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A critique of ‘Collision mortality has no discernable effect on population trends of North American Birds’
Posted by 20 Dec 2011 at 07:52 GMTon
Michael Schaub1, Marc Kéry1, Pius Korner1,2, Fränzi Korner-Nievergelt1,2
1Swiss Ornithological Institute, Seerose 1, CH-6204 Sempach, Switzerland
2oikostat GmbH, Ausserdorf 43, CH-6218 Ettiswil, Switzerland
In a recent paper, Arnold and Zink (2011) attempt to quantify the effects of collisions with large, man-made constructions on population trends of North American birds. They do so by investigating whether there is a statistical association between an estimated index of collision mortalities of birds and estimated long-term population trends in the North America Breeding Bird Survey (BBS). The question of whether there is a causal relationship or not is very relevant for conservation because large numbers of birds die every year due to the collision with buildings, wind turbines, electric power lines or other obstacles and the effects of this additional mortality on bird populations is currently unknown (Klem 1990, de Lucas et al. 2007, Hager et al. 2008, Drewitt and Langston 2008). To tackle this problem, Arnold and Zink (2011) first regressed the species-specific number of dead individuals found under a series of monitored buildings against the estimated continental population size of each species and an index of overlap of the species distribution with collision sites. Subsequently, they used the residual of a species as an index of its collision vulnerability. In a second step, they correlated vulnerability indices with the estimated long-term population trends of these species from analyses of the North American Breeding Bird Survey. Arnold and Zink (2011) found no correlation, and therefore stated “collision mortality has no discernable effect on population trends of North American birds”. We think that based on their study this bold conclusion is not justified, because there are fundamental flaws and also other problems in the analysis of Arnold and Zink (2011).
First of all, we challenge the very basis of their study, viz. to interpret the absence of a relationship between estimated collision risk and estimated population trend as evidence that collision mortality has no effects on population trends in North American birds. The following example illustrates the fundamental flaw in this reasoning (see figure 1 on www.oikostat.ch/exchange/...). Imagine a species A, which would have a strong overall positive population trend in the absence of collisions. In the presence of collisions the observed population trend is slightly negative. The vulnerability of species A, expressed as the difference between the two population trends, is large. In contrast, species B is in dire trouble, perhaps because its habitat in the breeding or the wintering grounds is being destroyed. Its population trend in the absence of collisions is strongly negative. As species B has a low collision vulnerability the observed population trend is only slightly less than what its population trend would be in the absence of collision mortality. The vulnerability of species B to collisions, again expressed as the difference between the two trends, is much smaller than that of species A. This example shows that a high collision vulnerability need not necessarily result in an observed, more negative population trend than a low collision vulnerability. Any correlation between collision vulnerability and population trends must be corrected for other effects on the population trends, before any inference can be made about the effects of collision mortality.
Thus, clearly in any correlative study, there is a risk that an observed relationship is not causal, but may be induced by another mechanism (e.g., Aldrich 1995) or, alternatively, that a causal relationship is hidden by the effects of another mechanism. Potential factors that may either affect population trends and/or collision vulnerability need to be included in such an analysis, otherwise there is a high risk to jump to unjustified conclusions due to pseudocorrelation. As an example of such confounding factors, imagine that bird species are categorized as urban and non-urban species. Urban species may generally have higher relative collision vulnerability than non-urban species, because they live closer to buildings on average. At the same time, urban species have higher population growth rates than non-urban species (Sauer and Link 2011). Even if there is indeed a negative correlation between collision vulnerability and population trend within each group, this may no longer be discernible if all species, urban and non-urban, are analyzed jointly without consideration of the habitat factor (see figure 2 on www.oikostat.ch/exchange/...). The conclusion would then be that there is no effect of collision mortality on population trends, which is clearly the wrong conclusion in this example. Another possible confounding factor in the analysis of Arnold and Zink of which we can think of is the life-history of the species. It is likely that many such confounding factors occur. Multivariate analyses should be used and confounding factors included in order to minimize the risk of reaching wrong conclusions. Surely, there may be always other confounding factors which are unknown, but a proper discussion of this problem is needed when such strong claims are made as the authors do in their title.
