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EUROPEAN REVIEW OF SOCIAL PSYCHOLOGY, 2002, 13, 293 – 323
Testing attitude–behaviour theories using non-experimental data: An examination of some hidden assumptions Stephen Sutton University of Cambridge, UK This chapter presents a detailed causal analysis of the two leading theories of attitude–behaviour relations, the theory of reasoned action (TRA) and the theory of planned behaviour (TPB). It is noted that the direct path from perceived behavioural control to behaviour in the TPB is causally ambiguous. Focusing on the attitude–intention relationship, timeline and path diagrams are used to illustrate some of the hidden assumptions that underlie the way these theories are usually tested using standard multiple regression applied to nonexperimental data. Randomised experiments are recommended as the best solution to the serious problems arising from omitted causes.
For the past quarter of a century, the theory of reasoned action (TRA; Ajzen & Fishbein, 1980; Fishbein & Ajzen, 1975) and its extension, the theory of planned behaviour (TPB; Ajzen, 1991; Ajzen & Fishbein, 2000) have been regarded as the leading theories of the attitude–behaviour relationship. These theories are usually ‘‘tested’’ in observational, nonexperimental studies using cross-sectional or prospective designs or a combination of the two. Numerous studies using this methodology have been published; see, for example, the recent meta-analysis of the TPB by Armitage and Conner (2001), and the quantitative reviews and metaanalyses of the TRA and the TPB summarised by Sutton (1998). This chapter examines some of the assumptions that underlie the way that the TRA and the TPB are usually tested. Many of these assumptions appear not to be widely appreciated by researchers in the field. They are implicit in the methods commonly used to investigate the theories, in particular in the standard multiple regression model applied to betweenAddress correspondence to: Stephen Sutton, University of Cambridge, Institute of Public Health, Robinson Way, Cambridge, CB2 2SR, UK, Email:
[email protected] I would like to thank the editors and four anonymous reviewers for valuable comments on earlier drafts of this chapter. # 2002 Psychology Press Ltd
http://www.tandf.co.uk/journals/pp/02699931.html
DOI: 10.1080/10463280240000019
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individuals data. (Note that structural equation modelling makes the same assumptions.) There are two reasons for examining these hidden assumptions. First, it would seem desirable as an end in itself that researchers are fully aware of the assumptions they are making. Second, the assumptions that are made have important methodological implications, for example with regard to whether a cross-sectional or a prospective design is more appropriate for investigating a particular causal relationship or, indeed, whether nonexperimental studies are appropriate at all. The present chapter treats the TRA and the TPB as causal models. It provides a detailed causal analysis (Heise, 1975) of these theories, focusing particularly on the attitude–intention relationship. The exposition is deliberately non-mathematical and makes minimal use of algebraic equations. Instead, diagrams (timeline and path diagrams) are used to illustrate the main points.
THE TRA AND THE TPB AS CAUSAL MODELS Figure 1 shows a simplified version of the TRA. It is simplified in that it omits the beliefs (behavioural and normative) and their respective weights (outcome evaluations and motivations to comply) that are assumed to underlie the global constructs of attitude (A) and subjective norm (S). The TRA is a causal model. Attitude and subjective norm are assumed to influence intention (I), which in turn, under certain conditions (correspondence/compatibility; stability of intention; behaviour under volitional control), is assumed to influence behaviour (B). Figure 2(a) shows the TPB. Again, the belief components have been omitted for simplicity. All the paths in this model represent genuine causal effects with the exception of the direct path from perceived behavioural control to behaviour, which is causally ambiguous (Sutton, 2002). One rationale for this direct link is that perceived behavioural control can often be used as a substitute for actual control (Ajzen, 1991). It goes without
Figure 1. Path diagram showing a simplified version of the theory of reasoned action. (A=attitude towards the behaviour; S=subjective norm; I=intention; B=behaviour.)
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Figure 2. Path diagrams showing the theory of planned behaviour. (A=attitude toward the behaviour; S=subjective norm; PC=perceived behavioural control; AC=actual behavioural control; I=intention; B=behaviour.) Model (a) is a simplified version of the theory, omitting the beliefs that are assumed to influence A, S, and PC. The path from PC to B is represented as a dashed line to indicate that it is causally ambiguous (see text). Model (b) is a version of the theory that includes actual as well as perceived control. The correlation between PC and AC, depicted by the double-arrowheaded path, represents the extent to which people accurately perceive the amount of control they have over the behaviour; for legibility, the other correlations among the variables on the left-hand side are not shown. Model (c) is identical to model (b) except that it includes a direct causal path from PC to B, represented by a dotted line.
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saying that actual control directly influences behaviour or performance: a person cannot achieve a good mark in a maths exam if they do not have the ability; they cannot buy petrol if the garage is closed. But, it is argued, actual control is often difficult to measure and it is less interesting psychologically than perceived control. Perceived control can be used a proxy for actual control to the extent that people’s perceptions of control are accurate. According to this rationale, the direct link between perceived behavioural control and behaviour is not a causal path, and changing perceived behavioural control would not lead to behaviour change directly. (It could lead to behaviour change indirectly, of course, via a change in intention.) In order to change behaviour directly, it is necessary to change actual control. Figure 2(b) shows a version of the TPB that includes actual control as well as perceived control. The path from actual control to behaviour represents a genuine causal effect. The correlation between perceived control and actual control, depicted by the double-arrowheaded path, represents the extent to which people accurately perceive the amount of actual control they have over the behaviour. This correlation may be large or small. The larger it is—in other words, the greater the accuracy of people’s perceptions—then the larger will be the direct predictive effect of perceived behavioural control on behaviour when estimated in the usual way, that is in the context of the model shown in Figure 2(a). But this is a predictive effect of perceived behavioural control not a causal effect. Figure 2(c) is identical to Figure 2(b) except that it also includes a direct causal path from perceived behavioural control to behaviour. Ajzen (1991, p.6) suggested a rationale for this causal path: . . . holding intention constant, the effort expended to bring a course of behaviour to a successful conclusion is likely to increase with perceived behavioral control. For instance, even if two individuals have equally strong intentions to learn to ski, and both try to do so, the person who is confident that he can master this activity is more likely to persevere than is the person who doubts his ability.
Note that this effect is held to be mediated by ‘‘effort’’ and ‘‘perseverance’’, neither of which are constructs in the theory. Thus the direct predictive effect of perceived behavioural control on behaviour shown in Figure 2(a) can be thought of as comprising causal and non-causal components. When we investigate the theory in the usual way and estimate this path, we are conflating a genuine causal effect and what is merely a predictive effect. It is important to try to estimate the relative size of these two components. This would seem to require laboratory-based experimental studies in which actual control and perceived behavioural control are manipulated.
