causal factors, indeed they suggest these are most important. Our final sentence gives the way forward: “However, the suggested enhancement of productivity by icebergs in the highly productive region of the 408 NW Atlantic means that this effect would be worth quantifying.”
Citation: https://doi.org/10.5194/os-2021-61-AC2
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AC2: 'Reply on RC2', Grant Bigg, 20 Oct 2021
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RC3: 'Comment on os-2021-61', Anonymous Referee #2, 23 Sep 2021
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AC3: 'Reply on RC3', Grant Bigg, 20 Oct 2021
Note that this is covered in the reply to RC2
Citation: https://doi.org/10.5194/os-2021-61-AC3
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AC3: 'Reply on RC3', Grant Bigg, 20 Oct 2021
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RC4: 'Comment on os-2021-61', Delphine Lannuzel, 23 Sep 2021
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AC4: 'Reply on RC4', Grant Bigg, 20 Oct 2021
Note that this is covered by the reply to RC2
Citation: https://doi.org/10.5194/os-2021-61-AC4
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AC4: 'Reply on RC4', Grant Bigg, 20 Oct 2021
Status: closed
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RC1: 'Review os-2021-61', Anonymous Referee #1, 30 Aug 2021
Bigg et al., present an analysis of iceberg distribution and chlorophyll analysis in the North Atlantic, investigating the links between iceberg distribution and primary production. The authors use satellite derived chlorophyll a, a historical record of the number of icebergs transported past 48 degrees south ‘I48N’, and a database of iceberg locations on a 1 degree grid resolution. By contrasting the dynamics of chla and iceberg density in a region of interest, and a control region, the authors investigate the role of N Atlantic icebergs in ocean fertilization. The statistical method used to do this, partial correlations, is novel in this context and is argued to show a weak but statistically significant positive effect of icebergs on chlorophyll a with a month time lag between iceberg presence and chlorophyll change. The conclusion of this paper rests heavily on the application of this technique and whether it not it is capable of distinguishing chlorophyll changes driven by iceberg passage from other ‘background’ changes.
I am a chemical oceanographer and thus whilst I’m familiar with the literature on icebergs and the use of satellite derived a, some of the statistical techniques herein are unfamiliar. With editorial consent, I did consult with a colleague concerning these aspects of the manuscript in an oceanographic context.
There are existing iceberg-chlorophyll tracking papers which explicitly show in detail (and test) appropriate statistical methods for assessing whether or not iceberg passage is associated with changes in chlorophyll, (Schwarz and Schodlok, 2009; Wu and Hou, 2017). Both of these works cited contain careful critical assessments of the methods used that robustly test whether or not the presence of an iceberg itself, rather than some coincident factor, is responsible for any associated change in chlorophyll, and whether or not any associated change in chlorophyll is different from background changes in the same region with the same timing. This work is not quite so careful, two obvious points could be raised with the method as described. First, given the technique is completely novel, why not test it in an area where icebergs are thought to have a strong influence based on existing work to see if the technique functions similarly? A different control factor would be required, but if the technique works, it should be possible to apply it to a box in a region where other studies have identified strong relationships between iceberg abundances and chla. The results of such a test would then justify the use of the technique to look for an iceberg influence somewhere more challenging where it would be more difficult to apply well tested techniques. Secondly, concerning the control parameter -the NAO index- used to account for variability due to other causes. It is not really clear to me why the NAO index used as a control parameter? Does this fully account for differences in wind driven mixing, is it completely independent of iceberg density or iceberg arrival within the region of interest? Have other control parameters been tested? Seasonal cycles can, and often do, cause artificially inflated correlations in datasets, so it’s very hard to account for this when making correlations between two seasonally variable parameters. To make a convincing case, as has been done in prior work, I think more testing of this is required, the authors could for example select some completely unrelated, but strongly seasonal, monthly time series around the N Atlantic/Greenland and attempt to do the same analysis. The authors’ case would be more convincing if they could robustly show that the weak correlation the paper hinges on is not spurious. The same comment can be made concerning a comparison between one region of interest and one control region- a comparison to multiple control regions would be more convincing, and I have some concerns about the choice of control region used.
There are also other specific problems with the statistics which I think preclude any conclusions supporting the authors’ hypothesis, particularly concerning a month ‘lag’ effect between iceberg arrival and fertilization. Such an effect is very difficult to explain using the known mechanisms via which icebergs could affect fertilization in this region and its appearance may relate to factors such as a difference in latitude and spring bloom commencement contrasting the control and ROI boxes rather than anything to do with icebergs in the ROI. More obviously, unless I’m mistaken, the control and the ROI boxes appear to be different sizes, thus statements comparing the two in terms of the number of points within each following application of any technique are not mathematically valid. What is the specific rationale for the size and location of the control box? As above, given the novelty of the technique it would have been better to pick multiple control regions, and to specifically find a control region with bloom dynamics the same as the ROI. The authors comment that the mean monthly chla in the control region is not distinguishable from the ROI, but I am not sure exactly what this means as chla data clearly shows that the spring bloom commences and peaks much earlier in the control region than it does in the ROI.
Main points
- I found the manuscript very hard to read, whilst some of the statistics are described in detail, other points (which could be tested statistically) are made as unsupported qualitative statements. For example, it’s not actually clear from reading the text where icebergs are within the ROI, or what the main area receiving iceberg tracks is. The authors refer to this ‘iceberg alley’ several times, so an obvious question is why not define this region and then we can see if there are/aren’t strong correlations specifically for this area of high iceberg tracks? Is the main ‘iceberg alley’ a subregion with the region of interest? Does this correspond to the patch of significant correlation highlighted within the ROI in several figures?
