cc: Alan Robock <robock@snowfall.envsci.rutgers.edu>
date: Mon Nov 15 16:01:00 2004
from: Phil Jones <p.jones@uea.ac.uk>
subject: Re: Fwd: Decision on Nature manuscript 2004-09-24002B (fwd)
to: Konstantin Vinnikov <kostya@atmos.umd.edu>, Norman Grody <ngantique@hotmail.com>, Ronald Stouffer <Ronald.Stouffer@noaa.gov>, Mitch Goldberg <Mitch.Goldberg@noaa.gov>

    Kostya,
         After a quick read, it seems to me that it would take some work to address the points
    made by the 3 reviewers. Views are so entrenched in this subject, that, as you say, you
    will likely get the same reviewers if you went to GRL. My assessment of the reviewers
    is that 1 is Kevin Trenberth and 3 is Ben Santer. So, you've not done too badly. You don't
    seem to have anyone from UAH. Ron will need to comment as to whether Reviewer 2's
    comments can be dealt with adequately. This one seems to be a modeller.
        So, as we've got three reasonable reviews, it might be worth pursuing. I can't see if
   being
    any easier going somewhere else. Nature suggest resubmitting elsewhere. If you do go
    in to more detail then JGR might be best. Alan can tell us which editor to submit it to.
    Cheers
    Phil
   At 14:14 13/11/2004, Konstantin Vinnikov wrote:

     Dear Norman, Ron, Phil and Mitch,
             Here are the reviews of our manuscript from Nature. I think that
     we should be able to identify reviewers.  Nevertheless, we have to make a
     decision, how to react.  My natural reaction is that we have to fight for
     this paper.  I think that we are able to address all the concerns.  But, a
     result will be still unpredictable.  Would we resubmit this paper to GRL,
     we will obtain the same comments.  The problem is in the state of minds in
     our scientific community.  Would you be so kind as to read the reviews
     and let me know your opinion. The attached is a copy of the manuscript.
     Yours,  Kostya
     ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~
     Dr. Konstantin Y. Vinnikov                   Office: (301) 405-5382
     Department of Meteorology                       Home: (301) 779-2970
     University of Maryland                           Fax: (301) 314-9482
     College Park, MD  20742                 E-mail: kostya@atmos.umd.edu
     ---------- Forwarded message ----------
     Date: Fri, 12 Nov 2004 19:51:34 -0500
     From: Alan Robock <robock@envsci.rutgers.edu>
     To: kostya@atmos.umd.edu
     Subject: Fwd: Decision on Nature manuscript 2004-09-24002B
     Dear Kostya,
     I am sorry to pass on this news to you.  I am on Easter Island, so cannot work
     on this for another week, but please share it with the co-authors and we can
     plan our next step.  I will go to Pucon on Sunday for a week at the IAVCEI
     conference and then home.  Except for this email, we are having a good time.
     Alan
     Alan Robock, Professor II
       Editor, JGR - Atmospheres
       Director, Center for Environmental Prediction
     Department of Environmental Sciences              Phone: +1-732-932-9478
     Rutgers University                                  Fax: +1-732-932-8644
     14 College Farm Road                   E-mail: robock@envsci.rutgers.edu
     New Brunswick, NJ 08901-8551  USA      [1]http://envsci.rutgers.edu/~robock
     ----- Forwarded message from h.langenberg@nature.com -----
         Date: Fri, 12 Nov 2004 16:11:03 UT
         From: h.langenberg@nature.com
     Reply-To: h.langenberg@nature.com
      Subject: Decision on Nature manuscript 2004-09-24002B
           To: robock@envsci.rutgers.edu
     12th November 2004
     Dear Professor Robock
     Your manuscript entitled "Observed and Model-Simulated Temperature Trends at the
     Surface and in the Troposphere" has now been seen by three referees, whose
     comments are attached.  I am sorry to say that all three referees raise a
     number of apparently important technical and general criticisms, which prevent
     us from offering to publish the paper in its present form. Moreover, we must
     form an editorial judgement, based on the referees' specific comments and our
     own editorial criteria, as to the likely suitability of a potential revised
     manuscript for publication in Nature, rather than a specialist journal.
