1
Research Internship
Differentiating between Perceptual and
Post-perceptual Biases
By
James Moultrie
12th June 2020
32 ECTS
January - June 2020
Supervisor:
N. Sanchez-Fuenzalida
Assessors:
Dr S. van Gaal
Dr F. van Opstal
The age-old question of “What is consciousness?” has troubled many researchers over millennia. First and foremost, one may ask, what does it mean to be conscious? Since the dualist mind-body view established from Plato to Descartes seems antiquated by now (Changeux, 2006; Lycan and Dennett, 1993), what makes up consciousness in our brain? What does it mean to be conscious of something? To begin answering these questions, let us examine one large distinction in the study of consciousness in neuroscience: generic consciousness and specific consciousness.
Generic consciousness focuses on how neural properties might explain when a state is conscious rather than not (Wu, 2018). This is where consciousness fits in its intransitive definition and becomes synonymous with ‘wakefulness’ (e.g. “the patient was still conscious”; Dehaene and Changeux, 2011; Dehaene et al., 2006; Kriegel and The Hegeler Institute, 2004; Rosenthal, 1997). This is linked to an aspect of consciousness called state consciousness, which posits that different degrees of consciousness exist in different mental states (Rosenthal, 1993) and wonders “how conscious [states] differ from those which are not” (Rosenthal, 1997). For example, when we are awake, when we are attentive to our environment, when we are asleep (Siclari et al., 2017), in a coma (Cavanna et al., 2010; Di Perri et al., 2016), or presumably any other state, we experience varying degrees of consciousness – these are thought to “vary almost continuously from coma and slow-wave sleep to full vigilance”(Dehaene and Changeux, 2011). Before wondering about how conscious a mental state may be, we must know whether the creature we are considering – the host of the mental state – is capable of being conscious in the first place. This is creature consciousness, which can be defined as the property of any cognitive system, be it a human or a bat, to be “awake and responsive to sensory stimulation” (Rosenthal, 2009). This may also vary in degree. For example, how conscious is a shrimp? Or a bee? Honey bees are diurnal animals, meaning that they are awake during the day and asleep during the night – much like humans (Kaiser and Steiner-Kaiser, 1983). Some of us have had the unpleasant experience of discovering firsthand their responsiveness to sensory stimulation. One may then wonder whether self-consciousness is necessary for a creature to be deemed conscious (Carruthers, 2000; Velmans, 2012). There have been countless attempts to deny consciousness from non-human animals, each time the boundary of consciousness being pushed further away – from a uniquely human property, to one shared with the great apes, then with mammals, and so on (there has been substantial work by C. Allen on this, see Allen and Trestman, 1995; Bekoff, 2007). We shall skip past these low-resolution definitional squabbles and assert that the study of generic consciousness fundamentally relates to the study of consciousness and its absence (Van Gulick, 2004).
Specific consciousness poses the arguably more technical question of how neural properties might explain the content of a conscious state (Wu, 2018). Here, it is implied that a conscious state is a prerequisite for the experience of conscious content (e.g. being awake rather than asleep; Baars, 1993; Dehaene et al., 2006). Specific consciousness also entails an essentially perceptual approach, as opposed to the physiological (or philosophical) approaches to generic consciousness. This is commonsensical, since perception is in great part what makes up the
content of what we experience. For example, assuming a normal, healthy condition, we can all see a vase of flowers and agree on what it is - granted, however, there remains a certain margin for interpretation, proper to our own experience (Aru et al., 2016). This idea of consciousness refers to the transitive definition of the word – to be conscious of something – and may seem synonymous with ‘awareness’ (e.g. “I am conscious of/aware of/consciously aware of the red light”; Velmans, 2009). This kind of consciousness, which may be called perceptual consciousness (Fazekas and Overgaard, 2018; Lau, 2008), will be the object of this paper: To what extent does our perception shape our conscious experience? Before diving in, we must first define two more important aspects of consciousness: phenomenal consciousness and access consciousness. Phenomenal consciousness refers to the qualia of a state, or what it is like to be in that state (Block, 1995; Nagel, 1974). This draws near to the idea of perceptual consciousness. It entails “the experiential properties of sensations, feelings, and perceptions” (Block, 1995). It is an aggregate of all the input that make up the conscious experience we have of a given phenomenon. Furthermore, and crucially, it excludes anything having to do with cognition and intentionality. It is therefore fundamentally specific, and fundamentally experiential. Access consciousness, on the other hand, is used for reasoning and direct deliberate control over action and speech. Accessing our consciousness entails introspection, knowledge, and awareness of the phenomena we perceive (Block, 1995). Dehaene and Changeux define it as “the observation that a piece of information, once conscious, becomes broadly available for multiple processes including action planning, voluntary redirection of attention, memory, evaluation, and verbal or non-verbal report” (Dehaene and Changeux, 2004). Access consciousness is therefore fundamentally functional. To understand the contents of consciousness in an experimental paradigm, many researchers consider the reportability of (and thus the access to) experienced content as a hallmark component (Dehaene and Changeux, 2011). If someone can report what they experience, then they are deemed conscious of that experience. According to global workspace theorists (e.g. Baars, Dehaene, Naccache), information is made widely available in the brain following a global “ignition” of pre-frontal, parieto-temporal and cingulate networks (Baars, 1993; Dehaene and Changeux, 2011; Dehaene and Naccache, 2001). This requires the attention of the creature in question: if a stimulus is available, then one can access it; if a stimulus receives attention, then one is accessing it. Stimuli too weak do not cross a subliminal threshold (etymologically, below the limit), meaning that activation is very weak and does not provoke an ignition of the networks. Strong enough stimuli which do not receive attention are deemed ‘pre-conscious’ and remain limited to localized networks (e.g. sensori-motor processors, ventral stream; Dehaene et al., 2006). This means that if a stimulus was shown but was unseen, it can be either because: the stimulus was limited by bottom-up strength, or by a (perhaps transient) lack of top-down attention. The former has been established and well demonstrated with visual masking paradigms, where target stimuli are flashed briefly between two ‘masking’ stimuli (Del Cul et al., 2009; Dehaene et al., 2001; Kouider and Dehaene, 2007). The latter is wonderfully exemplified with inattentional blindness, in a famous video featuring a gorilla (Simons and Chabris, 1999). Thus, for a stimulus to be seen
(i.e. reported), it requires both enough strength and attention (Dehaene and Changeux, 2011; Dehaene et al., 2006).
