USGS Home
Contact USGS
Search USGS

The "management" in "wildlife management" implies causality. We believe we can perform some management action that will produce a predictable response by wildlife. Even if the causes cannot be manipulated, it is useful to know the mechanisms that determine certain outcomes, such as that spring migration of birds is a response to increasing day length, or that drought reduces the number of wetland basins that contain water.

The concept of causation is most readily adopted in the physical sciences, where models of the behavior of atoms, planets, and other inanimate objects are applicable over a wide range of conditions (Barnard 1982) and the controlling factors are few (e.g., pressure and temperature are sufficient to determine the volume of a gas). In the physical sciences, causality implies lawlike necessity. In many fields, however, notions of causality reduce to those of probability, which suggests exceptions and lack of regularity. Here, causation means that an action "tends to make the consequence more likely, not absolutely certain" (Pearl 2000:1). This is so in wildlife ecology because of the multitude of factors that influence a system. For example, liberalizing hunting regulations for a species tends to increase harvest by hunters. In any specific instance, liberalization may not result in an increased harvest because of other influences such as population size of the species, weather conditions during the hunting season, and the cost of gasoline as it affects hunter activity.

Suppose you want to determine the effect on squirrel abundance of some treatment (= putative cause), for example, selective logging in a woodlot by removing all trees greater than 45cm diameter at breast height (dbh). The treatment effect on some woodlot can be defined as

where Y_t(u) is the number of squirrels in woodlot u after the treatment, and Y_c(u) is the number of squirrels in that woodlot if the treatment had not been applied (I follow Rubin [1974] and Holland [1986] here). If the woodlot is logged, then you can observe Y_t(u) but not Y_c(u). If the treatment is not applied, then you can observe Y_c(u) but not Y_t(u). Thus arises the fundamental problem of causal inference: you cannot observe the values of Y_t(u) and Y_c(u) on the same unit. That is, any particular woodlot is either logged or not.

Holland (1986) described 2 solutions to this problem. With the first, one has 2 units (u₁ and u₂, here woodlots) and assumes they are identical. Then the treatment effect T is estimated to be

where u₁ is treated and u₂ is not. This approach is based on the very strong assumption that the 2 woodlots, if not logged, would have the same number of squirrels, that is, Y_c(u₂) = Y_c(u₁). That assumption is not testable, of course, because 1 woodlot had been logged. It can be made more plausible by matching the 2 units as closely as possible or by believing that the units are identical. That latter belief comes more easily to physicists thinking about molecules than to ecologists thinking about woodlots, however.

Holland (1986) termed the other solution statistical. One gets an expected, or average, causal effect T over the units in some population:

where, unlike with the other solution, different units can be observed. The statistical solution replaces the causal effect of the treatment on a specific unit, which is impossible to observe, by the average causal effect in the population, which is possible to estimate.

This discussion reflects the need for a control, something to compare with the treated unit, which is required for either approach. To follow the statistical approach, we often invoke randomization. If, for example, we are to compare squirrel numbers on a treated woodlot and an untreated one, we might get led astray if the woodlots were of very different size, or if one contained more mast trees, or if one was rife with predators of squirrels and the other was not. One way—but not the only way—to protect against this possibly misleading outcome is to determine at random which woodlot receives the treatment and which does not. This can be done if the researcher has tight control over the experiment; it is impossible in many "natural experiments" and observational studies.

But even if you select at random a woodlot for treatment and another as a control, you still may end up by chance comparing a large woodlot that has numerous mast trees and few predators with a woodlot with opposite characteristics. This leads to the third important criterion for determining causation: replication. Repeating the randomization process and treatments on several woodlots reduces the chance that woodlots in any group consistently are more favorable to squirrels. In summary, then, assessing the effect of some treatment with a manipulative experiment requires a control, randomization, and replication (Fisher 1926).

One might attempt to determine the effect of selective logging on squirrels by comparing woodlots that have trees greater than 45 cm dbh with woodlots that lack such large trees. But such a comparison is not as definitive as a manipulative experiment. The 2 types of woodlots might differ in numerous ways, other than the presence or absence of large trees, that influence squirrel abundance. If variables that are known or suspected to be influential are measured, careful statistical analysis may account for their effects, but large samples may be necessary, and it is possible that an important variable went unmeasured.

An ideal design might involve a number of woodlots on which squirrel density is measured both before and after the treatment is applied. Then, instead of comparing the density of squirrels on treated versus untreated woodlots, one could compare the change in density (before and after treatment) between the 2groups. Crossover designs also provide a powerful way to reduce the influence of inherent differences among experimental units. Under a crossover design, for a certain time period, some units receive treatments and other units serve as controls. Then the roles of the units switch: control units receive treatments and formerly treated units are left alone to serve as controls. An obvious concern with crossover designs is that treatment effects may persist. One remedy is to have a time period between the 2phases of the study sufficient to allow treatment effects to dissipate. A crossover design would not be appropriate for the squirrel-woodlot example because the effect of logging would persist for decades, if not longer. Crossover designs were used by Balser et al. (1969) and Tapper et al. (1996) to estimate the effects of predator reduction on prey species. In these studies, predators were removed from 1 study area for 3 years, while another area served as a control; after 3 years, the treatments were switched.

Correlation versus Causation: the Importance of Mechanisms

It is always useful to have an understanding of the mechanisms that influence phenomena of interest and to distinguish causation from correlation. We might be able to relate mallard production to precipitation (Boyd 1981), but more useful is the understanding that precipitation affects the condition of wetlands where mallards breed, which in turn influences breeding propensity, clutch size, and survival of young (Johnson et al. 1992). We can have greater confidence in our findings if they are consistent with mechanisms that are both reasonable and supported by other evidence. The presence of such mechanisms gives credibility that the correlational smoke may in fact represent causational fire (Holland 1986). Romesburg (1981) argued that causation may be invoked if the correlational evidence is accompanied by, for example, the elimination of other possible causes, demonstration that the correlation occurs under a wide variety of circumstances, and the existence of a plausible dependence between the putative cause and the outcome. In a similar vein, mechanistic models are more useful than descriptive models for understanding systems (Johnson 2001a, Nichols 2001).