A new model of decision processing in instrumental learning tasks
Abstract
Learning and decisionmaking are interactive processes, yet cognitive modeling of errordriven learning and decisionmaking have largely evolved separately. Recently, evidence accumulation models (EAMs) of decisionmaking and reinforcement learning (RL) models of errordriven learning have been combined into joint RLEAMs that can in principle address these interactions. However, we show that the most commonly used combination, based on the diffusion decision model (DDM) for binary choice, consistently fails to capture crucial aspects of response times observed during reinforcement learning. We propose a new RLEAM based on an advantage racing diffusion (ARD) framework for choices among two or more options that not only addresses this problem but captures stimulus difficulty, speedaccuracy tradeoff, and stimulusresponsemapping reversal effects. The RLARD avoids fundamental limitations imposed by the DDM on addressing effects of absolute values of choices, as well as extensions beyond binary choice, and provides a computationally tractable basis for wider applications.
Introduction
Learning and decisionmaking are mutually influential cognitive processes. Learning processes refine the internal preferences and representations that inform decisions, and the outcomes of decisions underpin feedbackdriven learning (Bogacz and Larsen, 2011). Although this relation between learning and decisionmaking has been acknowledged (Bogacz and Larsen, 2011; Dayan and Daw, 2008), the study of cognitive processes underlying feedbackdriven learning on the one hand, and of perceptual and valuebased decisionmaking on the other, have progressed as largely separate scientific fields. In the study of errordriven learning (O'Doherty et al., 2017; Sutton and Barto, 2018), the decision process is typically simplified to softmax, a descriptive model that offers no processlevel understanding of how decisions arise from representations, and ignores choice response times (RTs). In contrast, evidenceaccumulation models (EAMs; Donkin and Brown, 2018; Forstmann et al., 2016; Ratcliff et al., 2016) provide a detailed process account of decisionmaking but are typically applied to tasks that minimize the influence of learning, and residual variability caused by learning is treated as noise.
Recent advances have emphasized how both modeling traditions can be combined in joint models of reinforcement learning (RL) and evidenceaccumulation decisionmaking processes, providing mutual benefits for both fields (Fontanesi et al., 2019a; Fontanesi et al., 2019b; Luzardo et al., 2017; McDougle and Collins, 2020; Miletić et al., 2020; Millner et al., 2018; Pedersen et al., 2017; Pedersen and Frank, 2020; Sewell et al., 2019; Sewell and Stallman, 2020; Shahar et al., 2019; Turner, 2019). Combined models generally propose that valuebased decisionmaking and learning interact as follows: For each decision, a subject gradually accumulates evidence for each choice option by sampling from a running average of the subjective value (or expected reward) associated with each choice option (known as Qvalues). Once a threshold level of evidence is reached, they commit to the decision and initiate a corresponding motor process. The response triggers feedback, which is used to update the internal representation of subjective values. The next time the subject encounters the same choice options this updated internal representation changes evidence accumulation.
The RLEAM framework has many benefits (Miletić et al., 2020). It allows for studying a rich set of behavioral data simultaneously, including entire RT distributions and trialbytrial dependencies in choices and RTs. It posits a theory of evidence accumulation that assumes a memory representation of rewards is the source of evidence, and it formalizes how these memory representations change due to learning. It complements earlier work connecting theories of reinforcement learning and decisionmaking (Bogacz and Larsen, 2011; Dayan and Daw, 2008) and their potential neural implementation in basal ganglia circuits (Bogacz and Larsen, 2011), by presenting a measurement model that can be fit to, and makes predictions about, behavioral data. Adding to benefits in terms of theory building, the RLEAM framework also has potential to improve parameter recovery properties compared to standard RL models (Shahar et al., 2019), and allows for the estimation of singletrial parameters of the decision model, which can be crucial in the analysis of neuroimaging data.
An important challenge of this framework is the number of modeling options in both the fields of reinforcement learning and decisionmaking. Even considering only modelfree (as opposed to modelbased, see Daw and Dayan, 2014) reinforcement learning, there exists a variety of learning rules (e.g. Palminteri et al., 2015; Rescorla and Wagner, 1972; Rummery and Niranjan, 1994; Sutton, 1988), as well as the possibility of multiple learning rates for positive and negative prediction errors (Christakou et al., 2013; Daw et al., 2002; Frank et al., 2009; Gershman, 2015; Frank et al., 2007; Niv et al., 2012), and many additional concepts, such as eligibility traces to allow for updating of previously visited states (Barto et al., 1981; Bogacz et al., 2007). Similarly, in the decisionmaking literature, there exists a wide range of evidenceaccumulation models, including most prominently the diffusion decision model (DDM; Ratcliff, 1978; Ratcliff et al., 2016) and race models such as the linear ballistic accumulator model (LBA; Brown and Heathcote, 2008) and racing diffusion (RD) models (Boucher et al., 2007; Hawkins and Heathcote, 2020; Leite and Ratcliff, 2010; Logan et al., 2014; Purcell et al., 2010; Ratcliff et al., 2011; Tillman et al., 2020).
The existence of this wide variety of modeling options is a doubleedged sword. On the one hand, it highlights the success of the general principles underlying both modeling traditions (i.e. learning from prediction errors and accumulatetothreshold decisions) in explaining behavior, and it allows for studying specific learning/decisionmaking phenomena. On the other hand, it constitutes a bewildering combinatorial explosion of potential RLEAMs; here, we provide empirical grounds to navigate this problem with respect to EAMs.
The DDM is the dominant EAM as currently used in reinforcement learning (Fontanesi et al., 2019a; Fontanesi et al., 2019b; Millner et al., 2018; Pedersen et al., 2017; Pedersen and Frank, 2020; Sewell et al., 2019; Sewell and Stallman, 2020; Shahar et al., 2019), but this choice is without experimental justification. Furthermore, the DDM has several theoretical drawbacks, such as its inability to explain multialternative decisionmaking and its strong commitment to the accumulation of the evidence difference, which leads to difficulties in explaining behavioral effects of absolute stimulus and reward magnitudes without additional mechanisms (Fontanesi et al., 2019a; Ratcliff et al., 2018; Teodorescu et al., 2016). Here, we compare the performance of different decisionmaking models in explaining choice behavior in a variety of instrumental learning tasks. Models that fail to capture crucial aspects of performance run the risk of producing misleading psychological inferences. For EAMs, the full RT distribution (i.e. its level of variability and skew) have proven to be crucial. Hence, it is important to assess which RLEAMs are able to capture not only learningrelated changes in choice probabilities and mean RT, but also the general shape of the entire RT distribution and how it changes with learning. Further, in order to be held forth as a general modeling framework, it is important to capture how all these measures interact with key phenomena in the decisionmaking and learning literature.
We compare the RLDDM with two RLEAMs based on a racing accumulator architecture (Figure 1). All the RLEAMs assume evidence accumulation is driven by Qvalues, which change based on errordriven learning as governed by the classical delta update rule. Rather than a twosided DDM process (Figure 1A), the alternative models adopt a neurally plausible RD architecture (Ratcliff et al., 2007), which conceptualize decisionmaking as a statistically independent race between singlesided diffusive accumulators, each collecting evidence for a different choice option. The first accumulator to reach its threshold triggers motor processes that execute the corresponding decision. The alternative models differ in how the mean values of evidence are constituted. The first model, the RLRD (Figure 1B), postulates accumulators are driven by the expected reward for their choice, plus a stimulusindependent baseline (c.f. an urgency signal; Miletić and van Maanen, 2019). The second model, the RLARD (advantage racing diffusion), uses the recently proposed advantage framework (van Ravenzwaaij et al., 2020), assuming that each accumulator is driven by weighted combination of three terms: the difference (‘advantage’) in mean reward expectancy of one choice option over the other, the sum of the mean reward expectancies, and the urgency signal. In perceptual choice, the advantage term consistently dominates the sum term by an order of magnitude (van Ravenzwaaij et al., 2020), but the sum term is necessary to explain the effects of absolute stimulus magnitude. We also fit a limited version of this model, RLlARD, with the weight of the sum term set to zero to test whether accounting for the influence of the sum is necessary even when reward magnitude is not manipulated, as was the case in our first experiments. The importance of sum and advantage terms is also quantified by their weights as estimated in full RLARD model fits.
For all models, we first test how well they account for RT distributions (central tendency, variability, and skewness of RTs), accuracies, and learningrelated changes in RT distributions and accuracies in a typical instrumental learning task (Frank et al., 2004). In this experiment, we also manipulated difficulty, that is, the magnitude of the difference in average reward between pairs of options. In two further experiments, we test the ability of the RLEAMs to capture key behavioral phenomena in the decisionmaking and reinforcementlearning literatures, respectively, speedaccuracy tradeoff (SAT), and reversals in reward contingencies, again in binary choice. In a final experiment, we show that the RLARD extends beyond binary choice, successfully explaining accuracy and full RT distributions from a threealternative instrumental learning task that manipulates reward magnitude.
Results
In the first experiment, participants made decisions between four sets of two abstract choice stimuli, each associated with a fixed reward probability (Figure 2A). On each trial, one choice option always had a higher expected reward than the other; we refer to this choice as the ‘correct’ choice. After each choice, participants received feedback in the form of points. Reward probabilities, and therefore choice difficulty, differed between the four sets (Figure 2B). In total, data from 55 subjects were included in the analysis, each performing 208 trials (see Materials and methods).
Throughout, we summarize RT distributions by calculating the 10th, 50th (median), and 90th percentiles separately for correct and error responses. The median summarizes central tendency, the difference between 10th and 90th percentiles summarizes variability and the larger difference between the 90th and 50th percentiles than between the 50th and 10th percentiles summarizes the positive skew that is always observed in RT distributions. To visualize the effect of learning, we divided all trials in 10 bins (approximately 20 trials each), and calculated accuracy and the RT percentiles per bin. Note that model fitting was not based on these data summaries. Instead, we used hierarchical Bayesian methods to fit models to the data from every trial and participant simultaneously. We compared model fits informally using posterior predictive distributions—calculating the same summary statistics on data generated from the fitted model as we did for the empirical data—and formally using the Bayesian Predictive Information Criterion (BPIC; Ando, 2007). The former method allows us to assess the absolute quality of fit (Palminteri et al., 2017) and detect misfits; the latter provides a modelselection criterion that trades off quality of fit with model complexity (lower BPICs are preferred), ensuring that a better fit is not only due to greater model flexibility.
