cc: Alan Robock date: Mon Nov 15 16:01:00 2004 from: Phil Jones subject: Re: Fwd: Decision on Nature manuscript 2004-09-24002B (fwd) to: Konstantin Vinnikov , Norman Grody , Ronald Stouffer , Mitch Goldberg 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 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 - The Macmillan Building, 4-6 Crinan Street, London N1 9XW, UK Tel +44 (0)207 833 4000; Fax +44 (0)207 843 4596; nature@nature.com - 968 National Press Building, 529 14th Street NW, Washington DC 20045, USA Tel +1 202 737 2355; Fax +1 202 628 1609; nature@naturedc.com - 225 Bush Street, Suite 1453, San Francisco CA 94104, USA Tel +1 415 403 9027; Fax +1 415 781 3805; nature@naturesf.com - *Nature's author and policy information sites are at [2]www.nature.com/nature/submit/ 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 ----------------------------------------------------------------------------