     In this regard, we cannot be encouraging. You will see that, while the referees
     find your work of some potential interest for others working on this topic,
     they raise concerns about the advance your findings represent over earlier work
     and the strength of the conclusions that can be drawn in view of a number of
     problems with the interpretation of the satellite data as well as the model
     simulations. We feel that these criticisms are sufficiently important as to
     prohibit publication of your work in Nature.
     I am sorry that we cannot be more positive on this occasion but hope that you
     find our referees' comments helpful when preparing your paper for resubmission
     elsewhere.
     Yours sincerely,
     Heike Langenberg
     -----------------------------------------------------------
     Dr Heike Langenberg
     Senior Editor
     -
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     Reviewers Comments:
     Referee #1(Remarks to the Author):
     Review of "Observed and model-simulated temperature trends at the surface and in
     the troposphere"  by K. Y. Vinnikov, N. C. Grody, A. Robock, R. J. Stouffer, P.
     D. Jones and M. D. Goldberg.
     Nature
     General comments
     This article presents some new results based on a reprocessed MSU record and
     some comparisons with a model result.  The article is full of hyperbole and
     rhetoric, and greatly overstates the greatness of the results and how well they
     agree with models.  It overlooks a number of problems and the discussion is not
     well balanced. This is not to say that the work is not a useful step in the
     ongoing saga of the development of a climate record out of the MSU series of
     instruments, but it is really just one step and far from the final one. Even if
     written in a more balanced way, it would be unlikely to be suitable for
     Nature.
     Other overall comments
     The article was accompanied by another article that is evidently in press in J
     Geophysical Research.  I read this article with interest.  It makes a good case
     that previous efforts to adjust the MSU time series for the changes in
     satellites have not been adequately physically based and that results differ as
     a consequence.   However, I was less convinced that it dealt adequately with
     surface emissivity effects or diurnal cycle effects that arise, not just from
     different crossing times of different satellites, but also especially from
     drift in a single satellite's orbit. Nor did it properly take into account that
     some satellite overlaps are small (with NOAA-9).  The Mears et al. works
     suggests that the diurnal cycle makes a difference of order 0.1C in MSU-2 for
     the drift associated with NOAA-11 and the difference is mostly over land, where
     it is much larger.  Nor did this work deal with other errors from things like
     satellite roll
        The paper uses two different latitude bands to deal with the nonlinear
     correction.  But it fails to come to grips with land vs ocean differences; it
     is only over land where the diurnal cycle really rears its head.  Also the huge
     differences in emissivity over the ocean and land (factor of 2) also suggest
     that there are differences between wet and dry land that are not dealt with
     properly.
     There is no validation of the result.  In particular, there are no comparisons
     with radiosondes or anything else to show that the results give "high quality
     data" or  "accurately adjust the satellite measurements", to quote from the
     Nature submission.  Applying the methodology of the earlier work means that
     only zonal means can be dealt with and there are no local retrievals.  So there
     is no way to examine land vs ocean trends or compare with radiosondes.  The
     figures show only zonal mean trends, which is unsatisfactory.
     In addition, the paper fails to show any time series.  We do not get to see
     whether there is a discontinuity at the time of NOAA 9 transitions (as seemed
     evident in the earlier paper).  Linear trends are not a very useful way to
     examine or evaluate the record, especially as that is the main part that is
     highly questionable.  At least one would like to see latitude-time series
     displayed.
     Another substantial issue is that MSU2 is NOT the same as the troposphere.
     Certainly a model can be weighted to replicate the MSU profile but that is only
     valid if the model has trends in the stratosphere that are similar.  The model
     results quoted do not have ozone depletion and certainly do NOT satisfy that
     criterion.  Elsewhere, the references to troposphere are not correct.
