Canadian Journal of Experimental Psychology 2009, Vol. 63, No. 1, 59 –73
© 2009 Canadian Psychological Association 1196-1961/09/$12.00 DOI: 10.1037/a0013403
Just Tell Me What to Do: Bringing Back Experimenter Control in Active Contingency Tasks With the Command-Performance Procedure and Finding Cue Density Effects Along the Way Samuel D. Hannah and Jennifer L. Beneteau McMaster University Active contingency tasks, such as those used to explore judgments of control, suffer from variability in the actual values of critical variables. The authors debut a new, easily implemented procedure that restores control over these variables to the experimenter simply by telling participants when to respond, and when to withhold responding. This command-performance procedure not only restores control over critical variables such actual contingency, it also allows response frequency to be manipulated independently of contingency or outcome frequency. This yields the first demonstration, to our knowledge, of the equivalent of a cue density effect in an active contingency task. Judgments of control are biased by response frequency outcome frequency, just as they are also biased by outcome frequency. Keywords: judgment of control, decision-making, cue density effect, contingency
1983, “1O” conditions). Important to note, response scheduling is left open to the participant. Not only are they free to decide when to respond, but also how often. This poses problems for the experimenter’s attempts to maintaining control over key variables, especially over the actual response-outcome contingency. The response-outcome contingency is usually measured with the statistic ⌬P (Allan, 1980), which ranges from ⫺1 to ⫹ 1. The ⌬P statistic is the difference between the probability of the outcome given that a response was generated (O兩R) and the probability of an outcome given that a response was withheld (O兩⬃R).
The ability to judge the degree of the contingency between our actions and what follows is crucial to many everyday activities. To determine whether we are mastering a new skill—a squash stroke, or the use of a new word processing programme—we need to be able to assess whether our actions are likely to be followed by the desired outcome. Active contingency judgments are also the basis of perceptions of self-control, and in this form take on even greater consequence. A number of researchers have argued that perceptions of control are linked to depression. For example, Alloy and Abramson (1979) famously suggested that depressed people were more accurate at assessing their control, which Alloy and Abramson called “depressive realism,” and that depression may involve the loss of self-protective “illusions of control.” Unfortunately, active contingency tasks are vulnerable to a confound arising from the incomplete control researchers have over these tasks (Hannah et al., 2007). Under conventional procedures, which we call open-performance procedures, a participant is given some binary response option—a button or switch that can be pressed or left unpressed (e.g., Alloy & Abramson, 1979), or a joystick that can be moved or not (e.g., Allan & Jenkins, 1983, “1R” conditions)—and some outcome occurs or does not—a light turns on or remains off (e.g., Alloy & Abramson, 1979), or a dot on the screen moves or remains stationary (e.g., Allan & Jenkins,
⌬P ⫽ 共O兩R兲 ⫺ 共O兩⬃R兲
(1)
Hannah et al. (2007) demonstrated that both the actual ⌬P experienced by the participant and the actual relative frequency of a positive outcome, or P(O), are influenced by the relative frequency of the participant’s responses, or P(R). P(O) ⫽ ⌬Pⴱ P(R) ⫹ (O兩⬃R)
(2)
Equation 2 implies that the experimenter shares control of ⌬P and P(O) with the participant. In this article, we will call these three variables—P(O), P(R) and ⌬P—environmental variables, because they define the experimental environment for a participant in any given block. Another implication of Equation 2 is that participants producing different levels of responding can be operating in different experimental environments when the experimenter expects them to be in the same environment. Furthermore, any attempt to untangle the processing underlying active contingency judgments risks having the manipulations themselves affect P(R), and therefore change ⌬P, or P(O), or both, from what the experimenter intends. Hannah et al. (2007) also presented a computer simulation showing that although the two most commonly used algorithms to schedule outcomes usually produce reasonable control over actual ⌬P and actual P(O), this control breaks down when P(R) is .7 or greater, or .3 or less. Even when P(R) averages to .5 across participants, however,
Samuel D. Hannah and Jennifer Beneteau, Department of Psychology, Neuroscience and Behaviour, McMaster University, Ontario, Canada. Funding for Samuel D. Hannah was provided by research grants from the National Science and Engineering Research Council of Canada to Lorraine G. Allan and Shepard Siegel. We thank Peter Graf, Helena Matute, and several anonymous reviewers for useful comments made on an earlier version of the article, and to Lorraine Allan for constant encouragement and frequent feedback. Correspondence concerning this article should be addressed to Samuel D. Hannah, Department of Psychology, Neuroscience and Behaviour, McMaster University, Hamilton, ON L8S 4K1, Canada. E-mail:
[email protected] 59
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control over ⌬P and P(O) is variable enough that for any given sample the actual values of ⌬P and P(O) can depart substantially from what was programmed. This variability within a given level of P(R) arises because the actual outcomes reflect not only the level of P(R), but also the match between the distribution of responses and the distribution of programmed outcomes given a response and given no response. The variability in environmental variables complicates demonstrations that participants’ judgments are tracking, or not tracking, objective ⌬P. It also complicates interpretations related to the biasing of perceived control or action-outcome contingency by P(O). This outcome density effect is a robust finding in observational contingencybased judgments (judging the degree of contingency or of causal relation between two external events, e.g., Allan, Siegel, & Tangen, 2005; White, 2003). It is somewhat less robust in studies of active contingency-based judgments (judging the degree of contingency between or of influence of one’s actions on an observed outcome, e.g., Shanks, 1985). Alloy and Abramson’s (1979) finding of depressive realism, for example, hinges upon the absence of an outcome density effect amongst depressed participants, at least when ⌬P is zero. However, this is a finding that has itself proven mercurial (see Allan, Siegel, & Hannah, 2007, for a recent review). Actual values for P(O) and ⌬P depend not only on their programmed values and the relations between themselves and P(R) outlined in Equation 2. They also depend on the distribution of responses across a block. In programming an active contingency study, a researcher sets up two probability spaces— one based on the probability of an outcome given a response (O兩R), and another based on the probability of an outcome given no response (O兩⬃R). Even given the same probability space and the same overall level of responding, these probability spaces can be sampled by different participants in very different ways, leading to very different values of ⌬P and P(O). To illustrate how the distribution of responses in relation to the distribution of programmed outcomes can influence environmental variables, consider the following imaginary experiment. For all participants, both P(O兩R) and P(O兩⬃R) are .5, so that P(O) equals .5 and ⌬P equals zero. To control the display of events in the experiment generator software, they follow the common technique of setting up two vectors, one (R vector) scheduling events following a participant’s response (outcome, no outcome) on a given trial, and the other (⬃R vector) scheduling events when a participant does not make a response. To control P(O) and ⌬P, the number of outcomes scheduled for the R vector is based on the target P(O兩R), and the number of outcomes scheduled for the ⬃R vector is based on the target P(O兩⬃R). Because the experimenters do not know how often or when a participant will respond, the number of elements in the vector must equal the total number of trials in a block. Both the R and ⬃R vectors thus contain five outcome and five no-outcome events. Figure 1 illustrates the response schedules for two participants, Participant A (left panel) and Participant B (right panel). To illustrate the impact response distribution can have on environmental variables with maximal clarity, we treat the R and ⬃R vectors as being randomised in a way that produces blocks of outcome and no-outcome events for both participants. The left panel of Figure 1 shows Participant A responding (middle column) on the first five trials, and withholding responses on the last five trials, for a P(R) of .5. The right panel of Figure 1 shows Participant B making responses only on the last five trials, for a P(R) of .5 as well. For both participants, however, the first
Figure 1. Schematic of response distribution across a block of trials for two participants (A and B) in a hypothetical active contingency experiment. The middle column of each panel represents each participant’s patterns of emitting a response (“R”) or withholding a response (“⬃R”). The flanking columns represent the programmed pattern of outcome events (“O”) or null outcome events (“⬃O”) contingent upon a response being emitted (left column) or withheld (right column). Although both hypothetical participants have an identical P(R) of .5, ⌬P varies from ⫹ 1.0 to ⫺1.0.
