On Sep 21, 2007, Hugues Goosse, the Climate of the Past editor responsible for the Juckes article, published a statement saying that a revised version of the Juckes et al article had been submitted to “conventional” refereeing and accepted on Sept 21, 2007. He said:
On the other hand, the authors disagree with one reviewer on some points for which no clear consensus could be gained from published literature. The arguments of the authors appear reasonable from our present knowledge of the field and are presented in a balanced way. As a consequence, I decided to accept the paper for publication in Climate of the Past.
I presume that I was the “one reviewer”, although Willis Eschenbach and Mark Rostron also submitted critical reviews. Under CP policies, authors are supposed to respond to review comments. I’ve collated my review comments together with Juckes’ replies. It is remarkable how insolent and unresponsive Juckes’ comments are.
In virtually every case, I’ve provided a detailed and analytical comment and Juckes virtually never makes a direct and straightforward reply, rebutting the comment in straightforward terms. See what you think.
I’ve interlaced my original comment with Juckes’ reply in block quotes and present comments in italics, collated from information here .
1. Juckes et al allege that our analyses contain a variety of errors, but do not cite or consider the following relevant literature: the reports of the U.S. National Research Council panel on Surface Temperature Reconstructions [North et al 2006 or the NRC Panel] and of the Chairman of the U.S. National Academy of Sciences Committee on Theoretical and Applied Statistics and associates [Wegman et al 2006], or the exchange in GRL between Huybers and ourselves (Huybers 2005; McIntyre and McKitrick 2005d – Reply to Huybers).
Wegman et al concluded that our criticisms were valid and compelling. The NRC Panel specifically endorsed our key criticisms: of the MBH principal components method (p.85, 106), of reliance on bristlecone pines as an essential proxy (50,106, 107); of inappropriate estimation of confidence intervals (107); of the failure of MBH verification r2 statistic (91,105). It is really quite amazing that Juckes et al have ventured into this controversy without any consideration or rebuttal of these relevant authorities.
Para 1: We allege there are serious flaws in McIntyre and McKitrick (2003, EE) and McIntyre and McKitrick (2005, EE). We do not say that every statement in these papers is false and the fact that some statements in those papers are indeed true does not have any bearing on the the assertion that there are serious errors.
Para 2: We are reviewing peer reviewed literature and are primarily interested in estimating the temperature of the past millenium. Prof. Wegmans views on who Prof. Mann might have talked and his survey of who has written papers with whom are very interesting, but not on the topic of our review.
Juckes’ reply was completely unresponsive. Most journals require authors to consider the relevant up-to-date literature. For example, this is explicitly in Climatic Change’s policies. Both the NRC and Wegman panels were obviously important and relevant considerations and any reviewer should have noted that Juckes failed to discuss the findings of these panels. Juckes avoids mention of the NRC panel and makes an insolent comment about Wegman. Juckes completely fails to deal with the fact that both panels endorsed certain of our claims and neither panel alleged that we had made “serious” errors.
3. In MM2005a-b, we illustrated the difference between the MBH PC1 and the PC1 from a principal components analysis using covariance matrices, but also discussed results using correlation matrices – a procedure which is exactly equivalent to dividing by the standard deviation. In our Reply to Huybers, not discussed by Juckes et al, we gave a comprehensive discussion of standardization issues in the context of the North American tree ring network, illustrating PC series under a variety of standardization methods, including the method said by Juckes et al to have been omitted. See recent online discussion at http://www.climateaudit.org/?p=929. http://www.climateaudit.org/?p=928, http://www.climateaudit.org/?p=893
Para 3: We are concerned with the temperature reconstruction, not with the principal components themselves. Now that the code used in MM2005 has been made available some aspects of the calculation are clearer.
This is both unresponsive and untrue.
The claim that the code used in MM2005 was only “now” made available was untrue. The code used in MM2005 was put online in 2005. The code for MM (2005 GRL) was utilized by Huybers in May 2005 and the code for MM (2005 EE) was utilized by Wahl and Ammann in May 2005 in their Climatic Change submission. Wahl and Ammann (May 2005) said ” in relation to the method used by MM in their re-calculation of the PCs according to the MM centering convention (cf. Supplementary Information website, MM05b)” and then refer to “the R code for the re-calculation of these PCs at the MM Supplemental Information website”.
It is unresponsive because the “serious flaws” that Juckes alleged in connection with MM were in connection with the calculation of the principal components. I responded to each of the supposed “serious flaws” and Juckes’ only response here and elsewhere is the arm-waving statement that “we are concerned with the temperature reconstruction”.
As to Juckes’ professed concern with the “Temperature reconstruction”, as readers well know, we consistently and explicitly stated that our work was entirely critical and that we did not present any reconstruction of our own as we did not endorse MBH98 methodology or proxies. The purpose of any graphics showing alternative calculations were as sensitivity studies to illustrate the non-robustness of MBH98 and the inability of MBH98 to make claims about 20th century uniqueness. Even Gavin SChmidt has recognized that we did not claim to present our reconstruction.
In addition to explicit caveats in the texts themselves, the FAQ section of the Supplementary Information to MM03 stated:
“Your graph seems to show that the 15th Century was warmer than todays climate: is this what you are claiming?
No. Were saying that Mann et al., based on their methodology and corrected data, cannot claim that the 20th century is warmer than the 15th century the nuance is a little different. To make a positive claim that the 15th century was warmer than the late 20th century would require an endorsement of both the methodology and the common interpretation of the results which we are neither qualified nor inclined to offer.” http://www.uoguelph.ca/~rmckitri/research/trcqa.html
Likewise, the FAQ for MM05 stated:
“Are you saying the 15th century was warmer than the present?
No, we are saying that the hockey stick graph used by IPCC provides no statistically significant information about how the current climate compares to that of the 15th century (and earlier). And notwithstanding that, to the extent readers consider the results informative, if a correct PC method and the unedited version of the Gaspé series are used, the graph used by the IPCC to measure the average temperature of the Northern Hemisphere shows values in the 15th century exceed those at the end of the 20th century. We do not think that we could be more explicit than this.” http://www.climate2003.com/FAQ.htm
4. In our Reply to Huybers, we observed that tree ring networks were in common dimensionless units and that statistical authorities (see references therein) recommended PC analysis using a covariance matrix in such cases. We are unaware of any general purpose statistical text recommending use of a correlation matrix in such circumstances and Juckes et al did not cite any. We have never assumed that any PC methodology could extract a temperature index from the grab-bag assortment of North American tree ring chronologies and stated that the onus was on the proponent of any methodology to establish the validity of the resulting series as a temperature proxy. The NRC Panel (p. 87) considered this issue and stated that, in this case, argument can be made for using the variables without further normalization and, in effect, endorsed our position that the methodology needed to be proved from scientific (rather than a priori statistical) considerations. Obviously, this discussion should have been considered by Juckes et al.
Para 4: The units are dimenionless, but not common.
Reply: Again, Juckes’ reply is both unresponsive. He did not provide a statistical authority to support his claim of an alleged error. His reply is inconsistent: tree ring chronologies are in dimensionless units. What is his argument that the chronologies are not in “common” units, if he has conceded that they are all in “dimensionless” units.
5-10. Furthermore, even before the discussion in Reply to Huybers, we had previously discussed the impact of dividing tree ring chronologies by their standard deviation in MM2005b as follows:
If the data are transformed as in MBH98, but the principal components are calculated on the covariance matrix, rather than directly on the de-centered data, the results move about halfway from MBH to MM. If the data are not transformed (MM), but the principal components are calculated on the correlation matrix rather than the covariance matrix, the results move part way from MM to MBH, with bristlecone pine data moving up from the PC4 to influence the PC2Eˇ .
If a centered PC calculation on the North American network is carried out Eˇ ., MBH-type results occur if the NOAMER network is expanded to 5 PCs in the AD1400 segment (as proposed in Mann et al., 2004b, 2004d). Specifically, MBH-type results occur as long as the PC4 is retained, while MM-type results occur in any combination which excludes the PC4.
In total, these disprove the Juckes et al claim that we had omitted consideration of the case in which tree ring proxies had been centred [and] normalised to unit variance (standardised) (i.e. correlation PCs) or that we had committed another apparent error: the omission of the normalization of proxies prior to the calculation of proxy principal components, as asserted in their SI.
In a recent online discussion http://www.climateaudit.org/?p=928 see comment #21, I presented these paragraphs to Juckes and challenged him to justify the above allegations. In comment #28, Juckes replied: Re 21: Sorry I missed the fact that you had given an answer to some points on a later page
Para 5,6,7,8,9, 10: See comment on para 3.
Again this totally unresponsive. The comment on para 3 says: “We are concerned with the temperature reconstruction, not with the principal components themselves. Now that the code used in MM2005 has been made available some aspects of the calculation are clearer.”
I provided a detailed analysis that disproved the two “serious flaws” supposedly identified by Juckes: 1) that we had omitted consideration of the case in which tree ring proxies had been centred [and] normalised to unit variance (standardised) (i.e. correlation PCs) or 2) that we had committed another apparent error: the omission of the normalization of proxies prior to the calculation of proxy principal components, as asserted in the Juckes SI.
Juckes made no attempt whatever to rebut my comment, but merely arm-waved that he was concerned about “temperature reconstructions”
11. Juckes et al have already withdrawn a false allegation that we had failed to archive our source code and, after the above admission, should also have withdrawn these further false allegations concerning supposed errors.
Para 11: We never suggested that the code was not archived. Since publication McIntyre has revealed the location of the archived code (an editted version of the code originally used, which does not appear to have been archived), provided an updated version correcting for the omission of the function which carried out the reconstruction, and added configuration files.
Here Juckes is again mendacious. In their original article, they stated: ” The code used by MM2005 is not, at the time of writing, available” When I objected, they made a lame and inaccurate “correction” (Clim. Past Discuss., 2, S516S517).
On page 19, line 6, the manuscript states: “The code used by MM2005 is not, at the time of writing, available”: This comment should have referred to the code used by MM2005c (their Energy and Environment paper) the code used by MM2005 (their GRL paper) was made available at time of publication.
As noted above, the code used in MM2005 (EE) was available in early 2005 – evidenced by its citation by Wahl and Ammann in May 2005.
12. In making these allegations, Juckes et al also perpetuated prior academic checkkiting by Wahl and Ammann. As support for the above allegations, Juckes et al cited statements on this topic in Wahl and Ammann (Climatic Change 2006). However this article did not itself demonstrate any of the alleged errors; it merely re-stated allegations from Ammann and Wahl (submitted to GRL). However, the Ammann and Wahl submission to GRL was rejected, in part, because, like Juckes et al, it failed to consider, let alone advance beyond, the prior exchange with Huybers.
Para 12: We repeat those aspects of Wahl and Ammanns calculations which are essential to our discussion. These are placed in the Appendix. There are variations between our approach and that of Wahl and Ammann, which are referred to in the manuscript.
Again this is unresponsive. If they want to do their own calculations and refer to them, then they are entitled to do so. The results that they cite from Wahl and Ammann go beyond their calculations and they have not justified the use of check-kited results.
13. This is not the only incident of academic check-kiting in Juckes et al. Juckes et al also cite Jones and Mann 2004 in connection with an alleged error in MM2003. Jones and Mann 2004 merely re-stated an allegation from a then unpublished submission by Mann et al to Climatic Change. The submission by Mann et al to Climatic Change was subsequently rejected.
Para 13, 14, 15, 16: The major finding claimed by MM2003 concerns the temperature of the reconstruction. We are concerned here with the temperature of the reconstruction. The reconstruction in MM2003 cannot be defended.
Again, this is totally unresponsive. They may wish to contest points made in MM2003, but this does not justify academic check-kiting, which Juckes ignores here.
14. Juckes et al claimed that an alleged misunderstanding of a then unreported stepwise principal components method was a major factor in the MM2003 conclusion that MBH principal components had been incorrectly calculated. I deny that this MM2003 conclusion was incorrect. Our claim – that MBH principal components were incorrectly calculated – has been endorsed by both Wegman et al and the NRC Panel.
Para 13, 14, 15, 16: The major finding claimed by MM2003 concerns the temperature of the reconstruction. We are concerned here with the temperature of the reconstruction. The reconstruction in MM2003 cannot be defended.
Again, Juckes is totally unresponsive to a very specific point.
15. I also deny that any alleged misunderstanding of the then unreported MBH stepwise PC method was a major or even a minor factor in our conclusion that the MBH principal components were incorrectly calculated. (In passing, stepwise principal components is not a method that we have seen used outside the MBH corpus and the validity of the method should be established before its correctness is asserted.)
Para 13, 14, 15, 16: The major finding claimed by MM2003 concerns the temperature of the reconstruction. We are concerned here with the temperature of the reconstruction. The reconstruction in MM2003 cannot be defended.
Again, Juckes is unresponsive to a very specific point.
16. There is more than one discrepancy between the methodology actually used in MBH98 and the methodology said to have been used. In MM2003, we had not fully disentangled the multiple problems in MBH98 PC methodology. In addition to the de-centering problem and unreported stepwise methodology, the data then available at Manns FTP site – the url being specifically provided by Manns associate, Scott Rutherford – contained spliced PCs from different steps, which, in addition, had been incorrectly collated, so that some networks contained identical 1980 values to 8 decimal places for as many as 7 different PCs. We specifically and intentionally avoided using networks that obviously had been incorrectly collated – which included the NOAMER network – and illustrated the defective MBH PC calculations with a short network (the AUSTRAL) network, which was not affected by the collation problems. By doing so, we used a network which was unaffected by the stepwise methodology. Thus, while there were various additional problems related to the incorrect splicing of stepwise PC series in the MBH98 data archive then online, these were not a major factor or even a minor factor in the example that we presented. Instead of considering our example, Juckes et al (see Figure 2) switched the example, substituting another network (the NOAMER network) which was affected by stepwise issues – but one which we intentionally did not use in MM2003 as an illustration.
Para 13, 14, 15, 16: The major finding claimed by MM2003 concerns the temperature of the reconstruction. We are concerned here with the temperature of the reconstruction. The reconstruction in MM2003 cannot be defended.
Once again, my comment was detailed and specific; Juckes’ reply is arm-waving and unresponsive.
17. Juckes et al discuss and illustrate results using a variation of the incorrect MBH principal components methodology (mbhx) in which the short-segment standardization is carried out on a segment of 150 years, rather than 79 years. Since the short-segment standardization method has itself been found wanting by both Wegman et al and North et al, I see little purpose of introducing the mbhx variation into peer-reviewed literature.
Similarly, Juckes et al discuss and illustrate results in which North American tree ring series ending prior to 1980 are excluded from the network, resulting in a diminished network of 56 series. Juckes et al say that this analysis is responding to an issue raised in MM2005, but this claim is incorrect. In MM2003, we noted that many 1980 values were obtained from extrapolations. However, in subsequent exchanges between MBH and ourselves, it became clear that this was not a major issue in terms of yielding variant results and was not carried forward into our 2005 articles as a key issue. There are many issues which are in play (e.g. the impact of bristlecones). Given the already crowded controversy in this field, I see little purpose in reviving an issue in peer-reviewed literature that is not actually in controversy and which has negligible impact on any result.
Para 17: These comments are included to point out that certain claims which have been made in the published literature and which are known to be false (including by the author of those claims, it appears) have not been withdrawn.
This is insolent and unresponsive. The claim in MM2003 that many MBH series lacked 1980 values and were extrapolated was true. This claim is not “known to be false” by myself or anyone else. The claim was true and there is no reason to “withdraw” it. Among the litany of errors in MBH, not all “mattered”. The MBH98 use of Paris precipitation in a New England gridcell (The rain in Maine falls mainly in the Seine) does not “matter” for their reconstruction as actual geographic locations of any proxy do not “matter” under MBH “teleconnection” methodology. So this issue was not pursued further in our 2005 articles either. But it doesn’t mean that the original observation was “false”; it wasn’t.
As a review comment, my point stands: surely there are enough disputes in this matter without different incorrect PC methodologies.
18. Juckes et al misrepresented our discussion of MBH99. In MM2005b, we explicitly stated that the key issue in MBH99 was the validity of bristlecones as a proxy, not principal components methodology (which did affect the 15th century networks). We observed that bristlecones in MBH99 received heavy weighting merely though longevity and not through the erroneous MBH98 principal components method. Here Juckes et al have distorted our analysis and constructed a straw man – see discussion at http://www.climateaudit.org/?p=926
Para 18: See comment on para 3 (which says “We are concerned with the temperature reconstruction, not with the principal components themselves. Now that the code used in MM2005 has been made available some aspects of the calculation are clearer.”)
Again, this is completely unresponsive and arm-waving.
Part 2
1. Section 2 of Juckes et al is less comprehensive than and adds nothing to the corresponding review of the NRC Panel.
Para 1: There does not appear to be a corresponding review in the NAS report.
I disagree with this response, but it’s low on my priorities.
2. Section 4 presents a reconstruction (the Union Reconstruction) whose proxies differ little from those in other recent literature; the statistical analysis of the reconstruction is very deficient, with the reconstruction even failing an elementary statistical significance test recommended by the NRC Panel.
Para 2: I believe, on the basis of discussion elsewhere, that the elementary statistical test” referred to here is the Durbin-Watson test, which relates to the correlations of the residual. This test is not relevant to the composite technique. The NRC panel are concerned primarily with multiple regression techniques which are not used in the majority of reconstructions.
I stand by my comment that the statistical analysis of the reconstruction is “very deficient”. The NRC panel are not “concerned primarily” with multiple regression techniques. They consider a variety of reconstructions. There’s no reason not to test a composite with a Durbin-Watson statistic; this does not preclude the consideration of other candidate statistics, but more rigorous testing than a correlation coefficient is surely needed.
3-5. Wegman et al 2006 criticized the overlap of proxies in supposedly independent studies. Despite this criticism published prior to the submission of Juckes et al, the Union reconstruction uses virtually the same collection of proxies as Osborn and Briffa 2006 and Hegerl et al 2006. Each consists of small collections (12-18 series). However, all three studies use two or more bristlecone/foxtail series, Tornetrask (twice in Juckes et al), Yamal, Taimyr, the Yang Composite and Fishers West Greenland. See http://www.climateaudit.org/?p=967.
This repetitive use of the same proxies compromises any claim of independence between studies – a problem also noted by the NRC Panel. Because of this repetitive use of the same data, important premises of significance testing are violated, an issue discussed in economics literature. For example, Greene [Journal of Economic Methodology 2000] observed that standard distributions cannot be used with re-cycled data:
“Because the existing data series is no longer free of pre-testing or specification search and so cannot yield test statistics with known distributions. An attempt to re-use the original data implies the actual distribution of any test statistic differs from standard distributions in an unknown manner.”
Para 3, 4, 5: The idea that data can only be used once is going to need a little more justification before it gains wide acceptance. The issue is not how many times the data was used, but how it was selected. We are not claiming independence from past studies.
Again, Juckes is unresponsive. There is certainly an issue in “how the data was selected”: why Yamal and not Polar Urals Update. Juckes gives no coherent answer. The quotation from Greene states that “the actual distribution of any test statistic differs from standard distributions in an unknown manner”. Notwithstanding massive recycling of stereotyped data, Juckes purports to test for significance using standard distributions.
6. In addition to this problem, there is inadequate testing against the possibility of spurious or nonsense correlations between unrelated series [Yule 1926; Granger and Newbold 1974; Hendry 1980; Phillips 1986 and a large economics literature]. Yules classic example of spurious correlation was between alcoholism and Church of England marriages. Hendry showed a spurious correlation between rainfall and inflation. The simulations performed in Juckes et al have virtually no power (in the statistical sense) as a test against possible spurious correlation between the Union reconstruction and temperature. For this purpose, a common, and not especially demanding, test is the Durbin-Watson test [Granger and Newbold 1974], whose use was encouraged by the NRC Panel (p. 87). According to my calculations, the Union Reconstruction failed even this test, contradicting the claims of Juckes et al to 99.98% significance. (See http://www.climateaudit.org/?p=945 ).
Para 6: The Durbin-Watson test does not test for spurious correlations.
Again, Juckes is completely unresponsive. The Durbin-Watson test was recommended as a test for spurious correlation by Granger and Newbold, 1974, although it’s not the only test that should be applied. Juckes’ assertion here is false. He does not substitute any alternative test of his own. No author submitting to an economics journal would make such a foolish claim, nor would any economics journal allow an author to make such a lame response.
7. Calibration-verification is a standard methodology in multiproxy studies and was recommended by the NRC Panel (88ff). In MM2005a-b, we observed that the 15th century MBH reconstruction failed the verification r2 test (that was said in MBH98 to have been considered) and, in MM2005b, we criticized the failure of Mann et al to report these adverse verification r2 results. Our finding of negligible verification r2 (and CE) values was confirmed by Wahl and Ammann. These findings were specifically noted by the NRC panel, in their decision to withdraw confidence intervals from the early portion of the MBH reconstruction. Juckes et al conspicuously did not reported calibration-verification results. My calculations indicate an extremely low verification r2 (or CE) values for the Union reconstruction. Verification r2 and CE results for the Union reconstruction should be reported; if the reconstruction fails verification r2 or CE tests, the authors should attempt to account for the failure if they can.
Para 7: We use all the available data for calibration. Again, the recommendations of the NRC panel relate to the use of the Mann et al. technique which we do not employ, except in order to comment on past work.
Again, Juckes’ answer is untrue. The NRC panel’s recommendations apply to composites, as well as to regressions. Also, Juckes’ statement that they do not use the MBH regression technique is untrue. Their inverse regression technique, considered at length as an alternative to composite, is identical to the MBH method in the AD1000 period (the MBH method is described so poorly that it’s not obvious, but the identity of methods has been demonstrated at cliamteaudit.)
8. Reconstructions that are slightly varied from the Juckes reconstruction (but with different medieval-modern relationships) are also 99.98% significant by the criterion of Juckes et al. Obviously the two different reconstructions cannot both be 99.98% significant – evidence that neither reconstruction is “99.98% significant”. See http://www.climateaudit.org/?p=903
Para 8: The significance given is, as stated, the significance of the correlation between the composite and the instrumental temperature in the calibration period.
Again, this is totally unresponsive. The problem is that, unlike Juckes, statisticians do not claim that reconstructions are “99.98% significant”. The point remains: if two different reconstructions are both 99.98% significant, then neither can be. Juckes gives no answer.
9. Juckes et al failed to provide any statistical references for the results in their Appendix 1, nor any proof of the claimed optimality (or a reference of the fact). They assert a noise model, but do not show that they carried out any tests to demonstrate that the noise model in Appendix 1 was applicable to the actual proxy network. Inspection of the residuals in the individual series strongly indicates that the noise model of their Appendix 1 is not valid – see http://www.climateaudit.org/?p=938
Para 9: The appendices are elementary and are provided to clarify the formulae used.
The comment stands. Statistics is a well-developed field. There’s no need for Juckes to develop home-made results, which may ignore some subtlety familiar to proper statisticians. If the results are as elementary as Juckes says, he should be able to provide a citation.
10. I was able to replicate some of Juckes CVM calculations, but not all of them. In the Union reconstruction, there is an unreported flipping of the Chesapeake Mg-Ca series, the procedure for which is not described. The mbhpc reconstruction appears not to have carried out a flipping of PC series said to have been carried out. MBH99 said that bristlecones should be corrected for CO2 fertilization. We disagree that MBH99 carried out a relevant correction, but Juckes et al appear to have use PC series without any effort whatever to apply such a correction – see http://www.climateaudit.org/?p=930
Para 10: Our main results do not use the Mann et al. PCs. We used them in order to evaluate and comment on past work. The flip in sign of the Chesapeake series was an error. This is corrected in the revision.
The orienting of series was supposed to be done in the computer programs. It’s not satisfactory that Juckes goes in after the fact and manually flips a series to match his preconception. Where did the error originate? Their “main” results may not use MBH PCs, but some of their subsidiary results do and Juckes is unresponsive.
11. Juckes et al have put source code online (good), but the source code contains virtually no relevant comments and seems to be a grudging accommodation, rather than an earnest effort to illuminate methodology for subsequent readers.
Para 11: The source code is the code used to carry out the calculations. It is provided to ensure full transparency.
Comment stands. The code is better than nothing, but it should include comments.
12. Juckes SI Figure 1 used rms normalization without any disclosure or explicit justification. Rms normalization is not used elsewhere in the study or, to my knowledge, in the relevant paleoclimate literature. It has the effect of minimizing the difference between MBH and other PC studies. I see no purpose whatever in permitting its use in this figure – especially without any disclosure of the methodology. See http://www.climateaudit.org/?p=897
Para 12: This will be changed.
