Implicit boundaries are remembered better than non-boundaries in statistical learning
Abstract
Changes in temporal context have been shown to impact episodic memory of the ‘boundary’ items involved in creating this temporal context. However, in most prior studies, changes in temporal context have been operationalized explicitly, typically through perceptually obvious visual or auditory stimuli that form a boundary between the previous and current context. In this work, we explore how recognition of items is impacted when temporal context change is operationalized implicitly through the order of presentation during the study phase. 57 participants, were exposed to a rotation judgment cover task for 15 randomly generated polygon items. Around half of the participants were presented with these items in a random order. The other half were presented with items such that 6 items formed ‘boundaries’ that led in and out of 3 temporal clusters. Similar to findings where boundaries are explicitly operationalized, we show that implicit boundaries are also better remembered than non-boundary items.
Introduction
We receive a continuous stream of sensory information in our daily lives. In order to make sense of it, we often parse it into meaningful chunks for storage, retrieval, and comprehension. For example, we may recall our drive to work as a series of discrete events: getting into the car, getting coffee, picking up a carpool colleague, hitting traffic on a particular street, parking, and walking over to the office. What aspects of the incoming stream help us organize continuous temporal information in discrete chunks? Cognitive psychologists have studied temporal chunking under several domains from event boundaries (Clewett et al. 2019; Zacks and Swallow 2007; Rouhani et al. 2020, 2018; DuBrow and Davachi 2013; Baldwin et al. 2008), language learning, (Romberg and Saffran 2010; Knowlton et al. 1992), categorization (Unger and Sloutsky 2022; Gabay et al. 2015), and motor sequencing (Bera et al. 2021; Tremblay et al. 2010; Savalia et al. 2016; Ostlund et al. 2009). Chunking a repeated sequence of experiences is crucial to abstracting patterns in the environment and forming habits for quick and efficient interactions with the environment (Dezfouli and Balleine 2012; Smith and Graybiel 2016; Dolan and Dayan 2013; Dezfouli et al. 2014; Gershman and Niv 2010; Botvinick 2012).
Event boundaries are traditionally demarcated by changes in the ongoing context, where context is often operationalized, explicitly by visual or semantic properties of the stimuli. Event segmentation models suggest that these boundary points serve a unique purpose in parsing the continuous stream of information that we receive. In particular, event boundaries contribute to both the segmentation of the continuous stream and the integration of information within these boundaries. These event boundaries are, for example, shown to be remembered better (Swallow et al. 2009; Rouhani et al. 2018, 2018; Zacks 2020; Radvansky and Zacks 2017; Heusser et al. 2018), serve as points of retrieval (Michelmann et al. 2023) and points of replay to promote long term memory (Hahamy et al. 2023; Sols et al. 2017) and easy parsing, help integrate memory across time (Clewett et al. 2019), and separate across boundary events while collapsing within boundary events (Clewett et al. 2019; Lositsky et al. 2016; Ezzyat and Davachi 2014; Brunec et al. 2018).
In most prior studies, event boundaries have been studied using explicit, typically visual context shifts. For example, Heusser et al. (2018) showed participants a stream of images surrounded by colored borders that visually operationalized context. Event boundaries were therefore operationalized by changing the color of the surrounding border after a few trials. Event boundaries as a function of explicit context change have also been operationalized by changing the associated stimulus (Ezzyat and Davachi 2014) – participants were presented with a pair of images on each trial, with the ‘scene’ image in the pair remaining constant for a short sequence of trials, creating a context, amid trial-unique the target images (‘object’ or ‘face’). As participants made judgments about the target image category, the associated scene occasionally changed, thus creating an event boundary (Ezzyat and Davachi 2014). In these and other previous studies on event boundaries, context changes were operationalized as perceptual or semantic shifts in ongoing sets of events that were visually presented to participants (Swallow et al. 2009; Baldassano et al. 2017). In more recent work, context change has also been operationalized as changes in ongoing reward contingencies associated with each stimulus (Rouhani et al. 2020).
Consistent findings across most studies in explicitly operationalized event boundaries, events or stimuli in an experimental paradigm that signal a shift in the ongoing context, show that event boundaries are often remembered better (Swallow et al. 2009; Radvansky and Zacks 2017; Heusser et al. 2018; Clewett et al. 2019; Rouhani et al. 2020; Ezzyat and Davachi 2014; Baldassano et al. 2017). Furthermore, events separated by explicit boundaries are perceived to be farther apart than events within boundaries, implying that events across boundaries are represented to be more distinct than events within boundaries (Clewett et al. 2019; Ezzyat and Davachi 2014; Brunec et al. 2018; Lositsky et al. 2016).
