In a recent paper by
Hoorn et al. (2012) reference is made to Grimm & Denk
(2012) as follows (p. 28): “Though being useful to unfold erroneous entries
regarding climatic ranges of extant plant taxa cited in the Palaeoflora
data base (Utescher and Mosbrugger,
2012), the study is not qualified to assess reliability and potential of the
CoA for the reason of various methodological flaws. These include the partly
very low number of taxa contributing with climate data in the analysis
(according to the method, a maximum number should be used), the use of
unspecific climate data (e.g. climate data for plant families when the more
specific data for a lower taxonomic level were not contained in the data base)
to reconstruct very specific climate conditions (e.g. the climate of the Alpine
zone in Georgia), and extensions of the climatic ranges derived from extreme stands
in high altitudinal areas thus introducing an additional bias (insufficiently
known lapse rates, microclimate, snow depth in the cold season, etc.). The Palaeoflora database is checked and updated in regular
intervals (Utescher and Mosbrugger,
2012) and new tests of the CoA on additional modern floras from various
continental areas that follow the published standard of the procedure (Mosbrugger and Utescher, 1997)
are on the way in order to provide further evidence for the reliability of the
method.”
A harsh critique.
However, this was it. No documentation or reference detailing where one can
find the listed “methodological flaws” in our paper and how they manipulated
our results, and how fossil plants assemblages would not suffer even more from
these draw-backs (if you are interested in more details, see our Responses
to Reviewer 2
of our paper). A quick check of the electronic Supplement
1, ‘sheet 1’ of Hoorn et al. (2012) revealed that
the best-resolved MAT interval is linked to the (still) erroneously recorded Engelhardia. So much for “being useful to unfold erroneous entries regarding
climatic ranges of extant plant taxa” Analyses without Engelhardia,
indicated as ‘ohne Engel’ in Hoorn et
al.’s Supplement 1, sheet 1, lead to badly resolved intervals (not mentioned or
discussed in the main text). Furthermore, Hoorn et al. explicitly note the
montane, continental setting of the analysed fossil plant assemblage. Wouldn’t
that be an “extreme stand in high altitudinal areas introducing an
additional bias”?
After
looking into the details of the study, I decided to contact the authors to
outline 1) how their paper and results actually support the conclusions in
Grimm & Denk (2012) and 2) to inquire about the
logic of using the “coexistence approach” (CA) to reconstruct the
palaeoclimatic conditions of a vegetation that perfectly falls within the range
(and setting) of the most mis-reconstructed modern
validation floras in our study.
The
mail below was addressed to Dr Hoorn and all main editors of of Palaeogeography,
Palaeoclimatology, Palaeoecology
(P^3) since I was unable to figure out, which editor was responsible for the
publication of Hoorn et al. (2012) and oversees CA papers published in this
journal (I still wonder).
From: Guido
Grimm [Guido.Grimm@nrm.se]
Sent: Friday, October 19, 2012 2:58 PM
To: Hoorn, Carina; dbottjer@usc.edu; t.correge@epoc.u-bordeaux1.fr; peter.kershaw@monash.edu; finns@geo.ku.dk
Cc: Thomas Denk
Subject: Comment to Hoorn et al. (2012) A late Eocene palynological record of climate change and Tibetan Plateau
uplift - Relevance of CA results and critique of Grimm & Denk (2012) included in this study
Dear Carina Hoorn and co-authors, dear editors of Palaeogeography, Palaeoclimatology,
Palaeoecology
In a recent paper by Hoorn et al. (2012) reference is
made to our study (Grimm & Denk, 2012) as follows
(p. 28): “Though being useful to unfold erroneous entries regarding climatic
ranges of extant plant taxa cited in the Palaeoflora
data base (Utescher and Mosbrugger,
2012), the study is not qualified to assess reliability and potential of the
CoA for the reason of various methodological flaws. These include the partly
very low number of taxa contributing with climate data in the analysis
(according to the method, a maximum number should be used), the use of
unspecific climate data (e.g. climate data for plant families when the more
specific data for a lower taxonomic level were not contained in the data base)
to reconstruct very specific climate conditions (e.g. the climate of the Alpine
zone in Georgia), and extensions of the climatic ranges derived from extreme
stands in high altitudinal areas thus introducing an additional bias
(insufficiently known lapse rates, microclimate, snow depth in the cold season,
etc.).”
