Thoughts on tipping points relevant to Praetorius & Mix (2014)

Tipping points are scary. The response of climate and other environmental systems to external forcing might not be a gradual, reversible change but a flip from one stable state to another. It may be very difficult to reverse this transition. Such tipping points or critical transitions are difficult to prepare for and could cause large social and economic costs. Fortunately, there are strong theoretical expectations that there should be early warning signals such as increasing autocorrelation and variance before a critical transition.

Classic examples of critical transitions between stable states include the onset of Dansgaard–Oeschger events, the Bølling-Allerød interstadial and the Holocene, and the switch between benthic and planktonic dominated lakes as eutrophication increases. Palaeo-scientists have sought to identify early warning signals in proxy records.

If palaeo-proxy data could be used to identify early warning signals of critical transitions, it would be very reassuring. It would imply that even with noisy data, impending critical transitions could be identified decades to centuries before they occur. Alas, not all the attempts are convincing.

A new paper in Science by Praetorius & Mix attempts to find an early warning indicator of the transition from the Last Glacial into the warm Bølling-Allerød.

Praetorius & Mix have produced a high-resolution foraminifera δ18O record from the Gulf of Alaska (GOA) and use a running correlation to show that this record is synchronised with the NGRIP δ18O record from Greenland just before the Bølling-Allerød. They call this synchronisation dynamic coupling and show that dynamic coupling can lead to critical transitions as the pooled variance is higher so that thresholds are more likely to be breached.

I have an alternative hypothesis: that the synchronisation of the GOA and NGRIP records does not cause the transition but is the result of the transition. Praetorius & Mix use a centred 2000-year window for calculating the running correlation; if the Bølling-Allerød transition was initiated in either the North Pacific or Atlantic (or indeed elsewhere) but affects both, the correlation would be expected to start to rise 1000 years before the transition, as soon as the transition enters the moving window.

Gulf of Alaska and NGRIP proxy records (top) and running correlations (bottom). The dashed line in the top panel marks the transition into the Bølling-Allerød. In the bottom panel it marks 500 or 1000 years before this transition.

Gulf of Alaska and NGRIP proxy records (top) and running correlations (bottom). The dashed line in the top panel marks the transition into the Bølling-Allerød. In the bottom panel the dashed lines mark 500 or 1000 years before this transition.

I’ve re-run the analysis of Praetorius & Mix. With a 2000 year window, the zero crossing of the running correlation is exactly 1000 years before the transition.  This is exactly what is expected if the correlation between the proxies is induced by the transition. It provides no evidence that dynamic synchronisation caused the transition.

If we repeat the analysis with a 1000 year moving window, the increase in correlation between the proxies occurs more than 500 years before the transition. So is this evidence for dynamic coupling? Perhaps, but we need to test whether the correlation is higher than expected by chance for two red-noise spectra. This is easily done by simulating many pseudoproxy records that have the same autocorrelation as NGRIP in this time window and finding the correlation between these and the GOA record. If the observed correlation between the GOA and NGRIP proxies is larger than the correlation of GOA and most of the simulated pseudoproxies, the correlation is significant. With 1000 trails, the one-sided p-value is 0.014. Unlike the 2000 year window used by Praetorius & Mix, the 1000 year window used here provides results that are compatible with the dynamic synchronisation hypothesis. The correlation is due to the shared trend in both records during this window, the temporal resolution is not good enough to test if the high frequency variability is also shared, so the results are not as persuasive as one would like.

Even if we accept the results as evidence of dynamic synchronisation as a precursor of critical transitions, dynamic synchronisation, like other early warning signals, may be of little practical use because of the high false alarm rate whenever windowed methods are used, because of the multiple testing. For example, correlations about as large as that preceding the Bølling-Allerød transition occur three times in the Holocene without being followed by a critical transition.


Praetorius, S.K. & Mix, A.C. 2014. Synchronization of North Pacific and Greenland climates preceded abrupt deglacial warming. Science 345, 444-448.

