After incidentally learning about a hidden regularity, participants can either continue to solve the task as instructed or, alternatively, apply a shortcut. Past research suggests that the amount of conflict implied by adopting a shortcut seems to bias the decision for vs. against continuing instruction-coherent task processing.We explored whether this decision might transfer from one incidental learning task to the next. Theories that conceptualize strategy change in incidental learning as a learning-plus-decision phenomenon suggest that high demands to adhere to instruction-coherent task processing in Task 1 will impede shortcut usage in Task 2, whereas low control demands will foster it. We sequentially applied two established incidental learning tasks differing in stimuli, responses and hidden regularity (the alphabet verification task followed by the serial reaction task, SRT). While some participants experienced a complete redundancy in the task material of the alphabet verification task (low demands to adhere to instructions), for others the redundancy was only partial. Thus, shortcut application would have led to errors (high demands to follow instructions). The low control demand condition showed the strongest usage of the fixed and repeating sequence of responses in the SRT. The transfer results are in line with the learning-plus-decision view of strategy change in incidental learning, rather than with resource theories of self-control.

**Keywords: incidental learning, information reduction, serial reaction task, transfer, cognitive conflict, instruction following, pliance**

### **INTRODUCTION**

The human factors literature counts many cases where, with experience, people change from processing a task as instructed to applying a shortcut (Reason, 1990; Niessen et al., 1999; Underwood et al., 2002). This has triggered experimental work on incidental learning to explore the role of cognitive control in strategy change (e.g., Strayer and Kramer, 1994; Haider and Frensch, 1999; Touron and Hertzog, 2004a,b; Haider et al., 2005; Hoyndorf and Haider, 2009). In some experimental setups participants who had discovered a shortcut were faced with high vs. low demands to adhere to instruction-coherent task processing instead of applying the shortcut. For instance, Gaschler and Frensch (2009)instructed participants to check strings for alphabet errors (see **Figure 1A** for an example). With practice, participants could learn that some string positions rarely contained alphabet errors so that time could be saved by skipping these positions when checking the strings. Experimental conditions differed in the amount of alphabet errors in these less relevant string positions. Disregarding the instruction to exhaustively check the strings led to few errors for one group of participants (low demand to secure adherence to instructions). On average this group showed a higher rate of shortcut usage than the group for which more errors would

have resulted from disregarding the instructions (high control demand).

Importantly, the number of errors that one would commit using the shortcut seemed to affect performance by influencing the probability that a participant fully used the shortcut vs. refrained from using it. Thus, an all-or-non adjustment of control was observed. While some participants started to use the shortcut on all following trials after some practice, others completely refrained from using it. Conflict level (i.e., level of errors implied by shortcut usage) was influencing how many of the participants used the shortcut, rather than to what extent they used it. The link between conflict level and shortcut-based errors seems plausible, given that response errors have been tied to similar control processes and neural substrates driving behavioral adjustment as the ones involved in case of competing response tendencies, decision uncertainty and unfavorable outcomes (e.g., Ridderinkhof et al., 2004). The adjustment of shortcut usage to control demands is in line with work suggesting that strategy change in incidental learning is based on a general decision to apply or not apply an incidentally discovered shortcut (e.g., Haider and Frensch, 1996, 2002). When people apply the shortcut, they do so for practiced and novel stimuli alike (cf. Gaschler et al., 2014a). For instance, Touron

and Hertzog (2004a,b) reported that most older (as compared to younger) research participants in incidental learning experiments were reluctant to apply a shortcut they had learned. While they had sufficiently memorized the set of search items in a match-tosample visual search task to avoid visual search in favor of faster memory search, they continued to solve the task as instructed. As the shortcut option is not mentioned in the instructions of incidental learning tasks, participants cannot be sure that the shortcut option they eventually discovered will hold throughout the experiment. In addition to the insecurity regarding the reliability of the shortcut, some participants reported reluctance to apply a shortcut because they placed more emphasis on accuracy than speed (see also Haider and Frensch, 1999).

Following or disregarding instructions is not a one-shot game. Learning theorists have suggested that people follow instructions, because they have generalized episodes in which instruction following was reinforced (e.g., Hayes et al., 1986, 2001; Törneke et al., 2008). On the one hand, participants might thus learn about contexts in which it generally pays off to follow instructions. On the other hand, they should also be able to learn under which conditions it is more advantageous to apply a shortcut instead of sticking to instruction-coherent task processing. As suggested above, people might decide to apply a shortcut, based on the experience that it rarely or never leads to errors. However, adaptation to the conflict level that a shortcut implies might not only affect processing of the current task, but also transfers to other tasks. Having experienced an incidental learning task in which a potential shortcut leads to few vs. many errors might influence the likelihood to adopt a shortcut discovered in a later task.

Theories that view strategy change as a phenomenon involving both, the learning of a shortcut option, as well as the decision to apply it or to refrain from applying it (e.g., Touron and Hertzog, 2004a,b; Gaschler et al., 2014a) can predict that experience with one incidental learning task offering a shortcut option, transfers to a second incidental learning task (see discussion for competing theories). Prior experience with low demands to refrain from shortcut usage will foster shortcut usage in the next incidental learning task. This is because the experience that shortcut application did not lead to errors in the first task, could bias the expectation that this would not be the case either in the next task (for expectation effects on conflict processing within task cf. Duthoo et al., 2013; or review by Gaschler et al., 2014b). Thus, after working on a task in which a shortcut could be discovered and adopted, participants should be more likely to use a shortcut on a task presented later on. Conversely, prior experience with a setup where the demands to refrain from applying a shortcut are high, could lead to the expectation of high control demands for the next task. In this case, participants would be more likely to refrain from using a shortcut in Task 2. A baseline condition not working on Task 1 should show intermediate levels of shortcut usage.

In the current experiment, we combined two established incidental learning tasks in order to study transfer of control demands. We used control demands in the task applied first as an independent variable and performance in the second task as a dependent variable. In two conditions participants first worked on the *alphabet verification task* (e.g., Haider and Frensch, 1996; Green and Wright, 2003; **Figure 1A**) and then on a variant of the *serial reaction task* (SRT; e.g., Nissen and Bullemer, 1987; Abrahamse et al., 2010; **Figure 1B**). In the alphabet verification task participants are instructed to tediously check alphanumeric strings. Yet they learn that these strings contain a redundant section that could be skipped. In the SRT participants receive choice reaction instructions for a consistent stimulus-response mapping. Instead of choosing reactions based on the stimulus of the current trial as instructed, they can substantially simplify task processing by learning and applying the fixed repeating sequence of stimuli and responses. While in typical variants of the SRT the sequence is long and learning remains implicit (e.g., Abrahamse et al., 2010), we used a variant with a short and simple sequence – similar to experiments in which participants have become aware of the sequence and became able to produce reactions without paying attention to the stimuli (cf. Haider and Rose, 2007; Rünger and Frensch, 2008; Schwager et al., 2012). Our variant of the SRT was constructed such that large gains in performance based on sequence knowledge were possible. Tubau et al. (2007, see also Verwey and Wright, 2014) showed that sequence knowledge allows participants to change from stimulus-based responding to memory-based responding. We used a rather simple repeating sequence. The six stimuli and keys were each presented once. The rationale behind this setup, established in Rünger and Frensch (2008), is that people would neither find it difficult to represent nor implement the shortcut option, once they have learned it – allowing us to focus on control demands (minimizing strategy performance problems).

As a novel approach to continuously assess sequence knowledge throughout practice, we included randomly interspersed ambiguous stimuli. If participants know the repeating sequence, they can give the response that would have been due according to the fixed repeating sequence if an ambiguous stimulus is presented. Otherwise they have to guess a response as the stimulus cannot be discriminated. In addition, we adopted a more traditional measure of sequence knowledge. Studies using the SRT usually measure sequence knowledge after practice with the sequential regularity by assessing the reaction time slowing in off-sequence blocks or randomly interspersed off-sequence deviant trials in comparison to trials following the sequence (e.g., Schvaneveldt and Gomez, 1998; Shanks et al., 2003; Abrahamse et al., 2010; Gaschler et al., 2012). We used this measure by randomly inserting deviant trials. We did so only at the end of practice, as reports of participants starting to rely on memorybased instead of stimulus-based response selection in the SRT come from setups using sequences without deviants (e.g., Tubau et al., 2007; Rünger and Frensch, 2008; Schwager et al., 2012). Providing a further reason for saving this measure for the end of practice, Verwey and Wright (2014) reported RT data suggesting that deviants might suppress the expression of sequence knowledge.

In summary, the present study set out to examine whether shortcut usage in one task transfers to a subsequent task. We hypothesized that prior experience with a setup where a shortcut can be safely applied should lead to increased shortcut usage in a second incidental learning task. Conversely, prior exposure to a shortcut which would lead to errors should reduce shortcut usage in the second task.

### **MATERIALS AND METHODS**

### **PARTICIPANTS**

One hundred and four students from different Berlin-based universities took part in the experiment and were paid € 10 (69 female; mean age 24.8 years, SD = 5.2). When entering the lab, participants were randomly assigned to the low or high control demand condition without knowledge of the experimenter. Conditions differed in the variant of the alphabet verification task that they were presented before working on the SRT. The participants of the baseline condition worked only on the SRT. Therefore, they were in the lab for a shorter time and were treated separately by the experimenter. Exclusion of four participants (see results) led to 32 participants in both, the high and the low control demand condition and 36 participants in the baseline condition. The experiment took place in the laboratories of the Psychology Department of Humboldt-Universität Berlin. We obtained informed consentfrom the participants and approval by the ethical review board.

### **MATERIALS AND APPARATUS OF TASK 1: ALPHABET VERIFICATION TASK**

The stimuli in the alphabet verification task consisted of 48 alphanumeric strings (e.g., C D E F G 4 L; see **Figure 1A**), presented two times in each of the four blocks of practice. Half of the strings were *valid*, following the order of the alphabet; the other half were *invalid*, deviating from it. The digit 4 in the letter-digitletter triplet indicated that the next four consecutive letters of the alphabet needed to be skipped at this string location, and that the string would continue with the fifth letter. Thus, "M 4 R," for instance, was to be interpreted as "M, skip N, O, P, Q, continue with R." There were either no, two or four letters forming a prefix before the letter-digit-letter triplet.

In the low control demand condition, violations of the alphabetical order only occurred in the letter-digit-letter triplet (five instead of the indicated four letters fitting the void). The prefix (i.e., the letter in front of the letter-digit-letter triplet) was always correct. In the high control demand condition, however, the prefix was free of errors only in 75% rather than 100% of the trials. The letters outside the triplet could therefore not be safely ignored. As in other work on strategy change with the alphabet verification task (e.g., Gaschler and Frensch, 2007), the length of the prefix was varied in order to obtain a reaction time measure of the extent of prefix processing. As long as participants adhere to the instructions and check the strings exhaustively, longer strings should lead to higher reaction times as compared to shorter strings. The impact of string length on RT should diminish with practice to the extent that participants stop to check the prefixes.

Each trial started with a fixation cross presented centrally for 200 ms that was followed by an alphanumeric string. Strings were centrally presented in bold Courier New font, size 26, at the center of a 17-inch CRT screen in black color on a light yellow background, controlled by a PC. The font ensured constant spacing between letters. The letters were ∼1.1◦ × 0.9◦ in size. Consecutive letters appeared ∼0.9◦ apart on the screen. After the manual response was registered, the string was erased from the screen and there was a blank interval of 200 ms before the fixation cross of the next trial appeared. Incorrect responses were immediately followed by a high tone as error signal. Participants responded by pressing either the "y" or the "," key on the second row from the bottom on a standard German PC keyboard. Half of the participants were instructed to use the "y" key to indicate that a string was valid and the "," key to indicate that the string was invalid; for the other half, the key assignment was reversed.

In the computerized instructions, the characteristics of the alphanumeric strings were described, and participants were shown how to evaluate the strings. Participants were instructed to pay attention to the entire string because errors could occur anywhere in the string. Furthermore, they were told to respond as quickly as possible while keeping the rate of errors below 10%. The alphanumeric strings used as examples in the instructions and in the 10 practice trials (triplets starting with E and F) contained violations of the alphabetical order outside the letter-digit-letter triplet and were not from the pool of material used for the rest of the task. The task was completed within ∼45 min.

