Author response:
Reviewer #1 (Public review):
A previous study from the same team (McDougle & Taylor, 2019) demonstrated that explicit strategies during visuomotor adaptation can be dissociated into retrieval-based and algorithmic strategies. However, whether these distinct forms of explicit processing differentially influence implicit recalibration has remained unresolved, with previous studies providing evidence both for relatively independent explicit and implicit processes and for interactions between them. This study addresses this question through a series of experiments that used Critical and Non-Critical targets to induce distinct strategic modes while maintaining comparable adaptation at the Critical target.
Experiment 1 replicated previous findings showing broader implicit generalization under algorithmic strategies. However, this broader generalization could be explained by spillover effects arising from adaptation at the Non-Critical targets. Experiment 2 was designed to reduce such spillover effects by increasing the spatial separation between the Critical and Non-Critical targets. Although broader generalization was still observed in the algorithmic condition, this effect was interpreted as reflecting greater variability in reaching behavior at the Critical target. Finally, Experiment 3 introduced additional controls using an error-clamp paradigm, and the difference in generalization width between the two strategies largely disappeared.
We appreciate the reviewer’s thoughtful and comprehensive summary of our study. One thing we would like to clarify is that the non-critical targets used in Experiment 1 received the same type of online continuous feedback as the critical target.Therefore the extent of implicit recalibration should be comparable between the critical and non-critical targets in Experiment 1. In contrast, for Experiment 2, we tightened the control for implicit recalibration at the non-critical targets by: 1) delivering delayed endpoint feedback for all non-critical targets while keeping the online continuous feedback for the critical target, which is known to suppress implicit recalibration, and 2) we widened the spatial gap between the critical and non-critical targets, to minimize spillover 2) As a result, the implicit recalibration was diminished at the non-critical targets, contributing to the shrinkage of the generalization curve around the critical target.
One other issue that we would like to make clear is that Experiment 1 was not a straight replication of a previous study, at least to our knowledge. We believe that the reviewer is referring to our previous study (McDougle and Taylor 2019), which found broader generalization for algorithmic strategies (Experiment 4). However, in that study cursor feedback was always delayed. As such, the observed broader generalization was most likely due to the strategy itself and not implicit recalibration.
Together, these findings led the authors to conclude that implicit recalibration is relatively insensitive to the type of explicit strategy employed and is primarily shaped by the statistics of the movement plans on which learning occurs.
The experimental design using Critical and Non-Critical targets is particularly interesting and represents a creative approach to manipulating strategy use. Reaction times were generally longer in the algorithmic group, even at the Critical target, suggesting that the manipulation was at least partially successful in biasing participants toward algorithmic versus retrieval-based strategies. The results that the implicit recalibration is independent of the explicit strategy (how you aim) but depends on the aiming point by the explicit strategies (where you aim) are basically reasonable.
We are glad to know that our primary finding and conclusion appears reasonable. While we acknowledge that the finding doesn’t appear to be particularly exciting at face value, it does speak to larger questions regarding the independence of different learning systems and how just statistical or surface-level differences in training can result in relatively large differences in apparent behavior that could be easily misinterpreted as the result of system interactions.
I would like the authors to clarify two points.
First, how reasonable is it to infer the use of distinct explicit strategies primarily from reaction time differences? While longer reaction times in the algorithmic group are consistent with greater computational demands, it remains unclear whether the longer reaction times observed at the Critical target necessarily reflect different strategy implementations at that location. In particular, could the increased cognitive demands associated with the Non-Critical targets in the algorithmic condition have carried over to the Critical target, thereby prolonging reaction times without implying qualitatively different strategies at the Critical target itself?
This is a fair concern, as RT is an indirect marker of strategy use and, by itself, cannot establish that participants used different strategies at the Critical target. Prior work, however, provided guidance for the design of our experimental manipulations. Algorithmic strategies, in which an aiming solution is computed online, are associated with longer RTs, whereas retrieval of a previously cached stimulus–response association produces substantially shorter RTs (McDougle and Taylor, 2019; Velazquez-Vargas and Taylor, 2024). Moreover, caching becomes increasingly difficult as the number of target-specific solutions increases, particularly beyond approximately four targets (Velazquez-Vargas and Taylor, 2024; Bejjanki and Taylor 2026). Our manipulation was designed around these findings: participants in the Algorithmic condition learned the 45° rotation across 10 targets, whereas participants in the Retrieval condition repeatedly encountered the 45° rotation only at the Critical target. As expected with this experimental design, RTs at the Critical target were significantly longer in the Algorithmic condition across all three experiments.