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A minimal model for estimating climate sensitivity

One of the classic tells that a fake climate skeptic is trying to squeeze a weak paper into the literature is that they submit it to a journal where it falls outside the usual scope of papers published there. The problem is that the editor is not familiar with the relevant literature nor with the most suitable reviewers and the paper does not get the robust peer review that it might get at a more appropriate journal. Roy Spencer’s paper in Remote Sensing is an exemplar of this ruse. (Someone wrote an article about this and other schemes fake skeptics use for publishing, but I cannot find it now.)

So when I see Craig Loehle’s new paper “A minimal model for estimating climate sensitivity” breathlessly announced by the ever credulous Anthony Watts, my scepticism is raised several notches when I see it is published in Ecological Modelling, rather than a journal with a climate focus.

We should not, of course, condemn this paper just because it is published in an inappropriate journal. There are many more reasons.

Loehle attempts to isolate the anthropogenic signal in the instrumental climate record by removing the “natural multi-decadal cycles”. The anthropogenic trend is then compared with the increase in log(CO2) to calculate transient climate sensitivity. This procedure is described as ” fewest possible assumptions and the least data uncertainty”. What could possibly go wrong?

Natural multidecadal climate variability, due to internal variability such as the Atlantic multidecadal oscillation and variability in external solar forcing, undoubtedly complicates the calculation of climate sensitivity from instrumental data: if it could be removed, calculations of sensitivity would be much easier. Loehle estimates natural multi-decadal variability as the sum of a linear trend and sine waves with periods of 20 and 60 years. This model is fitted to the data pre-1950 and the difference between predictions for this model and the observed climate 1950-present is claimed to represent anthropogenic forcing and noise.

The model of natural variability is devoid of physics, it is simply a curve fitting exercise with a large number of free parameters. Here is the formula

temperature~b0+b1*year+b2*sin(2*pi*(year-b3)/20)+b4*sin(2*pi*(year-b5)/60)

The source of the 20 and 60 year periods is not specified in the paper. Given that there is 100 years of data before 1950, when the anthropogenic is assumed to become detectable, it would obviously be madness to try to estimate the periodicity of 60 years from these data. These periods come from Loehle and Scafetta (2011) who estimate them from the Sun’s movement about the barycentre. Yes this is completely crazy. Even the sun does not respond on a 60 or 20 year cycle (the Gleißberg cycle is ~87 years and the Hale cycle is ~22 years), so there is absolutely no reason to suppose that interval variability in the Earth’s climate should respond to the location of the Sun relative to the barycentre.

The silliness does not end there. Loehle assumes that his predictions of natural climate variability are without error. Even if the model of natural variability was sensible, it would have uncertainties which should be propagated into the estimate of climate sensitivity. By ignoring these uncertainties Loehle artificially deflates the uncertainty on the climate sensitivity

Ignoring for the moment that the model is ridiculous, how much has the uncertainty been underestimated?

Loehle uses, but does not cite, the HadCrut3 dataset. I’m going to use the HadCrut4 dataset, any differences will be minor.

had<-read.table("http://www.metoffice.gov.uk/hadobs/hadcrut4/data/current/time_series/HadCRUT.4.2.0.0.annual_ns_avg.txt")[,1:2]
names(had)<-c("year", "temperature")
had<-had[!had$year==2014,] #remove partial year
head(had)

plot(had, type="l")

Now lets fit the model of natural variability for the pre-1950 data using non-linear least squares regression.

library(nlme)
mod<-nls(temperature~b0+b1*year+b2*sin(2*3.141593*(year-b3)/20)+b4*sin(2*3.141593*(year-b5)/60), data=had, subset=year<=1950, start=c(b0=0, b1=0, b2=1, b3=0, b4=1, b5=0))#using 3.14 rather than pi to avoid problems later

pred<-predict(mod, newdata=had[1])
lines(had$year, pred, col=2)
lines(had$year[had$year<=1950], pred[had$year<=1950], col=4)

Ideally we would use predict with the argument interval="confidence", but that argument is not yet implemented in R (there is some uncertainty about how best to do it). Instead I can use a Monte Carlo procedure developed by A. N. Spiess

predc<-predictNLS(mod, newdata=cbind(had[1], pi=pi))
matlines(had$year, predc[,6:7], lty=2, col=2)
HadCrut4 global temperatures (black) with Loehle's model of natural climate variability fitted in the blue portion of the solid curve, predicted in the red. The dashed red lines show the 95% MC confidence interval.