five trials in the R vector are scheduled for outcomes, and no outcomes are scheduled for the last five trials of the ⬃R vector. Whenever A responds, therefore, an outcome occurs, and whenever B responds, no outcome occurs, and the opposite happens on ⬃R trials. Despite identical levels of P(R), Participant A experiences a response-outcome ⌬P of ⫹ 1.0, whilst Participant B experiences a response-outcome ⌬P of ⫺1.0. Although P(O) is kept constant in this example, it too can be changed from what was programmed by response distributions; for example, if the block of outcome and no-outcome events given no-response (events in the right-hand column of each panel) were reversed for either participant, this would lead to a P(O) of 1.0 for that participant.1 Hannah et al. (2007) suggested a simple procedural change to the active contingency task that offers the possibility of holding P(R) nearly fixed at any level the researcher desired: Experimenters could simply tell participants when to respond. In programming the study, the researcher sets up a vector of four events—R & O, ⬃R & O, R & ⬃O, ⬃R & ⬃O— defining each trial in a block, as well as controlling 1 What is true for active contingency-based tasks, such as judgments control, using a discrete-trial format also holds for free-operant versions of these tasks. As Wasserman, Chatlosh, and Neunaber (1983) describe, “with free operants, no trials are discriminably arranged and responses may be repeatedly performed at any time” (p. 408). Because participants can respond freely across a time period that is not divided into explicit trials, calculation of actual ⌬P is difficult. Wasserman and Neunaber (1983) divided responding in their 1-min problems into 60 1-s bins. If at least one response occurred during a given bin, then the outcome occurred with a probability equal to the nominal P(O兩R); if no response occurred, then an outcome occurred with a probability equal to the nominal P(O兩⬃R). If people make multiple responses within a given 1-s sample bin, these are treated as a single response, while someone who perceives themselves as responding every three seconds will have the three seconds between taps treated as indicating two null-response bins. Because of this well-known difficulty in determining contingency in the free-operant procedure, it has been rarely used in the last decade.
COMMAND PERFORMANCE
the presentation of response and no-response prompts and outcomes. When told to make a response, the participant must make a response to advance the experiment. Responding during a ⬃R & O or a ⬃R & ⬃O trial turns it into an R & O or ⬃R & ⬃O trial, altering ⌬P slightly from what was intended, but leaving P(O) constant. By recording noncompliant responses, actual ⌬P can be easily calculated, and participants whose noncompliance exceeds some criterion can be identified and dropped from analysis. For all studies in this article, for example, we deemed as noncompliant those participants who responded on more than 10% of no-response trials, on at least half the blocks, and we excluded their ratings data from analysis. A second limit on leaving a response schedule open to the participant’s decision-making is that it confines investigation of the impact of response frequency, or, more generally, cue density, to purely correlational studies.2 Matute (1996) reported that groups with higher levels of mean P(R) had higher mean ratings of control and individual levels of P(R) were correlated with higher levels of perceived control across groups, even though for all participants the programmed ⌬P was zero, and programmed P(O) was .5. Matute concluded that P(R) influenced judgments of control. This influence could have arisen because changes in P(R) changed the actual ⌬P that people experienced without influencing decision-making directly. However, this influence could also have resulted from P(R) directly biasing some decision-making process, as has been claimed for inputs in observational tasks (Perales & Shanks, 2007). Understanding whether judgments of control are open to cue density effects, as posited for observational tasks (Perales & Shanks, 2007), could tell us the extent to which these tasks share common mechanisms, whether there is some general purpose contingencysensitive learning mechanism at work in all contingency-dependent judgments. Furthermore, a clear demonstration of a cue density effect that is not confounded with changes in outcome density would itself be a useful contribution given the ambiguity that surrounds many apparent cue density findings in observational tasks. The main goal of this article is to demonstrate that the command-performance procedure is a superior procedure over open-performance procedures. We will show that the commandperformance procedure substantially reduces variability in environmental variables, and that it allows for otherwise typical responding, producing reliable discrimination between levels of actual ⌬P and an outcome density effect. We will then proceed to implement a cue density manipulation whilst holding outcome density and ⌬P constant.
Experiment 1A: Initial Comparison of Open and Command Performance Procedures Hannah et al. (2007) noted it was an empirical matter as to whether such a command-performance procedure would produce data typical of the conventional open-performance procedure. For example, it might be that perceptions of control are dampened when actions are initiated at the instructions of another, attenuating a sense of volition that is critical for judging control. On the other hand, even though telling participants to make or withhold a response takes away their scheduling of responses, they still must initiate execution of the actions, and this may be enough to support a sense of volition. In Experiment 1A, we show that very similar patterns of data are elicited by the open-performance and command-perfor-
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mance procedures, but the command-performance procedure shows a marked reduction in variability in actual levels of ⌬P and P(R) compared with the conventional open-performance procedure, and eliminates the variability in P(O).
Method Participants Fifty-one McMaster undergraduates participated for course credit in first- and second-year psychology courses. Twenty-six were assigned randomly to the open-performance condition, and 25 to the command-performance condition.