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A further complication concerns the interaction between perceived behavioural control and intention on behaviour that was postulated by Ajzen and Madden (1986). This interaction derives from an interaction between intention and actual control. In particular, intention is expected to have a stronger influence on behaviour the greater the degree of actual control the person has over the behaviour. Stated differently, the effect of actual control on behaviour will be larger the stronger the person’s intention to perform the behaviour. To give a simple example, a person will succeed in buying petrol from the garage only if they intend to do so and the garage is open. In the analysis that follows, we attempt to explain some of the assumptions that underlie the way that the TRA and the TPB are usually tested in nonexperimental studies. We use simplified versions of the models, focusing particularly on the attitude–intention relationship. In the next section, timeline diagrams are used to represent the relationship between attitude and intention within an individual over time.
TIMELINE ANALYSIS OF THE ATTITUDE– INTENTION RELATIONSHIP Consider the effect of attitude and subjective norm on intention. This part of the TRA/TPB is usually tested for a given target population and target behaviour by conducting a cross-sectional study in which measures of A, S, and I are obtained in a suitable sample of individuals and the relationships between these variables are analysed using correlation and regression techniques. In particular, multiple linear regression is used to estimate the independent effects of A and S on I and the percentage of variance explained in I by these two predictors. The independent effects of A and S on I are commonly reported in terms of the beta weights (standardised partial regression coefficients) and their associated significance tests (t-tests of the hypothesis that each beta weight differs from zero). Alternatively, the unique percentage of variance explained or the squared semi-partial or part correlation may be reported; note that the significance test is the same as that for the corresponding regression coefficient. We focus here on the regression weights because, as estimates of the structural (=causal) coefficients, they can be regarded as more fundamental. Note that this analysis relates differences between individuals in I to differences between individuals in A (controlling for S) and to differences between individuals in S (controlling for A). For example, a beta weight 2 from this analysis of .4 for attitude can be interpreted as meaning that, holding S constant, a difference between individuals of one standard deviation unit on the attitude scale is associated with a difference between individuals of .4 standard deviation units on the intention scale.
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However, we usually wish to draw dynamic inferences from such crosssectional analyses (Berry, 1993). To state that attitude influences intention is usually understood to imply that if we could select an individual and intervene to increase their attitude, while holding all other variables constant, their intention would also increase. Thus, we wish to use a cross-sectional between-individuals analysis to draw inferences about processes that are assumed to occur within individuals over time. Drawing dynamic causal inferences from cross-sectional analyses requires a number of strong assumptions. In order to illustrate some of these assumptions, we consider a simplified version of the TRA/TPB in which attitude (A) is the only cause of intention (I). Let us assume that the within-individual relationship between A and I is described by the following equation: I=.5A+.5, that is, that an increase of one unit in A produces an increase of .5 units in I. For the moment, we assume that this structural coefficient is unstandardised. Figure 3 shows timelines depicting the changes over time in A and I for three individuals (P1, P2, P3). A and I are shown as being measured on 7-point scales scored from 1 to 7, where the intervals are assumed to be equal and a high score means a more positive attitude or a stronger intention. The timelines in Figure 3 should be thought of as representing the ‘‘true scores’’ on attitude and intention for these three individuals. For simplicity, we assume perfect measurement. In other words, we assume that if A or I were measured for an individual at any time during the time period depicted in Figure 3, the observed score would equal the true score. [Note that the standard regression model assumes that the dependent variable (here, intention) is continuous and unbounded, that is, that it can take any numerical value. For present purposes, we will ignore problems that arise from the use of bounded scales.] Consider the period to the left of the bold vertical line, that is, the period between T0 and T1. This could represent, say, a 4-week period prior to a cross-sectional study. For all three individuals, the cross-sectional relationship between A and I is described by the equation given above. For example, at the beginning of the period, P1 has a score of 2.5 on I, which equals .5 times their score on A (4) plus .5. Similarly, at the end of the period, P1’s score on I is 3, which equals .5 times A (5) plus .5. The discontinuous portions of the timelines for P1 and P2 are meant to indicate that these individuals had pre-existing attitudes and intentions. P1’s attitude is initially stable and so is their intention—remember that we are making the simplifying assumption that A is the sole cause of I, which means that I cannot change unless A changes. After a while, P1’s attitude increases (all changes in A and I are shown as occurring abruptly), and this is followed almost instantaneously by an increase in intention. The relationship between the change in I and the change in A reflects the structural coefficient of .5.
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Figure 3. Timeline diagrams showing changes over time in attitude (A) and intention (I) for three individuals (P1, P2, P3).
An increase of 1 unit in P1’s attitude (from 4 to 5 on the 7-point scale) produces an increase of .5 units in their intention (from 2.5 to 3). In causal analysis, it is assumed that cause always precedes effect by at least some minimal time period. Expositions of the TRA and the TPB are not explicit about the causal lag between attitude and intention (or between subjective norm and intention, or perceived behavioural control and intention). However, most applications of these models implicitly assume a very brief causal lag between a change in attitude and the corresponding change in intention; indeed, as we will see, this is one rationale for using a crosssectional rather than a prospective design to investigate the relationship between the two variables. Note that the increase in I does not produce any change in A (no reciprocal causation).
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During this same time period, P2 shows a decrease in attitude, which is immediately followed by a decrease in intention. The structural coefficient is again .5: a decrease of two units in attitude produces a decrease of one unit in intention. Note the symmetry of the relationship between A and I: a decrease of a given magnitude in A has the same effect on I (but in the opposite direction) as an increase of the same size. We have also assumed that the causal lag is the same in the two cases. Now consider P3. Initially, this person does not have an attitude or an intention towards performing the behaviour in question (they have never thought about performing it). But at some point in this period they form an attitude and this is immediately followed by formation of a corresponding intention. The same structural equation (I=.5A+.5) is assumed to apply here too. Now suppose that we conduct a cross-sectional study at time T1 in which we measure A and I perfectly (no measurement error) in a sample of individuals whose timelines are consistent with the patterns and characteristics of those shown in Figure 3. (For individuals who have never previously thought about performing the behaviour, completing a questionnaire may prompt the formation of an attitude and a corresponding intention. This measurement effect does not pose any problem so long as the same equation applies.) If all the assumptions referred to above hold for all individuals in the sample, then the cross-sectional between-individuals relationship between A and I as measured at time T1 will accurately reflect the withinindividual relationship between A and I. The equation I=.5A+.5 will describe the cross-sectional between-individuals relationship between A and I as well as the within-individual relationship between these two variables. Furthermore, the relationship between differences between individuals in A and differences between individuals in I will reflect the structural coefficient of .5. For example, at time T1, P1 and P2 differ by 1 unit on A (574) and by .5 units on I (372.5). Let us examine some of the assumptions in more detail: (1) It is assumed that the same structural coefficient applies to every individual in the sample, i.e., that, for any individual in the sample, an increase in A of one unit would produce the same increase in I. This assumption is not inherent in the TRA or the TPB, which, in principle, allow different structural coefficients for different individuals from the same target population with respect to the same target behaviour. Rather, the assumption is required by the use of between-individuals cross-sectional regression analysis. Figure 4(a) shows a case where two individuals have different coefficients. For person P4, the relationship between A and I is described by the equation I=.8A+.5, whereas for person P5 the relationship is
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Figure 4. Timeline diagrams showing changes over time in attitude (A) and intention (I) for four individuals (P4, P5, P6, P7).