Recent work has shown that event boundaries can also be formed without explicit, perceptual changes in context. Schapiro et al. (2013) showed participants a series of meaningless shapes. Unknown to the participants, the stream followed a modular graph structure (see Figure 1) where each shape was associated with a node of the graph and connections represented an equal probability of transitioning between nodes. After being exposed to the stimulus stream generated by such a random walk through the modular graph, participants were asked to hit a key when they felt there was a natural break in the stream. Participants pressed the key when they experienced the stream transition between clusters more frequently than when they experienced the stream between nodes within clusters. This finding has been linked to statistical learning of temporal graph structures and the effect of event boundaries is often measured by slowed reaction times when responding to a stimulus after experiencing a transition across-clusters than within-clusters in both visual and motor domains (Karuza 2022; Karuza et al. 2019; Kahn et al. 2018, 2018; Lynn, Kahn, et al. 2020; Lynn, Papadopoulos, et al. 2020; Lynn and Bassett 2020).
Crucially, in these studies, unlike most explicit boundary experiment designs, there are no systematic perceptual differences between the stimuli associated with the boundary nodes and those associated with non-boundary nodes (See Figure 1, for example). Boundaries are instead operationalized solely as a function of the temporal order in which these stimuli are presented. These implicitly operationalized boundaries (boundaries not marked by change in perceptual context) have been labeled as ‘event boundaries’, suggesting that implicit boundaries share representational properties with explicitly operationalized boundaries typically studied in the event boundary literature (Schapiro et al. 2013). However, past studies on implicit event boundaries have not assessed the memory representations of these boundaries using the same tests used in explicitly operationalized boundary paradigms, instead relying on observations from reaction times or the rate at which boundaries are detected as ‘natural breaks’ in a post-exposure parsing task (Schapiro et al. 2013). Testing whether the two types of event boundaries share effects on memory will thus provide direct evidence for a common mechanism underlying boundary formation and provide a unifying framework to study event cognition.
In this work, we test implicitly operationalized boundaries to assess whether they elicit the same behavioral properties as explicitly operationalized boundaries. In particular, we exposed participants to randomly generated meaningless polygon stimuli such that the trial order was structured by the graph structure previously used in (Schapiro et al. 2013) in contrast to a random, unstructured trial order. We then tested whether participants exposed to structured trial order recognized boundary items better (or worse) than non-boundary items. To preview our results, implicit boundary events are indeed recognized better than non-boundary events, providing support for a shared representation with explicitly operationalized boundaries.
Method
Participants
63 undergraduate students at the University of Massachusetts Amherst participated in this study. Participants were at least 18 years of age and were compensated via course credit. All study procedures were approved by the University Institutional Review Board, and all participants provided their informed consent for participating in this research study. Data from 6 participants who did not complete the study were discarded from further analyses. The participant sample size was not pre-determined via a statistical procedure but was equivalent to that of similar previous studies (Heusser et al. 2018).
Stimuli
Random closed polygons were generated to be used as stimuli for this experiment by connecting 6 vertex locations. The vertices of the polygons were pseudorandomly generated as follows: Cartesian coordinates of two vertices were drawn from a normal distribution centered around 0 with a standard deviation of 0.1 inches. The coordinates of the remaining four vertices were drawn from uniform distributions between 0.1 and 0.3 inches (i.e., the other 4 coordinates were at least 0.1 inches and at most 0.3 inches away from the center). A total of 300 polygons were generated, and 60 (15 were ‘old’ (studied) and 45 were ‘new’ (unstudied)) were randomly chosen from this set of 300 and used for each participant (See Figure 1 for examples). All presented stimuli were set to occupy 17.5% of the height of the visual display.
Design and Procedures
Participants were randomly assigned to either a structured graph exposure or an unstructured graph exposure group. The overall experimental procedures were the same across both groups.
The experiment consisted of 3 phases: study, exposure, and test. The study phase was shown once at the beginning of the study. The exposure and test phases were interleaved and repeated three times. Each exposure phase consisted of 250 trials, and each test phase consisted of 30 trials.
From the set of 60 stimuli chosen for each participant, 15 were randomly chosen as ‘old’ stimuli to be studied during the study and exposure phases. The remaining 45 were set to be used as ‘new’ items across the 3 recognition memory test phases described below (15 per test). The study phase was always at the beginning of the experiment, where participants were shown all 15 polygons in a 3x5 grid (See Figure 1). They were asked to carefully examine these polygons and to remember their orientation, as they would be tested on polygon orientations in the next phase of the experiment. After 4 seconds of the study phase, participants were presented an option to move to the next phase once they were ready – thus ensuring they viewed all 15 items for a minimum of 4 seconds. The study phase was followed by interleaved exposure and test phases phase for 3 blocks (See Figure 1). For each block of 250 exposure trials, participants were presented with one of these 15 polygons at a time and asked to judge whether the presented polygon was in its original orientation or rotated – the presented orientation was randomly determined to be the canonical orientation shown during the study phase or rotated by \(90^\circ\) clockwise or counterclockwise. Participants were provided feedback on their accuracy on each rotation judgment response, and an on-screen score was maintained in the top right corner to motivate accurate responses. Polygons were surrounded by a (purple, orange, or dark green) colored border to use for a later source memory test. The colored border was randomly assigned to each polygon for the study, with each color assigned to 5 of the 15 exposure polygons.