### **MATERIALS AND APPARATUS OF TASK 2: SRT**

In each trial, participants saw a random cloud of 72 dots, each colored in one of six colors for 250 ms in a centrally presented frame (**Figure 1B**). The frame was drawn in gray lines on a black background. Afterward, the cloud disappeared and the program awaited a response. A new stimulus was displayed after a response stimulus interval (RSI) of 100 ms. In order to allow for execution of fast response sequences (e.g., based on sequence knowledge), the stimulus presentation ended early in case participants responded during the stimulus presentation. Except on some irregular trials, (see below) one color was much more frequent (52 dots) as compared to the other five (four dots each) in each trial. At a distance of 3.6◦ beneath the 4.4◦ × 4.4◦ frame with the dots, a row of colored squares indicated the mapping between the dominant color and the response. Each color box was 1.2◦ high and 1◦ wide and the spacing was 0.5◦. Participants responded with the keys on the lower row of the keyboard (X to M) using index, middle, and ring fingers which they should keep resting on the keys. The keys were numbered 1 to 6 with stickers and the mapping of colors to keys was constant throughout the task.

Unbeknownst to the participants, stimuli (dominant stimulus colors) and the required responses followed a simple fixed repeating sequence. Sequences were drawn from a pool of 24 firstorder sequences of length six. Each of the six stimuli and responses occurred once and this sequence was constantly repeated. To avoid salient spatial patterns in the response positions, the sequences did not contain "runs" of three or more adjacent response locations (e.g., 1-2-3, 6-5-4 with responses numbered from left to right; cf. Rünger and Frensch, 2008). The selection of the sequences was matched between the conditions of the experiment.

Each of the seven blocks of the SRT consisted of 108 regular and 12 irregular trials. An auditory error feedback was presented during the RSI on regular trials, while any response in the irregular trials was regarded as correct. With (1) ambiguous and (2) deviant trials, we used two different kinds of irregular trials in different blocks in order to assess usage of sequence knowledge – the dependent variable of the experiment. Stimuli in irregular trials in Blocks 1 to 6 were maximally ambiguous. The cloud of dots contained dots of all colors with equal frequency. Thus, the stimulus did *not* suggest any of the six responses more strongly than the other five. Therefore, sequence knowledge should be measurable in a response bias. For instance, the ambiguous stimulus in **Figure 1B** elicits the response for green. As this response was due according to the fixed repeating sequence, such a response suggests sequence knowledge. No sequence knowledge would be evident if the participant pressed the key according to the sequence only at chance level (match in 1/6th of the ambiguous trials). If participants acquire knowledge about the fixed repeating sequence and decide to exploit it for the simplification of task processing, they should not only pass chance level in choosing responses according to the repeating sequence. Rather they should start to consistently respond according to the fixed and repeating sequence in the ambiguous trials.

In Block 7, the stimuli in deviant trials had a dominant color that did not follow the sequence. For instance, instead of a cloud of predominantly yellow dots that should appear based on the repeating sequence, a predominantly blue stimulus might be randomly inserted instead. Random deviants were drawn such that immediate repetitions of responses were avoided. Sequence knowledge was assessed as the reaction time difference between, on the one hand, the irregular trials and their immediate successors, and, on the other hand, the remainder of the trials with correct responses. We included the immediate successor of the deviant as a potentially slowed trial in order to increase the number of trials available for the RT estimate.

### **PROCEDURE**

Except for the baseline condition, participants started the experiment with the alphabet verification task. No references were made as to whether a part of the stimuli could be safely ignored or not. After completing the alphabet verification task, the experimenter started the automatized instructions of the serial reaction time task. Participants were told that this task is a speeded forced choice stimulus discrimination task. In doing so, no underlying regularities in the task material were mentioned. The experimenter then watched the first five trials to make sure that participants had properly understood the instructions. Only after completing the SRT participants were asked whether or not (forced choice) it would have been possible for them to skip checking a part of the string positions of the alphabet verification task (see results on manipulation check). Also the experimenter inquired about verbalizable sequence knowledge (SRT). Participants were asked to recall the fixed repeating sequence or otherwise guess a sequence of six elements. For each participant, the pattern of the correctly verbalized portion(s) of the trained sequence was compared to a simulation in order to estimate the likelihood that it was based on guessing (see Rünger and Frensch, 2008). The simulation determined how often the specific pattern of correct verbalizations observed for a participant (e.g., a triplet correct) would be obtained by matching the training sequence with a randomly generated sequence 10 million times. If the specific pattern of correct verbalizations occurred with low relative frequency in random matching, it was likely not the result of guessing.

### **RESULTS**

### **SCREENING OF THE DATA**

Screening of the data suggested that there was no speed–accuracy trade-off. In both tasks error trials tended to be slower rather than faster as compared to correct trials. In the low control demand condition, one participant did not fully complete the alphabet verification task and three participants were excluded because of error rates higher than 30%. The mean error rate of the remaining participants of the high control demand condition (*N* = 32) and those of the low control demand condition (*N* = 32) was 7.5% for either group. See below for SRT error rates of these conditions and the baseline condition (*N* = 36).

### **MANIPULATION CHECKS**

In the main analysis below we employed presence and variant of the alphabet verification task (high control demand condition, low control demand condition, baseline condition) as an independent variable for performance in the SRT. Beforehand, we checked whether the manipulation of the feasibility of information reduction actually led to performance effects in the alphabet verification task itself. As participants in the low control demand condition could safely skip to check some of the string positions, it was to be expected that they should be generally faster than participants of the high control demand condition. Furthermore, RTs in the low control demand condition should be less strongly influenced by string length, because the string prefixes (letters before the letter-digit-letter triplet) of varying length did not contain to-be-spotted alphabet errors and thus could be skipped. The data presented in **Figure 2** are in line with these predictions. A mixed ANOVA on RTs, including block and string length as within-subjects factor and control demand as a between-subjects factor showed a main effect of control demand condition, *F*(1,62) = 7.53, MSE = 16480000, *<sup>p</sup>* <sup>=</sup> 0.008, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.11, of block of practice, *F*(3,186) = 76.93, MSE <sup>=</sup> 1601747, *<sup>p</sup>* <sup>&</sup>lt; 0.001, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.55, and of string length on RT, *<sup>F</sup>*(2,124) <sup>=</sup> 72.43, MSE <sup>=</sup> 447654, *<sup>p</sup>* <sup>&</sup>lt; 0.001, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.54. Furthermore, there was an interaction between control demand condition and string length, *F*(2,124) = 4.53, MSE = 447654, *<sup>p</sup>* <sup>=</sup> 0.013, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.07, as string length was of less influence for participants of the low control demand condition than for participants who could not safely skip to check the string prefixes. With practice there was a decrease of processing of the string positions containing alphabet errors rarely or never, *F*(6,372) = 2.55, MSE <sup>=</sup> 204073, *<sup>p</sup>* <sup>=</sup> 0.02, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.04, for the interaction between block of practice and string length (other *F*s < 1.1). Note that we applied Greenhouse–Geisser correction in the ANOVAs when necessary.

Participants proved knowledgeable about whether or not information reduction had been possible in the version of the alphabet verification task they had been practicing. When asked to guess whether or not the prefix letters in their version of the task had or had not always been in correct alphabetical order, all participants of the high control demand condition correctly stated that errors in the alphabetical order had occurred in the letters placed in front of the letter-digit-letter triplet. Four of the participants in the low control demand condition incorrectly stated that this was the case in their version of the task as well,

**FIGURE 2 | Means of individual median reaction times.** On the *x*-axis, reaction times for short, medium, and long strings (s, m, l) are grouped together by block in order to display the amount of processing of irrelevant information. The impact of string length on RT is stronger in the high control demand condition as compared to the low control demand condition, indicating more processing of the additional letters when information reduction is not possible. Note that error trials as well as RT of trials with violations of the alphabetical order (high control demand condition) were excluded. Note that performance for the two conditions was very similar during the very first trials of Block 1 and quickly diverged afterward. This was evident when we compared (a) the trials of Block 1 that occurred before participants in the high control demand condition encountered the first strings with violation of the alphabetical order outside the letter-digit-letter triplet with (b) the yoked trials of the low control demand condition. As soon as participants in the high control demand condition were confronted with the strings including incorrect prefixes (RT from the latter trials being excluded from main analysis) RT differences between the conditions quickly developed. Error bars: between-subjects standard error of the mean.

while the others correctly reported that the prefixes had always been correct.

### **SLOWING BY OFF-SEQUENCE STIMULI**

In line with other implicit and incidental sequence learning studies we assessed sequence knowledge indirectly by comparing trials that follow the fixed repeating sequence with off-sequence trials at the end of practice. The RT difference between regular and deviant (plus following) trials in Block 7 is displayed in **Figure 3**. The ANOVA with control demand condition as between subjects factor showed a main effect of control demand, *F*(2,97) = 3.33, MSE <sup>=</sup> 11539.79, *<sup>p</sup>* <sup>=</sup> 0.04, <sup>η</sup><sup>2</sup> *<sup>p</sup>* = 0.064. Slowing was strongest for participants in the low control demand condition and weakest for those of the high control demand condition (these conditions yielded the only significant pair comparison according to Tukey-HSD, *p* = 0.04). The baseline condition lay in between.

### **SEQUENCE FOLLOWED IN AMBIGUOUS TRIALS**

**Figure 4A** suggests a practice-related increase in this dependent measure – the rate of ambiguous stimuli eliciting a response according to the repeating sequence. The mixed ANOVA with the factors block of practice and control demand condition showed a main effect of block of practice, *F*(3.48,337.48) = 15.78,

MSE <sup>=</sup> 444.96, *<sup>p</sup>* <sup>&</sup>lt; 0.001, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.14, and an interaction of practice and control demand condition, *F*(6.96,337.48) = 2.25, MSE <sup>=</sup> 444.96, *<sup>p</sup>* <sup>=</sup> 0.038, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.04, but no main effect of control demand condition, *F*(2,97) = 1.1. The increase in sequence following across blocks was strongest in the low control demand condition. As detailed below, between-participant variability in sequence-following in ambiguous trials was substantial. Therefore, we secured that the abovementioned pattern of results also holds with a more robust statistic. For this we determined the percentage of participants per condition and block of practice who showed above chance sequence following. We determined (based on the binomial distribution) how many sequence following responses within the 12 ambiguous trials per block of practice a participant should accumulate to be classified as an above-chance sequence follower for that block. Seven of 12 responses (i.e., >50% sequence following) are sufficient for *p* < 0.001. Supporting the above analysis, the percentage of sequence followers (**Figure 4B**) showed a similar pattern as the average rate of sequence following (**Figure 4A**). It increased the most in the low control demand condition, X<sup>2</sup> (2) <sup>=</sup> 6.93, *<sup>p</sup>* <sup>=</sup> 0.031, for the across-condition comparison of the rate in the last block of practice. Note that the Block 6 rate also mirrors the overall increase with practice, as all conditions started from 0 in Block 1.

Several participants eventually started to consistently respond to the randomly interspersed ambiguous trials according to what the fixed sequence would have suggested. Run analyses were employed to explore the consistency of sequence following. Guessing should lead to sequence-followed responses on individual ambiguous trials, but not on whole runs of them. Consistent replacement of random key presses to ambiguous stimuli by sequence memory-based responses was captured by determining the maximum run length of sequence-following responses in ambiguous trials. We used the ambiguous trials as probes of sequence following that were randomly inserted into the repeating sequence of regular trials. Thus, runs span over many regular

**FIGURE 4 |The average rate of % ambiguous trials the sequence was followed in the SRT increases over blocks of practice (chance level = 16.7%; A). (B)** Shows the proportion of participants using the sequence in at least 50% of the ambiguous trials of the respective block (i.e., *p* < 0.001 for that participant in that block). **(C)** Shows the distribution of sequence usage in the SRT. A larger proportion of participants of the low control demand condition as compared to the other conditions showed long chains of consistent sequence memory-based responses on randomly interspersed ambiguous trials. Error bars: between-subjects standard error of the mean or the proportion.

trials. For instance, a participant with a maximum run length of 30 has responded according to the fixed sequence without interruption for more than two blocks of practice (i.e., 12 ambiguous trials per block).

Cases where participants started to consistently respond according to the repeating sequence were especially pronounced in the low control demand condition. The maximum run length of sequence-consistent responses on subsequent ambiguous trials determined per participant was on average *M* = 8.9. It was *M* = 4.6 in the high control demand and the baseline condition. As depicted in **Figure 4C**, the distribution was heavily skewed in all conditions, as many participants did not show consistent usage of sequence knowledge in ambiguous trials. Yet, the low control demand condition yielded a high proportion of participants with especially long runs as compared to the other conditions. While 14 of the participants of the low control demand condition showed runs longer than four (four being the median of this condition; *p* < 0.001 for four consecutive hits; *Maximum* = 54 ambiguous trials), only six of the participants in both the high control demand condition and the baseline condition (*Maximum* = 30 and 29) showed sequence-consistent responses of the same run-length, <sup>X</sup>2(2)=7.74, *<sup>p</sup>* <sup>=</sup>0.025. In summary, different indicators converge in suggesting stronger usage of incidentally acquired sequence knowledge following the low control demand condition compared to the high control demand condition (and intermediate performance for the baseline condition).