Stimuli and Apparatus Stimulus presentation and response collection was controlled by Metacard software operating on an Apple eMac, 1.42 GHz Power PC G4. Participants sat approximately 50 cm away from the screen, and made responses by clicking an on-screen button via a computer mouse. Command performance. Initial trial display was a picture depicting one of three unlit light bulbs on a coloured background. Bulbs varied in size and background colours, and were randomly assigned to blocks. Bulbs were centered on the screen, directly above a respond button or a no-respond button. The no-respond button was colored reddish-brown, and bore the words “Do NOT press,” and the respond button was grey, bearing the words “Press to cheque light.” A prompt indicating whether the participant was to respond or not appeared to the left of picture, and below the screen’s horizontal midline. The bulb, button and instruction box were presented against a white screen. Open performance. The stimuli and apparatus used in the open-performance condition were identical to that used in the command performance, except the response prompts and the norespond button were eliminated. The respond button was therefore presented on all trials.
Procedure Command performance. Participants were told that their task was to determine how much control they had over three different light bulbs. They were further instructed to test the bulb by clicking or not clicking on a button as directed by onscreen prompts. On respond trials, the respond button appeared below the bulb picture, along with the respond prompt, which consisted of the words “Please test the light bulb by pressing the button now” presented on a green background. On respond trials, participants pressed the respond button by clicking on it with the mouse. If no response was made in three seconds, the prompt box began to flash. 2
Technically, cue density should refer to the relative frequency of an observed event, as the inputs in an observational tasks are. Although it may be more correct to use a more generic term like input density to refer to the relative frequency of either an observed cue or self-generated response, we feel the advantage of maintaining consistency with terminology in related research areas outweighs the advantage of strict correctness. Thus, throughout the article we will use cue density to refer to the relative frequency of any input, whether observed cue, response or both.
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On no-respond trials, the no-respond button appeared, along with the no-respond prompt, which consisted of the words “Please do not press the button” presented on a pink background. On no-respond trials, the participant waited for three seconds, whereupon the brown no-respond button disappeared. If participants pressed the no-respond button, the trial was covertly scored as a respond trial, and the actual ⌬P was recalculated. After the response period, the light bulb would either turn on for three seconds, or remain off for three seconds. Trials were separated by a white screen of two seconds duration. At the end of each block of 40 trials, participants were asked to rate their degree of control on a zero to 100 scale. Ratings were entered using a scrollbar. The left end of the scrollbar was marked “0,” indicating no control, and the right end was marked “100,” indicating perfect control. Instructions for using the scale appeared directly above it. Open performance. The open-performance procedure was identical to the command performance, except for the response stage of each trial. Participants were told that on any trial they could press a respond button or leave it alone, and see what effect that had on an unlit bulb. The grey respond button remained on the screen for three seconds. If left unpressed for three seconds, the button would disappear, and the trial was scored as a no-response trial. No response prompts were used. Each block of trials was defined by an event matrix, shown in Table 1; these matrices were based on those used by Allan et al. (2005). The matrices produce different values for the low and high levels of P(O) for the two levels of ⌬P. For ⌬P(0), low P(O) ⫽ .2, and high P(O) ⫽ .8; for ⌬P(.5), low P(O) ⫽ .3, and high P(O) ⫽ .7. Unfortunately, this makes any ⌬P ⫻ P(O) interaction uninterpretable; fortunately, we have no theoretical or empirical reason to be interested in any putative ⌬P ⫻ P(O) interaction.
Results and Discussion For all analyses, ␣ ⫽ .05, unless mentioned otherwise. Due to low and high levels of P(O) having different values across levels of ⌬P, interactions of ⌬P and P(O) cannot be interpreted. For all studies, analysis of variance (ANOVA) effects sizes are given as 2; like 2, 2 gives the proportion of variance accounted for by a treatment, but adjusts this for sample bias.
Environmental Variables: P(R), Actual P(O), and Actual ⌬P For all three variables, the values for each participant at each level of nominal P(O) are shown in Figure 2 for ⌬P(0) and in Figure 3 for
⌬P(.5). These figures give a graphic representation of the actual variability across performance conditions, and the reduction in variability for the command-performance condition over the open-performance condition for all variables is evident. As can be seen in Figure 3, for example, actual ⌬p values (middle panel) for the openperformance condition range from slightly negative to ⫹ 1.0 when nominal ⌬P is programmed for ⌬P(.5). Mean actual values of P(R) for Experiments 1A and 1B are given in Table 2, mean actual values of ⌬P are given in Table 3, and mean actual values of P(O) are given in Table 4. The constancy of the means in the commandperformance condition for all three environmental variables is obvious; standard deviations are as much as an order of magnitude smaller in the command-performance conditions than in the openperformance conditions. We are concerned with demonstrating that the command-performance procedure substantially reduces variability in environmental variables, and hold them constant across experimental conditions, rather than demonstrating mean differences in the values of environmental factors between procedures. One exception to this is P(R). The centres of mass for the P(R) scatter plots appear much higher in both Figure 2 and Figure 3 for the openperformance data than for the command-performance data, as are the means in Table 2. Furthermore, Table 2 suggests there is an increase in P(R) with P(O) for the open-performance participants, but not the command-performance participants. Although the differences in variance preclude direct comparison between performance conditions, separate 2 (⌬P: 0; .5) ⫻ 3 [P(O): low, medium, high] repeated measures conducted for each performance condition reveal a main effect of P(O) for open-performance participants, F(2, 50) ⫽ 3.86, MSE ⫽ 0.14, p ⬍ .05, 2 ⫽ 0.04, but not command-performance participants, F(2, 48) ⫽ 1.95, MSE ⫽ 0.0003, p ⬎ .15, 2 ⬍ 0.01. No other effects were significant in either ANOVA. Thus, for open-performance participants, responses increase as outcome density increases, but they are held constant across outcome density in the command performance procedure.
Control Ratings In Figure 4, control ratings rise as P(O) increases for both performance conditions and both contingency levels, suggesting an outcome density effect was found in all conditions. This is confirmed by a series of ANOVAs, beginning with a 2 (performance: open; command) ⫻ 2 (⌬P: 0; .5) ⫻ 3 [P(O): low; medium; high] mixed-design ANOVA, with performance as the between-subjects factor, and ⌬P
Table 1 Experiments 1A and 1B: Scheduled R-O Events for Each Level of ⌬P and P(O) P(O) ⌬P
.2
0
R ⬃R
.5
R ⬃R
O 4 4 .3 O 11 1
.5 ⬃O 16 16
R ⬃R
⬃O 9 19
R ⬃R
O 10 10 .5 O 15 5
.8 ⬃O 10 10
R ⬃R
⬃O 5 15
R ⬃R
O 16 16 .7 O 19 9
⬃O 4 4 ⬃O 1 11
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Figure 2. Actual environmental values for each subject and each level of P(O) in open-performance (left column), and command-performance (right column) conditions for nominal ⌬P(0), Experiment 1A. For all conditions, P(R) is shown in the top row, actual ⌬P in the middle row, and actual P(O) in the bottom row.
