To: <Sandy.Tudhope@ed.ac.uk>, "Tim Osborn" <firstname.lastname@example.org>
Subject: Re: Fw: 2005JC003188R Decision Letter
Date: Tue, 21 Feb 2006 15:37:10 -0000
Cc: <K.email@example.com>, "Brohan, Philip" <firstname.lastname@example.org>, <email@example.com>
am working my way through the comments
Have also re-read Mike Evans 2002 paper.
I am frustrated with the associate editors comments. He seems to be overtly defending
Mike's reconstruction which are quite different in nature - i.e. he reconstructed 2 spatial
fields - the 1st being ENSO related and the 2nd being probably related to the PDO although
it is not clear form the text.
The coral data-sets are also quite different, with only ~ 4 series being common to both
studies. In fact, many of the coral series used by Mike did not pass my screening process.
Lastly, the only statistic use by Mike for validation is the correlation coefficient. I
like to think I have been a little more robust at least in this regard.
I need to diplomatically word all this. I never wanted to criticise Mike's work in anyway
way. It was for that reason that I made little mention to it initially.
anyway, I hope to get a more cleaner version done by early next week.
will keep you all posted
PS. do you have the FORTRAN code for Ed Cook's SSA software?
----- Original Message -----
From: Tim Osborn
To: Rob Wilson ; Sandy.Tudhope@ed.ac.uk
Sent: Tuesday, February 21, 2006 3:00 PM
Subject: Re: Fw: 2005JC003188R Decision Letter
Hi Rob et al.,
seems like there are many points to address - some reasonable, some
Some easy things to do... change "all time scales" to "annual to
centennial time scales", minor inconsistencies pointed out.
Near the end the comments get a bit picky/stupid. e.g. "according to
CE reconstruction is less skillful than climatology". Doesn't RE
assume "climatology" (== calibration period mean) while CE compares
the skill against the assumption that the mean over the verification
period is known (which of course it isn't known for a general period
outside the instrumental period)? And I really don't think your
average reader will be confused into thinking that you calibrated
using observations before 1840! Though wording could be changed to
"the explained variance of the reconstruction using records available
before 1840 us quite low" or something similar that fits the flow of
the sentence. Also, earlier on, isn't it obvious from the editor's
own description of the method that you can indeed estimate
verification errors for all "nests", including those available during
the instrumental period, and thus it is obvious why verification
statistics can cover this entire period in Figure 2C,D. The editor
just needs to think about things a bit more!
The description of the calibration method can be written in the way
that is requested, I'm sure. The difficulty is actually in
countering the criticisms that (1) the reconstruction error obtained
by regression may no longer be appropriate after the "inflation"
step, (2) the use of calibration period residuals rather than
verification period residuals to provide the error bars (though here
the editor contradicts this suggestion by pointing out that the
verification errors apply to no period other than the verification
period, but if you assume the same for the calibration errors then
where can you get the errors from?).
Hope these quick comments help,
At 11:41 18/02/2006, Rob Wilson wrote:
>have just been away for a week to return to this reply from JGR.
>Have only gone through it quickly, but we obviously have a fussy
>associate editor to please.
>Should have gone for 'atmospheres' rather than 'oceans'.
>will go through it properly on Monday.
>Hope you are around over the next few days or so.
>PS. have used this e-mail address as the Uni server seems to be down
>----- Original Message -----
>Sent: Thursday, February 16, 2006 8:06 PM
>Subject: 2005JC003188R Decision Letter
>Dear Dr. Wilson:
>Thank you for submitting your manuscript "250-years of reconstructed
>and modeled tropical temperatures" [Paper #2005JC003188R].
>I am in agreement with the associate editor and the reviewers that
>your revisions fail to adequately address the original concerns
>about the reconstruction methodologies. If you want to convey that
>this is somehow far superior to earlier reconstructions of SST, then
>it is only fair that readers of JGR get a very very clear
>description of the methods used and a convincing argument as to why
>the reconstruction is better than prior published reports on such
>reconstructions. Please heed the detailed comments and carefully
>address each of the comments with appropriate revisions and clear
>responses. I will be obliged to reject the manuscript if you do not
>address these concerns since the main claim of an improved
>reconstruction of historic temperatures is not scientifically
>rigorous enough for publication in JGR-Oceans.