#### **FOLLOW-UP ANALYSES ON ERROR RATES AND REACTION TIMES**

Unexpectedly, the mean error rate for the regular trials of Blocks 1 to 6 of the SRT (**Figure 5A**) was higher for the baseline condition (*M* = 5%) compared to the low control demand condition (*M* = 2.8%) and the high control demand condition (*M* = 3.4%). The baseline condition differed from the other two conditions according to Tukey-HSD (*p*s < 0.05). An ANOVA including block of practice and control demand condition showed a main effect of practice, as error rates decreased, *F*(3.27,316.744) = 5.08, MSE <sup>=</sup> 9.19, *<sup>p</sup>* <sup>=</sup> 0.001, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.05, and a main effect of control demand condition, *F*(2,97) = 8.16, MSE = 31.93, *p* < 0.001, η2 <sup>p</sup> = 0.14. There was no interaction of block and condition (*F* = 1.08).

An analysis of the error rates in Block 7 (**Figure 5B**) showed that participants produced more errors in deviant trials (compared to regular trials). Error rate increased when exclusively taking into account errors in line with the disrupted sequence, but also when only considering errors in which participants neither followed the sequence nor the current off-sequence stimulus. An ANOVA including the error rates in regular vs. in deviant trials resulted in a main effect of trial type, *F*(1,97) = 32.31, MSE = 112.2, *p* < 0.001, η2 <sup>p</sup> = 0.25. There was neither a main effect of nor an interaction involving control demand condition (*F*s < 1). A large proportion of errors in deviant trials were responses in line with what the repeating sequence would have suggested. A main effect of trial type (but no effects involving control demand condition) was also obtained, when comparing error rate on regular trials with the rate of sequence following in deviant trials, *F*(1,97) = 5.23, MSE <sup>=</sup> 73.82, *<sup>p</sup>* <sup>=</sup> 0.024, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.05. The pattern of a higher error rate in deviant as compared to regular trials also held when only

Error bars: between-subjects standard error of the mean.

considering errors that were not in line with the response suggested by the repeating sequence, *F*(1,97) = 7.18, MSE = 29.98, *<sup>p</sup>* <sup>=</sup> 0.009, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.07.

Last we analyzed how RT developed across blocks of practice in regular trials. While **Figure 5C** suggests that performance on regular trials was slowest in the high control demand condition, this was not confirmed by an ANOVA with block of practice and control demand condition as factors. We obtained a main effect of block of practice, reflecting that participants becamefaster over the six blocks of practice, *F*(2.38,230.94) = 132.56, MSE = 19705.33, *p* < 0.001, η<sup>2</sup> <sup>p</sup> = 0.58. However, there was neither a main effect of control demand condition, *F*(2,97) = 2.06, nor an interaction of block and control demand condition, *F*(4.76,230.94) = 1.59. Note that an ANOVA involving trial type (regular trials vs. ambiguous trials) and block of practice did not show a main effect or interaction involving control demand condition either (*F*s < 1).

### **VERBALIZABLE SEQUENCE KNOWLEDGE**

The three experimental conditions did not differ with respect to the frequency with which the matches between verbalized sequence parts and practiced sequence were obtained by random matching in the simulation. The average relative frequencies were 13.39, 14.27, and 15.01%, for the low and high control demand condition and the baseline condition respectively (*F* < 1). As we administered the interview after the test block containing deviant trials, one could suspect that the measure of verbalizable sequence knowledge is too noisy to be useful. However, we obtained significant Spearman rank correlations of the measure with RT slowing on deviant trials (*r* = −0.395) and with the proportion of ambiguous trials responded to according to the fixed sequence in the last block of practice (*r* = −0.501; *p*s < 0.001). Thus, participants showing stronger behavioral signs of sequence knowledge also verbalized sequence patterns that were less frequently obtain in a random matching simulation (i.e., their verbalization was less likely based on guessing).

### **DISCUSSION**

We observed transfer between two incidental learning tasks, the alphabet verification task and the SRT. Participants who had the opportunity to discover *and* apply (low control demand condition) a shortcut in the first task, were more likely to apply a different shortcut in the second incidental learning task compared to participants in the high control demand condition. Low demands to adhere to instruction-based task processing in the alphabet verification task (i.e., option to skip to check some string positions without that this would lead to errors) apparently were transferred to the SRT (i.e., respond based on sequence memory rather than based on stimuli). Less usage of sequence knowledge was observed in the high control demand condition. These participants had experienced that instruction-coherent task processing has to be maintained as a shortcut would lead to errors in the alphabet verification task. The participants of the baseline condition showed intermediate application of sequence knowledge.

The two incidental learning tasks employed were highly dissimilar in terms of stimuli, responses, and hidden regularity that could be exploited for task processing. Thus, the transfer across tasks rules out that stimulus-specific processing episodes rather than learning of control demands can accountfor the results. Rather, the experiment illustrates general demand effects – an issue important and hard to control in research with human participants. Hertwig and Ortmann (2001) have for instance suggested that research

participants in psychological experiments often search for hidden regularities in the task material, because they suspect that task instructions convey a misleading or incomplete picture of what the experiment is really about (see also Harlow, 1949; Gaissmaier and Schooler, 2008). After taking part in an incidental learning experiment, research participants might (oftenfalsely) assume that hidden task regularities might be waiting to be found and safe to exploit in other experiments of the same or maybe even other research labs. This might distract them from performing tasks as instructed, threatening the validity of studies not interested in incidental learning and instruction following.

As the task material of the low control demand condition was set up to support the belief that exploitable task regularities might exist, participants might have been inclined to also search and apply shortcuts in the SRT afterward. Crucially, participants in the low control demand condition experienced no costs (i.e., errors) in applying the shortcut (rather than processing the alphanumeric strings as instructed). The baseline condition tended to be more similar to the high control demand condition than to the low control demand condition. This would suggest a larger impact of experiencing the *lack* of the demand to control shortcut usage on performance in a subsequent incidental learning task (rather than experiencing the demand to continue instruction-coherent task processing). This might seem plausible if the demand to follow instructions is default and rewarded in everyday life (cf. Hayes et al., 1986, 2001; Törneke et al., 2008). Currently we cannot distinguish these variants as only the difference between the low and the high control demand condition was statistically robust.

The current study at least provides tentative evidence for distinguishing influences of control demands on applying shortcut options from influences on learning about these shortcut options in the first place (cf. ErEl and Meiran, 2011). In principle, participants in the low control demand condition might either have been better at learning about the fixed repeating sequence, better at applying it, once they have learned about it, or both. Our measure of verbalizable sequence knowledge did not differ between the control demand conditions (though it correlated with performance indicators, suggesting that it was sensitive). This suggests that the control demand conditions differed primarily in applying rather than in knowing the fixed repeating sequence in the SRT.

The finding of transfer between incidental learning tasks is remarkable given that researchers have struggled to obtain transfer between structurally equivalent thought problems (cf. Helfenstein and Saariluoma, 2006; Frensch and Haider, 2008; but see Green et al., 2010). In the current study participants seemed to transfer the knowledge that shortcut options might exist and can be safely exploited to a different incidental learning task presented subsequently. Verbal reports suggest that this knowledge was explicit. Currently we can only speculate on the role of verbal knowledge in transfer between incidental learning tasks as data for direct comparisons of transfer in incidental (i.e., with verbal knowledge) vs. implicit learning tasks (i.e., without verbal knowledge) are lacking. Note however that according to implicit learning studies at least some transfer seems to be possible even without verbal knowledge of the task regularity. For instance, Leber et al. (2009) reported that participants who have adopted one attentional set (feature search mode vs. singleton detection mode) in training transferred it to another session despite changes in the coloring of the search targets. Turk-Browne and Scholl (2009) reported that visual statistical regularities, with respect to temporal sequence, transferred to spatial sequencing and *vice versa*. Stadler et al. (2000; see also Newell and Bright, 2002) reported the transfer of implicit knowledge about defining features of number strings across formats (digits vs. words).

The finding of transfer of control demands is theoretically relevant as such task-general influences on performance imply the item-general operation of control processes. The current work might contribute to alter the perspective on cognitive control in strategy change. Some models of skill acquisition focus on the aspect that strategy change can help to overcome attention-demanding task processing by applying a (memorybased) shortcut (e.g., Logan, 1988, 1992). However, in his instance theory of automatization, strategy change (e.g., from calculating simple arithmetic problems to retrieving the answer from memory), is a mandatory consequence of task practice. As soon as the memory strength is sufficient, the shortcut is automatically applied. Importantly, transfer across tasks with different types of shortcuts operating on different types of task material is not to be expected according to the instance theory and related models of strategy change in skill acquisition (e.g.,Cousineau and Larochelle, 2004), because shortcuts are based on knowledge that has to be acquired individually for each stimulus (e.g., the correct solution to an arithmetic problem). According to this perspective, strategy change relying on *automatic* memory retrieval of answers to formerly presented problems can free attentional resources. There is neither room for transfer across incidental learning tasks, nor for control processes that might modulate whether or not shortcut knowledge is applied. This changes, if participants can decide to apply or not apply a shortcut option which they have incidentally learned (e.g., Touron and Hertzog, 2004a,b; Gaschler and Frensch, 2009). According to the learning-plus-decision perspective on strategy change in incidental learning, incidentally learning about a shortcut option could lead to a demand of cognitive control — namely when shortcut application leads to errors. The current study provides first evidence for that such control demands might transfer across incidental learning tasks. It extends recent work showing that learning processes involved in strategy change can generalize across specific stimuli within a task: Strategy change is not confined to learning a shortcut specifically for each stimulus (cf. Logan, 1988, 1992), but instead transfers across stimuli within a task (cf. Gaschler et al., 2014a). For instance, Wilkins and Rawson (2010, p. 1134) conceptualized item-general practice gains as performance improvements "that accrue to all stimulus tokens of a given type, including both practiced and novel tokens of that type." The current work suggests that this might even include different tasks.

Apart from the learning-plus-decision perspective on strategy change discussed above, there is another theoretical perspective that can account for transfer between incidental learning tasks, but makes different predictions for the specific pattern of transfer that should occur: theories that places emphasis on potential psychological resources needed to refrain from shortcut usage. According to research on ego depletion (e.g., Baumeister et al., 2007; Hagger et al., 2010), working on a demanding task can exhaust a control resources that are then not available for the next task to come. Assuming that high demand conditions deplete cognitive control resources more than low demand conditions would have led to the following prediction: Working on a task that demands to refrain from using a shortcut option should have led to more shortcut usage in a later incidental learning task compared to a condition in which participants did not have to refrain from applying a shortcut in the first task. The least depletion of control resources should have taken place if participants do not have to work on a prior task at all. Thus, the baseline condition lacking experience with either variant of Task 1 should have shown the least shortcut usage. Different from these predictions, we obtained the strongest shortcut usage in the SRT in the low control demand condition. The demand to refrain from using a shortcut option in Task 1 should have diminished the capability to secure adherence to instructions in Task 2. As the alphabet verification task is tedious even when a part of the material can be skipped, the low control demand condition should have shown an intermediate level of shortcut usage, while it should have been lowest in the baseline condition (i.e., SRT only, hence least depleted). As we did not include independent measures of depletion (e.g., a pre–post-test comparison of selfreported fatigue) we are cautious to over-interpret our results with respect to resource-theories of self-control. Note that the unexpected high error rate on regular trials in the baseline condition is at odds with the resource perspective as well – rather predicting a lower error rate in the least depleting condition. Instead, our results are in line with theories that conceptualize strategy change in incidental learning tasks as a phenomenon involving (a) learning of the task regularity and (b) a decision to apply or not apply the shortcut (e.g., Strayer and Kramer, 1994; Touron and Hertzog, 2004a,b; Haider and Frensch, 2005; Haider et al., 2005).

While past work has documented that shortcut application can take place in an all-or-none manner, generalizing even to novel stimuli within a task (e.g., Gaschler and Frensch, 2007; Gaschler et al., 2014a), the current work, in addition, presents first evidence for transfer across different incidental learning tasks. Distinguishing between influences of specific processing episodes versus adaptation to general task structure is a key-problem shared by the literature on conflict adaptation (e.g., Jacoby et al., 2003; Mayr et al., 2003; Ullsperger et al., 2005; Schmidt and Besner, 2008) and the literature on strategy change in skill acquisition. One research strategy to accumulate evidence for adaptation to control demands (rather than to specific processing episodes with specific stimuli) has been the study of transfer of control from one task to another in task switching (e.g., Egner, 2008; Fernandez-Duque and Knight, 2008; but see Rünger et al., 2010). In that work the focus is on transfer of control between tasks on a trialby-trial basis. Others, have focused on learning of parameters controlling strategy selection over many trials (e.g., Gray et al., 2006; Gaschler and Frensch, 2009; Schouppe et al., 2014). Models of strategy selection (e.g., Rieskamp and Otto, 2006; Marewski and Schooler, 2011) might be expanded such that they can capture task-general learning of applicability vs. non-applicability of shortcuts.