This reads pretty much like a summary of the report of
the second anonymous reviewer of our paper [PDF]. This
reviewer did a very passionate and thorough report, however, most of her/his
objections are not relevant to our study, but reflect what she/he believed
we did show. During the review process, we rebutted all of her/his
critiques, including all points raised here again. (In
case you are interested in the whole discussion, our response to the reviewer’s
report is attached.) The other anonymous reviewer concluded that our study “unfortunately”
showed exactly what we said.
Hoorn et al. (2012) then finish this paragraph: “The
Palaeoflora database is checked and updated in
regular intervals (Utescher and Mosbrugger,
2012) and new tests of the CoA on additional modern floras from various
continental areas that follow the published standard of the procedure (Mosbrugger and Utescher, 1997)
are on the way in order to provide further evidence for the reliability of the
method.”
I checked the webpage referenced here, there is no
documentation whatsoever about changes to the data base, and how these changes
would have affected published climate reconstructions. In fact, the homepage
explicitly informs the reader (“About palaeoflora”)
that only selected data is available, hence, testable, online. I also find it
odd that editors and reviewers are fine with “tests on the way” that
will validate in the future a method they willingly accepted during the last 15
years (for most part untested; see Grimm & Denk,
2012). Wouldn’t it be a must to first show with new “tests” that CA does
actually work for floras such as the one used in your study and then
using the CA to draw conclusions?
Let’s come to the details of your CA part, which
nicely demonstrate the logical flaws inherent to many CA applications, as it is
also the case in this study. Which, funnily, fully support the conclusions of
our study (Grimm & Denk, 2012) unlike stated.
[1]“Though being useful to unfold erroneous entries
regarding climatic ranges of extant plant taxa cited in the Palaeoflora
data base… The Palaeoflora database is checked and
updated in regular intervals (Utescher and Mosbrugger, 2012)” — It has never been documented that this is the case, in contrast,
important (because climate-limiting) erroneous entries are kept! In a special
NECLIME issue, Kvaček (2007) stated based
on fossil plant associations and the fact that fossil counterparts of modern
NLR commonly had a wider ecological range that the MAT tolerances for several
NLR taxa, including the commonly used genus Engelhardia,
are too narrow in the Palaeoflora database. This
agrees with modern-day data (Engelhardia MATmin 10-11°C; Grimm & Denk, 2012, based on Atlas of Woody Plants in China,
corrected by altitudinal information in eFlora
of China). However, nothing has changed in the Palaeoflora
database: Engelhardia is still the only limiting taxon
for a min. MAT of 15.6 °C in your study. You write (p. 32) “Warm
temperate conditions with MAT>~15 °C result for the depth levels were Engelhardtia [the correct spelling is “Engelhardia”] is present in the spectra,
with the upper limits of CoA ranges being around 24 °C, especially in the lower
part of the profile, and ranging to ca. 22 °C when Picea
is present.”
Aside from its wrongly
recorded, but still used MATmin tolerance
and hence an unreliable reconstructed MAT interval, Engelhardia
is clearly a relict today (as already pointed out by Kvaček,
2007), and should, according to Mosbrugger & Utescher (1997), be excluded from analyses per se. Although
not mentioned in the text, you did such a test (Supplement
1, sheet 1): when Engelhardia is
excluded the reconstructed lower MAT interval boundaries drop 2.3 to 12.5°C according
to the data provided in your own Supplement 1, Sheet 1. The resulting
intervals are poorly resolved (∆MAT ranges from 6.8 to 20.8 °C); clearly
supporting our conclusion that the elimination of relict genera and correction
of wrong entries results in much less resolved intervals (Grimm & Denk, 2012).
Based on what is documented in Hoorn et al. (2012),
one cannot see whether changes were made to the database to correct erroneous
entries or whether newly added data for NLR are meaningful at all to draw conclusions
about “modest climatic cooling and drying trend” based on CA- results.
Your data (Supplement 1) and graph (Fig. 4) show nothing alike: the reliable
MAT intervals (“reliable samples only”, labelled as “ohne
Engel”, i.e. without Engelhardia, in Supplement
1, see above) change from 9/10 °C to 22 °C at 190/180 cm to 10/12 °C to 22–25
°C at 24 to 30 cm. Regarding the MAP, exactly the same interval (399 to
705 mm) is reconstructed for the lowermost and uppermost parts of the sediment
sample.