We agree with the reviewer, however, that this RT difference could in principle reflect a more general carryover of cognitive demands from the Non-Critical targets rather than online computation at the Critical target itself. We can address this possibility more directly by asking whether RT at the Critical target exhibits the parametric signature expected of an algorithmic process. A defining feature of mental rotation is that RT scales with the magnitude of the computed aiming solution (Georgopoulos and Massey, 1987; Bhat and Sanes, 1998; McDougle and Taylor, 2019; Velazquez-Vargas and Taylor, 2024). Although rotation magnitude was fixed in the present experiments, participants’ actual reach angles varied naturally from trial to trial. Indeed, McDougle and Taylor (2019) originally demonstrated this relationship using actual reach angle rather than imposed rotation magnitude. We can therefore test whether trial-by-trial RT covaries with reach angle at the Critical target in the Algorithmic condition but not in the Retrieval condition. Such a relationship would be difficult to explain as a nonspecific carryover of cognitive load and would instead provide direct evidence that preparation time at the Critical target reflects the computation of the aiming solution.
We also observe a second, independent difference at the Critical target: reach angles are consistently more variable in the Algorithmic condition than in the Retrieval condition across all three experiments (Figure S6). This pattern is consistent with repeated online computation producing variability in the selected aiming solution, whereas retrieval of a cached stimulus–response association produces a more stable response. Importantly, a general carryover account based solely on increased cognitive demands does not readily explain why movements to the Critical target should also be systematically more variable. Nor is this pattern easily explained by a speed–accuracy tradeoff: the Algorithmic group had more preparation time yet nevertheless exhibited greater variability. Consistent with this notion, Velázquez-Vargas and Taylor (2024) found that retrieving cached solutions produced less variable and more precise movements than movements that are not cached in the memory trace.
Third, we can conduct additional analysis to compare RT variability between algorithmic and retrieval groups at the critical target location. According to Logan instance theory (Logan, 1988), the retrieval of cached stimulus-response associations produces a stable RT profile, in contrast, trial-by-trial algorithmic computation can result in more variable trial-by-trial RT differences.
While we agree that RT differences alone should not be taken as definitive evidence of distinct strategies, our specific experimental design, the longer and more variable RTs at the Critical target, the greater trial-by-trial variability at that same target, and, if confirmed, a parametric relationship between RT and reach angle provide converging evidence that participants in the two conditions relied on different strategy implementations when preparing movements to the Critical target.
Second, the interpretation of Experiment 3 is not entirely clear to me. The manuscript argues that the algorithmic group continued to exhibit greater reaching variability than the retrieval group. If this variability indeed reflects greater variability in movement plans, one might expect a broader implicit generalization function in the algorithmic group. However, the generalization widths were comparable between groups. Could this result instead suggest that the implicit recalibration process itself generalized more narrowly in the algorithmic group, thereby offsetting the broader distribution of movement plans? More generally, I would appreciate further clarification regarding the relationship between reaching variability, movement-plan variability, and the resulting width of the implicit generalization function.
We appreciate the reviewer’s thoughtful comment and agree that this is an important distinction. First, we would like to clarify the relationship among reaching variability, movement-plan variability, and the width of the implicit generalization function. Previous work has shown that when implicit recalibration occurs at a particular target location without an explicit aiming strategy, its generalization across the workspace can be described by a Gaussian-shaped function centered near the trained target location (Morehead et al., 2017). When an explicit aiming strategy is involved, however, implicit recalibration is centered closer to the planned aiming location rather than the visual target itself (McDougle et al., 2017). Thus, implicit recalibration is greatest near the direction in which the movement is planned, and a broader spatial distribution of movement plans can, in principle, produce a broader aggregate implicit generalization function. In the present study, we therefore use trial-to-trial variability in endpoint hand angle as a behavioral proxy for variability in planned movement direction, while recognizing that endpoint variability may also contain contributions from execution-related noise.
This framework motivated the progression from Experiments 1 to 3. In Experiment 1, participants in the algorithmic condition exhibited substantially greater reaching variability, consistent with the idea that they sampled a wider range of movement plans across trials. Because error feedback associated with these different movement plans can induce implicit recalibration around each planned direction, greater variability in strategy use could contribute to the broader implicit generalization observed in the algorithmic group. In Experiment 2, we imposed stricter controls on spillover from noncritical targets, which reduced the overall breadth of generalization; nevertheless, model fits still suggested a modestly broader implicit generalization function in the algorithmic group, consistent with the remaining difference in reaching variability.