     The comparison with the model is a comparison of apples and oranges.  The
     forcings used in the model are not at all complete.  No other greenhouse gases
     and no ozone depletion in the stratosphere were used, aerosols incomplete, etc.
      There is no validation of whether the model has realistic changes in sea ice,
     or how El Nino events influence the result.  This is a most unsatisfactory
     comparison and has no merit.
     More detailed comments
     The rhetoric and exaggerated claims in the abstract are strong.  I disagree with
     the opening sentence.  The second sentence greatly overstates the case: this is
     not true for models run with ozone depletion in the stratosphere.  Several
     claims are made "for the first time" which are arguable.
     On p 3 the 10% value is very different for land vs ocean. As a result the use of
     zonal means is a problem.
     On p 4 first para the claim that Ref 1 has poor procedures is correct but ref 2
     does it differently and in a justifiable way but is not discussed.
     On p 4 the claim to a homogeneous record is not substantiated.
     On p 5: The vertical bars on Fig 1 appear to deal only with temporal variability
     but take no account of spatial variability and land-sea differences: they are
     zonal means.
     P5: the diurnal cycle effects depend on the satellite and length of record for
     the drift, and may not be linear: land vs ocean effects enter in.  The
     ascending and descending orbits are not at the same locations.
     P5 presumably the surface record in Fig 1 is processed for the same months as
     the MSU even though the base is 1961-90?
     P 6 top: if the authors had discriminated between land and ocean they might be
     aware of several papers published about disconnects between the surface and
     troposphere such as with continental temperature inversions in winter, trade
     wind inversions over the ocean, and so on.
     P 6 top: the work of Ref 20 is relevant to the discussion on Antarctica.
     P 6 on: the use of 1978-2004 is misleading since it is really November
     1978-February 2004.
     P6: The assumed surface emissivity is just that: assumed.  It does not treat the
     spatial variability.
     P 7: If one compares the Arctic trends, doesn't it make sense to first examine
     whether the model has realistic sea ice and its changes?  The agreement is not
     "remarkable"!
     P7 bottom: The statements about differences between observations and models seem
     at odds with work by Santer et al and GISS.
     P8: to do a credible job in Fig 3 it is necessary to deal with the seasonality
     and land vs ocean.  The conclusions are all hyperbole.
     Referee #2(Remarks to the Author):
     This paper claims to resolve the much debated disrecpancy that exists between
     observations and models in their representation of the difference between
     surface and free atmosphere temperature trends during the satellite era of
     measurement from the MSU instruments. The paper presents new analyses of zonal
     mean surface minus troposhperic air temperature trends (as represented by MSU
     channel 2) from observations and from a model.
      The paper rests on twin pillars. The first is a new analysis of the satellite
     data that produces a larger MSU2 trend (0.17K/decade for 1978-2004) than
     previous anaylses (compared to 0.12K/decade and 0.04K/decade for 1978-2002 from
     Mears et al, 2003 and Christy et al, 2003).
     I do not feel qualified to comment on this first pillar and whether the MSU data
     analysis is likely to be more accurate than previous analyses by other authors.
     I will comment instead on the other pillar of the analysis, the comparison with
     model results.  The authors use simulations of the GFDL R30 model that include
     the effects of increasing greenhouse gases and the direct effects of sulfate
     aerosols. They obtain a relatively good agreement between the zonal mean
     surface-free atmosphere trends from the model simulations and their new
     analysis.
     Can we be confident that this agreement is not a fortuitous
     cancellation of errors ? The most troubling issue from the modelling
     point of
     view is that the simulations considered do not contain a number of forcings
     that would seem to be potenitally important for understanding trends in surface
     and MSU2 temperatures over the 1978-2004 period, including stratospheric
     volcanic aerosols and stratospheric ozone depletion.