I can only advise the reviewers and editors of PPP to
at least require that climate tolerances of taxa used as NLRs are documented
together with a CA-based reconstruction following the example of other
publications in your journal (Xia et al., 2009; Jacques et al., 2010). Critical
minds like me then may take the results serious, and the public audience can
see whether the claim that the “…Palaeoflora
database is checked and updated in regular intervals…” is true. Data
curating takes time and gives little benefit, however, one may wonder why e.g.
the compendia of Thompson et al. (1999a, 1999b, 1999c, and 2001) never were
used to update the erroneous entries at least for North American species listed
as NLRs in the Palaeoflora database. It would also
help to understand whether “reconstructed” trends are just based on erroneously
recorded tolerances or real changes in the climatic preferences of the fossil
plant assemblages.
[2] “These include the partly very low number of taxa
contributing with climate data in the analysis (according to the method, a
maximum number should be used)” — In Supplement 1 you list between 4 and 30 available NLR, 2–24 if
only “forest taxa” are counted. Your cut-off point for non-poor samples
is 8 NLRs (p. 30, fig. 4): “Data points without range bars refer to poor
samples (N-taxa contributing with climate data <8)” On the other hand,
you separated “forest group” and “local group” taxa, and
Supplement 1, sheet 1 includes two assemblages with 4 and 6 NLRs among “reliable
samples only”. For the main conclusions in Grimm & Denk
(2012) only floras were used with at least 15 NLRs available in Palaeoflora data base. Such a threshold, in your case,
would reconstruct intervals between 15.6 °C to 18.4 °C and 8.7 °C to 24 °C for all the assemblages included in your
study; intervals then only differ by their width (become less informative) but
are inconclusive regarding cooling/warming events. As explicitly said in Mosbrugger & Utescher (1997)
the CA assumes only that the real value is comprised in the reconstructed
interval. For your case this means that the wider interval may indicate cooling
or warming. If you would have read our study and the studies referenced therein,
you at least could have argued that taxon-lists of temperate and boreal forests
typically result in broader intervals than those of subtropical forests.
We found (and documented) that CA/Palaeoflora fails to resolve correct mean annual
temperature (MAT) for numerous modern forests, the most disturbing example
being the Shennongjia transect (fig. 5 in our paper),
despite more than 60–120 genus-level taxa used as NLR in reconstructions of
fossil floras! We also demonstrated that CA/Palaeoflora
will always conclude on the same reconstructed MAT interval (typically around
16°C) when a high number of NLRs is used, even if randomly selected (refer to
the ES4 to Grimm & Denk, 2012, using exactly
the same data than used by Mosbrugger & Utescher, 1997, to validate the method). Your
best-resolved intervals 15.6 °C to 18.4 °C (13–19 NLR) fall
exactly in this range. Please note that your limiting taxa are the problematic Engelhardia (conservative MATmin
10–11 °C; not c. 15 °C, Supplement 1, sheet 1) and probably Cedrus (11.6–18.4 °C in Palaeoflora,
Oct. 2010), which you cite as a typical element of high-mountain conifer
forests (p. 33). In other words, the inclusion of a wrongly recorded taxon
(Engelhardia) and another that is considered allochthonous (Cedrus;
p. 33ff) reconstruct a warm-temperate (according to Köppen-Geiger)/
subtropical climate. If our results are not relevant to assess the reliability
and resolution of CA, how can 8 (or less) NLRs that represent a mixture of
high-mountain (p. 33ff) and low-land (?) “warm-temperate broad leaved
deciduous” forests be relevant for the climatic conditions under
which your fossil assemblages thrived?
[3] “the use of unspecific climate data (e.g. climate
data for plant families when the more specific data for a lower taxonomic level
were not contained in the data base) to reconstruct very specific climate
conditions (e.g. the climate of the Alpine zone in Georgia),” — One might think that a steppe-like environment in
penultimate vicinity of a temperate mesophytic forest would qualify for a very
specific climate condition. Your study further nicely illustrates that palynological data is taxonomically highly unspecific: of
the 8 NLRs listed for the “Steppe biome” 3 are family-level; and 7 out
of 19 listed for the “temperate broad-leaved” forest. If all NLRs are
pooled, one out of four NLRs used is family-level. Regarding this aspect of palaeo-palynological studies using CA, our re-validation
was much too precise: to test the CA potential for palynofloras
we would have needed to replace most of our species- and genus-level taxa with
accordingly indecisive family-level tolerances. Instead we got inconclusive
CA/corrected results for North American beech forests based on species-level
NLRs and hazardous wrong results for Chinese forest with more than 100
genus-level taxa listed in the Palaeoflora
database as potential NLRs. Our data and lists are freely accessible; you may
at any time check the CA potential for modern floras using taxa that can be
unambiguously identified in the pollen record.
