cc: " Moberg; Anders " , Gabi Hegerl , esper@wsl.ch, " Briffa; Keith " , " Osborn; Tim " , m.allen1@physics.ox.ac.uk, weber@knmi.nl date: Thu, 17 Aug 2006 18:38:17 +0100 from: Martin Juckes subject: mitrie -- response to comments from Eduardo to: Eduardo Zorita On Thursday 17 August 2006 11:31, Eduardo Zorita wrote: > >  > > Due to the ongoing debate, this has turned an even more difficult manuscript. In general, I think Martin did a very good job in the review of the literature. Concerning the new reconstructions and the evaluation of McIntyre work, I would not fully agree with some of the conclusions, which I thin do not follow from the material presented in the text. I have some remarks on this which you may consider useful. But I think that I am not the one that should give the manuscript the final shape, as Martin is the person in charge of the project. Please, consider the following comments as suggestions. > > eduardo > > > > Consensus: I would tend to avoid the word 'consensus', since it is not a well defined concept. > Depending on the meaning of consensus, each would agree with it to a certain degree. I would prefer to refer to a particular IPCC conclusion, or something similar. I think this review of the literature is very well written and informative, but I am not sure that each one of us will agree with each one of the concussions of each of the papers. > I've removed a couple of uses of `consensus' and tried to make the text clearer. There is an IPCC consensus (i.e. something members of the IPCC agreed on) -- and I think it is worth making a distinction between this and other peer reviewed results such as MBH1999 conclusions etc. I've now said that the papers reviewed in section 2 support the IPCC [that 1990s are likely to have been the warmest decade of the millenium in the Northern Hemisphere.] Later I've referred to a "general consensus": this is shorthand for saying that almost everyone agrees and where there is disagreement there are good grounds for dimissing it with regard to the specific point under discussion but not by any means implying taht people agree on other issues. > Page 12, section 2.8. I think the text is somewhat vague here, and it could be misunderstood. > Mann et al (2005) tested the RegEM method, not the original MBH98 method. It is true that applied to the > real proxies both methods, according to Mann, yield very similar results. But strictly speaking , Mann did not test the MBH98 method in the CSM simulation. The MBH98 method is thereby only by implication Text corrected > > I tested the the sensitivity of the MBH98, and not of RegEM, to the length of the calibration period. It may be the RegEM is less sensitive or not at all. Figure 4 and 5, if I understood well, support this dependency of MBH to the calibration period. Am I correct to interpret the large differences between the original MBH reconstruction (dashed red) and the black curve as due to the different calibration period (1901-1980 versus 1856-1980) and to the use of the leading PC or NHT as calibration target? At least in the period prior to 1600 I think these are the only methodological differences between both curves (?). I don't think so: the main difference is that the MBH1999 reconstruction uses more data for the more recent period, and also reconstructs more degrees of freedom. This should be stated in the text -- I'll check. I've tidied up this figure a bit. (Now figure 3, as I've omitted the previous figure 3). > My interpretation of this figure is also somewhat different. If the final reconstructions differs so strongly by using a longer calibration period (in general yielding stronger decadal variability in the reconstruction) I would tend to think that the method based on these proxies is quite unstable. What would happen if the calibration period could have been extended to 1800, for instance?. The main sensitivity which is clearly defined by the calculations I've done is that the adjustment of the North American tree-ring proxy 1 in MBH1999 shifts the AD1000 to AD1800 reconstruction up roughly 0.2K. This is now commented on. I'd like to look more closely at the 15th to 18th centuries, but I think this is best achieved by bringing in more proxies -- and I don't want to extend the scope of this study that far. I agree with you that there is an interesting and challenging issue about the 15th to 18th centuries, and hope to follow that up later (i.e. after submitting this). > > > Page 15: top. The role of forcing on the global or NH T is also recognized in the correlation between the NHT simulated by ECHO-G and CSM for the millennium. For the case of a second ECHO-G simulation /Gonzalez-Rouco et al.) the agreement is very close at 30-year timescale. > OK, I'll add the citation. > Section 3, beginning. > In my opinion, MM05 stress the inadequacies and uncertainties in the MBH work, but they not put forward their own reconstruction implying a warmer-than-today MWP. They believe that this is true, but in their works so far, at least to my knowledge, they do not assert that the MWP was warmer than present, only that the uncertainties are too large for such a claim. Figure 8 of McIntyre and McKitrick (2003) says "Corrected version: 20th century no longer highest". There 2005 paper does not reproduce this, so their published statement implying they have reproduced the results is false. They left out most of the data by mistake and got garbage -- it is fairly clear. > > Section 3: Consensus. This paragraph may be problematic. Again what is the consensus? If we look at the recent NAS report, which again not every one would agree with, the 'consensus' is reduced to the past 400 years in comparison to IPCC, leaving ample space for speculation before this period. Does the NAS report belong to the consensus? perhaps partially, but I am not sure to what extent. > The fact that there is ample space for speculation does not mean there cannot also be a consensus. I don't think a report should "belong" to the consensus, the consensus is the body of statements which are agreed on. > Section 3, discussion of MM05 and hockey-stick index. I have here a certain level of disagreement with these paragraphs. The issue raised by MM05 would be that the de-centering of the proxies prior to the calculations of the principal components tends to produce hockey-stick-shaped leading PC. I think this effect is true, at least with spatially uncorrelated red-noise series . It can be easily verified and it has been recognized in the NAS, the Wegman report and by Francis Zwiers. To be fair, following this issue is the problem of the truncation- just to keep the leading PC or further Pcs down the hiercharchy, and if this is done, the final differences could be probably minor. in the final reconstructions. But the paragraph