HadCrut4 global temperatures (black) with Loehle’s model of natural climate variability fitted in the blue portion of the solid curve, predicted in the red. The dashed red lines show the 95% MC confidence interval.

The uncertainty, which Loehle ignores, is broad. The uncertainty would be broader still if we relax the assumption that multidecadal natural climate variability consists of just a linear trend and sine waves with a 20 and 60 year period. This will have a large impact on the estimate of climate sensitivity.

Loehle minimal model might have the fewest possible assumptions, but they are not the most sensible.


Loehle, C. 2014. A minimal model for estimating climate sensitivity. Ecological Modelling, 276, 80–84

Posted in climate, Fake climate sceptics, Peer reviewed literature, R, Silliness | Tagged , | 1 Comment

The barycentre strikes back

Those who lament the timely closure of Pattern Recognition in Physics should lament no more: while the sun orbits the barycentre, papers that argue that this affects solar variability will get published. As evidence for this conjecture, I offer you McCracken et al (2014) and its precursor Abreu et al (2012).

Both papers discuss spectral peaks in a 9400-year record of solar activity reconstructed from the cosmogenic isotopes 14C and 10Be, from tree rings and ice cores respectively (high concentrations of the cosmogenic isotopes indicates a high flux of cosmic radiation and an inactive sun), and relate these spectral peaks to the influence of planets on the sun. Rather than invoking the “vanishingly small” planet-induced tides on the sun, both papers invoke the torque that the planets’ gravity imposes on the solar tachocline, the non-spherical layer that separates the inner and outer parts of the sun. The mechanism by which the very small torque forcing could be amplified into the reconstructed solar variability is left unspecified.

Figure 5 of Abreu et al shows the spectra of solar activity and their calculations of torque over the Holocene. Five of the peaks in the two spectra coincide. It’s looking promising. Nature certainly thought so.

Abreu et al figure 5. Comparison of solar activity and planetary torque in the frequency domain.  The spectra display significant peaks with very similar periodicities: the 88 yr Gleissberg and the 208 yr de Vries cycles are the most prominent, but periodicities around 104 yr, 150 yr, and 506 yr are also seen.

Abreu et al figure 5. Comparison of solar activity and planetary torque in the frequency domain.
The spectra display significant peaks with very similar periodicities: the 88 yr Gleissberg and the 208 yr de Vries cycles are the most prominent, but periodicities around 104 yr, 150 yr, and 506 yr are also seen.

Alas, there is problem. As Poluianov & Usoskin (2014) demonstrate, the data processing of Abreu et al will cause spurious spectral peaks in their torque spectrum. Abreu et al calculate the torque on a daily basis, but perform the spectral analysis on annually averaged data. This will cause aliasing of the sub-annual torque frequencies of Mercury and Venus, making them appear as low frequency spectral peaks. Poluianov & Usoskin (2014) repeat the analyses of Abreu et al, but using daily rather than annually averaged torque.

The planetary torque spectra computed here for the three sampling frequencies: 1, 10, and 365.24 year−1 for panels A – C, respectively.

Poluianov & Usoskin (2014) figure 3 Planetary torque spectra computed for three sampling frequencies: 1, 10, and 365.24 year−1 for panels A – C, respectively. Note how the spectral peaks change.