Third, Arnold and Zink (2011) also calculated the power of their analysis to detect effects and concluded that their analysis had a very high power to detect even partial effects. This reasoning is false. It is not possible to detect partial effects with high statistical power. This follows from the definition of a partial effect which is the regression coefficient that one would expect if all the other variables in the regression equation had been held constant experimentally (e.g. Sokal and Rohlf 1995). Thus, partial effects can only be detected when other effects on population changes are taken into account in the analyses. Furthermore, there are measurement errors along both axes (each species-specific population trend has an error, as has each collision vulnerability index), and these were not taken into account in the analysis. If measurement errors are included, the power would decline dramatically. Finally, even if the statistical power of the Arnold and Zink analysis is high, it does not prevent from the problem of a correlative study that causation cannot be inferred.
Lastly, we have serious reservations about an analysis that lumps all species: we do not think that this is meaningful for conservation management. Even if a sound analysis could show that there is no relationship between population trends and collision mortality across all species, this would not necessarily mean that no group of species, no single species or no population of one or some species is affected. Also, we would usually worry less about effects in such species as, say, introduced European starlings (Sturnus vulgaris) than on rare and declining native species, such as, say, Bachman’s warbler (Vermivora bachmanii). Arnold and Zink (2011) do not make the claim that no species or no individual population is affected, but we fear that stakeholder interested in building obstacles like towers, wind turbines or electric power lines could use this line of argumentation to avoid costly mitigation measures and to reduce the risk of not getting the permission for the construction. The management goal must be to avoid losing more species or affecting their populations negatively by the construction of such obstacles. Hence, assessments must necessarily be species-specific or even population-specific. As an analogy, consider the management of hunting pressure in game management. No sensible person would want to know whether hunting has an effect on the population trends across all species and across an entire area of North America. Rather, we want to know how strongly harvesting affects a particular population of each species and then define regulations based on that. It may be true that habitat loss and fragmentation are the main reasons for the negative population trends in many species and that collisions of birds with towers, buildings, wind turbines or electric power lines are of lesser importance to determine population trajectories. However, this does not mean that no species or no population is affected by this factor. Moreover, collision risks are rapidly increasing in importance. Careful comparative analyses can be insightful to obtain general conclusions averaged over many species, but we think that in the case of the effects of collisions on bird populations this is not what is needed. It is risky to make general and strong claims about the effect across all species, since we may buy the loss of some species or populations with the wellbeing of others. We therefore call for sound species-specific population assessment of the potential impact of obstacles and question the usefulness of such general analyses in this case.
Aldrich J. 1995. Correlation genuine and spurious in Pearson and Yule. Statistical Science 10: 364-376.
Arnold T. W. and R. M. Zink. 2011. Collision mortality has no discernable effect on population trends of North American birds. Plos ONE 6: e24708.
de Lucas, M., G. F. E. Janss, and M. Ferrer 2007. Birds and Wind Farms, Risk Assessment and Mitigation. Quercus, Madrid.
Drewitt A. L. and R. H. W. Langston. 2008. Collision effects of wind-power generators and other obstacles on birds. Annals of the New York Academy of Science 1134: 233-266.
Hager S. B., H. Trudell, K. J. McKay, S. M. Crandall, and L. Mayer. 2008. Bird density and mortality at windows. Wilson Journal of Ornithology 120: 550-564.
Klem D. Jr. 1990. Collisions between birds and windows: mortality and prevention. Journal of Field Ornithology 61: 120-128.
Sauer J. R. and W. A. Link. 2011. Analysis of the North American breeding bird survey using hierarchical models. The Auk 128: 87-98.
Sokal R. R. and F. J. Rohlf 1995. Biometry. 3rd edition. W.H. Freeman & Co., New York.