Last we would like to highlight that it is interesting to consider alternative task orders to study transfer across incidental learning tasks. Transfer of control demands across incidental learning tasks could be studied in either direction taking the alphabet verification task or the SRT as independent and dependent variable or *vice versa*. Control demands could be manipulated in the SRT by varying the amount of randomly inserted stimuli breaking the repeating sequence (cf. Verwey and Wright, 2014). However, for issues tied to task difficulty, we decided to use performance in the alphabet verification task as the independent variable in our experiment, varying whether participants (a) could safely apply a shortcut option (b) should not apply the shortcut or (c) did not have to work on this task at all. While the SRT is instructed as a simple choice reaction task and can be solved at reaction time levels of one second or less per trial – even without applying a shortcut – the alphabet verification task is much more tedious. Reaction times rarely reduce below three seconds per trial. From the perspective of the ego depletion theory, this task should exhaust more control resources when participants have to refrain from applying a shortcut and less, when control demands are low. Yet, even when participants can safely use the shortcut and skip to check some positions of the alphanumeric strings, each trial still contains a substantial amount of string positions to be checked. Thus, even the low control demand condition should be affected by exhaustion of control resources and thus show more shortcut usage in Task 2 as compared to the baseline condition.

In the current setup we tested whether being able to use vs. having to forego using a shortcut option in a demanding task affects shortcut usage in second incidental learning task. Reversing the order of the incidental learning tasks in future studies could additionally challenge control resource accounts. Assuming that the SRT is comparatively less demanding, withholding shortcut usage in the SRT should not lead to a substantial exhaustion of control resources. From this perspective, shortcut usage in the alphabet verification task should not differ depending on prior applicability of sequence knowledge in the SRT. The learningplus-decision perspective on strategy change however suggests that providing participants with the opportunity to find and apply a shortcut in a relatively easy task could strengthen shortcut usage in a more difficult task provided later on. Experiments on shortcut usage in arithmetic (Godau et al., 2014) indeed reflect that that offering an easy-to-find shortcut option can increase later shortcut usage. Therefore, the sequential regularity in the SRT (which can be detected and applied rather easily) could foster later shortcut usage in the alphabet verification task, if the tasks would be applied in the reversed order.

In summary, the present study offers a cognitive control perspective on strategy change in incidental learning tasks. In line with theories conceptualizing strategy change in incidental learning as a learning-plus-decision phenomenon, we observed transfer of control demands across incidental learning tasks. This provides further evidence for that control processes can be distinguished from adaptation to the specific material practiced.

#### **ACKNOWLEDGMENTS**

This work was supported by the Max Planck Research School on the Life Course and the Interdisciplinary Laboratory Image Knowledge Gestaltung, and by the grant WE 2852/3-1 by the Deutsche Forschungsgemeinschaft (DFG).

### **REFERENCES**

**Conflict of Interest Statement:** The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

*Received: 01 July 2014; accepted: 13 November 2014; published online: 28 November 2014.*

*Citation: Gaschler R, Marewski JN, Wenke D and Frensch PA (2014) Transferring control demands across incidental learning tasks – stronger sequence usage in serial reaction task after shortcut option in letter string checking. Front. Psychol. 5:1388. doi: 10.3389/fpsyg.2014.01388*

*This article was submitted to Cognition, a section of the journal Frontiers in Psychology. Copyright © 2014 Gaschler, Marewski, Wenke and Frensch. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) or licensor are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.*

## Resolved but not forgotten: Stroop conflict dredges up the past

### *Eliot Hazeltine\* and J. Toby Mordkoff*

*Department of Psychology, University of Iowa, Iowa City, IA, USA*

#### *Edited by:*

*James R. Schmidt, Ghent University, Belgium*

#### *Reviewed by:*

*Senne Braem, Ghent University, Belgium Mine Misirlisoy, Middle East Technical University, Turkey*

*\*Correspondence: Eliot Hazeltine, Department of Psychology, University of Iowa, 11 Seashore Hall East, Iowa City, IA 52242-1407, USA e-mail<EMAIL_ADDRESS>The magnitude of congruency effects depends on, among other things, the specifics of previous trials. To explain these modulating effects, a host of mechanisms by which previous trials affect the processing of relevant and irrelevant information on the present trial have been proposed, including feature repetition advantages, negative priming, itemspecific proportion congruency (ISPC) effects, display frequency effects, and sequential modulations of both congruency and frequency effects. However, few experiments have been designed to independently manipulate these factors. In the present study, we used a four-choice Stroop task in which we hold constant the frequencies of the stimulus features and responses, but manipulate the frequencies of their conjunctions. We modified the procedure used by Jacoby et al. (2003), under which the possible word–color pairings differed in terms of proportion occurrence, by adding neutral trials to obtain independent estimates of the effects of display frequency. The results indicate that feature repetitions, display frequency, and sequential modulations of both congruency and frequency effects all affect response time. However, no evidence for an ISPC effect was obtained; the display frequency effect measured on the neutral trials accounted for all differences in the congruency effect, as proposed by Schmidt and Besner (2008). Sequential modulations of congruency effects were observed when the overall proportion of congruent trials was held to a chance level and marginal display frequency was also held constant.

**Keywords: conflict adaptation, contingency, executive control, response conflict, response conflict adaptation, congruency sequence effect, ISPC effect**

### **INTRODUCTION**

Our perceptual worlds are cluttered with information, only a small fraction of which should drive behavior at a given time. Thus, it is necessary to differentiate between behaviorally relevant and irrelevant sources of information so that we do not reflexively act on the biggest, shiniest object we perceive. To study selection processes, researchers use the Stroop (1935), Simon (1969), and Eriksen and Eriksen (1974) tasks. These have revealed that selection is imperfect; performance is typically worse on incongruent trials, where the irrelevant and relevant sources of information indicate different responses, than on congruent trials, where the irrelevant and relevant sources of information indicate the same response.

### **SEQUENTIAL MODULATIONS OF CONGRUENCY EFFECTS**

Among the many factors influencing the effectiveness of our ability to select a source of information are immediately previous events. Gratton et al. (1992) is credited as being the first to report that the magnitude of the difference in response times (RTs) between incongruent and congruent trials is larger following a congruent trial than following an incongruent trial. This phenomenon has since been given many names, including conflict adaptation (Botvinick et al., 2001), the Gratton effect (Notebaert and Verguts, 2008), sequential modulation (Hazeltine et al., 2011b), and the congruence sequence effect (Lee and Cho, 2013). Given that one goal of this paper is to examine the various sources that

might contribute to this effect, we will use the atheoretical term "sequential modulation."

When discovered in a flanker task, sequential modulations were thought to reflect the operation of control mechanisms that dynamically weight the various sources on information in concert with task goals. Following Botvinick et al.'s (2001) influential paper proposing a model in which response conflict triggered a control process that changes the relative weightings of taskrelevant and task-irrelevant information, a sizeable literature emerged examining sequential modulations (e.g., Ullsperger et al., 2005; Wendt et al., 2006; Akçay and Hazeltine, 2007, 2011; Chen and Melara, 2009; Schmidt and De Houwer, 2011; Schmidt, 2013a), their time course (e.g., Notebaert et al., 2006; Egner et al., 2010; Duthoo et al., 2014), and their boundary conditions (e.g., Kiesel et al., 2006; Egner et al., 2007; Freitas et al., 2007; Akçay and Hazeltine, 2008; Notebaert and Verguts, 2008; Funes et al., 2010; Hazeltine et al., 2011b; Lee and Cho, 2013; Braem et al., 2014; Kim and Cho, 2014).

However, as researchers have probed deeper into this phenomenon, a host of potential ways that a previous trial can affect the current one has emerged (see Schmidt, 2013a). The claim that sequential modulations reflected changes in the weighting of particular stimuli or stimulus dimensions was first challenged by Mayr et al. (2003), who noted that many experiments examining sequential modulations used two-choice tasks so that when a congruent trial followed a congruent trial or an incongruent trial followed an incongruent trial, exact repetitions of the stimuli were possible, but when an incongruent trial followed a congruent trial or a congruent trial followed an incongruent trial, no exact repetitions were possible. In other words, the shorter RTs stemming from exact repetitions of stimuli (and the absence of the requirement to rebind stimulus features, see Hommel et al., 2004) only benefits congruent trials following congruent trials and/or incongruent trials following incongruent trials. Thus, the pattern of RTs attributed to control processes changing the weightings of various sources of information could be accounted for simply in terms of the effects of repetitions and alternations of stimulus features.

To address this confound, many researchers turned to fourchoice tasks, in which all types of congruency sequences can be obtained using stimulus features that did not appear on the immediately preceding trial. Many studies (Ullsperger et al., 2005; Akçay and Hazeltine, 2011; Hazeltine et al., 2011a,b; Lee and Cho, 2013; Kim and Cho, 2014) restrict the analyses of sequential effects to complete alternations, which can be done for all two-trial sequences of congruent and incongruent trials when the task is four-choice. It is also possible to remove trials in which the irrelevant feature on the previous trial indicates the same response as the relevant feature on the current trial (negative priming trials) and trials in which the relevant feature of the previous trial indicates the same response as the irrelevant feature of the current trial, given that these types of transitions may also affect RT, but these are less consistently eliminated from analyses of sequential modulations.

However, the use of four-choice tasks, even when all types of repetitions are removed, can give rise to additional issues for examining sequential modulations. In a typical four-choice conflict task, there are four possible relevant stimulus features each associated with a unique response and four possible irrelevant stimulus features each associated with one of those responses. When the relevant and irrelevant features are randomly paired, only 1/4 of the trials are congruent. Thus, a sequence of two congruent trials represents only 1/16 of the two-trial sequences, whereas a sequence of two incongruent trials, for example, represents 9/16 of the two-trial sequences. This imbalance changes depending on which feature repetitions are eliminated from the analyses (for a full discussion of this issue, see Mordkoff, 2012), but some researchers (e.g.,Akçay and Hazeltine, 2007, 2011; Hazeltine et al., 2011b) have opted to increase the rate of congruent trials to obtain more balanced numbers of trials in each of the cells for the analysis, as well as to maintain an equal probability of congruent and incongruent trials.

### **DISPLAY FREQUENCY AND CONTINGENCY**

And yet increasing the probability of congruent trials causes at least two new confounds with other potential contributors to RT: display frequency and contingency. Display frequency refers to the likelihood of a particular stimulus (i.e., combination of relevant and irrelevant information) appearing on a given trial. To make congruent trials as frequent as incongruent trials in standard four-choice designs as described above, each congruent stimulus must appear three times as often as any given incongruent stimulus, because there are three times as many incongruent stimuli

as congruent stimuli. It has been shown that more frequently presented stimuli produce shorter RTs than less frequently presented stimuli (Hick, 1952; Hyman, 1953).

Contingency effects emerge when the relative likelihood of a particular task-relevant feature or response given a particular taskirrelevant feature is different from the overall (or unconditional) probability of that particular task-relevant feature or response. For example, in a Stroop task where the red-colored stimuli are the word "RED" on 1/2 of the trials, and the words "GREEN," "BLUE," and "YELLOW" each appear 1/6 each, not only is RED-inred more frequent than GREEN-, BLUE-, or YELLOW-in-red, but contingencies now exist between the task-irrelevant word "RED" and the task-relevant red color and, therefore, the "red" response. Thus, even though participants are instructed not to attend to the word, it contains information indicating the likely response. Humans are highly sensitive to these contingencies, even when they occur in sources that are to be ignored (Miller, 1987; Mordkoff, 1996).

In this way, both display frequency and contingency may act to reduce RTs to congruent stimuli. Note that in Stroop tasks, where there is a one-to-one mapping between values of the relevant feature and the responses, it is not possible to distinguish between display frequency effects and contingency effects. Note, also, that there is evidence that performance can be affected by the frequency and contingencies that are associated with conjunctions of features, even when these conjunctions are unattended (Mordkoff and Halterman, 2008). While the effects of frequency and contingency are typically insufficient on their own to account for sequential modulations, they can contaminate measures of the congruency. Also, there is evidence that contingency effects may themselves be subject to sequential modulations (Schmidt et al., 2007). That is, the effects of contingency may be larger after trials in which a more frequent pairing of irrelevant and relevant information was presented than after trials in which a less frequent pairing was presented. Thus, the sequential modulation of contingency may be misinterpreted as the more standard modulation of congruency if congruency and contingency are confounded.