described by the equation I=.5A+.5. A between-individuals crosssectional analysis at T1 yields a single coefficient (in this case, 1.1), which cannot provide an accurate estimate of the two withinindividual coefficients. Within the framework of between-individuals cross-sectional regression analysis, structural coefficients can be allowed to vary for different subgroups of individuals by specifying interactions (Aiken & West, 1991; Cohen & Cohen, 1983). For example, an application of the TRA/TPB to the explanation of condom use intentions may allow men and women to have different coefficients for the attitude–intention relationship (cf. Sutton, McVey, & Glanz, 1999). However, within the standard regression model, it is still
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necessary to assume that all the men share the same coefficient and all the women share the same coefficient. If repeated measures of attitude and intention are obtained, either over time with respect to the same target behaviour or at one time point with respect to different target behaviours, then random-effects regression can be used to estimate different coefficients for different individuals (Hedeker, Flay, & Petraitis, 1996). In a random-effects regression analysis predicting I from A, a different coefficient for the effect of A is estimated for each individual, on the assumption that the coefficients vary randomly across individuals in the population and have a normal distribution. Thus, some individuals may show a strong positive relationship between A and I, others may show a weak positive relationship, and still others may show a near zero or even a weak negative relationship. The mean of these weights gives the ‘‘average’’ effect of A on I. The variance of these weights can be estimated, and the hypothesis that this variance is zero (i.e., that the same coefficient applies to everyone) can be tested directly. If there is significant individual variation in the regression coefficients, this variation can be modelled in terms of relevant individual-level characteristics. For example, it may be hypothesised that variation in the attitude coefficient is partly explained by variables such as gender (e.g., that women show a stronger relationship between A and I than men) or attitude strength. Random-effects regression has advantages over simply computing a correlation between attitude and intention for each individual in the sample or using standard regression to estimate a model for each individual, as has been done in a number of studies (e.g., Trafimow & Finlay, 1996). The paper by Hedeker and colleagues provides a very clear description of the method (although in their substantive example using the TRA, the measures of attitude and subjective norm departed widely from Ajzen and Fishbein’s 1980 recommendations). Random-effects regression models can be estimated using PROC MIXED in SAS or a multilevel modelling program such as MLwiN (Goldstein et al., 1998). (2) It is further assumed that the structural equation (in this example, I=.5A+.5) is stable over time and has held true throughout the history of the relationship between A and I for all individuals in the population, including the point at which the intention was formed. For some individuals (e.g., P3 in Figure 3), the history of the relationship may be brief; for others, it may extend back many years. It may be questioned whether this assumption need be so strict. Surely it is only necessary that the structural equation holds true for a relatively short period of time leading up to the cross-sectional study?
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If so, the cross-sectional analysis should still accurately reflect the recent history of the relationship between A and I. However, two problems arise from relaxing the assumption in this way. First, generalisability of the findings would be limited, and researchers would need regularly to repeat the same study in order to check that the same findings were obtained. Second, if the structural equation describing the relationship between A and I were believed or shown to be unstable over time, it would be necessary to try to explain why the structural relationship changes and why different equations hold at different time points. (3) It is assumed that the causal lag for the attitude–intention relationship is very short. Figure 4(b) shows a relatively long causal lag in which the change in I produced by a change in A does not occur until after T1, that is, until after the cross-sectional study has been conducted. This creates a mismatch between the values of A and I measured at T1. P6’s score on A is being compared with the ‘‘wrong’’ score on I. So the equation derived from a betweenindividuals cross-sectional analysis will not accurately reflect the true relationship between A and I. Where the causal lag is relatively long, a cross-sectional design is inappropriate, even if all the other assumptions hold. Instead, a prospective design should be employed in which A is measured at one time point (T1, say) and I is measured at a later time point (T2), where, ideally, the length of the follow-up period is approximately equal to the expected length of the causal lag (Finkel, 1995). If the follow-up period is shorter than the causal lag, a change in A that occurs just prior to T1 will not have produced its effect on I by T2; thus, the effect of recent changes in A will be missed at the later time point. If the follow-up period is too long, a change in A that takes place during the follow-up period may produce a change in I within the same period. In both cases, the value of A at T1 and the value of I at T2 will be mismatched. However, if the causal lag is very brief, a prospective design is not appropriate and a cross-sectional design should be employed. Thus, although it is widely believed that prospective designs allow stronger inferences to be drawn, this is the case only where the causal lag is relatively long and the follow-up period is carefully chosen so that it approximately equals the expected causal lag. In the extreme case where A (and therefore I) is extremely stable over the follow-up period (in the sense that individuals show little change over time relative to one another), it makes no difference whether a cross-sectional or a prospective design is used; both should yield similar estimates of the effect of A on I.