[4] “…and extensions of the climatic ranges derived from
extreme stands in high altitudinal areas thus introducing an additional bias
(insufficiently known lapse rates, microclimate, snow depth in the cold season,
etc.).” —Already in your
abstract you write: “The increase of taxa such as Piceaepollenites
and Abiespollenites indicates not only a cooling and
drying trend prior to the Eocene/Oligocene (E/O) boundary, but also the
existence of high altitude mountain habitats in the periphery of the Xining
Basin” On p. 7 you state “In the northern Tibetan Plateau, evidence
for high elevation is provided by the occurrence of pollen taxa related to high
altitude vegetation in the Xining Basin by ca. 38 Ma (Dupont-Nivet et al.,
2008; now dated at 36.1 Ma (C16n.2n), see Abels et al., 2011).” In the
discussion (p. 33f) you make a strong point arguing that your samples come from
sediments indicating nearby mountains higher than 1500 m a.s.l.
Let’s for the sake of your argument believe that we only got bad results
because we tested mountain forests thriving outside the natural climatic
envelopes of their constituting taxa as assumed here (quotation [4]). How can
you conclude that your results are not equally biased as ours, since your
pollen sample comes from a mountainous area that must have been equally
strongly affected by local climate phenomena such as “(insufficiently known
lapse rates, microclimate, snow depth in the cold season, etc.).”? Just to
note: for all our sample floras the application of the moist-adiabatic lapse
rate was tested using global climate data and station data from the area (see
e.g. ES 7 and 8 to Grimm & Denk, 2012) and
microclimate and snow depth/coverage also affect the latitudinal distribution
of species and genera. However, these effects are not more problematic than
defining a species’/genus’ tolerance at first hand using available distribution
data. This you would have known, in case somebody would have actually read our
paper and looked at the freely accessible Electronic supplement. As you discuss
in your text, the composition of your forest is not different to extant montane
forests in China, including such that were actually considered in Grimm & Denk (2012), and provided wrongly reconstructed
MAT intervals. I will again refer to the strongly wrong intervals we obtained
for high and mid-altitude forests in the Shennongjia
Forest District in Central China, which thrive under subtropical to boreal
climates and host very diverse woody plant assemblages, many ‘Tertiary relict’
taxa, and provides more than 100 potential NLRs at altitudes between 500 and
1500 m a.s.l. Do you really think these are more “extreme”
stands than the setting around your fossil assemblage?
Let me conclude this little comment: I honestly hope
you’ll keep on citing my paper, even to discredit it, but you should at least
try to provide some slight evidence for your claims. When I read the episode in
Material & Methods, I felt myself reminded of a famous quote from Goebbels:
a lie becomes truth if you only repeat it often enough. I cannot help
the impression that this is exactly the basis on which CA/Palaeoflora
works. The CA group had obviously access to our validation data and study since
May 2011, when our review process started. One could expect that they might
have found the time to de-validate our results and criticism, in case that
would have been feasible. To date, this has not been done. Instead, one is
again confronted with tests that will be done in the future to substantiate
conclusions already published and claims lacking documentation. And the reader
is expected to believe blindly. Do you consider this scientific?
I understand that CA reconstructions and conclusions
were not critically examined as long as there was no independent study
re-investigating the data and method. I wonder, whether there will ever be an
objective/constructive review of papers using this method and a discussion
about its reliability based on facts and not beliefs. Independent of the
question whether CA is informative or not, it is certainly not acceptable to
continue publishing results without documenting the data behind them. It is
hard to understand why e.g., Xia et al. (2009) and Jacques et al. (2010)
documented the data they used, but most others merely refer to a link to a
database that for the most part is not publicly available. After struggling
half a year digging into CA-publications to extract relevant information (see
Grimm & Denk, 2012, ES 2), I have come to the
conclusion that the reason for this secrecy is to avoid that the public can
immediately figure on which thin grounds CA reconstructions and conclusions are
based, as unfortunately also in the case of the Hoorn et al. paper.
Sincerely, Guido Grimm
Stockholm, October 19th
Two attachments:
PDF: Response to the points raised by reviewer #2 of
Grimm & Denk (2012), which correspond to those
raised in Hoorn et al. (2012, p.28)
XLS: Supplement 1 of Hoorn et al. (2012) illustrating the
basis for CA conclusions draw in the study. In blue, annotations added by me.