- In several places the statistical analysis and interpretation is flawed. As an example, there are comments related to the number of points within the control and region of interest (ROI), but the ROI is bigger than the control region, so the two cannot be compared directly in terms of number of points. Clustering of points (patchiness) is also described as if it supports the hypothesis, but patchiness is inherent in any random distribution, so the presence or absence of a “coherent area of statistically significant partial correlation” is meaningless in terms of testing the hypothesis unless this cluster corresponds to something quantitatively.
- There is presently a lot of qualitative discussion concerning biogeochemistry, but whilst the authors correctly identify the few known mechanisms that could explain a link between icebergs and primary production (upwelling/mixing or direct nutrient fertilization), they don’t provide any quantitative analysis of existing data to show which is likely to be effective in the North Atlantic. There are a couple of cruises that have iron/macronutrient data for the region and I’m not sure these support the authors’ hypothesis that addition of iceberg-derived-Fe could be increasing primary production. The Fe calculations that are provided seem out of place without commenting on what Fe and nutrient concentrations are in the region of interest and to what extent there could be Fe or nutrient-limitation in the region at the time of year concerned. They also seem circular, the authors summarize that Fe input into the region of interest could be massive compared to dust input (which is generally thought to be the main input by oceanographers), but if this were the case, and the authors’ hypothesis that any iceberg derived nutrients are being mixed in surface waters for a month before driving any increase in chla were correct, surely Fe concentrations across the region would be high and thus small changes in iceberg Fe delivery would not be needed to change primary production (there would be an excess of Fe relative to other nutrients)?
- The timing of the ‘lag’ investigated herein also seems dubious as this is not really consistent with the Fe fertilization discussed. The (Arrigo et al., 2017) reference cited for example shows a rapid effect of meltwater arrival on chla in a specific box off SW Greenland which is interpreted as possibly being Fe fertilization– but this statistic concerns bloom timing not total chla, so the mechanism doesn’t really compare to what the authors discuss herein. Fe cannot be transported long distances at the ocean surface, it is rapidly scavenged and drawn-down by primary producers even in areas where it isn’t considered a limiting nutrient (e.g. see discussion by (Birchill et al., 2017)) so the idea of an Fe plume from icebergs remaining in the ocean during the growth season, having no effect on primary production until one month after it was deposited is implausible. Fe addition experiments usually show a positive fertilization effect after 1-5 days (e.g. see Browning et al., 2019, 2021 in the ROI) consistent with the timing effect suggested off SW Greenland, and similarly where strong Fe fertilization is observed in the Southern Ocean elevated dFe concentrations are only noticeably observed within a few km of icebergs (Lin et al., 2011; Lin and Twining, 2012) with chla changes detected within days (see main comment for papers doing this well).
Line comments:
13-14 This is not really consistent with any known mechanism of iceberg fertilization. If a nutrient required for primary production in the N Atlantic was upwelled or released as the iceberg melted, it would be drawdown much faster than this during the growth season. Fe in particular does not have a long residence time in the ocean surface, especially during the growth season, so it’s not clear to me what this is ‘consistent’ with. It’s quite bizarre and unexpected.
15 By range, I assume the authors mean either upwelling or release from melting ice? So why not just say these two.
33 Do any icebergs from Greenland not enter the North Atlantic? – it would be very useful on some figure to show iceberg tracks, or areas of high iceberg observations as at present it is not clear at all where the icebergs are or where they generally go. Thus it’s very difficult to comment on the validity of the chosen boxes used in all statistics.
40-41 This is not a correct inference. High secondary production, or high abundances of seals/birds/fish etc does not necessarily imply local high primary production. E.g. it’s well documented seals rest on icebergs after sea ice loss, and there is generally a hotspot of feeding activity at glacier termini in the Arctic (Lydersen et al., 2014), but is not because local primary production is high - quite the opposite in this case, these zones have low primary production but the water column disturbances kill /stun prey making convenient hunting grounds. So ‘enriched ecosystem locally’ does not imply iceberg fertilization.
42 The reference cited does not show micronutrient limitation of the Labrador Sea, they suggest Fe limitation could occur in one specific region off SW Greenland, but only at a window between the spring and summer blooms, not across the Labrador Sea during summer as cited. Canadian GEOTRACES data would be better cited here as this shows low-nitrate/low-Fe conditions in summer in the Labrador Sea.
44-45 What iceberg depth / mixed layer depth is being referred to here? Based on the comments on iceberg dimensions herein, I would not expect more than a minority of large icebergs to penetrate the mixed layer depth in the Labrador Sea, only in well stratified coastal regions where the MLD is shallower.
47 Is there data on the nutrient content of icebergs? I would think this was generally very low for more macronutrients but I’m not sure you refer to any data to suggest the contrary. I’m not sure ‘bypasses removal in fjords’ is quote correct. Icebergs are subject to intensive melting in fjords around Greenland, loosing a majority of their volume and sediment, e.g. (Azetsu-Scott and Syvitski, 1999)
51 Raiswell et al,. don’t explicitly show this, I think it is worth asking how much of the iceberg derived sediment is actually exposed to UV light and for how long, a large fraction likely melts and gets deposited in fjords without ever being exposed to sunlight. e.g. above ref shows most of this sediment never enters the ocean surface (Azetsu-Scott and Syvitski, 1999)
52 What mechanism would icebergs promote spring productivity via? There’s no suggestion in the literature, or in this manuscript, of a mechanism via which icebergs could do this in the North Atlantic.
164 I don’t think (Schwarz and Schodlok, 2009) show this, they only test 6 day periods before and after iceberg transit.
176 “little iceberg meltwater” It is not clear to me what this means -melt from icebergs from the point they enter the ocean? Most freshwater from Greenland (which includes most iceberg melt as most of this occurs near-shore largely overlapping with where runoff enters the ocean) is advected counter-clockwise around the Labrador Sea and then follows the Labrador shelf precisely where the authors state there is no impact (?) e.g. see manuscripts modelling this (Luo et al., 2016)
Figure 3. Why are the ocean areas of the control and main regions different? The region of interest looks to be considerably larger than the control region? Several of the comparisons are invalid as there are fewer datapoints in the control region so it is not valid to comment on ‘less/more’ of anything relative to the control region.