To measure consciousness in the brain, also known as the “neural correlates of consciousness” i.e. the minimal neuronal mechanisms jointly sufficient for any one specific conscious percept (Crick and Koch, 1990; Koch, 2004), researchers may ask participants using subjective measures (where each trial is reported as “seen” or “unseen”), or objective measures (where performance is measured across trials (Persuh, 2017; 2009). In a detection task, participants are asked to report their visual experience on each trail (Del Cul et al., 2007; Pinto et al., 2017; Sergent and Dehaene, 2004). In a discrimination task, participants are asked to discriminate between responses options (Weiskrantz et al., 1995). The main issue taken with objective measures is that task performance may be a major confounding factor (Lau, 2008), and the main issue taken with subjective measures is that performance might be contaminated by response bias (e.g. participants might be incentivized by the researchers to respond in one way or another; Peters et al., 2016).
By asking participants what they saw during a trial, be it through detection or discrimination, research is only targeting access consciousness. However, one compelling finding has demonstrated a major limitation to this: blindsight patients. Blindsight patients have “blind” areas in their visual fields, typically resulting from damage in the visual cortex. When a stimulus is shown to the damaged part of their visual fields, they subjectively report that they saw “nothing”. Curiously, some of them can objectively guess above chance level about features of the object shown, such as motion, location, orientation, or color. Likewise, when asked to grasp the object in their blind visual field, they may shape their hand appropriately even if they report that they cannot see the item (Weiskrantz, 1986; Weiskrantz et al., 1995; Whitwell et al., 2011). This means that information that is not accessed is still processed to some extent. This entails there could be a distinction between what we respond and what we can consciously access, which has led researchers to believe that to study consciousness, reportability might not be essential. The distinction between what we perceive and what we can report is exemplified in the positions taken by several researchers. Ned Block believes that perception “overflows” access; Block, 2011). In line with the case of blindsight patients, even if subliminal or pre-conscious stimuli are not (yet) access-conscious, they might nonetheless form some kind of representation in the brain (“when observing a complex scene we are conscious of more than we can report or think about” (Block, 2011). One could then consider access consciousness as a constraint on the phenomenological experience we have, since what is reportable is supposedly always less “rich” than what is perceived. Naccache (2018) argues instead that access is pre-conditional to phenomenal consciousness, since the ability to know that one is phenomenally conscious of something is predicated on the fact that we can “access this experience and self-report it”. This would mean that anything that is phenomenally conscious is also access conscious by definition, and thus that access consciousness might be “all there is to it” (Naccache, 2018).
To circumvent this altogether, researchers are turning towards no-report paradigms (for a review, see Tsuchiya et al., 2015). For example, from neuronal activity in the visual cortex in macaques and in humans, researchers have been able to decode sensory stimuli (Graf et al., 2011; Vetter et al., 2014). Moreover, by using magnetoencephalography and paradigms such as binocular rivalry (presenting different stimuli to both eyes), researchers can measure when faces or houses arise to conscious awareness (Sandberg et al., 2013). Yet another technique consists of using optokinetic nystagmus (eye movements) and binocular rivalry, with colored gratings moving in opposite directions (Frässle et al., 2014). In these paradigms, objective measures are gathered without requiring a response from the participant. Taken together, the existence of blindsight, the distinction between perceptual and access consciousness, and the usage of no-report paradigms open up another question. Is what we report during a task truly a reflection of what we perceive? Or are there other processes at hand when pressing the response button? If so, what processes might there be? Let us illustrate some of these. In a detection task, a dim light is flashed on a screen. Due to the poor visibility of the stimuli, let us say that the average participant reports the light 50% of the time. Then, the researcher incentivizes the participant to report the light by rewarding them with money. Even if the average participant still sees the light only 50% of the time, they might be inclined to report it more often in order to maximize their reward. In this sense, the participant was biased. In theory, this bias was post-perceptual, since it was not the result of a manipulation of the stimulus itself, but rather a manipulation of the most favorable response to give. It took place ‘after perception’ when the participant was deciding what to respond.
Sanchez-Fuenzalida and colleagues conducted a similar experiment using the Müller-Lyer illusion. This manipulation affects the perceived length of lines (flanked by arrowheads facing either outwards or inwards) and is a well-established perceptual bias manipulation (Morgan et al., 1990; Wickens, 2001). With this manipulation, even if the line length remains technically the same, a participant would consider the line to be longer when the arrowheads are facing inwards, and shorter when the arrowheads are facing outwards. In addition to the Müller-Lyer manipulation, Sanchez-Fuenzalida used a category-cost contingency with two conditions: one yielded a larger monetary discount for erroneously reporting longer lines, and the other for shorter lines. This is considered a post-perceptual bias manipulation (Sutton and Barto, 1998). The task layout was the following: 5 (biased) discrimination tasks, where a target line would have to be categorized as shorter or longer than a previously presented unbiased reference line, followed by 1 perceptual task, where the participant would have to reproduce the average length of the presented lines. The second task was used as a proxy for perception (i.e. the perceived length of the presented lines). Crucially, there was no reward or discount in the averaging task, meaning that there was no clear incentive to perform the task in a biased way. Their hypothesis was that if the bias was perceptual (as in the Müller-Lyer), it would bias the responses in the discrimination task and in the averaging task. If the bias was post-perceptual (as in the category-cost contingency), it would bias only the responses in the discrimination task. To control for the different conditions, a flat discount was applied to erroneous
responses in the Müller-Lyer condition, and flat edges (yielding no perceptual bias) were flanked to the lines in the category-cost contingency condition. Next, we shall examine the measures that were used in this experiment. For example, how to assess the participants’ bias in the discrimination task, or in the averaging (perceptual) task? Furthermore, how to attribute a measured bias effect to a perceptual bias effect, or to a post-perceptual bias effect? In other words, did the participants report longer lines more often because they consciously perceived a greater number of lines being longer, or did they simply reporting a greater number of lines as longer as a way to minimize punishment?