13. I have tested some of Juckes CVM reconstruction, finding that trivial variations can yield different medieval-modern relations e.g. Esper CVM without foxtails; http://www.climateaudit.org/?p=885 ; Moberg CVM using Sargasso Sea SST instead of Arabian Sea G Bulloides wind speed and Polar Urals update instead of Yamal – see http://www.climateaudit.org/?p=903 and http://www.climateaudit.org/?p=887 Juckes justification for not using Sargasso Sea SST is not convincing http://www.climateaudit.org/?p=898 , nor is the exclusion of the Indigirka River series of Moberg et al 2005, which is an extension of the Yakutia series used in MBH98 – see http://www.climateaudit.org/?p=901
Para 13: The Sargasso Sea series finishes well before the end of our calibration period, so cannot be used in our reconstruction. It has been used in one peer reviewed study and cited on at least two web sites with its dating erroneously shifted 50 years forward, so that the last data point, which represents the 1900 to 1950 mean is instead presented as the 1950 to 2000 mean. The data file stored at the WDCP is ambiguous in this respect, but the data was clearly collected at a time when it could not represent the 1950 to 2000 mean. We have put all the data used in our study online: the Indigirka series is not available for publication in this way.
Juckes is both inaccurate and unresponsive here. The last data point in the Sargasso Sea study is based on modern sample information – which is essential for calibration! (Also note that tree ring chronologies routinely combine information from living trees and subfossil trees, where the data properties are different.)
Juckes is unresponsive in that my points remain unchallenged. One of Juckes’ coauthors (Moberg) used the Indigirka series – so Juckes should be able to put it online. And think about it: his defence to this point is that one of his coauthors won’t put the Indigirka data online and therefore it “can’t” be used. As Juckes said earlier, the issue is how data is “selected”.
14. Juckes et al Table 1 contains numerous geographical mislocations. Table 1 shows lists the Tornetrask site 4 times under different alter egos, using 3 different coordinates, none of which are correct. The two independent foxtail sites are only about 30 km apart (the coordinates being inaccurately reported in Juckes et al.) The Union reconstruction used two different versions of the Tornetrask site (which are obviously not independent) and neither justified this duplicate use nor the similar duplication of foxtail and bristlecone sites.
Para 14: The geolocation information does not affect the results: it will be corrected in the revised version.
Juckes does not respond to the duplicate use of foxtails, which, with correct locations, are shown to be very close.
15. Juckes failed to evaluate the validity of individual Union proxies in light of criticisms by the NRC panel and others. The use of percentage G. Bulloides as a temperature proxy was criticized by David Black, author of a G Bulloides series from Cariaco. Without addressing such criticisms, Juckes et al used a percentage G. Bulloides series from the Arabian Sea in the Union reconstruction – see http://www.climateaudit.org/?p=957 The NRC panel specifically said that strip-bark bristlecones and foxtails should be avoided in temperature reconstructions. Without addressing this criticism, out of only 18 proxy series in the Union reconstruction, Juckes et al used no fewer than 4 bristlecone and foxtail series from one gridcell.
Para 15: There is some confusion here between the requirements of different analytic approaches. The revised version seeks to make our modelling assumptions clearer. In particular, we do not assume that the signal to noise ratio in individual proxies is greater than unity. A simple estimate suggests that is not. In this situation selecting proxies on the basis of their individual correlations with temperature is inappropriate. The peer reviewed literature does not have clear evidence of a substantial CO2 fertilization effect. We note that all the proxies are influenced by factors other than temperature.
Again, Juckes is unresponsive. The NRC panel said that bristlecones should be “avoided” without limiting themselves to CO2 fertilization as an explanation. Notwithstanding this Juckes used 4 bristlecone/foxtail series and was unresponsive to this comment.
Closing Comments
As I review this, it is remarkably annoying to see how unresponsive Juckes was to the above comments, the unresponsiveness being so complete as to be insolent. I cannot imagine any author submitting to an economics journal making remarks like this.
As I re-read the above interlaced comments, I see virtually no case where Juckes has responded to my comments in a straightforward manner. For many of these comments, I am obviously knowledgeable as I am directly involved. If Juckes has responded in a straightforward manner, then Goosse and the subsequent referees might have been able to assess the merits or lack of merit of the argument. But Juckes arm-waved.
In his online comments at CPD, Goosse made no effort whatever to require Juckes to be responsive to criticisms – which, whether he agreed or disagreed with them, were detailed. In his online comments, Goosse commented only on Anonymous Referee #1, asking Juckes to accommodate these comments. Goosse made no effort whatever to ask Juckes to make adequate responses to my comments. Without obtaining any online response, Goosse concludes:
On the other hand, the authors disagree with one reviewer on some points for which no clear consensus could be gained from published literature. The arguments of the authors appear reasonable from our present knowledge of the field and are presented in a balanced way.
What a feckless and indolent bit of editing.
UPDATE: I wrote to MArtin Claussen about this and he has responded: see below. CP policies here
Climate Audit 
294 Comments
This is what happens when neither the author nor the editor understands what the reviewer is saying. Under such circumstances the editor is supposed to seek out additional referees with the proper expertise, but obviously this did not happen. I personally am dumbfounded at some of the mistakes Steve found in the paper, which range from serious to hilariously bad, and none of which should be dismissed with hand-waving. I wish I could get away with such handwaving, but have never had such luck ever.
For convenience, updated links to the two McIntyre comments to CoP re: Juckes et al. can be found here:
https://climateaudit.org/2007/09/14/is-juckes-et-al-2006-peer-reviewed/#comment-428161
Juckes was probably published to keep the consensus “check-kiting” science from hitting a dead end.
I’m starting to be very affraid of how climate science will be viewed in the future. The flagrant disregard of the scientific method, plus the bullying is sure to be used one day to teach the dark ages of science.
This is unbelievable. I have sometimes been on the receiving end of critical questions from reviewers and sometimes have been a critical reviewer myself. In either case specific criticisms require specific and informative answers. As Steve notes Juckes’ replies fall into neither category. In this case a reputable journal would not publish, or send to a third reviewer.
But as Steve has often said: “Hey this is Climate Science!”
P.S. you didn’t really believe that Mann and his cronies would agree, forgive, or forget what Steve did to their precious Hockey stick. This is the start of their (proxy) fightback.
Oh yes and by the way, Juckes’ comment in point 15 that “The peer reviewed literature does not have clear evidence of a substantial CO2 fertilization effect.”
Really???!
What about this meta analysis to start with?
Ainsworth, E.A. and Long, S.P. 2005. What have we learned from 15 years of free-air CO2 enrichment (FACE)? A meta-analytic review of the responses of photosynthesis, canopy properties and plant production to rising CO2. New Phytologist 165: 351-372.
Climate of the Past must be pretty desperate for papers in order to accept an author’s response like that one! It would certainly have been laughed out of any self-respecting bio journal.
RE: #3 – You of course assume a free and open society in the future, in which such a critical history would be not only allowed but encouraged. It may well turn out, that today’s quacks will become tomorrow’s heroes who “contained and mitigated the destructive factions who threatened to destroy the Earth.”
Juckes would no doubt think of himself as a man of principle, he is a member of the Green Party in the UK, and has stood for Local Council election in the Oxford area.
If he were a sensible, intelligent man of good will, could he not have quietly buried the paper. He could quite easily have come up with something about “needing more work” etc, and it would all have been forgotten about in time. Now he has attached his name to a paper which SteveM and Willis (and his contributors) have shown to be deeply, and widely flawed. Juckes and his fellows must know that, and if they don’t, it only increases the dangerousness of them having any impact in the literature on this subject.
Perhaps it was because they would have had to return the Dutch grant they got. Perhaps it was the “we can’t prove it this time, but other evidence backs us up, so we must be right” argument.
The Stern Report on the financial cost of global warming has found that climate change could not only devastate the environment and cause mass migration but could cut the world’s annual economic growth by 20 per cent.
It calculates that the total global cost of climate change could run to $9 trillion and it warns there is only a small window of 10 to 15 years to address the problem.
It is truly pathetic, and tragic, that policy decisions of this magnitude are to be based on such appallingly poor foundations as the Juckes et al, and other similar papers.
Lord protect us from meddling, statistically unqualified, “do gooders” from Oxford University.
OT request to Steve Mcintyre (or anyone)
I’ve read all the ‘where’s waldo” threads and was wondering if you have or could produce GISS temps plotted for each continent, to show graphically that most of the warming is in the Artcic and NE Hemisphere.
If these already exist where can i find them?
Thanks!
Re #9 windansea I’ll provide a link on Unthreaded #20.
Mark R. says “Juckes would no doubt think of himself as a man of principle, he is a member of the Green Party in the UK”
That explains it all. His Green Party causes are more important than the science. He probably believes himself to be saving the planet by pushing his false science. Juckes also probably believes that all of Steve M. criticism are wrong because the cause is righteous. Post-modern science.
I want a degree in Meta-Science. Should I apply to Oxford or Columbia?
Re:4
Keith. Yes, mindboggling.
Re:8
MarkR. Interesting that. A government grant and active Green. The thought that this might have any bearing on his research surely wouldn’t be cricket. As a “test” however, why not replace Green with Tory and government with business. Tar and feathers anyone?
Steve,
I’ve said it before: Climate of the Past needs Juckes more than it needs McIntyre. You have never published, nor do you seem intent to publish in that journal. You have no academic position, no publication record apart from a paper in GRL (E&E doesn’t count). The publication system is about structure and hierarchy. It is also about order. Scientific “truth” and advancement of knowledge is the avowed goal, but the underlying sociological forces are what really drives the process. Read Bruno Latour, the Actor-Network theory. You don’t have the right network to publish in journals. Juckes does. What do you expect? This is all very predictable.
Who is Hugues Goosse?
http://www.astr.ucl.ac.be/index.php?page=hgs%23HomePage
Goosse H., Renssen H., Timmermann A., Bradley R.S. and M.E. Mann, 2006. Using paleoclimate proxy-data to select optimal realisations in an ensemble of simulations of the climate of the past millennium. Climate Dynamics, 27, 165-184, DOI: 10.1007/s00382-006-0128-6
Told ya! It’s all about networking.
After reading this and related material, I’ve concluded that there is a new school of thought emerging in the climate sciences. An apt name for it would be the “Because-I-Told-You-So” movement, or BITYS for short.
I think the cloistered air at univerisities is to blame. Most of these people are so deferential with peers that they wouldn’t think of harshly criticizing them, if for no other reason than it might provoke an attack on their own work. This is what separates them from the business world where incisive criticism is necessary for organizations to improve and prosper.
And while they may be deferential to their peers, their hostility to criticism from outside the cloister’s walls is palpable.
#16 — Looking a little deeper in your link, thank-you Hans, we find this. Hugues Goosse is a true believer. Like Juckes, apparently.
As is usual in GCM science, Goosse’s GCM fit on the linked page shows no physical error bars; merely numerical standard deviations. It’s as though these people were never trained in the basics of the physics they practice. But they must have been so trained, of course. And so we see case after case of evidently willful professional negligence.
It’s not academic cloisterism, duke #18. It’s the positive feedback of reinforcement produced by the self-righteous resonance between true-believing scientists and the extreme propaganadists of environmental organizations. The latter provide the justificationism and the former tailor their interpretations to suit it. The circle is closed and hermetic.
On re-reading the above collation, I was again struck by how unresponsive Juckes was to the Review Comments and, more particularly, how Hugue Goosse failed to discharge his obligation as CP editor to require Juckes to comply with teh CP policy stating:
Accordingly, I sent the following letter to Martin Claussen, co-editor in chief of Climate of the Past, cc to Juckes and Valerie Masson-Delmotte (with the above collation attached):
By the way, Steve M., your experience with Hugues Goosse as editor of CotP is the opposite of the usual case in science. Typically, editors take persistent negative reviews more seriously than author rejoinders. When a dispute is protracted, a good editor should either come to grips with the paper him/herself and adjucate the issue with understanding, or else recruit an independent reviewer.
This rarely, if ever, happens however. More usually, the editor resorts to jerrynorthism and just wings a judgment. That judgment is almost invariably in favor of the reviewer’s call for rejection. That’s the safer way, because a wrong call in favor of the author makes the editor and journal look foolish. But a wrong call in favor of the reviewer just means the paper will be published elsewhere and no public injury is ever likely to be done to the reputation of the editor or the journal.
So, the editor will find something in the paper that is somehow questionable, will then decide that justifies the reviewer’s rejection, and finally inform the author that the manuscript is rejected.
But exactly the opposite happened with Goosse’s editorial decision for Juckes’ manuscript. Despite cogent reviewer objections, and diversionary author responses, Goosse as editor found in favor of Juckes. He accepted an obviously poor paper, risking later public exposure. That doesn’t mean Goosse is operating in cloistered academic safety. It means that Goosse is strongly pre-disposed toward Juckes’ result and interpretation. It means the review process was almost a conscious sham. The outcome was likely never in doubt, right from the start. It would have taken the equivalent of a nuclear explosion to cause Goosse to reject Juckes’ paper.
#20. Obviously I’ve seen that with Wahl and Ammann. They intentionally withheld information from Stephen Schneider in the initial review process about the rejection of the GRL article and pretended that it was still in play after it was rejected. They were unlucky that I was a reviewer and caught them in this mendacity. I reported it to Schneider. I’ve learned over the years that you can’t do business with people who are dishonest and this bit of dishonesty by Ammann and Wahl was top of my list in review comments. I urged Schneider to disassociate his journal from them. The result: I was terminated as a reviewer and the article accepted.
I know what these journal are going to do. But I’m not simply going to acquiesce. I’ll do whatever I can to make them justify each bit of dissembling. I’ll also put the dissembling in the public eye so people can see for themselves. No free passes.
#2 Reid:
“check-kiting science”
That’s a sharp and funny turn of phrase. A1
Re: #19
Re: #20
Those comments sum up well my skepticism of the process while my skepticism of the forecasts/predictions/scenarios remains mired in the lack of understandable levels of uncertainty attached to them.
Alas, I don’t get gobsmacked by climate science anymore. Unfortunately this climate literature scamming seems to be par for the science.
Post Modern Science – it is all about making the facts fit the narrative.
I’d rant and rave at length about the political ramifications, but it would be severely OT.
So are we going to see a further escalation in the proxy war? I hope so.
I have never had a paper reviewed. However, I have been design reviewed. This project would have been canceled with these sorts of answers.
#21 — Steve, maybe it’s time you, or you and Ross, wrote up an article documenting the dishonest treatment your work has received at the hands of authors and editors in climate science. The article should be for a popular audience, suitable for something like The Atlantic Monthly.
It’s time the public at large caught wind of the real corruption that infects climatology. As things are going now, the controversy is hidden in professional journals, where no one outside the privileged few ever venture or can even understand. That condition entirely suits the true believers, who will be content to endlessly engage polemics hidden within specialist journals all the while opportunistically advertising their insupportable fears to the public. And the opportunity is widely provided by a credulous media convinced that their political scruple is the measure of the science.
#23, Kenneth, I have an article under submission at Skeptic addressing exactly the issue of physical uncertainty. It’s been reviewed by professionals and is also written for an intelligent lay audience, with a Supporting Information document that contains all the calculations. It shows that the physical uncertainty in GCM predictions is gigantic compared to the temperature trends they’re purporting to predict. E.g., for a centennial predicted rise of 3.7 C, a minimal GCM physical error is (+/-)111 C. Suppositions of the certainty of future climate warming due specifically to human-produced CO2 are entirely without scientific merit.
I would bet dollars to doughnuts that there is a Congressional staffer assigned to watch this site and collect ammunition for any upcoming fight in the US Congress about implementing any kind of OCO mitigation scheme for the USA.
Climate Science is playing with fire.
The EU has already bought into The Narrative. No worries there. Except for the Brits. About 60% of the population there thinks that Global Warming is a tax extraction scheme.
26, I agree that while several aspects of this rather unwieldy issue have been exposed in the press, this particular one – this crass scientific malfeasance – hasn’t, and needs to be. The problem is, how to condense pages and pages of esoterica into something readable, and yet relate that the the actual documents and correspondence. That would require a very, very skilled writer.
Pat Frank (#20),
I can vouch that all of what you say is true based on personal experience. What happened to quality journals, Editors, and reviews?
IMHO it is because there are too many journals publishing too many questionable manuscripts based on questionable science. The result is exactly what you see.
Jerry
The British government’s chief scientific advisor has set out a universal ethical code for scientists.
Will these be applied to Juckes, and Jones, and Briffa etc et al, and the others? Let’s hope so.
Shouldn’t Goosse have declared a conflict of interest? He’d already co-Authored several papers with the “Hockey Team”, whose work was being reviewed. When (and it is when and not if) the General Public finds out about this…..
The “Journals” are run on the same basis as all printed media. The actual content is the booked advertising space. The rest is just filling.
#29 – Jerry, like you I’m truly shocked by the almost wholesale jettisoning of standards in climate science. It’s scandalous, and I’m certain future historians of science are going to have a field day with this.
The problem doesn’t seem to be the proliferation of second rate journals, editors, or science, though. For example, look at Ralph Cicerone stepping in to personally “review” Jim Hansen’s splice of the Indian Ocean proxy that Steve M. exposed awhile back. This happened at PNAS, one of the most venerable and scientifically respectable of journals.
In front of Congress, Cicerone testified in 2005 that, “gases trapped in dated ice cores have shown that for hundreds of thousands of years, changes in temperature have closely tracked atmospheric carbon dioxide concentrations.“, leaving the impression that CO2 led the changes in temperature rather than trailed them. This is conscious dishonesty by a man who is a top-ranked scientist and the president of the US NAS itself.
Likewise, Science and Nature are editorially committed to AGW. We even have Donald Kennedy stooping to a degraded polemic on 27 July 2007 in “Climate: Game Over,” writing this: “As data accumulate, denialists retreat to the safety of the Wall Street Journal op-ed page or seek social relaxation with old pals from the tobacco lobby from whom they first learned to “teach the controversy.””
[snip]
It appears to me that the real problem is that many (most?) scientists, including excellent ones, don’t really understand the meaning of the scientific methodology they practice. They use it merely as a tool in the lab, but discard it in their political or social thinking.
In the case of AGW, they have taken the disastrous step of actively excluding the objective methodology of science even in the doing of their science. It’s a local triumph of intellectual romanticism. In an 8 April 2005 editorial, Kennedy decried the ‘twilight of the Enlightenment.’ In fact, it is he who is eclipsing it. As the editor of one of the most prestigeous science magazines he has substituted his righteously sentimentalized environmental politics for the often frightening sanity of objective thinking.
It was Einstein who famously said that it would take only one scientist to refute Relativity Theory. This insight is the needle that unfailing punctures the “consensus” balloon, and the same insight from which Donald Kennedy and many others have determinedly turned their faces.
Mark wrote: The “Journals” are run on the same basis as all printed media. The actual content is the booked advertising space. The rest is just filling.
I’m not sure how the revenue streams operate now but the journals used to be heavily dependent on university libraries and departments. They paid very high subscription fees. The larger public libraries did the same. Sometimes subscriptions were also paid for faculty members. Circulation was larger than you might expect. It added up because actual printing and mailing costs are very low.
I suspect advertising now supplies a lot of revenue for some journals. The costly print subscriptions probably live on even though information access has moved to the web.
In the DElft University library the trend is toward online subscriptions. eg Recent copies of Nature you won’t find on the shelves anymore.
#22 — I’m pretty sure Steve M. coined that term. It’s deadly accurate, and I think he first used it in reference to the Wahl and Ammann paper.
If Juckes is a member of the Green Party then this should be stated along with the article. I see no mention of an obligatory ‘declaration of interests’ section that must accompany any submitted articles on the CP website.
The more a learn about ‘climate science’, the more I believe ‘climate science’ is a contradiction in terms.
Jesus, this is beyond belief:
The peer reviewed literature does not have clear evidence of a substantial CO2 fertilization effect.
Every friking greenhouse tomato we eat is composed mainly from fossil carbon (NG is combusted to provide excess CO2 in greenhouse):
a minimum carbon dioxide concentration of 1000 mmol mol-1 is recommended during the day as long as the greenhouse is not venting.
Just Google tomato carbon dioxide greenhouse.
There are hundreds, probably thousand peer-reviewed published papers on carbon fertilization, unanimously proving that carbon fertilization has huge impact on plants. CO2science.com is full of examples.
I thought nothing in Climate Science could astonish me any more
I don’t think skeptics/denialists need to worry about the AGW crowd, they are in the process of burying themselves (re circa 2010 onwards). I would not take it too seriously this whole matter….because it aint happening
I found another one (and its published at CoP too):
Climate of the Past
Could “Climate of the Past” refer to the climate of intolerance that existed in the Middle ages when the Inquisition was at its height and all dissenting views were denounced as heresy?
Just a comment on SM’s letter.
No editor of any journal will like to read the word
“defamatory” in a communication with an author/reviewer.
The issue of defamation arises in SMs view because the author
uses the word “error” in respect of SMs publication.
The nature of academic publishing is that
(i) Many statements are made that “X” or “Y” is wrong.
(ii) Some of these statements are of themselves incorrect.
If each verified instance of point (ii) was ground for
a legal action, then the whole publishing system would
collapse.
So SM should not raise that issue with any editor unless
statements are made that go beyond the strictly technical
issue (e.g. “SM is on a $100,000 retainer from an electricity
utility”). As I type this, I expect dozens of deliberately
incorrect statements are being made by authors/referees in
order to get something published or to kill a publication.
Some of these disputes are actively driven by deliberately
malicious acts. So SM should not feel like his experience
is in anyway unique!
If SM wants to step onto the playing field, he should not
be surprised the other guys play dirty. SM needs to learn
a few dirty tricks to help him survive. With regard to
his email to the editor, it stinks of “SM getting mad”
but I do not see how it is going to help “SM get even”.
The line about “defamation” will tend to make any editor
less sympathetic to SM.
SM needs a course on how to be vicious. e.g. SM should have
been smiling nicely at Goosse, while stabbing him in the back
by writing to the editor from the very outset. When I get
an idiot referee, I
(a) Am often collegial in my direct response to the referee
and try to smooth things over
(b) However, my separate communication to the editor is
really about discrediting the professional competence of the
referee. More or less setting the scene for me winning any
eventual adjudication.
When you enter the den of the mafia, there is no point in being
a boy scout.
#42. I realize that people allege error all the time. We alleged MBH made errors. Your point is also valid – that many allegations of error are themselves erroneous. Life goes on and journals go on.
I have no intention of taking any legal action BTW. I wouldn’t suffer material monetary damages by Juckes’ allegation. Monetarily, I would be better off if I were driven from the field and went back to mining deals. In addition, the journal did send the Juckes revision out to “conventional” referees and they could easily argue that this discharged their duty of due diligence in a legal sense.
Having said all that, if an allegation of error is made, it seems to me that a journal would still have a duty of due diligence to ensure that there was some reasonable foundation for the allegation. In the Review Comment process, I responded in detail to each allegation and Juckes did not present any rebuttal to my responses. Editor Goosse negligently did not enforce CP policies requiring Juckes to respond (other than insolently) to the Review Comments and we shall see whether the referees paid any attention to the Review Comment exchange. My guess is that they paid no attention to it whatever.
In practical terms, my guess is that the CP response will be what it will be, regardless of whether I modified the language a little.
RE: Declarations of conflict of interest. It is my observation that true and far reaching declarations are few and far between in all fields and industries. However, I can at least try to lead by example.
I have a financial interest in the design, manufacture and sale of products which are deemed “green” and “associated with lower energy consumption.”
Re#42:
When you enter the den of the mafia, there is no point in being
a boy scout.
Wisdom of street pusher does not apply to Mario Puso.
Jim (#42),
The den of the mafia says it all. It has become more of a game of politics than science. A qualified, objective editor would easily see thru any politically motivated review and discount it and also see thru obfuscation by an author. Unfortunately, many times (as in Goose’s case) the editor is biased, compromised, or incompetent and selects the reviewers accordingly. I mentioned an example of this earlier when we offered to provide a mathematical proof that a reviewer’s argument was incorrect. The editor in question would not consider the proof because he was receiving grant money in the area that the proof showed was of questionable scientific value.
A minor conflict of interest on the editor’s part and clearly the reason the reviewer was selected by the editor. Steve M. should not have to learn to play dirty. The journals need to choose qualified, objective editors and that has not been the case for these journals. The journals that do not
(or cannot) choose qualified editors should be exposed and avoided by competent scientists.
Ralph Cicerone is an NCAR senior scientist. Any conflict of interest there?
Jerry
Re: Jim’s comment in #42:
Jim, I would respond along those lines also if it were not for the efforts that I see here at CA that Steve M makes to put these issues in the public eye so people can see for themselves. He adds some inside facts on the statistical issues as well as looks at the involved personalities that I find most interesting and intriguing.
Probably one of the most fascinating reactions that Steve M receives here and at other blogs is those who come to defend what I see as the indefensible. Sometimes it becomes most apparent that the defenders simply want to avoid any chinks in their armor that might detract from their message and those responses can be rather humorous. Other times they provoke a reasoned response, of which, the validity and reasoning process used, the reader can judge for themselves.
See Steve M in # 21:
Jim,
You may run your life as you see fit, of course, and if the notion of “winning at all costs” seems to have merit to you, then by all means, pursue your interests in that way. However, in the end, I think you may find that what you have won is not nearly worth what it cost you. Personally I applaud the way Steve M. has maintained his integrity throughout this entire process.