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As mentioned above, applications of the TRA/TPB usually implicitly assume a very brief causal lag between all the variables in the model apart from behaviour; for example, between beliefs and attitude and between attitude and intention. However, there are some exceptions. For example, Liska (1984, p. 66) suggested that ‘‘. . . as information processing takes time, changes in attitudes may lag behind changes in beliefs, perhaps in some cases by months or even years . . . ’’, and Armitage and Conner (1999) employed a time lag of 3 months. Attitude–behaviour researchers should try to specify the causal lag for each of the relationships in the TRA/TPB or at least consider the implications of different causal lags. They should also consider the possibility that different relationships may have different causal lags. For example, it is conceivable, though admittedly not very plausible, that the attitude–intention and subjective norm– intention relationships have different causal lags. Furthermore, different individuals may have different causal lags (as well as different structural coefficients) for the same relationship. (4) Another key assumption is that there is no reciprocal causation. The causal flow is assumed to be one–way, in this case from attitude to intention. Changes in intention are assumed not to produce changes in attitude. (We also have to assume that changes in behaviour—not shown in the timeline diagrams—do not produce changes in attitude or intention.) Figure 4(c) illustrates reciprocal causation between A and I for one individual (P7). The structural equation for the effect of A on I is I=.5A+.5, as in Figure 3; the structural equation for the reverse effect of I on A is A=.4I+.5. The latter effect could be interpreted in terms of a tendency towards consistency, with attitude being ‘‘brought into line’’ with the new intention. For simplicity of presentation, we assume that the causal lags are the same for the two effects. Both coefficients are positive, creating a positive feedback loop. An increase of one unit in A produces an increase of .5 units in I. This in turn produces an increase of .2 units in A [=(.4)(.5)], which in turn leads to an increase of .1 units in I [=(.5)(.2)]. This in turn produces an increase of .04 units in A [=(.4)(.1)]. This process continues indefinitely with ever smaller effects (too small to be shown in the diagram). It can be shown that, given the structural coefficients that were (arbitrarily) selected for this example, A and I will converge to the values of 5.25 and 2.625 respectively (Heise, 1975; Kenny, 1979). Assuming that these values are approximately achieved by T1, a cross-sectional analysis carried out on data obtained at this time point from a sample of individuals all of whom share the same structural equations and assuming one-way causation from A to I would estimate the structural coefficient to be .5. Thus, if the
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incorrect assumption of one-way causation is made, the crosssectional data would be interpreted as indicating that an increase in A of one unit produces an increase in I of .5 units. In fact, because of reciprocal causation, a one unit increase in A produces an increase of .625 units in I (and A itself increases by a further .25 units as a consequence). Again, it might be thought that employing a prospective design would enable each of the two effects to be accurately estimated. Measures of attitude and intention would be obtained at two time points, T1 and T2. Attitude and intention at T2 would be regressed on attitude and intention at T1, in what is known as a crosslagged regression or a cross-lagged structural equation model. Interpretation focuses on the effect of attitude at T1 on intention at T2, and the effect of intention at T1 on attitude at T2. However, as noted in the preceding discussion of causal lags, the validity of this analysis would depend on choosing the correct follow-up period(s), taking into account the possible complication that the effects may have different causal lags—not implausible in this case. Moreover, if the causal lags were very brief, a prospective design would not be appropriate. An alternative to cross-lagged regression is cross-lagged panel correlation analysis, which has been used in several applications of the TRA/TPB (e.g., Armitage & Conner, 1999; Kahle & Beatty, 1987; Wittenbraker, Gibbs, & Kahle, 1983). This technique has attracted substantial criticism from methodologists over the years, most notably by Rogosa (1980), and can no longer be recommended. Even the two researchers who originally developed it have recently admitted that ‘‘it is certainly not the causal divining rod that some (including ourselves) once thought that it might be’’ and recommend its use only when ‘‘the goal is exploratory and the expectation is that there are few, if any, causal effects’’ (Campbell & Kenny, 1999, Chapter 9, p. 154).
Standardised versus unstandardised coefficients Throughout the examples considered above, we used unstandardised coefficients, that is, coefficients expressed in terms of units on 7-point scales scored from 1 to 7. Most studies that use the TRA or the TPB report standardised coefficients or beta weights where relationships are expressed in terms of standard deviation units. The reason for preferring standardised coefficients is that the scales used to measure constructs like attitude and intention are arbitrary in the sense that a 7-point scale could be scored 1 to
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7, 0 to 6, 73 to +3, or even 10 to 70. Although Ajzen and Fishbein (1980) present clear recommendations concerning how the TRA measures should be scored, any scheme based on a linear transformation of the numbers 1 to 7 could be used in practice: correlations and standardised regression coefficients would be unaffected. (An important exception to this rule occurs when a measure is used as a component of a multiplicative composite, as in behavioural beliefs for example; see Evans, 1991, and French and Hankins, in press). The arbitrary nature of the scales creates a problem when a researcher wishes to compare two effects (e.g., the effects of attitude and subjective norm on intention). If attitude is scored 1 to 7 and subjective norm is scored 10 to 70 (to take an extreme example), it may appear that the effect of attitude is larger than the effect of subjective norm. The usual solution is to standardise the coefficients so that the effects are expressed in terms of standard deviation units. The researcher can then compare the effect of attitude (in terms of the effect on intention, in standard deviation units, of increasing attitude by one standard deviation unit) with the effect of subjective norm (in terms of the effect on intention, in standard deviation units, of increasing subjective norm by one standard deviation unit). However, it can be argued that standardised coefficients are no less arbitrary than unstandardised coefficients, particularly when one wishes to compare findings from different subsamples within the same study (e.g., men and women), to compare samples from different studies, or to combine findings across studies, as in meta-analysis. Standardised coefficients depend on the standard deviations of variables, which may differ arbitrarily from study to study or between subgroups within a single study in ways that are unrelated to the true structural relationships between variables. Even if the scales used to measure attitudes and intentions are arbitrary, if all studies (or even if most studies) used the same items, it might be preferable to use unstandardised coefficients. However, so long as authors report the standardised coefficients, the standard deviations of the measures, and how the measures were scored, it is possible to calculate the unstandardised coefficients and to rescale them so that they can be compared and combined across studies if desired.
ALLOWING MULTIPLE CAUSES OF INTENTION In the preceding analysis using timeline diagrams, we made the simplifying assumption that attitude is the sole cause of intention. We now consider some of the assumptions that are necessary when this simplifying assumption is dropped. This section of the chapter was inspired by Clogg and Haritou (1997). The presentation in this chapter differs from that employed by Clogg and Haritou in a number of ways: it is less technical and
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uses path diagrams to make the argument more accessible; it adapts the general argument to the specific case of the TRA/TPB; and it considers a number of potential solutions to the problem identified by Clogg and Haritou that were not examined by those authors. First, consider Model I in Figure 5. This shows an arrow from attitude towards the behaviour (A) to intention (I). This arrow represents the causal effect that we wish to estimate for a given target behaviour and target population. We now allow I to be directly influenced by other causes apart from A, although initially we do not specify what these additional causal factors are. The aggregate (weighted additive composite) of all other causes is represented by u, and the effect of this aggregate is represented by the small arrow pointing at I. u is often referred to as the error or disturbance term. The disturbance term can be thought of as comprising two components: a systematic component consisting of other important causes of I apart from A (e.g., subjective norm), some of which may be correlated with A; and a random component consisting of tens, hundreds, or even thousands of minor, independent, and unstable causes of I. The latter causes would be impossible to specify in practice. Although individually the effects of these ‘‘random shocks’’ are assumed to be small, in aggregate their effect may be quite large. Conceivably, the majority of the variance in intention could be explained by the random component, thus placing a severe limit on the proportion of variance that could be explained by the major causal factors. Suppose we have hypothesised that A is an important cause of I and that the causal lag is very short. In order to estimate the causal effect of A on I, we could measure A and I at the same time point, and then regress I on A using linear regression. If certain assumptions hold (including those discussed in the first section of this chapter), the standardised regression coefficient (beta weight) from this analysis can be interpreted as an unbiased estimate of the causal effect of attitude on intention. (Note that, in this simple bivariate case, the standardised regression coefficient equals the correlation coefficient.) Given that we are now allowing multiple causes of I, in order to be able to interpret the regression coefficient as an unbiased estimate of the causal effect of A on I, an additional assumption is required, namely that the correlation between A and the aggregate of all other causes of I is zero. In Figure 5, the correlation between A and u is represented by the dashed double-arrowheaded line. This assumption is necessary because the least-squares estimation procedure underlying linear regression forces the residuals (the differences between the observed and predicted values of the dependent variable) to correlate zero with the predictor variables. But is it reasonable to assume that this approximates the situation in the real world? The answer to this question depends on how the error term is constituted. If there were no
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Figure 5. Path diagrams showing three models that could be estimated by regression analysis. (A=attitude; S=subjective norm; P=perceived behavioural control; I=intention; u, v, w are the disturbance terms for I; the continuous double-arrow-headed lines represent the [known] correlations among the predictor variables; the dashed double-arrow-headed lines represent the [unknown] correlations between the predictor variables and the disturbances.)