implies, in my opinion, that this criticism by MM05 has no grounds, which as I said is problematic and could open the manuscript with criticisms based on these recent reports. Its a theoretical possibility in certain parameter regimes, yes, but its not relevant here. I have no problem with MM05 raising this issue, the problem is the inaccurate and misleading material they put in their papers. > > I think that the calculation shown in Figure 3 is very useful, as it boils down to the issue raised by MM05: how relevant is the de-centering and standardization with real proxies?. Apparently, I get a different message from Figure3 (although I may have misinterpreted the text). I see quite large differences in the 20th century between the original MBH leading PC and the 'correct' calculation (whole period centering and standarization,blue line). Only the original MBH PC shows a positive trend in the 20th century. The blue lines seems even to show a negative trend or no trend at all. If this PCs were to be used in the MBH regression model (with trend included in the calibration) the results could be quite different. I would tend to think that this figure actually supports the MM05 criticism, since the hockey-stick shape of the leading PC disappears. I've moved this, and the associated reconstructions, into "supplementary material", mainly to avoid having to discuss all the issues around the AD1400 to present proxies, and also the difference between reconstructing multiple temperature PCs and then evaluating their mean and direct reconstruction of the mean temperature. There is some sensitivity to the principal components, but very little in the reconstruction. > > Section 3, end, bristlecone pines. I am also worried by this paragraph. The recent NAS report clearly states that the bristlecone pines should not be used for reconstructions in view of their potential problems. They cite previous analysis on this issue. I think that to refer to just one study indicating no fertilization effect could not be enough. However, I am not a dendroclimatologist. This could open the door to potential problems. > I've spoken to Ed. Cook last year and he didn't know of any specific evidence of CO2 fertilization in mature trees. I haven't seen the NAS report (what's its title?) -- it would be interesting to see what they base their argument on. As far as I know the one report I've cited covers the only study on mature trees in controlled conditions (its not easy to keep large trees in an enhanced CO2 environment). > Section 4 , end. years 1997 and onwards were the warmest in the millennium. I see here also potential problems with this claim, and I do not see the need to make our lives more complicated. The NAS report expressed that the uncertainties are too large for this type of conclusion and certainly this conclusion would attract some attention from the reader. I see two lines of criticism on this: one is that the standard errors have been calculated with the calibration residuals and these are an underestimation of the true uncertainties. A reviewer may require that the uncertainty range be calculated by cross-calibration or bootstraping. In the case of CVM perhaps this effect is not very important, as there is just one free parameter, but in the case of inverse regression there are much many more free parameters and the true uncertainties can be quite different from those estimated from the calibration residuals. This potential criticism could be exacerbated by the fact that the new reconstruction has not been tested in a validation period. I haven't quoted any uncertainties for the inverse regression result for this reason. The statements in the text should be simple statements of factual results: the maximum temperature in the preindustrial time is x and the highest temperature in the instrumental record is more than 4sigma greater, where sigma is .... > > The other line of criticism could be that the calibration period has been, as in all reconstructions, a priori truncated -data after 1980 are not considered as the proxies are known to not follow the temperature. Strictly speaking this truncation can be only justified by a credible physical explanation about the cause of this divergence. Statistically, I think it is not correct to a priori ignore some data because they do not fit. If one does so, I think the uncertainty range should be enlarged to encompass the possibility that this divergence could have happened in the past, i.e. an additional standard deviation of the instrumental NH T in the period 1980-2000 (or perhaps more correct, the square root of the sum of the error variance and the NHT variance in 1980-2000). Alternatively, one could include the period 1980-2000 in the calibration and due to the divergence the standard errors would grow, but perhaps this is practically not possible as the proxy time series may not have been archived for the last 20 years. Which data do you think I'm ignoring "because they don't fit"? This is a rather unnecessary accusation. The problem is that many of the proxies are not annually updated, so that, with the methods used in this study, extending the calibration period reduces the number of proxies. I'll do a couple of sensitivity studies, but ideally we need to develop a means of exploiting proxies which do not cover the whole calibration period. REGEM might do this, but I'm not entirely convinced as yet -- mainly because the complexity makes it difficult to know exactly what is going on. > > Section 5, conclusions. > > I share the worry of Anders Moberg about the wording 'serious flaws' in the analysis of MM05. This sentence would be based on Figure 3, if I understood properly, but as I said I think Figures 3 actually does not support this conclusion. > As far as MM05 goes, they make an clearly inaccurate claim about reproducing their earlier results. I only want to say the paper has "serious flaws", not that everything in it is wrong. > > Finally, I think it would strategically better to avoid conflicts on the particular point of whether some particular year was the warmest of the millennium or not, and to stress the fact that all reconstructions, also the new ones presented in the manuscript (with one exception) show MWP temperatures lower than late 20th century temperatures. > Up to a point (the year of the maximum is only given for information, to describe the reconstruction). > > Another conclusion could be, in my view, that the average temperature in the cold centuries in the millennium seems to be still quite uncertain. The new reconstructions, or the calculation of the leading PCs of the proxies, seem to be still quite sensitive to particular choices in the statistical set-up. > > yes, I'll try to emphasise this -- it is now in the first paragraph of the conclusions. > >