Experiment 3 was designed to further reduce the direct influence of strategic variability on the induction of implicit recalibration by using a modified error-clamp paradigm. Error-clamp feedback has been shown to elicit implicit recalibration independently of task success and the participant’s explicit strategy (Morehead et al., 2017). We therefore used error-clamp feedback as an incidental signal to induce implicit recalibration while participants implemented either algorithmic or retrieval-based strategies. Importantly, however, Experiment 3 did not completely eliminate between-group differences in reaching variability: the algorithmic group continued to show greater variability around the critical 45-degree location than the retrieval group. We agree with the reviewer that, in principle, comparable generalization widths could arise if this broader distribution of movement plans were offset by a narrower local generalization of implicit recalibration in the algorithmic group.
However, not all variability is equivalent—or well described by a Gaussian distribution. Depending on the direction of the skew, variability in aiming can produce different effects on the implicit recalibration function, appearing as either broader generalization or greater amplitude. These effects are difficult to appreciate in Figures 3 and 5 for Experiments 2 and 3, respectively. We therefore sought to illustrate this more clearly in Figure 6, which shows how differences in the underlying aim distributions can shape the resulting implicit recalibration function in directionally complex ways. What complicates matters further is that implicit recalibration can asymptote (Morehead et al., 2017; Kim et al., 2018; Wilterson & Taylor, 2021). As a result, plan-based generalization can distort the implicit recalibration function in different ways depending on which side of the aim the error falls. The block-by-block analysis, suggested by reviewer 2, may shed light on this issue because we can get a sense if implicit recalibration has reached asymptote.
At a minimum, in the revised manuscript, we work to make clearer that subtle changes in the reach distribution may have a corresponding impact on the shape of implicit recalibration’s generalization function.
Reviewer #2 (Public review):
This study addresses an important question in motor learning: whether algorithmic versus retrieval-based explicit strategies differentially shape implicit recalibration. The progressive experimental logic across three experiments is commendable, and the plan-based generalization account is a plausible and interesting interpretation. However, several methodological concerns limit the strength of the conclusions. I recommend the authors temper their claims accordingly, in the results/discussion section.
Concerns
(1) The retrieval group received 5 pre-exposure trials before main training began, which the algorithmic group did not. Faster RTs in the retrieval group could therefore reflect task familiarity from extra practice rather than efficient memory retrieval per se. I might have missed this, but I did not see performance data from these pre-exposure trials. The early training advantage in the retrieval group might be confounded with the 5 pre-exposure trials they received. Unless there is a direct comparison between the pre-exposure trials for the caching group and the first 5 trials of the algorithmic group, the claim that "storing and retrieving a memory from a short-term memory cache confers more rapid performance improvements than executing an algorithmic strategy" seems somewhat unwarranted.
We appreciate the reviewer raising this potential confound. We agree that the five pre-exposure trials in the Retrieval condition introduce a small difference in initial task familiarity. However, this account makes a straightforward prediction: if the shorter RTs in the Retrieval condition simply reflect five additional trials of general task experience, then the RT difference should disappear once the Algorithmic group has received a comparable amount of practice.
We can test this directly by comparing the five pre-exposure trials in the Retrieval condition with the first five trials of the Algorithmic condition. We will also compare these pre-exposure trials with a later five-trial window from the Algorithmic condition to determine whether additional practice substantially reduces Algorithmic RTs. Assuming the observed pattern is as expected, RTs in the Algorithmic condition remain substantially longer even after considerably more than five trials of practice. Thus, the group difference cannot be explained simply by the Retrieval group having five additional trials of task familiarity. This persistent RT difference, together with our prior work showing characteristic RT differences between algorithmic computation and retrieval of cached aiming solutions, supports our interpretation that the groups relied on different strategy implementations.
We are less certain what the reviewer means by the “early training advantage.” If this refers to angular error, we agree that the Retrieval group shows somewhat better performance very early in training, but this difference is not a central focus of the present study and largely disappears by the second or third training block. We will clarify the text so that we do not overinterpret this transient difference.