systematic component in the error term so that it consisted only of the random component, the expected value of the correlation between A and the error term would be zero. Similarly, if the error term consisted only of the random component and major causes of I each of which were uncorrelated
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with A, then the expected value of the correlation between A and the error term would again be zero. However, if the error term included major causes of I that were correlated with A, then the expected value of the correlation between A and the error term would not in general equal zero. Unfortunately, it is not possible to distinguish between these three cases in practice. Thus the assumption that A correlates zero with the aggregate of all other causes of I is arbitrary and untestable. The true correlation could be zero. But it could also be 0.40, or 70.70, or any other value between 71.0 and +1.0—we simply have no way of knowing. If the correlation is anything other than zero, our estimate of the causal effect of A on I will be ‘‘wrong’’ (biased) to an unknown extent. Now suppose we measure subjective norm (S) and include it in the regression model; in other words, we regress I on A and S (see Model II in Figure 5). In order to interpret the standardised partial regression coefficients from this analysis as unbiased estimates of the causal effects of A and S on I, we have to assume, among other things, that both A and S are correlated zero with the aggregate of all other causes of I; in other words, we now have to make two arbitrary and untestable assumptions. The aggregate variable in Model II is represented by v; it differs from u in Model I because we have removed S from the error term and made it one of the predictors. Note that, although Model II would be recognised by all attitude–behaviour researchers as the TRA (or, at least, part of it), Model I is not incompatible with the TRA. The difference between the two models is simply that, in Model I, S is unspecified and part of the error term, whereas, in Model II, it is explicitly identified as a variable that influences I. So if we choose to estimate Model I, we are not necessarily implying that we believe that subjective norm does not influence intention; rather we may have made a deliberate decision to leave subjective norm as part of the error term instead of specifying it as a predictor. If we expand the model by including a third predictor (P, which stands for perceived behavioural control), as in Model III, we have to make three arbitrary and untestable assumptions. Every time another predictor is added to the model, the number of such assumptions increases. The fact that drawing causal inferences from nonexperimental data rests on arbitrary and untestable assumptions involving unmeasured variables has very serious implications. It means that there is no basis for deciding which variables to include in a regression model and which to leave out, and that there is no basis for choosing between different models. In order to explain these implications, suppose that the true model is that represented by the path diagram in Figure 6(a). All relationships are assumed to be linear and additive, and all variables are assumed to be standardised. Two causes of I are specified (A and S); the correlation between them is a. v is a hypothetical variable representing the aggregate
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Figure 6. Path diagrams showing three alternative representations of a true causal model. (A=attitude; S=subjective norm; I=intention; u and v are the disturbance terms for I; a, e, f, h are correlation coefficients; the other coefficients are path coefficients; the numbers in parentheses represent the three different examples discussed in the text.)
of all other causes of I apart from A and S; it includes both random and systematic components. The correlations between v and the two specified causes, A and S, are represented by e and f respectively. Note that this
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diagram is not incompatible with the TPB or with extensions to the TPB; perceived behavioural control and other major determinants of intention can be thought of as unspecified components of (the systematic part of) the aggregate variable v. Figure 6(b) is an alternative representation of the true model in which S has been absorbed into the error term—symbolised by u in order to distinguish it from v in Figure 6(a). The correlation between A and u is represented by h. Figure 6(c) is yet another alternative representation of the true model. It shows the relationship between the two error terms u and v and thus how the diagram in Figure 6(b) can be obtained from the diagram in Figure 6(a). Specifically, u is a weighted additive composite of S and v: u=iS+jv. Note that u is completely determined by S and v. The causal effect of S on I in Figure 6(a) is decomposed in Figure 6(c) into an indirect effect consisting of a path from S to u and a path from u to I. By the rules of path analysis (Heise, 1975; Kenny, 1979), c ¼ ig
ð1Þ
Similarly, the causal effect of v on I in Figure 6(a) is decomposed in Figure 6(c) into an indirect effect comprising a path from v to u and a path from u to I: d ¼ jg
ð2Þ
The variance of u is given by the following equation: VarðuÞ ¼ i2 þ j2 þ 2ijf
ð3Þ
Because u is standardised, as are all the other variables in the model, this expression equals 1. The correlation between A and u, represented by h in Figure 6(b), is given by the following equation: rðA; uÞ ¼ ej þ ai
ð4Þ
which can be derived from Figure 6(c) using the rules of path analysis. Given numerical values for the coefficients in Figure 6(a), Equations 1–4 can be used to calculate h and g in Figure 6(b). The important point for present purposes is that Figure 6(a) and Figure 6(b) are two alternative representations of the same true model that differ in that in Figure 6(b) S is part of the error term, whereas in
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Figure 6(a) it has been removed from the error term and specified as a cause of I. In order to limit the number of possible cases for discussion, we will assume that none of the coefficients a, b, c, d in Figure 6 equals zero and that a does not equal 1 or 71. Suppose that we obtain perfect measures of A, S, and I in the population (so that we can ignore the problems arising from measurement error and of estimating population values from sample statistics). Suppose that we start by regressing I on A alone. If the correlation h in Figure 6(b) happens to equal zero, we will obtain an unbiased estimate of the true causal effect b of A on I. This is the case even though we have omitted S, a true cause of I, from the regression model and even though including S in the regression model would increase the percentage of variance explained in I. If the correlation h does not equal zero, the beta coefficient will be a biased estimate of the causal effect of A on I. In fact, the coefficient will equal b+gh [see Figure 6(b)]; thus the amount of bias is equal to +gh. Of course, in practice there is no way of telling whether h is zero or not, or how close to zero it is. The assumption that h=0 is an assumption of necessity: unless we make this arbitrary assumption, we cannot interpret the beta coefficient from the regression of I on A as an unbiased estimate of the causal effect of A on I. Now suppose we regress I on A and S. If the correlations e and f in Figure 6(a) both happen to equal zero, the beta coefficients obtained from this regression analysis will be