To answer these questions, we must first explain the experimental paradigm of Signal Detection Theory (Wickens, 2001). As was shown by Sanchez-Fuenzalida’s experiment, it is widely accepted that we base our judgments on perceptual input, in this case the varying size of the line lengths or the directions of the arrowheads, but also on internal decision thresholds called “criteria”. Put otherwise, these could reflect, respectively, “bottom-up sensory processes and top-down cognitive factors” (Kuang, 2019). Post-perceptual manipulations, such as rewards or punishments, may affect this criterion. As we will see, so can perceptual input (Witt et al., 2015). Nonetheless, if a participant were to respond more long lines as a result of being punished when incorrectly reporting short lines, this could be represented in SDT by a shift in the criterion (Wickens, 2001). Aside from the criterion, the other measure used in SDT is sensitivity, or d’ (d prime), which captures the participants’ ability to distinguish between signal and noise. When a stimulus is shown by an experimenter, based on whether the presented stimulus refers to the signal-present or to the signal-absent category and whether their answer is correct or incorrect, each response can be categorized as either Hit (H); Miss (M); False Alarm (FA); or Correct Rejection (CR). The distance between the means of the signal and noise distributions is d’. The criterion represents the participants’ likelihood to choose one response over the other, which would then represent a bias if it were unequal to 0 (Wickens, 2001). This is illustrated in Figure 1. Thus, to measure bias in the discrimination task, Sanchez-Fuenzalida used the participants criterion data as a function of condition – with this measure, he could tell if their responses on the same line length changed based on discounting or different arrowheads. Using the sensitivity data (also per condition), he could tell if it was easier or more difficult to differentiate correctly between long and short lines. However, one question remains unanswered: How do we tell if a measured bias effect is perceptual or post-perceptual?
Figure 1: Signal Detection Theory. The x axis represents the participants’ sensed intensity of the stimuli,
also known as internal response. This can also be a more concrete measure, such as the (unsensed) response of V1 neurons. The y axis represents the probability of that internal response to occur. The N distribution refers to when the signal is absent, and thus represents internal and external noise (task-irrelevant neural processes and task-(task-irrelevant environmental stimuli, respectively). The S distribution refers to when the signal is present, and thus represents the sum of internal noise, external noise, and signal. d’ represents the difference between the means of the two distributions, and thus the sensitivity of the participant to distinguish when the signal is present or absent. “Yes” and “No” refer to the question: Was the signal present? The criterion, represented by a vertical line, is the threshold at which the participant responds that the signal is present or absent. Overlapping distributions of noise (N) and signal + noise (S) cause false alarms (FAs) and misses on either side of the criterion (Wickens, 2001; Image taken from Higham, 2007).
To answer this, many researchers usually distinguish perceptual from post-perceptual biases by attributing the former to a shift in d’ and the latter to a shift in criterion (see, Rosenthal et al., 2009; Shams and Kim, 2010; Watkins et al., 2005). Similarly, authors using the stream/bounce illusion (seeing two identical objects cross path diagonally in the middle of screen, with an audio cue that is present or absent; Grove et al., 2012) mention that only d’ can capture perceptual changes and only c can capture bias or decisional processes. This is also the case with researchers using the ventriloquist effect (where an auditory and a visual stimulus’ locations must be assessed as “same” or “different”; Choe et al., 1975) as well as in other audiovisual interactions (Sanabria et al., 2007). More recently, however, it has been argued that SDT cannot dissociate perceptual biases from post-perceptual biases by using d’ and the criterion, since a perceptual bias can affect c without affecting d’ (Morgan et al., 1990; Raslear, 1985; Witt et al., 2015). Indeed, a perceptual bias can (and will) yield an effect solely on c if it shifts both the signal and noise distributions in a proportional manner. This would be the case in an experimental setup where the noise (or “signal absent”) distribution would not truly reflect an absence of stimuli, for example if the noise distribution would refer to the presentation of short lines rather than long ones. In this sense, the measured ‘criterion-alone’ effect could be wrongly interpreted as post-perceptual, since d’ remained unchanged. To
reformulate, this could be due to the fact that the bias manipulation affects both distributions equally – a shift would be noticed only in the criterion compared to the control condition, since this measure is relative to the signal and noise distributions. This is the case in the Müller-Lyer illusion, as demonstrated by Witt et al using simulated data, and by Sanchez-Fuenzalida using empirical data. Thus, according to Witt et al, “SDT is effective at discriminating between sensitivity and bias but cannot by itself determine the underlying source of the bias, be it perceptual or response based.” (Witt et al., 2015)
A more recent approach using drift diffusion models (DDMs) attempts to solve this problem. DDMs are used to model the evidence accumulation process leading to a response in a two-choice situation. A decision is made when the accumulation of evidence reaches one of two boundaries (Ratcliff, 1978). Researchers have attempted to separate the effects of response bias (e.g. stimulus-reward contingencies) and stimulus bias (e.g. memory strength required for categorization) using the measures of starting point and drift rate, respectively (White and Poldrack, 2014). The starting point of the model represents where the evidence for one the responses begins accumulating – if different from 0, it may represent bias towards one of the responses. Drift rate refers to the speed at which evidence for one of the responses is accumulated (Ratcliff, 1978). Although White and Poldrack assert with caution that either type of bias mainly affects either parameter of the model, they implicitly assume that a shift in starting point is inherently post-perceptual, and that a shift in drift rate is inherently perceptual. They conclude that response biases are post-perceptual and that stimulus biases are perceptual. However, both of these types of biases affect an internal criterion of the observer, and they do not empirically substantiate their assumption that post-perceptual and perceptual biases affect the starting point and drift rate respectively. Therefore, the question about the nature of criterion shifts as perceptual or post-perceptual is also left open.
Thus, as a follow up to Sanchez-Fuenzalida’s Müller-Lyer experiment, we aimed here to differentiate between perceptual and post-perceptual biases using the base-rate manipulation. A base-rate manipulation consists of changing the base-rate at which one stimulus or another appears during an experiment and informing the participant of such a manipulation (i.e. “75% of the target lines will now be longer than the reference line”). To this avail, we devised two tasks to test which effect(s) this bias manipulation would yield. We used two experiments in this study. First, we test the participants’ response bias by asking them to compare a series of lines, one by one, as being shorter or longer than a reference line. This is the length comparison task. After 5 such questions, we ask participants to estimate the average size of the lines they were just presented. This is the average length estimation task, which we use as a proxy for the length they actually perceived while performing the task. Because this task is not affected by the bias manipulation (or any other incentive to respond in a certain way), this should reflect a perceptual bias, or lack thereof, that would be yielded by the base-rate manipulation during the other task. In the second experiment, we changed the setup and tasks slightly. We further separated the perceptual and post-perceptual components of the tasks by replacing the averaging task with a reproduction task (reproducing
a single target line, rather than an average). With this new setup, participants would no longer have to base their perceptual task response on the discrimination trials affected by the bias manipulation, thus rendering the tasks independent from each other.