We first examine results aggregated over difficulty conditions. The posterior predictives of all four RLEAMs are shown in Figure 3, with the top row showing accuracies, and the middle and bottom rows correct and error RT distributions (parameter estimates for all models can be found in Table 1). The RLDDM generally explains the learningrelated increase in accuracy well, and if only the central tendency were relevant it might be considered to provide an adequate account of RT, although correct median RT is systematically underestimated. However, RT variability and skew are severely overestimated. The RLRD largely overcomes the RT distribution misfit, but it overestimates RTs in the first trial bins, and while capturing an increase in accuracy over trials, it is systematically underestimated. The RLARD models provide the best explanation of all key aspects of the data: except for a slight underestimation of accuracy in early trial bins (largely shared with the RLDDM), they capture accuracy well, and like the RLRD, they capture the RT distributions well, but without overpredicting the RTs in the early trials. The two RLARD models do not differ greatly in fit, except that the limited version slightly underestimates the decrease in RT with learning.
Figure 4 shows the data and RLARD model fit separated by difficulty (see Figure 4—figure supplement 1 for equivalent RLDDM fits, which again fail to capture RT distributions). The RLARD model displays the same excellent fit as to data aggregated over difficulty, except that it underestimates accuracy in early trials in the easiest condition (Figure 4, bottom right panel). Further inspections of the data revealed that 17 participants (31%) reached perfect accuracy in the first bin in this condition. Likely, they guessed correctly on the first occurrence of the easiest choice pair, repeated their choice, and received too little negative feedback in the next repetitions to change their choice strategy. Figure 4—figure supplement 2 shows that, with these 17 participants removed, the overestimation is largely mitigated. The delta rule assumes learning from feedback, and so cannot explain such high early accuracies. Working memory processes could have aided performance in the easiest condition, since the total number of stimuli pairs was limited and feedback was quite reliable, making it relatively easy to remember correctchoice options (Collins and Frank, 2018; Collins and Frank, 2012; McDougle and Collins, 2020).
Reward magnitude and Qvalue evolution
Qvalues represent the participants’ internal beliefs about how rewarding each choice option is. The RLlARD and RLDDM assume drift rates are driven only by the difference in Qvalues (Figure 5), and both underestimate the learningrelated decrease in RTs. Similar RLDDM underestimation has been detected before (Pedersen et al., 2017), with the proposed remedy being a decrease in the decision bound with time (but with no account of RT distributions). The RLARD explains the additional speedup through the increasing sum of Qvalues over trials (Figure 5C), which in turn increases drift rates (Figure 5D). In line with observations in perceptual decisionmaking (van Ravenzwaaij et al., 2020), the effect of the expected reward magnitude on drift rate is smaller (on average, ${w}_{s}=0.36$) than that of the Qvalue difference (${w}_{d}=2.25$) and the urgency signal (${V}_{0}=2.45$). Earlier work using an RLDDM (Fontanesi et al., 2019a) showed that higher reward magnitudes decrease RTs in reinforcement learning paradigms. There, the reward magnitude effect on RT was accounted for by allowing the threshold to change as a function of magnitude. However, this requires participants to rapidly adjust their threshold based on the identity of the stimuli, something that is usually not considered possible in EAMs (Donkin et al., 2011; Ratcliff, 1978). The RLARD avoids this problem, with magnitude effects entirely mediated by drift rates, and our results show that the expected reward magnitudes influence RTs due to learning even in the absence of a reward magnitude manipulation. Because the sum affects each accumulator equally, it changes RT with little effect on accuracy.
Speedaccuracy tradeoff
Speedaccuracy tradeoff (SAT) refers to the ability to strategically tradeoff decision speed for decision accuracy (Bogacz et al., 2010; Pachella and Pew, 1968; Ratcliff and Rouder, 1998). As participants can voluntarily trade speed for accuracy, RT and accuracy are not independent variables, so analysis methods considering only one of these variables while ignoring the other can be misleading. EAMs simultaneously consider RTs and accuracy and allow for estimation of SAT settings. The classical explanation in the DDM framework (Ratcliff and Rouder, 1998) holds that participants adjust their SAT by changing the decision threshold: increasing thresholds require a participant to accumulate more evidence, leading to slower but more accurate responses.
Empirical work draws a more complex picture. Several papers suggest that in addition to thresholds, drift rates (Arnold et al., 2015; Heathcote and Love, 2012; Ho et al., 2012; Rae et al., 2014; Sewell and Stallman, 2020) and sometimes even nondecision times (Arnold et al., 2015; Voss et al., 2004) can be affected. Increases in drift rates in a race model could indicate an urgency signal, implemented by drift gain modulation, with qualitatively similar effects to collapsing thresholds over the course of a decision (Cisek et al., 2009; Hawkins et al., 2015; Miletić, 2016; Miletić and van Maanen, 2019; Murphy et al., 2016; Thura and Cisek, 2016; Trueblood et al., 2021; van Maanen et al., 2019). In cognitively demanding tasks, it has been shown that two distinct components of evidence accumulation (quality and quantity of evidence) are affected by SAT manipulations, with quantity of evidence being analogous to an urgency signal (Boag et al., 2019b; Boag et al., 2019a). Recent evidence suggests that different SAT manipulations can affect different psychological processes: cuebased manipulations that instruct participants to be fast or accurate lead to overall threshold adjustments, whereas deadlinebased manipulations can lead to a collapse of thresholds (Katsimpokis et al., 2020).
Here, we apply an SAT manipulation to an instrumental learning task (Figure 2C). The paradigm differs from experiment one by the inclusion of a cuebased instruction to either stress response speed (‘SPD’) or response accuracy (‘ACC’) prior to each choice (randomly interleaved). Furthermore, on speed trials, participants had to respond within 0.6 s to receive a reward. Feedback was determined based on both the choice’s probabilistic outcome (‘+100’ or ‘+0’) and the RT: On trials where participants responded too late, they were additionally informed of the reward associated with their choice, had they been in time, so that they always received the feedback required to learn from their choices. After exclusions (see Materials and methods), data from 19 participants (324 trials each) were included in the analyses.
We used two mixed effects models to confirm the effect of the manipulation. A linear model predicting RT confirmed an interaction between trial bin and cue (b = 0.014, SE = 1.53*10^{3}, 95% CI [0.011, 0.017], p < 10^{16}), a main effect of cue (b = 0.189, SE = 9.5*10^{3}, 95% CI [0.207, 0.170], p < 10^{16}) and a main effect of trial bin (b = 0.015, SE = 1.08*10^{3}, 95% CI [0.018, 0.013], p < 10^{16}). Thus, RTs decreased with trial bin, were faster for the speed condition, but the effect of the cue was smaller for later trial bins. A logistic mixed effects model of choice accuracy showed a main effect of the cue (b = 0.39, SE = 0.13, 95% CI [0.65, 0.13], p = 0.003) and trial bin (b = 0.42, SE = 0.06, 95% CI [0.30, 0.53], p = 3.1*10^{12}), but not for an interaction (b = 0.115, SE = 0.08, 95% CI [0.05, 0.28], p = 0.165). Hence, participants were more often correct in the accuracy condition, and their accuracy increased over trial bins, but there was no evidence for a difference in the increase (on a logit scale) between SAT conditions.
Next, we compared the RLDDM and RLARD. In light of the multiple psychological mechanisms potentially affected by the SAT manipulation, we allowed different combinations of threshold, drift rate, and for the RLARD urgency, to vary with the SAT manipulation. We fit three RLDDM models, varying either threshold, the Qvalue weighting on the drift rates parameter (Sewell and Stallman, 2020), or both. For the RLARD, we fit all seven possible models with different combinations of the threshold, urgency, and drift rate parameters free to vary between SAT conditions.
Formal model comparison (see Table 1 for all BPIC values) indicates that the RLARD model combining response caution and urgency effects provides the best explanation of the data, in line with earlier research in nonlearning contexts (Katsimpokis et al., 2020; Miletić and van Maanen, 2019; Rae et al., 2014; Thura and Cisek, 2016). The advantage for the RLARD was substantial; the best RLDDM (with only a threshold effect) performed worse than the worst RLARD model. The data and posterior predictive distributions of the best RLDDM model and the winning RLARD model are shown in Figure 6. As in experiment 1, the RLDDM failed to capture the shape of RT distributions, although it fit the SAT effect on accuracy and median RTs. The RLARD model provides a much better account of the RT distributions, including the differences between SAT conditions. In Figure 6—figure supplement 1, we show that adding nondecision time variability to the RLDDM mitigates some of the misfit of the RT distributions, although it still consistently underpredicted the 10th percentile in the accuracy condition. Further, this model was still substantially outperformed by the RLARD in formal model selection (ΔBPIC = 209), and nondecision time variability was estimated as much greater than what is found in nonlearning contexts, raising the question of its psychological plausibility.
Both RLDDM and RLARD models tended to underestimate RTs and choice accuracy in the early trial bins in the accuracy emphasis condition. As in experiment 1, working memory may have contributed to the accurate but slow responses in the first trial bin for the accuracy condition (Collins and Frank, 2018; Collins and Frank, 2012; McDougle and Collins, 2020).
Reversal learning
Next, we tested whether the RLARD can capture changes in accuracy and RTs caused by a perturbation in the learning process due to reversals in reward contingencies. In the reversal learning paradigm (Behrens et al., 2007; Costa et al., 2015; Izquierdo et al., 2017) participants first learn a contingency between choice options and probabilistic rewards (the acquisition phase) that is then suddenly reversed without any warning (the reversal phase). If the link between Qvalues and decision mechanisms as proposed by the RLARD underlies decisions, the model should be able to account for the behavioral consequences (RT distributions and decisions) of Qvalue changes induced by the reversal.
Our reversal learning task had the same general structure as experiment 1 (Figure 1), except for the presence of reversals. Fortyseven participants completed four blocks of 128 trials each. Within each block, two pairs of stimuli were randomly interleaved. Between trials 61 and 68 (uniformly sampled) in each block, the reward probability switched between stimuli, such that stimuli that were correct during acquisition were incorrect after reversal (and vice versa). Participants were not informed of the reversals prior to the experiment, but many reported noticing them.
Data and the posterior predictive distributions of the RLDDM and the RLARD models are shown in Figure 7. Both models captured the change in choice proportions after the reversal reasonably well, although they underestimate the speed of change. In Figure 7—figure supplement 1, we show that the same is true for a standard softmax model, suggesting that the learning rule is the cause of this problem. Recent evidence indicates that, instead of only estimating expected values of both choice options by errordriven learning, participants may additionally learn the task structure, estimate the probability of a reversal occurring and adjust choice behavior accordingly. Such a modelbased learning strategy could increase the speed with which choice behavior changes after a reversal (Costa et al., 2015; Izquierdo et al., 2017; Jang et al., 2015), but as yet a learning rule that implements this strategy has not been developed.