Each polygon with its border was associated with a node in the graphs shown in Figure 1. The edges of the graphs determine the order in which the polygons were shown to participants during exposure. The trial order was determined by a random walk through these graphs – following each trial (i.e., presentation of a polygon associated with a node), the subsequent trial was determined by a random selection between all connected nodes (hence their associated polygons). For 27 participants in the structured exposure group, the trial order was determined by a random walk through the structured modular graph (Figure 1A) and for 30 participants in the unstructured exposure group, it was determined by a random walk through the unstructured graph (Figure 1B). Magenta nodes in Figure 1A are ‘boundary’ nodes that lead into and out of a cluster, whereas gray nodes are ‘non-boundary’ nodes. Note that the unstructured graph does not have boundary nodes in function, but to maintain the number of nodes assigned as boundaries and non-boundaries consistent across the two conditions for analyses, 6 corresponding nodes in the unstructured graph are labeled ‘boundary’ with 9 others serving as ‘non-boundary’ nodes. Finally, unlike in the structured graph condition, the same polygon could be presented in consecutive trials (as denoted by node recurrent connections).
After each block of the exposure phase, participants went through a recognition memory test (Figure 1). They were shown the 15 ‘old’ items from the exposure phase (in their original orientation) in addition to 15 new random polygon items (chosen from the set of 45 selected for each participant) and were asked to determine whether each of these polygons was old or new. The order of presentation of old and new items was randomized during the recognition memory test. A Stroop task was used prior to the recognition test of the third (final) block to wash out any effects of short-term memory. We avoided using the Stroop task before the recognition tests of the first two blocks to avoid longer, additional task-switching breaks in the continuous exposure sequences hence allowing the participants to develop a representation of the underlying transition structure.
After the final recognition memory test, participants went through a source memory test. Each of the 15 studied items was shown without the colored borders that surrounded them during exposure. Participants were asked to choose which of the three colored borders, provided as on-screen options, surrounded any particular item. This source memory task was added to provide an additional signal for memory in case of ceiling effects of recognition memory tasks. However, no analyses have been done on this source memory task.
Software note.
The experiment was designed using Psychopy (Peirce 2007), and conducted on desktop computers running Windows 7 with a resolution of 1920x1080. All linear models presented in the next section were conducted using the Python package Bambi (Capretto et al. 2022), whereas the Drift diffusion model was fit using the HSSM toolbox (Fengler et al., n.d.). Model comparisons and visualizations were created using Arviz (Kumar et al. 2019) and Seaborn (Waskom 2021).
Results
The overall average accuracy and median response time patterns during the exposure phase, for each participant across node and graph types for the three exposure blocks, are shown in Figure 4 (See Table 1 for complete descriptive statistics). Exposure accuracy is measured by the proportion of trials in which participants correctly recognized the canonical orientation of the polygons. Since participants are given feedback on their rotation judgment during exposure, we expect that this rotation judgment accuracy will increase and reaction times will decrease over trials.
To estimate the learning effects, we fit a Bayesian hierarchical mixed effects logistic regression model for rotation judgment accuracy and a hierarchical mixed effects linear regression model to estimate the rotation judgment log reaction times. The models included main effects of node type (boundary vs non-boundary), graph-type (structured vs unstructured), and (log) trial number along with 2- and 3-way interactions between all factors and a varying participant intercept. As expected, rotation judgment accuracy increased (log trials \(\beta = 0.13\), \(95\%\), HDI [0.08, 0.17]) and log response times decreased (log trials \(\beta = -0.21\), \(95\%\), HDI [-0.22, -0.19]) with exposure. While we find no reliable main effects of graph type on response times or accuracy, we observe mixed effects of node type on both response times and accuracy measures, along with interactions with other factors (such as graph type) in our models. (See Tables 2 and 3 for complete model statistics).
If participants accurately recognize the orientation of exposure items, they are also likely to recognize these items better at test, regardless of their role in the underlying graph structure. Thus, differences in exposure accuracy may impact our key measure of interest. i.e., recognition accuracy. To account for possible differences in encoding at exposure, we include exposure accuracy as a covariate in our analysis of recognition memory below.
Diffusion Modeling
The overall recognition accuracy and response time data separated by the test stimuli types (new, boundary, and non-boundary) are shown in Figure 7.
To assess the recognition memory differences between the boundary and non-boundary items and leverage variability in response times, we use the Drift Diffusion Model (DDM, Figure 8) commonly used in choice tasks. The DDM, which falls under a class of sequential sampling models, has been a widely successful model in modeling two-choice tasks in recognition memory (Ratcliff et al. 2004, 2022; Starns 2014; Starns and Ratcliff 2014; Ratcliff and Starns 2009).
Briefly, the DDM assumes that at the time of choice, evidence from the presented test item accumulates sequentially over time towards one of the two boundaries. For a previously studied item presented at test, the evidence tends to accumulate noisily towards the ‘old’ boundary whereas for a non-studied item, the evidence accumulates towards the ‘new’ boundary. The rate of evidence accumulation is controlled by the drift rate parameter, \(v\). A more positive \(v\) would imply more likely evidence accumulation towards the old boundary, whereas a more negative \(v\) implies more likely evidence accumulation towards the new boundary. Participants may be biased towards making an old or a new response at test; this bias is measured by the starting point parameter, \(z\). The boundary separation parameter \(a\) determines how the amount of evidence that needs to be accumulated to make a decision – a larger \(a\) implying a difficult task or cautious responses. Finally, the observed response consists of cognitive processes not affiliated with decision-making (such as time for the motor systems to click the relevant key once a decision has been made) which are modeled by a non-decision time parameter \(t_{er}\).