None of the spectral peaks found by Abreu et al remain – they are all aliasing artefact. The correct peaks don’t align with the peaks in the solar variability record. The aliasing problem should have demolished Abreu et al (Poluianov & Usoskin also argue the test for coherence between the torque and the solar record is too liberal), but in their response, Abreu et al (2014) basically declare that “tis but a scratch”. They admit that they have an aliasing problem, get confused about the effect of a constant term in their equation for calculating torque, and other things. Some how, the frequencies they originally found are still present, but as minor spectral peaks. It would be most curious for the sun to ignore major peaks in torque but respond to minor peaks.

Abreu et al maintain that using a Monte Carlo procedure, the odds of having the five peaks coincide is “is lower than 10−4“. They estimate this by counting the number of time the five spectral peaks are found in white or red noise processes, and from these calculate the probability of the five spectral peaks co-occurring. There are at least two problems with this, firstly the torque spectrum does not resemble red or white noise and second there are not just five spectral peaks in the solar reconstruction – there are at least eight. The relevant test is not finding the five peaks selected by Abreu et al in random data, but in finding any five out of eight peaks. There are 56 ways to do this – Abreu et al’s estimate of the odds is at least 56 times too low.

McCracken et al (2014) is a review of the evidence for planetary influences on solar activity. The three authors, who were all part of the Abreu et al team, declare

Despite our initial view that we would be able to prove beyond all reasonable doubt that no such correlation exists, it became clear that the contrary is true.

Six lines of evidence persuaded McCracken et al.

1) Four of the most prominent spectral peaks in the solar activity record approximate integer multiples of half the Neptune-Uranus synodic period of 171.42.

This looks like numerology to me.

It stretches credibility to believe that any physical mechanism links the Neptune-Uranus synodic period to one frequency in solar activity let alone four, especially given that Neptune and Uranus are much smaller and more distant than Jupiter. Yet McCracken et al write

The probability of these correlations occurring by chance is shown to be <10−4

This is, at the very least, a sloppy way to express the results of their Monte Carlo procedure, and is an example of the Texan sharpshooter fallacy. Given the eight planets, the number of orbital times and synodic periods is large, so it is really not that surprising that the solar spectral peaks are an integer multiple of one of these multiplied by a arbitrary fraction.

2) The frequencies in the solar proxy record match those in the torque applied by the planets to the solar tachocline, citing Abreu et al. These peaks in the torque spectrum are the ones that Poluianov & Usoskin demonstrated were spurious, arising from inappropriate data processing. McCracken et al neglect to cite Poluianov & Usoskin. They cannot claim not to have been aware of the work as together with Abreu they submitted their reply to Poluianov & Usoskin’s comment before McCracken et al was accepted. This does not look good.

Because torque diminishes with the cube of distance this second argument of McCracken et al contradicts the first as Neptune and Uranus are so remote from the Sun they apply very little torque compared with Jupiter and Venus.

3) The ~2300-year Hallstatt cycle in the solar activity data proxy approximates the half the period between the syzygy (alignment) of the four gas giants at 5272 BP and at 644 BP. Not the strongest of arguments: one peak of unknown statistical significance in the solar activity spectrum can be related to a transient planetary alignment of with no obvious mechanism for affecting the sun.

4) There is no new evidence at number 4. The argument is simply to state that if you multiple the miscalculated probability of argument 1 by that of argument 3 you get a very small and irrelevant number. That’s not quite how McCracken et al phrase it.

5) The barycentre, the centre of mass of the solar system about which the sun orbits, sometimes in a ordered pattern, sometimes in a disordered pattern depending on the alignment of the gas giants. These different modes of free fall, which comprise the Jose cycle, are compared with the solar activity spectrum to find patterns. Mechanisms are not so obvious.

  • Over the last thousand years, four of the seven periods with disordered phases of falling coincide with minima in solar activity. Not impressive evidence.
  • Sunspot cycle 20 is smaller than most others and coincides with a small rather than a large wobble of the sun about the barycentre. A single data point. Not impressive evidence.
  • During the Dalton minimum in solar activity some unusual sunspot cycles matched some small wobbles around the barycentre.

The figure in McCracken et al isn’t very good so I’ve plotted the sunspot data from WDC-SILSO and the sun-barycentre distance from the Horizon ephemerides. I cannot see any strong relationships here.

