A 2700-year annual timescale and accumulation history for an ice core from Roosevelt Island, West Antarctica

Winstrup, Mai; Vallelonga, Paul; Kjær, Helle A.; Fudge, Tyler J.; Lee, James E.; Riis, Marie H.; Edwards, Ross; Bertler, Nancy A. N.; Blunier, Thomas; Brook, Ed J.; Buizert, Christo; Ciobanu, Gabriela; Conway, Howard; Dahl-Jensen, Dorthe; Ellis, Aja; Emanuelsson, B. Daniel; Hindmarsh, Richard C. A.; Keller, Elizabeth D.; Kurbatov, Andrei V.; Mayewski, Paul A.; Neff, Peter D.; Pyne, Rebecca L.; Simonsen, Marius F.; Svensson, Anders; Tuohy, Andrea; Waddington, Edwin D.; Wheatley, Sarah

doi:https://doi.org/10.5194/cp-15-751-2019

Articles | Volume 15, issue 2

https://doi.org/10.5194/cp-15-751-2019

© Author(s) 2019. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/cp-15-751-2019

© Author(s) 2019. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 15, issue 2

Research article

|

10 Apr 2019

Research article |

| 10 Apr 2019

A 2700-year annual timescale and accumulation history for an ice core from Roosevelt Island, West Antarctica

Mai Winstrup, Paul Vallelonga, Helle A. Kjær, Tyler J. Fudge, James E. Lee, Marie H. Riis, Ross Edwards, Nancy A. N. Bertler, Thomas Blunier, Ed J. Brook, Christo Buizert, Gabriela Ciobanu, Howard Conway, Dorthe Dahl-Jensen, Aja Ellis, B. Daniel Emanuelsson, Richard C. A. Hindmarsh, Elizabeth D. Keller, Andrei V. Kurbatov, Paul A. Mayewski, Peter D. Neff, Rebecca L. Pyne, Marius F. Simonsen, Anders Svensson, Andrea Tuohy, Edwin D. Waddington, and Sarah Wheatley

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Final revised paper (published on 10 Apr 2019)
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Preprint (discussion started on 28 Aug 2017)
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Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review of Winstrup et al. 2017', Anonymous Referee #1, 11 Oct 2017
- AC1: 'Response to reviewer 1', Mai Winstrup, 08 Jun 2018
RC2: 'Review of « A 2700 year annual timescale and accumulation history for an ice core from Roosevelt Island, West Antarctica »', Anonymous Referee #2, 23 Oct 2017
- AC2: 'Response to reviewer 2', Mai Winstrup, 08 Jun 2018
- AC4: 'Author response to editor and reviewers', Mai Winstrup, 11 Jun 2018

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (13 Jun 2018) by Marit-Solveig Seidenkrantz

AR by Mai Winstrup on behalf of the Authors (30 Sep 2018) Author's response Manuscript

ED: Reconsider after major revisions (05 Oct 2018) by Marit-Solveig Seidenkrantz

AR by Paul Vallelonga on behalf of the Authors (06 Oct 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (08 Oct 2018) by Marit-Solveig Seidenkrantz

RR by Anonymous Referee #3 (01 Nov 2018)

Suggestions for revision or reasons for rejection

The paper estimates a record of snow accumulation for the last 2,700 years at Roosevelt Island, Antarctica. The record shows a decrease in accumulation since the mid-1960s that Bertler et al (2018) relate to an increase in sea ice extend.

The authors extract the information from an ice core following two main steps:
- Obtaining a detailed chronology that combines annual-layer counting, that follows the seasonality traces of a few chemical constituents, and a few historical constrains, like well dated volcanic eruptions.
- Estimating the past-accumulation records from the thickness of annual layers. For this, the authors have to estimate the influence of ice-flow from the time of deposition on the surface to the present: compaction from snow to ice, and compression.

In general, the document is clear and well written. I find a strong difference in level of detail between the sections related to ice-core analysis and establishing a chronology, and the sections related to ice-flow and deriving an accumulation record. More of that later.

I am not an expert on ice-core analysis so I will only say that the description of the methods in those sections reads well and they seem to be referenced. I have however serious concerns related to the reconstruction of past accumulation rates. I will group my concerns in terms of clarity, methodology and uncertainty.