187-188 This does not prove causation. What factors lead to high iceberg transfer into this region? These factors likely include wind/current forcing which also affects plankton dynamics. If icebergs did have an impact at this time of year, via what mechanism is this plausible? It is not clear to me what factors the NAO does/doesn’t account for.
191-192 This is not robust if the only test is whether or not correlation with chl is higher than one control region based on the fact that the control region has similar environmental forcing (and see my earlier comment concerning the timing of the spring bloom between the two regions). This should really be done compared to multiple iceberg free regions and ideally in regions with similar bloom dynamics rather than significant temporal offsets in the initiation of the bloom. If it is the case that only the main region of interest has a strong iceberg signal, then this basic statistic (that the correlation between chla in this region, and a control region with similar forcing is stronger in low iceberg years and weaker in high iceberg years) would hold generally with a comparison across all of the adjacent cells. The sensitivity of the statistic to the threshold of 100 should also be shown. Looking at Figure 1 for example, it looks like the best possible fit between spring mean chla and spring I48N would be obtained for the ranges I48N >900, or I48N >200 i.e. a correlation may be very sensitive to what threshold is used just because the dataset is small.
Figure 4 This is not particularly convincing without showing sensitivity analysis. For example, why is there also a positive 2 month threshold for the control region? If I understood correctly, what is shown here is the correlation between a list of numbers (I48N) that show a peak building from march, peaking in May, and then shouldering in July, with chla dynamics. The timing of the spring bloom varies by region/latitude and thus in a correctly selected region, the timing of the spring bloom peak and spring I48N peak will coincide creating a better correlation than is possible in a region where the events don’t coincide temporally. Looking at regional Chla, the spring bloom starts earlier in the control region peaking in April (i.e. too early to match the I48N) peak, whereas the bloom starts later in the region of interest and is more intense. So there is a better temporal overlap between the timing of I48N and the spring bloom in the region of interest. If the control region were instead at the same latitude with the same seasonal timing of the spring bloom, it may no longer be the case that there is a difference between the Person correlations shown. As above, multiple control regions around the ROI would be more convincing.
Figure 5 again shows a correlation between a list of numbers, IT, and local chlorophyll anomalies within small grid cells in the control region and region of interest. In looking at whether there are positive or negative correlations here, the number of cells must be considered. Again, if icebergs had no effect, IT could be considered a random list of numbers, in which case the correlation would be random i.e. equal roughly numbers of positive and negative correlation scattered across the regions. With a p value of 0.05 how many boxes within the regions would show a correlation in such a random scenario? Is this more or less than actually show a correlation? For the amount of grid cells and a p value of 0.05, the displayed data does not appear to show any convincing relationship. It’s hard to comment without knowing the number of grid cells, but from what I can see the balance between positive and negative values and the number of cells picked out by a p value of 0.05 seem to show not much difference from a random distribution.
273 Here and elsewhere the authors comment on the patches of statistically significant correlations, but patchiness would be observed in any random distribution. Do these patches actually correspond to anything meaningful, i.e. can you plot the intensity of iceberg distributions onto cells? If not, this discussion is relatively meaningless concerning Figure 5.
288 But (a) the control region is smaller and (b) randomly dispersed patched would be present in a random distribution. Patchiness is inherent in a random distribution, so patchiness doesn’t make any argument more convincing unless it can be shown quantitatively that the patches mean something i.e. do they correspond to areas with the highest iceberg intensity? As noted above, more correlation between chla and iceberg presence could simply reflect latitude as in the area of interest the timing of the spring bloom is better matched to the timing of iceberg arrival. It would be useful to have control regions distributed around the area of interest, not just one SW of it with an earlier bloom dynamic.
Figure 6. Similar comment to the above statistics. I’m not sure what this really shows, there’s a positive lag effect across the N Atlantic including in the ROI, but also in areas that don’t receive any iceberg influence outside the ROI? The region of interest doesn’t appear to show an iceberg ‘hotspot’ that can be delineated from any other effect, (unless as above the authors can specifically highlight the area of highest iceberg intensity) so I’m not sure this adds any evidence to support the authors hypothesis.
References referred to
Arrigo, K. R., van Dijken, G. L., Castelao, R. M., Luo, H., Rennermalm, Å. K., Tedesco, M., Mote, T. L., Oliver, H. and Yager, P. L.: Melting glaciers stimulate large summer phytoplankton blooms in southwest Greenland waters, Geophys. Res. Lett., 44(12), 6278–6285, doi:10.1002/2017GL073583, 2017.
Azetsu-Scott, K. and Syvitski, J. P. M.: Influence of melting icebergs on distribution, characteristics and transport of marine particles in an East Greenland fjord, J. Geophys. Res., 104(C3), 5321, doi:10.1029/1998JC900083, 1999.
Birchill, A. J., Milne, A., Woodward, E. M. S., Harris, C., Annett, A., Rusiecka, D., Achterberg, E. P., Gledhill, M., Ussher, S. J., Worsfold, P. J., Geibert, W. and Lohan, M. C.: Seasonal iron depletion in temperate shelf seas, Geophys. Res. Lett., 44(17), 8987–8996, doi:10.1002/2017GL073881, 2017.
Browning, T. J., Al-Hashem, A. A., Hopwood, M. J., Engel, A., Wakefield, E. D. and Achterberg, E. P.: Nutrient regulation of late spring phytoplankton blooms in the midlatitude North Atlantic, Limnol. Oceanogr., 65, 1136–1148, doi:10.1002/lno.11376, 2019.