The change in RT around the reversal was less marked than the change in choice probability. Once again, the RLDDM overestimates variability and skew. Both models fit the effects of learning and reversal similarly, but the fastest responses for the RLDDM decrease much too quickly during initial learning and the reduction in speed for the slowest responses due to the reversal is strongly overestimated. The RLARD provides a much better account of the shape of the RT distributions, and furthermore captures the increase in entire RT distributions (instead of only the median) after the reversal point. Formal model comparison also very strongly favors the RLARD over the RLDDM ($\mathrm{\Delta}BPIC=4051$). Figure 7—figure supplement 2 provides model comparisons to RLDDMs with betweentrial variability parameters, which lead to the same conclusion.
A notable aspect of the data is that choice behavior stabilizes approximately 20 trials after the reversal, whereas RTs remain high compared to just prior to the reversal point for up to ~40 trials. The RLARD explains this behavior through relatively high Qvalues for the choice option that was correct during the acquisition (but not reversal) phase (i.e. choice A). Figure 8 depicts the evolution of Qvalues, Qvalue differences and sums, and drift rates in the RLARD model. The Qvalues for both choice options increase until the reversal (Figure 8A), with a much faster increase for Q_{A}. At the reversal Q_{A} decreases and Q_{B} increases, but as Q_{A} decreases faster than Q_{B} increases there is a temporary decrease in Qvalue sums (Figure 8C). After approximately 10 trials postreversal, Q_{B} is higher than for Q_{A}, which flips the sign of the Qvalue differences (Figure 8B). However, Q_{A} after the reversal remains higher than the Q_{B} before the reversal, which causes the (absolute) Qvalue differences to be lower after the reversal than before. As a consequence, the drift rates for B after the reversal remain lower than the drift rates for A before the reversal, which increases RT. Clearly, it is important to take account of the sum of inputs to accumulators as well as the difference between them in order to provide an accurate account of the effects of learning.
Multialternative choice
Finally, we again drew on the advantage framework (van Ravenzwaaij et al., 2020) to extend the RLARD to multialternative choice tasks, a domain where the RLDDM cannot be applied. As in the twochoice case, the multialternative RLARD assumes one accumulator per pairwise difference between choice options. With three choice options (e.g. 1, 2, 3), there are six (directional) pairwise differences (12, 13, 21, 23, 31, 32), and therefore six accumulators (see Figure 9). All accumulators are assumed to race toward a common threshold, with their drift rates determined by the advantage framework’s combination of an urgency, an advantage, and a sum term. Since each response is associated with two accumulators (e.g. for option 1, one accumulating the advantage 1–2, and the other accumulating the advantage 1–3), a stopping rule is required to determine when a commitment to a response is made and evidence accumulation stops. Following Van Ravenzwaaij et al., we used the WinAll stopping rule, which proposes that the first response option for which both accumulators have reached their thresholds wins. RT is the first passage time of the slowest of these two winning accumulators, plus nondecision time.
To test how well the WinAll RLARD can explain empirical data, we performed a fourth experiment in which participants were required to repeatedly make decisions between three choice options (Figure 10). Within each of the four blocks, there were four randomly interleaved stimulus triplets that differed in difficulty (defined as the difference in reward probability between target stimulus and distractors) and reward magnitude (defined as the average reward probability): 0.8/0.25/0.25 (easy, high magnitude), 0.7/0.3/0.3 (hard, high magnitude), 0.7/0.15/0.15 (easy, low magnitude), and 0.6/0.2/0.2 (hard, low magnitude). This enabled us to simultaneously test whether the RLARD can account for a manipulation of difficulty and mean reward magnitude. Furthermore, we predicted that the requirement to learn 12 individual stimuli (per block) would interfere with the participants’ ability to rely on working memory (Collins and Frank, 2012), and therefore expected that the RLARD would provide a better account of accuracy in the early trial bins compared to experiments 1 and 2. After exclusions (see Materials and methods), data from 34 participants (432 trials each) were included in the analyses.
Data and posterior predictive distributions of the RLARD are shown in Figure 11. The top row represents accuracy, the middle row the RT quantiles corresponding to the correct (target) choice option, and the bottom row the RT quantiles of the incorrect choices (collapsed across the two distractor response options). Compared to experiments 1–3, the task was substantially more difficult, as evidenced by the relatively low accuracies. The RLARD model was able to account for all patterns in the data, including the increase in accuracy and decrease in RTs due to learning, the shape of the full RT distributions, as well as the difficulty and magnitude effects. Furthermore, there was a decrease in variance in the error RTs due to learning (the 10th quantile RTs even mildly increased), which was also captured by the model. Note finally that, contrary to experiments 1 and 2, the model did not underestimate the accuracy in early bins in the easy conditions, which suggests that the influence of working memory was, as predicted, more limited than in earlier experiments. A parameter recovery study (Figure 11—figure supplement 1) demonstrated that the model’s parameters could be recovered accurately.
Notably, Figure 11 suggests that the effects of the magnitude manipulation were larger in the hard than in the easy condition. As in previous experiments, we inspected the Qvalue evolution (Figure 12) to understand how this interaction arose. As expected, the high magnitude condition led to higher Qvalues (Figure 12A) than the low magnitude condition, increasing the Qvalue sums (Figure 12C). However, there was a second effect of the increased magnitude: even though the true reward probability differences were equal between magnitude conditions, the Qvalue differences for the response accumulators (${\mathrm{\Delta}\mathrm{Q}}_{TD}$; Figure 12B) were larger in the high compared to the low magnitude condition, particularly for harder choices. As a consequence, both the Qvalue sum (weighted by median ${w}_{s}=0.15$), and the smaller changes in the Qvalue difference (weighted by median ${w}_{d}=1.6$), increased the drift rates for the response accumulators (${v}_{TD}$; Figure 12D), which led to higher accuracy and faster responses.
Discussion
We compared combinations of different evidenceaccumulations models with a simple delta reinforcement learning rule (RLEAMs). The comparison tested the ability of the RLEAMs to provide a comprehensive account of behavior in learning contexts, not only in terms of the choices made but also the full distribution of the times to make them (RT). We examined a standard instrumental learning paradigm (Frank et al., 2004) that manipulated the difference in rewards between binary options (i.e. decision difficulty). We also examined two elaborations of that paradigm testing key phenomena from the decisionmaking and learning literatures, speedaccuracy tradeoffs (SAT), and reward reversals, respectively. Our benchmark was the dual threshold Diffusion Decision Model (DDM; Ratcliff, 1978), which has been used in almost all previous RLEAM research, but has not been compared to other RLEAMs, and has not been thoroughly evaluated on its ability to account for RT distributions in learning tasks. Our comparison used several different racing diffusion (RD) models, where decisions depend on the winner of a race between single barrier diffusion processes.
The RLDDM provided a markedly inferior account to the other models, consistently overestimating RT variability and skew. As these aspects of behavior are considered critical in evaluating models in decisionmaking literature (Forstmann et al., 2016; Ratcliff and McKoon, 2008; Voss et al., 2013), our results question whether the RLDDM provides an adequate model of instrumental learning. Furthermore, the DDM carries with it two important theoretical limitations. First, it can only address binary choice. This is unfortunate given that perhaps the most widely used clinical application of reinforcement learning, the Iowa gambling task (Bechara et al., 1994), requires choices among four options. Second, the input to the DDM combines the evidence for each choice (i.e., ‘Q’ values determined by the learning rule) into a single difference, and so requires extra mechanisms to account for known effects of overall reward magnitude (Fontanesi et al., 2019a). Although there are potential ways that the RLDDM might be modified to account for magnitude effects, such as increasing betweentrial drift rate variability in proportion to the mean rate (Ratcliff et al., 2018), its inability to extend beyond binary choice remains an enduring impediment.
The best alternative model that we tested, the RLARD (advantage racing diffusion), which is based on the recently proposed advantage accumulation framework (van Ravenzwaaij et al., 2020), remedied all of these problems. The input to each accumulator is the weighted sum of three components: stimulus independent ‘urgency’, the difference between evidence for the choice corresponding to the accumulator and the alternative (the advantage), and the sum of the two evidence values. The urgency component had a large effect in all fits and played a key role in explaining the effect of speedaccuracy tradeoffs. Although an urgency mechanism such as collapsing bounds (Boehm et al., 2016; Bowman et al., 2012; Hawkins et al., 2015; Milosavljevic et al., 2010) or gain modulation (Boehm et al., 2016; Churchland et al., 2008; Ditterich, 2006; Hawkins et al., 2015) could potentially improve the fits of the RLDDM, fitting DDMs with such mechanisms is computationally very expensive, usually requiring the researcher to use simulationbased approximations (e.g. Turner and Sederberg, 2014). This expense becomes infeasible in the case of RLEAMs since these models assume different drift rates per trial, requiring the simulation of an entire dataset per trial in the empirical data (for each iteration of the MCMC sampling process). Furthermore, the origin of the concept of urgency lies in studies using racing accumulator models (Ditterich, 2006; Mazurek et al., 2003; Reddi and Carpenter, 2000), which was only later incorporated in the DDM (Milosavljevic et al., 2010); the implementation in the RLARD remains conceptually close to the early proposals.
The advantage component of the RLARD, which is similar to the input to the DDM, was strongly supported over a model in which each accumulator only receives evidence favoring its own choice. The sum component provides a simple and theoretically transparent way to deal with reward magnitude effects in instrumental learning. Despite having the weakest effect among the three components, the sum was clearly necessary to provide an accurate fit to our data. It also played an important role in explaining the effect of reward reversals.
In all our models, we assumed a linear function to link Qvalue differences to drift rates. This may not be adequate in all settings. For example, Fontanesi et al., 2019a showed (within an RLDDM) that a nonlinear linking function provided a better fit to their data. This could be caused by a nonlinear mapping between objective values and subjective values; the account of perceptual choice using the advantage framework (van Ravenzwaaij et al., 2020) relied on a logarithmic mapping between (objective) luminance and (subjective) brightness magnitudes. Prospect Theory (e.g. Tversky and Kahneman, 1992) also assumes that increasingly large objective values relative to a reference point lead to increasingly small increases in subjective value. Such nonlinear effects only become evident for sufficiently large differences over an appropriate range. Although in our experiments the RLARD was able to explain the data well using a simple linear function, future applications may need to explicitly incorporate a nonlinear value function.