Clarity
Sections 5.2 and 5.3 are simply not clear. Technical terms are not explained or referenced. For example: Raymond stack, divide migration, divide/flank flow transitional type flow or thinning function.
A few important steps are not described or referenced. For example:
-How do the authors extract the information about the divide migration from the radar stratigraphy.
-How do they derive the thinning function from a vertical velocity that varies in depth and in time.
-How do they calculate the present surface thinning. The authors state that they use an ice-flow model to match the dated architecture of the Raymond stack. What ice-flow model? 1D, 2D? Using the velocity profile that they describe below and the time-varying vertical velocity implied by the time-varying accumulation?

Methodology
It is difficult to assess the quality of the methods without fully understanding them. However I want to make a few points with my current understanding of the methods but, in any case, the authors should discuss these points further.

-Divide Migration. The authors make a strong assumption about a divide migration of 500m amplitude between 500yr and 250yr ago. It has a strong effect on accumulation records, particularly when combined with the arbitrary vertical velocity profile assumed. I believe this is the main difference between the accumulation records between the initial and the revised version of the manuscript. ‘The correction’.
The authors assume that this should be evident by looking at Figure 6c. I disagree. In this particular case, we have radar-derived englacial strain-rates (Kingslake et al, 2014; Fig. 6b). The stronger near surface strain-rates are indicating where the weak strain-rates near the bed are at the present. Curiously enough, that area coincide in Figure 6b with the location of the Raymond stack. This shows that a) no migration has occurred as present Raymond area is on top of the bottom-most Raymond bumps and the tilt in Raymond stack is consequence of other factors, or b) the divide has gone back and forth recently. In any case, it is not evident what the authors are assuming and I have bough a new argument to the table.

-Vertical velocity at the divide. The authors assume that the ice-core site is currently at the divide position and they assume that that corresponds with the divide-type velocity (p=-1.22 in this paper; p=-0.78 in Kingslake et al (2014)). However a close inspection to Figure 6b reveals that the ‘divide flow’ in Figure 4 of Kingslake et al (2014) and Figure 6a in this paper is taken from about 500m east in the Figure of the summit position (green marker in Kinslake et al 2014). This position corresponds currently with the bottom-most position of the Raymond stack and not the ice-core location. This raises an important concern as, in summary, they are assuming that for the last 250yr the strain-rates are distributed following a distribution that does not correspond with the current conditions at the ice core site.

-Vertical velocity at the flank. The authors use an arbitrary combination of two measured vertical velocities. From a combination of 0.7 this and 0.3 of that. Why? There is no explanation and it has a strong impact on the results before 250yrs ago.

-Combination of flank/divide velocities. I have argued that I don’t think there is a migration. However, even in that case, why do the authors use the wrong shape functions? There are, according to Kingslake et al (2014), 35 englacial profiles at Roosevelt Island, one of them is really close to the ice-core site. Wouldn’t it make sense to use the englacial velocity from the site that is closest to the ice-core site?

-Vertical velocity to thinning function. I mentioned earlier that the authors do not explain how do they calculate the thinning function. I just want to highlight here that this is not a trivial point as thinning function includes the cumulative effect of vertical compression from the surface that, in turn, depends on the time-varying accumulation that is unknown (e.g., Parrenin et al (2007) suggest an iterative method). The authors however assume a vertical velocity related to present values of surface accumulation and a varying shape function.

Uncertainty.
It is difficult for me to predict the cumulative effect of all the factors I have just mention but, independently of them, the propagation of uncertainty has to be improved.
- I see no problem with the paper showing a favourite hypothesis, a divide migration, but the uncertainty should cover other other hypothesis: from no migration to a more recent migration. All this should be covered by repeating the estimation of accumulation with flank and divide velocities and showing them as two extreme cases within a range of scenarios.
- Also, I reiterate that I don’t know how the authors estimate the thinning function. However, they should include in the uncertainty the effect of assuming constant the present accumulation rate and thinning rate in the derivation of the time-dependent accumulation. The authors currently estimate sensitivity by comparing the effect of assuming (0.24+0.02) m/yr with 0.24 m/yr. My view is that this is a clear underestimation of uncertainty. It should include, at least, the variability of the derived accumulation records through the time of interest, around 0.2m/yr to 0.28m/yr, to capture the uncertainty induced by this assumption.

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RR by Anonymous Referee #4 (13 Nov 2018)

Suggestions for revision or reasons for rejection

Review of revised manuscript "A 2700-year annual timescale and accumulation history for an ice core from Roosevelt Island, West Antarctica" by Mai Winstrup et al.