Browning, T. J., AlâHashem, A. A., Hopwood, M. J., Engel, A., Belkin, I. M., Wakefield, E. D., Fischer, T. and Achterberg, E. P.: Iron regulation of North Atlantic eddy phytoplankton productivity, Geophys. Res. Lett., doi:10.1029/2020gl091403, 2021.
Lin, H. and Twining, B. S.: Chemical speciation of iron in Antarctic waters surrounding free-drifting icebergs, Mar. Chem., 128, 81–91, doi:10.1016/j.marchem.2011.10.005, 2012.
Lin, H., Rauschenberg, S., Hexel, C. R., Shaw, T. J. and Twining, B. S.: Free-drifting icebergs as sources of iron to the Weddell Sea, Deep. Res. Part Ii-Topical Stud. Oceanogr., 58(11–12), 1392–1406, doi:10.1016/j.dsr2.2010.11.020, 2011.
Luo, H., Castelao, R. M., Rennermalm, A. K., Tedesco, M., Bracco, A., Yager, P. L. and Mote, T. L.: Oceanic transport of surface meltwater from the southern Greenland ice sheet, Nat. Geosci., 9(7), 528–532, doi:10.1038/ngeo2708, 2016.
Lydersen, C., Assmy, P., Falk-Petersen, S., Kohler, J., Kovacs, K. M., Reigstad, M., Steen, H., Strøm, H., Sundfjord, A., Varpe, Ø., Walczowski, W., Weslawski, J. M. and Zajaczkowski, M.: The importance of tidewater glaciers for marine mammals and seabirds in Svalbard, Norway, J. Mar. Syst., 129, 452–471, doi:10.1016/j.jmarsys.2013.09.006, 2014.
Schwarz, J. N. and Schodlok, M. P.: Impact of drifting icebergs on surface phytoplankton biomass in the Southern Ocean: Ocean colour remote sensing and in situ iceberg tracking, Deep. Res. Part I Oceanogr. Res. Pap., 56(10), 1727–1741, doi:10.1016/j.dsr.2009.05.003, 2009.
Wu, S.-Y. and Hou, S.: Impact of icebergs on net primary productivity in the Southern Ocean, Cryosph., 11(2), 707–722, doi:10.5194/tc-11-707-2017, 2017.
Citation: https://doi.org/10.5194/os-2021-61-RC1 -
AC1: 'Reply on RC1', Grant Bigg, 20 Oct 2021
Reply to Reviewer 1
We welcome the reviewer’s careful analysis of our paper. However, we believe that they have unconsciously exaggerated the confidence of our findings. We are claiming that despite the complexity of the region and its forcing we think there is sufficient evidence to suggest that icebergs probably do have an influence on production in the NW Atlantic, but that this is difficult to isolate. Our paper is a call for more targeted studies to investigate such a link, to confirm or deny our speculative findings. We would be happy to make it clearer that the purpose of the paper is to provide a first analysis of a complex question.
Previous papers investigated the link between icebergs and production have studied the Southern Ocean, where the icebergs are larger and even casual inspection of images of iceberg motion compared to chlorophyll values provides strong suggestion that there is a signal to find. The various papers quoted by the reviewer do indeed carry out very careful analyses but in a region where the circumstantial evidence is stronger, and the database of the location and size data for icebergs is better than available to this paper. The NW Atlantic is a difficult region in which to seek a signal: the main iceberg flux corresponds with the timing of the spring bloom; the concentration in iceberg science there is for protection of shipping; and the region is one with significant climatic and weather variability. This is why we sought to use the novel technique of partial correlation, which is novel in oceanography but used as a standard statistical technique in other fields, as we note in the paper. Because the technique is not novel per se, and the circumstances of the study region are so unique, we did not consider it worth using the approach elsewhere. This could be done, but we do not agree with the Reviewer that this would strengthen our specific analysis.
The reviewer also questions why we used the NAO index as the control variable. We did explore a number of other possible control variables, as mentioned in the paper, however, we found the NAO, as a well used and acknowledged measure of North Atlantic climate variability, gave the strongest correlations. It is not correlated with iceberg numbers (Hanna et al., 2011; Zhao et al., 2016), if indirectly linked to iceberg calving and survival (e.g. Bigg et al., 2014; Zhao et al., 2016; Bigg et al., 2019). This is already referred to in the paper.
The reviewer also questions our control region choice. There are few other options in the region. We needed an area of a similar latitude, close to the coast, so experiencing similar seasonal river fluxes and climate, but not visited by icebergs. Areas north or east of the core region would not be suitable control analogues as they violate one or more of these conditions. We agree that no region would be a perfect control but argue that the region shown in Figure 3 is the best choice, given our core region. We defend our analysis in the paper showing that the mean chl in the control region is significantly correlated with that in the core area.
Addressing main points:
- The reviewer assumes the quality of the iceberg data is much better than it is in reality. We describe the various ways we have tried to reconstruct iceberg data in the paper, but using the basic number data provided by the International Ice Patrol, which includes all icebergs observed out to 35W, restricts options for a large-scale study. A more focused study could look at individual years and individual tracks but the quality and amount of the available data means that this is a task for a next step, rather than the first attempt to examine the question here. The iceberg tracks are sufficiently variable from year to year that we decided not to seek to define a smaller area. If it would help with assessment of the analysis we could provide a map of iceberg density. As an example, the density map for all icebergs observed in the high iceberg year of 2015 is given below. This shows that icebergs are present over much of our core area.
Figure 1: iceberg density map for icebergs seen in our region during the year 2015.
- We are not aware of discussion about “numbers of points” anywhere in the paper. We usually compare mean quantities of areas, whether chlorophyll a or iceberg number, with 1x1 degree fields. We are aware that our mention of clustering of points is not a statistically robust statement as random numbers will cluster, as the review points out. However, the spatial coherence of significance is at times suggestive and it would be remiss not to point this out to the reader.