#42, Jim:
For the record, not all defamatory remarks are necessarily actionable – although all actions for libel require a defamatory comment. Defamatory just means injurious to one’s reputation. Publicly assailing one’s competence by attributing “errors” to them seems injurious to one’s reputation. Whether the claim is true or false, it’s defamatory if a reader would hold Steve M. in less esteem than before.
You’re right that the editor may not read the definition of ‘defamation’ this way, but if he’s in the publishing business he should know better.
MAtin Claussen has responded as follows:
Am I misreading things, or is Martin Classen an amazing man when it comes to ad hoc logic, and thinking on one’s feet! Amazing, albeit, disgusting.
#50
In other words, he’s offended that you’re posting on this blog.
This part is interesting. If memory serves, their webpage denominated you guys as Reviewer #2, Reviewer #3, etc. Now it seems you guys were trespassing in this process, and your ‘unsolicited short comments’ weren’t worthy of comment. I wonder what it means to say the discussion phase was “closed automatically” [presumably, he means to the invited reviewers who chose not to respond in time…]. Does he mean the software timed out and wouldn’t accept comments from the tardy reviewers [if any existed…], or that they just decided to ignore anything after some point in time ?
Wow…so what he is saying is: “we solicited comments in an open discussion forum with no intention of making sure that the published paper dealt with serious issues raised by those comments”?
It looks like he is saying that even though they had one formal reviewer and 3 sets of obviously thoughtful and well justified unsolicited comments, that they went out and got 3 other reviewers whose names they won’t release and used their reviews as justification for ignoring the thoughtful and well justified unsolicited comments.
If that is the case, I have to wonder what the purpose of the online review forum is? If they intend to ignore the online comments, why even bother putting the forum online unless it is to give some illusion of open review while preserving the good ol boy network of peer review backslapping that was criticized by Wegman?
Claussen’s reply is interesting. Notice that he states that the “Short Comments” submitted by Willis Eschenbacn, Mark Rostron and myself were not considered in the review process. Claussen says:
Now in their policies, they say:
I guess that they were just pulling our legs. Teasing us into thinking that such Comments would be considered, when they had no intention of considering such Comments in their review process. Climate scientists are such pranksters.
Claussen says:
“Political pressure” – give me a break. I sent an email to him as he says that I am “free” to do. I didn’t ask the German Parliament into intervene or approach his funding agencies. What conceivable basis would he have for alleging that I’m applying “political pressure” to him?
As to “irregularities”: their policies say that they require authors to have “answered the Referee Comments and relevant Short Comments” prior to re-submitting. Juckes obviously did not do so and editor Goosse failed to require him to do so. So yes there was an irregularity. It may be “distasteful” to point it out, but the culinary failure occurred when Goosse allowed Juckes to proceed without answering the relevant Short Comments according to CP policy.
If CP editors view the Short Comment procedure as a sham, then they should change their policy stating that authors are required to answer “Short Comments” to reflect the sham so that third parties, such as myself, don’t waste their time taking the policy at face value.
I remember Willis even wondering why they were taking so long to answer the comments and what good is the whole system if nobody did. Here’s the page where he asked:
Willis’ question
So here we have a journal attempting to push the boundaries and have open discussion on papers in full public view.
But when it comes to discussing aspects of how they run their journal, and whether they have adhered to their own policies, that should be done in private, and to do so in public is tantamount to political pressure?!?
Can anyone else see the irony in this?
56, what I can see is not only irony, but a strong resemblance to what goes on in the larger media. The “circle the wagons” mentality here is very much like the same mentality on display at the New York Times (regarding Jason Blair), or with Dan Rather’s latest escapade. Or about 1023 other examples that I could serve up.
RE: #55 – “Received and published, 15 November 2006”
It says what it says. There is no differentiation in their “publication” system between “OK” comments, and “short comments” (let alone “to be ignored” comments from so called “denialists!”)
Some further CP policies.
Claussen said:
Now their policies say:
In the case of the Juckes revision, if the editor sends it out for refereeing, he is supposed to do it “in view of the access peer review and Interactive Public Discussion”. The Interactive Public Discussion obviously raised substantive issues with various claims made by Juckes, some pertaining to MM, some pertaining to their statistical methodology.
Now here’s an interesting phrase. Editor Goosse was supposed to consult referees in this second phase not as de novo referees, but “in the same way as during the completion of a traditional peer-review process”. I’d be interested in interpretations of this phrase. I would assume that “completion” referees are checking for whether the revision resolved issues raised in the first phase. In this case, if Goosse failed to draw their attention to the Interactive Public Discussion and failed to ensure that their comments were responsive to these issues (and merely sought de novo opinions), then he has once again been negligent in implementing CP policies. This doesn’t necessarily mean that he’s a wicked person or that he did it maliciously. However, it doesn;t seem to be consistent with stated CP policies.
RE #55
The response to Willis’ question can be found here.
Are you sure that’s not 1024 Larry? 😀
mosher, RC, climate insensitivity, comment #185…. lol
The response Willis question – That didn’t work so here is the address: http://www.climateaudit.org/?p=925#more-925
RE: #59 – (In a way too hip, quasi beatnickish voice)Oh, man, rules? Rules are for squares ….. man! Rules are made by the Man, man! Bad buzz, man, bad buzz!
#60: Goosse (the editor):
Claussen (co-editor in chief):
These guys are so funny 🙂
Steve: Note that the above quote is from an email from Goosse to Willis Eschenbach here: http://www.climateaudit.org/?p=925 .
#62: Ah, even better, Goosse:
Give ’em enough rope ….
Jean S is, as usual, sharp as a tack in his references. Folks, look at Willis’ prior correspondence with Goosse (that Jean S mentions above) http://www.climateaudit.org/?p=925 . Willis specifically corresponded with Goosse about Juckes’ failure to answer comments. Goosse wrote back to Willis assuring him that Juckes would be required to answer the Short Comments.
As it turns out, Juckes did not make anything other than an insolent response to the Short Comments and even thee were made long out of time – in March 2007. In reply to Goosse’s letter, Willis firmly put him on notice that he had an obligation to see that the questions were answered:
Here’s a more extended quot from Goosse’s response (Again pointed out by Jean S):
So it’s not as though Goosse had not been put squarely on notice that Juckes had failed to respond to Short Comments. Willis had explicitly and clearly done so and Goosse still failed to carry out his obligations as editor. And as Willis made clear, it was Goosse’s obligation not anyone else’s. Goosse admitted that the editors needed to check that the authors had “answered all the relevant comments”.
Now Claussen says that only the invited Referee Comments were considered. What duplicity.
In other words, the open part with the short reviews was a sham, the authors responses to, and the short reviews themselves, were not taken into consideration. It was the usual stitch up with members of the club presumably reviwing each others work.
Bt the way, I thought the first invited review was useless.
I’m begining to think that the best way might be to publish allegations of incompetence, and provoke a libel action, sort this out in a proper Court of Law, not these Kangaroo Courts.
#67: Steve, the credit goes to Cliff (#60).
Wagons… and circling, come to mind.
Mark
The publication has lost all credability, Climateaudit has just increased it’s own and climate science as a whole has had another brick removed from it’s supporting structure.
Kudos to Al Gore who invented the internet.
Actually, Hans, I think it was Tipper who invented the internet. Al just took the credit for it.
Denis_Dider Rousseau, another editor of CP copied by Claussen, wrote
#54, re: political pressure.
I believe this may be (weak) evidence that he is reading this blog, as you have made comments here that could be taken this way (to paraphrase, “they’ll publish whatever they’re going to publish, but I will not shut up and will make this known to the public no matter what”). Otherwise, I couldn’t guess why he said that.
#67: Well, that’s going to be a bit of a problem for the journal… I am referencing more and more people every day to CA so that they might watch this and all the other debacles unfold.
From #50: **The purpose of the discussion phase is to air disagreement. However, we do not expect reviewer and dissussant to come to an agreement in every case, and in that case, we rely on the chosen reviewers and editors. Your are free to publish your
opinion and to publish papers that refute whatever you agree with in the
paper by Juckes et al.**
Saying that they “rely on the chosen reviewers and editors” verifies what Dr. Wegman said about a club or society. Only the SOCIETY opinions matter.
Take a look at this interesting article on open source journals to get an idea how completely Goosse and Claussen have subverted the professed open review principles of their journal.
Excellent article. In taking this route the author quite rightly makes the point that weak and unsuported papers will not be published in the first place owing to the writers knowing in advance that they cannot restrict review to their kinfolk. It’s what has happened here for a long time.
Re: #50
Even though it may not be appreciated by the editors in question, thanks much Steve M for making those comments of Claussen public. They provided a good laugh and truly are material for a comedy routine. I particularly liked the comments excerpted below.
Why cannot these people simply play it straight and say what any half-way intelligent person can deduce: the open forum did not work the way they evidently planned it and thus they closed it.
A possible misspelling here? Shouldn’t that have been “…Rules are made by the Mann?”
But seriously, folks; The Editor of CotP is either incompetent and/or corrupt. He appears to be violating his own rules. But then again, what rules does the hockey team play by? Are there grounds for the publication itself to be discredited…that is, not acceptable for citation by “respectable” journals.
Consider the implications of the acceptance of this paper. For the next few years it will be cited to refute legitimate counterclaims. It may even be used to prevent the publication of some genuine work by carefully selected peer reviewers. The scandal of the AGW cabal continues to amplify.
#26, 28 & 29 seem to be on the right track. The attiude of the various publications need to be exposed to the light of public edification. Also, I solidly agree with the comments made in #33.
CP policies for editors state:
You know, I met with Nanne Weber of KNMI in Sep[t 2006, just before Juckes was submitted. Juckes et al was financed in Holland, with the Dutch paying Juckes to swan over to Beijing, with KNMI citing Juckes in their trashing of MM.
On Oct 26, 2006, M. N. Juckes, M. R. Allen, K. R. Briffa, J. Esper, G. C. Hegerl, A. Moberg, T. J. Osborn, S. L. Weber, and E. Zorita submitted “Millennial temperature reconstruction intercomparison and evaluation” to CPD. Indexed as CPD 2, 1001-1049
ts)
On Nov 8, 2006, virtually concurrently, D. M. Roche, T. M. Dokken, H. Goosse, H. Renssen, and S. L. Weber submitted “Climate of the last glacial maximum: sensitivity studies and model-data comparison with the LOVECLIM coupled model” to CPD. Indexed as CPD, 2, 1105-1153
D.M Roche is the editor who piled on to Claussen’s reply in the present discussion. Here’s Goosse as a coauthor with KNMI author Nanne Weber, with the Dutch on the hook for Juckes et al. And Claussen accuses me – who has no connections to this crowd – of applying “political pressure”. Since the charge is so ludicrous against me, it does make one wonder whether it comes from a guilty conscience.
Claussen’s claim about the lack of review comments was fatuous. This is supposed to be “open review”. Juckes et al was the 2nd most commented article they had, after Buger and Cubasch which they decided needed major revisions and they asked that it be re-submitted.
Claussen said that their policies require more than one referee. While most articles have more than one designated “referee”, I checked their record and in a quick survey located 3 articles that had only one “referee”, including one that was later than Juckes. The articles are:
http://www.cosis.net/members/journals/df/article.php?paper=cpd-3-221 Peyaud
http://www.cosis.net/members/journals/df/article.php?paper=cpd-2-535 Miller
http://www.cosis.net/members/journals/df/article.php?paper=cpd-2-485 Hole
In the case of Burger and Cubasch which was diagnosed as needing major revisions, they required re-submission.
Goosse said that Juckes et al also needed major revisions, but, in this case, instead of requiring open review as they had with Bürger, they did it behind closed doors. I’ll bet that there isn’t a sinlge other precedent in the short history of CP where a paper needing major revisions had been permitted to have a secret review.
Meanwhile, the joint publication of Roche, Weber and Goosse was proceeding along nicely towards publication in the same journal.
RE: #80 – Word. 😆
RE: 82
Steve M,
Would that be Gerd Bürger on Osborn and Briffa?
http://www.worldclimatereport.com/index.php/2007/09/25/questioning-20th-century-warmth/#more-253
Bürger, G., 2007. Comment on The Spatial Extent of 20th-Century Warmth in the Context of the Past 1200 Years. Science, 316, 1844a.
Did I understand it correctly, there is a revised version of Juckes et al, invisible to us, that will be published in CP soon?
#85. Yes, and, unique among CP submissions, it’s gone through a private and convenient offline review process.
Ya know, with these repeated black eyes, you’d think they’d wise up and stop pulling such shenanigans, or at least find a better way to disguise them. What a joke.
Mark
Re: SM #42
Basically, the main reason I posted was the word “defamatory”.
Also the word “insolent”.
Steve M’s post #42 was very good.
BTW, I used to be insolent in my replies to referees. When
they were wrong, and I could prove it, I often was somewhat
gloating and confrontational in my replies. This resulted in
unnecessary conflict. Now that I am older and wiser, I first
try a bit of greasy
dissimulation with the referee, while at the wame time pointing
out the matters of fact where the referee is wrong to the editor
and that suggesting the referee is incompetent. Positioning
the referee over the trapdoor in terms of later conflict.
I read the referees report, and if I decide the referee is
hostile through cause of incompetence, then I start to undermine
the referees credibility in terms of the editor.
Think in terms of a law trial. Insolence to opposing counsel
is allowed (if done well, it is quite entertaining), but insolence
or threats to the judge is always injurious to ones chances.
However, all this assumes that the adjudicator/judge/editor is
neutral!! So maybe, I am more of a boy scout (maybe a
particularly sneaky one) than SM.
If this is what they do to get a paper approved for their publication, what lengths will they go to prohibit any other paper from passing their review process? ( You know, if perhaps another paper brings to light some scientific truth about AGW or climate, or climate of the past they don’t want made public so much…) This mess makes me think about things like that as well.
Willis, Steve M., other Juckes reviewers:
When you went to all the trouble of preparing your submission, it was with the understanding that, if relevant [which they surely were…], your comments would be responded to and potentially affect the outcome of this paper. There was a complete dialogue here at CA documenting COtP procedures before you prepared your short comments. You had a reasonable expectation that your comments were desired and would be acted upon before you went to the considerable effort of compiling your comments.
The editor now says your comments were unsolicited and ignored. This looks a lot like a unilateral contract – having invited performance, he can’t breach or change the terms after you’ve completely performed.
Why don’t you send COtP a bill for your time at a reasonable rate ? In the case of Willis’ submission, all the persons who contibuted to the final contribution might bill time.
Re: #88
Jim, I think the point here is that Steve M’s purposes and intentions are different than yours and his tone and tact can be far more flexible. I find the public revelation of these situations with the emphasis that Steve M adds quite entertaining.
Insolence is not any more descriptive of Steve Ms tone than would be pusillanimity for your preferred tone in these matters. Certainly using insolence on your part in this discussion would seem to deny any pusillanimous on your part in this matter.
Carl #75:
He could also be refering to e-mails.
I could imagine that readers of this site and possibly others, have been sending correspondence to the Goose, and he doesn’t like being reminded that he’s not donig his job.
Editor Mosh pit:
Mr. Juckes, what you’ve just said is one of the most insanely idiotic things I have ever heard.
At no point in your rambling, incoherent response were you even close to anything that could be
considered a rational thought. Everyone in this room is now dumber for having listened to it.
I award you no points, and may God have mercy on your soul.
The following is a draft reply to Claussen’s letter, which I plan to send either tonight or tomorrow. Comments welcome.
Dear Dr Claussen,
Thank you for your prompt reply to my email.
First, your allegation that I have attempted to impose political pressure is absurd. I did not contact any of your funding agencies or politicians. Unlike the authors of Juckes et al, I have no connections to CP editors or editors-in-chief. During the review process for Juckes et al, I did not make informal, off-the-record inquiries or requests to editor Goosse. I wrote you an on-the-record letter as CP co-editor-in-chief, as you agree I am entitled to do. Since you have made the above false allegation to your CP co-editors, I request that you immediately withdraw the allegation that I attempted to impose political pressure on you.
Conflict of Interest Policy
Second, I draw your attention to a further breach of CP policies by editor Goosse in his handling of Juckes et al. CP policies for editors state:
The study, Juckes et al, submitted on Oct 26, 2006 to CPD, was funded by Dutch authorities. Nanne Weber of KNMI, a CP editor, was a co-author. Concurrently, on Nov 8, 2006, Weber and Hugues Goosse were co-authors in another CPD submission (D. M. Roche, T. M. Dokken, H. Goosse, H. Renssen, and S. L. Weber, Climate of the last glacial maximum: sensitivity studies and model-data comparison with the LOVECLIM coupled model.)
Obviously, Weber is a colleague with whom the editor [Goosse] has recently collaborated within the meaning of CP conflict policies. In this case, the breach of CP policies is exacerbated by the fact that the breach was known not only to editor Goosse, but to Weber, who, as a CP editor, knew of editor Goosses breach of the CP policy and apparently took no steps to request that he recuse himself as editor of Juckes et al.
Breach of Policy and Undertaking Requiring Authors to Adequately Answer
In my prior note to you, I observed that Juckes failed to answer what you call Short Comments:
In your reply, you did not contest this characterization of the matter. CP policy states categorically that, before a revised submission can be submitted, authors are required to adequately answer questions not simply from invited reviewers but from the scientific community. Indeed, this is held out in various papers by Pöschl as one of the supposed strengths of the EGU open review process. The CP policy states:
Obviously, editor Goosse did not ensure that this was done. Indeed, your letter indicates that the situation was even worse than previously characterized. You stated that, not only were Juckes et al not required to adequately answer the Short Comments, but that these Short Comments which you insultingly characterized as unsolicited were not even considered in arriving at an editorial decision:
This, by itself, is a breach of CP policies. In addition to being a breach of CP policy, editor Goosse’s failure here specifically breached an undertaking that he made to Willis Eschenbach (who had noted many problems with the Juckes article and who had complained about Juckes non-responsiveness). In an email, Goosse specifically assured Eschenbach that Short Comments would be considered and that he, as editor, recognized his obligation to ensure that Juckes et al adequately answered the Short Comments.
On Nov 21, 2006, editor Goosse wrote to Willis Eschenbach as follows:
Editor Goosse did not say to Eschenbach that these Short Comments would be considered as unsolicited and not considered in the review process. Eschenbach, who remained concerned that Juckes evasions would continue, reminded Goosse that it was his responsibility to see that these questions were answered:
Goosse replied, acknowledging this responsibility and assuring Eschenbach that the authors would be required to adequately answer all questions:
Eschenbach reported this assurance at climateaudit.org. Around the same time, I met with Valerie Masson-Delmotte, who asked me to assist with the refereeing in another troublesome article, which I agreed to do and did. On the basis of CP policies, the assurances of editor Goosse in respect to Short Comments and the invitation to act as a referee in another article, I submitted detailed comments under the Short Comment policy under the expectation that authors would be required to adequately answer Short Commments and that the Short Comments would be considered in the review process.
Editor Goosse breached both CP policy and his undertaking to Willis Eschenbach by failing to ensure that Juckes adequately answered the Short Comments.
I am further shocked that editor Goosse now says that these Short Comments were not considered in arriving at an editorial decision and even more shocked by your disparagement of these Short Comments as unsolicited and apparent acquiescence in this total disregard of editor Goosse for CP open review policies.
The Special Review Process for Weber and her Associates
Not only did editor Goosse fail to require Juckes et al adequately answer the Short Comments and fail to consider the Short Comments in the editorial decision, you have now revealed that editor Goosse then implemented a special ad hoc and closed review for his coauthor Weber and her associates, which breached CP policies in several respects.
Many of the problems with editor Goosses subsequent decisions stem back to his failure to require Juckes to adequately answer all questions. CP procedures presume the completion of this step, which was not carried out.
CP policies do not describe a de novo closed-door peer review in response to a revised manuscript. They call for peer review completion which is supposed to be in view of the public peer review and Interactive Public Discussion, stated as follows:
This policy clearly required that the Short Comments be considered in assessing the revised manuscript. It did not permit editor Goosse to completely ignore the Short Comments and set up a private de novo review for his coauthor and CP editor, Weber, and her associates. Editor Goosse himself even admitted that the Juckes (Weber and others) article required major revisions at the end of the end of the discussion phase and additional evaluation.
While CP does not have a long history, in the case of another highly commented CPD article (Bürger and Cubasch) where substantial revisions were required, the CP editor (who in this case had no conflicts) required re-entry of the revised manuscript into the open process:
This is obviously what editor Goosse was obliged to do as well. He had no authority to initiate his own closed de novo conventional peer review for his co-author Weber and her associates, in total breach of CP and EGU open access journal policies particularly in the face of strong criticism of Juckes et al in the Short Comments and Juckes total failure to respond to these comments.
Excuses are insufficient
In your reply to my complaint, you purported to excuse the irregularities in Goosses handling of the article as follows:
While most articles have at least 2 referees, there were at least 3 articles with only one referee ( Miller et al; Hole; Peyaud et al) of which one article (Peyaud et al) was subsequent to Juckes et al. So the fact that only one invited referee had responded is really quite beside the point.
It is not as though Juckes et al lacked comments. Juckes et al was the 2nd most commented upon CPD article last year. One of the premises of EGU open review policies described by Pöschl is that the open review can attract specialists with whom the editors may not be familiar, as occurred in this case. So while the invited referees may have let down editor Goosse, there was substantial comment in the open review Short Comments available to editor Goosse, which he was obliged to consider.
If editor Goosse wished to ensure that an additional invited referee was on record, such a report could have been readily added to the archive by journal staff. (I can attest to this personally as my referee comments on Bürger were a few hours out of time and I sent them to journal staff, who manually inserted them into the record without difficulty.)
But your excuse, even if valid (which it isnt) doesnt change any of the irregularities in Goosses handling of the file, including his failure to ensure that Juckes et al adequately answered all issues and his now reported failure to consider the Short Comments in his editorial decision.
Conclusion
In your letter to me, you stated:
As noted above, your suggestion that I have tried to impose political pressure is absurd. While you may regard the suggestion of irregularities distasteful, it is the irregularities themselves that you should find distasteful. As noted above, these include:
The breach of the CP conflict of interest policy by editor Goosse in acting as editor for a submission by his coauthor Weber;
A concurrent breach of CP conflict of interest policy by CP editor Weber, who was aware of this breach of CP conflict of interest policy and took no steps to ask editor Goosse to recuse himself from the file;
The failure of editor Goosse to ensure that Juckes, Weber et al adequately answered the issues raised in the Interactive Public Discussion;
The failure of editor Goosse to live up to his undertaking to Willis Eschenbach that he would ensure that Juckes, Weber et al would answer the issues raised in Short Comments;
Editor Goosses decision to receive a revised submission without Juckes et al previously adequately answering the issues raised in the Interactive Public Discussion;
Editor Goosses failure to consider the Short Comments in reaching an editorial decision
Editor Goosses institution of an ad hoc and special de novo review procedure for an article recognized to require major revisions and failing to require the re-submission of the article as a new submission to CPD.
You observed that:
I certainly endorse that objective. I commend you and your journal for the work that you are doing. Your journal has objectives that I endorse and excellent policies on open review. But respect must be earned and, if you distort and bend your policies in favor of submissions by your own editors and their associates, you will not earn such respect. In cases where conflict of interest is involved, you must endeavour to be scrupulous and, in this case, unfortunately that did not occur.
At this point, there is an easy way in which you as co-editor in chief can fix the situation. Obviously, under CP conflict policies, editor Goosse should not have handled the submission by co-author Weber and her associates. This may or may not be related to subsequent handling of the file, but, at this point, this is impossible to ascertain. Editor Goosse should voluntarily recuse himself from handling the file. The acceptance of Juckes et al by editor Goosse should be rescinded and editor Weber should gracefully accept the rescinding of the acceptance.
Under this proposed resolution of the matter, if Weber, Juckes and their coauthors wish to re-submit their revised manuscript to CPD, as Bürger was required to do, they would remain free to do so. In such a new review process, the new editor could then ensure that Juckes et al adequately answered all questions in accordance with CP policy and that there was neither any impropriety nor appearance of impropriety in the handling of the revised submission.
YT, SM
Steve M. is meticulous and methodical. It is his nature, but also required by his role as a skeptic. He expects to be held to a very high standard. Hugues Goosse has no such expectation and must be surprised and annoyed to see the errors he made listed in such detail. What Steve is doing, I think, is leaving a paper trail. People will be asking how the science got so fouled up. Goosse’s errors are a fine example of how we got to where we are today.
Minor typos:
**Under “The special review process for Weber …”
…This policy clearly required that the Short Comments be considered in assessing the revised manuscript. They did not permit editor Goosse …
should be “It did not permit editor…”
**Under “Excuses are insufficient”
It is also as though Juckes et al lacked comments.
should be “It is not as though…”
**Under “Conclusion”
In such new review process, the new editor …
should be “In such a new review process, …”
Sounds good!