Finally, we showed that the RLARD can be extended to multialternative choice. In a threealternative instrumental learning experiment, it accurately predicted the learning curves and full RT distributions for four conditions that differed in difficulty and reward magnitude. Furthermore, examination of Qvalue evolution clarified how the reward magnitude manipulation led to the observed behavioral effects. Notably, the number of choice options only changes the architecture of the RLARD while the number of parameters remains constant, and all accumulators in the model remain driven by the same three components: an urgency signal, an advantage, and a sum component. As a consequence, parametric complexity does not increase with number of choices and the model remained fully recoverable despite the relatively low number of trials.
It is perhaps surprising that the RLDDM consistently overestimated RT variability and skewness given that the DDM typically provides much better fits to data from perceptual decisionmaking tasks without learning. The inclusion of betweentrial variability in nondecision times partially mitigated the misfit but required an implausibly high nondecision time variability, and model comparisons still favored the RLARD. Previous work on the RLDDM did not investigate this issue. In many RLDDM papers, RT distributions are either not visualized at all, or are plotted using (defective) probability density functions on top of a histogram of RT data, making it hard to detect misfit, particularly with respect to skew due to the slow tail of the distribution. One exception is Pedersen and Frank, 2020, whose quantilebased plots show the same pattern that we found here of overestimated variability and skewness for more difficult choice conditions, despite including betweentrial variability in nondecision times. In a nonlearning context, it has been shown that the DDM overestimates skewness in highrisk preferential choice data (Dutilh and Rieskamp, 2016). Together these results suggest that decision processes in valuebased decision in general, and instrumental learning tasks in particular, may be fundamentally different from a twosided diffusion process, and instead better captured by a race model such as the RLARD.
In the current work, we chose to use racing diffusion processes over the more often used LBA models for reasons of parsimony: errordriven learning introduces betweentrial variability in accumulation rates, which are explicitly modeled in the RLEAM framework. As the LBA includes betweentrial variability in drift rates as a free parameter, multiple parameters can account for the same variance. Nonetheless, exploratory fits (see Figure 4—figure supplement 3) confirmed our expectation that an RLALBA (Advantage LBA) model fit the data of experiment one well, although formal model comparisons preferred the RLARD. Future work might consider completely replacing one or more sources of between trial variability in the LBA with structured fluctuations due to learning and adaption mechanisms.
The parametrization of the ARD model used in the current paper followed the ALBA model proposed by van Ravenzwaaij et al., 2020. This parametrization interprets the influence on drift rates in terms of advantages and magnitudes. However, as both the weights on Qvalue differences and sums ($w}_{d$ and $w}_{s$) are freely estimated parameters, the equations that define the drift rates can be rearranged as follows:
where $w}_{e}={w}_{d}+{w}_{s$ in the parametrization of Equation 4, and $w}_{i}={w}_{d}{w}_{s$. This reparametrization shows that each drift rate is determined by an excitatory influence ${w}_{e}$ of the Qvalue associated with the accumulator, and an inhibitory influence ${w}_{i}$ of the Qvalue associated with the other accumulator. Turner, 2019 proposed that inhibition plays an important role in learning tasks. Although the locus of inhibition is different in the two models, there are clear parallels that bear further investigation.
A limitation of the current work is that we collapsed across blocks in analyzing the data of experiments 2, 3, and 4. However, in more detailed explorations (see Figure 6—figure supplement 3) there were indications of secondorder changes across blocks. In experiment 2, participants were faster in the first trial bin of the second and third block compared to the first block, suggesting additional practice or adaptation effects at the beginning of the experiment. In experiment 3, participants slowed down, and learned the reversal faster, after the first block. This suggests they learned about the presence of reversals in the first block and applied a different strategy in the later blocks. Although it is known that participants increase their learning rates in volatile environments (Behrens et al., 2007), this by itself does not explain a decrease in response speed. Potentially, if participants understood the task structure after the first block, modelbased strategies, such as estimating the probability of a reversal having occurred, also slowed down responses. In experiment 4, participants were slower (but equally accurate) in the first block compared to the later blocks, suggesting again additional practice or adaptation effects. Future experiments should investigate the nature of these additional adaptation effects.
Although the account of data provided by the RLARD model was generally quite accurate, some elements of misfit suggest the need for further model development. RT and accuracy were underestimated in the initial trials of the easiest condition in experiment 1, in the accuracy emphasis condition in experiment 2, and prior to reversals in experiment 3. Furthermore, the RLARD model underestimated the speed with which choice probability changed after reversal of stimulusresponse mappings. These misfits point to a limited ability to capture the learningrelated changes in behavior. This is to some degree unsurprising, since we used a very simple model of errordriven learning. Future work might explore more sophisticated mechanisms, such as multiple learning rates (Daw et al., 2002; Fontanesi et al., 2019a; Gershman, 2015; Pedersen et al., 2017) or different learning rules (Fontanesi et al., 2019b; Fontanesi et al., 2019a). Furthermore, there is clearly a role for working memory in some reinforcement learning tasks (Collins and Frank, 2018; Collins and Frank, 2012), likely explaining the accurate but slow responses we observed in the early trial bins for easy conditions in experiments 1–3. The multialternative choice experiment, with 12 individual stimuli per block, hampered participants’ ability to employ working memory strategies, so even earlytrial performance was explained by purely errordriven learning.
In summary, we believe that the ARD decision mechanism provides a firm basis for further explorations of the mutual benefits that arise from the combination of reinforcement learning and evidenceaccumulation models, providing constraint that is based on a more comprehensive account of data than has been possible in the past. As it stands, the RLARD’s parameter recovery properties are good even with relatively low trial numbers, making it a suitable measurement model for simultaneously studying learning and decisionmaking processes, and interindividual differences therein. Further, the advantage framework extends to multiple choice while maintaining analytical tractability and addressing key empirical phenomena in that domain, such as Hick’s Law and responsecompetition effects (van Ravenzwaaij et al., 2020), enabling future applications to clinical settings, such as in the Iowa gambling task (Bechara et al., 1994).
Materials and methods
Experiment 1
Participants
61 participants (mean age 21 years old [SD 2.33], 47 women, 56 right handed) were recruited from the subject pool of the department of Psychology, University of Amsterdam, and participated for course credits. All participants had normal or correctedtonormal vision and gave written informed consent prior to the experiment onset. They did not participate in the other experiments. The study was approved by the local ethics committee.
Task
Request a detailed protocolThe task was an instrumental probabilistic learning task (Frank et al., 2004). On each trial, the subject was presented with two abstract symbols (a ‘stimulus pair’) representing two choice options (see Figure 2A for an example trial). Each choice option had a fixed probability of being rewarded with points when chosen, with one choice option always having a higher probability of being rewarded than the other. The task is to discover, by trial and error, which choice options are most likely to lead to rewards, and thereby to collect as many points as possible.
After a short practice block to get familiar with the task, participants completed one block of 208 trials. Four different pairs of abstract symbols were included, each presented 52 times. Stimulus pairs differed in their associated reward probabilities: 0.8/0.2, 0.7/0.3, 0.65/0.35, and 0.6/0.4. The size of the reward, if obtained, was always the same: ‘+100’ (or ‘+0’ otherwise). Reward probabilities were chosen such that they differed only in the betweenchoice difference in reward probability, leading to varying choice difficulties while keeping the mean reward magnitude fixed.
Participants were instructed to earn as many points as possible, and to always respond before the deadline of 2 s. Feedback consisted of two parts: an ‘outcome’ and a ‘reward’. The outcome corresponded to the probabilistic outcome of the choice, whereas the reward corresponded to the actual number of earned points. When participants responded before the deadline, the reward was equal to the outcome. If they were too late, the outcome was shown to allow participants to learn from their choice, but the reward they received was set to 0 to encourage responding in time. Participants received a bonus depending on the number of points earned (maximum +0.5 course credits, mean received +0.24). The task was coded in PsychoPy (Peirce et al., 2019). After this block, participants performed two more blocks of the same task with different manipulations, which are not of current interest.
Exclusion
Request a detailed protocolSix participants were excluded from analysis: One reported, after the experiment, not to have understood the task, one reported a technical issue, and four did not reach an abovechance accuracy level as determined by a binomial test (accuracy cutoff 0.55, corresponding to p<0.05). The final sample thus consisted of 55 subjects (14 men, mean age 21 years old [SD 2.39], 51 righthanded).
Cognitive modeling
Request a detailed protocolThe main analysis consists of fitting four RLEAMs to the data and comparing the quality of the fits penalized by model complexity. We compared four different decision models: the DDM (Ratcliff, 1978), a racing diffusion (Boucher et al., 2007; Logan et al., 2014; Purcell et al., 2010; Turner, 2019) model, and two Advantage Racing Diffusion (ARD; van Ravenzwaaij et al., 2020) models (see Figure 1 for an overview). Although the former is a twosided diffusion process, the latter three models employ a race architecture.
For all models we used the simple delta update rule as a learning model:
where ${Q}_{i,t}$ is the value representation of choice option $i$ on trial $t$, $\alpha $ the learning rate, and ${r}_{t}$ the reward on trial $t$. The difference between the actual reward and the value representation of the chosen stimulus, ${r}_{t}{Q}_{i,t}$, is known as the reward prediction error. The learning rate controls the speed at which Qvalues change in response to the reward prediction error, with larger learning rates leading to stronger fluctuations. In this model, only the Qvalue of the chosen option is updated.
RLEAM 1: RLDDM
Request a detailed protocolIn the first RLEAM, we use the DDM (Ratcliff, 1978) as a choice model (Figure 1, left column). The DDM assumes that evidence accumulation is governed by:
$v$ is the mean speed of evidence accumulation (the drift rate), and $s$ is the standard deviation of the withintrial accumulation white noise (W). The RLDDM assumes that the drift rate depends linearly on the difference of value representations:
$w$ is a weighting variable, and ${Q}_{t,1}$ and ${Q}_{t,2}$ are the Qvalues for both choice options per trial, which change each trial according to Equation 1. Hence,
The starting point of evidence accumulation, z, lies between decision boundaries $a$ and $a$. Here, as in earlier RLDDM work (Fontanesi et al., 2019a; Fontanesi et al., 2019b; Pedersen et al., 2017), we assume an unbiased start of the decision process (i.e., z = 0). Evidence accumulation finishes when threshold $a$ or $a$ is reached, and the decision for the choice corresponding to ${Q}_{1}$ or ${Q}_{2}$, respectively, is made. The response time is the time required for the evidenceaccumulation process to reach the bound, plus an intercept called the nondecision time ($t0$). The nondecision time is the sum of the time required for perceptual encoding and the time required for the execution of the motor response. Parameter s was fixed to 1 to satisfy scaling constraints (Donkin et al., 2009; van Maanen and Miletić, 2020). In total, this specification of the RLDDM has 4 free parameters ($\alpha ,w,a,t0$).
