I’ve had a little more time to look at this paper–discovering in the process that it had already made headlines in the popular media, including at a number of blogs. A few of those articles discuss some details, but not many and not too deep, while others are just rehashes or synopses of what the authors say. Painful experience teaches me that I’m not going to learn much of what I really want to know from that stuff. Google the article title if you want to read some of it.
In part one, I made some general, and tangential, comments about reading science papers. Here, I’ll look specifically at analytical issues of the paper in more depth, asking some questions if nothing else. Please get hold of the paper and read it if you can. It helps nothing whatsoever if you just take my word here–I’m not after that, it doesn’t foster progress in understanding. Maybe I’ve missed, or mis-interpreted, something important. Maybe something crucial in fact.
The authors are to be commended for paying the extra money to make the paper open access (assuming that’s what happened). However, there appear to me to be a number of serious questions to be raised. These fall under (at least) four different categories as I see it: (1) subject matter issues dealing with recent past, and future, climate estimation, (2) biodiversity-related issues as affected by climate change, (3) terminology/scale/scope issues and (4) statistical/mathematical/data issues. These are quick and rough categories and not mutually exclusive.
The paper is essentially a large GIS exercise, and in fact the authors state that the paper originated from a class exercise. They took the spatially specific, monthly and yearly output for seven climate variables from the 39 GCMs used in the CMIP5 that had data going back to 1860, and overlaid those onto coarse-scale species richness maps for 13 very broadly defined taxa, as obtained from the IUCN among others, using an interpolation routine to account for the different native spatial resolutions of the climate and taxon information. From this they compute the first year in which the future annual state of each variable always exceeds the range established from 1860 to 2005. They also do this for monthly data, and they do some sensitivity testing to things like the length of the historical period used. Then they add a paragraph about probable species climatic tolerances (and range limits) as a function of latitude, state very generally what that might imply for “biodiversity”… and that’s it. As a GIS class exercise, great, as a paper published in Nature, I’m not at all so sure.
The authors used the data from two of the emissions scenarios used in CMIP5–one of which (they state), RCP4.5, takes the atmosphere to just under 540 ppm by 2100 (mean of 1.69 ppm/year) and the other (RCP8.5) to just under 940 ppm; they refer to these as the “concerted rapid CO2 mitigation” and “business-as-usual” scenarios, respectively. The former value might indeed turn out to be unrealistically low, but is not greatly different from the current rate of about 1.85 ppm/year. The latter value, conversely, differs from the current rate by a vastly larger amount, averaging roughly (936-378)/95 = 5.9 ppm/year. One could certainly question the usefulness of using a rate that is over 300% of the current rate, and also the descriptive labels applied to the numbers; in what sense is a 300 percent increase in any way “business as usual”? The results from that extreme scenario (and that one alone) are what are presented in their Figure 2 and “Extended Data Figure 4“.
Also, how did they come up with their stated year 2100 CO2 concentration values of 538 and 936 for the two RCPs (Representative Concentration Pathways)? The RCPs used in CMIP5 are defined in terms of radiative forcing in W/m^2 (or, CO2 equivalent ppm), not CO2 concentration per se. Their paper cites Taylor et al 2012, but in looking at that, and also the paper on which it is based (Taylor et al, 2008), I can find in neither publication just where/how they got their CO2 concentration numbers. Why also, did they not analyze the less extreme scenario embodied by RCP6.0, which represents about a doubling of radiative forcing from 2006 to 2100? The basis for this choice is not stated. And what exactly is the justification for using only a 20 year period, 1986 to 2005, to test for correlations between modeled and actual climate variables? That’s a very big issue by itself, a central focus for climate modelers.
Look at the middle panel in each row (“Absolute Change”). Note that the scale for precipitation is roughly about 10 fold higher than that for transpiration. Note also, in the left-most panels of each row, that the expected year of climate departure over a vast chunk of the planet (deep blue color), is the last decade, 2090-2010, especially for precipitation. But 2100 is just an arbitrarily defined end point of the CMIP5 simulations, nothing more. So this might well indicate that for much of the planet, the expected year of departure actually falls out somewhere beyond 2100. And again, this is for the worst case scenario, the RCP8.5, about three times the current radiative forcing.
Moreover, look at the axis scales. How can it be that for a large percentage of the planet’s land surface, the projected drop in precipitation rate (light blue-green shading, and white) is, very roughly, about ten times greater than is the drop in transpiration rate? This implies directly that in much of the tropics, which are the focus of much of the discussion and emphasis in the paper, there is a pronounced excess in precipitation relative to what thermal energy can transpire, and that the projected increase in temperature therefore does not come anywhere close to removing this water from the land in most places. This in turn has very important implications for vegetation stability, and with it, a whole slew of ecological variables (diversity, biomass, etc), since continued transpiration is absolutely vital to plant temperature regulation, and plants form the basis of any ecosystem. Granted that I am looking only at large scale graphical displays in making these judgements, not spatially-specific numerical values, and therefore cannot discriminate between say, the wet and seasonally dry tropics, but that is the information they provided. There might be some tropical areas in which water would be predicted to become limiting, but again, we are talking about an extreme radiative forcing (RCP8.5 radiative forcing is equal to ~ 1350 ppm CO2 equivalent, according to Taylor et al., linked to above) assumed to occur less than 90 years from the present.
There are also very important questions to be raised regarding the validity of using 145 years as the historical reference period when you are addressing the issue of climate change on biodiversity dynamics. The world’s species did not evolve within, or adapt to, a 145 year climate window. This is a positively enormous topic that I unfortunately can’t begin to do justice to at the moment, but it needs to be at least mentioned in passing.
Another issue. I was slow to wrap my mind around the authors’ intent here, but once I got it the thought immediately occurred that, certainly, other groups must have done this kind of analysis, given (1) the importance of the potential speed of climate change, and (2) that the CMIP5 and AR5 are both very recent. If so, then the authors could just focus on the spatial and biodiversity effects issues, given that the lead author is a biogeographer (and presumably many of the junior authors as well, who are in his lab, many of them graduate students). Projected/modeled climate change from climate models is one subject, and how climatic changes might affect coarse taxonomic groupings on large spatial scales is another, no?
In looking for data used in, or from, the study, I found, at the lead author’s web site, a page titled “clarifications“, which contains an apology for not having cited nine relevant works since 2009, which the authors were made aware of, after publication, by Ed Hawkins, studies which Mora says support their findings. Coincidentally, Hawkins, who has published on this topic (time of climate departure from historical ranges), had just blogged on the topic about a week earlier. Were Mora et al. not aware of these studies? That’s how it appears. How can you get a paper published in Nature without being fully up to date on recent work in a field and/or bringing it into the discussion? Well, one way would be if the reviewers and handling editor were also ignorant of them, or for whatever reason did not raise the issue in their comments. Is that the case here?
That’s all I have time for, I will have to leave it there, at least for now.