If instead the reviewer is referring to RT, then the matched-trial analysis directly addresses the concern. Five additional familiarization trials could plausibly produce a brief initial advantage, but such an effect should dissipate within a small number of subsequent trials. In contrast, the RT difference between the Algorithmic and Retrieval conditions remains robust throughout training. We therefore do not think that general task familiarity provides a sufficient explanation for the observed RT differences.
The algorithmic group also visited the critical target approximately 40% of trials across 356 trials (about 140 trials?). McDougle & Taylor (2019) showed that 300 trials of practice with 2 targets is enough transition from algorithmic to caching strategies. It seems likely that the number of visits to the critical target here was sufficient for caching to develop in the algorithmic condition. This concern about caching in the algorithmic group has implications for the implicit recalibration measurements. As I understand it, the 7 exclusion blocks were distributed throughout training, and so, implicit recalibration was measured across both early and late practice. If caching emerged in the algorithmic group during late practice, then the generalization functions - averaged across all 7 exclusion blocks - conflate early algorithmic strategy and later caching. The broader generalization function observed in the algorithmic group may therefore be driven primarily by early exclusion blocks, while later exclusion blocks may increasingly resemble the retrieval group as caching develops. This is testable in the data: if generalization breadth in the algorithmic group narrows across the 7 exclusion blocks while remaining stable in the retrieval group, that would be consistent with a strategy transition occurring during training. The authors should either report exclusion block-by-block generalization functions separately for each group, or acknowledge that the averaged generalization functions may obscure a strategy transition in the algorithmic group.
The reviewer raises an interesting possibility. In McDougle and Taylor (2019), however, the transition from algorithmic computation to retrieval occurred in a condition with only two targets in the task set. With repeated practice, participants needed to retain only two target-specific aiming solutions, making it feasible to replace online computation with retrieval of cached stimulus–response associations. By contrast, the Algorithmic condition in the present study contained 10 target locations. Our prior work suggests that caching becomes increasingly difficult once the number of target-specific solutions exceeds approximately four, at least over the timescale of several hundred trials (Velázquez-Vargas and Taylor, 2024; Bejjanki and Taylor, 2026). Thus, our task was designed to maintain pressure toward an algorithmic strategy throughout training.
The reviewer nevertheless raises a more specific possibility that is not ruled out simply by the size of the target set: participants might selectively cache the aiming solution for the frequently sampled Critical target while continuing to use an algorithmic strategy at the remaining targets. We think the existing behavioral data argue against such a clear transition.
First, reaction times at the Critical target in the Algorithmic condition remained substantially longer than those in the Retrieval condition throughout training. If participants had cached the aiming solution for the Critical target, we would expect preparation times at that location to be the same as the Retrieval condition. However, the RTs for the Algorithmic and Retrieval conditions are significantly different in the last block of training.
Second, within the Algorithmic condition, reaction times at the Critical target remained similar to those at the Non-Critical targets. Selective caching of the Critical target predicts a different pattern: preparation should become faster at the Critical target than at the surrounding locations, where participants would still need to compute the appropriate aiming solution. However, we do not observe a significant difference between RTs at Critical and Non-critical targets for the Algorithmic conditions at the end of the training block. Taken together, these two observations suggest that the Critical target continued to be treated similarly to the other members of the 10-target set rather than becoming a privileged, cached stimulus–response association.
Third, participants would have to single out the Critical target as being distinct. All targets had the same visual appearance, the Critical target was never presented on consecutive trials, and participants were not informed that it had a special role in the experiment. However, we acknowledge that its higher sampling frequency, its somewhat greater separation from neighboring targets, and the location of the subsequent exclusion trials could nevertheless have made it more salient. Thus, we cannot rule out selective caching solely from the task structure.
For this reason, we agree that the reviewer’s proposed analysis provides a useful additional test. If the Critical-target strategy progressively transitioned from algorithmic computation to retrieval, one prediction is that the generalization function in the Algorithmic condition should become narrower across successive exclusion blocks and increasingly resemble that of the Retrieval condition. We will therefore attempt to estimate the width of the generalization functions as a function of the training block between the Algorithmic and Retrieval conditions.
There is, however, an important limitation to interpreting block-by-block generalization functions in this experiment. Implicit recalibration is both plan-based and temporally labile. Generalization is centered around the planned aiming direction (McDougle et al., 2017), and recent work indicates that implicit adaptation can decay over relatively short intervals (Zhou et al 2017; Hadjiosif et al 2023). Consequently, the first trial of an exclusion block provides the cleanest sample of the current state of implicit recalibration. Across later trials in the block, the measured response can be influenced both by temporal decay and by where the sampled target falls relative to the participant’s current aiming direction.