Furthermore, we fit four additional RLDDMs (RLDDM A1A4) with betweentrial variabilities in start point, drift rate, and nondecision time, as well as a nonlinear link function between Qvalues and drift rates (Fontanesi et al., 2019a). RLDDM A1 uses the nonlinear function ${v}_{t}=\frac{2{v}_{max}}{1+\mathrm{e}\mathrm{x}\mathrm{p}\left(w\left({Q}_{t,1}{Q}_{t,2}\right)\right)}{v}_{max}$ to link Qvalues to drift rates (Fontanesi et al., 2019b). For the new ${v}_{max}$ parameter, $\mathcal{\mathcal{N}}\left(\mathrm{2,5}\right)$ (truncated at 0) and $\mathrm{\Gamma}\left(\mathrm{1,1}\right)$ were used as priors for the hypermean and hyperSD, respectively. RLDDM A2 includes betweentrial variabilities in both drift rate ${s}_{v}$ and start point ${s}_{z}$, with $\mathcal{\mathcal{N}}\left(\mathrm{0.1,0.1}\right)$ and $\mathcal{\mathcal{N}}\left(\mathrm{0.1,0.1}\right)$ as priors for hypermeans (respectively, both truncated at 0) and $\mathrm{\Gamma}\left(\mathrm{1,1}\right)$ for the hyperSD. Drift rate variability was estimated as a proportion of the current drift rate, such that ${s}_{v,t}={v}_{t}*{s}_{v}$ (which allows for higher variability terms for higher Qvalue differences, but retains the ratio $v/{s}_{v})$. RLDDM A3 included ${s}_{v}$, ${s}_{z}$, and also betweentrial variability in nondecision time ${s}_{t0}$, for which $\mathcal{\mathcal{N}}\left(\mathrm{0.1,0.1}\right)$ (truncated at 0) and $\mathrm{\Gamma}\left(\mathrm{1,1}\right)$ were used as priors for the hypermean and hyperSD, respectively. RLDDM A4 used all three betweentrial variabilities as well as the nonlinear link function. The quality of fits of these additional models can be found in Figure 3—figure supplement 1. Foreshadowing the results, the RLDDM A3 improved the quality of fit compared to the RLDDM, but required an implausibly high nondecision time variability: The acrosssubject mean of the median posterior estimates of the t0 and ${s}_{t0}$ parameters indicate a nondecision time distribution of [0.27 s, 0.64 s]. The range of 0.37 s is very high in light of the literature (Tran et al., 2021), raising the question of its psychological plausibility. For this reason, as well as since the RLDDM is used most often without ${s}_{t0}$, we focus on the RLDDM (without betweentrial variabilities) in the main text.
RLEAM 2: RLRD
Request a detailed protocolThe RLRD (Figure 1, middle panel) assumes that two evidence accumulators independently accrue evidence for one choice option each, both racing toward a common threshold $a$ (assuming no response bias). The first accumulator to hit the bound wins, and the corresponding decision is made. For each choice option i, the dynamics of accumulation are governed by:
${V}_{0}$ is a parameter specifying the drift rate in the absence of any evidence, $w$ a weighting parameter, and $s$ the standard deviation of withintrial noise. As such, the mean speed of accumulation (the drift rate ${v}_{i}$) is the sum of two independent factors: an evidenceindependent baseline speed ${V}_{0}$, and an evidencedependent weighted Qvalue, $w{Q}_{i}$. Since ${V}_{0}$ is assumed to be identical across accumulators, and governs the speed of accumulation unrelated to the amount of evidence, we interpret this parameter as an additive urgency signal (Miletić and van Maanen, 2019), with conceptually similar behavioral effects as collapsing bounds (Hawkins et al., 2015). Similar to the DDM, a nondecision time parameter accounts for the time for perceptual encoding and the motor response time. Parameter $s$ was fixed to 1 to satisfy scaling constraints (Donkin et al., 2009; van Maanen and Miletić, 2020). In total, the RLRD has 5 free parameters $(\alpha ,w,a,v0,t0)$.
Each accumulator’s first passage times are Wald (also known as inverted Gaussian) distributed (Anders et al., 2016). In an independent race model, each accumulator’s first passage time distribution is normalized to the probability of the response with which it is associated (Brown and Heathcote, 2008; Turner, 2019).
RLEAM 3 and 4: RLARD
Request a detailed protocolThirdly, we fit two racing diffusion models based on an advantage race architecture (van Ravenzwaaij et al., 2020). An advantage race model using an LBA has been shown to provide a natural account for multialternative choice phenomena such as Hick’s law, as well as stimulus magnitude effects in perceptual decisionmaking. As in the RLRD, accumulators race toward a common bound, but the speed of evidence accumulation ${v}_{i}$ depends on multiple factors: first, as in the RLRD, the evidenceindependent speed of accumulation ${V}_{0}$; second, the advantage of the evidence for one choice option over the other (c.f. the DDM, where the difference between evidence for both choice options is accumulated); and third, the sum of the total available evidence. Combined, for two accumulators in the RLEAM framework, this leads to:
In the original work proposing the advantage accumulation framework (van Ravenzwaaij et al., 2020), it was shown that the ${w}_{d}$ parameter had a much stronger influence on evidenceaccumulation rates than the ${w}_{s}$ parameter. Therefore, we first fixed the ${w}_{s}$ parameter to 0, to test whether the accumulation of differences is sufficient to capture all trends in the data. We term this model the RLlARD (l = limited), which we compare to the RLARD in which we fit ${w}_{s}$ as a free parameter.
As previously, parameter $s$ was fixed to 1 to satisfy scaling constraints (Donkin et al., 2009; van Maanen and Miletić, 2020). The RLARD also has a threshold, nondecision time, and learning rate parameter, totaling five $(\alpha ,{w}_{d},a,{V}_{0},t0)$ and 6 free parameters $(\alpha ,{w}_{d},{w}_{s},a,{V}_{0},t0)$ for the RLlARD and RLARD, respectively. A parameter recovery study (e.g. Heathcote et al., 2015; Miletić et al., 2017; Moran, 2016; Spektor and Kellen, 2018) was performed to confirm that datagenerating parameters can be recovered using the experimental paradigm at hand. The results are shown in Figure 3—figure supplement 2.
Bayesian hierarchical parameter estimation, posterior predictive distributions, model comparisons
Request a detailed protocolWe estimated grouplevel and subjectlevel posterior distributions of each model’s parameter using a combination of differential evolution (DE) and Markovchain Monte Carlo sampling (MCMC) with MetropolisHastings (Ter Braak, 2006; Turner et al., 2013). Sampling settings were default as implemented in the Dynamic Models of Choice R software (Heathcote et al., 2019): The number of chains, D, was three times the number of free parameters. Crossover probability was set to $2.38/\sqrt{D}$ at the subject level and $U[0,1]$ at the group level. Migration probability was set to 0.05 during burnin only. Convergence was assessed using visual inspection of the chain traces and GelmanRubin diagnostic (Brooks and Gelman, 1998; Gelman and Rubin, 1992) (individual and multivariate potential scale factors < 1.03 in all cases).
Hierarchical models were fit assuming independent normal population (“hyper”) distributions for each parameter. For all models, we estimated the learning rate on a probit scale (mapping [0, 1] onto the real domain), with a normal prior $\alpha \text{}\sim \text{}\mathrm{\Phi}\left(\mathfrak{N}\left(1.6,\text{}5\right)\right)$ (Spektor and Kellen, 2018). Prior distributions for all estimated hypermean decisionrelated parameters were vague. RLEAMs, the threshold parameter $\mathrm{a}~\mathcal{\mathcal{N}}\left(3,\mathrm{}5\right)$ truncated at 0, and $\mathrm{t}0~\mathcal{\mathcal{N}}\left(0.3,\mathrm{}0.5\right)$ truncated at 0.025 s and 1 s (all estimation was carried out on the seconds scale). For the RLDDM, $\mathrm{w}~\mathcal{\mathcal{N}}(2,\mathrm{}5)$. For the RLRD, $\mathrm{w}~\mathcal{\mathcal{N}}(9,\mathrm{}5)$, and for the RLARD models, ${\mathrm{w}}_{d}\text{}\sim \text{}\mathfrak{N}\left(9,\text{}5\right)$ and ${\mathrm{w}}_{s}\text{}\sim \text{}\mathfrak{N}\left(0,\text{}3\right)$. For the hyperSD, a $\mathrm{\Gamma}\left(\mathrm{1,1}\right)$ distribution was used as prior. Plots of superimposed prior and posterior hyperdistributions confirmed that these prior settings were not influential.
In initial explorations, we also freely estimated the Qvalues at trial 0. However, in the RLEAMs, the posterior distributions for these Qvalues consistently converged on 0, which was therefore subsequently used as a fixed value for all results reported in this paper.
To visualize the quality of model fit, we took 100 random samples from the estimated parameter posteriors and simulated the experimental design with these parameters. For each behavioral measure (e.g. RT quantiles, accuracy), credible intervals were estimated by taking the range between the 2.5% and 97.5% quantiles of the averages over participants.
To quantitatively compare the fit of different models, penalized by their complexity, we used the Bayesian predictive information criterion (BPIC; Ando, 2007). The BPIC is an analogue of the Bayesian information criterion (BIC), but (unlike the BIC) suitable for models estimated using Bayesian methods. Compared to the deviance information criterion (Spiegelhalter et al., 2002), the BPIC penalizes model complexity more strongly to prevent overfitting (c.f. AIC vs. BIC). Lower BPIC values indicate better tradeoffs between fit quality and model complexity.
Experiment 2
Participants
23 participants (mean age 19 years old [SD 1.06 years], 7 men, 23 righthanded) were recruited from the subject pool of the Department of Psychology of the University of Amsterdam and participated for course credits. Participants did not participate in the other experiments. All participants had normal or correctedtonormal vision and gave written informed consent prior to the experiment onset. The study was approved by the local ethics committee.