>Please submit your revised manuscript by March 28, 2006. If you do
>not plan to submit a revision, or if you cannot do so in the time
>allotted, I would be grateful if you could let me know as soon as
>Please review the Important Links to JGR Information attached below
>before uploading your revised manuscript.
>When you are ready to submit your revision, please use the link
>Editor, Journal of Geophysical Research - Oceans
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>The authors adequately addressed many of the reviewers'
>remarks and requests for revisions.
>However, there are significant outstanding issues detailed
>below. The paper needs a thorough revision to become
>1. The paper lacks a clear description of the reconstruction
>technique. From the text, figures, tables, and the authors'
>responses, one can guess that the following approach was
>used, in order to produce the main ("full period")
>reconstruction that the authors use for model comparison and
>interpretation: (1) for each year before 1870 the subset of
>coral records for which this year's value is available
>("nest") is identified; (2) standardized values of the
>"nest" records are averaged together for each year for which
>the entire nest is available; (3) a linear regression of the
>nest values is performed on the instrumental annual tropical
>SST averages for the period 1897-1981 (or its subperiod for
>which the nest values are available); (4) the obtained
>linear regression formula for that nest is tested on the
>period 1870-1896, and the verification statistics is
>derived; (5) the reconstruction of the target year is
>performed using the same linear regression for this nest,
>and the "verification" statistics is attributed to this
>Very small percentage of the readers will be able to
>understand this procedure from the paper in its current
>form. There are a few reasons for that: (a) the paper lacks
>an explicit coherent description of this procedure, (b) the
>additional "inflation" of the reconstruction (p.9, lines
>2-3) is performed, but neither the explicit formula for it
>is given, nor how this inflation affects the reconstruction
>error in verification is discussed, (c) it would seem
>natural to use the verification error for the error bars,
>but it appears that the authors are using the calibration
>error, although no adequate description is given, (d) the
>authors are taking a lot of liberty with using verification
>statistics - unlike error bar estimates these are not
>supposed to be attributed to the periods other than those
>for which they were computed, or at least it is highly
>unusual to do that, (e) what values are given as coral
>reconstructions for the instrumental period is not
>explained: calibration values for corresponding nests? (f)
>why "verification" statistics in Fig 2C,D cover the entire
>calibration period is unclear, (g) the presence of the
>specific calibration formula in the upper right corner of
>Fig 2 is very confusing in the context of this work, but the
>authors failed to take any action despite the hint from
>Reviewer 2 (remark 3.3).
>The authors have to provide an unambigous description of all
>aspects of their reconstruction procedure. But all
>additional information they provide about their
>reconstruction should help the reader to understand the main
>message, rather than to get confused or completely drowned
>under the confusing information flow. Therefore the
>"split-period" calibrations need to be reported only if they
>help to deliver the main message, which is not the case in
>the present version. Same with statistics: a lot of it is
>reported, but what purpose it serves is unclear. All
>statistics more complicated than correlation coefficient
>needs to be explicitly defined, to make the presentation
>unambigous. In their reply, the authors call Durbin-Watson
>statistic "standard". Well it's not for JGR-Oceans, where at
>least since 1994 it's never been used (in the entire body of
>all AGU journals it was only about 15 times). Same with sign
>test: the readers of JGR-Oceans should not be expected to
>have dendroclimatological textbooks by Cook and Kairiukstis
>or by Fritts in their posesion in order to look up and
>interpret the authors' results. Some of these statistics
>are only introduced in table captions, and in a puzzling
>way, e.g. Table 2A, lines 3-4: LIN r = correlation of linear
>trend in residual series. What is meant here is probably the
>correlationcoefficient of residual with the time variable,
>but in any case, LIN r is not a good notation.