RE: A critique of ‘Collision mortality has no discernable effect on population trends of North American Birds’
20 Dec 2011 at 12:27 GMTreplied to on
Todd W. Arnold1, Robert M. Zink2
1Department of Fisheries, Wildlife, and Conservation Biology, University of Minnesota, St. Paul, Minnesota, United States of America; 2Bell Museum and Department of Ecology, Evolution and Behavior, University of Minnesota, St. Paul, Minnesota, United States of America
We welcome the opportunity to respond to the critique posed by Schaub et al. (2011) of our recent paper "Collision mortality has no discernable effect on population trends of North American birds" (Arnold and Zink 2011), and we thank them for voicing their concerns in this public forum. Although we dispute most of their criticisms, we agree that our conclusions are too important to be accepted without careful scrutiny by the scientific community.
We believe that careful examination of Schaub et al.'s first argument actually supports our claim that "collision mortality has no discernable effect on population trends of North American birds." Schaub and colleagues imagine bird species A, which would be increasing substantially, were it not for very high collision vulnerability that causes the population to decline only slightly. Species B is declining precipitously for other reasons and the additional effect of a modest level of collision vulnerability is a slight additional reduction in population trend. Nevertheless, given different initial trajectories of population growth in the absence of collision mortality, species A with high collision vulnerability actually has greater population growth than species B. We avoided making comparisons based on limited numbers of species because we acknowledged that there was substantial measurement error in both collision vulnerability and population trends, but if we imagine species A and species B are groups of 50-80 species with similar properties, then Schaub et al.'s analogy might resemble our analysis.
Under such a scenario as this, we would ask "what factors are causing populations in group A to increase so dramatically and populations in group B to decline so precipitously, in the absence of collision mortality?" These are seemingly the factors that matter the most to the long-term population dynamics of North America's landbirds, and we would argue that these are the factors most deserving of attention by conservation biologists (also, these are likely the places where mitigation efforts would be most effective). If collision mortality were one of these prominent factors, then it should have appeared in our analysis as a significant predictor of long-term population trends, but it did not. We do not argue that collision mortality has no role in population dynamics, only that it has a small and (in our analysis) indiscernible role.
The fact that "baseline population trends" (i.e. the unobservable trajectory of a population in the absence of collision mortality) might vary widely among species does not preclude an assessment of the unique impact of collision vulnerability on overall population trend, although it would render such an effect more difficult to detect. But Schaub et al.'s analogy seems to imply that collision vulnerability might also be positively correlated with baseline population trends, such that effect sizes for collision mortality are high among species that are otherwise increasing and small among species that are otherwise declining. We are skeptical, but point out that even this interpretation suggests that collision mortality is important only among species that can demographically accommodate the additional mortality, whereas species that are declining strongly are declining for reasons other than collision mortality, an interpretation that is scarcely different from our own.
Nevertheless, we think the graphs prepared by Schaub et al. are potentially insightful, because they posit that collision mortality constitutes an additive source of mortality, and that population trajectories would be noticeably different in the absence of collision mortality. We believe that reconciliation of our apparently unpalatable result hinges on the fact that collision mortality is not additive, but rather is compensated by other forms of mortality, such that most collision mortality: 1) represents birds that would have died anyway, or 2) creates habitat vacancies that allow birds that otherwise would have died to survive, via density-dependent feedback (Boyce et al. 1999). We acknowledge that our results currently lack a mechanistic explanation (i.e., demonstration of an ecological process whereby population trajectories would not be impacted by a large source of mortality) and view this as a shortcoming of our study.
Our analysis was indeed correlative, rather than experimental, but we were not correlating population trends with numbers of communication towers or El Niño events, but with measures of actual mortality. Populations only change as a result of births, immigration, deaths, and emigration, so all other things being equal, a substantially larger pile of dead bodies from species A should correlate with a declining population, assuming that this source of mortality is indeed important. Obviously a weak effect could masquerade as a strong effect if the weak factor was highly correlated to a stronger but unmeasured effect, but collision mortality has been widely touted as one of the strongest anthropogenic impacts on bird populations, so we expected it to play a dominant role in this analysis.