Distance between the sun and the barycentre (black) and the mean number of sunspots. red

Distance between the sun and the barycentre (black) and the mean number of sunspots (red). Clear, repeated relationships between the two curves are not obvious.

  • More interesting is the claim that the 20 Grand Minima in the Holocene (including the Maunder Minimum) all occurred during disordered phases of the Sun’s motions. Although this “close association” in figure 7 is not so obvious in the figure 8. McCracken et al rate the probability of the association occurring by chance if the wobble had no effect as 0.01. This is the only evidence I’ve found interesting, but it is hardly conclusive evidence.
McCracken et al Figure 7 The occurrence of Grand Minimum Events within the Jose cycles over the past 9400 years. The vertical dashed line indicates the approximate end of the ordered phase: the dotted lines the occurrence of barycentric anomalies. The open blocks represent periods of increasing cosmic-ray intensity; the solid blue blocks correspond to the periods of highest intensity.

McCracken et al Figure 7 The occurrence of Grand Minimum Events within the Jose cycles over the past 9400 years. The vertical dashed line indicates the approximate end of the ordered phase: the dotted lines the occurrence of barycentric anomalies. The open blocks represent periods of increasing cosmic-ray intensity; the solid blue blocks correspond to the periods of highest intensity (ie solar minima).

McCracken et al figure 8. The correspondence between variations in the paleo-cosmic-ray record and features of the Jose cycle for the sequence of Grand Minima in the interval 4000 – 2800 BP. The hashed blocks correspond to the ordered phase of the Jose cycle. The narrow vertical blocks represent the barycentric anomalies; their width indicates their duration. The Jose Cycles (JC) are numbered from the beginning of the Holocene.

McCracken et al figure 8. The correspondence between variations in the paleo-cosmic-ray record and features of the Jose cycle for the sequence of Grand Minima in the interval 4000 – 2800 BP. Hashed blocks correspond to the ordered phase of the Jose cycle; narrow vertical blocks represent the barycentric anomalies. Jose Cycles (JC) are numbered from the beginning of the Holocene.

So out of the six lines of evidence in McCracken, only one is in the least interesting, meriting some further investigation. The other five lines are very dubious.

Finding patterns of planetary dynamics that correlate with solar activity is easy. There are a multitude of patterns, some are bound to correlate (occasionally, at least if you squint). Testing if these patterns are real is complicated by the lack of a suitable test case – using the same data for exploratory analysis and confirmatory analysis is an easy way to get Type 1 errors, results that appear to be statistically significant but are no more than by chance. Fitting models with half the data and testing the fit for the other half would be a good strategy (but no peeping allowed).

One of two things is required to make planetary-solar interactions convincing 1) good predictions of the next few sunspot cycles, 2) a physical model of solar activity that can only match observed record of solar activity when planetary alignment is considered. The first will take decades to be realised, so might the second.


Abreu J.A., Albert C., Beer J., Ferriz-Mas A., McCracken, K.G. & Steinhilber, F. 2012. Is there a planetary influence on solar activity? Astronomy and Astrophysics 548, A88.

Abreu J.A., Albert C., Beer J., Ferriz-Mas A., McCracken, K.G. & Steinhilber, F. 2014. Response to: “Critical Analysis of a Hypothesis of the Planetary Tidal Influence on Solar Activity” by S. Poluianov and I. Usoskin Solar Physics 289, 2343–2344.

McCracken, K.G., Beer J. & Steinhilber, F. 2014. Evidence for Planetary Forcing of the Cosmic Ray Intensity and Solar Activity Throughout the Past 9400 Years. Solar Physics 289, 3207-3229.

Poluianov S. & Usoskin, I. 2014. Critical Analysis of a Hypothesis of the Planetary Tidal Influence on Solar Activity Solar Physics (2014) 289, 2333–2342.

Posted in Peer reviewed literature, solar variability | Tagged , , , | 6 Comments

Kind of crazy

Today it is 30°C in Bergen. It is rare for it to be this warm — most summers do not reach this temperature.