### **DISPLAY FREQUENCY, CONTINGENCY, AND THE ITEM-SPECIFIC PROPORTION CONGRUENCY (ISPC) EFFECT**

Display frequency and contingency effects not only complicate the interpretation of sequential modulations, but, as noted by Schmidt and Besner (2008), they can also provide an alternative explanation for the item-specific proportion congruency (ISPC) effect reported by Jacoby et al. (2003). It had been established that the magnitude of congruency effects depended on the overall proportion of congruent trials (Logan and Zbrodoff, 1979; Tzelgov et al., 1992), but Jacoby et al. (2003) found that the magnitude of the congruency effect for a given task-irrelevant feature can depend on the proportion of trials on which that particular feature is paired with a congruent versus incongruent task-relevant feature. Jacoby et al. (2003) concluded that item-specific processes modulate the influence of task-irrelevant information in the Stroop task, a proposal that has been incorporated into recent models of sequential modulations (e.g., Verguts and Notebaert, 2008; Blais and Verguts, 2012). The proposal that control is implemented

in a feature-specific manner has broad implications for theories of attention and executive function, so determining whether the ISPC effect does indeed reflect the tracking of the usefulness of individual feature values is a critical issue.

However, in Stroop tasks in which some word–color pairs are presented more frequently than others, irrelevant features become predictive of both relevant features and correct responses, and Schmidt and Besner (2008) showed that such contingencies could completely explain the pattern of results without appealing to differences in attentional control (see also, Grandjean et al., 2013). While both frequency and contingency provide possible explanations for the ISPC effect, the design used by Jacoby et al. (2003) did not allow for the independent measurement of these effects, because both were confounded with the putative ISPC effect. To address this, Schmidt (2013b) designed a Stroop task in which there were three types of incongruent trials: frequently paired colors and words with words that were usually incongruent (high/low), infrequently paired colors and words with words that were usually incongruent (low/low), and infrequently paired colors and words with words that were usually congruent (low/high). The high/low were performed 40 ms faster than the low/low trials, indicating a robust contingency effect, but there was no difference in RT for the low/high and low/low trials, suggesting that the proportion congruence had little impact on performance.

Thus, there is evidence to suggest that the ISPC is really driven by contingency. Here, we directly test whether ISPC effects and display- frequency/contingency effects are approximately the same size to determine if the latter can account for the former. In essence, the question is whether a specific feature value (e.g., the word "red") can be associated with something abstract like congruence or incongruence rather than being associated with a particular response.

### **EXPERIMENT**

The goal of the present study was to tease apart the various potential modulators of congruency effects: repetition effects, frequency (and contingency) effects, and sequential modulations. To do this, we use a four-choice Stroop task in which we hold constant the marginal frequencies of the relevant and irrelevant stimulus features, as well as the responses, but manipulate the frequencies of their conjunctions. We modify the procedure used by Jacoby et al. (2003) and Schmidt and Besner (2008) in which the possible word–color pairings differ in terms of the proportion of trials on which they occur (display frequency; see also, Schmidt, 2013b). In a Stroop task where there is a one-to-one mapping between the relevant stimulus feature (color) and the response, changing the display frequencies of individual color/word pairings necessarily changes the proportion of congruence for the particular words. That is, the proportion congruence of a word can be increased only by making the congruent color/word pairs more frequent than the incongruent color/word pairs. In order to decrease the proportion congruence of a word, it must be presented in an incongruent color more frequently than in the congruent color. Therefore, to obtain separate and independent measures of the effects of frequency in the absence of congruency, we include neutral trials. On these trials, the irrelevant word is not associated with an option within the

response set, but different words appear more frequently in some colors than in others, matching (exactly) the frequency differences of the congruent and incongruent trials.

### **METHOD**

### *Participants*

One hundred and six undergraduate students (58 females) at the University of Iowa participated to fulfill their course requirements. All were self-reported to be native English speakers with correctedto-normal vision. Participants provided informed consent but were naïve to the study's design and purpose.

### *Stimuli and apparatus*

The stimuli were presented against a black background on a 17 inch LCD monitor of a personal computer. The viewing distance was approximately 120 cm. Visual basic software was used to control and present the stimuli. The Speech Recognition software from Windows XP was used to record the RT and accuracy of each trial.

Four ink colors (red, yellow, green, and blue) were paired with four color words (RED, BLUE, YELLOW, and GREEN) and four neutral words (CAR, LINE, FOLDER, and SHIRT) to form Stroop trials and neutral trials (see **Table 1**). All colors were presented at chance level (16 of 64 presentations) and all words were presented at chance level (8 of 64 presentations), as well. The overall proportion congruent of the block was at chance level (8 of 64 presentations). The trial frequencies of the neutral trials were selected to match those of the congruent and incongruent Stroop trials. The four neutral words (CAR, LINE, FOLDER, and SHIRT) were chosen to match the length of the color words.

To manipulate item frequency, the pairings of colors and words was arranged so that for each color there was one color word and one non-color word paired with it four times every 64 trials (frequent pairing), one color word and one non-color word paired with it twice every 64 trials (moderate pairing), and two color words and two non-color words paired with it once every 64 trials (infrequent pairing; see **Table 1**). Participants were randomly assigned to one of four color-word pairing mappings so that the roles of the four colors were counterbalanced across participants. With this arrangement, we were able to vary the frequencies for the contingencies between words and colors while having a neutral match for each congruent and incongruent word.

### *Procedure*

Each trial started with a fixation cross of 500 ms. After a blank of 300 ms, target stimulus was presented. Participants were instructed to name the ink color as quickly and accurately as possible. Participants had 5,000 ms to respond. After an incorrect response, a display with the words "you said:" followed by the word recorded by the voice recognition system on one line and "correct response:" followed by the correct color name on another line. All of the words in the error display were white presented on a black background. The incorrect response and correct word were presented in white for 1000 ms following an error trial. After a correct response or the error display, a blank display was presented for 700 ms. Participants performed 15 blocks of 64 trials each. The first two blocks were treated as practice blocks.

**Table 1 | Example design in terms of display frequency as a function of task-relevant color and task-irrelevant word.**

*Row labels (in lower case) indicate colors; column labels (in upper case) indicate words. Table entries (numbers) indicate trials per block. Numbers in bold indicate congruent trials. PC indicates the proportion congruence for a word; C, chance.*

### **RESULTS AND DISCUSSION**

Two participants were removed from the analysis due to the malfunctioning of the speech recognition system. The mean proportion correct was 0.97. Inspection of the cell means of accuracy indicated that any effects of accuracy would be small (<3%), so our analyses focused on RT. The first two trials of each block, error trials (2.8%), trials immediately following an error trial (2.8%), and trials with RTs less than 150 ms (3.0%) or greater than 2,000 ms (0.3%) were excluded from the analysis.

### *Repetition effects*

Our questions concern the various ways that the composition of previous trials affects performance on subsequent trials (see Dalrymple-Alford and Budayr, 1966), so we first assessed the effects relating to feature repetitions. Five types of trials were considered: trials with no repeated features (NO), trials in which the relevant feature (color) repeated (CC), trials in which the irrelevant feature (word) repeated (WW), trials in which the relevant feature on the previous trial indicated the same response as the irrelevant feature on the current trial (CW), and trials in which the irrelevant feature on the previous trial indicated the same response as the relevant feature on the current trial (WC). We eliminated from the analysis trials in which multiple forms of repetition occurred. Because the frequencies of these various forms of repetitions differ depending on the congruency of the previous and current trial, we restricted our analyses to incongruent trials that followed incongruent trials. Furthermore, to avoid any confounding effects of frequency (the mean frequencies of the four repetition types and control trials differed), we also restricted the analyses to frequent color-word pairings. It was not possible to hold constant the frequency of the previous trial, because this eliminated the possibility of WW and CC trials. Moreover, with these restrictions, it was not possible to perform an ANOVA with the presence/absence of each type of repetition as a factor. Instead, we performed a one-way ANOVA on these five trial types, which revealed a significant effect, *F*(4,408) = 34.26, *p* < 0.0001.

To examine this finding more closely, we directly compared each repetition type (CC, CW, WC, and WW) to the NO trials (**Figure 1**). Because our focus was on the potential contaminating effect of these repetitions on measures of congruency rather than on the repetition effects themselves, we adopted a liberal statistical threshold uncorrected for multiple comparisons. RTs on the trials

on which only color repeated (CC) were 109 ms shorter (575 ms) than RTs on NO trials, *t*(103) = 8.16; *p* < 0.0001. RTs on the trials on which only the word repeated (WW) were 31 ms shorter (653 ms) than RTs on NO trials, *t*(103) = 2.40; *p* < 0.05. Thus, the benefit associated with having to inhibit the same irrelevant word that had to be inhibited on the previous trial was larger than any cost associated with rebinding a repeated word with a novel color. The mean RT for CW trials (657 ms) was 27 ms faster than for NO trials, *t*(103) = 2.42; *p* < 0.05. Because we analyzed only incongruent trials, this result suggests that it is easier to suppress an inappropriate response when it was produced on the immediately preceding trial. Finally, the mean RT on WC trials (690 ms) was 6 ms longer than NO trials, but this difference was not significant, *t* < 1. Thus, there was little evidence that this form of negative priming affected RT in this experiment.

The absence of any costs associated with partial repetitions was unexpected (see, e.g., Hommel, 1998), so to further examine whether rebinding costs played a role in RT, we examined sequences of neutral trials in which the irrelevant word was not associated with a color and therefore should not have produced much response competition. Frequent neutral word–color combinations following neutral word–color combinations produced mean RTs of 578 ms when no features repeated. When only the word repeated, these trials produced RTs of 582 ms, which was not significantly different, *t* < 1. This finding suggests that rebinding costs did not play a major role in the RT in the present experiment, possibly because there were many possible relevant and irrelevant features.

#### *Frequency and the ISPC effect*

Three of the four types of repetition (CC, WW, CW) produced effects on RT on their own that were similar or greater in magnitude to some modulations of congruency effects. Therefore, we adopted a conservative approach and eliminated trials with any of the four possible forms of repetitions before testing whether display frequency is sufficient to account for the ISPC effect. Moreover, because frequency may modulate congruency effects, as in the ISPC effect, we first examined frequency in the neutral trials only. Note that with the present design, the effects of display frequency and contingency are confounded, so we use the term "frequency" to refer to the combined effects of both. An estimate of the frequency effect was obtained with a one-way ANOVA, which revealed a significant effect, *F*(2,206) = 10.02, *<sup>p</sup>* <sup>&</sup>lt; 0.0001, MSE <sup>=</sup> 356.16, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.09. Within the neutral trials, frequent combinations of relevant and irrelevant features produced RTs of 577 ms, chance combinations produced RTs of 582 ms, and infrequent combinations produced RTs of 589 ms.

Our next step was to determine whether the frequency effect could account for any observed ISPC effect in the congruent and incongruent trials. Thus, we first determined whether the data indicated ISPC effects and then assessed whether this effect could be explained by frequency as measured in the neutral trials. Therefore, we categorized each trial according to whether the task-irrelevant word was paired with a congruent color frequently (1/2 of trials that the word appeared), at chance (1/4 of trials) or infrequently (1/8 of trials; see **Table 1**) as in Schmidt and Besner (2008). The data were then submitted to a two-way ANOVA with this factor and congruency (without the neutral trials).

There was a significant main effect for congruency, *<sup>F</sup>*(1,103) <sup>=</sup> 241.34, *<sup>p</sup>* <sup>&</sup>lt; 0.0001, MSE <sup>=</sup> 6158.87, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.70, but not for the proportion of congruency of the word, *F* < 1. Critically, the interaction between the two factors was significant, *<sup>F</sup>*(2,206) <sup>=</sup> 4.59, *<sup>p</sup>* <sup>&</sup>lt; 0.05, MSE <sup>=</sup> 1972.60, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.43, indicating a significant ISPC effect. When the irrelevant word was frequently congruent, the congruency effect was 111 ms (incongruent 688 ms; congruent 577 ms). When the irrelevant word was congruent at a chance rate, the congruency effect was 97 ms (incongruent 683 ms; congruent 586 ms), and when the irrelevant word was infrequently congruent, the congruency effect was 85 ms (incongruent 678 ms; congruent 593 ms).

However, as pointed out by Schmidt and Besner (2008), this analysis confounds frequency and ISPC effects, so we next examined whether this effect could be accounted for with the frequency effect as measured in the neutral trials. For congruent trials, pairs that include frequently congruent words are themselves more frequent; that is, the frequency of the word–color combination and the proportion that the word is paired with a congruent color is perfectly confounded for congruent trials. Thus, differences in

the effect of frequency on the congruent trials and the effect of frequency on the neutral trials provide evidence for an ISPC effect. Frequent congruent trials were performed 16 ms faster than infrequent congruent trials (577 vs. 593 ms), and frequent neutral trials were performed 12 ms faster than infrequent neutrals trials (577 vs. 589 ms); the magnitude of the frequency effect did not differ for the two trial types, *t* < 1 (**Figure 2A**), so it does not appear that the RTs of congruent trials are affected by the proportion of trials in which the word is congruent beyond what would be expected by the proportion of trials in which the word is paired with that color.