#94, Steve M.:
I think you must be missing a word here.
As a matter of fact checking, I hope you’re positive that Nanne Weber and S.L. Weber are the same person.
How about a short paragraph mentioning the editors-in-chief duty to the journal’s academic reputation, and how allowing papers to be published that neglect NAS findings, et Al. does not seem like good stewardship.
typos:
Obviously, editor Juckes did not ensure that this was done (editor Goosse)
It is also as though Juckes et al lacked comments (missing not)
back to lurking – keep up the good work
yes.
http://www.knmi.nl/~weber/
http://www.knmi.nl/~weber/papers.html
The line:
should be
Great response. Especially this:
Great letter! It seems you go over the same point two or three times every so often, but it’s overall a very polite, specific and understandable reply. (I wish I had understood all the objections to the article that well!!!)
As far as the who/whom thing, I think that should be
specialists with whom the editors may not be familiar
but it might read better to leave it
specialists the editors may not be familiar with
Steve,
I mostly lurk here. I have nothing for respect for you and your skills and I share your disdain for a lot of this dung that is passing as science. (here comes the but…)
But, I am confused by what you hope to gain by letters such as this one. I give your chance of this letter reversing the editor¡¦s decision at between 0% and 2% and closer to zero. I will acknowledge that even if you had Miss Manners write the letter for you; your chances would probably never go over about 30%.
However, there is a larger point here. Letters such as this one make it easier for your adversaries to marginalize you as a person who is only in this arena for the joy of the fight. I don¡¦t see it that way. It is my impression that you are a person who is trying to make sure the outcome is correct. So, I hope that you leave the professionals in the field that want to side with you the room they will need to do so. When their friends feel insulted (most often because their work is not up to snuff and you were the one who pointed it out) the tone of the correspondence becomes more important than it really should be.
So I have a few suggestions:
c Start your tough letters with some of the more collegial or conciliatory tones that usually appears at the bottom of those letters and repeat the softer tone at the bottom as well.
c Try to avoid phrasing that can be misinterpreted as accusatory. I would suggest getting rid of the words ¡§you¡¨ or ¡§yours¡¨ every time you can. E.g. ¡§Your decision¡¨ is more likely to draw an unfortunate emotional response than ¡§the decision.¡¨
c Try using questions as a way to make your point ¡V such as ¡§As I read your written policy, blah blah ¡K this does not seem to match the blah, blah ¡K I see in the outcome. Can you explain to me how I am misreading your policy or the details I am missing regarding how your actions actually match the written policy?
c Try to always leave a way for the recipient to agree with you without looking like they got in a fight with you and lost. Saving face is always important and will usually trump the issue at hand.
I return to lurking. I hope you will take these suggestions in the manner in which I intended them.
RE: #103 – The letter constitutes a key piece of history. Prior to our harried technological age, personal correspondance was considered all of the following: proper etiquette, a way to formalize communications, a way to record key exchanges in the history record, and a pleasant art form to partake in. It is heartening for me to witness the fact the Steve M is a traditionalist in this critical regard. Kudos to Steve M!
The issue is that if at first you are civil, and you are told things, and they are misrepresented, why worry about the feelings of people that you’ve already given the chance to do the right thing? No, you let them know they didn’t do the right thing, but you do it civilly.
We’ve already seen things like this play out in the past, haven’t we? It’ll probably just get dropped again. sigh
But certainly it’s always best to give people an out, but given the reply that Steve is replying to, I don’t know how that’s possible. It’s already been attempted, and well.
#33 “[snip]” — Steve, I just finished reading “The Lysenko Effect” by Nils Roll-Hansen. The willing participation by scientists in the smear polemics of Lysenkoism in the old SU is striking and scary. What Donald Kennedy wrote in his July 2007 Science editorial is part and parcel of that pathology. The comment you snipped was not an ad hominem, but a dead-on description of what he was about.
I really liked SMs reply, but for one sentence ..
I would not have written the following, or would have couched
it in a less confrontational tone.
“Since you have made the above false allegation to your CP co-editors, I request that
you immediately withdraw the allegation that I attempted to impose political pressure on you.”
Some people do tend to view having their correspondence as having
plasted over the internet as “pressure”. The point SM wished to
make had mostly been made, and this could have been written
in much more concilliatory tone.
Rule #1, Academic publishing. Do not antagonize the editor.
Assuming the editor is neutral, no need to back him into a corner.
If you think the editor is not neutral, then by all means
write anything you want.
I have to agree that the point wasn’t to get them to change, it was to, as the lawyers say, “build the record”. We’re in a new and interesting place in the history of correspondence over such matters with the internet. All of this correspondence, which once upon a time took place privately, is now done on stage. Whether the people at COtP want it or not, this is all going on in front of the world. That’s the point.
#94 — excellent letter, Steve. You laid the case out very clearly and logically. In the last section, among the bulletted irregularities, you could include at the end,
‘Co-editor-in-chief Claussen acting as an accessory after the fact to the irregularities committed by editor Goosse.’
And,
‘The support of Claussen’s illicit collusion by co-editor-in-chief Denis_Dider Rousseau.’
CotP seems ethically mindless to the core.
In passing, Claussen’s end-comment that, “I am sorry to say that I find it distasteful that you suggest irregularities in the behaviour of our editors and that you try to impose any political pressure.” [snip] This sort of transference of self-traits onto an opponent is very characteristic of recourse to sentimentalized justification of a position that cannot be justified by fact. Being righteous, in other words, takes precedence over being right. Climate science is full of this.
It reads like a no brainer, game-set-match prosecution’s case, in criminal court. Too bad there will be no justice served in this case …..
quick note in the interest of spelling people’s names correctly: it’s “Denis-Didier Rousseau”
(two i’s in “Didier”)
Steve, The only area for improvement ( not weakness ) I see is in the opening. It’s largely a matter of taste.
“First, your speculation that I have attempted to impose political pressure is baseless.
I did not contact any of your funding agencies or politicians. Moreover, you are immune from political
pressure and I find your admission to the contrary quite telling.
Further, I have no connections to CP editors or editors-in-chief. In contrast, Jukes et al have several publically documented
connections to the editors that present the appearence of impropriety.
During the review process for Juckes et al, I did not make informal, off-the-record inquiries or
requests to editor Goosse. This is a simple matter that phone and email records will settle in my
favor.
Sorry. I put Mosh pit back in his cage now
Good letter – although I completely agree with jcspe 103 above.
Firstly, I would not thank him for a prompt reply – it’s what should be expected. It’s always best NOT to appear to be criticising (or praising) the person but the person’s actions. It’s usually a good idea to phrase your understanding of the facts less definitely and more subjectively.
For example:
“First, I find your allegation that I have attempted to impose political pressure to be puzzling as I have not contacted any of your funding agencies or politicians. I have no connections to CP editors or editors-in-chief, as it would appear the authors of Juckes et al have. During the review process for Juckes et al, I did not make informal, off-the-record inquiries or requests to editor Goosse. I wrote you an on-the-record letter as CP co-editor-in-chief, as we agree I am entitled to do. Since the above allegation made to your CP co-editors is false, I request that you immediately withdraw it.”
Keep up the excellent, focussed work.
Steve M., I do not understand why you snip out analogies placing the corruption in climate science within the larger context of a wide-spread, almost systemic, pathology of human thinking. The analogies are instructive. Sentimentalized righteous justification is a common failing even among thoughtful people and one of which we are best consciously aware, so that we can be alert to it and strive to avoid it.
Steve: Pat, there are a few words that are automatic deletes here. I’m not going to try to sort out whether they are being used in a sensible way or not. Those words would normally cause a post to be deleted entirely.
#103. I understand the point that you’re making.
Do I expect that an individual decision will be changed? I’d like to think so, but, as you say, the odds are not in my favor. Do I think that using less direct language would make any difference to the outcome? I doubt it.
As to your comment:
I don’t think that I picked this fight. I played the Climate of the Past review game by the rules. I submitted a Short Comment (as did Willis) within their rules, relying on CP policies and specific assurances from the editor. They are the ones that broke their own rules in order to disregard the Short Comment.
This sort of fight is a waste of my time. But if I didn’t do anything, this sort of thing would make me mad. Rather than get angry about it, I’ve adopted the policy that, when these sorts of events occur, I will do what I can within the rules of whatever journal I’m doing with and put sunshine on the issue. After I do so, I figure that I’ve done what I can and any anger is long gone.
As to how this sort of thing is perceived, I think that reasonable and decent people like (say) Eduardo Zorita or Gerd Bürger or Valerie Masson-Delmotte or Rob Wilson would at least wince at how Goosse and now Claussen have handled this matter. They may think that it’s a waste of energy to fight the system and it probably is. But I don’t think that they’d say that I was wrong about anything here (and, if any one of them do write me publicly or privately and say so, I’d take that advice seriously and probably follow it.)
Oh.. congratulations for your courage in recruiting comments from a crazed crowd
of blue pencil carrying nit pickers.
Re #107:
And later:
Perhaps Jim could enlarge upon why it’s inappropriate to be “confrontational” or not to be “conciliatory”.
It’s clear, Jim, that you are a gentleman. However, I don’t see the value of pussy-footing in this instance. The response of the Editors to SMc were clearly confrontational and non-conciliatory. I see no value in treating unprincipled people with kid gloves when they’re using brass knuckles. Apple-polishing [I had another more scatalogical phrase in mind] may work in private corespondence or even in face-to-face meetings, but this is a new and public media. Tact doesn’t work as well when one is trying to make his case in a public forum.
112 is a very important suggestion that does not ratchet up the conflict… “baseless” (vs “absurd”) is better for a professional letter. I might suggest, “without foundation” as an improvement over both.
RE 118.
Thanks. I’ll not vomit on your suggestion to replace my perfectly sensible
“baseless” for the wordy “without foundation.”
Laconically yours, Mosh pit.
Steve: the letter makes a powerful and persuasive case. For that reason, the inclusion of what might be called “fighting words” in three passages is unnecessary.
As noted, the term “absurd” is unnecessarily provocative. Of suggested replacements above, I like “baseless” best. Other possibilities are “false” or “demonstrably false.”
The use of the word “insulting” to characterize his use of the word “unsolicited” is also unnecessary and can be simply struck from the sentence.
The last instance of unnecessary contentiousness is the parenthetical insertion “(which it isn’t),” regarding whether his excuse is valid. Your view of his excuse is abundantly clear and doesn’t need to be repeated.
Someone else mentioned the word “defamatory” is in the text, but I didn’t see it. If it’s there and you are suggesting you are being defamed, I’d strike that also.
I worked on construction sites for many years. First rule I learned in a construction dispute: be the coolest head in the room. Of course, I occasionally broke that rule, but only with good reason, i.e. when it would appreciably improve the outcome.
aurbo says:
September 26th, 2007 at 7:35 pm
117
Aurbo,
I can’t speak for Jim, but I can answer your question as it seems to me. Pussy-footing as you call it is often necessary in trying to achieve your goals.
Much of my work is navigating government bureaucracies on behalf of other government bureaucracies or private firms and individuals. I usually represent the party with the least amount of power, and I am usually on the winning side. Before I gained experience in this arena I entered every battle with too much pride and tried to win them all. I soon learned it was poor strategy and seldom effective for a whole host of reasons.
If Steve wanted my advice I would tell him that he can win this entire war, but only by being very careful about confrontations. At this point the AGW-alarmist crowd has all the power. They are well-funded, have political patronage that is committed to the cause (I think over-committed, which will make them dangerous if/when they get desperate), have a long list of impressive credentials, have an well-oiled PR machine, have the media in their pocket, have the incredible incentive of a real good chance of confiscating unbelievable amounts of tax revenue from countless countries, have a many-year head start, and are not bound by any standards, or an obligation to tell the truth or play fair.
On the other hand, Steve is only one talented man with a blog in an uphill battle. In these circumstances it is all the more important that he play the game very carefully. Think of it like a card game such as pinochle. Only the truly rare hand can be played all at once for a win those hands where you are dealt all the power. In a more typical hand if one plays trump too fast, or in the wrong order, a loss is almost guaranteed. Yet crafty players still win even when dealt bad hands.
So, it really depends on what Steve really wants to get out of this. I accept his answer that he wants to respond to unfair treatment by calling a spade a spade and then moving on. As he sees it he did not pick this fight and he does not have time for it. Fair enough, I respect his view on the matter.
But Steve could win this whole war with the right strategies. First the AGW-alarmist crowds strengths are also their weaknesses. They are proud to the point of arrogance. They are sloppy with their own rules. They step on people and make enemies. Second, their behavior makes it pretty obvious that they know their science sucks.
Third, they have a time window that will run out. They can depend on everyone who remembers the dust bowl dying away, but they cannot keep new people from asking, why isnt it happening yet? Sooner or later they have to get some serious warming or their game is up.
So, until the time is right to adjust tactics I would play the game as outlined best by Hans Bleiker. I would always be collegial and cooperative. I would always talk about the problem and never the people involved. I would always demonstrate that my approach is reasonable, sensible, and responsible and make sure that when the opposition says anything unreasonable or irresponsible it is very obvious to everyone. I would give them plenty of room to arrogantly over-extend and never stop them from doing so, because that is part of what I actually want. I would always present the impression that my side was actively listening, carefully considering what we were being told, and truly caring about the issues and their effects on people.
Simultaneously I would also drive people nuts with a slow erosion of their position through one small, pointed question after another. My goal would be to inflict a horrible political or bureaucratic death by tiny paper cuts. This is a key point — as this slow erosion takes place the foundation starts to crumple under people. At that time there are allies available that used to be on the other side. This is how you really find out where the bodies are buried. But, there will be no allies available if they feel like I ever offended them or did not play fair with their pals. It is a funny situation; the powerful side can be unfair for years and you just have to live with it. Because if you want people to shift allegiances in the end your side can never be less than fair even once even to the pals they always knew damn well deserved it.
As a lurker, I have to agree with jcspe #121. As several commenters have noted, the politics of change is important. I’d argue that it is especially important given the stakes involved.
I say this not to diminish Steve Mc’s justifiable annoyance, but as one who has really learned about AGW from this site, and who admires everyone’s work.
jcspe, #121: I agree with everything you said, but I would add that if anyone is in need of a long, deep consultation with Hans Bleiker, it’s Claussen, Goosse, Juckes, et al.
The era of limited public scrutiny is over. It was once considered almost inconceivable that scientists might allow their work to be tainted by ulterior motives. That is no longer the case.
vincit omnia veritas
theduke:
September 26th, 2007 at 11:16 pm
#123 — it is my sincerest prayer that you are right.
#121.
I’m not trying to “win” a war. I’m trying to understand exactly what can be relied on and what can’t. Even if someone like Mann is a shameless over-promoter, it doesn’t mean that alarm isn’t justified. I’m familiar with situations where important mining discoveries have been made by stock promoters e.g. the Hemlo gold mine by Murray Pezim. On the face of it, you couldn’t rely on anything, but there was still something real. So I don’t preclude the possibility that, buried beneath the Mannian dreck that has accrued in this field, a valid and coherent argument for concern can be articulated and verified.
If I were younger and worried about career advancement, I would be deferential to journal editors, as young academics have to be, whether the deference is earned or not. Also Martin Claussen and Hugues Goosse are obviously both bright, conscientious and able people and the sort of people that I’d probably like in person. I’d much prefer to be on friendly terms with them.
But right now, aside from matters hockey stick and such, I think that it is important that people understand exactly what can be relied on in the journal review process and what can’t, and that this process itself be put in the sunshine.
On the other hand, I consistently under-estimate the stubbornness of people in protected academic environments. In these particular circumstances, in Claussen’s shoes, I’d probably cut my losses on this file on the grounds of the Weber-Goosse conflict of interest alone, and tell Weber and Juckes that their revision has to go back into the queue like any other article. I’d be cross at Goosse for how he handled the matter as well. I think that that’s what would happen in most businesses. But Claussen isn’t me. Academics are very stubborn and very pompous and their tendency is to tough these things out.
So what’s my objective: probably this. To shed a little sunshine on the process so that people can understand how this particular sausage is made.
Steve M,
Your first issue, in #94, is really the key to this entire matter. Dr. Claussen has set the tone of your response by accusing you of ‘imposing political pressure’, when the actual case is that political ‘climate science’ has corrupted the open and honest public review process that CPD claims in their policies. What Dr. Claussen is objecting to, and calling political, is your extending open and honest public review to their review process. I think the good doctor trying to push your button and spin your response into the realm of politics, to marginalize your objections as political.
Instead of demanding withdrawal of the allegation, I would suggest simply asking Dr. Claussen to clarify what he meant by “your attempt to impose political pressure”, pointing out that you have taken no overt political actions and are only objecting to a failure of their stated open review policies in a manner that is consistent with those same policies, i.e. open and honest public review. I think that this approach would be a better start to your response, because it would focus the core issue of the failure of CPD policies rather than the side issue of your being unfairly be accused of an act that you have not committed. The point here is to dismiss the personal and the political, and focus on the integrity of the CPD open review process, i.e. reverse Dr. Claussen’s spin.
Cliff
#126. Nicely put – agreed.
OK, here’s what I sent (thanks for the feedback).
Dear Dr Claussen,
Thank you for your prompt reply to my email.
First, I would appreciate an explanation of your allegation that I attempted to impose political pressure. I did not contact any of your funding agencies or politicians. Unlike the authors of Juckes et al, I have no connections to Climate of the Past (CP) editors or editors-in-chief or European funding agencies or politicians. During the review process for Juckes et al, I did not make informal, off-the-record inquiries or requests to editor Goosse or yourself. When I became aware of apparent irregularities in the handling of Juckes et al, I wrote to you, in your capacity as CP co-editor in chief, asking that you ensure compliance with stated CP policies, in an on-the-record letter as you agree that I am entitled to do. Far from trying to impose political pressure, I am merely asking that you observe CP policies.
Conflict of Interest Policy
In addition to the points made in my previous letter, I draw your attention to a breach of CP conflict of interest policy by editor Goosse in his handling of Juckes et al. CP policies for editors state:
Nanne Weber of KNMI, a CP editor, was a co-author of Juckes et al., which was funded by Dutch authorities and submitted on Oct 26, 2006 to CPD. Concurrently, on Nov 8, 2006, Weber and Hugues Goosse were co-authors in another CPD submission (D. M. Roche, T. M. Dokken, H. Goosse, H. Renssen, and S. L. Weber, Climate of the last glacial maximum: sensitivity studies and model-data comparison with the LOVECLIM coupled model.) Obviously, Weber is a colleague with whom the editor [Goosse] has recently collaborated within the meaning of CP conflict policies and accordingly there is a clear-cut breach of CP conflict of interest policy. Indeed you might well review how Goosse became editor of this article given this obvious conflict.
In this case, the breach of CP policies is exacerbated by the fact that the breach was known not only to editor Goosse, but to Weber, who, as a CP editor, knew of editor Goosses breach of the CP policy and apparently took no steps to request that he recuse himself as editor of Juckes et al.
Breach of Policy and Undertaking Requiring Authors to Adequately Answer
CP policy states categorically that, before a revised submission can be submitted, authors are required to adequately answer issues raised not simply from invited reviewers but from the scientific community. Indeed, this is held out in various papers by Pöschl as one of the supposed strengths of the EGU open review process. The CP policy states:
In my prior note to you, I observed that Juckes failed to answer what you call Short Comments:
In your reply, you did not contest this characterization of the matter. It is self-evident that editor Goosse did not ensure that Juckes et al adequately answered the issues raised in the Short Comments from the scientific community. Indeed, your letter indicates that the situation was even worse than previously characterized. You stated that, not only were Juckes et al not required to adequately answer the Short Comments, but that these Short Comments which you inappropriately characterized as unsolicited were not even considered in arriving at an editorial decision:
This, by itself, is a further breach of CP policies. In addition to being a breach of CP policy, editor Goosses failure here specifically breached an undertaking that he had specifically made to Willis Eschenbach (who had noted many problems with the Juckes article and who had complained about Juckes non-responsiveness). In an email, Goosse specifically assured Eschenbach that Short Comments would be considered and that he, as editor, recognized his obligation to ensure that Juckes et al adequately answered the Short Comments.
On Nov 21, 2006, editor Goosse wrote to Willis Eschenbach as follows:
Editor Goosse did not say to Eschenbach that these Short Comments would not be considered in the review process; he said the opposite. Eschenbach, who remained concerned that Juckes evasions would continue, reminded Goosse that it was his responsibility to see that these questions were answered:
Goosse acknowledgied this responsibility and assured Eschenbach that the authors would be required to adequately answer all questions as follows:
Eschenbach reported this assurance at climateaudit.org. Around the same time, I met with Valerie Masson-Delmotte, who asked me to assist with the refereeing in another troublesome article, which I agreed to do and did. On the basis of CP policies, the assurances of editor Goosse in respect to Short Comments and the invitation to act as a referee in another article, I submitted detailed comments under the Short Comment policy under the expectation that authors would be required to adequately answer Short Commments and that the Short Comments would be considered in the review process.
Editor Goosse breached both CP policy and his undertaking to Willis Eschenbach by failing to ensure that Juckes adequately answered the Short Comments and by failing to consider these Short Comments in arriving at an editorial decision. In addition, given the policies of CP and EGU journals, it is inappropriate for you to disparage these Short Comments as unsolicited and apparently acquiesce in editor Goosse’s disregard for CP open review policies.
The Special Review Process for Weber and her Associates
Not only did editor Goosse fail to require Juckes et al adequately answer the Short Comments and fail to consider the Short Comments in the editorial decision, in your letter, you reported that editor Goosse implemented what appears to be a special ad hoc and closed review for his coauthor Weber and her associates, which breached CP policies in several respects.
CP policies do not describe a de novo closed-door peer review in response to a revised manuscript. They call for peer review completion which is supposed to be in view of the public peer review and Interactive Public Discussion, stated as follows:
This policy clearly contemplates completion of an adequate answer to issues raised in the Interactive Public Discussion; many of the problems with editor Goosses subsequent decisions stem back to his failure to require Juckes to adequately answer all questions. The above policy also clearly required that the Short Comments, which are an integral part of the Interactive Public Discussion, be considered in assessing the revised manuscript. This policy did not permit editor Goosse to completely circumvent the Interactive Public Discussion (including the Short Comments) and set up a private de novo review for his coauthor and CP editor, Weber, and her associates.
Editor Goosse himself even admitted that the Juckes (Weber and others) article required major revisions at the end of the end of the discussion phase and additional evaluation.
While CP does not have a long history, in the case of another highly commented CPD article (Bürger and Cubasch) where substantial revisions were required, the CP editor (who in this case had no conflicts) required re-entry of the revised manuscript into the open process:
This is obviously what editor Goosse was obliged to do as well. He had no authority to initiate his own closed de novo conventional peer review for his co-author Weber and her associates, in total breach of CP and EGU open access journal policies particularly in the face of strong criticism of Juckes et al in the Short Comments and Juckes total failure to respond to these comments.
Proffered excuses are insufficient
In your reply to my complaint, you purported to excuse the irregularities in Goosses handling of the article as follows:
While most articles have at least 2 referees, there were at least 3 articles with only one referee ( Miller et al; Hole; Peyaud et al) of which one article (Peyaud et al) was subsequent to Juckes et al. So the fact that only one invited referee had responded is really quite beside the point.
It is not as though Juckes et al lacked comments. Juckes et al was the 2nd most commented upon CPD article last year. One of the premises of EGU open review policies described by Pöschl is that the open review can attract specialists with whom the editors may not be familiar, as occurred in this case. So while the invited referees may have let down editor Goosse, there was substantial comment in the open review Short Comments available to editor Goosse, which he was obliged to consider. If editor Goosse wished to ensure that an additional invited referee was on record, such a report could have been readily added to the archive by journal staff. (I can attest to this personally as my referee comments on Bürger were a few hours out of time and I sent them to journal staff, who manually inserted them into the record without difficulty.)
But your excuse, even if valid (which it isnt), wouldnt change any of the irregularities in Goosses handling of the file, including his failure to ensure that Juckes et al adequately answered all issues and his now reported failure to consider the Short Comments in his editorial decision.
Conclusion
In your letter to me, you stated:
As noted above, there is no foundation for your claim that I tried to impose political pressure. While you may regard the suggestion of irregularities distasteful, it is the irregularities themselves that you should find distasteful. As noted above, these include:
· The breach of the CP conflict of interest policy by editor Goosse in acting as editor for a submission by his coauthor Weber;
· A concurrent breach of CP conflict of interest policy by CP editor Weber, who was aware of this breach of CP conflict of interest policy and took no steps to ask editor Goosse to recuse himself from the file;
· The failure of editor Goosse to ensure that Juckes, Weber et al adequately answered the issues raised in the Interactive Public Discussion;
· The failure of editor Goosse to live up to his undertaking to Willis Eschenbach that he would ensure that Juckes, Weber et al would answer the issues raised in Short Comments;
· Editor Goosses decision to receive a revised submission without Juckes et al previously adequately answering the issues raised in the Interactive Public Discussion;
· Editor Goosses failure to consider the Short Comments in reaching an editorial decision;
· Editor Goosses institution of an ad hoc and special de novo review procedure for an article recognized to require major revisions and failing to require the re-submission of the article as a new submission to CPD.