     Figure 4 of Broccoli et al (JGR, 108, D24,doi:10.1029/2003) shows a large
     difference between the surface warming trends in runs of the GFDL R30 model
     with and without stratospheric volcanic aerosols.  Fig 2 of Santer et al
     (Science, Contributions of anthropogenic and natural forcing to recent
     tropopause height changes, 2003) shows a very small MSU T2 cooling from
     1970-1999 from volcanoes in the PCM model. This implies that if there is a
     surface cooling from volcanoes over this period (and the GFDL R30 results imply
     of order 0.1K/decade cooling), this could potentially reduce the surface minus
     MSU T2 trend from the model
     thereby worsening the model data agreement. However, there are also indications
     that the GFDL R30 model (fig 9 of Broccoli et al) has a systematically too
     strong cooling response to volcanic aerosol.
     These considerations seem to undermine the argument that the GFDL R30 model is
     reproducing the newly analysed MSU data for the right reasons, ie by capturing
     the most important processes correctly. Santer et al (Science, 2000) obtained
     the best agreement in surface minus MSU 2LT trends with model runs that
     included the effects of Pinatubo in addition to greenhouse gas, aerosol and
     ozone forcings. This study on the other hand ignores the effects of volcanic
     aerosols and a number of other relevant forcings. The paper would therefore
     benefit from some further consideration of these issues.
     Referee #3(Remarks to the Author):
     In an independent analysis of satellite MSU observations, Vinnikov
     and Grody (Science, 2003) showed a T2 trend of 0.22 to 0.26 per
     decade, larger than those from both UAH (~ 0.01k/decade) and RSS
     (~ 0.1k/decade) teams.  This paper by Vinnikov et al. is a welcome
     improvement in their analysis in which they have now accounted for
     instrumentation calibration.  They find a new global T2 trend of 0.17
     K/decade, claiming an agreement with the global observed surface trend
     (0.17 K/decade).  The paper further shows that the observations
     are consistent with GCM simulations in terms of the latitudinal
     distribution of the trends from the surface and troposphere. The
     physically-based procedure used in this study to calibrate MSU
     observation, which is reported in Grody et al. (2004; JGR), might also
     indicate the potential uncertainties in the empirical approach adopted
     by both UAH and RSS.  But I do not recommend a publication of this paper
     in Nature because of the following major concerns.
     First, the two parameters, dT and dU in Eq. (1) are estimated by
     grouping the MSU observations into two equal-area latitudinal bands,
     which is not validated.  These two parameters can also be derived
     by grouping the data into two equal-time periods, leading to a
     quite different T2 trend.  Also without explicitly removing the
     satellites' diurnal drifting effects, dT and dU are directly affected
     by the difference between satellite measurements due to the diurnal
     variation, which are independent of the calibration errors.
     Second, this study does not explicitly consider the impact of
     satellite diurnal drifting on the T2 trend.  The cited bias of 0.04
     K/decade due to the diurnal variation is too small, which can easily
     be shown from the trend differences between the RSS and UAH for
     their time series after 1987 even both have the diurnal cycle
     corrections.
     Third, in view of known biases (at least in terms of signs) in both
     GCM (e.g., positive bias due to not including ozone depletion) and
     satellite MSU data analysis (e.g., negative bias due to the diurnal
     effect), the agreement between the GCM and observation indicates other
     biases in either GCM or data, which cancel these known biases.  Thus,
     the authors' conclusion that the agreement of model and data gives
     confidence in both is not justified.
     In summary, although improvements have been made, this paper is no more
     convincing than Vinikov and Grody (Science, 2003) in terms of deriving
     more realistic tropospheric temperature trends based on satellite
     observations.
     ********************END********************
     ----- End forwarded message -----

   Prof. Phil Jones
   Climatic Research Unit        Telephone +44 (0) 1603 592090
   School of Environmental Sciences    Fax +44 (0) 1603 507784
   University of East Anglia
   Norwich                          Email    p.jones@uea.ac.uk
   NR4 7TJ
   UK
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