To minimize systematic sampling bias, the starting exclusion target was randomized across participants. This means that these effects should average out at the group level, but individual exclusion blocks do not provide equally precise samples of the entire generalization function. A fully balanced estimate of every position within each exclusion block would require substantially more participants than were included in the present experiments. We will therefore present the blockwise analysis while interpreting changes in the estimated breadth cautiously.
(2) The error-clamp paradigm in Experiment 3 introduces two problems. First, it breaks the relationship between planned movement direction and feedback of movement direction, likely reducing the sense of agency over movement feedback (indeed, typical error clamp study instructions tell participants to ignore the movement feedback). Reduced agency may itself suppress differences between algorithmic and caching conditions. First, if strategy type exerts its influence on implicit recalibration via the explicit plan - as the plan-based generalization account predicts - then severing the link between intended movement and feedback might close off the channel through which strategy could shape the implicit system, regardless of which strategy is used. Second, reduced agency could modify the explicit strategies themselves. For caching, the stimulus-response association might be reinforced by a consistent relationship between intended movement and observed outcome; the clamped feedback may make it more difficult to reinforce the cached response, weakening the stimulus-response association. For the algorithmic strategy, effortful mental rotation may depend on the perception that the computation meaningfully determines the outcome; as participants understand that clamped feedback does not depend on their behavior (although yes, the text-based "Excellent/Good Move feedback) does depend on their behavior, they may engage in somewhat less complete mental rotation. Both possibilities could contribute to convergence between groups in generalization. It is noted that the preserved RT difference between groups in Experiment 3 partially argues against a loss of effort under the algorithmic condition, but it does not rule out weakened formation of stimulation-response associations during caching.
The reviewer raises an important point. By design, the error-clamp manipulation in Experiment 3 decouples the participant’s planned movement from the visual consequence of that movement. While this gives us precise control over the error driving implicit recalibration, it could reduce agency over the cursor and thereby alter the interaction between explicit strategy and implicit learning in ways that are difficult to rule out completely. In particular, as the reviewer notes, reduced agency could potentially weaken either the influence of the explicit plan on implicit recalibration or the strategies themselves. Because Experiment 3 was intended to test for the absence of a strategy-dependent difference in implicit recalibration, we acknowledge that higher-order interactions of this kind represent an inherent limitation of our study if Experiment 3 is taken in isolation.
There are nevertheless several observations that make us think that reduced agency is unlikely to provide the primary explanation for the convergence between groups. First, the progression across Experiments 1–3 is informative. In Experiment 1, where participants retained normal control over the cursor, the broader generalization function in the Algorithmic condition closely mirrored the broader distribution of reach directions. This relationship suggests that the apparent difference in implicit generalization could arise from differences in where participants planned their movements rather than from a direct effect of strategy type on the implicit system. In Experiment 2, we sought to reduce the difference in the distribution of planned movements while preserving normal action–outcome contingencies and, importantly, the generalization functions became correspondingly more similar. Experiment 3 then controlled the error signal itself and again produced similar generalization across strategy conditions. Taken together, this progression favors the interpretation that strategy affects the measured generalization function indirectly, through differences in the distribution of movement plans, rather than directly altering the underlying implicit recalibration process.
We nevertheless agree that these experiments cannot exclude all possible interactions between explicit and implicit learning systems. Indeed, whether these systems interact directly has been an important and persistent question in the sensorimotor adaptation literature. Several studies have reported evidence consistent with direct interactions (e.g., Albert et al., 2022; Maresch and Donchin 2021; t’Hart and Henriques 2024), whereas our own work has generally pointed toward indirect interactions mediated by factors such as movement planning and the current state of implicit adaptation (Taylor et al 2010; Taylor and Ivry 2011; McDougle et al 2017). Indeed, our recent study was designed specifically to distinguish these possibilities under tighter experimental control (Chen and Taylor, 2026), yet we found that the interaction between explicit and implicit processes is more complex than a simple independent-versus-interacting dichotomy. Going forward, we think it is more cautious to first rule out low-level statistical or distributional differences that could account for apparent effects before invoking higher-order interactions between learning systems.