You observed that:
I certainly endorse that objective. I commend you and your journal for the work that you are doing. Your journal has objectives that I endorse and excellent policies on open review. But respect must be earned and, if you distort and bend your policies in favor of submissions by your own editors and their associates, you will not earn such respect. In cases where conflict of interest is involved, you must endeavour to be scrupulous and, in this case, unfortunately that did not occur.
At this point, there is an easy way in which you as co-editor in chief can fix the situation. Obviously, under CP conflict policies, editor Goosse should not have handled the submission by co-author Weber and her associates. This may or may not be related to subsequent handling of the file, but, at this point, this is impossible to ascertain. Editor Goosse should voluntarily recuse himself from handling the file. The acceptance of Juckes et al by editor Goosse should be rescinded and editor Weber should gracefully accept the rescinding of the acceptance.
Under this proposed resolution of the matter, if Weber, Juckes and their coauthors wish to re-submit their revised manuscript to CPD, as Bürger was required to do, they would remain free to do so. In such a new review process, the new editor could then ensure that Juckes et al adequately answered all questions in accordance with CP policy and that there was neither any impropriety nor appearance of impropriety in the handling of the revised submission. If the revised submission has merit, it should be able to withstand public scrutiny in the CPD open review process.
Yours truly
Stephen McIntyre
The likely result will be, cowering back into the comfort zone of old fashioned “elite” review in the academic equivalent of smoke filled back rooms. “We tried to use an open review process, but got too many ‘unqualified’ reviewers, including ‘denialist’ activists, and the process was too time consuming to manage. Sorry!”
#129. I’m not sure about this. EGU is pushing this system for a variety of journals, see ACP. If someone from EGU assessed this, they’d be forced to conclude that the Short Comments were justified and that the editors reverted back to closed practices, contrary to EGU policies.
Steve:
I realize it is too late, but I want to offer a few suggestions for future reference.
1. The letter would be more effective if it was shorter. Many of the important points get lost in the argumenative discussion-room style of the letter. Many of your short postings in this thread are more compelling than the letter you sent to Claussen. Necessary documentary detail can be referenced in a detailed attachment.
2. The single most critical action you are requesting from Claussen should be concisely stated in the first paragraph. In this case, I presume that would be requiring resubmission of the revised Juckes work and his assurance that the review process will reflect journal policies.
3. The next paragraphs should summarize the reasons resubmission should be required, again with references to attached documentary detail.
4. The final paragraph should begin with a concilliatory appeal to jointly held higher interests (open review, best interests of science, etc.), yet ending quite firmly by stating your expectation that he will agree to your request
5. Finally, regarding the “political pressure” comment. If it was his aim to irritate you, why let him know he succeeded? If it was a somewhat innocent mistatement, why berate him over it? If you just can’t let it go without response, place it in an “Other Objections” section of the documentary detail so that your objection is on the record.
Keep up the good work, Steve. The frustration you must feel at times is almost unimaginable. My only wish is that I had more time to pitch in and help.
Steve, I don’t know what your problem is with the Rather analogy, I think it’s perfect. But if you don’t like it, I won’t do it again.
Steve: OT in this context with potential to spiral off.
I have to agree with #31. Steve’s email is much too long and the raking over every detail just screams “crank”. If it was shorter and more consice it would be far more effective. The tone is also important. If Steve wants to win the journal round then the hectoring tone (particularly in the first paragraph) is the wrong way to go about it. All it’s going to do is to raise the temperature. Far better to treat them like adults and be courteous rather than jumping down their throats. It might be very satisfying to play the outraged martyr in front of the audience here, but it’s no way to deal with a serious academic matter.
Last year, I met with Nanne Weber during my KNMI visit. She’s a nice person, although she didn’t have the slightest interest in trying to actually understand how the proxy calculations worked. As it turns out, she’s well and truly in the middle of the Goosse mess, because there’s a red-letter and incontrovertible breach of the CP conflict of interest policy. Conflict of interest breaches affect all the parties involved – it’s not just a journal problem (although it is a journal problem); it’s also an issue for each of the parties individually.
I’ve drafted the following letter to Nanne Weber as the person in the middle, suggesting that she voluntarily terminate the present submission process without requiring Claussen to make a decision and that they re-submit the revised submission through the front door to CPD, requesting a new and unconflicted editor.
Needless to say, the honorable course of action for Juckes would be to do so himself, without Nanne Weber having to get involved. IF they think that their revised submission meets CP standards, they should be able to comply with CPD open review.
Remember the real purpose of the letter. The purpose is not victory in this particular battle. The purpose is to create a record. (A secondary purpose is an experiment in human behavior, let us observe the subsequent reactions.)
#133. You’re probably right about it being too long. When I started this, I didn’t have high expectations of changing the decision and, to some extent, documenting the details was relevant (in case I wanted to re-visit the matter).
However, I now believe that the only sensible course of action is for the authors to voluntarily terminate the present process, including the tainted acceptance, and re-submit, as suggested in the letter to Nanne Weber. The conflict of interest breach is a red-letter issue, that’s easy for anyone to understand and easy to focus on. There’s little point in trying tough it out, when re-submission to CPD is an available option. Knowing academics, they’d probably pick Michael Mann as a guest editor for the re-submission. However, if they do try to tough it out, they will have missed multiple chances to remedy the situation.
This allegation of conflict of interest is all a bit lawyerly for my taste. If two coathors are both far down the author list, neither may view it as a direct collaboration, rather each collaborated with the senior author. Indeed I have numerous coauthors that I have neither met nor corresponded with.
Who should edit the manuscripts: the best and most active scientists who have become editors, but have collaborated, perhaps tenuously, with most of the small palaeo-climate community, or Dr. Boehmer-Christiansen?
Picking apart fine details of protocol may amuse the crowd, but does nothing to improve the science.
#137. If a conflict policy isn’t practical, then the journal should change the policy to one that is. They’re the ones that set up the policy – not me – and I presume that there’s a reason for it. They say that this is their policy. So they should honor it.
Are you saying that Goosse would claim that Nanne Weber was not a colleague with whom he had recently collaborated? C’mon. Are you saying that he wouldn’t have noticed that Nanne Weber was one of the Juckes co-authors? Puh-leeze.
Re: #137
If you cannot and do not understand how such networking constitutes a blatant conflict of interest, then you must either be disingenuous or too ill informed about the scientific method to be trusted with avoiding such conflicts of interest. Scientific advancement is not attained by three bobblehead monkeys all nodding their consensus agreement with eyes covered, ears covered, and mouth covered to the amusement of the crowd. Scientific advancement is attained by collegial and incisive criticism were possible and by bitter and determined criticism when necessary. In all cases, scientific advancement is not attained by avoiding criticism and leaving problematic hypotheses unchallneged. This is a clear case of conflict of interest, and relying upon a circle of former co-authors to serve as an adversarial challenge is an oxymoron.
But, RichardT, what about the main concern here? Why are relevant comments being ignored and why are things being decided in secret?
Real conflicts of interest are easily avoided by prudent editors. The problem is with the “perceived conflicts”, as there is no limit to the perception of those who wish to find fault.
If you can find a recent paper where Goosse and Juckes collaborated, then you have a story. Goosse and Weber being low ranking coauthors is unlikely to constitute a conflict of interest in any real sense.
You could make much more impact on science if you stuck to scientific arguments and ignored this froth.
#139
I don’t know if you have ever reviewed a manuscript, or been on an editorial board, but I have absolutely no difficulties delivering cutting critiques and recommending rejection of manuscripts submitted by people I have previously worked with.
richardT, you say:
While this may be true, you’re missing the point entirely. If it’s no problem, if it’s all perfectly fine and not an issue as you say … then why have a policy against it?
And if they have a policy against it … then why ignore the policy?
The whole thing, as you might imagine, is very disturbing to me. I put a lot of work both into analyzing the Juckes paper, and in collating other peoples’ analysis of the paper. I was assured by both the editors, and by the journal policies, that our efforts would be considered in the review. Having them go back on their word, and on their policies, is extremely frustrating.
w.
#141. Richard, I’m not sure that the conflict is quite as incidental as you say. The study was funded by the Dutch. KNMI relied on Juckes to say to say MM were “wrong” in their Annual Report and in articles written in the Dutch press by Rob van Dorland. Matters MM have been very topical in Holland. Nanne Weber represented KNMI in this study. My notes on my visit to KNMI are here
As to what her substantive role was, that’s an interesting question. As far as I can tell, she knew nothing about the statistical analysis and, when I presented at KNMI, she didn’t have the faintest interest in statistical issues. Also she has no previous articles on proxy reconstructions. So why was she listed as a co-author and what did she do?
If I were to guess at her role, I’ll bet that she represented the Dutch money in the MITRIE “project”, which only has this piece of dreck to show for its expenditures. If she was accountable in some way for the MITRIE project expenditures, her interest would not be merely incidental.
One more thing, as Willis has said clearly and I agree totally, CP editor Goosse gave assurances that our Short Comments would be considered in the Juckes review and then spit in our face. His disregard was complete. Maybe it seems to you that pursuing these folks on the basis of the breach of the conflict of interest policy is a bit like prosecuting Al Capone for tax evasion – and it is. But sometimes you take what you can get. And BTW most people in the world are not nearly as cavalier as you about conflicts of interest.
With no first-hand knowledge and based only on what I’ve read on these threads, forgive me if this is off-base: I think the letter to Nanne Weber runs the risk of appearing to pick on an underling who may merely be someone who goes along to get along. I suggest that you concentrate your fire on the principals.
#144. Nope, the Dutch are right in the center of this thing. The MITRIE thing got cooked up in Holland in the first place.
#145: If she was one of the chefs, then the letter is appropriate.
In the KNMI Annual Report published in August 2006 , they stated:
This was one month after the Wegman Report categorically said the opposite, and the North Report much more elliptically had conceded our main points (with North telling the House Subcommittee that he agreed with Wegman’s findings). So did KNMI have something more than an incidental interest in the publication of Juckes et al? Sure it did. I’ll bet that Nanne knew the status of this thing from beginning to end.
RichardT #141 I have no trouble myself with not only reviewing and editing the product produced by people I’ve worked with before. I have no issue with being critical and merciless with anything produced by my friends either. Or any of my family. Wrong is wrong. But how many people can look their (say wife) in the eye and tell them their new novel is crap, or they can’t write by heavily editing their work for them. Or tell them they should find a new career because they don’t have any skill at (say detective work)? Whatever. And more importantly, how many people are going to believe it even if it’s true unless they have firsthand knowledge themselves?
As Willis said in the next post, he was told they could comment. Steve read their rules and expectee them to be followed. Work was done, and then it turns out it was a lie, with some BS excuse about it. And even on a lower level, exactly, if it’s no issue, why have a policy? If you have a policy, it should be followed. And equally by everyone. These other issues are just branches from the main one, distractions; the policy is to to avoid apparent conflicts of interest. It doesn’t matter if there is or not. In this case it’s fairly obvious there is at least partly one, that makes it even worse.
And Steve, the next post, certainly if they’ve done multiple things bad, you can still only use for leverage what you can use for leverage. And it won’t be everything (or in a lot of cases, anything) They’ve so badly botched this, and then so blatently are trying to do damage control (and a terrrible job at it) I totally agree; don’t let it get you angry, do what you can about it, and then see where it goes. Then move on. That’s the way to flow.
RichardT said
I have some extensive experience with conflict of interest policy, incidents, and the battles that ensue.
A clear policy, properly followed, avoids exactly the unlimited fault-finding perception issue. State clearly the boundaries on disclosure and action. Follow through well. There’s great protection in this. Sure, rules can’t define everything but they provide a good playing field.
The problem is almost _always_ with how potential conflicts are handled. The general goal is to shed enough light on “potential” situations so that nothing could ever get close to becoming a real conflict of interest. If you ever get into a real conflict of interest situation, you know your relationship is in bad shape.
It’s quite disturbing that anyone can seriously consider whether a real conflict of interest is involved here.
In this case, we don’t need to speculate any further on the mysteries of “real” or “perceived” conflict since they defined the prohibited conflict to specifically include “recent collaboration”. (Their definition BTW is very standard.) So the only question that we need to answer is:
The answer is: yes. That’s all we need to know. End of story. If they are going to play the sort of games that they did, they’d better make sure that their hands are clean. They didn’t.
#150, exactly. They defined what is prohibited. It’s their game, but the rules are public. Can’t change the rules mid-game. And everyone can see what happened.
There’s a minimal opportunity to correct this honorably, as an “unintentional” breach. I honestly hope they take advantage of the opportunity. Otherwise, in my experience these situations rarely end well.
I believe that we can learn from RichardT’s comments on this issue as he presents what I judge would be the prevailing view of the mainstream science community in his summarily dismissing these issues as froth without addressing the main points put forth by Steve M and other posters. He admits to no wrongdoing on the part of those representing the system and evidently in terms of following their own rules and just good practices for keeping an open forum open. Perhaps the community does not want see these efforts as having any legitimacy because they take them as efforts to slowly erode away the credibility of the community and its consensus POV and not as someone like Steve M, who in my view, is merely pointing to weaknesses in the system without attempting to change the prevailing POV.
Re: #133
OK, now that you have critiqued Steve M’s approach how about the replies he has received? Are they the way to deal with a serious academic matter? Do you really think that the editors would feel compelled to reply to a suspected crank? They replied for a reason, but do you think if they had a legitimate answer to give they would have answered as they did? I think you left out all the good parts of the exchange.
By the way, if Steve M went hat in hand to the powers that be I doubt that he would receive a reply. He and Willis E become confrontational to these editors when they presented their reviews. Why else would they be totally ignored in the open forum process and effectively lead to the closing of the forum? I think that these editors know full well that Steve M and Willis E are outside the system and thus do not have to deal with a serious academic matter as tenuously as those from within the system evidently do.
#145:
If she is one of the chefs, then the Goosse is cooked?
Eric Wolff, another co-editor, sent the following response.
Whether Weber was a “regular” editor or a “Guest” editor is irrelevant. In this particular case, I suspect that most CP editors, other than Goosse, were unconflicted – why use Goosse, who aside from his collaboration with Nanne Weber, has also recently collaborated with Bradley and Mann? What conceivable purpose was served by using Goosse in what would be known in advance to be controversial? Wolff says: “I am sure no favours were given or expected.” Well, I’m not “sure” of this at all – Juckes et al were not required to comply with CP policies on “adequately answering” the Short Comments and the Short Comments were not considered in the editorial process. The purpose of the conflict of interest policy is precisely to avoid the type of situation that has arisen here. There were other alternatives. Wollff says: “I would be surprised if she even made herself aware of who the editor of the paper was.” Did Wolff ask her? Personally, I don’t believe this for a minute. The Juckes et al paper originated as a KNMI project. Weber was the KNMI point-person on the paper. If she didn’t know who was handling the paper and what it’s status was, she wouldn’t be doing her job at KNMI.
As Wolff says, it was self-evident that the Short Comments were “unsolicited”, so why say it? It was disparaging – although that in itself is not a breach of CP policy. It was the ignoring of the Short Comments in breach of open review policy that was truly “disparaging”.
Wolff has left out a step. The author is entitled to submit a revised version only after adequately answering the outstanding issues. Juckes made no effort to answer the issues raised in the Short Comments other than a mocking response. Wolff doesn’t even keep the story straight. He says that Juckes did not receive any “special process”. On the other hand, Claussen said that it did receive a special process: Claussen said that the open process had only one referee and because of this, Goosse instituted got 3 new referees for a closed process. I’ll bet that no other CP paper has had a similar history. Wolff didn’t cite any precedents.
This is the type of annoying answer that is all too typical of bureaucracies. I don’t think that any expert person could look at Juckes’ responses and state that it was his honest opinion that the comments had been “adequately answered” (is there a difference between adequately “answered” and adequately “addressed”? I don’t believe that Eric Wolff would state this as his personal opinion. I don’t think that Valerie Masson-Delmotte would state this as her professional opinion. So while it may be a “matter of judgement” to some degree, I don’t believe that any editor of science papers could honestly say that the comments had been “adequately answered”.
I don’t expect “consensus”. What I expected was an adequate answer – as Juckes was required to do under CP policies and as Goosse had promised Willis Eschenbach.
One of the particular reasons why the topic is generating “heat” rather than “light” is because Goosse double-crossed Willis (and secondarily myself). He gave personal assurances to Willis that the Short Comments would be considered and then spit in Willis’ and my face.
Trying to complain to bureaucracies is very much an uphill battle. This reminds me of my complaint to the Toronto Police SErvices Board a number of years ago when one of my sons was stomped in the head by bouncers, suffering severe internal head injuries; the investigating police officer covered up the investigation, including destroying a witness statement. I tried to pursue it, but got nowhere. Even the destruction of a witness statement didn’t matter to the police. Yeah, I’m sure that they thought that I was a “crank”. If you google William McCormack Junior toronto police, you’ll find that the police officer in question was eventually caught on unrelated matters a couple of years after my complaint. It was a big scandal in Toronto for a while.
To me, the real issue here is not the incestuous conflict of interest, although it is a major issue. The real issue is that many of the substantive scientific questions raised in the open review process were totally ignored. This was despite Goosse’s email to me stating:
And to think that I was actually excited when the Climate of the Past Open Review process began …
There are many more issues in this whole affair that are problematic, but that’s the main one. Ask for reviews and then ignore them.
The only good news in all of this, in a schadenfreude kind of way, is the loss of the reputation of CoP. The latest one I heard was:
w.
PS – Yes, I know I’ll likely get flamed for being too harsh, and too unprofessional, and the like … but me, I’m just a guy who grew up on a cattle ranch, in a time and place where a man’s word was his bond, and if you told someone you were inviting his comments and would seriously consider and reply to them, you did so. Call me old-fashioned, but ignoring a man’s scientific ideas and objections after you have specifically asked for them strikes me as both churlish and dishonest.
PPS – I found the following comment from Martin Claussen hilarious:
“Closed automatically”? Like it’s some automatic door that closes on its own, and the editors couldn’t prevent it from closing?
And the solution was to realize it was a bad situation, but rather than simply keeping the discussion phase open, just close the barn door after the horse has bolted?
This is definitely the funniest excuse I’ve heard in quite a while, “the automatic door ate my homework”.
Steve M,
In the end there were legitimate and substantial scientific issues that were raised in the review process (the source is irrelevant – the issues just happened to be raised by Willis and you) and those issues were not addressed by the authors of the manuscript. No amount of obfuscation by the editors of the journal can imply that the manuscript was handled appropriately when those underlying scientific questions have not been addressed. IMHO it is a very damming statement about the quality of the journal (and that is probably why the authors submitted the manuscript
to that journal in the first place). The manuscript wouldn’t stand a chance of being published in a reputable mathematical journal.
Jerry
Willis (#156),
I see that we are in complete agreement.
Jerry
Re: #155
You didn’t mention Wolff’s straw man argument in 1. He says it is “…often undesirable, to bar editors and reviewers who have been associated with every co-author of a paper”, but the policy makes no such demand. Instead, it mentions “…colleagues with whom the editor has recently collaborated,…” (emphasis mine). Perhaps this episode could have been avoided, had the Editors been more knowledgeable of their own policies…
Re: #156
Willis, hopefully the online comments will remain accessible so that others can appreciate the effort you (and others here) made to craft a constructive review.
I’m curious to see whether or not the CoP Editors now have the guts to fix their incorrect description of the Open Discussion process.
They’re plenty knowledgeable of their own policies, they simply refuse to follow them for their favorites, and do the arm-waving when challenged to make it look legit. Nobody with any integrity thinks this crapola is even close to honest.
Mark
re 160:
There is a backup of the site.
http://web.archive.org/web/20070209004809/http://www.cosis.net/members/journals/df/article.php?a_id=4661
Their comments remind me those of some not-exactly-intelligent physicists who submit crazy papers sometimes somewhere. It is amazing what percentage of their statements are demonstrably incorrect and how they can never focus on the real essence of a question.
#157:
That’s the point. And it is a trivial point. Which climate science paper would be published in a math journal? None. And no economics-, hydrodynamics- etc. paper either, because it simply is no mathematics. It’s swampy dark science.
The problem with the Juckes CP discussion was not that it was a bad paper. The problem was that it served as a punching ball, representing the bulk of reconstruction papers written so far, as many of the valid (“relevant”) comments could actually be applied to any of those papers. And with that same energy one could probably invalidate many more papers of the hardcore empirical type (never forget: even Newton is incorrect.)
Juckes attracted practically all criticisms formulated here at CA over the years, and CA didn’t hesitate to submit them – albeit in summarized form – to CPD as “short comments”. What for? To achieve a rejection of Juckes and official “proof” of being right? – I found that a bit naive.
And while I agree with many of the expressed criticisms, one should not overdo it and demand mathematical rigor in each and every step. BTW, econometrics, which often serves as CA’s role model of applied statistics, did not come up with any useful economic forecast so far, did it? How would that compare to climate forecasts? 😉
Whether the criticisms are valid or not, you have to acknowledge that CPD is not a blog. I myself was at first mislead here, and only later understood that CPD runs at a different speed. Blogging discourse goes at higher speed and frequency, sometimes too high to allow for thorough verification (Steve’s claims on Parial Least Squares regression are still awaiting proof.) And CPD’s Short Comments on a paper are certainly not a wise choice to place fundamental criticisms on the entire field. An article, yes, an article!, maybe even at CPD, would have been better and is still a choice.
Stepping back, I’m fascinated by what this episode demonstrates about the insular culture of (this portion of) the climate science community.
In essence, they’re saying:
* This is a new arena led by a small group of expert scientists — you can’t seriously expect us to work with true independence, true critical commentary.
* So yes, we declared the “proper” rules for our interactions and journals (it legitimizes our work among stakeholders.) Be patient, in a few decades perhaps we’ll be big enough to actually live by those rules. But for now, we function by whatever means necessary to advance our science.
* Your comments were far outside the stream of our active discussion — you are not speaking our language. If you aren’t speaking our language, you really are not able to helpfully “edit” our work.
The result:
SteveM says:
Well, yes. The ultimate insular culture.
And Gerd says:
I once wrote a paper for a class. The paper came back with all but a few words redlined. I was completely devastated. But I could not reject the authority of the commenter.
In this case, due to the insular culture, the “fundamental criticisms” have accumulated to the point where, as Gerd has outlined, a knowledgeable outsider must suspend disbelief to interact with this group in a way they can receive.
Reminds me a bit of visiting Boonville California long ago, with its own culture and (almost-but-not-really english) language, Boontling.
At first it all appears comprehensible, but over time you realize they’re just… different.
(Today, Boontling has all but disappeared as tourists zoom through on their way to Mendocino.)
I am sure I remember correctly, and if we search the first threads containing Juckes’ own comments here on CA; Juckes straight up invited you SteveM, and everyone or anyone at CA to participate in this review process online at the Climate of the Past website!
Re# SM #136
Too long does not matter that much in academic articles.
In academic articles, it is sometimes expected that your propositions
be absolutely demonstrated to be true (I can hear derisive
laughter from some of the readership already). So it is not uncommon
to exhaustively cover all possible objections (which can lead
to something that is exhausting to read!).
There is not much harm in being exhaustively thorough. The
editors will cope.
HI, Gerd. Glad that you’re commenting on this.
No, that’s not why I submitted Comments on Juckes. I submitted comments on Juckes as an expert both in the field and on my own papers, and because the open review process and the undertakings of Goosse to Willis Eschenbach said that they were obliged to consider such comments.
In respect to false comments on my own papers, I figured that it was worth the effort of trying to require Juckes to “adequately answer” my Comments and I presumed, incorrectly as it turns out, that if he failed to answer the Comments adequately, that these claims would be removed – perhaps with other parts of the article intact. Even Referee #1 suggested that this section be changed. As it turns out, Juckes did not “adequately answer” these Comments, but was allowed to proceed anyway.
As to the more statistical points, you’re right that similar points could be raised against other articles in the field. But that doesn’t mean that the observations were incorrect as to this particular article. I had the right to comment and did so. CP ignored the comments – shame on them. If I had not submitted the comments, then they would have said – why are you criticising after the fact? you had a chance to comment during the Interactive Public Discussion Phase and didn’t. So I played by the rules; they didn’t.
Gerd, let me ask you a question as an expert in the field. Wolff says that it’s a “matter of judgement” of whether Juckes adequately answered the Short Comments. I do not believe that any competent editor can look at Juckes ‘ answers and honestly say that he “adequately” answered the Comments. I don’t believe that Wolff would. I don’t believe that Claussen would. I don’t believe that Masson would. Would you?
I didn’t demand “demand mathematical rigor in each and every step”; I demanded no more than undergraduate competence. Even that seemed out of reach of these folks. THe points that I submitted in my Short Comments were pertinent to the Juckes article. I didn’t expect them to respond at blog speed. I expected them to respond in terms of their own process. They didn’t.