Task
Request a detailed protocolParticipants performed the same task as in experiment 1, with the addition of an SAT manipulation (Figure 2C). The SAT manipulation included both an instructional cue and a response deadline. Prior to each trial, a cue instructed participants to emphasize either decision speed (‘SPD’) or decision accuracy (‘ACC’) in the upcoming trial, and in speed trials, participants did not earn points if they were too late (>600 ms). As in experiment 1, after each choice participants received feedback consisting of two components: an outcome and a reward. The outcome refers to the outcome of the probabilistic gamble, whereas the reward refers to the number of points participants actually received. If participants responded in time, the reward was equal to the outcome. In speed trials, participants did not earn points if they responded later than 600 ms after stimulus onset, even if the outcome was +100. On trials where participants responded too late, they were additionally informed of the reward that was associated with their choice, had they been in time. This way, even when participants are too late, they still receive the feedback that can be used to learn from their choices.
The deadline manipulation was added because we hypothesized that instructional cues alone would not be sufficient to persuade participants to change their behavior in the instrumental learning task, since that task specifically requires them to accumulate points. If the received number of points was independent of response times, the optimal strategy to collect most points would be to ignore the cue and focus on accuracy only.
Participants performed 324 trials divided over three blocks. Within each block, three pairs of stimuli were shown, with associated reward probabilities of 0.8/0.2, 0.7/0.3, and 0.6/0.4. Speed and accuracy trials were randomly interleaved. Figure 2C depicts the sequence of events in each trial. As this experiment also served as a pilot for an fMRI experiment, we added fixation crosses between each phase of the trial, with jittered durations. A prestimulus fixation cross lasted 0.5, 1, 1.5, or 2 s; fixation crosses between cue and stimulus, between stimulus and highlight, and between highlight and feedback lasted 0, 0.5, 1, or 1.5 s; and an intertrial interval fixation cross lasted 0.5, 1, 1.5, 2, 2.5 s. Each trial took 7.5 s. The experiment took approximately 45 min.
Exclusion
Request a detailed protocolFour participants did not reach abovechance performance as indicated by a binomial test (cutoff 0.55, p<0.05), and were excluded from further analyses. The final sample thus consisted of 19 participants (mean age 19 years old [SD 1.16 years], 6 men, 19 righthanded). For one additional participant, a technical error occurred after the first block. This participant was included in the analyses, since the Bayesian estimation framework naturally downweighs the influence of participants with fewer trials.
Manipulation check and acrossblock differences in behavior
Request a detailed protocolWe expected an interaction between SAT conditions and learning. In the early trials, participants have not yet learned the reward contingencies, causing a low evidence accumulation rate compared to later trials. With low rates it takes longer to reach the decision threshold, and small changes in the threshold settings or drift rates (by means of an additive urgency signal) can cause large behavioral effects. Therefore, we expected the behavioral effects of the SAT manipulation to become smaller over the course of learning.
To formally test for the behavioral effects of the SAT manipulation in experiment 2, we fit two mixed effects models (Gelman and Hill, 2007): A linear model with RT as dependent variable, and a logistic model with accuracy as the dependent variable. As fixed effects, trial bin and SAT condition were included. Trial bins were obtained by splitting all trials in ten bins (approximately 20 trials each) per participant. As random effects, only participant was included. For the logistic model using accuracy as a dependent variable, we logtransformed trial bin numbers (Evans et al., 2018; Heathcote et al., 2000), to account for the nonlinear relation between accuracy and trial bin (Figure 6, top row). Mixed effects analyses were done using lme4 (Bates et al., 2015). For all mixed effects models, we report parameter estimates of the fixed effects, their standard error and confidence interval, as well as a pvalue obtained from a tdistribution with the denominator degrees of freedom approximated using Satterthwaite's method (Satterthwaite, 1941), as implemented in the lmerTest package (Kuznetsova et al., 2017) for the R programming language (R Development Core Team, 2017).
Next, we tested for the across block stability of behavior using two mixed effects models. One linear mixed effects model was used to predict RT with block number, trial bin, and their interaction, with a random intercept for participant. A second, logistic mixed effects model was used to test the effect of block, trial bin (logtransformed, as above), and their interaction on choice accuracy. In both models, trial bin is expected to influence the outcome variables, but the assumption of across block stability in behavior is violated if there are main effects of block number and/or interaction effects between block number and trial bin. Mean RT and accuracy by block is shown together with the formal test results in Figure 6—figure supplement 3.
Cognitive modeling
Request a detailed protocolWe fit three RLDDMs and seven RLARDs. The three RLDDM models varied either threshold, the Qvalue weighting on the drift rates parameter (Sewell and Stallman, 2020), or both. The seven RLARD allowed all unique combinations of the threshold, urgency, and drift rate parameters free to vary between the speed and accuracy conditions.
For the accuracy condition, we used the same priors as in experiment 1. In the speed condition, the parameters that were free to vary were estimated as proportional differences from the accuracy conditions; specifically: ${a}_{spd}=\left(1+{m}_{a,spd}\right)*{a}_{acc}$, $V}_{0,spd}=\left(1+{m}_{{V}_{0,spd}}\right)\ast {V}_{0,acc$, and $v}_{i,spd}=\left(1+{m}_{v,spd}\right)\ast {v}_{i,acc$. The prior used was $\mathcal{\mathcal{N}}(0,\mathrm{}5)$ for the hypermean and $\mathrm{\Gamma}(1,\mathrm{}1)$ for the hyperSD of all parameters $m$, truncated at 1.
As in experiment 1, we performed a parameter recovery study to confirm that the datagenerating parameters can be recovered, using the winning model and a simulation of the paradigm of experiment 2. The results are shown in Figure 6—figure supplement 2.
Additionally, we performed a second model comparison using three variants of RLDDM A3 (i.e., including betweentrial variabilities in start point, drift rate, and nondecision time), which varied the threshold, the Qvalue weighting on the drift rate parameters, and both. The results are shown in Figure 6—figure supplement 1, and lead to the same conclusions as the RLDDM.
Experiment 3
Participants
Fortyseven participants (mean age 21 years old [SD 2.81 years], 16 men, 40 righthanded) were recruited from the subject pool of the Department of Psychology of the University of Amsterdam and participated for course credits. Participants did not participate in the other experiments. All participants had normal or correctedtonormal vision and gave written informed consent prior to the experiment onset. The study was approved by the local ethics committee.
Task
Request a detailed protocolThe reversal learning task had the same general task structure as experiment 1. Participants completed four blocks of 128 trials each, totaling 512 trials. Within each block, two pairs of stimuli were randomly interleaved, with associated reward probabilities of 0.8/0.2 and 0.7/0.3. Between trials 61 and 68 (uniformly sampled) of each block, the reward probability switched between stimuli, such that the stimulus with a prereversal reward probability of 0.8/0.7 had a postreversal reward probability of 0.2/0.3 (and vice versa). Participants were not informed of the reversals prior to the experiment, but many reported noticing them.
In addition to the reversal learning task, the experimental session also contained a working memory task that is not of current interest. Thirty participants performed the reversal learning task before the working memory task, and 17 participants afterwards. The entire experiment took approximately one hour.
Cognitive modeling
Request a detailed protocolWe first tested whether a standard softmax model is able to capture the quick change in choice behavior after the occurrence of a reversal. Softmax is given by:
where ${P}_{i,t}$ is the probability of choosing option $i$ on trial $t$, J is the total number of choice options, and $\beta $ is a free parameter often called the inverse temperature. The inverse temperature is often interpreted in terms of the exploration/exploitation tradeoff (Daw et al., 2006), with higher values indicating more exploitation. In twochoice settings, Equation 5 can be rewritten as:
which highlights that the choice probability is driven by the difference in Qvalues, weighted by the inverse temperature parameter. We hierarchically fit the softmax model using the same parameter estimation methods as in experiment 1. Priors for the hypermean were set to $\beta ~N\left(\mathrm{1,5}\right)$ truncated at 0, and for the hyperSD $\mathrm{\Gamma}\left(\mathrm{1,1}\right)$.
Then, the RLDDM and RLARD were fit to the data using the same methods as in experiment 1. Again, we performed a parameter recovery study, of which the results are shown in Figure 7—figure supplement 3. Similarly, we also fit RLDDM A3 to the data. In an initial fit, the MCMC chains for 11 (out of 47) participants got stuck in values for ${s}_{z}$ of 1 (i.e. ${s}_{z}$ covered the entire range between both thresholds), which are implausibly high and moreover led to convergence problems. We refit this model with the prior on ${s}_{z}~\mathcal{\mathcal{N}}\left(\mathrm{0.1,0.1}\right)$ truncated at 0 and 0.5 (i.e. setting the maximum range of betweentrial start point variability to be half the range between the lower and upper threshold), which did converge. The posterior predictives are shown in Figure 7—figure supplement 2. This model led to the same overall conclusions as the standard RLDDM.
Experiment 4
Participants
Fortythree participants (mean age 20 years old [SD 4.29 years], 5 men, 36 righthanded) were recruited from the subject pool of the Department of Psychology of the University of Amsterdam and participated for course credits. They did not participate in the other experiments. All participants had normal or correctedtonormal vision and gave written informed consent prior to the experiment onset. The study was approved by the local ethics committee. Participants performed the task online.
Task
Request a detailed protocolThe threealternative instrumental learning task had the same general task structure as before. Participants completed three blocks of 144 trials each, totaling 432 trials. Within each block, four triplets of stimuli were randomly interleaved. We used a factorial design to manipulate both difficulty (defined as the difference between the target and distractor reward probability) and reward magnitude (defined as the mean probability of reward per triplet): 0.8/0.25/0.25 (easy, high magnitude), 0.7/0.3/0.3 (hard, high magnitude), 0.7/0.15/0.15 (easy, low magnitude), and 0.6/0.2/0.2 (hard, low magnitude). The entire experiment took approximately 30 min.
Exclusion
Request a detailed protocolNine subjects did not reach abovechance accuracy and were excluded from analysis (accuracy cutoff 0.37, corresponding to p<0.05 in a binomial test). The final sample thus consisted of 34 subjects (three men, mean age 20 years old [SD 4.68 years], 28 righthanded).
Cognitive modeling
Request a detailed protocolA threealternative RLARD with the WinAll stopping rule was fit to the data. The multialternative version of the RLARD includes one accumulator per directional pairwise difference between choice options, leading to a total of six accumulators (12, 13, 21, 23, 31, 32) for the case of three choice options. Each accumulator is governed by the same evidenceaccumulation dynamics as in the twoalternative RLARD:
Hence, each choice option (e.g. 1) is associated with two accumulators that collect evidence for the advantage of that option over the other two options (12, 13). The WinAll stopping rule proposes that a final choice is made when two conditions are satisfied: (1) both accumulators corresponding to that choice reached their thresholds, and (2) for each other choice option at least one accumulator has not yet reached the threshold. The corresponding response time is the decision time of the slowest of the two winning accumulators, plus the nondecision time. The probability of response one at time t is then given by van Ravenzwaaij et al., 2020; derivation in their Appendix:
where I are choice options {2,3}, J is an option in {2,3} that is not I, and K is an option in {1,2,3} that is not I. PDF and CDF refer to the probability density and cumulative density function of the Wald distribution.
