Climate Audit

Reader Bart S. has argued that Cook et al [QSR 2004] disposed of the "Divergence Problem", the name applied at the NAS panel on March 2-3, 2006 for the problem that, if the proxies do not record late 20th century warming, how can we be sure that they recorded potential earlier warming in the MWP.

Since many people here are alien to the scientific litterature on the topics they discuss, i would like to draw the attention to a paper published by Cook et al. in QSR 2004, I am sure it has been audited here before, but the audit seems to have failed to notice the fact that the paper speeks directly to the “divergency” issue. First by showing that the diergency is an issue not for the complete set of time series of Esper et al, but only for the northern ones, as also Briffa said in 1998, then showing that during medieval times this difference or divergency between mid and high latitude series does not appear. Bottom line – no evidence of MWP divergency.

I’ve not posted before on Cook et al [2004], but it’s not obvious to me that it represents an advance beyond Briffa’s cargo cult explanations for divergence.

Also see posts 529 and 570.

First, let me permit myself a snippy comment. The handling of statistical matters by the Hockey Team, including the calculation of confidence intervals, is about as "alien to the scientific literature" [statistics] as one could imagine. Before complaining about an alleged mote in our eye, it might make sense to examine the beam in the eye of the Hockey Team.

Second, I think that the scope of commentary on tree ring sites on this blog is commendably broad, given my resources. I do not claim to have "audited" every multiproxy study nor do I believe that it is my responsibility. I have not commented previously on Cook et al [QSR 2004], but am familiar with it, have a pdf copy handy and will make some comments in response to reader Bart S.

Third, Bart S, like many readers, seems to think that the idea of attempting to verify studies that are being relied upon for policy purposes warrants a snide comment. I am puzzled as to why people think this way.

Fourth, many multiproxy studies remain inaccessible to any form of verification. Briffa has published many articles on his 387 site network without ever disclosing the identity of the sites and has refused to provide this information. Cook et al. [2004] is a re-consideration of the 14-site network in Esper et al [2002]. Measurement data for most of the sites is not archived; data citations are not given for most of the sites and are inconsistent in other cases. Digital versions of the site chronologies used by Esper et al [2002] were not archived and were disclosed to me only last month and only after an intervention by Science in response to repeated requests (and probably only because of the publicity that I can shine on such refusals.) In addition, Osborn and Briffa [2006] provided some information on the Esper et al. network that was not previously available (although not necessarily consistent either.)

Finally, the issue of the Divergence Problem under that name was raised at the NAS panel. I’ve posted on many other aspects of the panel since then (and played in a squash tournament). If I’ve not posted on some paper that may be relevant, it hardly warrants a snide comment. There are limits on my time, priorities and energy.

Having said that, Cook et al. [2004] does refer to divergence issues and is worthwhile to comment in the light of the NAS panel. I might note that D’Arrigo, who presented at the NAS panel and who was asked to explain the Divergence Problem, was a co-author of Cook et al [QSR 2004] and did not seem to have at hand the explanation supposedly offered here by Bart S. It’s quite possible that she might have thought of this explanation afterwards and wished she’d mentioned it at the time. So I don’t mention her omission as a gotcha, but I’m merely observing that she had an opportunity to offer this supposed explanation and, to my recollection, did not do so (but I missed part of her talk as well).

Anyway, having vented a little, here is some information from Cook et al [QSR 2004]. Their Figure 6 (shown below) shows a difference between "Northern (55-70N) and Southern (30-55N) RCS chronologies, as illustrated below. The Southern sites of this 14-site network show a strong late-century growth pulse, while the Northern sites show a decline. Note that this information is only for the small 14-site network and not for the large 387-site Schweingruber-Briffa network. (I’ll look at the larger network from this point of view on another occasion.) Reader Bart S. characterizes this graphic as showing (1) that the "divergence" between modern instrumental temperature and ring width is a problem only for the North sites (blue) and (2) there was no prior divergence between the two RCS series in the MWP. Here’s how Cook et al. expressed it:

After AD 1950, there is clear divergence, particularly between the “North” and “South” subset chronologies. This is probably an expression of the well-documented large scale loss of growth sensitivity to climate in boreal forest conifers (Briffa et al., 1998a, b), a phenomenon that is not yet fully understood. The “South” chronologies may also show evidence of abnormally accelerated growth in the 20th century (Briffa et al., 1998a, b).