- We would be happy to remove any discussion about iron in the Discussion. However, the reviewer has not appreciated that this is a “back of the envelope” approach showing that such fertilization by icebergs is not impossible in the NW Atlantic. We do not claim it is occurring. Further fieldwork would be needed to verify this. However, we stand by the spirit of the qualitative discussion given. This is a field that promotes polarization of viewpoints and we do not attempt to join this but merely explore possibilities.
- The Reviewer questions the one month lag suggested between iceberg presence and productivity maxima. This has previously been found in the Antarctic as possible, both for icebergs (Duprat et al., 2016) and for iron-fertilization experiments (e.g. SOFEX). We do not claim to know what drives this, which was a clear signal in the analysis, but present several possibilities linked to ocean circulation. We are not proposing an iron explanation for this phenomenon. More fieldwork is needed to establish the robustness and cause of this phenomenon. Our analysis is only a first step.
Line Comments:
- 13-14: We agree the abstract sentence is misleading. We suggest it is changed to “In addition, a spatial time-lag analysis is consistent with the main cause for the iceberg-chlorophyll relationship being linked to advection of the nutrients entrained in iceberg meltwater.” We stand by the 2-4 week delay found in the analysis, which is consistent with Southern Ocean work, as suggested above.
- 15: we kept the cause vague deliberately, so as not to miss any currently unknown mechanisms.
- 33: Of course not all Greenland icebergs enter the Labrador Current. Probably only a few per cent reach the area of interest (see Marsh et al., 2019). This comment clearly suggests we should add a map of iceberg density in a final paper version (e.g. like Figure 1 above).
- 40/41 & 42: We are happy to omit the inference from higher trophic levels and alter the reference in l. 42.
- 44-45: Much of the region discussed is coastal or on the Grand Banks and so relatively shallow. We can certainly change the statement to make it clear it is larger icebergs that are referred to in terms of causing vertical mixing.
- 47/51: There isn’t much information available on nutrient levels in icebergs but sufficient evidence just from open ocean pictures that some exists (see figures in chapter 2 of Bigg, 2016). We are not questioning that most icebergs don’t escape fjords, but some clearly do (see l. 33 comment above). We are focusing on those that reach the Newfoundland area.
- 52: The reviewer misreads our statement. We merely say the iceberg peak corresponds to the timing of the spring bloom. Nowhere do we say the latter is caused by icebergs. It is this co-incidence of timing that makes our analysis much more difficult.
- 164: We suggest modifying the line to “Remote sensing analysis in the Southern Ocean also suggests that the impact of fertilization from melting icebergs can have a time lag of some days (Schwarz and Schodlock, 2009) to weeks (Duprat et al., 2016).”
- 176: we are referring to meltwater from nearby icebergs clearly. We suggest changing this sentence to “A nearby coastal area, which will experience many of the same environmental forcings as the main area, but which almost no icebergs reach (see Fig. 13 of Wilton et al., 2015), was also defined as a control area.”
Figure 3: the areas are different in size. However, analysis is in terms of comparisons between means. There is no discussion where point numbers play a role in the analysis. Nevertheless, if desired, we could alter the box sizes to make them comparable. Some of the analysis already only goes to 52N, removing 80 grid boxes and making the areas roughly the same.
- 187-188: causation is not intended. We can change the wording to remove this connotation: “The next step is correlating the monthly mean chlorophyll between the control and iceberg areas for just the months during the peak iceberg season of April-June.”
- 191-192: The argument in this whole paragraph is to suggest that the control and main areas do experience different behaviours when icebergs are present in one. It is not definitive, merely suggestive. We could remove the whole paragraph but feel the reader loses some of the rationale behind our thought processes by doing so.
Figure 4: we agree this is not particularly convincing. It is why the analysis then takes on its novel approach, to try to strengthen the hints Figure 4 provided. The reviewer is being too critical of what is clearly the first step of the analysis. Note that the 2 month control area correlation is not statistically significant and we do address this aspect in the text (l. 264-5).
Figure 5: we agree that this is not strong. This fact is why we then go on to the lag study, as is stated in l. 291. This is a difficult problem and unlike some scientific approaches we here show our steps to arrive at the best answer we could with the data available. Science is not perfect and the process of argument reasoning is often not shown. (l. 273 and 288 are also part of the discussion that ends needing to move to a deeper analysis so we will not directly reply to these points)
Figure 6: we feel the Reviewer had decided against the paper’s theme by this point and was not prepared to examine the evidence in Figure 6 – and most importantly the video – in a positive way. We believe Fig. 6 and the video clearly show an increase and movement of regions of positive correlation. We do not claim to know what causes this but the Discussion attempts to address this question. The answer awaits further work.
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RC2: 'Comment on os-2021-61', Delphine Lannuzel, 23 Sep 2021
Review - Evidence for iceberg fertilization of the NW Atlantic
General comment:
The North Atlantic basin bloom has been widely studied, as far back as 1950s with Sverdrup testing his critical depth theory using Spring bloom data. This initial theory has since be challenged with work from Siegel et al 2002 and Behrenfeld a few years later. Nitrate is generally the main limiting nutrient in the North Atlantic since the Sarahan dust supplies enough Fe to surface waters for it not to be limiting. Iron can however sometimes be found at levels too low to support marine productivity, as shown in papers from Rijkenberg et al 2014 and Achterberg et al., 2018.
The Ice Sheets have been recognised as important sources of trace elements to the polar seas, with potentially a significant contribution to the global carbon sequestration. In the Southern Ocean the fertilization effect from large icebergs on local surface productivity can be seen from satellites recording ocean colour. In the North Atlantic, some work by Smith et al 2013 and others suggests that icebergs from the Greenland ice sheet may well play a role in boosting local productivity and this is the hypothesis that the authors are aiming to test here.
I think that topic is extremely interesting, whether the hypothesis is proven right or wrong. However I find the manuscript hard to follow and the execution not very convincing, which is unfortunate. I suggest below some different ways to appraoch the work and I hope you find some of my comments useful.