In their revised manuscript the authors made a serious effort to address the issues raised in the first round of reviews. The manuscript has been restructured for clarity and several potential sources of misunderstanding have been eliminated. In particular the independence of the RICE17 age scale w.r.t the WAIS Divide ice core chronology is now made clear. Likewise the manuscript benefits from several related publications now being published or accessible in their discussion stage. This especially concerns the companion paper of Lee et al.
However, there are still two fundamental issues to be fully resolved before the manuscript can be considered for final publication in CP.

1. The automated annual layer counting by the StratiCounter algorithm is the backbone of the RICE17 chronology, but the authors provide no evidence of its performance in identifying annual layers, especially for the deeper and more thinned core sections. At present, the manuscript only contains one figure (Fig. 4) showing the manual assignment of annual layers in a very shallow section of the core, which is not enough. A separate figure would be needed showing exemplarily the automated layer identification. Of special interest here would be the depth section that has been manually counted to initialize the algorithm, as well as part of the deep sections with thinned layers.
As an added benefit, such a figure would also provide evidence of how clear an annual signal can be counted in the various proxies - here referring to the discussion in the first round of reviews about using BC vs. H+ for counting.
Although the main text would be adequate, I suppose the figure could also be placed in the supplement part S2 if the authors would not like to further increase the volume of the main manuscript.

2. The volcanic identification and matching against WAIS remains elusive to me and needs to be clarified further. The detection of a presumably volcanic signal in the various proxies seems to rest on manually selecting even small peaks in the signals. The manual approach appears somewhat arbitrary by comparison to the automated annual layer counting procedure. This is especially so since the authors are aware of the difficulties associated with the high background of non-volcanic sulphur/sulfate and acidity and state to have removed a number of peaks previously considered as volcanic markers. At present, it appears questionable and unclear from the manuscript how reliably volcanic signals are in fact recorded at RICE. Hence, selecting volcanic signals would benefit from a more quantitative detection technique, or at least from employing clearly stated criteria.
The development of the non-sea-salt conductivity (nss-cond) may provide remedy in this context, but is not convincingly shown to record volcanic signals. For instance, Figure 9 shows three distinct peaks in nss-cond (around 162, 164 and 168 m RICE depth). The other match points, however, have little or no sign of a peak, including the Pleiades tephra horizon. There is an additional peak around 169 m not considered. Moreover, judging from Figure 9 the signals of H+ and ECM appear to perform equal or even better (less noise) in indicating peaks at the presumed volcanic markers - which would argue against the need to use nss-cond. Based on Figure 9, I am not convinced that the acidity signal provides more information than the nss-S signal, other than its higher depth resolution.
The authors are aware of potential pitfalls associated with nss-cond calculated as a secondary quantity, but do not quantify how much (or how little) the signal is affected by these problems. For example, this concerns potential false peaks produced by uncertainty in depth-alignment between Cond and Ca++, as well as peaks through very low Ca++.
Consequently, I believe the volcanic identification and matching needs to be expanded and clarified, ideally including: i) a quantitative approach to peak detection, e.g. by employing a local "peak-over-threshold" criterion, ii) a more convincing demonstration of the new volcanic proxy nss-cond, including addressing the pitfalls of a secondary quantity, and iii) showing a more extended version of Figure 9 as a side-by-side comparison between RICE and WAIS volcanic signals, also at depths not including the distinct tephra marker of Pleiades.

Detailed comments:

Introduction: The companionship to the Lee et al. paper should be mentioned explicitly when stating the scope of this work.

P6 L37-38: " Some uncertain layers were counted as a year in the timescale, while others were not."
This procedure remains unclear. As I am sure the authors are aware, a typical approach here is to count uncertain layers as 0.5+/-0.5 years. Why was this procedure not adopted in this case? It is also not clear what uncertainty estimate was obtained and why this should be a 95% confidence interval.

P8 L5-6: "The calcium and conductivity records frequently displayed multiple peaks per year, limiting their contribution to the annual layer interpretations."
This is another reason why it would be very important to see the performance of StratiCounter in such a case.

P8 L20-23: "Using ... the modelled density profile fits well the observed values".
How were the parameters used here obtained, i.e. why these values selected?
Also, from Figure S2 it can be seen that this statement is true only for the top 50 m. Below that depth there is a substantial misfit in the lower core - including depth of the firn-ice transition. This should at least be mentioned - I assume consequences of the misfit would be negligible if only an extrapolation of near-surface values was concerned.