>2. The authors resisted the gentle insistence of Reviewer 2
>(remark 5.1) on quantifying the role of trends in the
>model-reconstruction intercomparison. To put it more
>bluntly, the significant correlations reported on p.11 and
>Table 3 are only significant because of the long term
>trends. If the 50- or 100-year the trends were subtracted,
>no significant correlation of residuals would be
>left. Trends themselves have such a small numbers of degrees
>of freedom (6, if separate trends are computed for 50 yr
>periods), that reported correlations are not significant for
>them. Therefore the authors' claim in conclusions of "a
>strong mutual agreement between the reconstruction and two
>global coupled-climate models" (p.14, lines 21-22) is not
>properly supported by the presented results and most likely
>incorrect. The authors have to change somehow their line of
>argument about model-data consistency to make it correct and
>acceptable for publication.
>3. The authors claim to develop "first coral-based, large
>scale temperature reconstruction, exclusive to the tropics,
>that represents past SST variability at all time-scales."
>First, how can it possibly do this at "all" time-scales and
>what scales other reconstructions of similar length exclude?
>Second, why Evans et al 2002 reconstruction doesn't count?
>In general, the authors seem to operate with understanding
>that their reconstruction is superior to that by Evans et al
>2002 (e.g. their reply to remark 3.4 by Reviewer 2). The
>basis for that is unclear, since they use a simpler
>technique, a simlar coral data set, and they only try to
>reconstruct the tropical mean, rather than the entire
>field. The actual advantages of their product compared with
>earlier works need to be made clear in the paper.
>4. The revision seems to have been made in a great haste, so
>that the changes the authors made often result in
>inconsistencies with the surrounding text.
>Abstract, lines 14-16: this sentence is grammatically
>p.4, line 15: raw records are not data transforms
>p.4 lines 18-19 and p.5 lines 11-12 are in conflict. Logical
>way to present the material is to say that 16 records passed
>the screening, but then 2 of them were excluded for that and
>p.6, line 7: MTA is mentioned here, but it is only in the
>captions to Table 2 that it is explained that MTA is a
>combined mean of MAI and TAR. This is inappropriate use of
>caption, not to mention that (1) TAR is called MaiTar in the
>Table header, (2) the number of records is reduced to 13
>now, to confuse the reader further.
>p. 7, line 6: add "here" after "was used" to break the false
>attribution of this sentence to Evans et al 1998 work.
>p.8, line 5. ST abbreviation intoduced earlier is not used
>p.8 lines 9-11: "calculated" used twice.
>p.8 line 20 - p.9 line 5. Ambigous, confusing description of
>the crucial part of the procedure.
>p.9, lines 6-18. (1) attribution of the statistics to the
>entire nest record creates very bad effects here: "prior to
>1840, the explained calibration vatiance is quite low". For
>a reader who hasn't internalize the authors approach, the
>reference to calibration before 1840 will be shocking. (2)
>Strictly speaking, for the entire period before 1850 the
>reconstruction has less skill than climatology, according to
>CE in the Figure 2B. The authors have to deal with a
>complicated task of explaining that to the reader, while
>also arguing that since after 1750 the CE is a bit better
>that before 1750, they chose to use the reconstruction after
>1750 for comparison with the models. (The Reviewer 1 was
>concerned about this too in the first remark).
>p.9, line 19: ". . . appear improved" compared to what?
>p.15, lines 19-21. Again, it needs to be explained better
>what is the contribution of the present paper to evaluating
>the potential for reconstructing large scale tropical
>temperatures from a network of coral proxies, as compared to
>Evans et al papers, where this task seems to have been
>accomplished before from a few different angles.
>p.24, line 1: "Simple zero order OLS regression" is not
>simple: what does zero order mean in this context?
>p.24, line 5. "model residual" is confusing, because the
>only models called so in the paper are GCMs. But here
>"model" denotes a linear regression model.
>Page 41. Table S1. (1) it would be helpful to explain that
>left part of these tables are calibration statistics and
>right are verification statistics. (2) What is aR^2:
>"multiple" correlation coefficient? Is R different from r?
>(3) Why full-period verification statistics are missing for
>nests after 1879?
Dr Timothy J Osborn
Climatic Research Unit
School of Environmental Sciences, University of East Anglia
Norwich NR4 7TJ, UK
phone: +44 1603 592089
fax: +44 1603 507784