Despite the visual complexity of Figure 9, the threealternative RLARD remains highly constrained by the linking functions of Equation 7 and the Qvalue evolution. As only the architecture of the linking between Qvalues and accumulators was generalized to accommodate the third choice option, there remains the same number of parameters as in the twoalternative case. Note that the threealternative WinAll RLARD naturally reduces to the twochoice RLARD when one of the choice options is removed.
We fit the threealternative RLARD using the same fitting methods (including the same priors) as in experiment 1. We also performed a parameter recovery study using the same methods as in earlier experiments, the results of which are shown in Figure 11—figure supplement 1.
Code availability statement
Request a detailed protocolAll analysis codes are available on OSF (https://osf.io/ygrve/).
Data availability
All data analysed in this study are available from https://osf.io/ygrve/.

Open Science FrameworkID ygrve. A new model of decision processing in instrumental learning tasks.
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Decision letter

Valentin WyartReviewing Editor; École normale supérieure, PSL University, INSERM, France

Joshua I GoldSenior Editor; University of Pennsylvania, United States

Jan Willem de GeeReviewer; Baylor College of Medicine, United States
In the interests of transparency, eLife publishes the most substantive revision requests and the accompanying author responses.
Acceptance summary:
Your responses to the reviewers' comments have convincingly addressed earlier concerns as to how the advantage racing model fares in reinforcement problems with more than two alternatives – a situation where its superiority over standard driftdiffusion models is clearest. The additional experiment described in the revised manuscript, and the formal derivation of the advantage racing model for reinforcement problems with more than two alternatives, constitute two important additions to the study which now provides a qualitative theoretical advance over the existing literature. The revised manuscript describes a convincing set of experiments and analyses that supports advantage racing as a good model of the interplay between learning and decisionmaking in reinforcement problems varying stimulus difficulty, speedaccuracy tradeoff and stimulusresponse mapping. Congratulations for an insightful study of human behavior.
Decision letter after peer review:
Thank you for submitting your article "A new model of decision processing in instrumental learning tasks" for consideration by eLife. Your article has been reviewed by two peer reviewers, and the evaluation has been overseen by a Reviewing Editor and Joshua Gold as the Senior Editor. The following individual involved in review of your submission has agreed to reveal their identity: Jan Willem de Gee (Reviewer #1).
The reviewers have discussed the reviews with one another and the Reviewing Editor has drafted this decision to help you prepare a revised submission.
As the editors have judged that your manuscript is of interest, but as described below that additional experiments are required before it is published, we would like to draw your attention to changes in our revision policy that we have made in response to COVID19 (https://elifesciences.org/articles/57162). First, because many researchers have temporarily lost access to the labs, we will give authors as much time as they need to submit revised manuscripts. We are also offering, if you choose, to post the manuscript to bioRxiv (if it is not already there) along with this decision letter and a formal designation that the manuscript is "in revision at eLife". Please let us know if you would like to pursue this option.
Summary:
This cognitive modeling study on a timely topic investigates the combination of reinforcement learning and decisionmaking for modeling choice and reactiontime data in sequential reinforcement problems (e.g., bandit tasks). The central claim of the paper is that the oftenused combination of reinforcement learning with the driftdiffusion model (which decides based on the difference between option values) does not provide an adequate model of instrumental learning. Instead, the authors propose an "advantage racing" model which provides better fits to choice and reactiontime data in different variants of twoalternative forcedchoice tasks. Furthermore, the authors emphasize that their advantage racing model allows for fitting decision problems with more than two alternatives – something which the standard driftdiffusion model cannot do. These findings can be of interest for researchers investigating learning and decisionmaking.
The study asks an important question for understanding the interaction between reinforcement learning and decisionmaking, the methods appear sound, and the manuscript is clearly written. The superiority of the advantage racing model is key to the novelty of the study, which otherwise relies on a canonical task studied in several recent papers on the same issue. However, the reviewers feel that the framing of the study and its conclusions would require additional analyses experiments to transform the manuscript from a modest quantitative improvement into a qualitative theoretical advance. In particular, as described in the paragraphs below, the authors should test how their advantage racing model fares in reinforcement problems with more than two alternatives. This is, from their own account throughout the paper, a situation where their model could show most clearly its superiority over standard driftdiffusion models used in the recent literature. The section below describes the essential revisions that the authors should address in a pointbypoint fashion in a revised version of their manuscript.
Essential revisions:
1) Starting from the Abstract, the authors allude to reinforcement problems with more than 2 alternatives (1) and to the role of absolute choice values (2) in characterizing the limitations of the standard DDM. However, in the current manuscript, point 1 is not addressed (and actually does not appear to be amenable to the current model implementation, see the next point), and point 2 is addressed via modest quantitative improvements to model fits rather than true qualitative divergence between their model and other models' ability to capture specific behavioral effects.
The authors could greatly strengthen their conclusions if they extend their model to RL data sets with (1) more than two alternatives, and (2) variations in the absolute mean reward across blocks of learning trials. These experimental variants, which would put the superiority of the advantage racing model to a real test, would afford to test qualitative predictions possibly not shared by existing alternatives. For instance, does their model predict set size effects during instrumental learning? Does their model predict qualitative shifts in choice and reaction times when different task blocks have different mean rewards? At the moment the primary results rely solely on improved fits, but it would be important to show their model's unique ability to capture more salient qualitative behavioral effects. This point requires either the reanalysis of existing data from reinforcement problems with more than two alternatives and/or with blockwise variations in mean reward, or the collection of additional data. We understand the difficulty of collecting data in the current context, but this additional data is very important to support the qualitative superiority of the advantage racing model.
2) It is not clear how the advantage racing model would easily transfer to problems with more than two alternatives. As depicted in Equation 1, the model depends on the difference between two unique Qvalues (weighted by w_{D}). How would this be implemented with more than two alternatives? There are several possibilities of implementations (e.g., the current Qvalue relative to the top Qvalue, the current Qvalue minus the average Qvalue, etc.), but they seem to require additional heuristics that are not described in the current implementation of the advantage racing model. The authors could also incorporate modulation of drift rates by policies, or use an actorcritic approach. In any case, the model in its current form cannot straightforwardly transfer to more than two alternatives. Given that the authors stress the benefits of their model for sequential reinforcement problems with more than two alternatives, they should provide an implementation of their model that can transfer to more than two alternatives (and also test this implementation against human data in such problems, see the previous point).
3) All three racing models (including the authors' preferred model) implement an urgency signal. It is unclear why the authors did not consider a similar mechanism within the DDM framework. Within this framework, urgency could possibly be implemented either as (linearly or hyperbolically) collapsing bounds, or as selfexcitation (inverse of leak). Both implementations require only one extra parameter, as in the racing models used by the authors. The lack of explicit urgency needs to be addressed, because the current superiority of the advantage racing model could be due in part to its urgency component which is absent from the driftdiffusion model. And the importance of urgency in such problems has already been reported in earlier studies.
4) The authors appreciate the rigorous parameter recovery analyses in the supplement, but it would be very useful to perform also a model “separability” analysis – i.e., plot a confusion matrix between alternative models. Indeed, it seems like several of the tested models are relatively similar qualitatively speaking and it would thus be very useful to know how confusable they are. The fact that parameters from one known groundtruth model can be recovered accurately does not speak to the confusability between different models.
5) It is unclear that the authors are implementing SARSA (Rummery and Niranjan, 1994). Indeed, SARSA is: Q(s,a)[t+1] = Q(s,a)[t] + lr(r[t+1] + discount(Q(s,a)[t+1]) – Q(s,a)[t]. However, this task is a “singlestep” problem. So it seems like the authors are rather implementing SAR – i.e., the standard RescorlaWagner “delta” rule. Please clarify this modeling aspect.
6) The basic aggregate behavior and model fitting quality should be described and illustrated beyond percentile distributions of reactiontimes for correct and error trials. The authors should plot the grandaverage RT distributions for subjects and bestfitting model predictions (pooled across subjects and trials). How variable were subjects' behavior? The reviewers understand that the model was fit hierarchically, but it would be nice (possibly in the supplement) to see a distribution of fit quality across subjects (1), to see RT distributions of a couple of good and bad fits (2), and to check whether the results hold after excluding the subjects with worst fits (if there are any outliers, 3). Related, in the RT percentile plots (Figures 3 and 4), it would be useful to see some measure of variability between subjects.
7) The authors write that RLAEMs assume that "[...] a subject gradually accumulates evidence for each choice option by sampling from a distribution of memory representations of the subjective value (or expected reward) associated with each choice option (known as Qvalues)." It is unclear what the authors mean by "a distribution of memory representations". Either the authors could replace this by "a running average of rewards", or they truly mean something like sampling from memory – like recent papers e.g., Bornstein et al., 2017, Nat. Comm. Sampling from (a distribution of) memory representations is a relatively new idea, and I think it would help if the authors would be more circumscribed in the interpretation of these results, and also provide more context and rationale both in the Introduction and Discussion. For example, an interesting Discussion paragraph would be on how such a memorysampling process might actually be implemented in the brain.
https://doi.org/10.7554/eLife.63055.sa1Author response
Essential revisions:
1) Starting from the Abstract, the authors allude to reinforcement problems with more than 2 alternatives (1) and to the role of absolute choice values (2) in characterizing the limitations of the standard DDM. However, in the current manuscript, point 1 is not addressed (and actually does not appear to be amenable to the current model implementation, see the next point), and point 2 is addressed via modest quantitative improvements to model fits rather than true qualitative divergence between their model and other models' ability to capture specific behavioral effects. The authors could greatly strengthen their conclusions if they extend their model to RL data sets with (1) more than two alternatives, and (2) variations in the absolute mean reward across blocks of learning trials. These experimental variants, which would put the superiority of the advantage racing model to a real test, would afford to test qualitative predictions possibly not shared by existing alternatives. For instance, does their model predict set size effects during instrumental learning? Does their model predict qualitative shifts in choice and reaction times when different task blocks have different mean rewards? At the moment the primary results rely solely on improved fits, but it would be important to show their model's unique ability to capture more salient qualitative behavioral effects. This point requires either the reanalysis of existing data from reinforcement problems with more than two alternatives and/or with blockwise variations in mean reward, or the collection of additional data. We understand the difficulty of collecting data in the current context, but this additional data is very important to support the qualitative superiority of the advantage racing model.