and P(O) as within-subject factors. The only significant main effects were those of P(O) and ⌬P: P(O), F(2, 98) ⫽ 48.74, MSE ⫽ 22264, p ⬍ .001, 2 ⫽ 0.16; ⌬P, F(1, 49) ⫽ 189.50, MSE ⫽ 61469, p ⬍ .001, 2 ⫽ 0.22. As P(O) increased from low through medium to high levels, ratings of control increased from 37.3 through 48.2 to 66.5. As ⌬P increased from ⌬P(0) to ⌬P(.5), ratings of control increased from 36.5 to 64.9. Whilst the ⌬P ⫻ P(O) interaction was significant [F(2, 98) ⫽ 3.45, MSE ⫽ 1041, p ⬍ .05, 2 ⬍ 0.01], of more interest was the Performance ⫻ P(O) interaction, F(2, 98) ⫽ 6.73, MSE ⫽ 3075, p ⬍ .002, 2 ⫽ 0.02. Separate 2 (⌬P: 0; .5) ⫻ 3 [P(O): low; medium; high] repeated measures ANOVAs conducted for each performance condition find only main effects of both ⌬P and P(O) for each performance condition. For the open-performance condition, ⌬P: F(1, 25) ⫽ 136.08, MSE ⫽ 35642, p ⬍ .001, 2 ⫽ 0.23; P(O): F(2, 50) ⫽ 38.53, MSE ⫽ 21015, p ⬍ .001, 2 ⫽ 0.27. Open-performance participants in-
creased their ratings of control from 35.4 through 48.6 to 74.9 as P(O) increased from low through medium to high levels; they increased their ratings from 37.8 to 68.1 also as ⌬P increased from ⌬P(0) to ⌬P(.5). For the command-performance condition, ⌬P: F(1, 24) ⫽ 67.05, MSE ⫽ 26110, p ⬍ .001, 2 ⫽ 0.21; P(O): F(2, 48) ⫽ 11.87, MSE ⫽ 4324.1, p ⬍ .001, 2 ⫽ 0.07. Command-performance participants increased their ratings of control from 39.3 through 47.8 to 57.9 as P(O) increased from low through medium to high levels; they also increased their ratings from 35.1 to 61.5 as ⌬P increased from ⌬P(0) to ⌬P(.5). The command-performance procedure yielded a substantial reduction in the variability of actual ⌬P and P(O), and actual P(R) was not only kept almost exactly to programmed levels, but held nearly perfectly constant across increasing levels of P(O). In contrast, the more conventional open-performance procedure not only yielded higher levels of P(R), but also these levels increased as P(O)
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Figure 3. Actual environmental values for each subject and each level of P(O) in open-performance (left column), and command-performance (right column) conditions for nominal ⌬P(.5), Experiment 1A. For all conditions, P(R) is shown in the top row, actual ⌬P in the middle row, and actual P(O) in the bottom row.
increased. This is especially problematic if P(R) can bias judgments of control, as then the effects of P(O) are confounded with those of P(R). Both ⌬P and P(O) influenced the control ratings of both open and command performance participants, and in similar ways. The command-performance condition produced the usual pattern of effects we see in conventional open-performance procedures. However, P(O) seems to have had a slightly bigger influence on the open performance participants than on the command performance participants. This is suggested by Figure 4, the Response ⫻ P(O) interaction, and by the larger value of 2 for the main effect of P(O) for the open-performance compared with the commandperformance condition in the ANOVAs conducted within each performance condition. This greater influence of P(O) may reflect some intrinsic difference in the performance conditions, or it may reflect that only open-performance participants had two biasing factors increase with P(O)—P(O) and P(R).
Experiment 1B: Equating Response Levels In Experiment 1B we try to equate responsiveness to P(O) by encouraging participants in the open-performance condition to try to maintain a P(R) level of .5. This may not only result in equal responsiveness to P(O)—providing indirect evidence of a cue density effect— but may prove just as effective as the command-performance procedure at controlling variability in ⌬P and P(O) due to deviations from target P(R) rates. An instructional manipulation would be a simpler solution to the problem of lack of control over environmental variables than even the command-performance procedure. Out of concern that the six blocks needed to run Experiment 1A may be fatiguing, especially with the open-performance participants having also to monitor their responding, contingency was manipulated between participants rather than within. This reduced the number of blocks run for each participant from six to three.
COMMAND PERFORMANCE
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Table 2 Mean Actual P(R), Experiments 1A & 1B Nominal ⌬P (0)
Nominal ⌬P(.5)
Nominal ⌬P(0)
Nominal ⌬P(.5)
Experiment 1A
.2
.5
.8
.3
.5
.7
Experiment 1B
.2
.5
.8
.3
.5
.7
Open performance Command performance
.645 .176 .505 .012
.681 .160 .503 .008
.742 .173 .505 .010
.656 .230 .511 .024
.738 .169 .503 .011
.765 .171 .508 .020
Open performance Command performance
.524 .048 .503 .008
.565 .070 .503 .008
.563 .101 .503 .008
.563 .102 .510 .020
.570 .119 .515 .038
.560 .103 .518 .043
Note. Standard deviations in italics.
Method
Results and Discussion
Participants
Environmental Variables: P(R), Actual P(O), and Actual ⌬P
One hundred eight McMaster undergraduates participated for course credit in first- and second-year psychology courses. Of these 108, 56 were assigned randomly to the contingent condition, ⌬P(.5), with 28 participants in each performance condition (openperformance, command-performance). Of the 52 participants in the noncontingent condition, ⌬P(0), 26 participants were assigned randomly to each performance condition. Two participants in each contingent performance conditions were noncompliant, and their ratings data was excluded from analysis. All four are retained in the reporting of environmental variables, however, because the reason to compare these measures is not to assess some psychological process or mental representation, but to assess two procedures’ effectiveness as controlling participant variability. For the ratings data, N ⫽ 26 for all groups, whilst for the environmental data N ⫽ 28 for both contingent groups.
For all three variables, the values for each participant at each level of nominal P(O) are shown in Figure 5 for ⌬P(0) and in Figure 6 for ⌬P(.5). Mean actual values of P(R) are given in Table 2, mean actual values of ⌬P are given in Table 3, and mean actual values of P(O) are given in Table 4. Although there is less variance in the open-performance condition than in Experiment 1A, the SDs given in Tables 2, 3, and 4 are many times smaller in the command-performance than in the open-performance condition, and Figures 5 and 6 display much less variability in subject values in for the command-performance relative to the open-performance condition. Table 2 reveals that P(R) for both performance conditions are flat across P(O), demonstrating the effectiveness of the instructions to open-performance participants. We take the constancy of P(R) in all conditions as obvious enough that analytic confirmation is not required.