You’re right that I need to write up Partial Least Squares. IT’s interesting and ironic. It also shows the horrendous grasp of multivariate methods endemic in the field and integrates some results back into statistical mainstream.
Quite frankly, I’m flabbergasted at the degree to which they perverted their review process. They ignored the Interactive Public Discussion. The review of a revised paper was supposed to take place only after adequate answers, “in view” of the Interactive Public Discussion and be similar to the “completion” of ordinary review – not de novo review. Instead of doing that, they solicited de novo new reviewers, did so behind closed doors, ignored the Interactive Public Discussion (as they now admit). It now turns out that editor Goosse was in breach of a red-letter conflict of interest rule.
Re: Gerd #164
“And CPDs Short Comments on a paper are certainly not a wise choice to place fundamental criticisms on the entire field. An article, yes, an article!,
maybe even at CPD, would have been better and is still a choice.”
There is a lot of wisdom in Gerds last sentence.
Re: #164
Think about that statement for a moment: given the role model cannot predict what does that say about the abilities of climate science to predict. I could not agree more with this telling admission.
Ross has been bugging me to write up some unfinished work as well. The problem for me is mostly that the articles that I have to respond to – Juckes ; Wahl and Ammann; are such dreck. If I’m doing something, Gerd’s suggestion of doing something on PLS is not a bad idea.
I suppose that what “gerd” is saying is that the rejection of Juckes’ paper in the face of the short comments would have meant the repudiation of much if not all of the field of proxy reconstructions. From a political point of view, this would be an impossibility for a climate science journal. How could they do this when the IPCC has made reconstrcution the poster child for their reports?
Apparently, proxy reconstructions are unsound both scientifically and mathematically. As an aside, imagine a journal requiring rigor in the mathematical developments within a paper! However to admit this would be to deny much of what the IPC is about and that is something that could not be done. I have seen this in my own field in which research in a grossly impractical technology persists because there is no way to admit that it cannot be made to work. Instead, anybody who criticizes the method is accused of being incorrect and incompetent – very much like how M&M are treated in climate science. However I have noticed that interest and participation in that community is just slowly fading away along with their technology.
Total straw man and Stan has a point that’s equally compelling. Mathematical rigor does not guarantee a successful prediction tool in nearly any field, particularly those bound by otherwise chaotic dynamics. However, absent such rigor, such a guarantee is even less likely, which is the case in point regarding climate science. At least the field of econometrics is making an honest effort to get it right; the same cannot be said for much of climate science.
Mark
Re: #163
I was about to unfairly generalize about Steve M and the climate academicians being worlds apart in their views of all these contentions when an academician, although not a climate academiciuan, like Lubos M comes along and makes the observation “they can never focus on the real essence of a question”. That amazes me also — unless I judge that they are being overly defensive about their fellow academicians.
Re: #172
Imaginary email exchange from a number of months
ago. HT#1 = Hockey Team member #1
HT#1: We gotta get SM off our backs?
HT#2: Yeah, its getting annoying. And it could get more uncomfortable
if he starts publishing standalone articles. We can ignore
Wegman because it is not peer-reviewed.
HT#3: Why not write up some stuff that really is not important
and make sure SM notices.
HT#2: You mean like throwing a bone to a dog?
HT#3: Exactly. We need to distract him on some stuff. We can send it
to COPT and invite him to comment.
HT#1: Yeah, who do we get?
HT#2: Doesn’t really matter, just make sure his pet peeves are
in there.
HT#3: That will keep him busy for a few months :-).
HT#2: Main thing is we do not want him to publish. There are
some guys, you know like Storch or Burger, who might let
something slip through.
HT#1: They are not 100% with the program. Just leave it to me, I
know that …..
RE 170.
Yes, and consider this. Climate models are driven by inputs from “emission scenarios.”
The SRES. The Sres are essentially storylines for potential futures, informed
by assumptions about economic development and population growth. Very simply
the scenarios decompose into classes of energy Mix ( crudely coal vs nukes), energy
density ( the rate of technology transfer) and Population growth.
For a brief space here let us grant the accuracy of a GCM, given it has proper input.
The issue remains, how does one forecast Tons of carbon spewed in the atmosphere over the next 100 years. Models of
economy and population. So, criticizing econometrics, however justified, when one
uses the progeny of those models to drive a GCM is profoundly dense. Unless of course one
expects to recieve a purple heart for self inflicted wounds.
Re: #175
Jim, without a conspiratorial bent this time, perhaps you could give us a rendition of the conversation that took place in deciding to close the open forum and bringing in 3 unnamed reviewers. Feel free to invoke some humour, although playing it straight would be funny enough.
Random thought kinda related…. Update the proxies… Surfacestations does tree rings.
But can they afford all the “heavy equipment” that is required?
Mark
Re: Ken #175
More recent, chat room conversation
HT#1 OK, I’ve been on the phone to Duucckks, he will close
the review for us.
HT#2 Why do that?
HT#1 We will close the review, and basically ignore SMs comments.
There are a few statements that will really set him off.
HT#2 You mean, the unpublished references that say he is in error.
HT#1 When he finds out they are still in there, he will really go
nuts. He will write to the editors and try to get them to unpublish
it or stuff like that.
HT#3 The editors won’t like that!
HT#2 He won’t really understand the the editor mindset. They are
like football umpires, even when they’re wrong, they’re right.
And the more they’re wrong, the more they say they’re right.
HT#3 Yeah, once the decision comes down, its almost next to
impossible to change their minds.
HT#2 Won’t they get pissed off at Duuccks?
HT#1 Yeah, but they will forget him once SM starts the correspondence
and all the conspirancy theories start at CA. We need to get
someone to post there about the moral corruption of the
editors and egg him on.
HT#2 Thats brilliant! Besides keeping him busy, he will irritate
the editors no end. This will make it easier to stop him
publishing. So they will be automatically hostile if anything
from SM crosses their desk.
HT#1 Yep. He really does not understand that editors are not
likely to reverse a decision to publish no matter what the
circumstances, and won’t let it go. Some of the guys on the
editorial board at COTP are not 100% with our program. The
reaction of SM will alienate them and make it harder for
him to publish.
HT#3 We gotta make sure there is someone at CA posting that
SM needs to expose the den or corruoption. I’ll organize ….
Would it have been hard for CP to get an unconflicted editor? Absolutely not. Here is a list of their editors. It’s hard to find a conflicted editor. Only a couple had conflicts, but Goosse’s were the worst.
Claussen, Bracconot, Guiot, Lohmann, Mikolajewicz, Renssen, Loutre had stale collaborations with Weber; other than Goosse, Brovkin also had a current collaboration with Weber. Goosse has two current and one older collaborations with Weber. And again, Weber is not an incidental author. She turns out to be the person that the Dutch funding agency originally dealt with and who presumably sponsored Juckes. KNMI had officially spoken out against our work as well.
Goosse was the most conflicted possible editor in the entire CP roster. Not just through his connection with Weber, but with his associations with Mann and Bradley.
As to the others: Juckes doesn’t seem to have collaborated much with anybody recently – his only Google Scholar listing in the past 6 years is on “Global Warming and Nuclear Power”. [Update: note comment below for atmospheric physics articles by Juckes that were not in the Google Scholar listing that I used] I haven’t canvassed Briffa, Osborn, Moberg etc., but I’m familiar with their corpus and don’t recall seeing the names of the CP editors listed below. So I don’t think that they present conflict problems.
So why did the most conflicted editor get carriage of the Juckes, Weber file? It looks like, under CP editor processes, an editor can volunteer and seize control of a paper, without anyone paying any attention to it. It looks like this is what happened here: Goosse was probably not “asked” by Claussen or the others to referee he probably took carriage of the file without any editors in chief paying attention.
So the excuses by Wolff for the conflict are absurd and irrelevant. Almost any CP editor other than Goosse would have had no conflict of interest. The most conflicted editor handled the file, and yes, Dr Wolff, he did favors for the authors.
Martin Claussen
Gerald M. Ganssen
Denis-Didier Rousseau
Eric W. Wolff
Luc Beaufort
Torsten Bickert
Pascale Braconnot
Ed Brook
Victor Brovkin
Han Dolman
Helena Filipsson
Hubertus Fischer
Markus Fuchs
Hugues Goosse 3 articles
Joel Guiot 2006
Christine Hatté
Simon Jung
Thorsten Kiefer
Claudia Kubatzki
Gerrit Lohmann 2002
Marie-France Loutre 2007
Valérie Masson-Delmotte
Uwe Mikolajewicz
André Paul
Frank Peeters
Volker Rath
Hans Renssen
Jan-Berend Stuut
Pinxian Wang
Richard Zeebe
Patrizia Ziveri
Tas van Ommen
Re: #181
Yeh, it would have been possible to get a better choice
of editor.
But, the nature of the beast is that it will never be admitted
(especially given that any admission will be plastered over
Climate Audit!).
Hmm, we already have a LOT plastered on CA. Will this be Climategate?
#182. Wolff’s defence of the breach of the conflict of interest policy was:
In this case, it was not only not “impossible” to find an unconflicted editor; it was easy. Indeed, it was hard to find conflicted editors. IT’s not just that the other editors would be “better”. The issue is that Goosse was conflicted and then made further breaches of CP policies. And the editors in chief seem unable to tell a straightforward story in defence – Wolff’s implausible and fictitious tale of “impossibility” being only the most recent.
#183, #184
There may be people on the editorial board who are
actually really, really, annoyed. But they will
maintain the solidarity of the editorial board.
Can you imagine watching the superbowl, and having
an active umpire giving commentary on whether the
officials on the day are giving correct decisions!
Basically, the outcome (as opposed to the procedure)
is really in the chickens… category. This is not
first sub-standard article to be published this year.
With respect to choosing editors, it is entirely
possible articles come in, the abstract is emailed
to all editorial board members, and whoever volunteers
first picks up the article. Editors assume other
editors are trustworthy. In some journals, you
are allowed to choose your editor.
Most conflict of interest issues in journals concern
people making sure their arch enemies are not a referee
or editor. 90% of angst comes from this, and thats
where the attention will be focussed. There is
much less concern that someone will get their best friend
as a referee. The academic community is generally
more concerned about getting their articles published
(this is where the thrust of COI is aimed), and exhibits
less concern about stopping other peoples papers.
Fair enough. But if this happened, it is odd that one of the editors has not said so. And just how is the conflict of interest problem policed?
Steve, #184: a salient point. The logical follow-up question is why. Are editors reluctant because they would have to be harshly critical of the work? Because they don’t want to be in the house of cards when it falls?
Jim:
Are you really Karl Rove?
Sorry about the multiple posts. i didn’t think they were being accepted. Please delete a couple of them.
Jim, I understand that editorial boards are like other organizations. If you’re representing an organization, you may be mad as a boil at how something was handled, but obliged to defend the organization publicly.
But having said that, you still have an obligation to mitigate situations, rather than make them worse. In this particular case, if I were Claussen or Wolff, is to decide the thing on the Goosse conflict of interest alone – so that I didn’t have to wade through any of the other issues, where I might not like the outcome or what I found. On the breach issue, you can just say: so sad, so sorry, it was an oversight- and not admit any culpability other than that. The remedy is easy and imposes no hardship on the parties: re-submission of the revised article to the CPD process. I’d say to Juckes and Weber: touch luck, we didn’t expect this to be an issue, but it is and we have to do what we have to do. What are they going to say? Nothing.
That’s what I’d do. It would be off my desk and the story would be over. I’d suggest to Juckes off the record that they should answer the questions next time in a way that would pass at least a cursory smell test. And I’d tell the new editor to do the review by the book.
Instead of doing something simple and fair like that, they’ve decided that they’d rather tough it out – the Richard Nixon approach. That doesn’t bother me. In fact, it amuses me. It will be interesting to investigate the whole Juckes process from start to finish – what happened on the first day when the Dutch ministry met with Nanne Weber, how did Martin Juckes, whose only recent article was “Global Warming and Nuclear Power”, get selected as the point man for the Dutch? The M&M story had a big play in Holland and CA has a lot of Dutch readers. Journal review processes are very much part of modern climate science; maybe something interesting will turn up. So we can have some fun with this.
RE: #172 – Yes, the methodological implications are probably the reason why the orthodoxy have hoped that this particular line of criticism will either go away or be silenced. Once you’ve discredited the purported temperature reconstruction, then reconstructions of ENSO, hurricanes, glacier mass balance, sea ice, or what have you, which have used similar methodologies, would be suspect. The house of cards may fall down. There is much at stake, and the orthodoxy will fight dirty. They may even start to fight much harder, in ways which will shock us. It could get very, very ugly.
Let me put this nonsense into some perspective.
Parker published a paper on UHI a while back. It has become part of the spine
in the argument that UHI bias does not infect the land surface record.
We looked at his paper. After it was accepted, after it was published, after it had
enter the blessed canon of the church of AGW.
We submitted 20 or so questions to him. He had no obligation to answer. He could have
told us to sod off or #sand. He did not. He answered the inquiries. Did we reach
consensus? Nope. Were his answers adequate? did they address the issues or sidestep?
They addressed the issues. No proceedures or guidelines compelled Parker to do
the intellectualy honest thing. He just did the thing any honest person proud of his
work would do. He addressed the issues. Were he devious no guidelines could prevent him
from weasling the rules and redefining the meaning of “is”
In the end no set of proceedures is foolproof or maliceproof or obsfucationproof or
weaselproof. Every system of proceedures can be hacked.
That said, Imagine the fury that would ensue were St.Mac to author a paper on Climate
of the Past while Willis served as editor and the Manns short comments recieved short
schrift.
#181
1. Juckes MN, An annual cycle of long lived stratospheric gases from MIPAS, ATMOSPHERIC CHEMISTRY AND PHYSICS 7 (7): 1879-1897 2007
2. Geer AJ, Lahoz WA, Bekki S, et al., The ASSET intercomparison of ozone analyses: method and first results, ATMOSPHERIC CHEMISTRY AND PHYSICS 6: 5445-5474 DEC 5 2006
3. Juckes MN, Evaluation of MIPAS ozone fields assimilated using a new algorithm constrained by isentropic tracer advection, ATMOSPHERIC CHEMISTRY AND PHYSICS 6: 1549-1565 MAY 15 2006
4. Juckes M, Lawrence B, Data assimilation for re-analyses: potential gains from full use of post-analysis-time observations, TELLUS SERIES A-DYNAMIC METEOROLOGY AND OCEANOGRAPHY 58 (2): 171-178 MAR 2006
5. Pascoe CL, Gray LJ, Crooks SA, et al., The quasi-biennial oscillation: Analysis using ERA-40 data, JOURNAL OF GEOPHYSICAL RESEARCH-ATMOSPHERES 110 (D8): Art. No. D08105 APR 20 2005
6. Sparrow SN, Gray LJ, Juckes M, et al., Simulations of stratospheric flow regimes during northern hemisphere winter, ADVANCES IN SPACE RESEARCH 34 (2): 337-342 2004
7. Gray LJ, Sparrow S, Juckes M, et al., Flow regimes in the winter stratosphere of the northern hemisphere, QUARTERLY JOURNAL OF THE ROYAL METEOROLOGICAL SOCIETY 129 (589): 925-945 Part C JAN 2003
8. Juckes M, A generalization of the transformed Eulerian-mean meridional circulation, QUARTERLY JOURNAL OF THE ROYAL METEOROLOGICAL SOCIETY 127 (571): 147-160 Part A JAN 2001
Steve M.:
Editor-in-Chief Claussen says the short comments were ignored by the Juckes article editor, but Co-Editor Wolff argues that:
I’m not sure how anybody could believe that pretending comments don’t exist constitutes ‘adequately addressing’ them. If the Dutch government is going to such great pains to neutralize that article in Natuurwetenschap & Techniek (NWT), perhaps you should contact that magazine directly with an outline for a great story on how Dutch tax dollars are being spent to remanufacture public opinion and undermine confidence in their journalism.
I still leave open the possibility of you and Willis sending bills for services rendered to COtP. (See #90)
Jim, per your Post #180, let me give it a try:
Editor1: I think we have a problem with our new open forum concept.
Editor2: Look we have hyped this open forum as a means of using, or harnessing may be a better word, some of the internet reactions in terms of openness and quick response time. If we have a problem you had better describe it right now and have a reasonable solution, otherwise we could lose some well earned credibility here.
Editor1: I thought we had intended to go into this new mode with a toe in the water approach whereby we would have invited reviewers appear in the open forum and give public comments and then use those reviews as our basis for accepting/rejecting the paper. We would also open the forum and encourage comments from the general public as part of PR for our rather unique open forum, but certainly, in wanting and needing to maintain control of the review process, we need editorial flexibility in using those uninvited comments.
Editor2: We have been rather aggressive in encouraging those uninvited comments and it would appear that our rules and promises to the public have set in place the perception, if not the rule, that public comments will be presented to the authors of the papers for replies. Thats no big deal when the authors are assured that their papers are being officially reviewed by invited reviewers.
Editor1: In this case I believe it is a problem and please let me explain without interruption. The paper in question was presented for review and we received a single official review but at the same time a number of uninvited reviews that went into great detail in critiquing and questioning many parts of the paper. The authors of the paper did not feel obliged to answer the uninvited reviewers, assuming I would guess that they were not to be counted in the official verdict of the papers acceptance or rejection.
Editor2: I think I see the problem. With one official uncritical review and several unofficial ones that are critical of the paper we would appear to be remiss in our duties, and particularly so if we claim an open forum (even if it is at this time in name only), if we did not use the unofficial reviews or at least push the authors for replies to them.
Editor1: In a nutshell that is problem, but more specifically the authors will really rebel if we push them to answer to critical reviewers whom they feel are truly outsiders to climate science.
Editor2: So why not simply do what we normally do in these cases to keep the community happy. After all we know that none in the community will be upset if we play the rules in their favor. PR is PR and openness is a good selling point for the community but in the end we serve the community and it is the community that should set the tone.
Editor1: The community has always come to our defense before when we bend and interpret the rules, but in this case I feel we must cover ourselves by reviewing a paper which has come to be controversial by inviting additional reviewers.
Editor2: Ah, yes the time limit has passed for the open forum so our invited guests can now review out of the public glare. Remember that time limit thingy as it well could come in handy if we are accused of bending the rules. We can use it to show that we steadfastly adhere to the rules.
Editor1: Yeah, thats the ticket.
The above is a fictional account only to outline possible motivations for actions. In reality I would suggest that most of the above took place more in the form of progressive reactions. Somehow also the original script with the original actors was funnier.
Re #178, #179… hmmm… good idea.
Stan Palmer says:
September 28th, 2007 at 8:27 am,
What field do you work in?
#157 — Jerry Browning wrote, “The manuscript wouldnt stand a chance of being published in a reputable mathematical journal.”
#164 — Gerd replied, “Thats the point. And it is a trivial point. Which climate science paper would be published in a math journal? None.”
If I’m not mistaken, the Jerry’s meaning was that the manuscript would not be published in a math journal because the the Juckes paper was demonstrated — that’s demonstrated — to be founded on mathematical garbage. It was a bad paper, Gerd, your demurral notwithstanding. That is the whole point. Apart, I mean, from the derivative point of the poor professional ethics at CotP.
Not to wander too far afield here, but I’d like to summarize the AGW bidding (using Steve M.’s worthy terminology.)
1) The hocky stick is pure trash. M&M03, 05 demonstrated that fact. Steve M. has continued his relentless examination of proxy thermometry and continues to find it entirely wanting. Really sincere congratulations on keeping your civility in the face of continually shameful treatment, Steve. But anyway, people like Juckes continue to publish me-too Mannian analogues abetted by tendentious journal editors like Goosse. Paleodendrothermometry extracts quantitative results out of qualitative judgments, and when faced with this spectre of false precision on CA, Rob Wilson, a good-guy player in the field, is dismissive. Et tu the rest of the field. Principle components as such have no physical meaning whatever, but following Mann’s malfeasance paleothermometric climatologists negligently continue treat PC’s as physically orthogonal data sets.
2) Over at surfacestations.org Anthony Watts and his volunteers have surveyed 33% of the USHCN and found that 85% of the stations don’t meet code. Meanwhile, the ‘Where’s Waldo” threads here at CA have found that in the ROW, South America and Africa are MIA. Doug Keenan at infomath.org has evidence that the surface record of China was fabricated, and in response Phil Jones shows concern by remaining adamantly obstructionist. That leaves Russia, Europe and NA for the Northern Hemisphere and Australia, NZ, and perhaps South Africa for the SH. The 85% deficient US network is commonly held to be of the highest quality. Is the Russian network that good? Is Europe’s? With Hansen’s typically trendy adjustments plus all the rest of that in mind, a better estimate of the so-called 20th century global average surface temperature increase is more likely to be 0.4C(+/-)0.3C. I.e., no big deal.
3) The representation of uncertainty in GCM climate projections is unbearably specious. Numerical error propagated into and through physical theory becomes physical uncertainty and accumulates in an iterated time-wise temperature projection. The wise scientific heads over at the IPCC seem somehow to have overlooked this along with, apparently, the world’s entire inventory of climate modelers. Probably because that insight is hiding under the bed behind the dust-bunnies where the theory-bias error is also hiding out.
And so at the end of it all, where exactly is the A in GW? Over to you, Team Emperor.
RE 198: Damn pat, I thought I could wax elephant.
Pat Frank (#198),
Your interpretation of my comment is the correct one. Thanks for
stating it so eloquently and summarizing the AGW “evidence”
so succinctly.
Jerry
Re: SM #190
“Id say to Juckes and Weber ..”
Unfortunately, the position of the editorial board is already
fixed and unlikely to change unless you can arrange to have a
horse’s head left in their beds.
One form of redress is a refereed comment once it appears.
Let me tell you a story, earlier this year I noticed an
article by A appear in journal X. This was unusual in that I
had already refereed the article for journals X, Y and Z
a year ago. I was in fact the adjudicator for journals
X and Y to sort out the confliciting referees reports.
Anyway, next time I submitted an article to Y, I asked
my file editor, how come the article by A was published
since I’d already rejected it?
So, anyway, my editor says ???, this was a new article and
your name was not on the file.
Alright, I’d had noticed the title had changed, but the article
had 95% overlap with the previous version. Obviously, the
author had changed the title, submitted again, while pretending
it was a completely new submission. So I wrote back to my
editor, this is the file ##, for a manuscript which is 95% the
same. It was a big file, BTW.
My editor, remained mute on this point. But then, what could he
say or and could he do? It was not his fault, but author A had
pretty much dudded the journal (and the quality of the referees
obviously left much to be desired). At this stage, I can
jump-up-and-down demanding retribution, that the article be
unpublished (and how would that be accomplished?) and in general
make life uncomfortable for the editors.
But why bother, I had made my point and author A has his name on
the hit list. If I really wanted to, I could write a comment.
But basically, the article will be ignored by everyone who
actually knows something and I have better things to do with my
time.
Take home message, shrug your shoulders and move on. You might
communicate with the editors but just speak your mind but do
not put them on the spot by demanding retribution or acknowledgement
that the process was corrupt, perverted or whatever. If necessary,
write a referreed comment (by the way, comments always engender
a lot of work for any editor) on matters of fact that were
wrong in Juckes.
Jim (#201),
I have seen this suggestion before. A journal publishes a piece of junk and then tells a disgruntled reviewer to write a comment essentially wasting
additional time of the reviewer to correct what should have been done in the review process. I bit off on this suggestion one time in a comment on such a piece of junk. Yes, we destroyed the “science” in the nonsensical manuscript. But the journal that accepted that piece of junk is still in business. It is a no win situation and the open blog is more efficient at
revealing the smoke filled back room politics. I might also say that when reviewers could not stop one of our manuscripts because of the strength of the mathematics, they would threaten to comment on our article, but the
threats were never carried out or backfired.
Jerry
jae says:
September 28th, 2007 at 10:24 am
Hmm, we already have a LOT plastered on CA. Will this be Climategate?
I like Climate in Wonderland.
Re 164
“And while I agree with many of the expressed criticisms, one should not overdo it and demand mathematical rigor in each and every step. BTW, econometrics, which often serves as CAs role model of applied statistics, did not come up with any useful economic forecast so far, did it? How would that compare to climate forecasts?”
This is either a cheap jibe or ignorance. Econometrics, especially the portions that Steve refers to – is about the theory of non-experimental statistical inference. It is not just, or even primarily, about forecasts. While it has applications to forecasting, it also has many other applications including how to do adequate hypothesis testing when the assumptions of “ordinary” statistical inference are violated. Much of the time series work in econometrics was set off by the observation that atheoretical time series models outperformed the econometric forecasting models of the 1970s. The response was to marry time series insights with the theory-based models. These models, though far from perfect, do deliver better forecasts than simple no-change (or no-change in growth rates) forecasts, or atheoretic time series models over short time horizons (4-8 quarters.)