We followed the reviewers’ advice to perform an additional experiment. Specifically, we designed an instrumental learning task in which the participants had to repeatedly choose between three choice alternatives. The RLDDM cannot be applied in settings beyond twochoice alternatives, providing a strong qualitative divergence between the models’ predictions and capabilities. Within this multialternative experiment, we included a reward magnitude manipulation to test whether the RLARD is able to capture the behavioral effects of changes in overall reward magnitude.
We describe the new experiment as well as the multialternative RLARD in the main text of the revised manuscript. For convenience, we copied the relevant text below:
“Multialternative choice
Finally, we again drew on Van Ravenzwaaij et al.’s (Van Ravenzwaaij et al., 2020) advantage framework to extend the RLARD to multialternative choice tasks, a domain where the RLDDM cannot be applied. […] As a consequence, both the Qvalue sum (weighted by median ${w}_{S}=0.15$), and the smaller changes in the Qvalue difference (weighted by median ${w}_{D}=1.6$), increased the drift rates for the response accumulators (${v}_{TD}$; Figure 12D), which led to higher accuracy and faster responses.”
Furthermore, the Materials and methods section provides more detail on experiment 4 and on the implementation of the RLARD:
“Experiment 4
Participants
43 participants (mean age 20 years old [SD 4.29 years], 5 men, 36 righthanded) were recruited from the subject pool of the Department of Psychology of the University of Amsterdam and participated for course credits. […] We also performed a parameter recovery study using the same methods as in earlier experiments, the results of which are shown in Figure 11—figure supplement 1.”
2) It is not clear how the advantage racing model would easily transfer to problems with more than two alternatives. As depicted in Equation 1, the model depends on the difference between two unique Qvalues (weighted by w_{D}). How would this be implemented with more than two alternatives? There are several possibilities of implementations (e.g., the current Qvalue relative to the top Qvalue, the current Qvalue minus the average Qvalue, etc.), but they seem to require additional heuristics that are not described in the current implementation of the advantage racing model. The authors could also incorporate modulation of drift rates by policies, or use an actorcritic approach. In any case, the model in its current form cannot straightforwardly transfer to more than two alternatives. Given that the authors stress the benefits of their model for sequential reinforcement problems with more than two alternatives, they should provide an implementation of their model that can transfer to more than two alternatives (and also test this implementation against human data in such problems, see the previous point).
We addressed the implementation of the multialternative RLARD in response to comment 1 above.
3) All three racing models (including the authors' preferred model) implement an urgency signal. It is unclear why the authors did not consider a similar mechanism within the DDM framework. Within this framework, urgency could possibly be implemented either as (linearly or hyperbolically) collapsing bounds, or as selfexcitation (inverse of leak). Both implementations require only one extra parameter, as in the racing models used by the authors. The lack of explicit urgency needs to be addressed, because the current superiority of the advantage racing model could be due in part to its urgency component which is absent from the driftdiffusion model. And the importance of urgency in such problems has already been reported in earlier studies.
We agree with the reviewer that including an urgency mechanism in the RLDDM could potentially improve the model’s quality of fit. However, there is no known analytical solution to the likelihood of the DDM with collapsing bounds or an urgency gain signal. Researchers interested in fitting the DDM with an urgency mechanism therefore must resort to simulationbased approximations of the likelihood function. In stationary experiments, the urgencyDDM must be simulated for N trials (commonly in the range of 10,00050,000; e.g., Miletić et al., 2017; Trueblood et al., 2020) per condition per subject in each iteration of the MCMC sampling process. While computationally expensive, with good computational facilities this can still be feasible. However, the RLDDM has singletrial drift rates, implying that the likelihood distribution needs to be approximated for each individual trial separately, hence requiring the simulation of N trials per trial per subject, providing a 208fold increase in the number of trials that need to be simulated for experiment 1 alone (and more for the other experiments). The explosion in the number of simulations becomes computationally infeasible.
Secondly, it is important to point out that the origin of the concept of urgency lies in racing accumulator models, similar to the implementation we used in the RLARD. The development of DDMs with collapsing bounds and urgency gain signals was only later. As such, our model’s urgency mechanism remains close to the original concept.
In the revised manuscript, we address this point in the Discussion:
“Although an urgency mechanism such as collapsing bounds (Boehm et al., 2016; Bowman et al., 2012; Hawkins et al., 2015; Milosavljevic et al., 2010) or gain modulation (Boehm et al., 2016; Churchland et al., 2008; Ditterich, 2006; Hawkins et al., 2015) could potentially improve the fits of the RLDDM, fitting DDMs with such mechanisms is computationally very expensive, usually requiring the researcher to use simulationbased approximations (e.g., Turner and Sederberg, 2014). […] Furthermore, the origin of the concept of urgency lies in studies using racing accumulator models (Ditterich, 2006; Mazurek et al., 2003; Reddi and Carpenter, 2000), which was only later incorporated in the DDM (Milosavljevic et al., 2010); the implementation in the RLARD remains conceptually close to the early proposals.”
4) The authors appreciate the rigorous parameter recovery analyses in the supplement, but it would be very useful to perform also a model “separability” analysis – i.e., plot a confusion matrix between alternative models. Indeed, it seems like several of the tested models are relatively similar qualitatively speaking and it would thus be very useful to know how confusable they are. The fact that parameters from one known groundtruth model can be recovered accurately does not speak to the confusability between different models.
In the revised manuscript, we included confusion matrices as Figure 3—figure supplement 3. Since our main focus is on the comparison between the RLARD and the RLDDM (and the generation of the confusion matrices is computationally intensive), we only compared these two models. These results show that the BPIC nearly always correctly identified the datagenerating models.
5) It is unclear that the authors are implementing SARSA (Rummery and Niranjan, 1994). Indeed, SARSA is: Q(s,a)[t+1] = Q(s,a)[t] + lr(r[t+1] + discount(Q(s,a)[t+1]) – Q(s,a)[t]. However, this task is a “singlestep” problem. So it seems like the authors are rather implementing SAR – i.e., the standard RescorlaWagner “delta” rule. Please clarify this modeling aspect.
We apologize for this confusion, and removed all references to “SARSA”, which we substituted with the “delta rule”.
6) The basic aggregate behavior and model fitting quality should be described and illustrated beyond percentile distributions of reactiontimes for correct and error trials. The authors should plot the grandaverage RT distributions for subjects and bestfitting model predictions (pooled across subjects and trials). How variable were subjects' behavior? The reviewers understand that the model was fit hierarchically, but it would be nice (possibly in the supplement) to see a distribution of fit quality across subjects (1), to see RT distributions of a couple of good and bad fits (2), and to check whether the results hold after excluding the subjects with worst fits (if there are any outliers, 3). Related, in the RT percentile plots (Figures 3 and 4), it would be useful to see some measure of variability between subjects.
We included the following additional plots:
Figure 3—figure supplement 4, showing grand average RT distributions (both data and posterior predictive distributions), as well as the RT distributions for the first 10 subjects. From visual inspection of similar plots for all subjects, we found no subjects for which the model clearly misfit the empirical RT distributions; the quality of fit of the first 10 subjects was representative of the quality of fit of all other subjects. For experiments 24, similar plots are now provided as Figure 6—figure supplement 4, Figure 7—figure supplement 4, Figure 11—figure supplement 2, respectively.
Figure 4—figure supplement 4, which replicates Figure 4 but includes error bars (standard error) on points of empirical data to visualize betweensubject variability. Since this plot combines two different approaches to the concept of uncertainty (a frequentist approach, where uncertainty is assumed to lie in the data, and a Bayesian approach, where the uncertainty is assumed to lie in the model), we prefer to keep this figure supplementary instead of replacing the main figure to retain consistency in our Bayesian approach in the main text. For experiments 24, similar plots are now provided as Figure 6—figure supplement 5, Figure 7—figure supplement 5, and Figure 11—figure supplement 3, respectively.
7) The authors write that RLAEMs assume that "[…] a subject gradually accumulates evidence for each choice option by sampling from a distribution of memory representations of the subjective value (or expected reward) associated with each choice option (known as Qvalues)." It is unclear what the authors mean by "a distribution of memory representations". Either the authors could replace this by "a running average of rewards", or they truly mean something like sampling from memory – like recent papers e.g., Bornstein et al., 2017, Nat. Comm. Sampling from (a distribution of) memory representations is a relatively new idea, and I think it would help if the authors would be more circumscribed in the interpretation of these results, and also provide more context and rationale both in the Introduction and Discussion. For example, an interesting Discussion paragraph would be on how such a memorysampling process might actually be implemented in the brain.
We apologize for the confusion raised by our original phrasing. We intended that drift rates are sampled from a running average of rewards. We rephrased the sentence accordingly.
https://doi.org/10.7554/eLife.63055.sa2Article and author information
Author details
Funding
Nederlandse Organisatie voor Wetenschappelijk Onderzoek (016.vici.185.052)
 Birte U Forstmann
Australian Research Council (DP150100272)
 Andrew Heathcote
Australian Research Council (DP160101891)
 Andrew Heathcote
University of Amsterdam (VIP Grant)
 Andrew Heathcote
The funders had no role in study design, data collection and interpretation, or the decision to submit the work for publication.
Acknowledgements
We thank Barbara Mathiopoulou and Chris Riddell for their help collecting the data. This work was supported by an NWOVICI grant (BUF), an ABC VIP grant and ARC DP150100272 and DP160101891 grants (AH).
Ethics
Human subjects: Informed consent was obtained in all experiments prior to the experiment onset. The local ethics board of the Department of Psychology, University of Amsterdam, approved the study, with reference numbers 2018BC9620 (experiment 1), 2019BC10672 (experiment 2), 2019BC10250 (experiment 3), and 2020BC12788 (experiment 4).
Senior Editor
 Joshua I Gold, University of Pennsylvania, United States
Reviewing Editor
 Valentin Wyart, École normale supérieure, PSL University, INSERM, France
Reviewer
 Jan Willem de Gee, Baylor College of Medicine, United States
Publication history
 Received: September 15, 2020
 Accepted: January 26, 2021
 Accepted Manuscript published: January 27, 2021 (version 1)
 Version of Record published: February 12, 2021 (version 2)
Copyright
© 2021, Miletić et al.
This article is distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use and redistribution provided that the original author and source are credited.
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