Control Ratings Stimuli, Apparatus, and Procedure Everything was identical to Experiment 1A except for two changes. Open-performance participants were instructed to maintain a P(R) of .5, and open-performance participants with P(R) levels above .7 or below .3 in two or more blocks were deemed noncompliant. The command-performance conditions used the same noncompliance criterion as in Experiment 1A. At the end of reading the verbal instructions, the experimenter quizzed each participant as to the desired P(R) level to ensure they were aware of what the target P(R) was, and to reinforce the importance of holding close to it. Also, contingency was manipulated between participants within each performance condition.
Figure 7 indicates that an outcome density effect is elicited for all performance and contingency conditions, as mean control ratings rose with P(O). Figure 7 also depicts a greater effect of ⌬P on ratings for the command-performance condition than for the openperformance condition. Analysis of participants’ control ratings confirms this interpretation. The 2 (performance: open; command) ⫻ 2 (⌬P: 0; .5) ⫻ 3 [P(O): low; medium; high] mixed-design ANOVA with performance and ⌬P as the between-subjects factors, and P(O) as the within-subject factor finds a main effect of P(O), F(2, 200) ⫽ 24.62, MSE ⫽ 9812, p ⬍ .001, 2 ⫽ 0.07. The main effect of ⌬P was also significant, F(1, 100) ⫽ 40.63, MSE ⫽ 47879, p ⬍ .001,
Table 3 Mean Actual ⌬P Across Levels of Nominal P(O), Within Nominal ⌬P, Experiments 1A & 1B Nominal ⌬P (0)
Nominal ⌬P(.5)
Nominal ⌬P(0)
Nominal ⌬P(.5)
Experiment 1A
.2
.5
.8
.3
.5
.7
Experiment 1B
.2
.5
.8
.3
.5
.7
Open performance Command performance
–.046 .141 .000 .014
.037 .226 .002 .018
.115 .270 – .004
.465 .138 .492 .017
.531 .169 .498 .010
.506 .277 .503 .024
Open performance Command performance
.003 .089 –.002 .007
–.003 .148 –.002 .017
.005 .186 .002 .007
.488 .098 .489 .022
.512 .110 .486 .063
.490 .109 .487 .050
Note. Standard deviations in italics.
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Table 4 Mean Actual P(O) Across Levels of Nominal P(O), Within Nominal ⌬P, Experiments 1A & 1B Nominal ⌬P (0)
Nominal ⌬P(.5)
Nominal ⌬P(0)
Nominal ⌬P(.5)
Experiment 1A
.2
.5
.8
.3
.5
.7
Experiment 1B
.2
.5
.8
.3
.5
.7
Open performance Command performance
.193 .044 .200 na
.518 .057 .500 na
.797 .039 .800 na
.363 .131 .300 na
.620 .088 .500 na
.826 .100 .700 na
Open performance Command performance
.204 .043 .200 na
.507 .058 .500 na
.803 .042 .800 na
.323 .080 .300 na
.520 .073 .500 na
.724 .079 .700 na
Note.
For the command performance condition, no variation in P(O) is possible. Standard deviations in italics.
2 ⫽ 0.17. Overall, ratings increased from 36.9 through 49.9 to 56.2 as P(O) increased from low through medium to high; ratings also increased from 39.5 to 55.8 as ⌬P increased from ⌬P(0) to ⌬P(.5). The only significant interactions were the two-way interaction of ⌬P ⫻ P(O), F(2, 200) ⫽ 3.32, MSE ⫽ 1324, p ⬍ .05, 2 ⬍ .01, and the two-way interaction of Performance ⫻ ⌬P, F(1, 100) ⫽ 4.69, MSE ⫽ 5526, p ⬍ .05, 2 ⫽ 0.02. To help interpret the Performance ⫻ ⌬P interaction, we performed separate 2 (⌬P: 0; .5) ⫻ 3 [P(O): low; medium; high] mixed-design ANOVAs, with ⌬P as the sole between-subjects factor, for each performance condition. Both ANOVAs produced similar effects. For the open-performance condition, only the main effects of ⌬P and P(O) were significant. For ⌬P, F(1, 50) ⫽ 7.14, MSE ⫽ 10437, p ⬍ .025, 2 ⫽ 0.07, ratings increased from 39.5 to 55.8 as ⌬P increased from ⌬P(0) to ⌬P(.5). For P(O), F(2, 100) ⫽ 12.35, MSE ⫽ 5010, p ⬍ .001, 2 ⫽ 0.07, ratings increased from 36.9 through 49.9 to 56.2 as P(O) increased from low through medium to high. For the
command-performance condition, main effects of ⌬P and P(O) were also the only significant effects. For ⌬P, F(1, 50) ⫽ 48.00, MSE ⫽ 42967, p ⬍ .001, 2 ⫽ 0.30, ratings increased from 35.6 to 68.8 as ⌬P increased from ⌬P(0) to ⌬P(.5). For P(O), F(2, 100) ⫽ 12.77, MSE ⫽ 4997, p ⬍ .001, 2 ⫽ 0.07, ratings increased from 42.9 through 51.2 to 62.4 as P(O) increased from low through medium to high. The Performance ⫻ ⌬P interaction seems due to ⌬P having a larger effect on the command-performance participants than on the open-performance participants. Although variability in environmental variables was reduced in the open-performance condition compared with Experiment 1A, values of ⌬P and P(O) were still better constrained by the commandperformance procedure. The command-performance procedure again produced reliable discriminability between contingency levels, and an outcome density effect for all levels of ⌬P. It even resulted in better discriminability of contingency than the open-performance condition. This is unlikely to reflect the shift from a within-subject to a betweensubjects design, as that should affect both performance conditions. It would be consistent, however, with the instructions to maintain a fixed level of P(R) producing a cost to participants due to having to monitor performance whilst attending to the display.3 Therefore, whilst the variability found in conventional designs can be constrained by instruction means, such instructional constraints impair the processing of contingencies, distorting the processing that is the focus of such designs. The lack of any P(O) ⫻ Performance interaction also provides some evidence that the greater effect of P(O) found in Experiment 1A for open-performance participants reflects that for open-performance participants only, P(R) increased as P(O) increased, and this provided an additional source of biasing. This would imply that judgments of control are susceptible to cue density effects. A cue density manipulation is the focus of Experiment 2.