Prior work has shown that the memory strength of previously studied items impacts the drift rate towards old/new responses (Ratcliff et al. 2004, 2022). A higher positive drift rate parameter implies a stronger match to items in memory which leads to a quicker accumulation of evidence towards the ‘old’ response boundary. Similarly, a stronger mismatch to memory (as measured by the higher negative drift rate parameter) implies a quicker accumulation of evidence towards the ‘new’ response boundary (Ratcliff et al. 2004, 2022).
If implicitly operationalized event boundaries in this study indeed share representations with explicitly operationalized event boundaries, the memory strength of the boundary node items should be enhanced relative to those non-boundary node items for participants exposed to a random walk through the structured graph. No such difference is expected for participants exposed to a random walk in an unstructured graph, since there are no functional boundary nodes.
The drift rate parameter of the DDM has been associated with memory strength (Starns 2014). The drift rate should thus be higher for boundary nodes for structured random walk participants than for non-boundary nodes. This difference in boundary vs non-boundary item drift rates should be relatively higher for participants exposed to a random walk in the structured graph than for the participants in our control condition. On the other hand, for participants exposed to a random walk in the unstructured graph, the drift rates between items assigned boundary and non-boundary labels should be equivalent.
To test this hypothesis, we parameterized the DDM for the recognition tasks in our study as follows: \[\begin{aligned} v \sim 0 + exposure\ accuracy + node\ type + (node\ type|participant)\\ z \sim block + (1|participant) \\ a \sim block + (1|participant) \\ t_{er} \sim (1|participant) \end{aligned}\]
We allow the drift rate parameter, v to vary for each node type (note that for recognition tests, node types are labeled ‘boundary’, ‘non-boundary’, and ‘new’) with accuracy at exposure as a covariate. For old items, the accuracy at exposure was the proportion of trials participants correctly recognized the true orientation in the exposure block immediately before the current test block. For new items, accuracy at exposure was fixed at the average accuracy across all old items – thus assuming that the stronger encoding of an old item improves recognition of a new item. We further assumed that over time, as participants get more familiar with the old items through repeated exposure, the amount of evidence required for them to choose an old/new response at test will be lower. We thus allowed the boundary parameter to change per block 1. We also allowed the choice-bias parameter, z, to change over blocks to account for changing biases during the experiment. Finally, the non-decision time parameter was allowed to vary for each participant to account for individual differences in non-decision processes. The noise coefficient (scaling parameter) used for our modeling work is set to 1. We also compared the models including node type to models without node type as a factor affecting drift rate for both structured and unstructured participants, along with including/excluding block effects in all parameters and present the model that best fit our data (See Tables 6 and 7 for comparison results and Figures 12 and 13 for posterior predictive distributions from the winning model to visualize model fits).
DDM Results
The modeling framework above incorporates response time distributions during recognition memory tasks. In particular, if an item is quickly and accurately recognized as old or new, in addition to good accuracy, such recognition would result in faster reaction times. This effect is captured by the drift rate parameter of the DDM.
We tested whether boundary nodes have a higher drift rate than non-boundary nodes (operationalized implicitly as a function of the structured-graph-based trial order during exposure) by subtracting the posterior samples of the drift rate parameter for stimuli associated with non-boundary nodes from those associated with boundary nodes for both unstructured (control) and structured (experimental) graph types (Figure 9). We find that 95.6% of the posterior parameter difference between non-boundary and boundary node stimuli in the structured condition was above 0 (\(M = 0.15, 95\%\ HDI:[-0.035, 0.287]\)2. In comparison, 49.6% of this difference distribution was above 0 for the unstructured condition (\(M = 0, 95\%\ HDI: [-0.16, 0.17]\)) 3.
We estimate the effect of interactions between node-type-dependent drift rate differences and conditions by subtracting the posterior difference estimates. While this difference of differences is not reliably above 0 (\(M = 0.147, 95\%HDI\ [-.084, .384]\)) the interaction effect strongly trends towards statistical reliability with \(88.8\%\) of posterior difference of differences samples above 0. Note that while we label 6 nodes in the unstructured graph as ‘boundary’ nodes, functionally, these are no different from non-boundary nodes, as each stimulus is randomly assigned to each node and each node is in turn connected to every other node of the graph. Results presented in Figure 5 come from a single random assignment of these nodes as boundary or non-boundary.