I’ll discuss possible reasons for "abnormally accelerated growth" at South sites in a moment. Cook et al go on to say:

Note that it [the RCS reconstruction] does very well at tracking the instrumental data on inter-decadal and longer timescales up to about 1982, after which the tree ring estimates systematically under-estimate the actual warming. This departure probably reflects the loss of climate sensitivity noted earlier in the “North” chronology shown in Fig. 6. Whether or not a similar loss of sensitivity has occurred in the past is unknown with any certainty, but no earlier periods of similar divergence are apparent between the “North” and the other regional chronologies. This result suggests that the large-scale loss of climate sensitivity documented by Briffa et al. (1998a, b) is unique to the 20th century, which argues for an anthropogenic cause ….

There’s a little bit more argument here than the pure cargo cult "explanation" of Briffa et al., but not much. There is no plausible candidate for an anthropogenic cause for the North Site Divergence is offered. If one proceeds to identify the actual South sites, one can quickly see that the Cook et al. do not explain the Divergence Problem and is not an actual advance beyond Briffa’s cargo cult.

Original Caption. Fig. 6. Testing the regional robustness of the ECS tree-ring data. The “linear” and “non-linear” chronologies are the same as those shown in Esper et al. (2002). The other chronologies have been grouped by geographic location of the sites. The number of sites in each geographic group is provided in parentheses in the plot legend.

North and South Sites

Let’s start by identifying the North and South sites, since that will give some insight into the problem. Cook et al said that there were 8 North and 6 South sites. Using a 55 deg N dividing line, I identified 7 North sites and 5 South sites – with Jasper, Alberta at 52N being one of the "South" sites – a seemingly odd classification.) If the "Quebec" site is cana169, as indicated in Osborn and Briffa [2006], it is located at 55o 20′ N; perhaps Cook et al. classified this as a "South" site. (This identification in Osborn and Briffa may be incorrect and it’s possible that Esper et al used some other site – no accurate data citation exists in Esper et al 2002). Again a site on the shores of James Bay seems like a very odd inclusion as a South site, if it is, as its climate would be far more "northerly" than Gotland or Jaemtland.

Whatever the ultimate identifications may be, the main issue here is that the South sites undoubtedly include two foxtail sites and the Jacoby Sol Dav, Mongolia site, which, between them, impart the 20th century growth pulse to the South sites in Cook et al. As readers of this site know, Bristlecones and foxtails are cousins on opposite sides of the Owens Valley in California. I presume that the "abnormally accelerated growth" affecting South sites, alluded to here by Cook et al. in very vague terms, is the cluster of issues surrounding bristlecones and other high-altitude low-latitude sites, including CO2 fertilization. Ironically, D’Arrigo et al [2006] excluded the two foxtail sites because they did not have a correlation to gridcell temperature (an amusing contradiction to Osborn and Briffa 2006, who claimed the exact opposite in an article published the same week.)

On this record, there does not appear to be a Divergence Problem for the South Sites. But the 20th century ramp here is largely created by two high-altitude low-latitude foxtail sites, where CO2 and other fertilization (phosphate, nitrate) issues have been specifically identified by specialists. This is presumably the "abnormally accelerated growth" alluded to in veiled terms by Cook et al, but not further discussed. The relationship between bristlecone/foxtail growth in the 20th century and temperature is arguably spurious. If so, one could reasonably conclude that the divergence between late 20th century growth at high-altitude low-latitude sites and North sites is due to fertilization impact on the South sites. One is then left with merely cargo cult explanations of the Divergence Problem at North Sites.

Aside from fertilization issues, the foxtail sites are in arid locations and moisture stressed as well. There is no ecological report on Sol Dav, Mongolia, but other Mongolia sites are described as precipitation proxies and, until some definitive information on the Sol Dav site is provided, I don’t see how it can be relied on as a temperature proxy. One could plausibly interpret the above record as showing increased 20th century precipitation in arid sites (Woodhouse discusses a "20th century pluvial" in the American Southwest). Millar et al 2006 suggest that the MWP was warmer and slightly drier. If the foxtail chronologies are moisture-stressed, then their attenuated MWP levels – which is inconsistent with the ecological niche information as an index of temperature – may simply be recording additional precipitation stress at these altitudes in the MWP – hardly inconsistent with Millar et al [2006].