Experiment 2: Cue Density Effects Applying a command-performance procedure eliminates variability in actual P(O), and tightly controls variability in both P(R) and ⌬P, whilst still producing reliable discrimination between ⌬P levels and an outcome density effect. However, it is unique in that it allows researchers to implement a cue density manipulation in active contingency tasks; that is, it allows researchers to observe the effect of systematic variations of P(R). Cue density effects have only been demonstrated in a few contingency-based experiments, all involving observational tasks, primarily causal reasoning (Perales, Catena, Figure 4. Mean judgments of control across performance conditions as a function of P(O), for nominal ⌬P(0) (open circles) and nominal ⌬P(.5) (solid circles), Experiment 1A. Error bars represent ⫾ 1 SE.
3
We thank Peter Graf for suggesting this interpretation.
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Figure 5. Actual environmental values for each subject and each level of P(O) in open-performance (left column), and command-performance (right column) conditions for nominal ⌬P(0), Experiment 1B. For all conditions, P(R) is shown in the top row, actual ⌬P in the middle row, and actual P(O) in the bottom row.
Shanks, & Gonza´lez, 2005; Wasserman, Kao, Van Hamme, Katagiri, & Young, 1996; White, 2003). It is reasonable to expect that because a judgment of control is also at least partially dependent on contingency information, cue density effects should be found in a judgment of control task as well, but there are two reasons why they may not. The first reason has to do with the ambiguous nature of the cue density effect. The second reason has to do with saliency differences between an external versus self-generated cue. Perales and Shanks (2007, p. 588) note, “The [cue density] effect does not appear in every case, and, in global terms, its magnitude is modest.” However, even this understates the ambiguity surrounding cue density effects. Several of the favourable findings Perales and Shanks cite in their review of cue density effects arose when cue density was confounded with outcome density, including the positive finding in their 2005 study (Perales et al., 2005; Experiment 1). Both White (2003) and Wasserman et
al. (1996) have experiments in which cue density is manipulated unconfounded with either ⌬P or P(O). However, as Perales and Shanks note, some conditions in these two papers produce successful cue density effects and other conditions within the same experiments produce failures. This erratic pattern suggests either that cue density effects—when unconfounded from both ⌬P or P(O)—are fragile, or Type I errors. Even if the cue density effect is real in observational tasks, the saliency differences between external and self-generated cues are substantial, and could change the manifestation of cue density effects from those seen in an observational task. If cue density can bias contingency-based decisions, such biasing may be dependent on participants not recognising the source of the bias. A motor response in a judgment of control task has to be deliberately generated by participants, making it a much more salient cue than an observed external event of little consequence to participants. As a cue, a voluntary
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Figure 6. Actual environmental values for each subject and each level of P(O) in open-performance (left column), and command-performance (right column) conditions for nominal ⌬P(.5), Experiment 1B. For all conditions, P(R) is shown in the top row, actual ⌬P in the middle row, and actual P(O) in the bottom row.
response is much less likely to be overlooked. On the other hand, it is also possible that the greater salience of a self-generated cue actually makes it a more potent source of biasing. Using the commandperformance procedure to implement a cue density manipulation in a judgment of control task thus fills a large empirical hole.
Apparatus and Stimuli Apparatus and stimuli were identical to those used in the command-performance procedure used in Experiments 1A and 1B.
Procedures and Design Method Participants Twenty-six McMaster undergraduates participated for course credit in first- and second-year psychology courses. Two were dropped from analysis, one for noncompliance, and one because they repeatedly expressed confusion about the nature of the task to the experimenter during the experiment, and assigned a rating of ⫹ 100 (perfect control) to all blocks, including both noncontingent blocks.4 This left 24 participants contributing analyzable data.
A command-performance procedure nearly identical to that used in Experiments 1A and 1B was used. However, the frequency of response commands varied across blocks, crossed with levels of ⌬P. 4 We maintained the definition of noncompliance as responding on more than 10% of no-response trials in at least half of the blocks. With 50 trials, when P(R) ⫽ .2, the 10% threshold is set to a limit of four responses during no-response trials; when P(R) ⫽ .8, the threshold becomes one response during no-response trials.
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Table 6 Mean Actual Values of P(R) and ⌬P, Across Levels of Nominal P(O), Within Nominal ⌬P, Experiment 2 Nominal ⌬P (0)
P(R) ⌬P Note.
Figure 7. Mean judgments of control across performance conditions as a function of P(O), for nominal ⌬P(0) (open circles) and nominal ⌬P(.5) (solid circles), Experiment 1B. Error bars represent ⫾ 1 SE.
Nominal ⌬P (.5)
.2
.8
.2
.8
.201 .004 .002 .012
.807 .014 .000 .048
.200 .000 .500 .000
.807 .010 .491 .013
Standard deviations in italics.
0.11; ratings increased 33.8 to 55.1 as ⌬P increased from ⌬P(0) to ⌬P(.5). For the main effect of P(R), F(1, 23) ⫽ 6.12, MSE ⫽ 4496, p ⬍ .05, 2 ⫽ 0.04, ratings increased from 37.6 to 51.3 as P(R) increased from .2 to .8. No other effects were significant. Ratings increased as P(R) increased within each level of ⌬P, even though P(O) was fixed at .5 for all conditions. This is the first demonstration of a cue density effect in a judgment of control task, or any active contingency task. It is also one of the few demonstrations of a cue density effect that is unconfounded by changes in P(O) in any type of contingency-based judgment. The magnitude of effect, as measured by 2 is modest compared with the effects of ⌬P and P(O) in Experiments 1A and 1B, as is the case for cue density effects in observational tasks (reviewed in Perales & Shanks, 2007).
General Discussion The experiment is a 2 ⫻ 2 repeated-measures design, with ⌬P (0; .5) and P(R) (.2; .8) varied within-subject. Matrices giving the cell frequencies for each P(R) ⫻ ⌬P level are given in Table 5. P(O) was held constant to .5 across all blocks. Block order was randomised for each participant at the start of the experiment.
The command-performance procedure substantially reduced variability in environmental variables of an active contingency task compared with an open-performance procedure, whilst yielding the same
Results and Discussion Mean actual P(R) and ⌬p values are reported in Table 6, and are extremely close to, and often exactly at, nominal values. Mean control ratings are shown in Figure 8, and it appears that ratings increase as a function of ⌬P and P(R). A 2 (⌬P: 0; .5) ⫻ 2 [P(R): .2; .8] repeated measures ANOVA performed on participant control ratings confirms that both factors affect ratings. For the main effect of ⌬P, F(1, 23) ⫽ 18.23, MSE ⫽ 10901, p ⬍ .001, 2 ⫽ Table 5 Scheduled R-O Events for Each Level of ⌬P and P(R), Experiment 2 P(R) .2 ⌬P 0
O 5 20 9 16
.8 ⬃O
.5
R ⬃R R ⬃R
5 20 1 24
Note.