Of course, congruent trials represent only one half of the congruency effect, and thus do not provide a strong test of whether the ISPC effect can be accounted for by frequency effects on their

**FIGURE 2 | (A)** Frequency effects for congruent (open circles) and neutral (filled squares) trials with the overall mean of the trial type (congruent or neutral) subtracted out. **(B)** The change in the magnitude of the congruency effect (the ISPC effect) as observed in the congruent and incongruent trials (filled squares) and estimated from the neutral trials (open circles).

own. However, while frequency and proportion congruent are perfectly confounded in the congruent trials, the relationship between the two factors is much more complex for the incongruent trials. For example, the infrequent incongruent stimuli are composed of words that are frequently incongruent, incongruent at chance rate and infrequently incongruent. In short, the effect of frequency on the incongruent trials is less informative regarding the effect of proportion congruency than the congruent trials, because of the complex relationship between the two factors.

The critical question is whether the observed frequency effect in the neutrals can account for the interaction between frequency and proportion congruent (that is, the ISPC effect) in the congruent and incongruent trials. However, when determining the congruency effect for frequently congruent words, for example, RTs from trials in which the word is frequently paired with the congruent color are compared to RTs from trials in which the same word is paired with other colors that it appears with less frequently. Similarly, when determining the congruency effect for the infrequently congruent words, RTs from trials in which the word is infrequently paired with the congruent color are compared to RTs from trials in which the same word is paired with a mixture of other colors that were not infrequently paired with the word.

Therefore, to evaluate whether the ISPC effect could be explained by display frequency, we calculated for each participant the expected change in the magnitude of the congruency effect based on the frequency effect observed in the neutral trials and the proportions of frequent, chance, and infrequent pairings making up the incongruent trials. This procedure predicted a 25 ms change in the congruency effect between trials with frequently congruently words and trials with infrequently congruent words, which was similar to the observed 26 ms change in the congruency effect (i.e., the ISPC effect), *t* < 1 (**Figure 2B**). In short, it appears that display frequency can account for the ISPC effect without assuming that individual irrelevant items have individually modulated congruency effects based on the likelihood that the irrelevant item is congruent. Consistent with the conclusions of Schmidt and Besner (2008), there is no evidence for item-specific control processes.

#### *Sequential modulations*

We now return to the debate about whether sequential modulations of congruency effects can be observed without repetition and frequency confounds (e.g., Mayr et al., 2003; Hommel et al., 2004; Ullsperger et al., 2005; Akçay and Hazeltine, 2007, 2011; Hazeltine et al., 2011b; Schmidt, 2013a). To examine this in the present data set, we selected the trials without any of the four types of repetitions and looked only at the most frequent combinations of colors and words because, with repetitions removed, the different types of transitions consist of trials with different mean frequencies. These criteria led to five participants not having any trials in which a congruent trial followed a congruent trial, so these individuals were removed from the analysis. The data from remaining 99 participants were submitted to a two-way ANOVA with previous congruency and current congruency as factors. This produced main effects previous congruency, *F*(2,196) = 15.86, *p* < 0.0001, MSE <sup>=</sup> 3833.75, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.14, congruency, *F*(2,196) = 169.41, *<sup>p</sup>* <sup>&</sup>lt; 0.0001, MSE <sup>=</sup> 6259.28, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.63, and an interaction between

the two factors, *F*(4,392) = 6.45, *p* < 0.0001, MSE = 2706.71, η2 <sup>p</sup> = 0.06.

As depicted in **Figure 3**, the congruency of the previous trial affects the magnitude of the congruency on the current trial, even when repetitions and contingency effects are accounted for. The pattern is somewhat atypical in that the smallest congruency effects are observed after neutral trials (83 ms) rather than after incongruent trials (111 ms). As is typical when sequential modulations are observed, the congruency effect was largest (134 ms) after congruent trials.

Finally, we examined whether the frequency effect was moderated by the frequency of the previous trial (see, Schmidt et al., 2007). To do this, we looked at neutral trials that followed neutral trials, so that sequential modulations of frequency effects would not be confounded with sequential modulations of congruency effects. A two-way ANOVA with current frequency and previous frequency as factors, looking only at trials with no repetitions of any kind, revealed a significant effect of current frequency, *<sup>F</sup>*(2,206) <sup>=</sup> 3.77, *<sup>p</sup>* <sup>&</sup>lt; 0.05, MSE <sup>=</sup> 2271.17, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.04, and a significant interaction between current frequency × previous frequency, *<sup>F</sup>*(4,412) <sup>=</sup> 2.41, *<sup>p</sup>* <sup>&</sup>lt; 0.05, MSE <sup>=</sup> 2364.36, <sup>η</sup><sup>2</sup> <sup>p</sup> = 0.02. The difference between frequent items and infrequent items was 1 ms following infrequent items, 21 ms following moderately frequent items and 7 ms following frequent items. Thus, while the interaction was significant, replicating Schmidt et al. (2007), the effect appeared to be small and, as above, non-monotonic. Nonetheless, this finding indicates that when congruency is confounded with frequency, the source of sequential modulations is ambiguous.

#### **GENERAL DISCUSSION**

In the present study we sought to assess the various contributors to the magnitude of congruency effects using a four-choice Stroop task with neutral trials and a large number of participants. The results indicate that the majority factors did indeed impact performance, making them candidate sources of changes in the

**FIGURE 3 | Response times for the congruent (open circles), neutral (gray squares), and incongruent (black diamonds) as a function of the congruency of the previous trials.**

congruency effect. Feature repetitions, frequency, and sequential modulations of both congruency and frequency all produced significant effects on RT when the other factors were held constant.

The present findings make three principle contributions. First and most generally, they indicate RTs depend on a host of factors. While these factors are difficult to dissociate, in the present study we ran a relatively large number of subjects and manipulated item frequency independently from the frequency of individual features (e.g., the color blue or the word "shirt"), which was held constant. Under these conditions, it was apparent that repetitions of irrelevant sources of information shortened RT.

Second, the findings demonstrate that trial-frequency effects (and/or contingency effects), as measured in neutral trials, are of a magnitude that is sufficient to allow them to account for the ISPC effect on their own. That is, while previous work (e.g., Schmidt and Besner, 2008; Schmidt, 2013b) demonstrated that contingency effects provided a possible explanation for the ISPC effect, the present findings indicate that the ISPC effect is the same magnitude as what is predicted by the contingency effect, as measured in the neutral trials. Thus, we conclude that there is no evidence for an ISPC effect.

Third, the findings indicate that sequential modulation of congruency effects can be observed when feature repetitions, negative priming, and frequency effects are all controlled, and congruent and incongruent trials occur at overall frequencies equal to chance. While previous studies have shown that sequential modulations can occur without contingency effects (e.g., Kim and Cho, 2014; Schmidt and Weissman, 2014; Weissman et al., 2014), the present study shows that sequential modulations and contingency effects can co-occur, indicating that the former do not only emerge in the absence of the latter (see Bugg, 2014). Moreover, just one eighth of the trials in the present experiment were congruent, which may account for the somewhat unusual pattern of sequential modulations (**Figure 3**). The relative relatedness between the congruent and incongruent words may also have affected the pattern of sequential modulations, just as it may have affected the pattern of partial repetitions. This would explain why congruency effects were smallest after neutral trials rather than after incongruent trials. In any case, the data suggest that the congruency of the previous trial can affect the magnitude of the congruency effect on the current trial independent of feature repetitions and display frequency.

In sum, the data indicate that RTs reflect a set of processes that are sensitive to a range of factors that include both specific (e.g., the individual features) and abstract (e.g., the congruency and frequency of the conjoined item) information relating to the previous trial. However, there is no evidence that modulations of the congruency effect are implemented at the level of individual features; that is, there is no evidence for an ISPC. On the other hand, sequential modulations of congruency effects are apparent when repetitions are eliminated and display frequencies held constant. However, given that the events of the previous trial affect the processing of the current trial in a myriad of ways, sequential modulations may be difficult to study using tasks that do not allow for the various contributors to be isolated and estimated. As in other domains, the resolution of conflict is complicated when so little of the past is forgotten.

### **ACKNOWLEDGMENTS**

The authors wish to thank Jaeyong Lee for his assistance conducting the experiments and two anonymous reviewers for their very helpful comments.

### **REFERENCES**

**Conflict of Interest Statement:** The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

*Received: 09 September 2014; accepted: 01 November 2014; published online: 20 November 2014.*

*Citation: Hazeltine E and Mordkoff JT (2014) Resolved but not forgotten: Stroop conflict dredges up the past. Front. Psychol. 5:1327. doi: 10.3389/fpsyg.2014.01327*

*This article was submitted to Cognition, a section of the journal Frontiers in Psychology. Copyright © 2014 Hazeltine and Mordkoff. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) or licensor are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.*

## The Gratton effect remains after controlling for contingencies and stimulus repetitions

### *Chris Blais 1,2,3\*, Aikaterini Stefanidi <sup>1</sup> and Gene A. Brewer <sup>1</sup>*

*<sup>1</sup> Department of Psychology, Arizona State University, Tempe, AZ, USA*

*<sup>2</sup> Department of Communications, Arizona State University, Tempe, AZ, USA*

*<sup>3</sup> Center for Strategic Communication, Arizona State University, Tempe, AZ, USA*

#### *Edited by:*

*Wim Notebaert, Ghent University, Belgium*

#### *Reviewed by:*

*Marco Steinhauser, Catholic University of Eichstätt-Ingolstadt, Germany Kobe Desender, Universiteit Gent, Belgium*

#### *\*Correspondence:*

*Chris Blais, Department of Psychology, Arizona State University, 950 McAllister Ave., Tempe, AZ 85287, USA e-mail<EMAIL_ADDRESS>
### **Highlights:**

The Gratton effect, the observation that the size of the Stroop effect is larger following a congruent trial compared to an incongruent trial, is one pivotal observation in support of the conflict-monitoring hypothesis. Previous reports have demonstrated that non-conflict components, such as feature binding, also contribute to this effect. Critically, Schmidt and De Houwer (2011) report a flanker task and a button-press Stroop task suggesting that there is no conflict adaptation in the Gratton effect; it is entirely caused by feature binding. The current investigation attempts to replicate and extend this important finding across two experiments using a canonical four-choice Stroop task with vocal responses. In contrast to Schmidt and De Houwer, we observe reliable conflict adaptation after controlling for feature binding. We argue that the overall strength of conflict is critical for determining whether a conflict adaptation component will remain in the Gratton effect after explaining binding components.

**Keywords: conflict monitoring, cognitive control, cognitive control mechanisms, Stroop effect, conflict adaptation, Gratton effect, feature binding**

### **INTRODUCTION**

The Gratton effect (Gratton et al., 1992) refers to the finding that congruency effects (i.e., Stroop and flanker effects) are reduced following incongruent trials compared to congruent trials. The most widespread explanation of the Gratton effect is the conflict adaptation hypothesis (Carter et al., 1998; Botvinick et al., 2001, 2004), which states that response conflict from the previous trial signals a *need for control* that manifests as a modulation of response times and error rates on the subsequent trial. The net result is that the size of the Stroop effect is larger following a congruent trial than following an incongruent trial. First observed in a flanker task (Eriksen and Eriksen, 1974), it has been observed in many conflict tasks such as Stroop (Kerns et al., 2004; Mayr and Awh, 2009) and Simon (Akçay and Hazeltine, 2007).

An account of the Gratton effect based solely on conflict adaption is unlikely. Others have pointed out that binding effects, namely feature repetition biases, also contribute to the Gratton effect (Mayr et al., 2003; Hommel et al., 2004; Mayr and Awh, 2009). While there is considerable debate in the field, most would acknowledge that any Gratton effect that remains after all binding sources have been eliminated is consistent with conflict adaptation.

Schmidt and De Houwer (2011) were the first to assess two different binding effects, namely contingency biases and congruency switch costs. They reported a Stroop and a flanker experiment in which they eliminated three possible binding confounds: (1) feature repetition biases, (2) sequential contingency biases, and (3) congruency switch costs. Controlling the first two biases was sufficient to eliminate the Gratton effect in RTs for both tasks, and errors in the flanker task. They attributed the remaining Gratton effect in the error data for the Stroop task to a congruency switch cost by showing that there was no congruency repetition by congruency interaction (see below). Thus, the critical question is whether there is indeed a Gratton effect after such sources have been eliminated.