In short, Cook et al 2004 resolves nothing. They provide no explanation of the Divergence Problem for North Sites that rises above cargo cult science. The foxtail site chronologies are additionally inconsistent with the ecological niche information of Millar et al [2006] for the Sierra Nevadas. The issue of whether these tree ring site chronologies can accurately recover medieval warming – the Divergence Problem – remains alive.

UPDATE – March 15
If one actually tries to verify the results of Cook et al. [2004], there are some serious obstacles.

First, as noted above, it is impossible to replicate the number of sites. For the calculations below, I’ve used 5 South sites, allocating the Quebec site to the North roster, both by definition of 55-70N and its logic as a North site.

Second, measurement data is either not archived or incomplete for many of the sites.

Third, the distinction between linear and non-linear trees in the original Esper et al article is not defined operationally and both Esper and Science have refused to provide an operational definition.

Fourth, even the RCS site chronologies were unavailable until a few weeks ago and even then, left out the Mongolia RCS chronology inexplicably.

For the calculations below, I’ve used the Mongolia chronology saved with Jones and Mann [2004] and the 13 Esper site chronologies provided to me by Science in February 2006 (after months of waiting.) I’ve defined North and South according to the table above(which differs a little from Cook et al).

The figurre below shows the average of available chronologies in the North and South rosters from 800-1996 smoothing using a gaussian filter of length 41.

Reader Bart S. has argued that the North and South chronologies are coherent prior to 1950 and diverge only afterwards – which he attributes to an unknown anthropogenic cause affecting North (but not South) sites. Here’s how Cook et al expressed the supposed coherence:

the low frequency signal in the mean RCS chronology and the various subset chronologies is generally robust, particularly over the AD 1200-1950 interval. The average correlation between the mean RCS chronology and the subset chronologies is 0.82 for the full AD 831-1990 period and 0.87 for the AD 1200-1950 period. Prior to AD 1200, there is more separation between the subset chronologies, which is consistent with the significant decline in replication described earlier.

First, the correlation between North and South chronologies calculated as above over the 1000-1850 period is only 0.09. The correlation in the period 1200-1950 is 0.44. In most cases, the correlation between smoothed chronologies is surprisingly lower than between the unsmoothed chronologies; the one exception is the 1200-1950 case. Given the interest in the MWP period, which is mostly before 1200, it’s disquieting that the supposed coherence between North and South chronologies does not extend to this period. Cook et al blame this on a lack of replication in the MWP period. However, their replication is no worse than many similar multiproxies, which have not cavilled at opining on MWP-modern relationships.

Table 1. Correlations between Averages of “North”‘? and “South” Esper Chronologies.

Hockey Team statistical practice frequently includes turning a blind eye to autocorrelation. I’ve noticed that Hockey Team articles often report information on spectra. Econometricians tend to prefer to look at time-domain information such as autocorrelation functions. While spectra and autocorrelation functions contain the same information, they lend themselves to somewhat different perspectives. Here are the autocorrelation functions for the North and South averages with the autocorrelation function for the CRU NH temperature series also shown for reference.

Figure 3. Autocorrelation functions for North and South averages. Red- Autocorrelation function for CRU NH temperature.

As you can see, the North and South chronologies are VERY autocorrelated and the decorrelation time is VERY long. I wouldn’t attach much significance to the longer autocorrelations for the temperature series as the series is very short. But the greater persistence of the tree ring series is obvious. Cook et al have observed that the North and South series are correlated over one portion of their history, but not over other portions. They failed to observe the correlation over the entire length was very low. The “best” correlations that I’ve been able to replicate are much lower than those reported in Cook et al., where correlations exceeding 0.8 are thrown around. Is there anything here that is inconsistent with the behavior of highly autocorrelated series? I’ll bet that David Stockwell wouldn’t think so. (I’ve posted up digital versions of my calculations of the North Average and South Average here.)