unbiased estimates of the true causal effects of A and S on I, i.e., of b and c in Figure 6(a). The coefficients shown in the first set of parentheses in the diagrams in Figure 6 provide an example. A and S are assumed to be correlated 0.60. The true causal effects of A and S on I are 0.40 and 0.20 respectively. Because the correlations e and f are both zero, regressing I on A and S yields unbiased estimates of these causal effects. Thirty percent of the variance in I is explained by these two predictors. This example shows that unbiased estimates of causal effects can be obtained even if the regression model does not explain a large proportion of variance in the criterion. If either or both of the correlations e and f do not equal zero, the beta coefficients obtained from regressing I on A and S will not in general be unbiased estimates of the true causal effects of A and S on I. [In fact, it can be shown that the coefficient for A will equal b+(d(e7af)/(17a2)), that is, the amount of bias equals +(d(e7af)/(17a2)); and that the coefficient for S will equal c+(d(f7ae)/(1-a2)), that is, the bias equals +(d(f7ae)/(17a2)).] We have considered two different sets of assumptions: h=0, and e,f=0. It can be shown that these assumptions are not independent. Specifically, if h=0 then e and f cannot both equal zero. This means that if h=0 and we regress I on A alone, we will obtain an unbiased estimate of the effect of A
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on I, but if we also include S in the regression model, the estimates of the effects of A and S will be biased. This is known as included variable bias: including S, a true cause of I, in the regression model leads to biased estimates of the effects of A and S; excluding it yields an unbiased estimate of the effect of A. The reverse is also true: If e and f both equal zero, h cannot equal zero. Thus if e,f=0 and we regress I on A and S, we will obtain unbiased estimates of both coefficients, but if we omit S from the regression model, we will obtain a biased estimate of the effect of A. This is known as excluded variable bias: excluding S, a true cause of I, from the regression model yields a biased estimate. The assumptions we have been considering (h=0; e,f=0) are special cases. In general, we would expect neither set of assumptions to be satisfied, in which case both analyses (regressing I on A alone, and regressing I on A and S) will yield biased estimates. The coefficients shown in the second set of parentheses in the diagrams in Figure 6 provide an example. Here e=0.20, f=0.30 [Figure 6(a) and Figure 6(c)], and h=0.36 [Figure 6(b)]. The true causal effects of A and S on I are 0.40 and 0.20 respectively. Regressing I on A alone yields a biased estimate of the effect of A (0.68 instead of 0.40). Regressing I on A and S also yields biased estimates (0.39 for A and 0.42 for S). We would conclude from the latter analysis that the causal effects of A and S on I are approximately equal, whereas, in the true model, the causal effect of A is twice as large as the causal effect of S. Note that, in this example, bias sufficient to lead to an erroneous conclusion is generated by only medium-sized correlations between A and v and S and v [Figure 6(a)]. The regression model that includes both A and S has greater predictive power than the model that includes A alone (or, indeed, than the model that includes S alone). The proportions of variance in I explained by A alone, S alone, and A and S together are 0.46, 0.48, and 0.55 respectively. However, although it has better predictive power, the regression model that includes A and S yields biased estimates because the required assumptions (e,f=0) are not met. We now consider a more extreme example in which close to 100% of the variance is explained in I by a regression model that includes both A and S but where the estimates of the causal effects of these variables are seriously biased. Examine the coefficients in the third set of parentheses in the diagrams in Figure 6. In this example, e=0.80, f=0.50, and h=0.51, so, as in the second example, neither set of assumptions holds. The true causal effects of A and S on I are 0.20 and 0.52 respectively. Regressing I on A alone yields a biased estimate of the effect of A (0.65 instead of 0.20). Regressing I on A and S also yields biased estimates (0.58 for A and 0.73 for S). This regression model explains 96% of the variance in I, which is 53
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percentage points greater than is explained by A alone and 33 percentage points greater than is explained by S alone. This example is a stark illustration of the general point that the validity of a regression model depends on the validity of its assumptions, not on its predictive power. A common strategy among researchers who use the TRA/ TPB is to try to identify variables that add significantly and substantially to the proportion of variance explained in intention or behaviour. However, the arguments and examples presented above show that this emphasis on variance explained is misplaced. If the aim is to obtain unbiased estimates of causal effects, predictive power is not an appropriate criterion for preferring one regression model to another. Although it is often said that the decision concerning which variables to include in a regression model should be guided by theory, the above arguments demonstrate that theory provides no guidance at all. The TPB, for instance, postulates that A, S, and P (perceived behavioural control) are important causes of I. A researcher investigating this theory would naturally measure A, S, P, and I and would include A, S, and P as predictors in the regression model. But, as we have shown, even if the theory is actually correct, this analysis may yield biased estimates of the effects of the three putative determinants of I, and, furthermore, leaving P (or P and S) out of the analysis may yield an unbiased estimate of A. Thus, in this context, theory does no more than identify the variables for which causal effects need to be estimated. It offers no help in deciding whether to include all of them or only a subset of them in a regression analysis. All the above arguments apply equally to prospective nonexperimental designs. For example, suppose we wish to estimate the causal effect of attitude (A) on behaviour (B). Even if we correctly specify the causal lag, we still have to assume that A correlates zero with the aggregate of all other causes of B, which, as we have argued, is an arbitrary and untestable assumption. Thus, the problem cannot be solved by employing a prospective design. It might be thought that if a number of studies were conducted using the TRA or the TPB and if the results were combined using meta-analysis, any biases would tend to cancel out. Unfortunately, this is not likely to be the case. For example, suppose again that the true model for a particular behaviour and target population is that shown in Figure 6 and that e and f do not both equal zero. Suppose that a number of studies using identical measures of A, S, and I are conducted on different samples drawn from the target population, and that I is regressed on A and S in each study. The findings will vary due to sampling variability, but the estimates of the causal effects of A and S on I will be biased on average across studies; hence, a meta-analysis will also yield biased estimates.
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We now consider four potential solutions to the problem of omitted variables before outlining the advantages of randomised experimental designs.