Finally, one motivation for the present study was that much of the literature on implicit generalization trains participants at a single target location before measuring generalization across the workspace. Under such conditions, participants have ample opportunity to retrieve a stable target-specific aiming solution. If algorithmic and retrieval strategies fundamentally alter implicit generalization, then many existing estimates of generalization may characterize implicit learning under retrieval-like conditions rather than providing a strategy-independent property of the implicit system. Across the present experiments, we find little evidence for such a fundamental difference once the distribution of movement plans and the experienced error are better controlled. We therefore think the most parsimonious interpretation of the current results is that algorithmic and retrieval strategies primarily influence implicit generalization indirectly through how movements are planned.
We plan to revise the manuscript to acknowledge that Experiment 3 cannot completely rule out higher-order effects associated with reduced agency under error-clamp feedback. We will also provide additional validation that participants were implementing distinct strategies, beyond the group-level RT differences, by testing whether RT in the Algorithmic condition scales with the instructed rotation magnitude, and whether RT variability shows group-level difference (Logan, 1988). If present, this relationship would provide stronger evidence that participants continued to engage the intended strategy under the clamp. We agree, however, that confirming distinct strategy use would not by itself rule out the possibility that reduced agency altered how those strategies interacted with implicit recalibration.
Reviewer #3 (Public review):
Summary:
This manuscript asks whether two forms of explicit strategy use in visuomotor adaptation, i.e., algorithmic mental rotation and retrieval of a cached aiming solution, differentially influence implicit recalibration. The question is relevant because much prior work treats explicit strategy as a unitary process, whereas the algorithmic/retrieval distinction is theoretically meaningful and grounded in cognitive theory. Across three experiments, the authors report that algorithmic strategy conditions initially produced broader fitted implicit generalization functions than retrieval conditions, but that this difference was reduced or eliminated when reach variability and sensory prediction errors were more tightly controlled.
Strengths:
The paper is clearly written, theoretically well-motivated, and employs a commendably transparent and progressive experimental logic. The three-experiment structure, in which confounds are systematically identified and addressed, represents a strong model of cumulative experimental design (I will certainly use it in teaching courses on experimental methods):
Experiment 1 establishes an apparent difference in implicit generalization breadth. Experiment 2 attempts to reduce error spillover from Non-Critical targets by increasing angular separation and using delayed endpoint feedback. Experiment 3 uses an error-clamp design to decouple variable reaching from error feedback. This sequence is appropriate for testing whether the initial difference reflects a strategy-dependent change in implicit recalibration or instead follows from the distribution of movement plans and error exposure. The authors also provide reaction-time and performance data that are broadly consistent with the intended distinction between algorithmic and retrieval-like task performance.
We thank the reviewer for this thoughtful and constructive assessment of the manuscript. We especially appreciate their recognition of the progressive experimental logic across the three experiments and of the broader theoretical motivation for distinguishing algorithmic and retrieval-based strategies. We are also grateful for the reviewer’s comments on the clarity and transparency of the work.
Weaknesses:
The evidence does not support the strongest claims made in the manuscript, namely that algorithmic and retrieval strategies generally do not reshape implicit recalibration.
In general, I am skeptical of the authors' interpretation of null results. Several central conclusions depend on non-significant group differences, especially in Experiment 3. Non-significant tests are repeatedly treated as evidence that groups are equivalent or that confounds are absent (e.g., implicit recalibration magnitude (Algorithmic: 11.43 {plus minus} 6.43{degree sign}; Retrieval: 15.49 {plus minus} 8.99{degree sign}; t(38) = −1.65, p = .11), adaptation level before Exclusion probes (F(1,256) = 3.04, p = .08) and Exclusion RT differences (F(1,266) = 3.15, p = .08), whereas a modest model-dependent breadth effect (bootstrap p = .02) is treated as meaningful (for more on the model-dependent breadth effect, see below).
Without confidence intervals, equivalence tests, or Bayesian analyses, I think that the authors' interpretations comprise an inferential gap. A failure to find a significant difference is not equivalent to evidence of equivalence, particularly given that the implicit recalibration signal gets progressively attenuated across experiments (Experiment 1: ~16-17{degree sign}; Experiment 2: ~11-15{degree sign}; Experiment 3: ~7-8{degree sign}). With a substantially diminished signal in Experiment 3, the null result could partly reflect reduced statistical sensitivity rather than true equivalence.