#204. Econometrics and business finance have also spent quite a bit of time and effort on problems of spurious correlation – on exactly why stock market “systems” don’t work. This is precisely on point in Mannian and Juckesian proxy work.
Re Gerald
“I have seen this suggestion before. A journal publishes a piece of junk and then
tells a disgruntled reviewer to write a comment essentially wasting
additional time of the reviewer to correct what should have been done in the
review process. I bit off on this suggestion one time in a comment on such a
piece of junk.”
This reaction seems a bit over the top. If everytime a journal made
a procedural mistake it ended up being liquidated, there would not be any
journals left at all! I have written comments myself, and they are
are more time consuming than normal articles, and I mainly do this
when I am particularly irritated (this describes SMs state of mind)
and prepared to devote time to the fight.
What you seem to implying is that SM undertake a course of
action to destroy COTP or get all the editors sacked. They will
really like that!
BTW, I noticed that you still sent stuff into the
JOURNAL OF THE ATMOSPHERIC SCIENCES after the comment
in 2000.
Re: Gerald 202
“I have have seen this suggestion before. A journal publishes a piece of junk and then tells a disgruntled reviewer to write a comment essentially wasting
additional time of the reviewer to correct what should have been done in the review process. I bit off on this suggestion one time in a comment on such a piece of junk.
Yes, we destroyed the science in the nonsensical manuscript. But the journal that accepted that piece of junk is still in business.”
This seems a bit over the top. If every journal that made a procedural
or refereeing mistake was liquidated, I don’t think there would be
any journals left. I have written comments myself, I think I have
four now, but I only undertake them when my level of irritation
is sufficient to carry me through the rather exhausting procedure.
I do not think it is SMs best interests to initiate a course
of events that aims to destroy the journal or have the entire
editorial board sacked (I may be implying a bit too much here).
BTW, I did notice that you still published in the Journal of
Atmsopheric Sciences after your comment in year 2000.
Jim, we get your point: you are not disposed to be a fixer of the system or for that matter dwell much on its problems. That the intelligent and informed reader can decide the merits of a paper(s) that makes it through the holes in the system is apparent from the discussion here of the paper in question. By Steve M taking this a step beyond the fat and happy stage and not letting it all go at that, he prods the system and to his credit he gets responses. My selfish interest in all this is that it affords me a look inside the system that I otherwise would not have. That the exchanges do not attempt to be so polite as to be esoteric provides, in my view, a better look at the climate science publishing world.
For those of us not directly involved in publishing scientific papers in this field, it affords an additional point of reference when judging the worth of what is being published in the climate community. I never re-entered the academic world once I left graduate school, but, as a graduate student working on a daily basis with professors, I saw first hand how large some could loom over the long haul and how small some could act on occasion.
Sorry about the duplicate post. Sometimes a firewall gets in
the way and I do not know whether a post is successful. SM,
could you delete one of the posts and also this post as well.
#207. Jim, I realize that I do a lot of things that are “not in my best interest” – running climateaudit is probably top of the list.
Perhaps because my background is in business and I have experience with securities regulators – where conflict of interest and misrepresentations are taken seriously – I simply don’t accept the lack of moral compass that people try to fob off in Team climate science. Sure it seems quixotic to try to change journal practices, but I’m trying to do so. I’ve drawn a lot of attention to data archiving as an issue; and while progress is slow, I can see some progress.
In some cases, it’s important that the authors be honest, as opposed to getting into a Comment-Reply neverendum. Wahl and Ammann stated that all our results were wrong and, among other misdeeds, withheld their verification r2 results (which confirmed our results.) As it happened, I was an anonymous reviewer and requested the verification r2 results, which they refused to provide. They said that their concurrent GRL submission showed that M&M were incompetent. As it happened, their GRL submission had already been rejected and they had intentionally try to mislead Stephen Schneider, which I pointed out to him. Not that Schneider cared.
I met with Ammann in San Francisco – I bought lunch. As noted previously, I offered to cooperate in assessing exactly what we agreed on and disagreed on in a joint publication as our codes matched; he said that that would be bad for his career advancement. (BTW I made the same offer to Nanne Weber; she also turned it down.)
I told Ammann that he was obligated to report the failed Mann verification statistics and it would be a mistake for him not do so so. He said that he wasn’t going to report the adverse verification statistics. I filed an academic misconduct complaint against Ammann. I pursued this with no satisfaction whatever as Ammann seemed like a nice young man and I’d rather avoid this sort of thing; I gave him every opportunity to change his mind. In the end, the withheld verification r2 statistics were included in the revised version (the revised version in turn being withheld from IPCC WG1 until it was made an issue at climateaudit.) The North panel cited Wahl and Ammann as a source for the failed verification statistics. So now this is on the record from Mann’s own acolytes and not merely in the he said-she said. So I am prepared to be persistent about these things.
Jim, you also purport to describe my state of mind as follows:
I actually work quite hard at not being angry and generally succeed. Usually my attitude is more one of puzzle solving. I write a complaint and I get fatuous comments back, that are wrong or off point. Instead of getting angry about it, this intrigues me. I wonder – OK, now I’ll take a closer look at the matter and see exactly what policies are involved, what the back story is, because this doesn’t make any sense. In this particular incident, because it originated in Holland where matters M&M have got a lot of attention, there’s the potential for an interesting back story: why was Nanne Weber funded for this study in the first place (it arose out of the Dutch attention to M&M arising out of Marcel Crok’s award-winning NWT article)? Why was Juckes chosen? How did the most conflicted CP editor get his claws on the article? Did he do favors for the authors? Does the Juckes article as revised withhold adverse verification statistics, as the Mann and original Wahl and Ammann article did?
Re: Ken #209
How did you know I was “fat and happy”!?
I am not going to predict the outcome of this entire
blog based way of doing science. It will certainly be
interesting to see how it pans out.
My concern is SM getting something into “the system”.
Basically, the whole Academic publishing business
is a game, and has its own set of rules. I am part
of the system in physics, and I know how to play
the game. I read this blog, and I see some incredibly
idiotic suggestions from some of the SM cheerleaders
that are essentially self-defeating. There were posts by
people other than myself, who are established in their
Academic communities, and they were more or less
suggesting (like myself) that there are better ways
for SM to accomplish his aims.
There is an underlying theme here from some of the
cheerleaders that
All climate science and all climate scientists are institutionally
corrupt. In which case, what about Gerd, and how come
the HT get their articles rejected every now and then?
You will find there is a greater diversity of opinion
than that.
There is undertone in this thread,
1) That playing the game is incompatible with moral purity.
Well it isn’t.
And let me suggest that there is a bit of matyrdom
complex rolling through here. Basically, “we lost
because of the corruption and malfeasance of the
system” leading to a misplaced warmer inner glow. Now
while there maybe corruption, going about your business
with poor tactical and strategic acumen is also
leads to adverse results (and a lot of people who
have adverse results in the academic sphere, often
attribute it to a corrupt referee, or such, because
that is a more comforting explanation than the alternative
which is that it was due to their own stupidity).
Anyway, I’m back on this tedious point again and I just won’t let
it go. But of course, one of the themes of this entire thread
is the extent that SM should question the editors of COTP
until they admit their mistakes :-).
BTW, I will try and go back to lurking and resist the temptation
to post.
Re: #209
“Jim, you also purport to describe my state of mind as follows:
SM, yeah, I should not have tried to guess your state of mind.
It is always a mistake to do that.
You have made no efforts to hide the fact. You are part of a system with which you have learned to deal and profit from. I have no problem with that as long as I know from where you are coming.
Your references to wrongly motivated cheerleading may apply to some here but that should not in any manner or form change anyones view of what Steve M is doing or rights or wrongs of these specific issues with climate science publishing. Such baseless references that defenders of the science frequently make on their visits to CA here always appear to me to greatly weaken their cases.
The main outputs of all these discussions at CA are for me the learning experience that it provides, vis a vis evaluating the quality of climate science papers, the personalities involved and any legitimate defenses of the system. It is for the participants of blogs such as CA to learn by filtering out the chaff of biased cheerleading whether that cheerleading be in support of SteveM or in defense of a system or particular science community.
#211 I think this is the most sensible post in the entire thread.
Re: #201
Jim, you say that “…basically, the article will be ignored by everyone who
actually knows something…”. While true, this ignores the fact that climatology enjoys increasing influence on popular and political culture, where most don’t ‘know something’.
As for underlying themes here, this place attracts a pretty diverse crowd belief-wise. I think Steve’s been pretty clear on what he personally thinks.
#211. Jim, Ross McKitrick’s advice in this situation is exactly the same as yours. I realize that there’s all sorts of dreck in academic worlds, but it’s going to cost me time to deal with this particular dreck.
Once Juckes et al gets its phony stamp of approval, people will say that it’s time to “move on”. Of course, the Team wants to get the last word in and then “move on”. I’ll end up in squabbles with Climate of the Past about the Reply and get dragged into more controversy.
#211 — Jim, I’m an academic physical scientist as well, and have occasionally had substantive conflicts with others in my field. Typically, these play out pretty fast (a couple of years) because reference to fact and theory quickly determines who is right (if either party is). This is not the case in HT science. Mannian time-series reconstructions were clearly shown wrong. But rather than concede this and get on with good science, Mann and others fought back using polemical assaults, outright lies (‘calculating r^2 would be a foolish and wrong thing to do’), obfuscations of their own self-contradictory results, and persistence in using the very methods proved wrong. This is clear evidence of corruption. They have had the willing compliance of journal editors who have the professional expertise to know they’re wrong. This is evidence of corruption.
Further, I don’t know of any other field of science where this sort of thing is such standard practice. I also know of no other field of science where a blind commitment to false precision underlays an entire enterprise (dendrothermometry). Nor do I know of another field where systematic error analysis is so uniformly avoided as in climate modeling. Nor one in which bad results are touted with such certainty, as in climate science. Nor one which has made such an unholy and wholesale pact with propagandizing ideologues. Nor one in which character assassination is used so casually to enforce a viewpoint.
‘Widespread corruption’ may be the wrong term to describe these goings on. How about widespread delusional sanctimony? That, at least, allows for a kind of psycho-ethical exculpation. But in any case, widespread it is, and pathological it is. And scandalous it certainly is.
my humble 2 cents.
Peer-review is a sine qua non for being accepted in scientific circles; but once you are in the circle, it becomes evident that there are an awful lot of papers which are not only dreck, but in some cases even rotten to the core. Not that I approve; merely stating the obvious. Look at the office of research integrity.
The key issue is that you look better by publishing good stuff yourself, even if your good publications are showing that someone else’s data/methods are poor. Get the good publications out; then they are part of the peer-reviewed literature, and can be cited. Even the willingly -blind have to accept significant numbers of peer-reviewed papers that say something they don’t like.
jim’s general tenor seems good. Most academics run publishing for nothing, and you have to give a paper to someone who knows something about the area; so conflict of interest is endemic. The CPD paper is mildly embarrassing , but hey; it is a low impact journal, and the referee’s comments are public for part of the process. If juckes was evasive, it is part of the record.
Publish !
per
Re: #214
Rah, Rah, Rah, sis boom bah. Yay, Yay, Jim.
#218, per, you’ve been following this for a long time and if you and Ross say the same thing, I’ll accept the point. It irritates me that people like Wolff make false statements – would I prefer that Wolff’s misstatements were delusional or mendacious? I don’t know. When I was fencing with Karl Ziemelis of NAture on getting MAnn’s data, it was sort of fun. HE was very polished, very Sir Humphrey smooth but definitely impenetrable. At a certain point, you knew that you were getting nowhere, but I felt that he had at least understood the points – he just wasn’t going to concede on them. At the time, I’d have felt comfortable calling him up if I was in London and asking him for lunch. On the other hand, Wolff and Claussen seem deluded.
I should briefly note my complete inconsequentiality !
I am sure that you, and any objective observer, are fully capable of forming a view on the actions of an editor who is now on the public record. In fact, I have a little bit of sympathy for editors, who may be dragged into a situation where they are more-or-less obliged to honour the judgement of someone else. If an editor is left covering for a decision which transpires to be not perfect, – well, there are worse crimes.
Besides which, I have no feeling here for malevolence, merely the much lesser issue of less than perfect understanding, perhaps in a cozy context. I am sure that Lubos will back me up if I note the saying- against stupidity, the gods themselves contend in vain !
I believe I understand your perspective, as enunciated above. Publishing your own work in a good journal is much the best way to drive a stake through the heart of the bad math that is so pernicious for eco-science.
best regards
per
214, that was Niccolo Machiavelli speaking. Maybe he’s right.
Jim (#206),
The number of procedural mistakes increases with the distance from rigorous mathematics, i.e. there is more hand waving and games. Certainly the first journals to go would be the soft science ones. No loss. Note that
the reason that Steve M. has had an impact is because the hockey team and the NAS could not refute his mathematical arguments.
Jerry
Folks, also remember that one of my main themes has been that journal peer review is not a satisfactory form of due diligence for policy decisions. I haven’t grown up with journal peer review and I come at it a bit like an anthropologist. I like to see what happens when you do things. What happens when you complain to a journal? What happens when you ask for things? What happens when you file FOI requests? What happens if you publicize Science magazine about withholding data? (They don’t “appreciate it”). What happens if you ask the IPCC TSU for data? What happens if you ask a journal for data? Think of this abstracted from the particular issue, but as case study data.
Journal peer review is a cultural phenomenon, as is the subset in climate science. It deserves to be studied more widely. Most academics are so used to the system that they don’t perceive it as a cultural phenomenon – they just accept it or they have incentives to try to get along.
Does any of this prodding accomplish anything? You never know.
Steve,
It will be interesting to see Appendix A2 of the CP version..
#223
At the risk of being unpopular here, are you sure that Steve has actually had much impact at all? Pressure for archiving of data existed long before he started his blog and the idea that science should be underpinned by rigorous data analysis is hardly new. What has he actually changed? Not much as far as I can see. Some of this is down to his reluctance to leave the nice warm pool of CA and publish some stuff where people might actually see it (and E&E doesn’t count). None of this is to demean what he has tried to do, but it is to be realistic about the way in which science works. If he were to spend a fraction of the time he spends here in writing some papers then I suspect his impact would increase substantially. If he wrote a couple of papers outlining how to do really solid data analysis in reconstructions (with error limits!), rather than trying to pick fights all the time, then that would be real progress. If it was well written and in a good journal then young academics joining the field would pick up the methods and use them. Instead, Steve himself tells us that his biggest impact on a young academic so far has been to file a complaint of academic misconduct against one. Not going to win people round. It makes me feel like banging my head on the table in frustration.
I have no doubt that the cheerleaders here will just reply that climate scientists are all corrupt and Steve shouldn’t risk getting tainted by contact with them, but this is silly. There is no monolithic block of scientists engaged in a conspiracy and good work will get recognised – once it is somewhere where people can see it.
DaveR,
It seems that you are volunteering to coauthor a paper with Steve? Pick your
subject, I’m sure he will be happy for the help! Or are you just one of those
people that likes to nag for other people to do the work?
# 227
I wish I had the time or the knowledge to help him write some of his work up for the journals. But I have to publish in my own field and find it hard enough to find the time to do that. I’d like to think that a bit of nagging might actually help get him over his writer’s block. Some of the stuff he’s done looks absolutely excellent, but it’s hosted on a web site that might vanish overnight and it’s mixed in with a lot of general internet silliness which undermines his desire to be taken seriously. Factual, papers that presented a cast-iron way of handling reconstruction data would be a really strong and worthwile contribution to the science.
DaveR is right in #226. You should be publishing at least one paper a year, Steve.
E&E does count, however. M&M03 is the paper that blew the hockey stick to bits, and caught both the worldwide attention and the wrath of the HS society of reverence and worship.
No Pat,
I do not agree with you.
E&E does not count in a Mann made world.
And DaveR is simply wrong if he asserts that
“once it is somewhere where people can see it”
and refers to an obscure 1000+ mag. and not here in
the blogosphere.
Re:#226
DaveR, you say “…and good work will get recognised – once it is somewhere where people can see it.”
I certainly agree 100% and do endorse Steve publishing in a traditional journal. However, this blog isn’t ‘nowhere’. Even scientists ignore the internet at their peril these days.
#168:
No, and I explicitly mentioned that in my rejection of the first version. The second version that is going to print now (and which you still haven’t seen yet, I assume) has considerable corrections in this part. I finally decided to accept that version given that some remaining issues could be resolved.
You say/cite
but CP policies in fact state
Doesn’t this simply mean that after the interactive discussion the editor is free to proceed just like in traditional, and that is, closed review? – So what happened was that the editor approached 3 additional reviewers not despite of but because of the interactive discussion.
230, there’s an odd dynamic though, where the story has more credibility in the larger blogosphere if it’s backed up by an article in an obscure but peer-reviewed journal. You don’t get your message out in the journal, but you get your street cred that way. Your detractors can’t play the “amateur” card on you as easily as if you just posted it on a blog. The published paper then makes a nice annex to a blog entry.
In other words, it’s not an “either-or” proposition.
#176:
well, my point was not the most serious one, but now that you jump on it:
“Climate forecast” would be a purely physically based prediction of, say, the ENSO or the NAO, or the short-term predictions recently put underway by the Hadley Center. No such thing exists for economic models, by lacking first principles. And no such thing exists for the climate of 2100. That’s why we speak of scenarios, and you seem to know that.
Re: #234
Climate science has the potential, but surely it is currently a long way from physics and chemistry. I like to use the potential dangers of and opportunities for data snooping
as a measure of the direct applications of first principles — climate science to this layperson has a ways to go.
Re: #226
He probably has not made as much impact on climate scientists as he has on others outside the field because publishing in that system takes time as you and others have noted. That could also say more about the disposition of that community than Steve Ms efforts. Your reference to the search for good practices as not being new implies therefore it is not worth pursuing. I find that a bit confusing in terms of how problems are addressed.
You seem to generalize in reference to cheerleaders here (incorrectly in my view) and then make the obviously correct statement that generalizing about scientists is wrongheaded. Appearances of cheerleading comes in all forms including a rah, rah of scientists for peer-review. The only way to avoid this is to discuss specific issues such as Steve M attempts to do in introducing these threads.
In my view, Steve M’s publishing ambitions are probably a personal choice that he alone has to make. You would have to put yourself in his shoes to do that. Not everyone views the satisfaction from or the need to publish the same, but one does not have to be a politician in order to properly critique politicians. I do wonder at times if the frustration of participants here, such as you, is as much with Steve Ms failure to publish more or the fact that he points to problems with the peer-review process and products of it. I firmly believe that a knight in shining armor will not come along and rescue or make better climate science. I believe the adage heal thyself (with a little prodding) applies here.
Gerd, thanks for the comments. Your comments are considerably more reasonable than those from Claussen and Wolff, which intentionally or unintentionally aggravated the dispute. It’s interesting to note that you were one of the referees. You would be someone that I would have recommended so I can hardly criticize CP on that score. Having said that, I disagree with your two comments here about how Goosse handled the process. (And, as always, I welcome your rational and inquisitive approach.)
You quoted the following comment of mine:
This was an aspect of Wolff’s response that particularly grated. Wolff’s said that the adequacy of the answers was a “matter of judgment”. Perhaps, but an editor is required, at a minimum, to use “reasonable” judgement. Juckes’ answers would fail an undergraduate examination. Obviously no competent editor could honestly argue that Juckes’ answers were adequate. Wolff’s implication otherwise was false and pointlessly provocative. This provocation was exacerbated by Claussen’s statement that the Short Comments were not considered in reaching an editorial decision.
You agreed that the answers were not “adequate” as follows:
This is not as bad a situation as described by Claussen and Wolff. At least you agree that the answers were not adequate, and, even though the other two referees seem to have paid no attention to these Comments, it sounds like you may have. It’s still not what is set out in CP policies which state the following:
Under this policy, Juckes was not entitled to submit a revised version until he had provided adequate answers, which you agree that he hadn’t. This is very relevant to the debate: while Juckes may have patched up his revised version, there is still no on-the-record set of “adequate answers” to the first set of Comments. All you say here is that Juckes patched and improved the revision, not that he ever provided “adequate answers”. This has been a particular sore point, since Goosse personally assured Willis Eschenbach that he would require adequate answers and then double-crossed Eschenbach on the promise.
As we sit, while there is a lot of water under the bridge, there is still no set of “adequate answers” by Juckes on the public record, as there should have been before the submission of a revised version. Even at this late stage, I think that you should require Juckes to place such answers on the record, as they should have been long ago.
You also quoted my following comment:
noting the following CP policy (which I think that I’ve quoted):
The full sentence is:
You ask:
That’s not the way that I read the policy. For the situation as you describe it to apply, the clause would have to read as follows:
That’s not what it says. It says:
So what’s the difference between the two situations. I think that one needs to understand clearly the differences, if any, between the “completion” of traditional peer review and “traditional peer review” simpliciter. Forgive me if I seem legalistic here; I’ve had a lot of experience with contracts and, unlike most academics, have learned to pay very close attention to the exact language; I assume that all the words have purpose. My interpretation of the difference is that the “completion” phase is premised on answering of all comments, positive initial review and conditional acceptance, and that, in the completion stage, the referees check to see that requested revisions are made, not to start from scratch. They don’t go back to square one. Contrast this with what happened here. Goosse took the process essentially back to square one and conducted a closed review process, all of which is off the record. Whether this is a good process or a bad process, it’s not the process described in CP policies. So in answer to your question, I don’t think that it’s the same thing at all. If you can show how these words can be interpreted otherwise, I’d appreciate it.
I doubt that in the short history of CP, that there is any precedent for Goosse’s handling of the situation – where an author failed to adequately answer questions raised in the Interactive Public Discussion; then submitted a revised version without doing so; where 3 new referees were added for the revised version, which was treated for all intents and purposes as a de novo review. Perhaps you could ask Claussen whether there are any precedents. (If there are, that would affect my views on the matter.)
As noted before, the entire matter is made worse by Goosse’s conflicts, which were of two types: his collaboration with co-author Nanne Weber (which was specifically prohibited), but probably a worse conflict was his prior collaboration with Mann and Bradley, whose work was obviously at issue. At this point, we won’t know what an unconflicted editor might have done. In my opinion, the only way to really clear the air would be to put the revised manuscript back into the CPD process as you were required to do. If the revised article is satisfactory, it should be able to withstand open review.
Steve M,
The following quote is from Steve R (#226).
Might I say that I have also seen this type of comment before in the form of “we knew all of this” even when the field didn’t know any of the mathematics and the reviewer was defending his turf. Don’t get sucked in by this type of statement. You have had an impact and your auditing of this area has revealed a number of serious problems with climate science(?). In my own case I was drawn to your site by your honesty and open mindedness.
Jerry
#232 (Gerd):
Let’s forget the technical issues for a while (of which some were IMO incorrectable without a complete rewrite, and it will be interesting to see how they are handled in the accepted version). At least in my field, regular papers should contain some novelty, and I can say that I’ve rejected well written papers solely based on the lack of novelty. When I’m reviewing a paper I tend to ask myself what information readers will get from this paper they won’t get from other papers.
So my question to Gerd as a reviewer is what novelty worth publishing did you find in Juckes et al.?
I’ve never been an editor, so I’m just applying common sense to this, although I have published reviewed papers.
As an editor, if I sent a paper out to three reviewers, and two said it was fine while one found serious errors in the paper … I’d fire the first two reviewers for missing the errors, and hire two more.
This is doubly true if the errors had been previously pointed out in a public review process.
But what do I know, I’m a reformed cowboy, not an editor …
w.
#237. Steve, you write
Wouldn’t that imply that the completion-phase referees are the same as the original ones? I read
(from CP policies) somewhat differently.
re: #239
some papers merely confirm previously published results, a process akin to auditing, I believe.
It is appropriate to note that there is a “pecking-order” of journals. The highest require work of the utmost novelty; whereas the lowest are sometimes happy that you have spelled your name correctly. So the issue of how much novelty you need for a peer-reviewed publicatoin is very much a grey area. COPD is not the top journal.
re: #240
by and large, referees do their task for free, and editors have to ask referees for the favour of their services. If you were to “fire” referees, they would be better off than if you send papers to them; so that is scarcely a punishment. Most referees have areas where they are thoroughly familiar, and associated areas where they have less knowledge of an area. Humiliating a referee when they are outside their area of knowledge merely loses their expertise when you need their specialist area.
Sometimes, there can be less than a dozen people in the world with the expertise to answer a question. If you have a surefire way to locate THE specialist(s) necessary for a world class review, when you don’t pay them, it takes them a whole load of time, you don’t know them, and you may not even know they exist or that you need them, then you are ahead of the game in scientific publishing. I am not trying to be trite; merely pointing out the practical difficulties.
per
#242. per, The stated purpose of open review at EGU journals is to mitigate exactly that problem. I think that you’re missing an important nuance of the objection here. Among other things, it’s the failure of CP to honor their open review process. They had careful, if”unsolicited,” review comments from highly knowledgeable people that they say they ignored. Instead of paying attention to these knowledgeable comments, they went and got new referees and violated their open review procedure.