1. Mauro’s method The correlation between any two variables (r(1,2)) is constrained by their correlations with a third variable (r(1,3) and r(2,3)). Specifically, the mathematically possible upper and lower limits for r(1,2) are given by the following expression (see Cohen & Cohen, 1983, p.280):
rð1; 3Þrð2; 3Þ
qffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffi ½ð1 r2 ð1; 3ÞÞð1 r2 ð2; 3ÞÞ
(This constraint was used in constructing the second and third examples presented earlier to ensure that in each case the true model was mathematically possible.) Mauro (1990) used this constraint as the first step of a method for estimating the effects of omitted variables. Consider the simplest possible case in which we wish to estimate the effect of attitude (A) on intention (I). We measure A and I and compute the correlation between them, which is 0.30 say. This is also the value of the beta weight. From this analysis, we may provisionally conclude that A has a substantial positive effect on I. However, we may have omitted a variable X that is an important cause of I. Mauro shows that for any value of the correlation between A and X, it is possible to determine (i) the range of values of the correlation between X and the criterion (I) that are mathematically possible (using the expression given above), and (ii) the size of this correlation that would be required for the omitted variable to reduce the effect attributed to A to nonsignificance or to reverse its sign. To apply Mauro’s method, we would first make an assumption about the size of the correlation between A and X (e.g., that it is positive and lies between 0.10 and 0.50). We would then calculate the range of values of the correlation between X and I that were mathematically possible given this assumption and given the observed correlation between A and I. In this simple example, the range of possible values is very wide (between 70.92 and +0.98). We may wish to rule out some of these values as implausible. For example, we might want to assume that the correlation takes only positive values. The final step is to examine the implications of particular values of this correlation. For example, suppose r(X,I)=0.50 and r(X,A)=0.10. Under these assumptions, it can be shown that, controlling for X, the beta weight
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for A would be reduced only slightly from 0.30 to 0.25. Now suppose r(X,I)=0.50 and r(X,A)=0.50. The beta weight for A would be further reduced to 0.07, which may be sufficient to change the initial conclusion that A has a substantial positive effect on I. If r(X,I) were as high as 0.80, then if r(X,A)=0.50, the beta weight for A would equal 70.13, which is of opposite sign to the original value. This is an example of suppression (Cohen & Cohen, 1983, pp.94–96). A value of 0.80 for r(X,I) may or may not be regarded as plausible. Mauro’s method is a useful technique for conducting sensitivity analyses (‘‘what if’’ this correlation had this value?), but for the following reasons it cannot be regarded as providing a general solution to the problems raised in the second part of this chapter: (1) Although the method can be extended to the case of multiple predictors, it is limited to exploring the effects of a single omitted variable. (2) It requires assumptions to be made about the correlations between the omitted variable and the predictors in order to investigate the consequences for the correlation between the omitted variable and the criterion. (3) These assumptions may be difficult to make (although in some cases estimates of the relevant correlations may be available from other studies). (4) It abandons the aim of obtaining accurate estimates of causal effects and replaces it with the weaker aim of determining whether or not a given predictor variable has a positive or negative causal effect on the criterion. (5) It makes the implicit assumption that a regression model in which the omitted variable were included would yield unbiased estimates; in other words, it assumes that the predictor variables in this model would correlate zero with the aggregate of all other causes of the criterion variable.
2. Instrumental variables Another potential solution is to use instrumental variables (Heise, 1975, pp.160–185; Kenny, 1979, pp.93–95). Suppose we want to estimate the effect of A on I but we suspect that A is correlated with the disturbance of I. Figure 7 shows an additional variable Z, which: (i) has a direct influence on A; (ii) does not have a direct influence on I; and (iii) is not correlated with the disturbance of I (represented by v in this diagram). Z serves as an instrument for A in the A?I relationship. The effect of Z on A is represented by a, the effect of A on I by b. Since r(Z,I)=ab and r(Z,A)=a, an estimate of b can be obtained very simply from r(Z,I)/r(Z,A). More generally, estimates of effects in instrumental variable models can be obtained by means of two-stage least-squares (2SLS). Applied to this simple example, 2SLS would involve first regressing A on Z, saving the predicted values of A, and then regressing I on these predicted values. Because by assumption Z is uncorrelated with the disturbance of I, the
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Figure 7. Path diagram showing an instrumental variable model in which Z serves as an instrument for attitude (A) in its relationship with intention (I). a and b are path coefficients. u and v are the disturbance terms for A and I. The dashed double-arrowheaded line represents the (unknown) correlation between the disturbances.
predicted values of A will also have this property. Thus the variable consisting of the predicted values of A can be thought of as a ‘‘purified’’ version of A. Two-stage least-squares is implemented in widely used statistical packages including SPSS and STATA. The estimates of causal effects obtained by this method are consistent, that is, they may be biased in small samples, but converge on the true value as the sample size increases. Alternatively, models can be estimated by maximum likelihood in specialist structural equation modelling packages; again, relatively large samples are recommended. As well as satisfying the conditions outlined above, an instrument should ideally have a high correlation with its target variable (A in this example); this increases the precision of the estimates. More than one instrument may be used in order to maximise the prediction of the target variable. The main problem with this method is the difficulty of identifying suitable instruments. Variables such as gender may be used, on the argument that variables whose values are fixed are less likely to be correlated with the disturbance term than those that change over time, but they may correlate only weakly with the target variable. Another possibility is to use a lagged version of the target variable. Thus, if A and I were measured at time T, an earlier measure of A, assessed at time T-1, would probably be highly correlated with the later measure and could be used as an instrument if it could be assumed: (i) that it did not influence I at time T directly (but only via A at time T); and (ii) that it was not correlated with unmeasured causes of I at time T.
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3. Clogg and Haritou’s method Clogg and Haritou (1997) propose an entirely different approach. Suppose again that we want to estimate the causal effect of A on I. Other variables in addition to A may influence I directly; for example, subjective norm (S), perceived behavioural control (P), anticipated regret, and moral norm. If we obtained measures of all these variables on the same sample, there would be 16 (i.e., 24) possible regression models that could be estimated in which I was the dependent variable and A was included as a predictor: A as the sole predictor; A and S as predictors; A and P as predictors; A, S, and P as predictors; and so on. In general, if there are k possible predictors in addition to A, there will be 2k different regression models and hence the same number of different estimates of the partial regression coefficient for A. Thus in our example we would have 16 different estimates of the causal effect of A on I. According to Clogg and Haritou, there is no basis for choosing one of these estimates in preference to any other, because we don’t know for which, if any, of the 16 regression models the required assumptions are satisfied, and the percentage of variance explained is not a relevant criterion for model selection. Their suggested solution is to compute the mean of the 16 coefficients and treat this as a point estimate of the true population effect, and to place a confidence interval around this estimate to convey the degree of uncertainty attached to it. There are two sources of uncertainty: that due to sampling variability (reflected in the standard errors of the regression coefficients) and that due to the variability in the estimate of the A?I effect across the 16 different models (which can be measured by the variance of the estimates around the mean). They suggest computing an estimate of the standard deviation as the square root of the sum of the average squared standard error of the coefficients and the between-coefficients variance, and then using plus or minus two standard deviations to compute the 95% confidence limits around the mean coefficient. The result is an interval estimate that reflects both sampling variance and uncertainty in model selection. Clogg and Haritou’s method is simple enough to implement, but, as the number of predictors increases, the number of different regression models increases rapidly (with 10 predictors, there are 1024 different models), and it would require major changes in how the data from TRA/TPB studies were analysed and how the results were reported.