Introduction:
The introduction is needs to be approached differently. I would instead use the following structure: 1/ Known drivers are of the NA bloom. you can go as far back as Sverdrup 1953, then Siegel et al 2002, then Berehnfeld. Here what is important is a critical assessment of the role of the wind mixed layer depths and light in initiation of the blooms. The Siegel et al 2002 is especially key since it covers the area of interest that this paper focuses. Do note that 71 - 87% of Fe in NA comes from dust (from Sahara). 2/a section on macronutrients and Fe limitation in the NA, referring to the RijkenBerg work, then 3/ your hypothesis: icebergs may supply additional Fe to a localised region of the NA.
Note that lines 53-61 are already results/discussion and need to be removed.
Figure 1 needs work: a)we need lat/long and main landmarks. It would also be good to see the limits of the study area for satellite derived ocean color analysis, as well as detailed bathymetry. Here for exemple it looks like the enhanced Chla areas match shallow bathymetry, which makes sense. ie. coastal waters being more productive than offshore waters (from upwelling and/or local eddies). b) is confusing. The reader is not quite sure what they’re looking at. I would remove it
Methods:
The Methods are confusing as they currently stand. The way I would approach the study is by comparing the climatology of Chla vs frequency of icebergs transiting through the study area. ie. in years that we have higher occurence of icebergs passing through the study area, do we see anomalies in Chla records? You could stick to the bloom period, ie. April-May. and secondly are these positively and significantly correlated? I would set the scene that way lines 74-80, then explain how the Chla and icebergs data were obtained. One point to emphasize is that the data does not report size, which I think is key. ie. small icebergs are unlikely to alter the area of interest as much as a giant iceberg would.
I would move lines 75-80 to the "iceberg data" subsection, and 80-83 to the Chla subsection.
Line 82: Also it would be worth mentioning that polar areas are quite tricky with ocean colour - clouds decrease data coverage and large solar zenith angles can lead to an underestimation of the in situ chlâa - see Sirjacobs et al., 2011.
Line 88: Please define the box/area of study as xx–xx°N and xxx–xxx°W - we need the same spatial limits for Chla and icebergs analysis otherwise we're comparing apples and pears
Line 92-94: Before applying the standardisation did you test the difference between MODISâAqua and SeaWiFS values in the area when co-located data are available. ie. what is the mean difference between the 2 products for your study area, and is this different statistically?
Line 101-103: Here instead you should record the flux of icebergs transiting through the defined study area from any direction - ie. why 48N? and where it that relative to the study area? We really need lat/long on Figure 1.
Line 163: this is a Southern Ocean reference
Line 165: is it really a time lag, or that the fertilisation effect can last for weeks? in the case of Fe, there is no way that this Fe would stay in surface waters for that long. Nitrate might (not that I have any references to support this statement), but not Fe. This idea is carried through the whole manuscript yet I cannot wrap my head around such a long Fe residence time.
Line 175-177: I am not fond of this approach. Region A is influenced by coastal processes, which is not the case for the "iceberg" region. What I would do instead is simply run a climatology of the iceberg area as I suggested above. ie. do you see enhanced (above average) Chla the years that more icebergs transit through the area? noting that other processes (large scale weather forcings like NAO, eddies) may explain any anomalies in surface Chla
Figure 3: Again here, if you superpose bathymetry I think that you will see that the control area and iceberg area have completely different bathymetry, therefore physical and chemical settings.
Line 181-192: The drivers of the blooms will be different, even though you may have a similar end results. To really nail this down, you would need to run a climatology of bloom start, bloom end and bloom amplitude (and max) in both regions (see Arctic and Antarctic phytoplankton bloom phenology studies). Check e.g., / bathymetry, 2/wind mixed layer depths, 3/Sea surface height (i.e do you have eddies?), or as studied later the NAO.
If results are exactly the same then maybe yes you can say the 2 areas undergo similar environmental conditions (before adding icebergs influence to the mix). But at the moment, the approach is not rigorous enough.
Line 199-204- remove this text
Line 207: I am struggling with this section - I don't think that this approach holds particularly well - Why would you expect a temporal decoupling between icebergs passing and the Chla anomaly? Please explain, set the scene for the reader.
Results & Discussion:
Given the lack of rigorous approach to the study I have to admit that I did not particularly trust the results and discussion sections, nor spent considerable time on them, simply because they are not well founded.
In Figure 4 for exemple the signals are very patchy and it's difficult to say that weak correlations translate into direct causation. There are a lot of studies on the NA spring bloom that should be cited/explained before suggesting that icebergs drove these trends.
The section on fertilization is also weak - when you say fertilization, is it Fe? or is it that the icebergs create local mixing that may bring NO3 up? Please explain. One thing to also highlight here is that not all Fe is bio-available. Plus you need enough Fe binding ligands in seawater to keep this Fe in surface waters. This is where the lag time is a really tricky concept to grasp.
Line 375-376: Is there any obvious trends in that flux? I would have imagined that maybe the flux of icebergs may have significantly increased since 1958. If that’s the case, then this work could become really interesting from a climate change angle, ie. as the polar ice sheet continue to lose mass.
The whole section of Fe fluxes to the area needs tightening. Go source by source, using data from the literature to report possible Fe flux to the study area, ideally reported in umol Fe/m2/d. Please check the units and the conversions carefully.
Conclusions:
The conclusions are not really supported by the results. The authors are so keen to draw a line between icebergs and phytoplankton bloom, that they dismiss other possible drivers. This needs rewriting.