In this setting, if the bias effect is perceptual, we would expect it to bias the participant’s response (length comparison bias; H1) and perception (average estimation error/reproduction error; H1A). This is our alternative hypothesis (HA), which is not predicted. If the bias effect is post-perceptual, we would expect it to bias response (H1) but not perception (H0). This is our main hypothesis (HB), which is predicted. In both cases, for H1, the bias to response should be in the correct bias direction (i.e. base-rate condition long biases responses towards longer lines). Because we are assuming that our manipulation biases the criterion and will have little effect on d’, which is supported by data on the Length comparison task from Sanchez-Fuenzalida’s experiment, we know that there should be no difference in sensitivity between conditions (H0B). If there is a difference in sensitivity between the two conditions (H1B), then it could be the case that there is a perceptual bias, which would point towards HA. Thus, if our main hypothesis is supported by sufficient evidence (H1 + H0 + H0B), we will be able to conclude that the base-rate manipulation is a post-perceptual bias. If the alternative hypothesis is supported by sufficient evidence (H1 + H1A + H1B), we will be able to conclude that the base-rate manipulation is a perceptual bias.
Experiment 1
Methods
Participants Fifteen naive undergraduate or graduate students (Mean age = 21, SD = 4.25, 12
females) from the University of Amsterdam participated in this experiment. They all had normal or normal to corrected vision, and a level of English sufficient to read and understand the instructions. They gave written informed consent prior to participating in the study, which was approved by the university's ethics committee. The experiment lasted on average 35.7 minutes (SD = 11), excluding the instruction period and the breaks. Participants were rewarded 10€ or 1 research credit for completing the experiment. Additionally, up to 5€ (or .5 research credits) could be earned based on performance (see Procedure).
Apparatus Stimuli were generated and scripted using a desktop computer running a software
designed on Python 2.7. They were presented on a monitor of 23” with a resolution of 1920x1080 and a refreshment rate of 120Hz. The size of each pixel was 0.265mm. At a viewing distance of 70cm, each pixel was approximately 0.02 visual angle degrees.
Experimental designThis experiment employs one bias source (a base-rate manipulation) and a within-participants factor with two bias directions (short/long) nested in the bias source.
Independent variable: Base-rate manipulation
Bias direction long: The target line distribution is skewed so that 75% of the lines presented during the next block are longer than the reference line. Participants were informed about this manipulation.
Bias direction short: The target line distribution is skewed so that 75% of the lines presented during the next block are shorter than the reference line. Participants are informed about this manipulation. These bias manipulations are shown in Figure 2.
Figure 2: Base-rate manipulation
For each bias direction, a greater proportion of the lines are longer or shorter than the reference. The reference line is always 300 pixels long, and all lines are 4 pixels thick.
Confusion matrix
According to each participant’s responses and the line type that was presented, we labeled the trials as shown in Table 1.
Table 1 : Confusion matrix.
Line type Participant response Confusion matrix
Long Long True long
Short False short
Short Long False long
To correct for perfect performance, 0.5 is added to the frequencies of every cell in the confusion matrix if any of the cells are zero. (Hautus, 1995)
We calculate the Hit rate and False alarm rate as follows: Hit - rate = Trueshorttrials : (Trueshorttrial+Falselongtrials) FA - rate= Falseshorttrials : (Falseshorttrials + Truelongtrials)
Dependent variables
Length comparison sensitivity: From participants’ responses in the length comparison task, we calculate the decision sensitivity (d’). We calculate each participant’s d’ for each bias direction, as follows:
d '=Z(Hit−rate)−Z(FA−rate)
Length comparison bias: From participants’ responses in the length comparison task, we calculate the decision bias (c). We calculate each participant’s criterion for each bias direction, as follows:
c= -1/2[Z(Hit - rate)+Z(FA - rate)]
Average length estimation error: From participants’ responses in the average length estimation task, we calculate their average deviation from the actual average length of the presented lines.
For each mini-block, the average length of the target lines presented is calculated then subtracted to the average estimation of the participant, as follows:
Mini-block estimation error = Mini-block average estimation - Mini-block average
Tasks
Length comparison task Subjects were presented with a target line which they would have to
report as shorter or longer than the reference line by clicking the left or right mouse button respectively. Responses were blocked for the first 200ms after stimulus onset to avoid accidental clicks, or devious ways of completing the experiment (i.e. rushing it). This task was self-paced.
Average length estimation task After 5 trials of the length comparison task, participants had
to estimate the average length of the 5 previous target lines they saw by moving the mouse upwards or downwards until they confirmed their estimation with the middle mouse button. This task was self-paced.
Stimuli Visual stimuli consisted of a reference line and target lines. The reference line was the
same throughout the entire experiment and consisted of a line of 300 pixels wide. Target lines differed from that size based on the titrated length extracted from the staircase procedure (see Staircase procedure). All lines were 4 pixels thick.
General procedure
Instructions Prior to beginning the experiment, participants went through the instructions and
example mini-blocks for approximately 10 minutes. In order: they completed mini-blocks of the length comparison task with instructions (e.g. “Left-click for ‘shorter’”) and feedback for correct/incorrect responses (i.e. “Correct” or “Incorrect”) until they obtained at least 10 correct responses. They were informed that the target line would exhibit a slight horizontal jitter at every trial, in order to prevent using the edges of the lines to estimate their length. Then, they were informed that they would no longer receive feedback or instructions and completed mini-blocks with such parameters until they obtained at least 10 correct responses. They were informed that a staircase procedure would take place to adjust the level of the task to their skill, and underwent the staircase procedure explained in the following section, completing length comparison mini-blocks with no instruction or feedback until a minimum of 25 reversals was reached. They received instructions for the averaging task, then completed mini-blocks containing 5 length comparison trials and 1 averaging trial, with feedback on their performance on the averaging task (i.e. “You overestimated/underestimated the average length”). They were required to obtain an estimation error of no more than 30 pixels to advance to the next step. They were also informed that they would have to repeat the mini-blocks at the end of the experiment should their estimation be too off track, even though this was not truly the case, as an incentive to perform the task to the best of their ability. Participants then received instructions for the base-rate manipulation. To ensure that they understood these instructions properly, they were asked to identify correctly whether the given base-rate manipulation would yield more long lines or more short lines (shown on the screen in a similar layout to the ‘Bias’ boxes in Figure 2). This was done for each bias direction alternatively until they obtained 4 correct responses. Finally, they were reminded of the discounting procedure and the bonus payment they could receive. Apart from the fixation cross, most of the stimuli and tasks of this experiment were self-paced. If the participants were too slow to respond to the trials (more than 2 seconds per trial), the researchers instructed them to keep a certain speed and rhythm while answering, and that each trial shouldn’t last longer than 1 second.