We are somewhat bemused by the example of urban versus non-urban birds, because we had included this as a covariate in an earlier unsuccessful submission of our paper to a different journal:
"Urban birds were about 2-fold less vulnerable to collision (F1,187 = 3.85, P = 0.05), and this result did not change if the analysis was restricted to buildings or towers only. However, these variables were not independent (i.e. most foliage gleaning birds are long-distance nocturnal migrants that avoid urban areas), so we conducted multivariate analyses to determine which variable(s) were most strongly associated with collision risk. After controlling for timing of migration, migration distance and urban habitat use were no longer significant (P > 0.23), but foraging mode became more important (F6,160 = 3.09, P = 0.007)."
Thus the effect of urbanization was contrary to what Schaub et al. imagine, but inclusion of this and other factors did not alter our conclusions. Any factor(s) that help explain long-term population trends would allow for a more powerful assessment of collision effects, but we elected to pursue a simple analysis for this paper, which was intended for non-ecological audiences. We had always imagined following up this paper with a more thorough multivariate analysis of site-specific mortality intended for an ornithological or ecological journal. We have conducted many preliminary analyses along these lines, and while we have identified other factors that affect collision vulnerability (e.g. habitat, foraging mode, phylogeny), we have not identified additional factors that alter our conclusion about population trends.
Barring potential concerns about unrecognized but strongly correlated predictors (which we rejected above), it makes no difference if we consider the variance component of Y = a + bX + e to consist entirely of random error or to consist of random error plus unrecognized structural variation (e.g. due to urban vs. rural habitats, life-history variation, etc.). To the extent that other meaningful predictors of population trends could be identified and included in the model (thereby reducing residual variation), a more powerful detection threshold could be achieved, and perhaps an effect of collision mortality would be discovered. But our cursory analysis suggests that it will be smaller than ~ 0.5% per year for a 10-fold increase in mortality risk.
We agree that our "cookbook" power analysis did not fully account for the complexity of our data (i.e. error in both X and Y, which we acknowledged in the last paragraph of our Materials and Methods; Warton et al. 2006). However, simple Monte Carlo simulations that recognize 5, 10, or 20% measurement error in X (relative collision vulnerability) do not appreciably affect the power of our analysis to detect a correlation between collision vulnerability and population declines (slopes are more affected, but in the absence of a correlation slopes are always nonsensical).
We doubt that Schaub and colleagues would be criticizing the non-experimental nature of our analysis had it revealed a significant negative correlation between collision vulnerability and population trends and we would ask any of our potential critics this critical question: "Would you be skeptical of our methods if we had concluded that buildings and communication towers were bad for birds?"
We agree with Schaub et al.'s final point that our analysis does not preclude that populations of some species may be deleteriously impacted by collision mortality. We will venture that Bachman's warbler (Vermivora bachmanii) is already extinct, but accept their point that for a species already at risk, the added burden of collision mortality might contribute importantly to extinction risk, and our analysis highlighted golden-winged warblers (Vermivora chrysoptera) and Bachman's sparrows (Peucaea aestivalis) as two species worthy of focused attention (Arnold and Zink 2011: Table S1). But we strongly dispute the contention that assessments of risk must be species or even population specific. Caughley (1994) accused conservation biologists of becoming humdrum if every declining population demanded a case-specific approach. Surely, every population has a somewhat unique collection of limiting factors, but there must also be common factors that affect large assemblages of species, and for North American birds, collisions with buildings or communication towers have been widely implicated as just such factors.
Rachel Carson (1962) first highlighted the threats posed to birds by organochlorine pesticides, and DDT was subsequently banned in the U.S. in 1972. We identified a set of 23 birds from 8 different orders believed to be highly impacted by DDT as based on specific mention of DDT in their Birds of North America account and by the existence of > 30 academic references to DDT in a Google Scholar search that included "Silent Spring", DDT, and the English common name of each species. These 23 species had a mean positive population trend of +1.43% per year (SE = 0.59, t = 2.41, P = 0.02) in the decades post-DDT. Eleven species showed significant population increases; only 2 showed significant declines. By contrast, 300 species with no mention of DDT in their BNA account had no net population change (-0.08% per year, SE = 0.19, t = 0.45, P = 0.65). We leave it to others to parse out any confounding effects of urban habitats or life-history variation, but we believe our methodology is powerful even on much cruder data sets than collision mortality, where our measures of vulnerability were based on over a quarter-million carcasses.
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