Citation: https://doi.org/10.5194/os-2021-61-RC2 -
AC2: 'Reply on RC2', Grant Bigg, 20 Oct 2021
Reply to Reviewer 2
We welcome the reviewer’s careful reading of our paper. However, as with Reviewer 1, we believe that they have unconsciously exaggerated the confidence of our findings. We are claiming that despite the complexity of the region and its forcing we think there is sufficient evidence to suggest that icebergs probably do have an influence on production in the NW Atlantic, but that this is difficult to isolate. In other words, chlorophyll peaks have a range of causes, as the Reviewer rightly points out in their overview of the subject at the beginning of the review, but we are only proposing that an iceberg influence is discernible, rather than dominant, or even important. Our paper is more a call for targeted studies to investigate such a link, to confirm or deny our speculative findings. We would be happy to make it clearer that the purpose of the paper is to provide a first analysis of a complex question.
The introduction is needs to be approached differently. I would instead use the following structure: 1/ Known drivers are of the NA bloom. you can go as far back as Sverdrup 1953, then Siegel et al 2002, then Berehnfeld. Here what is important is a critical assessment of the role of the wind mixed layer depths and light in initiation of the blooms. The Siegel et al 2002 is especially key since it covers the area of interest that this paper focuses. Do note that 71 - 87% of Fe in NA comes from dust (from Sahara). 2/a section on macronutrients and Fe limitation in the NA, referring to the RijkenBerg work, then 3/ your hypothesis: icebergs may supply additional Fe to a localised region of the NA.
We would be happy to rewrite the Introduction towards the approach suggested, however, it does change the purpose of the paper to be explicitly about what explains chlorophyll behaviour in the NW Atlantic. This is changing the intention beyond what the paper is trying to do, which is see whether there is any evidence for icebergs to influence productivity in the North Atlantic as it is known to do in the Southern Ocean.
Note that lines 53-61 are already results/discussion and need to be removed.
These lines are helping to set the scene for the discussion in the paper and so pertinent to the Introduction. We think the focus of the paper would be lost by removing this text.
Figure 1 needs work: a)we need lat/long and main landmarks. It would also be good to see the limits of the study area for satellite derived ocean color analysis, as well as detailed bathymetry. Here for exemple it looks like the enhanced Chla areas match shallow bathymetry, which makes sense. ie. coastal waters being more productive than offshore waters (from upwelling and/or local eddies). b) is confusing. The reader is not quite sure what they’re looking at. I would remove it
Figure 1 could be improved by adding bathymetry and more labelling. Part b is not confusing – it shows very clearly that there is no strong link between the established measure of iceberg numbers in the region and chlorophyll levels during the peak iceberg season. It clearly shows that icebergs are not the dominant cause of variability in chlorophyll and that we need to look deeper to seek what influence they do have.
Methods:
The Methods are confusing as they currently stand. The way I would approach the study is by comparing the climatology of Chla vs frequency of icebergs transiting through the study area. ie. in years that we have higher occurence of icebergs passing through the study area, do we see anomalies in Chla records? You could stick to the bloom period, ie. April-May. and secondly are these positively and significantly correlated? I would set the scene that way lines 74-80, then explain how the Chla and icebergs data were obtained. One point to emphasize is that the data does not report size, which I think is key. ie. small icebergs are unlikely to alter the area of interest as much as a giant iceberg would.
The Reviewer is recommending we swap the initial results to become a motivator for the methods used. While we can see this argument, isn’t that what Fig. 1b has already done? We prefer to leave the order of the methods as it is.
I would move lines 75-80 to the "iceberg data" subsection, and 80-83 to the Chla subsection.
We were trying to say there were issues with both main data sources for our analysis. The respective texts could be moved as suggested.
Line 82: Also it would be worth mentioning that polar areas are quite tricky with ocean colour - clouds decrease data coverage and large solar zenith angles can lead to an underestimation of the in situ chlâa - see Sirjacobs et al., 2011.
This is a helpful suggestion and can be added in a revision.
Line 88: Please define the box/area of study as xx–xx°N and xxx–xxx°W - we need the same spatial limits for Chla and icebergs analysis otherwise we're comparing apples and pears
This can be added, although note that we obtained much more of the North Atlantic surface with the chlorophyll data than icebergs, to be able to compare within iceberg-influence areas from non-iceberg areas.
Line 92-94: Before applying the standardisation did you test the difference between MODISâAqua and SeaWiFS values in the area when co-located data are available. ie. what is the mean difference between the 2 products for your study area, and is this different statistically?
We did look at the difference and found it small but non-zero. We can give values in a revision.
Line 101-103: Here instead you should record the flux of icebergs transiting through the defined study area from any direction - ie. why 48N? and where it that relative to the study area? We really need lat/long on Figure 1.
We agree we should show 48N on Figure 1 – it is level with the southern coast of Newfoundland approximately. Icebergs are largely taken through the study area by the Labrador Current along the western shore of the Atlantic basin, so an east-west line is most sensible for this analysis (and has been the standard used by the International Ice Patrol for over 100 years). A map of iceberg density could be shown, as was also suggested by reviewer 1 (please see Figure 1 from the reply to this reviewer).
Line 163: this is a Southern Ocean reference
Wording here can be altered to make it clear we are seeking information from a Southern Ocean source. This is where the vast majority of iceberg analysis has originated.
Line 165: is it really a time lag, or that the fertilisation effect can last for weeks? in the case of Fe, there is no way that this Fe would stay in surface waters for that long. Nitrate might (not that I have any references to support this statement), but not Fe. This idea is carried through the whole manuscript yet I cannot wrap my head around such a long Fe residence time.
There have been few in-situ observations so the answer to this question is unknown. However, it is well established that fertilization effects after iceberg passage in the Southern Ocean are visible for up to several weeks. There may be a range of causes: direct input of nutrients/trace nutrients from melting icebergs; enhanced vertical mixing of nutrients from below the surface in meltwater plumes; slow mixing of initial localised concentrations to larger areas; a requirement for time to pass for the conjunction of light, nutrients, currents and chlorophyll growth to occur. It is not the aim or purpose of this paper to explain the time delay, but to present it. See l. 354-359 for a discussion of this point.