#241. Gerd, I don’t understand what you’re saying. How do you you interpret the phrase “the completion of a traditional review process” – as opposed to just a traditional review?
Re:#241, 243
The wording of the description of the review process (http://www.climate-of-the-past.net/review/index.html) in step 8 doesn’t indicate whether the referees are newly chosen or the same as in the Open Discussion phase. It thus accommodates two standard variations of the process: 1) If the editor feels a decision can be made based on the current referees and Open Discussion, no new referees are needed (this should be the majority of cases); 2) In exceptional cases where the editor cannot make a decision (again, including consideration of the Open Discussion), one or more additional referees are recruited.
Unfortunately, in this case it seems the editor “rolled-his-own” variation by ignoring the Open Discussion comments.
per (#242),
An editor has tremendous control over the reviewers he/she chooses. If the editor is biased in any way, it is quite easy for the editor to choose the reviewers according to those biases. If the editor is qualified and impartial, he has the power to reject an incompetent reviewer’s remarks. The sad thing about this whole process is that there is little recourse within the same journal when a biased or incompetent editor rejects a quality manuscript, even though that journal is most appropriate for the manuscript.
I have made the following suggestions to JAS (and they were ignored). Because of the possibility of bias on the part of an editor, have a list of reviewers for the journal on various areas. The reviewers are then chosen randomly from the subject area of the manuscript and the authors allowed to respond to the reviews at this point. This entire part of the review could be performed by a computer.
The reviews and responses are then assigned to an editor with no apparent conflict of interest. Then the editor can make a judgment on the manuscript. Although this does not entirely remove possible bias of an editor, it reduces his power in the selection of the reviewers (and I believe this is one of the main problems with the current system).
I have always signed my reviews because I do not like the smoke filled back room feeling of the review process and am willing to stand behind any comments I make. I am also fully aware how many reviewers take advantage of the anonymity to stop manuscripts that have an adverse impact on their egos or funding. I believe that if the reviewers were required to sign their reviews, much of the games would stop. (This is equivalent to the justice system where the accused is able to face the accusers.) If the reviewer has a legitimate scientific comment, he/she should be willing to identify himself (herself) ( just as Willis did).
Jerry
One of my favorite quotes is, ‘if you pay only peanuts, all you get are monkeys’ – but that is definitely not what you get with most academic journals and referees. In my experience as a journal editor (although not in a field related to climate science), reviewers do an outstanding job, usually putting in considerable work and time, being constructive and considerably helping authors with fresh ideas and constructive criticism. As an editor I can ask the best people in the world in a particular scientific field to give up their time freely for no reward other than that is how the system works! Journal editors in almost all fields also get NO pay for their work. Reviewers get NO pay for their work. Can you imagine asking the best lawyers, accountants, surgeons – you name the area – in the world! to freely give up hours of their time to review other people’s work – usually considerably improving it for nothing other than a brief acknowledgment? Not likely without a hefty bill is it? and yet that is how the scientific system works.
OK, so perhaps that makes some of you think, amateurs! But I am proud of the system and what, in general it produces. I can’t comment on climate science because I am not involved in that area but from what I am familiar with, the system works with decency, honesty and integrity and is generally very constructive, helping authors to produce the best product. I would like these points to be borne in mind whilst general peer review bashing is going on.
Having said all that, peer review is a good system in general but not by any means perfect given the way that it operates. I would fully agree that once work becomes so significant that billions, or potentially trillions of dollars/euros/whatever currency you fancy, of world economy – depends upon it that well funded, thorough and independent scrutiny of its supports should be undertaken. That is what I am not seeing with climate science.
#245
I wish it were possible to hold up a single system as the best way forward. While the system you suggest sounds good, I am sure it too would have its problems. One of the difficulties of open review is the possibility of retribution; and yes, I am certain that would happen. Just look at Mann’s refereeing in COPD; just imagine him if he knew you had bounced his grant/ paper.
#243
In all faith, you need some sort of umpire at some stage. The umpire doesn’t necessarily have the skill set to cover everything, and has to deal with a whole load. Faced with a contentious set of comments that they may not be able to evaluate, it may well be a rational decision to go ask a whole set of new referees. If they come back positive, or are eventually satisfied, then you have to weigh the positive comments against the negative comments (from unknowns). You may know you are right, but I put it to you that a non-expert editor may have some difficulty in balancing your opinion against a set of referees who say the paper is okay. I am equally certain that such diametrically opposing referee reports are part and parcel of peer-review. Yet this is normally dealt with in an urbane manner.
Editors will also bear in mind the status of their journal in deciding what to accept. There is always another experiment that could be done, or some flaw in the approach. You are not going to set the bar too high for COPD.
I think it would be a much better approach to be humorous about the COPD paper; and much more effective. But even better, is to publish 🙂
per
In some cases, having a ref that doesnt’t know the subject is a good thing, if you ensure:
They are sufficiently intelligent
They don’t know the participants
They have any pre-conceived notions
They don’t have any stake in the issue
They are outgoing enough to put up with any pushback
They are given some mechanism of enforcing their decisions
Actually, that should be that one of the reasons it might be a good thing is they probably
have no pre-conceived notions.
I have found the ongoing discussion here to be enlightening vis a vis climate science peer-review and the peer-review process in general. It also reinforces an instinct not to prejudge a persons POV until you understand from whence it comes. It has become obvious from the discussion in this thread that no one is going to change any other ones mind on these issues.
I also think that when it comes down to lawyerly interpretations, the discussion veers from the more important issue of what are the intentions and mindset of those carrying out the peer-review process. Rules can be interpreted willy-nilly to serve the purposes of interpreter and the system administrators, but in the end, the critical question has to be: what is that purpose?
I have a problem with a discussion that also has generalized the specific issues of peer-review in climate science, and a particular part of the field at that. I see climate science certainly differing from the commonly labeled hard sciences and from other softer sciences by the issues and seeming immediacy posed by AGW and the related policy issues that appear to be part and parcel of many climate science papers.
Therefore, when a scientist from outside of climate science comes here to defend peer-review as they view it from the perspective of their own field, they certainly would not necessarily relate to the experiences of Steve M with climate science. Settling issues at a slower, more methodical pace and/or within the confines of a harder science with fewer gray areas is certainly not what I see in climate science at the moment. The peer-review system with all of its problems which scientists appear to freely divulge here apparently does not have the potential repercussions for the general case that it can have for climate science. Because of the critical policy implications for work coming out of climate science, it also is more susceptible in my view for politics entering the science and the peer-review process.
I would conclude by suggesting that this discussion needs to stay specifically on the specific issues that Steve M raises and we need to find the intent of the peer-review process specifically in these cases and avoid lawyering it to death.
Perspective is important.
Regardless, if I was the boss of a lot of these folks, I would be holding their feet to the first on it. I hate sloppy work from myself, those that work for me even more.
IL (#246),
I have seen both the best and worst in editors and reviews. To say that an editor or reviewer does it for free is not quite the case. An editor likes the prestige and vitae line item. And both editors and reviewers can protect their funding and power trips by controlling the results. I
find it quite pathetic that the so called educated and scholarly resort
to retribution and other unsavory tactics. In my experience this group is quite large and tends to consist of the scientists that are the least competent.
Jerry
Jim in #211 said:
You miss the point: the group gathered here is challenging the way so-called “professional” scientists are “doing science.” The way these professionals are “doing science” has the potential to dictate radical changes in the way man interacts with the earth. Their way of “doing science” needs to be examined far more closely than it has heretofore.
I do not speak for the people here, but my sense is that they would view you as a tired old scientific academician who has knuckled under to the rules of the “game.” They would also suggest (and have) that the stakes involved here are far greater than they are in any other scientific discipline, particularly if the underlying “consensus” science is flawed.
I am one of the cheerleaders. By that I mean, I have, to paraphrase Shakespeare, small science and less climatology. I can contribute little of scientific value to what goes on here, but am fascinated by the implications of what is being attempted. I’ve always believed that there was a misanthropic side to environmentalism that could conceivably be coloring research done to expose and alleviate anthropogenic environmental problems, and not just those in climate science. As a builder, for example, I am aware of the impact environmentalists had on the timber industry in the Northwest. And while I’m not opposed to sustainable forestry, I think the methods used that eventually crippled that industry were heavy-handed.
I have a degree in history. My sense is that something historically significant is going on here at ClimateAudit. No one I’ve read who posts here is saying all climate science is corrupt. If, however, policy changes being introduced by governments around the world– changes that could cost taxpayers, a variety of industries, their workers and consumers countless billions of dollars– are based on faulty science, then we have a serious problem. It is essential that the science that is propelling these changes be above reproach. From what I’ve seen, there are understandably grave doubts about the accuracy and veracity of the science that is being relied upon to write laws that will profoundly effect future generations.
Playing the game by clinging to corrupt or incomplete science is immoral. Mankind is being scolded into believing that we face catastrophic changes unless we radically alter the way we progress and prosper on earth. We need to know that these demands for human behavioral change are based on predictions that are founded in science that is accurate and verifiable.
This is preposterous on its face. I don’t speak for Steve, but my impression is that this blog exists to examine the science frequently portrayed as infallible by people who often view themselves as the self-appointed messianic saviours of mankind. Nor has anyone here that I’ve read claimed defeat. What is defeat, afterall, given the mission? To the contrary, the work here continues and most contributors seem optimistic that it will bear fruit, regardless of whether it confirms or disproves the assertions of the AGW believers. So much for “poor tactical and strategic acumen.” I see people working calmly and efficiently trying to improve the science.
Because of your cynicism, your use of the word “tedious” is appropriate. I hope your questions have been answered–if not by me, then by others. Afterall, I’m not a scientist who’s become jaded by “playing the game.” Rather, I’m someone who would like to see the complete truth about AGW revealed.
Duke. Well said. I agree with all the above.
I have a shorter reason. SteveM and others have shown that the Peer Review Method of codifying scientific knowledge is capable of consistently producing wrong outcomes, particularly in the field of climate change. Partly, it is to do with a failure of the quality of the people involved, but ultimately, it is a systemic failure. We must have a system which is designed to be failsafe, and that is not reliant on the moral courage of individuals. The Peer Review System is not failsafe.
#239:
Jean, studying the sensitivity of reconstructions to different proxy selections and algorithms is always worth publishing. Specifically, I said in my review
#243:
That’s too bad, Steve, but not relevant at this point (I don’t know either what that completion refers to). My question to you was: Does your interpretation of the CP review process not imply identical referees for the entire phase?
#255: So what novel information you obtained from the paper? To me the varying of the simple linear regression type algorithms is pretty much covered here and some associated problems with Juckes et al’s proxy selection can be uncovered from here. 🙂
From 155: Eric Wolff, a CoP coeditor, responded:
Does anyone else feel that this argument not only does not stand up, but does not even apply to the paper in question? The Juckes paper was not less extreme than a paper with 80 co-authors, it was not at all comparable. It had only a handful of authors, and the journal had 30 non-conflicted editors available. Yet who did the editing? The most conflicted editor. THE editor who had prominent, current, collaboration with a co-author of the paper, in clear breach of the journals policy.
The policy is not really all that tough. All the journal has to do is find an editor who has not recently been working with a papers co-authors. The policy is also mandatory, not just desirable. Implementing it was easy, not just possible. Whether the policy might have practicable with an 80-author paper is irrelevant.
The fact that neither Goosse nor the Chief Editors perceived a conflict of interest is also irrelevant. The whole point of a written policy is to avoid relying on the self-perceptions, and potential self-delusions, of the editors.
Duke,
Far from being defeated, I see us gaining ground everyday on “The Team”.
The science has always supported the anti-alarmist position, and now the weight of the evidence is starting to impact policy makers, despite the noise and interference of those who livelihood and reputations depend on the public being paniced into supporting the alarmist position.
Jean S,
in addition, we can read this paper, check this reference,
and finally we have a paper with something about estimator variances (Eqs 2.7-2.9), confidence region (Eq 2.11), and even diagnostics (Sect. 2.4). Pretreatment of data is also mentioned (Sect. 3.5). Quite easy to find out that Juckes INVR equals to Sundberg’s
(Eq 2.3), more general is $latex \hat{x}_{EGLS[}/tex] (Eq 2.5) but I guess standardization proxies does at least something like that.
CVM with uncertainty estimate from calibration residuals is not mentioned in Sundberg’s paper, and if that method is mentioned in CP version of Juckes et al, I’m sure Sundberg will update his paper. Maybe there’s the novelty, estimator with upper-bounded errors, regardless of data. But same kind of method is embedded in MBH98, so Mann should be acknowledged.
#260:
UC,
Indeed, how could I miss that! The methodology is truly groundbreaking for the whole scientific community. No more error bars punching holes to your ceiling!
Gerd, you say:
But the report should not be misleading. How do you justify CP withholding information that trivial variations in proxy selection result in different medieval-modern relationships as raised here?
How do you justify claims of “99.98%” statistical significance for the Juckes reconstruction when the trivial variations are also “99.98%” significant”?
Sorta OT but sorta not, UC, Jean S. and anyone else interested, have you looked at the new Van Trees book (edited by), “Bayesian Bounds for Parameter Estimation and Nonlinear Filtering/Tracking”? May have some useful nuggets of information related to some of these issues. It is in my “recommend” list from Amazon, but I’m waiting for some reviews before purchasing it.
http://tinyurl.com/22m4ob
Mark
#263: Mark, it is a reprint book (a collection of papers). You can save some of your hard earned ExxonMobil money, and read the original articles 😉 The table of contents is here.
Yeah, I knew that, but I figured it may be a good collection all contained within one convenient location. Accessing the actual papers sometimes costs significant ExxonMobil dollars (you know, the kind we’re all getting but never get to spend) as well. I can’t tell you how many $13 IEEE papers I have. 🙂 Besides, they have included some of their own text as well…
Mark
Steve M (#262),
Now you begin to see the problem. The manuscript was accepted in spite of serious scientific issues. Why? Because of an editor with obvious conflicts of interest and reviewers that think that a trivial experiment is worth publishing. And as someone else noted, now that article (and millions of other ones accepted in the same vein) will be referenced by the same network in order to gain citations and to waste other authors time during their review process. You can also see why I became disgusted with the game.
Jerry
Jean,
It is kind of hidden in MBH98 algorithm description (unlike everything else 🙂 ) , but see
http://holocene.meteo.psu.edu/shared/research/MANNETAL98/METHODS/AlgorithmDescription.txt
#262: Steve, #256?
Re: Taxi-drivers and peer-review
Yesterday I was in a Taxi, travelling to the city
from my urban campus. Anyway, as part of conversation
with the driver of the Taxi it became apparent to him
that I was a physicist. Well,…
He started a rant about a particular paper in published
by Luis Alvarez on the JFK assasination. Anyway, Luis
pointed out that a bullet entering from the back, would
not necessarily lead to the head recoiling forward. It
all depends on the velocity and amount of blood, bone
and brain that also leave the head travelling in the forward
direction. Our Taxi-driver really, really disliked the
the publication of this article by Alvarez, since it
obviously contradicted his consipancy theory. One of his
issues leading to his sense of moral outrage about the
article was that the Alvarez article was not peer-reviewed!
This peer-review issue does seem to crop up in strange places.
#269:
And that is relevant to the Juckes paper controversy in what way?
Or is it irrelevant?
Your call.
Jim 269, you’re lucky he didn’t start in about 9/11, and how jet fuel can’t melt steel.
Re: #269
Unfortunately, as I recall the poll results of the US public, the taxi driver would be part of the consensus on this issue. To know you as a physicist and about peer-review tells me your driver’s background was atypical of a full-time taxi cab operator or he was profoundly over qualified.
272, don’t underestimate how much junk science a taxi driver can pick up from the internet if he gets connected to certain sites. Hordes of dilettante scientists is one of the prices we pay for for Al Gore’s invention.
BTW, there is an interesting video produced by Penn and Teller on Alverez’s thesis where they wrapped a melon in duct tape, and shot it with a rifle, and sure enough, it fell toward the gun, as Alverez predicted.
Steve, there is a pattern of unresponsiveness in this blog, with a pile of outstanding issues having accumulated over time. Where are the answers to #7 here, #21 here, and #41 here? And now again #256 of this post.
I’m sure there are more, and the pattern is always that you “move on” to what’s more important to you at the moment. I know you are very busy catching flaws in the work of others, which certainly is very essential work. But if you don’t meet your own standards in this enterprise this blog, with its lack of memory, is little more than white noise.
Pardon me, Gerd, but I would take exception to that. Steve is but one man and no man can answer every question which is posed to him.
Nevertheless, unlike many others, he at least tries to answer the vast majority of issues put to him here.
I would also add that, whilst you seem to insist that Steve, personally, answer you, he is most certainly not the only knowledgable person here and, in most cases, others have endeavoured to provide you with answers. That is unacceptable, it would seem.
It is so unfair as to be almost unspeakable to accuse Steve of “moving on”, given the context of this blog. Steve puts an enormous amount of time and effort into answering past questions, is very persistent about past issues and I have often seen him respond to peoples comments in posts which he made months ago.
Your post bears the implication that Steve is trying to hide something, deal selectively with certain issues and ignore others, in pursuit of some undisclosed agenda.
That’s never been my impression and I believe it’s an unfair characterization.
You had a choice of politely requesting that Steve address some outstanding issues of concern to you, or making a not-so-subtle accusation of bias and “political” agenda.
You chose the later. Your choice.
Bradh, I would think it best to allow Steve M to reply to the substance of a visiting scientist’s comments. We should assume that there is substance. The rest of us posters can give style points. Gerd’s comments deserve high scores for sarcasm and intent to put down with the purpose of provoking a reply.
#274. Gerd, I really do need to work on the multivariate issues and I have gotten overtaken by other events. On the white noise query #21 though, I replied and I’m not sure what else I can say.
On #256. My interpretation of the term “completion of traditional review” is that there is a presumption of a first stage review with issues raised by referees, a revise-and-resubmit, and a checking by the referees that the revision met the issues raised in the first review. The completion refereeing would not be raising brand new issues that they had not thought about in the first stage. Usually the completion referees would be the same. If there were a substitute, then they would still have to pay attention to the initial reviews and the terms of the revise-and-resubmit. In this, as you agree, Goosse failed to ensure that Juckes answered the issues and from then on, it was impossible to adhere to CP policies. The referees were all changed and the process changed from open review under CP and EGU policies to closed review – in which the editor in chief said that no consideration was paid to the Interactive Public Discussion in total breach of EGU policies.
Doing original work is different than auditing and takes longer. The multivariate work is worth doing and I should do it. But not doing it yet does not generalize to a “pattern of unresponsiveness”, which is a very unfair statement.
Having said that, I’d like to persuade you of the merit of what I have in mind on the multivariate issue but the ball’s in my court and I don’t mind the prodding.
Ken,
You misunderstand me. I will most certainly leave the substance to the scientists.
Gerd’s post didn’t go to science, but to diligence. Gerd also reflected on Steve’s motives, due to his alleged tardiness in dealing with certain matters. I thought that to be unfair. I commented on that and I don’t think it’s out of line.
Re: #279
Brad, I have no problem with your comment – I simple needed it as an excuse to point to Gerd’s not very well disguised attempt to provoke an answer from Steve M. As a casual observation, I would say that Gerd uses those techniques more than most of the scientists passing through here.
The final Juckes et al is available here:
http://www.clim-past.net/3/591/2007/cp-3-591-2007.html
Here’s my first observation: the discussion paper had nine authors, the final paper only eight! E. Zorita is not anymore listed as an author!
Jean S., you say:
This is excellent news. I advised Dr. Zorita to get off the sinking ship … I guess he did, which is excellent news, he’s one of the good guys.
Now, off to look at the paper.
w.
Eduardo Zorita perhaps found that he wanted to do science, rather than ‘climate science’. Clearly not his best career choice, but integrity is a man’s choice. These days the world has a shortage of gentlemen and scholars, I’m glad to see that Eduardo has chosen to add his name to that short list.
Cliff
Page 11.
They put an additional spurious Proxy in each group so they would be able to say the studies were able to withstand removal of the Bristlecone Proxies. CHEATS. Drat, I forgot to put that bit in my note, did anyone else?
Still no cross correlation of individual Proxies. More CHEATING.
That would be a logical first check for robustness, wouldn’t it?
Or: How well does one proxy predict another?
RE 225
The most obvious error in the original A2 has been corrected, but CVM is still there. Seems that this science progresses slowly, hopefully soon they will learn how to compute uncertainties.
#286: Really slowly.
Seems to me that there is nothing but cosmetic changes. The meaningless upper bounded “standard error” estimate is still there along with the most ridiculous “significance” estimation probably ever published. How hard is it for these guys to understand a simple thing that if your proxies correlate positively with the target series, so should your “random sequences” otherwise their statistics simply do not match and you are comparing apples to oranges? I can only wonder what went through the heads of these additional reviewers as for instance the above mentioned things were explicitly spelled out in e.g. Willis’ review.
But hey, climate science really progresses: now we know that it is not needed to have even 18 proxies to reconstruct the northern hemisphere temperature, just 13 is enough! So all you working with the instrumental US48 data, you can stop now: since the contiguous U.S. represents only about 4% of the NH area, one instrumental series should definitely be plenty. Pick your favorite.
#277, just for the record:
Yes, and until then claims that multivariate calibration/inverse regression, with or without rescaling, equals PLS are unfounded.
You replied that ‘white noise is uncorrelated’, and used the R-function ‘rnorm’. So you really don’t know about multivariate normals with a given covariance structure, generated, e.g., by the mvrnorm function? Come on Steve, this I just can’t believe, as a more basic statistical concept is hard to find.
No, I agreed to ‘Juckes didn’t answer’, not to ‘Goose failed to ensure that Juckes answered’. Again, the main problem for the Editor was (I guess) that besides the wealth of ‘short comments’ only one reviewer responded in the first round, so he approached 3 additional reviewers for a second round. To close this round was probably not the best idea, but it was still consistent with CP policies. Open review would have revealed all the differences between editor and reviewers, and Juckes reaction/non-reaction to them.
Sorry, maybe that was a bit too harsh. But would you agree that your enterprise here is slightly more complex than simple ‘puzzle solving’, as you like to characterize it?
#287:
Jean, did you read their reviews?
#288: Gerd, no, I did not. As far as I know they are not publicly available. That’s why I said “I can only wonder” based on the fact that e.g. those issues listed in #287 are still there. If you are willing to share those reviews, my e-mail is: jean_sbls@yahoo.com
Or just pick one long instrumental series, scale it using CVM (any calibration period you prefer) and you’ll get pretty accurate global temperature series. That’s how this ‘science’ works.
For those who demand some mathematical rigor, Technometrics August 1989 issue has two very interesting papers,
1. Multivariate Calibration With More Variables than Observations ( Sundberg and Brown)
2. Small-Disturbance Asymptotic Theory for Linear-Calibration Estimators (Srivastava and Singh)
In 1. it is noted that
in reconstruction terms, n is calibration years, p is # of unknowns per year and q is number of proxies per year. Quite easy to see that in MBH98, from AD1700 step onwards the residual covariance matrix (
) is singular. But Mann doesn’t really want to estimate uncertainties, so he doesn’t need such a matrix.
Wrt Juckes et al CP paper, article 2. might be more interesting. In the new Appendix A2 it is said that
Srivastava and Singh are also after a compromise between the two known calibration methods
It seems to me that CVM is a member of that family, and thus this paper should be on ‘must read’ list. Some caution is needed, as the discussed Small-Disturbance Asymptotic theory assumes that random errors in the calibration are not large. In proxy vs. temperature calibration it seems that all we have is random errors..
Gerd
If Steve says he uses rnorm, it answers your question completely, samples from multivariate normal distribution; entries of covariance matrix outside the main diagonal all zero. He didn’t use mvrnorm.
BTW, in the mainstream multivariate calibration papers, generally noise is allowed to be correlated spatially but not in time (*). In these climate proxy reconstruction papers it is admitted that proxy noise is red (in time). Maybe even as red as temperature signal itself. As with the model proxy = temperature times zero plus noise .
(*) see e.g. Confidence and Conflict in Multivariate Calibration, Philip J. Brown; Rolf Sundberg, J . R. Statist. Soc. B (1987) 49, No. 1, pp. 46-57
Gerd. Do you have a qualified Statistician at your University? Why not get his/her opinion?
If you look at the individual charts of all the Proxies used you will see that they do not correlate with each other. There is no way any proper statistical process can fix that.
Using novel and untested methods which are not approved by qualified Statisticians, certainly doesn’t.
Please talk to a qualified Statistician.
Just a further thought. Here is a quote from Dougherty’s first year econometrics test, 3rd edition: “The main point of Granger and Newbold’s experiment was to show that it was easy to obtain apparently significant results, even if the model were nonsense, if evidence of autocorrelation were ignored.”
The powerpoint presentations associated with the book can be found here
http://www.oup.com/uk/orc/bin/9780199280964/01student/ppts/ch13/
The one on spurious regression gives a clear straightforward explanation.