But I am still cold working in my office. Indeed my office is so cold that the radiator is on.

Heating and cooling are two of the most energy intensive operations in a building — doing both simultaneously while making the building unpleasantly cold is plain crazy. I’ve complained.

This isn’t some ancient building, designed before the idea that energy saving was good. The biology department building is less than five years old.

 

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This is a “good” solar-proxy correlation

It has been a while since I have posted a review of a paper purporting to find a correlation between a proxy and solar activity. This is not for lack of interest — plans are developing for a meta-analysis, but some preliminary work is still in progress.

Meanwhile, I’d like to take a look at El Bilali et al (2013). El Bilali et al reconstruct eastern Canadian climate over the last few thousand years using the δ18O of cellulose of Sphagnum moss from an ombrotrophic bog (a bog that receives water and nutrients from precipitation only rather than groundwater or run-off and is consequentially very nutrient poor).

El Bilali et al claim that the oxygen isotopic composition of the Sphagnum in their record is dependent on temperature and that precipitation and evaporation effects are small.

I’m interested in the section correlating the δ18Ocel  record with solar activity. This is the section of text of interest:

The Mer Bleue Bog temporal δ18Ocel record generally correlates with the Beryllium (10Be) isotope anomaly, sunspot number, and solar variation events records. The Maunder minima and maximum cooling is less pronounced in the δ18Ocel data than in the Northern Hemisphere reconstructed paleotemperature record (Moberg et al., 2005), which may be due to less pronounced cooling in eastern Ontario. The δ18Ocel record from Mer Bleue Bog shows a good correlation with the smoothed 10Be-record (Figure 6a, b). The low δ18Ocel values at ~AD 1810–1820 are verified by repeated and high-resolution sampling (Table 2) and may be related to the lower solar activity during the Dalton Minimum (Figure 6), to the cooling influence of the Tambora volcanic eruption for the summer of AD 1816 and subsequent years, or both.

Comparison of isotope record of cellulose of Mer Bleue Bog through the last 600 years with (a) solar activity events Spörer,  Maunder and Dalton minima and (b) Beryllium isotope anomaly (Bard et al., 2000) and measured sunspot numbers from the last 250 years. The  vertical dashed line marks ad 1816.

Comparison of isotope record of cellulose of Mer Bleue Bog through the last 600 years with (a) solar activity events Spörer, Maunder and Dalton minima and (b) Beryllium isotope anomaly (Bard et al., 2000) and measured sunspot numbers from the last 250 years. The vertical dashed line marks AD 1816.

I showed this figure to the students at the INTIMATE training school, and asked them whether the correlation was positive or negative. Not one of them was prepared to raise their hand in agreement with either possibility. It is clear from the text that El Bilali et al believe the correlation between the inverted 10Be and δ18Ocel to be positive. I can only see a relationship in the period after AD 1700 in the unsmoothed 10Be, and none at all in the smoothed record, which is supposed to have a good correlation.

Curiously, the 10Be-record from Bard et al (2000) goes back to AD 843, but the figure is truncated at AD 1400 even though the δ18Ocel extends for thousands of years. Normally if half the data were not shown, I would suspect that the correlation breaks down in the portion unseen, but here I don’t think the correlation could get much worse.

Whenever I am presented with a “good” correlation between proxy records I want to ask what the correlation coefficient is (almost guaranteed bluster if you do this at a conference). Like many papers reporting a “good correlation”, El Bilali et al do not attempt to put numbers on the strength of their correlation even though this is not difficult to do. As El Bilali et al provide the data in their paper, the INTIMATE class could estimate the correlation coefficient for these records, using linear interpolation to put the dates on the same time scale. The Pearson correlation is less than 0.1 (note however that the age-depth model the INTIMATE class generated using Bacon probably differs from the original): not exactly what I would call good. Allowing for chronological uncertainty didn’t improve matters.