We agree with the reviewer that our original interpretation of several non-significant effects was too strong, especially without providing some form of equivalence test. Our central hypothesis predicts little or no difference between algorithmic and retrieval-based strategies under conditions in which movement plans and error exposure are controlled, and we therefore face the inherent difficulty of drawing conclusions from an expected null effect. As the reviewer notes, a non-significant conventional hypothesis test does not by itself provide evidence that two conditions are equivalent.
We therefore plan to supplement the existing analyses with quantitative assessments of the strength of evidence for the null/equivalence, using Bayesian factor analyses to confirm whether two conditions are equivalent. These analyses will allow us to distinguish between effects that are sufficiently small to support our theoretical interpretation and effects for which the data are simply inconclusive. We will also revise the manuscript throughout to avoid treating p > .05 as evidence of equivalence in the absence of such supporting analyses.
We also now appreciate that the magnitude of implicit recalibration decreases progressively across experiments. This reduction could diminish our sensitivity to differences between the Algorithmic and Retrieval conditions and therefore represents an important qualification on the null result. Because the experiments used similar trial structures and were conducted with the same experimental equipment, the source of this reduction is not immediately clear. The block-by-block analysis suggested by Reviewer 2 may provide useful insight into how implicit recalibration evolves over the course of training and whether this attenuation emerges gradually within experiments.
My main technical concern is the analysis of generalization breadth already alluded to. The central claims rely on group-level Gaussian fits to only seven Exclusion probe locations spanning −45{degree sign} to +45{degree sign} around the Critical target. In several cases, the fitted centers and widths are poorly constrained by the sampled range. For example, in Experiment 2 the algorithmic group's fitted center is shifted to approximately 29{degree sign}, meaning that the probe range samples the function asymmetrically relative to its own peak. In Experiment 3, fitted centers are near or outside the sampled range, while estimated widths are very broad. Under these conditions, the width parameter may partly reflect extrapolation or parameter trade-offs between center, amplitude, and width rather than a genuine difference in generalization breadth.
Based on prior work characterizing implicit generalization in relative isolation from explicit strategy (Morehead et al., 2017; Poh and Taylor, 2019), we expected a relatively narrow generalization function, with a full width at half maximum of approximately 30°. We therefore expected probes spanning −45° to +45° around the Critical target to capture most of the function. At the same time, prior work on plan-based generalization predicts that the function should shift toward the participant’s aiming direction (Day et al., 2016; McDougle et al., 2017; Chen and Taylor, 2026), which complicates the choice of where to center the probes. Expanding the range and density of probe locations is also not cost-free, because additional exclusion trials increase temporal decay (Hajiosif et al., 2023) and begin to overlap with trained locations.
We nevertheless agree with the reviewer that, when the fitted center approaches the edge of the sampled range, estimates of Gaussian width can become poorly constrained and may partly reflect parameter trade-offs or extrapolation beyond the observed data. We therefore plan to test whether the group differences persist when the Gaussian fits are constrained so that their centers fall within the sampled range. We will also examine complementary nonparametric measures of generalization breadth, such as the area between the group generalization curves across the sampled probe locations. Convergence across these approaches would provide stronger evidence that the reported differences reflect the observed shape of the generalization functions rather than instability in the Gaussian parameter estimates. If the results are not robust across approaches, we will revise the manuscript to qualify the interpretation of the fitted width estimates accordingly.
Lastly, I think that the authors' use of an error-clamp paradigm is, from an experimental point of view, quite elegant. By controlling the sensory prediction error independently of reach direction, they can isolate implicit recalibration from the confounds identified in Experiments 1 and 2. However, I see a fundamental problem or question concerning construct validity here: In Experiments 1 and 2, the algorithmic strategy was operationalized as participants computing a counterrotated aiming direction in response to a visible cursor rotation. This is a naturalistic context where mental rotation is both required and meaningfully connected to task success. In Experiment 3, however, there is no visuomotor rotation to compensate for. The error-clamp renders the cursor feedback task-irrelevant. Instead, participants are instructed via text commands (e.g., "move towards 45{degree sign}") to reach invisible locations, rendering the "algorithmic strategy" in this context essentially an instructed spatial navigation toward arbitrary angular locations, not genuine visuomotor mental rotation driven by an error signal.
To put it differently, are we sure that the cognitive process engaged by the algorithmic group in Experiment 3 is the same as the algorithmic mental rotation strategy in Experiments 1 and 2? If not, then the null result in Experiment 3 may not speak to the original question about how algorithmic strategies interact with implicit recalibration after all. Instead, it may reflect the absence of a genuine strategy manipulation.