Line 175-177: I am not fond of this approach. Region A is influenced by coastal processes, which is not the case for the "iceberg" region. What I would do instead is simply run a climatology of the iceberg area as I suggested above. ie. do you see enhanced (above average) Chla the years that more icebergs transit through the area? noting that other processes (large scale weather forcings like NAO, eddies) may explain any anomalies in surface Chla
The suggested approach was already presented in Figure 1b – this is not enough to demonstrate any link that might occur between iceberg numbers and chlorophyll
Figure 3: Again here, if you superpose bathymetry I think that you will see that the control area and iceberg area have completely different bathymetry, therefore physical and chemical settings.
No control area is perfect. However, both areas have significant coastal regions, areas with significant riverine fluxes and also areas of deep water. Both also cross the Gulf Stream, so contain some polar-source water and sub-tropical source water. The reader also needs to note this approach begins the analysis but does not drive it beyond the starting analysis.
Line 181-192: The drivers of the blooms will be different, even though you may have a similar end results. To really nail this down, you would need to run a climatology of bloom start, bloom end and bloom amplitude (and max) in both regions (see Arctic and Antarctic phytoplankton bloom phenology studies). Check e.g., / bathymetry, 2/wind mixed layer depths, 3/Sea surface height (i.e do you have eddies?), or as studied later the NAO.
We agree with the reviewer about the diversity of causes of blooms. However, the paper is not about untangling this question in the NW Atlantic but about trying to see whether icebergs are a non-trivial factor that has previously been neglected.
If results are exactly the same then maybe yes you can say the 2 areas undergo similar environmental conditions (before adding icebergs influence to the mix). But at the moment, the approach is not rigorous enough.
This is just the first step of the analysis, and the approach suggested would distort the direction of the paper’s argument.
Line 199-204- remove this text
We do not understand this comment. Surely we need to show the novel approach of partial correlations used here is an established technique in the wider fields of science?
Line 207: I am struggling with this section – I don’t think that this approach holds particularly well – Why would you expect a temporal decoupling between icebergs passing and the Chla anomaly? Please explain, set the scene for the reader.
We explain above why there might be a time lag. This is a well established observed fact in the Southern Ocean.
Results & Discussion:
Given the lack of rigorous approach to the study I have to admit that I did not particularly trust the results and discussion sections, nor spent considerable time on them, simply because they are not well founded.
In Figure 4 for exemple the signals are very patchy and it's difficult to say that weak correlations translate into direct causation. There are a lot of studies on the NA spring bloom that should be cited/explained before suggesting that icebergs drove these trends.
This is a first attempt at addressing a problem that has been mentioned in the literature (Smith et al. 2013), but never approached before. The whole point of Figure 4 is that it suggests a weak, but statistically significant, link between icebergs and chlorophyll. We are not suggesting this is a causal relationship, but merely that the results merit deeper investigation that we then go onto.
The section on fertilization is also weak - when you say fertilization, is it Fe? or is it that the icebergs create local mixing that may bring NO3 up? Please explain. One thing to also highlight here is that not all Fe is bio-available. Plus you need enough Fe binding ligands in seawater to keep this Fe in surface waters. This is where the lag time is a really tricky concept to grasp.
We have already addressed these issues in replies above. We are aware of the bio-availability question – iron is not necessarily the answer to what aspect of an iceberg’s melting assists production and we stress this throughout.
Line 375-376: Is there any obvious trends in that flux? I would have imagined that maybe the flux of icebergs may have significantly increased since 1958. If that’s the case, then this work could become really interesting from a climate change angle, ie. as the polar ice sheet continue to lose mass.
Please see Bigg et al. (2014) for more discussion of the long-term variability of iceberg flux in the NW Atlantic. During the time during which remote sensing data has been available, however, fluxes are highly variable but do not show any clear trend.
The whole section of Fe fluxes to the area needs tightening. Go source by source, using data from the literature to report possible Fe flux to the study area, ideally reported in umol Fe/m2/d. Please check the units and the conversions carefully.
We can be more careful about units. However, please note the intention of the Discussion is to show that Fe might be important from iceberg sources, not to prove it is. More fieldwork and modelling would be required for the latter. This is beyond the scope of our exploratory analysis.
Conclusions:
The conclusions are not really supported by the results. The authors are so keen to draw a line between icebergs and phytoplankton bloom, that they dismiss other possible drivers. This needs rewriting.
The reviewer exaggerates what we are claiming here. As we close by saying: “Smith et al. (2013) speculated that this iceberg effect was likely to exist in the North Atlantic and here we have moved towards confirming its presence. The analysis has also shown that it is possible that it is iceberg-delivered Fe that contributes to this enhanced productivity.” Neither of these statements are decisive and they do not exclude other causal factors, indeed they suggest these are most important. Our final sentence gives the way forward: “However, the suggested enhancement of productivity by icebergs in the highly productive region of the 408 NW Atlantic means that this effect would be worth quantifying.”
Citation: https://doi.org/10.5194/os-2021-61-AC2
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AC2: 'Reply on RC2', Grant Bigg, 20 Oct 2021
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RC3: 'Comment on os-2021-61', Anonymous Referee #2, 23 Sep 2021
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AC3: 'Reply on RC3', Grant Bigg, 20 Oct 2021
Note that this is covered in the reply to RC2
Citation: https://doi.org/10.5194/os-2021-61-AC3
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AC3: 'Reply on RC3', Grant Bigg, 20 Oct 2021
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RC4: 'Comment on os-2021-61', Delphine Lannuzel, 23 Sep 2021
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AC4: 'Reply on RC4', Grant Bigg, 20 Oct 2021
Note that this is covered by the reply to RC2
Citation: https://doi.org/10.5194/os-2021-61-AC4
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AC4: 'Reply on RC4', Grant Bigg, 20 Oct 2021
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