The implications of this finding are profound. The Gratton effect is one of the key findings in support of the conflictmonitoring hypothesis (Carter et al., 1998), and demonstrating that the Gratton effect is entirely the result of feature binding would necessitate reinterpreting literally hundreds of experiments. Therefore, the current paper reviews the three binding confounds, citing literature which shows that no one confound alone can explain the Gratton effect. We then attempt to replicate Schmidt and De Houwer (2011), first by reanalyzing data from a large-scale Stroop study (Blais et al., 2010), and second with a new experiment. In contrast to the findings reported by Schmidt and De Houwer, a robust Gratton effect is observed reasserting that, at least in some tasks, conflict adaptation does contribute to the size of the Gratton effect.

Schmidt and De Houwer (2011) provided an in depth discussion of the following three confounds. They are briefly outlined here to orient readers to the issues.

### **FEATURE REPETITIONS**

Following Mayr et al.'s (2003) seminal paper demonstrating that feature repetitions cause the Gratton effect, it has become standard practice to, at the very least, eliminate complete repetitions when both the target feature and distractor feature repeat on the next trial. To eliminate all possible sources of feature repetitions (i.e., target-*>*target, distractor-*>*distractor, target-*>*distractor, and distractor-*>*target transitions), it is necessary to use at least a four-choice task. Studies that have used both a four-choice task, and eliminated all the feature repetition conditions tend to show that, although the Gratton effect is reduced in size, it is not eliminated (e.g., in a Simon task: Akçay and Hazeltine, 2007; in a flanker task: Verbruggen et al., 2006).

### **CONTINGENCY CONFOUNDS**

Contingency biases are another confound that may also increase the size of the Gratton effect. Participants are often presented with color words in their congruent color more often than would be expected by chance. These types of contingencies are problematic because participants learn them and end up responding faster to the high contingency trials (i.e., when the word is presented in its most frequent color) compared to the low contingency trials (i.e., when the word is presented in a color other than its more frequent color).

Mayr et al. (2003) manipulated proportion congruency between subjects in a flanker task and reported an increase in the size of the Gratton effect. In addition, Schmidt et al. (2007) had subjects identify the color of a non-color word (e.g., MOVE). Critically, the authors systematically paired how often each word would appear in a specific color to create high and low contingency items. For example, in the 75% contingent condition, MOVE might appear in orange on 75% of trials and in red, blue, or green on the remaining 25% of trials. Although there is no conflict *per se*, in addition to finding contingency effects (i.e., subjects were faster to press the orange key if the word was MOVE compared to any other word), they also observed a pseudo-Gratton effect. That is, the contingency effect was larger if preceded by a high contingency item in comparison to a low contingency item.

### **CONGRUENCY SWITCH COSTS**

Schmidt and De Houwer (2011) proposed the congruency switch hypothesis, a novel third confound against the conflict adaptation account of the Gratton effect. The logic is similar to the task-switch hypothesis (e.g., Monsell, 2003). In short, for an incongruent trial, the system must select between two activated response codes, and bind one to the color and the other to the word. But, for congruent trials, the system simply binds the one activated response code to both the color and the word. Thus, it is conceivable that the system must be reconfigured to respond to a congruent trial compared to an incongruent trial. If so, there may be a cost associated with it. More generally, if even slightly different strategies are used in response to congruent vs. incongruent trials, then switching from one trial type to the next may incur a cost.

To test if a congruency switch is contributing to the Gratton effect, Schmidt and De Houwer (2011) suggest that "analyzing congruency as a function of switch rather than n-1 congruency should lead to roughly additive effect of congruency and switch." (p. 179). They noted that visual inspection of Freitas et al. (2007) seems to support this hypothesis.

### **EXPERIMENT 1: A GRATTON ANALYSES OF Blais et al. (2010)**

To summarize, there are at least three binding confounds that preclude a conflict adaption hypothesis of the Gratton effect. The evidence in the literature suggests that (1) feature repetitions alone cannot account for a Gratton effect, (2) contingency effects can lead to a pseudo-Gratton effect, and (3) there is speculative evidence that congruency switch costs can yield a Gratton effect.

The current paper reports a series of new analyses from a recent large-scale Stroop study which looked at the role of one's awareness of the proportion of congruent trials on the size of the Stroop effect (Blais et al., 2010). Two important findings emerge. First, when there is no contingency between the color and the word (the 25% congruent condition), there is still a strong Gratton effect after stimulus repetition trials are removed that cannot be explained by a congruency switch. Second, across the entire range of proportions between the 10 and 80% range, the size of the Gratton effect is statistically equal both when stimulus repetition trials are included, and excluded, from the analysis. This finding suggests that color-word contingency plays no role in the Gratton effect.

### **METHOD**

For full methodological details, see Blais et al. (2010). Briefly, fifteen subjects spent 8–10 h in the lab performing 19,000 trials in a vocal Stroop task. These trials were administered in blocks of 100 trials across 19 different proportion congruency conditions ranging from 5 to 95% in increments of 5. The order of the 190 blocks was randomized, and each participant received the same order. Each subject responded vocally to the color (RED, BLUE, YELLOW, or GREEN) that the word (red, blue, yellow, or green) was presented in. Stimuli for each block were sampled randomly *with* replacement from the set of 16 possible stimuli such that, if the proportion congruency level was 30%, then 30 congruent stimuli were selected, followed by 70 incongruent stimuli. These 100 items were then randomly sorted and presented to the subject.

It is important to note that 9 of these subjects were asked to estimate the proportion of congruent trials and rate their confidence of this estimate following each block of 100 trials. There was no difference between these two groups on any of the analysis reported here, and so they are treated as a homogenous group of 15 subjects. Since this is a four-choice task, there is no contingency between the color and the word (i.e., the word green is equally likely to appear in any of the four colors) in the 25% congruent condition.

The same correct RTs data as in the original report were used. That is, correct RTs longer than 2000 ms (outliers) or shorter than Blais et al. Gratton effect without repetitions

200 ms (anticipatory) were excluded, along with any RTs more than 2.5 standard deviations away from the mean within each subject by block by congruency cell.

### **RESULTS**

### **ANALYSES OF RTs**

### *Including stimulus repetitions*

**Table 1** shows the mean RT for the four previous congruencyby-congruency cells at each level of proportion congruency. To maximize power, a 2 (previous congruency) by 2 (current congruency) ANOVA was conducted separately for each proportion condition. The results of this analysis are on the bottom portion of **Table 1**. To summarize, there was a significant main effect of congruency at each level of proportion congruency. There was a significant main effect of previous congruency at all levels of proportion except [15, 70, 75]. Critically, these factors interacted to produce a Gratton effect at all levels of proportion except [10].

The solid black circles in **Figure 1A** show the size of the Gratton effect as a function of the proportion of congruent trials. According to pure contingency accounts of the Gratton effect, an increase in the contingency between the color and the word should result in an increase in the size of the Gratton effect. Even though the trend lines appear relatively flat, a repeated measures regression analysis was performed to check for the presence of a non-zero, positive, slope. Specifically, a slope and intercept estimate was calculated for each subject, and a onesample *t*-test was conducted on these estimates. Conceptually, a positive slope indicates that the Gratton effect increases as the proportion of congruent trials increases. The results of this reveal a slope of 0.139 ± 0.131 ms, *t*(14) = 1*.*07, *p >* 0*.*30, and an intercept of 31.789 ± 7.701, *t*(14) = 4*.*13, *p <* 0*.*001. This is shown as the solid black line in **Figure 1A**. Thus, the proportion of congruent trials does not impact the size of the Gratton effect.

### *Excluding stimulus repetitions*

**Table 2** further divides the mean RT from the four previous congruency x congruency cells in **Table 1** into the 15 cells that comprise the non-orthogonal feature repetition types (word-*>*word, color-*>*color, word-*>*color, color-*>*word). In this four-choice task, this amounts to keeping approximately 56% of trials per subject. The same set of ANOVAs reported above were conducted on the cells for which there are no stimulus-repetitions, indicated by the bolded rows in the **Table 2**. The results are reported in the middle portion of **Table 2**. There was a significant main effect of congruency at each level of proportion congruency. There was a significant main effect of previous congruency at all levels of proportion except [60, 65, 70, 80]. The Gratton effect was only significant for the [15, 20, 45, 50, 60, 65] conditions.

Although many of the Gratton effects were no longer statistically significant, paired *t*-tests showed that the reduction in the size of the Gratton effect from **Tables 1**, **2** was only reliable for the [55], *p <* 0*.*027, condition, and was marginal in the [30], *p* = 0*.*070, condition. For all other comparisons, *p*s *>* 0.15. For the present purposes, the fate of the 25% congruent condition is most critical, although the size of the Gratton effect was marginal,

**Response times for each of the four 2 (previous congruency) × 2 (congruency) cells as a function of the proportion of congruent**

 **trials.**

**Table 1 |**

*The bold values signify that p < 0.05.*

*p* = 0*.*057, two-tailed, it was not statistically smaller than when repetitions were included. That is, the 34 ± 9 ms Gratton effect in **Table 1** was statistically equivalent to the 26 ± 12 ms Gratton effect in **Table 2**, *p >* 0*.*50.

The solid gray circles in **Figure 1A** show the size of the Gratton effect as a function of the proportion of congruent trials. The same repeated measures regression analysis reported above yielded a slope of 0.438 ± 0.382, *t*(14) = 1*.*15, *p >* 0*.*25, and an intercept of 10.937 ± 13.026, *t*(14) = 0*.*84, *p >* 0*.*40. This is shown as the dotted gray line in **Figure 1A**. Although the slope is numerically larger and the intercept is numerically smaller than in the previous analysis that included repetition effects, both are statistically equivalent to the previous parameter estimates (*p* = 0*.*441 for the slope, and *p* = 0*.*111 for the intercept).

### *Can the switch hypothesis account for the remaining Gratton effect?*

Even though the size of the Gratton effects were statistically equivalent across most of the proportion conditions, visual inspection of **Figure 1** suggests that, generally, the Gratton effect is numerically smaller when repetitions are removed. To assess whether the remaining Gratton effect is the result of congruency switching (i.e., Schmidt and De Houwer, 2011), a 2 (Switch) × 2 (Congruency) analysis was conducted at each proportion level. The results of this analysis are shown on the bottom proportion of **Table 2**. An in-depth description of the logic of this analysis is provided by Schmidt and De Houwer (2011). Briefly, additive effects of congruency switch (whether the congruency on the previous trial is the same, or different, on the current trials) and congruency are consistent with an interpretation in which the Gratton effect results from a reconfiguration switch cost. An interaction of these factors cannot rule out a conflict adaption account of the Gratton effect. There was a main effect of congruency at all levels of proportion. There was a switch cost at the following levels of proportion [15, 20, 30, 40, 45, 60, 65]. Critically, these factors interact, rather than add, at each level of proportion except [60, 70, 75, 80]. Furthermore, and even at the levels of proportion at which they fail to interact, the effect seems too large to attribute to purely additive factors.

#### **ANALYSES OF ERRORS**

Despite a very low error rate of 2.1%, for the sake of completeness, the entire set of analyses performed on RTs was also done on error rates. It should be noted that the lack of a main effect of congruency effect in many of the analyses, make it difficult to interpret "higher order" effects, such as the Gratton effect, or the increase in the size of the Gratton effect as the proportion of trials increases. It should also be noted that the same analyses performed on efficiency scores (RT divided by accuracy for each cell; Townsend and Ashby, 1983) yields effects which completely replicate the analyses on the RT data.

#### *Including stimulus repetitions*

**Table 3** mirrors **Table 1** with mean percent error rate in place of RTs. The same analysis contained in **Table 1** is shown at the bottom of **Table 3**. There was a significant main effect of congruency at each level of proportion congruency except [30]. There was only a significant main effect of previous congruency at [80]. Similarly, there was only a Gratton effect at [80].

*The bold values signify that p < 0.05.*

Blais et al. Gratton effect without repetitions

Despite the general absence of effects, for completeness the same repeated-measures regression analyses performed on the RT data were conducted here. The solid black circles in **Figure 1B** show the size of the Gratton effect as a function of the proportion of congruent trials. The results of this analysis reveal a slope of 0.014 ± 0.032 ms, *t*(14) = 0*.*44, *p >* 0*.*50, and an intercept of −0.698 ± 0.802, *t*(14) = −0.87, *p <* 0*.*40. This is shown as the solid black line in **Figure 1B**.

### *Excluding stimulus repetitions*

**Table 4** mirrors **Table 2** with mean percent error rate in place of RTs. The same analysis contained in **Table 2** is shown in the middle of **Table 4**. There was a significant main effect of congruency at each level of proportion congruency [10, 20, 25, 45, 55, 80]. There was a significant main effect of previous congruency only at [40, 65]. There were no significant Gratton effects.

