from: Tim Osborn <t.osbornatXYZxyz.ac.uk>
subject: review of JD/2001/000589
to: jgr-atmospheresatXYZxyz.org, firstname.lastname@example.org
Here is my belated review of the manuscript by Gillet et al. "How linear is the Arctic Oscillation response to greenhouse gases?". Overall, the manuscript presents some interesting new results, inter-model comparisons and provides some discussion of the possible physical/dynamical mechanisms that may be important in generating the behaviour of the Arctic Oscillation in response to enhanced greenhouse gas concentrations. This is certainly appropriate subject matter for JGR-Atmospheres, and the overall method and data are adequately used. I would recommend publication in JGR-Atmospheres, after addressing the minor comments that I outline below.
(1) Abstract, lines 5-6: "...the observed response in the models...": do NOT use the word "observed" when describing model output because it is so easy to get confused - reserve "observed" for actual observations and use "simulated" or something similar when dealing with model output. Please check the remainder of the manuscript for this ambiguous usage.
(2) Page 3-4: "Shindell et al.  are the only workers who have compared their modelled trend with that observed,...": this is not true because Osborn et al.  (which is already cited) compared simulated and observed trends.
(3) Page 5, lines 16-17: "...problems associated with a station-based index discussed previously": I couldn't find a discussion of these problems earlier in the paper, though if you add one please keep it brief.
(4) Page 6, lines 15-18: You should state in the text briefly why a linear response implies little role for oceanic coupling. Does it also imply no role for land-ocean temperature contrast, or meridional surface temperature gradients? They are things that wouldn't be linear with the forcing, in general, though it is possible that they could be quasi-linear in these particular simulations? Maybe worth a line or two of discussion.
(5) Page 7, paragraph 2: You should state the period for which the observed sensitivity was estimated. Also, if both the AO time series and the greenhouse gas forcing time series are dominated by quasi-linear trends over this period, have you adequately taken into account how the reduced degrees of freedom widen the uncertainty range on the sensitivity coefficient?
(6) Page 12, paragraph 1: It is difficult to argue that the two models analysed, particularly HadCM3, are doing poorly other than having a warm bias. The warm bias could easily explain the less-skewed distribution, because the models are typically not reaching the radiatively-determined minimum temperature (Figure 5bc) because of their warm bias, and thus do not have the opportunity to simulated a skewed distribution. Of course, one could argue that they have a warm bias because they simulated these stratospheric processes poorly, but that doesn't seem to be what the authors are arguing, dismissing the warm bias as less important/striking than the distribution shape.
(7) Page 12, paragraph 2: This paragraph is much too strongly worded given the complete lack of statistical testing presented. HadCM3 does show an increased skew (visually at least), so it might be doing the correct thing other than the warm bias. And to say "neither model is able to realistically simulate the observed change in the distribution..." is clearly insupportable given the lack of statistical testing and the fact that the observed change itself may not be statistically significant, let alone the difference between model and observed changes.
(8)Page 15, lines 10-11: I hope that "area-weighted mean" is the global area-weighted mean and not the area-weighted mean of the region north of 20N only. The text implies the latter, but that is clearly wrong since atmospheric mass need only be conserved in the global mean.