PS Please note that I will publish this letter and any
response from your side to it on my homepage at a later point, with reference
to our paper (Grimm & Denk, 2012). Conversely,
you are naturally free to distribute this email and attached documents. If
you’re not involved in this matter or not want to get involved, consider this
email as not sent.
Quite shortly after, Dr Hoorn replied to my mail (see below), however,
was not able to or did not want to clarify any inconsistencies in the CA
application, results and conclusion in her study (which make up about 1/3 of
it). Instead she delegated the entire responsibility for this part to Torsten Utescher, who is listed as the 5th of six
co-authors, and considers her erroneous results and conclusions and logical
inconsistencies (see my critique above) part of a “larger issue”. But the point above in my critique of her paper was:
A) If Grimm & Denk (2012) is not “fundamentally flawed” but showed the bare truth of CA, then the CA
results in Hoorn et al. (2012) are biased.
B) If Grimm & Denk (2012) is “fundamentally
flawed” because we selected mostly stands where plants grow outside their
“usual” climatic envelopes (however this can be accommodated by CA who uses
only min and max tolerances requires some arcane knowledge) and too few
limiting taxa as stated in Hoorn et al. (2012), then this all applies also to
floral assemblages in Hoorn et al. (2012) and their CA results are equally
flawed.
So either way, the climate interval reconstructions presented in Hoorn
et al. (2012) are highly problematic, if not entirely wrong.
From: Hoorn, Carina [mailto:M.C.Hoorn@uva.nl]
Sent: den 19 oktober 2012 16:22
To: Guido Grimm
Cc: Thomas Denk; dbottjer@usc.edu; t.correge@epoc.u-bordeaux1.fr; peter.kershaw@monash.edu; finns@geo.ku.dk; Guillaume
Dupont-Nivet; Hemmo Abels; t.utescher@uni-bonn.de
Subject: RE: Comment to Hoorn et al. (2012) A late Eocene palynological record of climate change and Tibetan Plateau
uplift - Relevance of CA results and critique of Grimm & Denk (2012) included in this study
Dear
Sir,
The
reference to your paper in our CA section was made on recommendation of one of
our reviewers. I was not aware that the text resembled another text and I
apologize if perhaps it is too crude a statement. The CA section was produced by my co-author Torsten Utescher. I expect he may want to debate this matter
further with you.
In my view this debate seems to comprise a larger
issue that extends beyond our paper and for this reason perhaps you can
both decide on a suitable forum to display this discussion?
Sincerely
yours,
Dr. Carina Hoorn
I decided to wait a month to see if somebody else
of the addressees of my and Dr Hoorn’s mail will eventually come up with
something more substantial. After all, Grimm & Denk
(2012) was publicly discredited in Hoorn et al. (2012) and I feel a first
author should not allow statements in her/his paper if she/he is not able to
substantiate or at least judge them. Furthermore, my critique dealt with the
actual results and conclusions put forward in her paper, how can this “extend beyond the paper”?
Any “larger
issue” has already been dealt with in our paper; Dr Hoorn and her
co-authors would have known that, if they’d actually read the paper Grimm &
Denk (2012), which Dr Utescher
apparently regards as fundamentally flawed.
But then the first month went, the second, and the
year was over.
So I wrote finally a second mail, about four months
later.
From: Guido Grimm
Sent: den 15 february 2013 17:40
To: Hoorn, Carina [mailto:M.C.Hoorn@uva.nl]
Cc: Thomas Denk; dbottjer@usc.edu; t.correge@epoc.u-bordeaux1.fr; peter.kershaw@monash.edu; finns@geo.ku.dk; Guillaume Dupont-Nivet; Hemmo Abels; t.utescher@uni-bonn.de
Subject: RE: Comment to Hoorn et al. (2012) A late Eocene palynological record of climate change and Tibetan Plateau
uplift - Relevance of CA results and critique of Grimm & Denk (2012) included in this study
Dear Dr
Hoorn, dear editor(s) of P^3 and other addresses of the mail of C. Hoorn from
19th Oct, 2012
Please
apologize for the late reaction to your response. I was hoping for some
reaction to your response and my (detailed) critique on the logical and
technical flaws in the CA result that you presented in your paper. I have to
admit that I was a bit surprised that a first author of a paper can so easily
delegate responsibility regarding results and conclusions that may not be the
most important ones of the study, but nevertheless make up a large portion of
the abstract and conclusions; and are considered as sufficiently important to
be reported at all.