4. Abandon causal inferences A more radical response to the omitted variables problem is to abandon the attempt to draw causal inferences and to focus instead on prediction. This suggestion is not meant to be taken entirely seriously, but it provides an
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instructive contrast to causal analysis. Prediction may have huge practical value, particularly when the outcome is behaviour, rather than simply intention, and when the time interval allows interventions to be applied. For example, it would be extremely useful to know which criminals are most likely to re-offend when released from prison. Those considered to be at high risk could then be offered a special rehabilitation programme or released only under certain parole conditions. If the aim is prediction rather than explanation, the strong assumptions required for drawing causal inferences can be dropped. For example, the predictor variables do not have to be theoretical determinants of the target behaviour. Any predictor that works can be included in the regression model. Past behaviour, for instance, may be a particularly good predictor of future behaviour, even though its theoretical status as a determinant of future behaviour is contentious (Sutton, 1994). Similarly, it does not matter if relevant causal variables are omitted from the model. Furthermore, when the aim is prediction, emphasis on the overall predictive power of the model, as measured by the percentage of variance explained, is entirely appropriate.
EXPERIMENTAL DESIGNS The need to make the arbitrary and untestable assumptions discussed in the preceding section can in principle be avoided by the use of randomised experimental designs. For instance, suppose the aim is to investigate the causal effect of attitude on intention. Attitude towards a particular behaviour could be experimentally manipulated in a between-individuals design by randomly assigning participants to ‘‘high’’ or ‘‘low’’ attitude conditions. Assuming a very brief causal lag, intention would be measured within a few minutes of delivering the manipulation. Randomisation guarantees that all variables, apart from those that are influenced by the experimental manipulation, will correlate zero with the experimental manipulation—not necessarily within a single study (unless the sample size is extremely large), but on average in the long run, over a series of similar experiments. Thus, across a series of similar studies, use of the randomised experimental design will yield an unbiased estimate of the causal effect of the experimental manipulation on intention. According to the TRA/TPB, attitude towards the behaviour cannot be directly manipulated: changes in attitude are assumed to follow from changes in salient beliefs about the consequences of the target behaviour. Thus, an experimental study may attempt to manipulate attitude by presenting information about the possible consequences. This is expected to produce a change in attitude, and a measure of attitude may be included as a manipulation check. The effect of the manipulation on the manipulation check will also be estimated without bias over a series of similar
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experiments. Other variables may be measured in order to check that the experimental manipulation does not influence factors that it was not designed to influence (e.g., subjective norm). If, over a series of studies, the manipulation influences both the manipulation check and the main dependent variable (intention in this example) but does not influence other putative determinants of intention, then this could be interpreted as providing support for the theory. Of course, this pattern of findings does not show that the effect of the manipulation on intention is mediated entirely by attitude, as the TRA/ TPB would predict. Mediation analysis (Baron & Kenny, 1986) can be employed to test this hypothesis, although investigators should be aware that this procedure requires assumptions similar to those that have been considered in the present chapter (e.g., that causation is unidirectional, from attitude to intention, and that the disturbance terms for attitude and intention are uncorrelated). Furthermore, use of the randomised experimental design brings a new set of problems, for example the possibility of demand effects. It is not within the scope of the present chapter to discuss all the limitations and assumptions of randomised experiments. The main point we wish to make here is that the randomised experimental design provides the best solution to the problems arising from omitted variables, and researchers in this field should make much more use of it. Indeed, it is remarkable how few studies to date have used this approach to test predictions from the TRA/TPB. The study by McCarty (1981) provides a rare example. Using messages about contraceptive use, he attempted to manipulate the attitudinal and normative components of the TRA orthogonally. Unfortunately, the manipulation was not effective; it had no differential effects on measures of attitude and subjective norm, and there was no significant effect on intention. Although this particular study was not successful in this respect, more studies of this kind are needed, using large samples, proper randomisation, and careful development and pretesting of messages.
SUMMARY AND CONCLUSIONS This chapter has provided a detailed causal analysis of the TRA and the TPB. These theories were treated as causal models (although it was noted that the direct path from perceived behavioural control to behaviour in the TPB is causally ambiguous). They are usually tested in nonexperimental studies. Unfortunately, whether derived from cross-sectional or prospective designs, such data allow only weak conditional causal inferences to be drawn. A number of strong assumptions need to be made, including assumptions about the length of the causal interval, the stability of the
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structural equation over time, the invariance of the equation across individuals, and the direction of causation. Although it is widely believed that prospective designs allow stronger inferences to be drawn than crosssectional designs, this is not necessarily the case. If the causal lag is very short, a prospective design may not be appropriate. Attitude–behaviour researchers should carefully consider the degree of fit between the assumptions that underlie the TRA/TPB and those implied by the use of regression analysis applied to cross-sectional or prospective data. For example, they should try to specify the causal lag for each of the relationships in the TRA/TPB and select a research design accordingly. They should also consider how violations of the assumptions may affect the conclusions that are drawn. With nonexperimental data, it is also necessary to assume that each of the predictor variables is uncorrelated with the aggregate of omitted direct causes of the dependent variable (intention in our example). This assumption has serious implications for deciding which variables to include in a regression model and for choosing between different models. If the aim is to obtain unbiased estimates of causal effects, the percentage of variance explained is not an appropriate criterion for model selection. A regression model that explains a large amount of variance may yield seriously biased estimates. Conversely, a model that explains only a small amount of variance may nevertheless yield unbiased estimates. On the other hand, if the aim is prediction rather than explanation, an emphasis on predictive power is entirely appropriate. Attitude–behaviour researchers who use nonexperimental designs to estimate causal effects should therefore be extremely cautious in interpreting their findings. The same caution should be applied to the interpretation of meta-analyses that integrate the findings from nonexperimental studies. Several potential solutions to the problems arising from omitted causes were described. Mauro’s (1990) method for estimating the effects of omitted variables is a useful technique for exploring the consequences of different patterns of correlations among included and omitted variables. It requires additional assumptions to be made, but in some cases data that inform these assumptions may be available from other studies. The instrumental variables approach also requires extra assumptions. The main problem with this method is identifying variables that satisfy these assumptions. However, the method may be useful in some situations when suitable instruments can be found. The technique proposed by Clogg and Haritou (1997) does not solve the problems arising from omitted causes, but it does provide a way of quantifying the uncertainty due to model selection. Although each of these approaches has its uses, the best general solution to the problems arising from omitted causes is to employ randomised experimental designs wherever possible. It is hoped that this chapter will
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encourage attitude–behaviour researchers to focus their efforts and resources on testing the TRA and the TPB in experimental studies. Manuscript received ???? Manuscript accepted ????
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