Note, the second author of this article is Timothy Patterson, who has several papers reporting solar-proxy relationships, some I’ve discussed before which I have not found persuasive.


El Bilali, H., Patterson, R.T., Prokoph, A., 2013. A Holocene paleoclimate reconstruction for eastern Canada based on δ18O cellulose of Sphagnum mosses from Mer Bleue Bog. The Holocene. 23, 1260–1271.

Posted in climate, Peer reviewed literature, solar variability | Tagged , , | 1 Comment

A biased and incomplete summary of Sea Ice Proxy workshop

Sea-ice is an important component of the Earth’s climate system, for example, it greatly increases the proportion of sunlight reflected at high latitudes – the albedo of ice is ~0.6 whereas it is only 0.1 for open water. Because of this importance, palaeoclimatologists want to be able to reconstruct its past extent.

This week, many of these palaeoecologists met in Bremerhaven for the third and final Pages Sea-Ice Proxy workshop, hosted by Rainer Gersonde at the AWI. There were about 30 presentations, some of which were about modelling sea-ice which I won’t discuss here. A diverse range of techniques for reconstructing sea-ice were presented, summarised here as coralline algae, biomarkers, ice-core proxies and biotic assemblages. I apologise if I have omitted or misrepresented anything.

If you have been to a rocky shore, you may have noticed a red crust on some of the rocks. That was probably coralline red algae. In most places, coralline red algae (which are not related to corals) form only a thin calcareous crust. In cold water at high latitudes where grazing rates are low, they can form a thick crust with a layer of reproductive cells marking each year’s growth and permitting the age to be calculated in the same way as a tree can be dated by counting the rings. Unfortunately the variability in layer widths is too small for crusts of different ages to be cross-dated. Jochen Halfar, who has found algal crusts up to 646-years old, presented his work using the width of the growth bands and the calcium magnesium ratio of the algal crusts to reconstruct sea ice extent (growth is slow in years when ice blocks the sun) and temperature.

I thought this was a really nice proxy, unfortunately it is limited to the last ~1000 years because of the availability of material, and there can be hiatuses in the crust caused by severe grazing or iceberg damage. The best material comes from 20-25 m water depth, where the growth rate is high enough, but grazing not too severe. This limits the proxy to coastal areas, so it may be better at recording fast ice attached to the land rather than drift ice which occurs over most of the ocean.

A biomarker called IP25 was the most popular proxy, with at least seven presentations discussing it, beginning with an overview of recent developments by Simon Belt. IP25 stands for Ice Proxy with 25 carbon atoms and is apparently produced only by algae that live in sea-ice. The diatoms that produce IP25 have now been identified and constitute only a small proportion of the diatom community in sea ice. The presence of IP25 seems to be a reliable indicator of the presence of sea ice. Its absence is trickier to interpret: there might be no sea ice; or the sea ice might be so thick that the base is dark and the diatoms cannot grow. Fortunately other biomarkers derived from phytoplankton can be used to distinguish these situations: if these markers are present, but IP25 is not it indicates open water conditions. A schematic figure by Juliane Müller showing this relationship between sea-ice IP25 and other biomarkers was by far the most popular figure of the workshop, included in every IP25 presentation. Kerstin Fahl discussed alternative sources of the phytoplankton biomarkers, including algae in the sea-ice and freshwater algal sources. Despite these complications, the method appears to work.

One potential problem with IP25, as with all biomarkers, is the potential for degradation. Xiaotong Xiao showed some records from the central Arctic, where sedimentations rates are low, that all showed an increase in IP25 towards the present. Simon Belt queried whether this was a real sea-ice signal or the result of progressive degradation.

IP25-producing diatoms only live in the Arctic. Fortunately Lukas Smik showed that there are other biomarkers in the Southern Ocean that can be used to indicate sea ice there.