P(O) ⫽ .5 for all conditions
R ⬃R R ⬃R
O
⬃O
20 5 24 1
20 5 16 9
Figure 8. Mean judgments of control across levels of P(R), for nominal ⌬P(0) (open circles) and nominal ⌬P(.5) (solid circles), Experiment 2. Error bars represent ⫾ 1 SE.
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pattern of data seen in the conventional open-performance procedure. In both Experiment 1A and 1B, command-performance participants reliably discriminated between contingency levels, and were positively biased by outcome density. Although an instruction manipulation in Experiment 1B reduced variability in environmental variables compared with the open-performance procedure in Experiment 1A, there was still greater variability in these variables when compared with the command-performance procedure. More problematic, the instructional manipulation seemed to impair discrimination of contingency, presumably because of the greater load imposed by having to monitor response rate. Not only were we able to produce conventional data with the procedure, we were also able to use it to implement a cue density manipulation in judgments of control for the first time in any type of active contingency judgment task (Experiment 2). This resulted in a clear demonstration of a cue density effect: Ratings of control increased as P(R) increased, even with P(O) and ⌬P held constant. We should point out that not only is this the first unambiguous demonstration of a cue density in an active contingency setting, but one of the few demonstrations of a cue density effect that is not confounded with outcome density in any task. Whilst Matute’s (1996) data may also reflect cue density effects, the correlational nature of Matute’s study means that we cannot be sure the difference in ratings across levels of P(R) was not due to changes in P(O) or ⌬P driven by P(R), or some combination of cue density and variance in environmental variables. As found in observational contingency tasks (Perales & Shanks, 2007), the cue density effect seems much smaller than the outcome density effect, judging by the relative sizes of 2. This result is important, as there are very few studies in which cue density is manipulated independent of outcome density within an observational task. Even White’s (2004) systematic exploration of cue density has cue density entirely confounded with outcome density. Given the mixed results for obtaining cue density effects in the two papers we could find in which cue density varies independently of outcome density (Wasserman et al., 1996; White, 2003), it would be reasonable to remain skeptical about the existence of any cue density effect. Our finding of a unambiguous cue density effect in a different paradigm from those used before provides needed confirmation that the effect is real; this conclusion is reinforced by the consistency in the cue density effect size relative to that of outcome density effects across this article and previous studies. It also raises the possibility that cue density effects may have contributed to Alloy and Abramson’s (1979) finding of depressive realism. The behaviour of Alloy and Abramson’s nondepressed participants is no surprise: increases in P(O) routinely produce substantial increases in contingency/control judgments. As we have shown in Experiments 1A and 1B, this is true even when P(R) is held constant. What is to be explained is the failure to find outcome density effects in Alloy and Abramson’s depressed participants. Possibly, their depressed participants decreased P(R) as P(O) increased. This could not only change environmental variables, as discussed throughout this article, but may have also resulted in a positive outcome density effect being countered with a negative cue density effect. However, this conclusion should be treated with some caution. As we noted earlier, cue density effects are quite small, especially as compared with outcome density effects. Nevertheless, along
with concerns about the impact of shifts in P(R) on the real value of environmental variables, these results add to the uncertainty regarding the status of the realism of depressive realism.
Cue Density Effects and Their Implications The similarity of findings with regards to cue density effects between this article and the work in observational tasks reviewed by Perales and Shanks (2007) suggests that a common mechanism may underlie cue density effects in both active and observational contingency tasks, despite the differences in the nature of cues. Perales and Shanks have championed the evidence integration (EI) model, showing it can fit a wide range of causal judgment data, including both outcome density and cue density effects. The model is basically a weighted version of the ⌬D rule (Allan & Jenkins, 1983), and largely the same as White’s (2003, 2004) weighted proportion Confirming Information (pCI) rule that is the basis of White’s evidential evaluation model. In all these versions, the evidence confirming a positive contingency is contrasted with the evidence disconfirming a positive contingency. Such a contrast would be a generic enough mechanism to account for the similarity in findings across active and observation tasks. Using a schematic contingency matrix as presented in Table 7 as a reference, we can see that positive confirmatory evidence is found in the a/d diagonal, and positive disconfirmatory evidence is found in the b/c diagonal. In the EI model (Perales & Shanks, 2007), this difference is computed after weighting the four cells. This weighted difference is taken as a proportion of the total number of (weighted) events, as indicated below: EI ⫽ 共共waa兲 ⫹ 共wdd兲兲 ⫺ 共共wbb兲 ⫹ 共wcc兲兲/共waa ⫹ wbb ⫹ wcc ⫹ wdd兲
(3)
In the ⌬P rule that is the basis of models such as Cheng’s probabilistic contrast model (Cheng & Novick, 1992) and Cheng’s later power probabilistic contrast (PC) model (Cheng, 1997), it is the difference in the rows (or, more correctly, the row-based proportion of outcomes) that drives decision-making. The weighting of the a, b, c, d cells is critical to the EI model. Without differentially weighting these four cells, it is as limited as the ⌬P rule, as neither is able to account for outcome density or cue density effects. With this weighting in place, the EI model can account for both effects. Unfortunately, with this cell weighting in place, the same model can also account for the absence of these effects or even their reversal, as the model has four free parameters— one for each cell. Without an accompanying theory specifying how weights for the four cells are set, it seems in danger of fitting any effect, even those that are empirically invalid.