Staircase procedure Using a staircase procedure, we titrated the length deviation of the target
line to achieve a 75% of accuracy. The initial value of the deviation was 20 pixels. This value was updated trial-by-trial using a weighted up-down method (Kaernbach, 1991). The step size was 2 pixels and the up/down update was 2/1 pixels. There was a minimal value correction so
the titrated value could not go lower than 2 pixels. Participants completed 25 reversals but only the last 20 reversal values were used to calculate the final threshold value.
Line length distribution For each experiment, a normally-shaped distribution of target lines
was drawn using the titrated deviation value mentioned above. The value could not be less than 3 pixels so no target value could have the same length as the reference line. First an integer-only distribution around zero ranged between -2 and 2 was drawn. The distribution had 300 observations for each bias direction of the base-rate manipulation. The distribution was composed by 38.67% of 0 values, 42.66% of -1 and 1 values, and 18.66% of -2 and 2 values. Then the reference line length values were added to each value of the distribution. To create the shorter- and longer-than-the-reference distributions the titrated deviation value was subtracted and added to each value of the distribution respectively. This means that the final distribution for the experiment had 600 observations for the base-rate manipulation. This distribution was first divided between short and long bias direction, which were used for half of the experiment respectively. The distribution was presented in its entirety during the experiment.
Procedure In each mini-block, after seeing the reference line along with the base rate
information, participants encountered 5 trials with the length comparison task then 1 trial with the average length estimation task. Between each trial, a fixation cross was presented for 500ms. The experiment consisted of 3 blocks of 40 mini-blocks. Every 10 mini-blocks, participants received feedback on their performance and were offered to take a short break, resuming the experiment by pressing the spacebar. Between each block, participants were required to take a break by exiting the cubicle for at least 3 minutes. This is illustrated in Figure 3. Thus, participants performed a total of 600 trials of the length comparison task and 120 trials of the average length estimation task, excluding trials performed during the instruction period. Participants could obtain up to 5 euros of extra payment for this experiment. On each length comparison trial, 5 cents would be discounted from that sum for each incorrect response. This was done in order to keep the participants engaged and motivated to fulfill the task, since pilot data showed that discounting rather than rewarding participants produced a larger bias effect, which is also in line with the finding that punishment motivates people more than rewards (Kahneman and Tversky, 1977). At the end of the experiment, participants would be awarded the remainder of that sum, rounded up to the highest (e.g. if a discount of 2.65€ was applied by the end of the experiment, participants would be rewarded 3 euros of extra payment). Participants in Experiment 1 were rewarded, on average, 10,53€ (or equivalent in research credits).
Figure 3. Experiment 1, Task layout. In each mini-block, participants completed 5 length
comparison trials then 1 averaging trial. Feedback on their performance (correct responses, mistakes, and monetary discount) was shown every 10 mini-blocks.
Statistical models for data analysis
We hypothesized 4 models for each task to explain the interactions of the bias directions (shown in Figure 4).
Figure 4: Statistical models. These models were established prior to collecting data for the
experiment. The first model reflects the (expected) scenario in which the bias direction long would bias participants responses towards reporting more longer lines and the bias direction short towards shorter lines. The second model reflects the reversed (unexpected) scenario. The third model is the unconstrained model, and the fourth one is the null model.
Let mu1 be the average value in the bias direction long and mu2 the average value for bias direction short. These values are specific to each task - in the length comparison task it corresponds to the criterion value, and in the average estimation/reproduction task it corresponds to the estimation/reproduction error. The models were also tested on the sensitivity data, where mu1 and mu2 correspond to d’ values of each bias direction respectively.
Model A: mu1 > mu2
This model captures the case where the criterion values in the base-rate long condition are bigger than those in the base-rate short condition. This means that participants responses were biased in the ‘correct’ or expected direction. This model is a measure to ensure that the base-rate manipulation is functioning properly. In the length comparison task, in represents H1, which is expected. In the averaging/reproduction task, however, it represents H1A, which is unexpected.
Model B: mu2 > mu1
This is the reverse model, where the base-rate manipulation would have the opposite effect as expected, and the criterion values would be bigger in the rate short condition than in the base-rate long condition. This model is unlikely to be the preferred one, and figures in none of our hypotheses.
Model C: mu1 ≠ mu2
This model is the most general and captures any relationship between the two conditions, regardless of bias direction. We are including this model in order to have a reference point to compare the other models to. This model is preferred to any of the more constrained models if none of the aforementioned theories are good enough at predicting the data. (Haaf et al., 2018)
Model 0: mu1 = mu2
This model captures whether there is no effect from the manipulations. In the averaging/reproduction task, it represents H0. For the sensitivity data, it represents H0B. H1B (sensitivity data) could therefore be represented by either of the more constrained models (MA, MB, or MC).
Results
Sensitivity
As stated in the introduction, we knew prior to the experiment that sensitivity data (obtained from the length comparison task) should stay the same between both conditions. Furthermore, we hypothesized that the base-rate manipulation should not affect sensitivity, which is represented by d’ in SDT. Therefore, to confirm that the bias manipulation yielded no effects on d’, we tested the sensitivity data with our model comparison by comparing the Unconstrained model (MC) to the Null model (M0), expecting M0 to be preferred. For d’ values, M0 is preferred over MC by a factor of 7.69 to 1. The change in sensitivity between conditions per participant is shown in Figure 5.
Figure 5: Experiment 1, Sensitivity results. Each participant’s sensitivity is represented by a dot,
colored by condition. The lines represent the shift in each participant's sensitivity between conditions. The central, larger dots represent the mean sensitivity per condition. The bars represent standard deviation.
Length comparison task
We wanted to know if participants’ responses in the length comparison would be biased by the base-rate manipulation, which was what we expected. To do so, we first tested whether there was an effect of the bias manipulation as a whole by comparing MC to M0. MC is preferred over M0 by a Bayes factor of 21.5 to 1. Then, we wanted to know whether each bias direction would bias the participants’ responses in the expected direction. We were expecting the base-rate long condition to bias participants into responding more long lines, and conversely for the base-rate short condition, into responding more short lines. As we expected, the bias (or criterion) was superior to 0 in the base-rate long condition (0.376), and inferior to 0 in the base-rate short condition (-0.244; Figure 6). Because MC had performed
better than M0, we then tested MC against the more constrained models (MA and MB), MA representing the correct (expected) bias direction and MB the reversed (unexpected) one. MA is preferred over MC by a factor of 2 to 1. MC is preferred to MB by a factor of 1111 to 1. Therefore, MA is the most preferred model, and MB the least preferred model.