See Table 4 and 5 for full parameter statistics of the DDM for structured and unstructured conditions respectively. Interestingly, in both unstructured (M(a block 1) = -0.17, 95%HDI [-0.21, -0.13], M(a block 2) = -0.24, 95%HDI [-0.29, -0.2]) and structured (M(a block 1) = -0.18, 95%HDI [-0.23, -0.13], M(a block 2) = -0.19, 95%HDI [-0.23, -0.14]) graph conditions, the boundary parameter a is reliably lower in blocks 2 and 3 relative to block 1 implying that participants do seem to require less evidence in the later blocks to make their old or new decision. The bias parameter is lower for blocks 2 and 3 relative to block 1 in the unstructured graph condition (M(z block 1) = -0.05, 95%HDI [-0.07, -0.02], M(z block 2) = -0.03, 95%HDI [-0.06, -0.01]) but mixed in the structured graph condition (M(z block 1) = -0.03, 95%HDI [-0.06, -0.01], M(z block 2) = -0.01, 95%HDI [-0.03, 0.02]) implying that participants may alter their bias towards new responses in subsequent memory tests albeit, these bias effects, if they exist, are very small. Finally, new item recognition appears to be faster in the unstructured condition (M = -1.19, 95%HDI [-1.5, -0.89]) than in the structured condition (M = -0.84, 95%HDI [-1.18, -0.52]).
The diffusion modeling results thus provide evidence that items that serve as implicit, temporally defined, boundary events are remembered better than items that serve as non-boundary events. Our control condition which accounts for the number of items serving as boundary vs non-boundary nodes but does not assign a functional event boundary role do not show this difference. These findings thus suggest a shared memory representation between implicit and explicit event boundaries.
Converging evidence for better implicit boundary memory using alternative metrics
We test our hypothesis using two additional metrics to evaluate the reliability of findings using the DDM model. First, we use the Balance Integration Score (BIS) as proposed in Liesefeld et al. (2015) to test whether boundary nodes in structured graph conditions are better remembered while accounting for speed-accuracy trade-offs and providing for equal weighting of response times and accuracy measures (Liesefeld and Janczyk 2019). We compute BIS by first z-scoring the proportion correct and response time measures for each participant and node type and then subtracting the standardized response times from the standardized proportion correct measures. Our BIS distribution through this standard calculation was left-skewed, likely due to near-ceiling accuracies. Thus, we power-transformed our BIS scores and fit the following linear mixed effects model separately to structured and unstructured graph conditions:
\[2^{BIS} ~ 0 + node type:block + accuracy\ exposure + (1|participant)\]
In line with our findings using the DDM, as shown in Figure 10, we observe a reliably higher BIS for boundary compared to non-boundary nodes in the structured condition (node type : block M = 0.09, SD = 0.05, 95% HDI [0.01, 0.18]) and not in the unstructured condition (node type : block M = -0.04, SD = 0.04, 95% HDI [-0.12, 0.04]).
It is possible that the effects we observed are due to incidental correlations between graph and node types and between subject variability. To ensure robustness of our estimates, we also perform a bootstrap analysis where we assign ‘boundary’ and ‘non-boundary’ labels to 100 random samples of the 15 nodes for each participant and re-fit our models for both structured and unstructured graph conditions (Figure 11). Specifically, we randomly assigned boundary or non-boundary labels to our stimuli 100 times. We fit the same DDM parametrization to these 100 random assignments and extracted the posterior drift rate estimates for memory responses to these boundary and non-boundary labeled items. We then subtracted these drift posterior estimates for non-boundary stimuli from those of the boundary stimuli (similar to analyses presented in Figure 9). We then computed the mean of these difference distributions to build a bootstrapped empirical null distribution and computed the proportion (out of 100) of both empirical null distributions (from structured and unstructured conditions) that are higher than the mean difference for our true boundary-non-boundary assignment conditions.
As seen in Figure 11, we find that only 6% of structured empirical null distribution samples are higher than the true estimated mean and 13% of unstructured empirical null distribution samples are higher than the true estimated mean, providing further support to our modeling results, indicating that boundary nodes in structured graphs have a higher drift rate during the later recognition test than non-boundary nodes. This analysis suggests that the probability of observing the node type group level effects in our results by chance is relatively small.
Discussion
The primary goal of this work was to test whether findings in the explicitly operationalized event boundary literature replicate when boundaries are operationalized implicitly, through temporal statistics without perceptual context changes. Shared properties between these two operationalizations of event boundaries imply shared representations in memory, thereby providing a framework for future research to study shared algorithmic processes that lead to the formation of event boundaries. In particular, we test whether, similar to findings in the explicitly operationalized event boundary literature (where boundary events are perceptually different from the ongoing stream of events), participants remember implicitly operationalized boundary events (where boundary events are not perceptually different but serve as a gateway to a different cluster defined by temporal co-occurrences). We use the drift-diffusion model on our empirical results to show that boundary nodes are remembered better than non-boundary nodes even when boundaries are not operationalized explicitly.