Ice cores are excellent archives of a wide variety of proxies, including several with a link to sea-ice. The challenge is to understand the mechanisms behind this link so that the proxy can be interpreted correctly. Eric Wolff discussed the sodium record in ice cores. On inter-annual time scales, the record is to be dominated by meteorology – how many salt-bearing storms pass over the ice core site. On longer time scales, sea-ice extent seems to be more important. There are three major potential sources of Na: sea-spray from the open ocean; frost flowers that form on sea ice that freezes in calm conditions; and from salty snow blown off sea-ice after it has wicked up some sea water. Understanding the proxy requires quantifying relative importance of these sources. Marcus Frey presented some work on the latter source – measuring the amount of snow whipped up in a winter storm over sea-ice does not sound like my idea of fun.

Paul Vallelonga showed some new work on halogen deposition in ice. It looks like a complex process, with summer peaks in bromine but winter peaks in iodine concentration despite a summer maxima in emissions. Morgane Philippe had to cancel her talk, so I didn’t hear the latest news about the potential of sulphate and methanesulphonic acid (MSA; produced by phytoplankton) for reconstructing sea-ice, but I did hear that MSA is not stable over long time periods, limiting the duration of records that can be generated. A new ice core from Renland, a small ice cap near the eastern coast of Greenland, to be cored next year has great promise for reconstructing sea-ice as it is much closer to the sea-ice than the central Greenland cores.

A range of taxonomic groups were shown as indicators of sea-ice. Ostracods, crustaceans with calcareous shells like a bivalve, were mentioned briefly by Marit-Solveig Seidenkrantz. Some species are restricted to perennial sea-ice. Reconstructions based on their presence were not not rated as very confident in her compilation of Arctic sea-ice records from the Holocene. She also mentioned a strain of the planktonic foraminifera Neogloboquadrina pachyderma (sin) that has been identified from DNA evidence as being associate with sea-ice. Unfortunately it cannot be identified on morphological grounds, and any DNA found in the sediment will suffer from the usual problems of variable preservation of biomarkers.

Diatoms got more discussion, with Verena Benz, Oliver Esper and Rainer Gersonde presenting work on Southern Ocean diatoms, and Beth Caissie and Jian Ren presenting work from the North Pacific. Some of the diatoms grow in sea-ice, so there are grounds to expect a mechanistic link to sea-ice. Unfortunately the same taxa can also be found remote from sea-ice, complicating interpretation as Jian Ren showed. The team working on the Southern Ocean have amassed an impressive collection of diatom stratigraphies (Oliver Esper made Beth Caissie rather envious when he said he could count a slide in half an hour rather than half a day, such is the material in the Southern Ocean siliceous oozes). I would have liked to see some diatom stratigraphies and reconstruction diagnostics rather than just the reconstructions. The three research groups that work on diatoms in the Southern Ocean are collaborating to generate a combined transfer function and a synthesis of the reconstructions.

For all their importance as a proxy of sea-ice, dinocysts hardly got a mention. Jian Ren showed that the classic dinocyst sea-ice indicators were abundant south of the ice margin. Anne de Vernal was present but did not present. My argument that the uncertainty on dinocyst-based reconstructions is much larger than suggested by naïve cross-validation was not challenged.

Jian Ren’s talk was one of the few to show several sea-ice proxies from the same core. Of course they did not agree. The challenge is to understand what is going on in these multiproxy studies rather than generating case-by-case explanations of why the proxies don’t agree. These explanations could never be applied to a core with only a single proxy!

I think that covers the main news from the meeting.

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Small tornado in Bremerhaven

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The last couple of days I’ve been discussing sea-ice reconstructions at the Pages Sea-Ice Proxy workshop in Bremerhaven. A huge range of proxies have been presented, ranging from traces of halogens in ice cores to transfer function based reconstructions. One very promising proxy is the annual growth bands of coralline algae. Growth is poor when sea ice cover is high. Many of the presentations have stressed the need to understand the mechanic link between the proxy and sea ice.

That was one of the themes I explored in my presention of some of my work on transfer functions. Rather than dwelling on the problems of autocorrelation and other issues, I focused on the problems identified in Steve Juggins’ “sick science” paper.

My contribution seemed well received. I’ll post it here shortly.

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