Average estimation task
We expected the base-rate manipulation to have no effect on this task, since the manipulation should affect response and not perception and we used the average estimation task as a proxy for perception. Similarly to the length comparison task, we first tested if the bias manipulation would yield an effect as a whole by comparing the MC to M0. M0 is preferred over MC by a factor of 6.25 to 1, which is what we expected. Because we expected there to be no effect of the bias manipulation as a whole, we also expected that there to be no specific effects for bias direction. We compared MC to the more constrained models. MB is preferred over MC by a factor of 1.31 to 1, MC over MA by a factor of 1.47 to 1, and MB over MA by a factor of 1.92 to 1. Therefore, M0 is the most preferred model and MA the least preferred model. We had expected M0 to be the most preferred model.
Figure 6: Experiment 1, Bias and average estimation error results. On the left panel, each
participant’s criterion is represented by a dot, colored by condition. The lines represent the shift in each participant's criterion between conditions. The central, larger dots represent the mean criterion per condition. The bars represent standard deviation. On the right panel, the same is represented for the estimation error.
Discussion
Our results indicate that the length comparison task provided strong evidence for H1. However, we found only anecdotal evidence for the expected bias direction. Nonetheless, the evidence for the ‘correct’ bias direction over the Unconstrained model was superior to that of ‘reversed’ bias direction over the Unconstrained model, which suggests that the data we gathered points towards ‘correct’ bias direction, as expected. We suspect that with stronger statistical power, our model comparison would reveal stronger effects. In the average estimation task, we found moderate evidence for H0. Because the null model was the best explanation for our data, we suspect that given more data and statistical power, the null model would yield stronger evidence for H0. Furthermore, because the null model is preferred over the unconstrained model, it is de facto also preferred over the more constrained models, A and B. Using the sensitivity data from the length comparison task, we found moderate evidence for H0B. We expected the evidence for this model to be stronger, as the effect was predicted to be on the criterion, and participant’s sensitivity was expected to stay the same between conditions. This could be due to a lack of statistical power or to an absence of effect. Nonetheless, the model comparison points towards the direction of our hypothesis. We suspect that given more data on the length comparison task, there would be stronger evidence for H0B.
The main limitation proper to this study was a potential carryover effect from the length comparison task to the averaging task, which had already been noticed in Sanchez-Fuenzalida’s previous experiment (see Introduction). Because the tasks were juxtaposed by design in each mini-block, if there were to be a bias effect whilst judging the 5 lines for the length comparison task, then there could also be a bias whilst judging the average of those lines. For example, if a participant were to report 4 out of the 5 lines as being longer than the reference, once the averaging question was prompted, they might have thought that therefore their average should be longer as well (Ferris et al., 2001). It has also been demonstrated that participants may show a “tendency for estimates of individual stimuli to be biased toward the central value of the presented set of stimuli” (Crawford et al., 2000), suggesting that the central value of 5 biased lines would be reflected in the estimation of a single average line. To address this, we attempted to dissociate the tasks in Experiment 2 by making the perceptual task (reproduction task) independent from the discrimination task. Overall, the data from this experiment gives us moderate evidence for our main hypothesis (H1+H0+H0B).
Experiment 2
Methods
Participants Fourteen naive undergraduate or graduate students (M= 21, SD = 1.95, 7 females)
from the University of Amsterdam participated in this experiment. They all had normal or normal to corrected vision, and a level of English sufficient to read and understand the instructions. They gave written informed consent prior to participating in the study, which was approved by the university's ethics committee. The experiment lasted on average 29.5 minutes (SD = 5.5), excluding the instruction period and the breaks. Participants were rewarded 10€ or 1 research credits for completing the experiment. Additionally, up to 5€ (or 0.5 research credits) could be earned based on performance (see Procedure).
Apparatus Identical to Experiment 1.
Experimental design
Independent variables Identical to Experiment 1. Dependent variables
Length comparison sensitivity: Identical to Experiment 1 Length comparison bias: Identical to Experiment 1
Reproduction error: From participants’ responses in the reproduction task, we calculate their mean deviation from the actual length of the presented line. This was done for each reproduction trial using the following formula:
Reproduction error = Target line - Reproduction estimation
These measures were then averaged per subject and per condition.
Tasks
Length comparison task Identical to Experiment 1.
Reproduction task Participants had to estimate the exact length of the single previous target
line presented to them by reproducing it, moving the mouse upwards or downwards until they confirmed their estimation by pressing the middle mouse button.
Stimuli were presented for 500ms, then one of the two questions would appear. Responses were self-paced in both tasks.
General procedure
Instructions Aside from the target line disappearing before the response option was
prompted, the instruction period was identical to Experiment 1 up until the staircase procedure. Then, participants were presented with the reproduction task, including instructions for the task and feedback on their performance (i.e. “You overestimated/underestimated the line length”). Participants completed 2 mini-blocks of this task alone, and no minimal error margin was instantiated. Then, participants underwent 2 mini-blocks of 5 trials each where a total of 5 length comparison and 5 reproduction trials were intermixed randomly, without any instructions or feedback. These mini-blocks were therefore similar to the ones shown during the experiment. The participants went through the same instructions for the base-rate manipulation and payment instructions as in Experiment 1. They were also asked to speed up if the researchers noticed that their pace was too slow. To reiterate, in the intermixed instruction mini-block as in the experiment, stimuli were presented for 500ms, and only after they had disappeared would one of the two questions would appear.
Staircase procedure Identical to Experiment 1.
Line length distribution The target line length distribution was obtained similarly as in
Experiment 1, except that the distribution for each bias direction contained 150 observations. Thus, the distribution for the base-rate manipulation contained 300 trials and was then doubled to be presented entirely for each task. Thus, the distribution was presented in its entirety twice for each experiment.
Procedure In Experiment 2, the average length estimation task was replaced with the
reproduction task. Participants were told to reproduce the length of the (single) target line just presented to them, rather than average the 5 previous lines. In addition, the length comparison task and the reproduction task were presented randomly throughout each mini-block, following a 50% distribution over the entire block. Thus, participants could not rely on the knowledge of task layout to know which trial would come next. On each trial, task information was prompted only once the target stimuli had disappeared. Participants would undergo a total of 5 trials per mini-block, rather than 6. This is illustrated in Figure 7. Thus, participants performed a total of 300 trials for the length comparison task and 300 for the reproduction task, excluding trials performed during the training period. Extra payment conditions were identical to Experiment 1 for the length comparison task. However, participants were discounted on the reproduction task, unlike the averaging task. Based on Sanchez-Fuenzalida’s previous experiment, it was found that an error margin of 35 pixels would produce an average of 75% correct on each feedback screen. Thus, in an attempt to maintain consistent feedback screens between the two experiments, the error margin for a
correct reproduction trail was set to 35 pixels. Participants in Experiment 2 were rewarded, on average, 11,53€ (or equivalent in research credits).