In this work, we use the DDM to measure differences in memory strength between boundary and non-boundary nodes. DDM is one (highly successful) model of memory that incorporates response time distributions along with choices. Several other sequential sampling models can be similarly used in this formulation to provide evidence of better memory strength for boundary items. Most notably, a direct extension of the Generalized Context model for recognition memory is the Exemplar Based Random Walk (EBRW) model (Nosofsky et al. 2011) which assumes that evidence towards old/new recognition choice options is accumulated in proportion to background activation of all items in memory may be extended to incorporate non-boundary items as background activation with boundary items providing an additional boost in its evidence accumulation process. Recent extensions of the DDM also incorporate reinforcement learning-driven modulation of drift rates which may provide a dynamic characterization of memory processes during learning (Pedersen et al. 2017). Further work is needed to understand how extensions to DDM and other choice reaction time models can be extended to incorporate the effects of temporal order.
The effect of structured exposure on identifying new stimuli is intriguing (Tables 4, and 5). The drift rate posteriors for new items for participants in the unstructured exposure condition are faster (more negative) than for participants in the structured exposure condition. Likely, the interleaved presentation in unstructured exposure generally provides for a richer representation of each exemplar in memory especially in comparison to the non-boundary items in the structured exposure condition, thereby allowing for easier discrimination with new items at test. A similar benefit of interleaved presentation has been observed in categorization tasks (Carvalho and Goldstone 2014, 2017). Nevertheless, future work should aim to explain the cognitive processes that lead to better recognition of new items in the absence of structured learning.
We use the DDM to model participant behavior during the recognition test phase and particularly rely on drift rates to identify the differences in memory of items associated with boundary and non-boundary nodes. The DDM models the psychological process of sequentially sampling evidence towards the ‘old’ or ‘new’ boundary after having viewed the stimulus. The drift rate parameter of the DDM controls the speed at which this evidence is accumulated towards either boundary of the DDM, with a higher drift rate implying greater speed, thus enabling faster recognition for old items along with higher hit rates (Figure S2). In the context of our experiment, the higher drift rate for boundary nodes, relative to non-boundary nodes, implies that boundary items are more readily available in memory and are therefore recognized faster. In particular, even when stimuli are meaningless and non-verbalizable, if they functionally serve as implicit bottlenecks in the ongoing temporal experience, they show properties of typical explicitly operationalized event boundaries. Our findings thus add to prior work indicating the boundary items serve a special role in the structuring of memory and its recall by serving as access points of memory retrievalbott (Michelmann et al. 2023; Heusser et al. 2018; Karuza et al. 2019).
The addition of prior exposure accuracy in our modeling may introduce unwanted effects. For example, prior accuracy may be related to node type. Furthermore, since our items were randomly generated, it is possible that some items were verbalizable, enabling participants to remember them better. It is also possible that the random walk during exposure led to greater exposure to some items than others. Additionally, it is also possible that the randomized presented rotation led to participants spending more time studying some items since they were harder to mentally rotate. Thus, if participants remembered an item better during exposure as a result of any of the above-stated reasons, we expect them to have better recognition memory for those items regardless of their functional role in the temporal graph. Since our goal was to identify whether boundary drift rates were higher beyond the specific visual properties of the studied items and experimental variability, by using exposure accuracy as a covariate, we attempted to account for these effects. Nevertheless, exposure accuracy for each stimulus is a crude metric to account for these effects, and future research could better account for the effects of exposure by explicitly controlling the visual properties of the stimuli.
Our results also show an unexpected but interesting effect – recognition performance (for both old and new items) is generally better for participants in the unstructured graph group than those in the structured graph group. We speculate that the interleaved nature of exposure presented to the unstructured graph participants may have led to a better overall memory of studied polygons. Such an interleaving benefit has been observed in prior work on the spacing effect (Carvalho and Goldstone 2017; Vlach et al. 2008; Wang et al. 2020). Furthermore, it is also possible that the difference in lag between repeated presentation of our stimuli and the randomness of the rotation judgment task has contributed to this difference. The random walk nature through a modular graph necessitates that if a module switch occurs after presentation of a stimulus, repeated presentation of that stimulus would occur with a larger lag in the structured condition. This lag may contribute to relatively lower accuracy exposure, as 10 of 15 stimuli at any given time will be presented at a larger lag in this condition (Figure S5). Furthermore, for stimuli presented at smaller lags (i.e., when the random walk traverses within a module), the randomization of the presented rotation may induce an additional bias leading to lower accuracy at exposure. While we account for potential benefits by including accuracy at exposure as a covariate, future experimental design equalizing recognition performance across exposure types should provide stronger evidence towards node-type advantage due to structured graph exposure.
Our experimental work provides evidence that implicit event boundaries, similar to explicit event boundaries, play a special role in organizing implicit memory. However, it is unclear what temporal order learning-driven algorithmic and neural mechanisms may underlie this benefit. Following the prediction error-based account of boundary formation in event segmentation theory, and the implicit nature of our task, it is likely that an algorithmic mechanism that accounts for the establishment of temporal context such as the Temporal Context Model (Howard et al. 2005; Polyn et al. 2009) or a predictive-representations based Successor Representation (Gershman et al. 2012; Dayan 1993; Momennejad et al. 2017; Gershman 2018) may be used to characterize our findings. Neurally, the complementary learning systems (CLS) theorized to be involved in statistical learning in the hippocampus may provide an indication of where differences in boundary vs non-boundary items are represented in the brain (Schapiro and Turk-Browne 2015; Schapiro et al. 2013, 2017; O’Reilly et al. 2014). Future work should aim to address the underlying algorithmic and neural representations that jointly explain the effects of implicit environmental statistical regularities on memory representations.