Table 7 Schematic: Contingency Matrix
R/C ⬃R/⬃C
O
⬃O
a c
b d
COMMAND PERFORMANCE
Perales and Shanks’ (2007) support for the EI model is a result of its performance in a meta-analysis which pit the EI against three other models, including both a weighted ⌬P rule and the RescorlaWagner model (Rescorla & Wagner, 1972), using a crossvalidation measure to mitigate model complexity. The crossvalidation does help to address concerns about the complexity of the EI model. The model, however, can only provide testable predictions if applied to questions in which the weights can be reliably determined from previous data. Given that these are just cases in which much is already known, it seems as though there would be little room to make new predictions. If the EI model— or any other model in which cell weighting is critical—is to be useful in understanding contingency-based judgments, some theory of how cells are weighted is needed. This is largely the same as asserting that there is a need to understand the role of attention in contingency judgments, as to weight a cell over others is the same as to select some events for more processing than other events. Such an account should be able to describe both attentional effects due to explicit reasoning and those due to more stimulus-driven factors. Approaches such as causal model theory (Waldmann & Holyoak, 1992) can be seen efforts to understand the influence of concepts upon attention and cell weighting, but stimulus-driven influences have largely been ignored. All of the approaches discussed by Perales and Shanks (2007) are single-process models. Rather than trying to capture the flexibility in judgments of control, causality and contingency by introducing single-process models with many parameters, perhaps dual-process models are needed (Allan, Hannah, Crump, & Siegel, 2008; Perales et al., 2005; Vadillo & Matute, 2007). Allan has been arguing for one dual-process approach, signal detection theory, in recent years (Allan et al., 2008; Allan et al., 2005). Dualprocess models have also become quite prominent in reasoning and decision-making research (e.g., De Neys, 2006; Evans, 2003; Stanovich & West, 2000). As a final observation, we note that the command-performance procedure not only allows us to manipulate the rate of responding, but also the pattern of responding. In most versions of contingency-based tasks, whether active or observational, the information unfolds over time, and the organisation of this temporal sequence may influence judgments. This would allow researchers, for example, to explore the kind of primacy and recency effects that have been examined in contingency and causality judgments (e.g., Collins & Shanks, 2002; Vadillo & Matute, 2007). Researchers could also investigate whether the predictability of responding can mediate control judgments. Perhaps people estimate control partly in terms of how predictable events are in a task, and have trouble discriminating sources of predictability. Such a “fuzzy prediction” heuristic may explain why increasing levels of either P(R) or P(O) can bias control judgments, and may be applicable to judgments of observed contingencies.
The ITI Hypothesis: A Victim of Lack of Control? That control ratings exhibited an outcome density effect in all conditions where P(O) was manipulated despite an intertrial interval (ITI) of only two seconds is not consistent with the findings of Msetfi, Murphy, Simpson, and Kornbrot (2005). Msetfi et al. (2005) had depressed and nondepressed participants judge their control over the onset of a light bulb, just as our participants did.
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In their second experiment, they found no outcome density effects amongst either depressed or nondepressed people when the intertrial interval was only three seconds, and found an outcome density effect only for nondepressed participants when the intertrial interval was 15 seconds. We produced outcome density effects for all conditions with an intertrial interval of two seconds. Outcome density effects with ITIs of two to six seconds have been found in several studies of active contingency judgments (Dickinson, Shanks, & Evenden, 1984; Shanks, 1985), and in the depressive realism literature (Benassi & Mahler, 1985, Experiment 2, depressed participants; Va´zquez, 1987, Experiment 2, nondepressed participants). Contrary to Msetfi et al.’s claim that no outcome density effects were found in Allan and Jenkins (1983), there is a clear outcome density trend in all their “1O” tasks. Allan and Jenkins were investigating the effects of task structure, rather than outcome density per se, and thus varied, amongst other things, whether outcomes consisted of an outcome that could occur or not (“1O” tasks, typical of most studies, including ours) or consisted of one of two outcomes (“2O” tasks). No outcome density effect, of course, can be found in 2O tasks, as some outcome is always occurring; all that can vary is the frequency of one of the two outcomes. At least one failure to produce outcome density effects at long ITIs has also been found in the depressive realism literature (Bryson, Doan, & Pasquali, 1984, 15 second ITI). It appears that Msetfi et al.’s short ITI results are rather anomalous. We suggest that one reason for the anomaly may be that the actual responseoutcome contingencies or actual P(O) may not be properly controlled in the short ITI condition.
Volition and Personal Control It could be argued that by telling participants when to respond, some aspect of volition is removed or changed. However, participants in the command-performance task produce very similar patterns of data as those produced in conventional procedures, where participants’ volition is unconstrained. The command-performance procedure seems to measure what conventional procedures measure. If volition is changed in the command-performance procedure relative to open-performance procedures, this is not important to ratings of control within a specific task. Lagnado and Sloman (2004) showed that intervening produced more efficient learning than observational learning in causal learning; one reason for this, they noted, may be that intervening allows volitional hypothesis testing, making hypothesis testing more efficient. However, Lagnado and Sloman refuted this in their Experiment 3, where they tested a volitional intervention condition against a forced intervention condition, where, much as in the command-performance procedure, participants were told when to intervene. No differences between causal learning conditions were found. If a judgment of control is a form of causal learning where the cause is our own action, then Lagnado and Sloman’s results, like ours, imply that volitional hypothesis testing is not necessary for judgments of control. Nor is there any reason why volition should differ in the command-performance procedure relative to open-performance procedures. The actions of participants still arise due to a conscious decision made by the participants to press or not press a button—their responses still elicit what Synofzik, Vos-
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gerau, and Newen (2008) called the “mineness” of volitional action. We could imagine that following orders to act may change participants’ emotional experience of the task, and this may change their global sense of control— how much control they have in their life— but such a judgment of global control is quite distinct from judgments of local control— how much control they have in performing some task. If the command-performance procedure does alter the sense of global control then this would make the command performance procedure more interesting. It may be, for example, that people’s sense of personal control at a global level is slightly diminished following a command-performance procedure compared with an open-performance procedure. This would tell us something about the psychological impact of following orders, without subjecting participants to any onerous or stressful manipulation. The role of volition and the relation between global and local perceptions of control is entirely speculative. We do know that the command performance procedure elicits typical patterns of control ratings, including outcome density effects, whilst holding environmental variables exactly on nominal values, as for P(O), or close to nominal values, as for ⌬P and P(R). The command-performance procedure allows experimenters to explore judgments of control with the same kind of rigour brought to judgments of causality or contingency judgments. The experimenter has taken back the degree of freedom previously lost to the participant (Gibbon, Berryman, & Thompson, 1974; Hannah et al., 2007).
Re´sume´ Les taˆches de contingence active, comme celles utilise´es pour explorer les jugements de controˆle, souffrent de variabilite´ quant a` la valeur re´elle des variables critiques (Hannah, Allan, & Siegel, 2007). Nous pre´sentons une nouvelle proce´dure, facilement imple´mente´e, qui permet a` l’expe´rimentateur de reprendre le controˆle de ces variables, simplement en indiquant aux participants quand re´pondre et quand ne pas re´pondre. Cette proce´dure de commande de performance permet non seulement un plus grand controˆle sur les variables critiques, telles que la contingence re´elle, mais elle permet aussi de manipuler la fre´quence des re´ponses inde´pendamment de la contingence et de la fre´quence des conse´quences. Cela constitue la premie`re de´monstration d’un e´quivalent de l’effet de la densite´ de l’indice dans une taˆche de contingence active. Les jugements du controˆle sont biaise´s par la fre´quence de re´ponse, tout comme elles le sont par la fre´quence de la conse´quence. Mots-cle´s : jugement du controˆle, prise de de´cision, effet de densite´ de l’indice, contingence
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Received October 10, 2007 Accepted July 17, 2008 䡲