Figure 7: Experiment 2, Task layout. In each mini-block, participants completed a total of 5
trials composed of a combination of length comparison and reproduction trials. Participants would not know which task they had to complete until the target stimuli had already disappeared. Feedback on their performance (correct responses, mistakes, and monetary discount) was shown every 10 mini-blocks.
Statistical models for data analysis
The models described in Experiment 1 were also used in Experiment 2 (see Figure 4). In the reproduction task, mu1 and mu2 correspond to the reproduction errors (rather than average estimation errors) for each bias direction.
Results
Sensitivity
As stated in the introduction, we knew prior to the experiment that sensitivity data (obtained from the length comparison task) should stay the same between both conditions. Furthermore, we hypothesized that the base-rate manipulation should not affect perception, which would be represented by d’ in SDT. Therefore, to confirm that the bias manipulation yielded no effects on d’, we tested the sensitivity data with our model comparison by comparing the Unconstrained model (MC) to the Null model (M0), expecting M0 to be preferred. For d’ values, M0 is preferred over MC by a factor of 6.67 to 1. The change in sensitivity between conditions per participant is shown in Figure 8.
Figure 8: Experiment 2, Sensitivity results. Each participant’s sensitivity is represented by a dot,
colored by condition. The lines represent the shift in each participant's sensitivity between conditions. The central, larger dots represent the mean sensitivity per condition. The bars represent standard deviation.
Length comparison task
We wanted to know if participants’ responses in the length comparison would be biased by the base-rate manipulation, which was what we expected. To do so, we first tested whether there was an effect of the bias manipulation as a whole by comparing the Unconstrained model (MC) to the Null model (M0). MC is preferred over M0 by a Bayes factor of 1.88 to 1. Then, we wanted to know whether each bias direction would bias the participants’ responses in the expected direction. We were expecting the base-rate long condition to bias participants into responding more long lines, and conversely for the base-rate short condition, into responding more short lines. As we expected, the bias (or criterion) was superior to 0 in the
base-rate long condition (0.007), and inferior to 0 in the base-rate short condition (-0.379; Figure 8). Because MC had performed better than M0, we then tested MC against the more constrained models (MA and MB), MA representing the correct (expected) bias direction and MB the reversed (unexpected) one. MA is preferred over MC by a factor of 1.96 to 1. MC is preferred to MB by a factor of 33 to 1. Therefore, MA is the most preferred model, and MB the least preferred model. The change in criterion between conditions per participant is shown in Figure 9 (left panel).
Reproduction task
We expected the base-rate manipulation to have no effect on this task, since the manipulation should affect response and not perception and we used the reproduction task as a proxy for perception. Similarly to the length comparison task, we first tested if the bias manipulation would yield an effect as a whole by comparing the MC to M0. M0 is preferred over MC by a factor of 6.67 to 1, which is what we expected. Because we expected there to be no effect of the bias manipulation as a whole, we also expected there to be no specific effects for bias direction. We compared MC to the more constrained models. MB is preferred over MC by a factor of 1.2 to 1, MC over MA by a factor of 1.28 to 1, and MB over MA by a factor of 1.53 to 1. Therefore, M0 is the most preferred model and MA the least preferred model. We had expected M0 to be the most preferred model. The change in reproduction error between conditions per participant is shown Figure 9 (right panel).
Figure 9: Experiment 2, Bias and reproduction error results. On the left panel, each
participant’s criterion is represented by a dot, colored by condition. The lines represent the shift in each participant's criterion between conditions. The central, larger dots represent the mean criterion per condition. The bars represent standard deviation. On the right panel, the same is represented for the reproduction error.
Discussion
Our results indicate that the length comparison task provided anecdotal evidence for H1. We also found anecdotal evidence in favor of the expected bias direction. We suspect that both of these findings were limited mainly by statistical power. Given more data, we expect stronger evidence for both of these hypotheses. In the reproduction task, we found moderate evidence for H0. Because the null model was the best explanation for our data, we suspect that given more data and statistical power, the null model would yield stronger evidence for H0. Because the null model is preferred to the unconstrained model, it is de facto preferred to the more constrained models, A and B. Using the sensitivity data from the length comparison task, we found moderate evidence for H0B. We expected the evidence for this model to be stronger, as the effect was predicted to be on the criterion, and participant’s sensitivity was expected to stay the same between conditions. This could be due to a lack of statistical power or to an absence of effect. Nonetheless, the model comparison points towards the direction of our main hypothesis. We suspect that given more data on the length comparison task, there would be stronger evidence for H0B.
One major difference in this experiment compared to experiment 1 was that target lines disappeared before subjects were prompted which task to perform. This means that in the length comparison task, participants could no longer rely on current visual input to make their decision – they had to judge a line stored in their memory (the target line), compared to another line they remembered from up to ‘5 lines ago’ (the reference line). This had the effect of making the length comparison task more difficult overall. Rather than seeing the line they had to discriminate, they were required to remember the line to discriminate. In such a scenario, task performance would also depend on visual memory, attention, and working memory, which could add confounds of inter-participant variability of performance, but also of intra-participant variability throughout the task. We suggest that the difficulty of the length comparison task may have contributed to the models yielding lower evidence for H1 and H0B.
General discussion
This series of experiments (including Sanchez-Fuenzalida’s experiment mentioned in the Introduction) are an attempt to verify experimentally the findings of Witt and colleagues (2015). Because they used simulated data, we were compelled to test their findings on real data to solidify them, but also by expanding them to other manipulations than the Müller-Lyer illusion. In their publication, Witt and colleagues assert that SDT cannot distinguish between perceptual and post-perceptual manipulations by using only the criterion, since the same criterion value could represent either a proportional shift of the signal and noise distributions (as a result of perceptual bias in the ‘signal present’ and ‘signal absent’ conditions, e.g. Müller-Lyer) or a shift in the criterion itself (as a result of response bias, e.g. payoff), with no way of differentiating between the two. In their conclusion, they suggest that “potentially effective
techniques include methodological designs that reduce the possibility of decision-based biases, the use of converging measures such as indirect and action-based measures, and the use of neuroimaging techniques”. Although we did not use any neuroimaging techniques in this experiment, the aim of our perceptual task (average estimation/reproduction task) was to provide an indirect, action-based measure that would reduce the possibility of decision-based biases. This was further adjusted in Experiment 2 to reduce the decision bias carried over from the discrimination task.