P9 L15: "estimated using an ice-flow model to match the dated architecture of the Raymond stack"
This is rather vague. What ice-flow model was used? Is this work done by the authors or the approach of Kingslake et al. (2014)? Please clarify.

P9 L19-20: "a linear combination with divide-type velocities weighted by 0.7 and flank-type velocities weighted by 0.3."
Please state why these values were used. Was this an arbitrary selection? If so, would uncertainty in these values contribute to the uncertainty in thinning function? This approach remains unclear.

P9 L29-30: "Except for the uppermost part of the record, uncertainty in the thinning function dominates the total uncertainty, and only this factor will be considered here."
This is an important statement but is not supported by any evidence. Please explain.

P9 L31 ff: This paragraph has some vague statements making it hard to fully comprehend. E.g. Was the near-surface uncertainty in density (it is only extrapolated) considered here? And: "(b) variation of the vertical velocity profile over time in ways not accounted for." E.g. I assume you are referring here to your change in weights of the linear combination?

P10 L3-4: "We suggest to interpret this uncertainty as a 95% (2σ) confidence interval."
It is not clear why this needs to be exactly a 95% confidence level, or why this confinement to 95% is even needed.

P10 L13-14: "The CFA acidity record is driven primarily by the influx of non-sea-salt sulfur-containing compounds, as evident by its high resemblance to the IC non-sea-salt sulfate and ICP-MS non-sea-salt sulfur records in the top part of the core (Fig. 4)."
This may be true, but how can it be reconciled with the later statements about using acidity as a more reliable tracer of volcanic events, e.g. the statements about halide acids from regional volcanism? See comment for P19 L23 below.

P10 L28 and L33: Should be now Figure 9, not 8.

P13 L24: Please give a definition of how the conductivity-to-calcium excess was calculated.

P13 L27-28: "Nevertheless, peaks in the conductivity-to-calcium excess showed high consistency with peaks in total acidity, and it proved to be a reliable tracer for volcanic activity."
Referring to main comment 2., this needs to be shown in more convincing detail. For instance, how does the excess signal look for the recent historical eruptions used in the paper, such as Krakatau?

P13 L36: The Kalteyer, 2015 reference is not accessible without a login from the University of Maine.

P14 L44: "Fig 9a" should be Figure 10.

P15 L40: "It has been suggested that this shift is due to other factors than temperature (Bertler et al., 2018),..."
Vague statement, please clarify what "other factors" are.

P16 L35-36: "Present accumulation rates show a distinct decrease on the downwind (western) side of the ice divide with a gradient of ~5 10-3 m w.e./km yr-1, although muted around the summit area."
Where does this data come from? Is there a missing citation?

P19, L23 ff. "The halide acids are highly soluble, and will be removed from the atmosphere relatively quickly during transport. Hence, they will contribute to increased ice acidity in ice cores located close to the eruption site, whereas only sulfate is deposited from distant volcanic eruptions. By focusing on acidity as volcanic tracer instead of sulfur, the RICE volcanic proxies may thus be more sensitive to regional volcanism than to larger far-field eruptions."
As pointed out above, if acidity is dominated by non-sea-salt sulfur as claimed earlier in the manuscript, how would additional, presumably volcanic acids, leave a detectable imprint? In other words, if the H+ data shown in Figure 9 would be down-sampled to the depth-resolution of nss-S shown in the same Figure, would there be in fact a discernible difference between the two datasets, especially at the locations of the assumed eruptions? The reader is unable to evaluate this based on the presented data in Figure 9.

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ED: Reconsider after major revisions (13 Nov 2018) by Marit-Solveig Seidenkrantz

AR by Mai Winstrup on behalf of the Authors (15 Feb 2019) Author's response Manuscript

ED: Publish as is (20 Feb 2019) by Marit-Solveig Seidenkrantz

Short summary

We present a 2700-year timescale and snow accumulation history for an ice core from Roosevelt Island, Ross Ice Shelf, Antarctica. We observe a long-term slightly decreasing trend in accumulation during most of the period but a rapid decline since the mid-1960s. The latter is linked to a recent strengthening of the Amundsen Sea Low and the expansion of regional sea ice. The year 1965 CE may thus mark the onset of significant increases in sea-ice extent in the eastern Ross Sea.