Finally, in our experiment, we use a specific graph structure and a random walk through it to investigate possible shared properties of implicit and explicit event boundaries. Future work should aim to generalize this effect by also attempt to identify if altering the properties of various graph topologies can lead to different experimental observations.
Conclusion
Findings of our empirical study presented in this article show that, similar to explicitly operationalized boundaries, implicitly operationalized boundary events are remembered better than non-boundary events. Our work provides an indication that the underlying mechanisms that learn and represent event boundaries may rely not just on perceptual, but also on temporal regularities, thereby leading to structured organization of memory hinged at event boundaries.
Acknowledgements
We would like to thank all RDCL and DMM lab research assistants who helped collect data for this article.
Data Availibility Statement
Code and data used for this manuscript are made openly available in the GitHub repository: https://github.com/tejas-savalia/implicit-boundary-memory.
Funding
No funding was received for work presented in this article.
| accuracy | rt | ||||||
| mean | std | mean | std | ||||
| phase | block | stimulus type | graph type | ||||
| 0 | boundary | structured | 0.683 | 0.465 | 1.644 | 1.911 | |
| unstructured | 0.739 | 0.439 | 1.710 | 1.732 | |||
| 3-8 | non-boundary | structured | 0.669 | 0.471 | 1.619 | 1.728 | |
| unstructured | 0.728 | 0.445 | 1.713 | 1.689 | |||
| 2-8 | 1 | boundary | structured | 0.735 | 0.441 | 1.244 | 1.322 |
| unstructured | 0.796 | 0.403 | 1.283 | 1.243 | |||
| 3-8 | non-boundary | structured | 0.739 | 0.439 | 1.250 | 1.343 | |
| unstructured | 0.790 | 0.408 | 1.263 | 1.217 | |||
| 2-8 | 2 | boundary | structured | 0.757 | 0.429 | 1.168 | 1.657 |
| unstructured | 0.843 | 0.363 | 1.111 | 1.334 | |||
| 3-8 | non-boundary | structured | 0.765 | 0.424 | 1.192 | 1.656 | |
| unstructured | 0.838 | 0.369 | 1.085 | 1.546 | |||
| 1-8 | 0 | boundary | structured | 0.796 | 0.404 | 1.681 | 1.490 |
| unstructured | 0.878 | 0.328 | 1.805 | 1.712 | |||
| 3-8 | new | structured | 0.721 | 0.449 | 1.899 | 1.569 | |
| unstructured | 0.782 | 0.413 | 1.770 | 1.666 | |||
| 3-8 | non-boundary | structured | 0.782 | 0.414 | 1.715 | 1.602 | |
| unstructured | 0.904 | 0.296 | 1.570 | 1.291 | |||
| 2-8 | 1 | boundary | structured | 0.833 | 0.374 | 1.564 | 2.573 |
| unstructured | 0.911 | 0.285 | 1.212 | 0.959 | |||
| 3-8 | new | structured | 0.800 | 0.400 | 1.420 | 1.486 | |
| unstructured | 0.873 | 0.333 | 1.338 | 1.056 | |||
| 3-8 | non-boundary | structured | 0.860 | 0.348 | 1.618 | 1.812 | |
| unstructured | 0.874 | 0.332 | 1.139 | 0.709 | |||
| 2-8 | 2 | boundary | structured | 0.907 | 0.291 | 1.196 | 1.194 |
| unstructured | 0.900 | 0.301 | 1.075 | 0.694 | |||
| 3-8 | new | structured | 0.751 | 0.433 | 1.454 | 2.322 | |
| unstructured | 0.844 | 0.363 | 1.292 | 1.127 | |||
| 3-8 | non-boundary | structured | 0.893 | 0.310 | 1.370 | 1.869 | |
| unstructured | 0.926 | 0.262 | 1.045 | 0.729 | |||
| 1-8 |
| HDI | ||||
| mean | sd | 2.5% | 97.5% | |
| Intercept | 1.13 | 0.11 | 0.91 | 1.31 |
| graph type[unstructured] | 0.05 | 0.15 | -0.24 | 0.33 |
| log trials | -0.21 | 0.01 | -0.22 | -0.19 |
| log trials:graph type[unstructured] | 0.00 | 0.01 | -0.02 | 0.02 |
| log trials:node type[nonboundary] | 0.01 | 0.01 | -0.01 | 0.03 |
| log trials:node type:graph type[nonboundary, unstructured] | -0.02 | 0.01 | -0.05 | 0.00 |
| node type[nonboundary] | -0.06 | 0.05 | -0.16 | 0.05 |