Nonetheless, the fact that we used a discrimination task was a limitation to this study in and of itself. In line with the findings from Witt and colleagues (2015), it is impossible to distinguish properly on the discrimination task only whether this is a perceptual or post-perceptual bias, as we cannot know for sure whether the measured biases are due to a shift in criterion or to a proportional shift of both distributions – effectively, the base-rate long condition could have shifted both the signal (long lines) and signal + noise (short lines) distributions to the right side of the criterion, or, equally, could have shifted the criterion to the left side of the distributions. We aimed to make this clearer with the perceptual tasks – an action-based, bias-free, indirect measure for perception. The same perceptual task was used in Sanchez-Fuenzalida’s experiment, and in the case of a perceptual manipulation such as the Müller-Lyer illusion, participants’ results on this task would present a bias (towards short or long) as well. Because the perceptual task results here were not biased by the base-rate manipulation, but the discrimination task results were, we can make a soft conclusion - given our moderate evidence - that the base-rate manipulation yields post-perceptual bias effects. Several limitations impede on the strength of this conclusion.
The first limitation, and perhaps the most recurring one, is statistical power. Our data collection was driven to a halt because of environmental circumstances (COVID19 pandemic) that shut down most university infrastructures. Because of this statistical underpowering, we cannot make any firm conclusions with regards to our initial hypotheses. However, it is clear that most patterns of the data are in the direction of our main hypothesis: there is moderate evidence for H1 (strong in Experiment 1, anecdotal in Experiment 2), moderate evidence for H0, and moderate evidence for H0B. As such, with this experimental setup, it seems unlikely that a cognitive manipulation such as the base-rate may affect perception. On the contrary, the base-rate manipulation does seem to have an effect on participants’ response. Another limitation could be whether we were truly measuring perception in the perceptual tasks. What we truly measured was the participants’ capacity to estimate and reproduce the average length of 5 lines, or the length of a single line, as a proxy for perception. This proxy also includes confounds that were present during the entire experiment and varied across participants, such as visual memory or motoric skills (Anii and Kudo, 1997; Renshaw, 1945). For example, if one of the participants had extensive experience with controlling fine mouse movements (e.g. a graphic designer), then their performance on the perceptual task could be superior to that of a participant without such experience. Ergo, rather than measuring what
they perceived, we could have been measuring how accurately they could reproduce what they perceived.
This question of ‘perceptual or post-perceptual’ is increasingly intriguing to researchers. To disentangle them, many researchers have used DDMs, as mentioned in the introduction. This framework seems promising. Although White and Poldrack implicitly assume a relationship between response bias and starting point on one hand, and stimulus bias and drift rate on the other (see Introduction; White and Poldrack, 2014), Mulder and colleagues (2012) show empirically that different types of choice bias are associated to changes in starting point. In their study, they examined the underlying neural networks of choice bias by comparing a payoff manipulation and a prior probability manipulation using 3T fMRI and a random dot motion task. Both manipulations resulted in a change in starting point in the DDM, and in no significant change of drift rate. However, this framework seems limited since the parameters of the DDM do not necessarily capture perceptual or post-perceptual processes per se. Although White and Poldrack implicitly assume that they do, Mulder and colleagues (2012) are more cautious in their interpretation. The authors simply conclude by establishing a common neural circuit for different types of prior knowledge (choice bias), with no explicit mention to differentiating perceptual and post-perceptual biases. On one hand they demonstrate that different choice bias result in a change in starting point, but on the other hand, they provide no evidence that perceptual biases affect the drift rate of the model. Yet, another study demonstrates that payoff manipulations affect the drift rate of the model when rewards are vicarious (i.e. to a friend or relative) rather than to the observer themselves (Bottemanne and Dreher, 2019). Thus, by attempting to attribute changes in drift rate and starting point to perceptual and post-perceptual processes respectively, one may run the risk of falling into the same binary and dichotomous trap that has mislead many SDT researchers over the years. Instead, the DDM offers a more comprehensive approach than SDT by incorporating other parameters, namely, reaction time. The parameter of reaction time per trial can further be decomposed into reaction time per correct, incorrect, congruent, and incongruent trial, yielding qualitatively richer information than the 4-option confusion matrix used in SDT which does not incorporate reaction time. For example, Dekel and Savi show, in a multi-center, multi-experiment study (Dekel and Sagi, 2020), that perceptual biases (such as tilt aftereffect and tilt illusion, using Gabor patches) decrease as reaction time increases. However, they do not make any clear distinctions with regards to perceptual and post-perceptual biases strictly speaking: in their study, the context-dependent biases listed above are “clearly at least partially perceptual” (Dekel and Sagi, 2020), but prior-dependent biases, such as the base-rate manipulation, are admittedly more complicated to categorize, since they may idiosyncratically yield both sensory and decision biases (Linares et al., 2019). Nevertheless, Dekel and Savi showed that both context- and prior-dependent biases either reduced or disappeared with longer reaction times. Together, these studies demonstrate to us that a more intricate analysis of DDM parameters may shed some light with regards to understanding the effects (and perhaps the nature) of a bias manipulation. It seems idealistic,
however, to think that either type of bias manipulation, be it perceptual or post-perceptual, may be mapped directly onto the parameters of drift rate and starting point respectively and separately.
A potential next step to test our perceptual task based framework would be by using a detection task rather than a discrimination task. Witt and colleagues (2015) mention that perceptual biases will necessarily reflect themselves in the sensitivity to discriminate whether the signal is present or not (d’) if and only if the experimental setup presents trials that consist of a signal that is strictly present or strictly absent – ergo, where absent trials mean than no stimulus was shown at all, unlike in this experiment where an ‘absent’ trial was one where a short line was presented. This entails that any change in c will be the result of a change in the internal criterion. One could then apply a bias manipulation to such a detection task as well as to a perceptual, action-based task, in order to disentangle whether the investigated bias manipulation was perceptual or post-perceptual. By incorporating neuroimaging techniques and DDMs as in Mulder and colleagues’ study, one could maximize the information yielded by the experiment and thus better understand the effects and nature of the investigated bias.
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