From your
response (and the lack of responses from anybody else) I understand that
neither you nor any other of your co-authors is either capable or willing to
clarify the problems in your analysis and in the data you relied on, blindly as
you state in your response. The points I raised are addressing inconsistencies
in your analysis, results and conclusions; there is no wider
scope than that. The most important flaw in your analysis is that the climatic
trend you report is entirely based on a wrongly-recorded MAT range of one
NLR, a known relict genus, and another NLR, which you discuss as a high-montane
allochthonous element. If you cannot explain the
logic behind this, you may want to consider publishing an Erratum where you
dissociate yourself from the CA results in your study and clarify that the
maybe too “crude” comment on our work is just expressing the beliefs of one of
your co-authors, T. Utescher.
It is also
obvious that neither you nor any other of your co-authors had really read our
paper, when you decided on its content, including whoever is responsible for
the uncritical dissemination of CA results in the editorial board or among the
reviewers of P^3. The broader scope, first-order error biasing all CA results
and general limitations of CA if these errors are corrected, is already
addressed in our paper, and the general debate on CA could have been started.
Just one number: The only validation of CA so far, in the original paper, which
concluded CA works used 4 modern floras, provided no documentation on the
tolerance of potential NLRs, nor which were actually recorded for each flora.
We used over 200 modern floral assemblages and showed that CA/Palaeoflora,
converges always to something between 13–17 °C, independent of the actual
climate and the composition of the plant assemblage. All data used is
documented (and freely available), so if there is a fundamental flaw, Dr Utescher could have already made a reply since he
apparently had access to our paper since April 2011. On the other hand, most of
the data in Dr Utescher’s database are not publicly
available, i.e. essentially refers to unpublished data (this includes Hoorn et
al., 2012), so there is little more to discuss at this point. The little
that is documented demonstrates that you still relied on known wrong entries (Engelhardia) to infer “slight” climate shifts, which
is in contrast to Hoorn et al. (2012), M&M, stating the usefulness of Grimm
& Denk (2012) to identify and eliminate errors in
the database.
Allow me a
related final comment addressed to you as the responsible author of your study
and editors and reviewers affiliated with P^3: The lack of documentation in
studies applying CA+Palaeoflora like yours is
alarming. There are only a few notable exceptions, published in P^3, not
co-authored by Dr Utescher or other veteran authors
affiliated with NECLIME, that used (for most part) NLR tolerances derived from
other sources than Palaeflora (referenced in Grimm
& Denk, 2012). Only quite recently a paper was
published in P^3, Quan, Liu & Utescher
(2012), which is the first (!) study that that actually documents
the primary climate tolerances used for the reconstruction based on the Climbot/Palaeoflora database, and
the second where some reviewer (which was not me or my co-author) may have
forced the authors to reference our paper like in your case. [NB: In this
second paper, Dr Utescher restrained himself from
repeating his “to crude a statement”
as you put it. In this paper the authors simply repeat the statement also found
in your M&M part that our study was useful to correct error in the
database. Haven’t checked that, though, but if I find some time to waste, I’ll
think about it.]
I may be an
old-fashioned idealist, but I would think first or corresponding authors
should ensure that all critical data used is also documented or at least
available. There is no shame having used wrong data, as long as it can be
understood how it affected the analyses and conclusions. Are you able to provide
me the tolerance data and NLRs lists for each assemblage you used to
reconstruct the palaeoclimate intervals produced in
your study, so that I would be able to test your results for primary
data-errors and other biases? Dr Utescher already
informed me some years ago that he only shares data from the Climbot/Palaeoflora database in
the course of “joint-research”. Which I find a bit unethical,
since these data have been already used for many publications. I wonder
how the situation is for an author like you, who joined research with Dr Utescher.
But, of
course, the greater responsibility lies with the reviewers and editors who
obviously don’t bother for a necessary minimum of documentation in the case of
CA (see the according supplement to Grimm & Denk,
2012). A method that is massively affected by the climate tolerances of
individual NLRs and the sample of NLRs used (see your Appendix 1,
sheet 1, reconstructed MAT interval with and without Engelhardia,
labelled “ohne Engel”, the significant difference
between these two “analyses” not even mentioned in the main text), should
document these tolerances above anything! Otherwise, any result is absolutely
meaningless.
With kindest
regards, G. Grimm
PS I will
upload this correspondence to my homepage (www.palaeogrimm.org)
as I said in my first email (maybe next week, if I find the time) linked to the
according reference on my publication page. You or anyone else is welcomed to
write replies (crude or not), which I will equally link to our paper. Maybe an
open debate will eventually start.
So far I got no reply, if I get one, I will post it here.