| node type:graph type[nonboundary, unstructured] | 0.12 | 0.07 | -0.02 | 0.25 |
| HDI | ||||
| mean | sd | 2.5% | 97.5% | |
| Intercept | 0.46 | 0.24 | -0.02 | 0.91 |
| graph type[unstructured] | -0.38 | 0.34 | -0.97 | 0.35 |
| graph type:node type[unstructured, nonboundary] | 0.34 | 0.25 | -0.15 | 0.83 |
| log trials | 0.13 | 0.02 | 0.08 | 0.17 |
| log trials:graph type[unstructured] | 0.14 | 0.04 | 0.07 | 0.20 |
| log trials:graph type:node type[unstructured, nonboundary] | -0.06 | 0.04 | -0.15 | 0.02 |
| log trials:node type[nonboundary] | 0.06 | 0.03 | 0.00 | 0.12 |
| node type[nonboundary] | -0.36 | 0.18 | -0.71 | -0.01 |
| HDI | ||||
| mean | sd | 2.5% | 97.5% | |
| z block[1] | -0.03 | 0.01 | -0.06 | -0.01 |
| z block[2] | -0.01 | 0.01 | -0.03 | 0.02 |
| a block[1] | -0.18 | 0.03 | -0.23 | -0.13 |
| a block[2] | -0.19 | 0.02 | -0.23 | -0.14 |
| v accuracy exposure | 0.57 | 0.14 | 0.31 | 0.85 |
| v boundary | 0.63 | 0.12 | 0.42 | 0.88 |
| v new | -0.84 | 0.17 | -1.18 | -0.52 |
| v non-boundary | 0.49 | 0.12 | 0.27 | 0.72 |
| z Intercept | 0.52 | 0.01 | 0.49 | 0.54 |
| a Intercept | 1.20 | 0.04 | 1.11 | 1.28 |
| t Intercept | 0.44 | 0.03 | 0.38 | 0.49 |
| HDI | ||||
| mean | sd | 2.5% | 97.5% | |
| z block[1] | -0.05 | 0.01 | -0.07 | -0.02 |
| z block[2] | -0.03 | 0.01 | -0.06 | -0.01 |
| a block[1] | -0.17 | 0.02 | -0.21 | -0.13 |
| a block[2] | -0.24 | 0.02 | -0.29 | -0.20 |
| v accuracy exposure | 0.51 | 0.14 | 0.25 | 0.80 |
| v boundary | 0.85 | 0.12 | 0.62 | 1.11 |
| v new | -1.19 | 0.16 | -1.50 | -0.89 |
| v non-boundary | 0.85 | 0.13 | 0.61 | 1.10 |
| z Intercept | 0.53 | 0.01 | 0.50 | 0.56 |
| a Intercept | 1.14 | 0.04 | 1.07 | 1.22 |
| t Intercept | 0.48 | 0.02 | 0.44 | 0.52 |
| rank | elpd loo | p loo | weight | |
|---|---|---|---|---|
| v\(\sim\)nodetype, z\(\sim\)block, a\(\sim\)block | 0 | -3322.44 | 178.28 | 0.44 |
| v\(\sim\)nodetype+block, z\(\sim\)block, a\(\sim\)block | 1 | -3323.68 | 183.07 | 0.42 |
| v\(\sim\)nodetype, a\(\sim\)block | 2 | -3325.19 | 177.83 | 0.00 |
| v\(\sim\)nodetype | 3 | -3357.94 | 171.50 | 0.12 |
| a\(\sim\)block | 4 | -3947.96 | 150.93 | 0.02 |
| rank | elpd loo | p loo | weight | |
|---|---|---|---|---|
| v\(\sim\)nodetype, z\(\sim\)block, a\(\sim\)block | 0 | -2810.24 | 157.96 | 0.95 |
| v\(\sim\)nodetype+block, z\(\sim\)block, a\(\sim\)block | 1 | -2811.99 | 159.81 | 0.00 |
| v\(\sim\)nodetype, a\(\sim\)block | 2 | -2816.23 | 156.42 | 0.00 |
| v\(\sim\)nodetype | 3 | -2870.71 | 147.43 | 0.05 |
| a\(\sim\)block | 4 | -3747.71 | 108.54 | 0.01 |
References
Footnotes
Note that in HSSM, the software used for analyses, the decision boundary parameter is modeled as [-a, a]. Boundary estimates in the conventional setup([0, a]) should be halved to recreate our results.↩︎
Note that while the 95% HDI for drift rate differences in structured condition does include 0, our apriori predictions assume directionality – that is if implicit boundaries are remembered better, we expect this difference to be reliably above 0. Thus, our inference relies on the proportion of posterior samples above 0 as opposed to the 95% HDI.↩︎
See Supplementary Figure S4 for conforming results from a complex model fit including block as a factor on drift rates.↩︎
Citation
@article{savalia2026,
author = {Savalia, Tejas and J. Starns, Jeffrey and L. Cohen, Andrew},
title = {Implicit Boundaries Are Remembered Better Than Non-Boundaries
in Statistical Learning},
journal = {Memory},
volume = {34},
number = {9},
date = {2026-09-04},
url = {https://doi.org},
doi = {10.1080/09658211.2026.2719605},
langid = {en}
}