Paired *t*-tests showed that, with the exception of [15, 25, 70] where the ps were marginal (0.095, 0.084, and 0.087 respectively), the size of the Gratton effects in **Tables 3**, **4** were statistically equivalent (*p*s *>* 0.15).

The solid gray circles in **Figure 1B** show the size of the Gratton effect as a function of the proportion of congruent trials. The same repeated measures regression analysis reported above yielded a slope of 0.038 ± 0.017, *t*(14) = 2*.*26, *p* = 0*.*040, and an intercept of −0.250 ± 0.281, *t*(14) = −0.89, *p >* 0*.*35. This significant slope is difficult to interpret given the fact that there is no significant Gratton effect in any of the proportion conditions. This is shown as the gray line in **Figure 1B**. Although the slope is larger and the intercept is smaller than in the previous analysis which included repetition effects, both are statistically equivalent to the previous parameter estimates, *p* = 0*.*614 for the slope and *p* = 0*.*627 for the intercept.

#### *Can the switch hypothesis account for the remaining Gratton effect?*

Although there was no significant Gratton effect, a 2 (Switch) × 2 (Congruency) analysis was still conducted at each proportion level. Although these factors only interact at [55, 65, 80], it would be difficult to argue that Switch and Congruency are additive given the absence of a main effect of switch effect at all levels of proportion except the ones at which the factors interact, [55, 65, 80].

### **DISCUSSION**

Experiment 1 reanalyzed a large-scale vocal Stroop study to assess the presence of a conflict adaptation component to the Gratton effect after ruling out three possible sources of binding confounds. There is no contingency bias in the 25% congruency condition. The analyses confirmed the presence of a Gratton effect in this condition, which could not be explained by the congruency switch hypothesis. Experiment 2 provides an independent replication of this result confirming that the Gratton effect remains after controlling for the three biases described by Schmidt and De Houwer (2011).

These analyses revealed two additional findings. First, the size of the Gratton effect in a vocal Stroop task is not affected by the contingencies between the color and the word as indicated by the statistically zero slopes in **Figure 1A**. Second, stimulus repetitions

**Table 3 | Error rates for each of the four 2 (previous**

**congruency)**

 **x 2**

**(congruency)**

 **cells as a function of the proportion**

 **of congruent**

 **trials.**

*The bold values signify that p < 0.05.*

have little effect on the size of the Gratton effect in a vocal Stroop task. Although excluding stimulus repetition, in general, reduces the size of the effect, the real impact appears to be on the amount of variance in the size of the Gratton effect. That is, the average Gratton effect collapsed across proportions is 38 ± 5 ms with repetitions and 31 ± 8 ms without. These estimates are statistically equal (*p >* 0*.*30). However, the standard deviation of the size of the Gratton effect across proportions is 30 ± 3 ms with repetitions and 86 ± 10 ms without. These estimates are quite different, *t*(14) = 6*.*04, *p <* 0*.*001. It is difficult to know whether the increase in variance occurs because of the fact that various stimulus repetition types account for 24.8, 50.5, 49.8, and 83.0% of trials in the CC, CI, IC, and II conditions respectively, or due an unknown psychological construct.

### **POTENTIAL ISSUES**

The astute reader will have identified one potentially important problem with these re-analyses: the proportion of congruent trials—the color-word contingency—was manipulated withinsubjects. So, even though a given block of 100 trials in the middle of the session may have a chance-level contingency (i.e., the 25% blocks) between the word and the color, that block was preceded by many blocks of trials in which the contingency between the color and the word was greater that chance.

As noted in the methods, each subject received the same random block order. Coincidently, the first block was the 25% congruent condition. Thus, to avoid any possible longer-term association confounds, analyses looking only at this first block of 100 trials1 were conducted both including and excluding repetitions. A Gratton effect measuring 42 ± 14 ms was observed with repetitions, *F*(1*,* 13) = 8*.*76, *p* = 0*.*011, and measuring 52 ± 18 ms was observed without repetitions, *F*(1*,* 13) = 8*.*44, *p* = 0*.*012. In addition, the remaining Gratton effect cannot be explained by the congruency switch hypothesis. Specifically, response times, excluding repetitions, yields a 70 ± 28 ms congruency switch x congruency interaction *F*(1*,* 13) = 6*.*83, *p* = 0*.*020 comprised of a Stroop effect of 99 ± 20 ms, *t*(13) = 5*.*27, *p <* 0*.*001, following a congruency repetition and 29 ± 20 ms, *t*(13) = 1*.*53, *p* = 0*.*153, following a congruency switch.

### **EXPERIMENT 2: A GRATTON ANALYSIS OF THE 25% CONGRUENCY CONDITION**

Excluding feature repetitions in Experiment 1 raised an important issue; the absence of a reliable reduction in the Gratton effect when feature repetitions are excluded is inconsistent with the results of previous studies on this issue. We suspect this may have occurred because (1) we had a relatively small sample size for addressing this issue and (2) because proportion was manipulated within-subjects, it may be that subjects actually formed non-zero contingencies between the color and word pairs. To address these concerns, we conducted a new experiment with the goal of replicating these results with a larger sample size and using only the 25% congruency condition. The results from Experiment 2 indicated that there is still a strong Gratton effect after stimulus repetition trials are removed that cannot be explained by a congruency switch, suggesting that color-word contingency plays no role in the Gratton effect.

### **METHODS**

For full methodological details, see Blais et al. (2010). Briefly, thirty subjects were asked to perform 820 trials in a vocal Stroop task. The first 20 trials were considered practice and were used to calibrate the microphone and not included in any of the reported analyses. The remaining 800 trials were divided into four blocks of 200 trials with a self-paced break between them. Importantly, the trials were 25% congruent; 200 trials were congruent and 600 were incongruent, thus any of the four words were equally likely to appear in any of the four colors thereby eliminating all word-color association biases.

### **RESULTS**

### **ANALYSES OF RTs**

### *Including stimulus repetitions*

The same 2 (previous congruency) by 2 (current congruency) ANOVA reported in Experiment 1 was conducted on these data. The results are shown in **Table 5**. There was a significant main effect of congruency, with congruent trials (761 ms) responded to faster than incongruent trials (833 ms), and a significant main effect of previous congruency, with trials on which the previous trial was congruent (783 ms) being responded to faster than trials on which the previous trial was incongruent (811 ms). Critically, these factors interacted to produce a Gratton effect, *F*(1*,* 29) = 15*.*9, *p <* 0*.*001: the Stroop effect was larger following congruent trials (92 ± 11 ms) than following incongruent trials (54 ± 8 ms).

### **Table 5 | Response times and error rates for each of the four 2 (previous congruency) × 2 (congruency) cells in Experiment 2.**

*The bottom portion of the table lists the parameter estimates obtained from the ANOVA testing for the presence of a Gratton effect. The bold values signify that p < 0.05.*

<sup>1</sup>One subject was dropped from the analysis because they had no observations in the congruent-congruent condition after excluding repetition trials.

### *Excluding stimulus repetitions*

The same 2 (previous congruency) by 2 (current congruency) ANOVA reported in Experiment 1, but excluding stimulus repetitions, was conducted on these data. The results are shown in **Table 6**. There was a significant main effect of congruency, with congruent trials (795 ms) responded to faster than incongruent trials (867 ms), *F*(1*,* 29) = 57*.*6, *p <* 0*.*001 and a significant main effect of previous congruency, with trials on which the previous trial was congruent (817 ms) being responded to faster than trials on which the previous trial was incongruent (845 ms), *F*(1*,* 29) = 14*.*1, *p <* 0*.*001. Critically, these factors interacted to produce a Gratton effect, *F*(1*,* 29) = 10*.*1, *p <* 0*.*005: the Stroop effect was larger following congruent trials (89 ± 11 ms) than following incongruent trials (56 ± 10 ms).

### *Can the switch hypothesis account for the remaining Gratton effect?*

To assess whether the remaining Gratton effect is the result of congruency switching (i.e., Schmidt and De Houwer, 2011), a 2 (Switch) × 2 (Congruency) analysis was conducted on data after excluding stimulus repetitions. Again, an in-depth description of the logic of this analysis is provided by Schmidt and De Houwer (2011). In short, additive effects of congruency switch (whether the congruency on the previous trial is the same, or different, on the current trials) and congruency are consistent with an interpretation in which the Gratton effect results from a reconfiguration switch cost. An interaction of these factors cannot rule out a conflict adaption account of the Gratton effect. There was a main effect of congruency, with congruent trials (795 ms) responded to faster than incongruent trials (867 ms), *F*(1*,* 29) = 57*.*6, *p <* 0*.*001. There was a switch cost, congruency switch trials (839 ms) were responded to slower than congruency repetition trials (823 ms), *F*(1*,* 29) = 10*.*1, *p <* 0*.*005. Critically, these factors interact, rather than add, *F*(1*,* 29) = 14*.*1, *p <* 0*.*001, the Stroop effect is larger on congruency repetition trials (101 ± 12 ms) vs. congruency switch trials (45 ± 12 ms), thereby ruling out the switch hypothesis as an explanation for the remaining Gratton effect.

### **ANALYSES OF ERRORS**

The overall rate rates was only 1.4%, but for the sake of completeness, the entire set of analyses performed on RTs was also done on error rates.

### *Including stimulus repetitions*

The same 2 (previous congruency) by 2 (current congruency) ANOVA reported in Experiment 1 was conducted on these data. There was a significant main effect of congruency, with congruent trials (0.4%) responded to more accurately than incongruent trials (2.3%), and a significant main effect of previous congruency, with trials on which the previous trial was congruent (1.2%) being responded to more accurately than trials on which the previous trial was incongruent (1.7%), *F*(1*,* 29) = 7*.*5, *p <* 0*.*05. Critically, these factors interacted to produce a Gratton effect; the Stroop effect was larger following congruent trials (2.4 ± 0.4%) than following incongruent trials (1.5 ± 0.2%).

**Table 6 | Response times and error rates for each of the four 2 (previous congruency) × 2 (congruency) cells in Experiment 2 after dividing them into whether they contain target-***>***target, distractor-***>***distractor, target-***>***distractor, or distractor-***>***target repetitions.**

*The middle portion of the table lists the parameter estimates obtained from the ANOVA testing for the presence of a Gratton effect, and the bottom portion of the table lists the parameter estimates obtained from the ANOVA testing whether the remaining Gratton effect results from the congruency switching hypothesis. Note: The absence of an interaction in the bottom portion is consistent with the switching hypothesis. The bold values signify that p < 0.05.*

### *Excluding stimulus repetitions*

The same 2 (previous congruency) by 2 (current congruency) ANOVA reported in Experiment 1, but excluding stimulus repetitions, was conducted on these data. There was a significant main effect of congruency, with congruent trials (0.5%) responded to more accurately than incongruent trials (2.6%), and a significant main effect of previous congruency, with trials on which the previous trial was congruent (1.8%) being responded to less accurately than trials on which the previous trial was incongruent (1.2%). These factors failed to interact to produce a Gratton effect; the Stroop effect was statistically equivalent following congruent trials (2.5 ± 0.6%) than following incongruent trials (1.8 ± 0.3%).

### *Can the switch hypothesis account for the remaining Gratton effect?*

To assess whether the remaining Gratton effect is the result of congruency switching (i.e., Schmidt and De Houwer, 2011), a 2 (Switch) × 2 (Congruency) analysis was conducted on data after excluding stimulus repetitions. Again, an in-depth description of the logic of this analysis is provided by Schmidt and De Houwer (2011). In short, additive effects of congruency switch (whether the congruency on the previous trial is the same, or different, on the current trials) and congruency are consistent with an interpretation in which the Gratton effect results from a reconfiguration switch cost. An interaction of these factors cannot rule out a conflict adaption account of the Gratton effect. There was a main effect of congruency, with congruent trials (0.5%) responded to faster than incongruent trials (2.6%). There was no switch cost; congruency switch trials (1.7%) were responded equivalently to congruency repetition trials (1.3%). Critically, these factors interact, rather than add; the Stroop effect is larger on congruency repetition trials (2.8 ± 0.6%) vs. congruency switch trials (1.5 ± 0.3%), thereby ruling out the switch hypothesis as an explanation for the remaining Gratton effect.

### **DISCREPANCIES WITH SCHMIDT AND DE HOUWER**

What seems clear from the current set of experiments using a vocal Stroop task is that at least part of the Gratton effect results from conflict adaptation. The vocal Stroop task has been called the gold standard of attention measures (e.g., MacLeod, 1992). Anyone who has done a standard vocal Stroop task knows how difficult it is to not blurt out the word. That is, individuals must suppress an extremely strong, obligatory urge to read the word. That is, it seems fairly obvious that the desire to read aloud the word is the major source of conflict. Thus, conflict adaptation is more likely in this task because conflict is more pervasive, and hence more disturbing, for participants (e.g., Desender et al., 2014).