This concern is closely related to that raised by Reviewer 2. We are fairly confident that participants in Experiment 3 were nevertheless engaging in the intended strategy manipulation. Participants in the Algorithmic condition showed substantially longer RTs than those in the Retrieval condition, and they were able to accurately generate the instructed angular reach directions across trials. The two conditions also differed in the variability of both RT and reach direction, consistent with online computation of an aiming solution in the Algorithmic condition and retrieval of a more stable cached response in the Retrieval condition. We can provide an additional validation by examining the relationship between RT and reach angle and comparing RT variability across two conditions. If RT scales parametrically with instructed reach angle in the Algorithmic condition but not in the Retrieval condition, this would provide stronger evidence that participants were engaging an online mental-rotation-like computation rather than simply following arbitrary spatial instructions. Moreover, RT yielded by the retrieval strategy would tend to be less variable than the algorithmic strategy.
We agree, however, that this does not fully address the reviewer’s broader concern. Experiment 3 necessarily changed the context in which the strategy was implemented. In Experiments 1 and 2, mental rotation was used to counteract a visuomotor perturbation and was therefore directly tied to successful control of the cursor. In Experiment 3, the error clamp removed this instrumental relationship: participants still had to compute and execute different angular reach directions, but those computations no longer determined the visual cursor outcome. In that sense, the algorithmic process in Experiment 3 was less naturally embedded in the task and could reasonably be viewed as a somewhat different instantiation of the task.
We therefore acknowledge that Experiment 3 cannot establish with certainty that the same higher-order cognitive process was engaged in exactly the same way as in Experiments 1 and 2, nor can it rule out the possibility that this change in task relevance altered how explicit strategy interacted with implicit recalibration. At the same time, when considered together with Experiments 1 and 2, we think the overall pattern remains informative. The apparent strategy-dependent difference in generalization was largest when movement plans and error exposure differed most, became smaller when these factors were better controlled while normal action–outcome contingencies were preserved, and was eliminated when the error signal itself was experimentally controlled. This progression is more consistent with an indirect influence of strategy through differences in movement planning and error exposure than with a robust direct effect of strategy type on implicit recalibration.
Nonetheless, we agree that Experiment 3 should not be interpreted as a definitive test of whether algorithmic strategy, in its more relevant visuomotor adaptation context, can lead to different interactions with implicit recalibration compared to a retrieval strategy. We plan to revise the manuscript to make this limitation explicit.
To their credit, the authors report a compelling RT dissociation that mirrors Experiments 1 and 2: The algorithmic group shows slower RT, which is decreasing over training (0.98s → 0.76s), whereas the retrieval group exhibits faster, stable RT (0.52s → 0.45s). While this pattern is consistent with genuine strategy differences persisting in Experiment 3, it could also reflect the greater spatial precision demands of reaching to invisible targets from text instructions, rather than genuine mental rotation per se. Reaching to an invisible location defined by a verbal angular label is inherently more demanding than reaching to a visible target, regardless of strategy type, and this demand is asymmetrically present in the two groups, since Non-Critical targets are invisible for the algorithmic group but visible for the retrieval group.
Thus, from my point of view, experiment 3 should not be used as definitive evidence that algorithmic and retrieval strategies during standard visuomotor adaptation cannot differentially influence implicit recalibration.
We agree that the RT difference in Experiment 3, by itself, cannot rule out the possibility that the Algorithmic condition imposed greater spatial precision demands because participants were reaching to invisible locations specified by angular instructions. We can, however, test for a more diagnostic signature of algorithmic computation by examining whether RT scales parametrically with the instructed reach angle. A general cost associated with reaching to invisible targets could increase overall RT, but it would not necessarily predict the characteristic increase in preparation time with the magnitude of the required angular transformation.
We will therefore examine the relationship between RT and instructed reach angle in Experiment 3. If RT increases systematically with angular displacement in the Algorithmic condition, this would provide additional evidence that the longer RTs reflect online computation of the instructed aiming direction rather than simply the greater difficulty of reaching invisible targets.
We can also compare this RT–angle relationship across experiments. If participants are engaging the same underlying algorithmic computation in Experiments 1–3, we would expect the slope relating RT to angular displacement to be similar across experiments, even if the overall intercept differs because of differences in task structure and spatial demands. A comparable slope would therefore provide converging evidence that the same computational process was engaged despite the altered task context in Experiment 3.
We acknowledge, however, that similarity of the slopes would itself require yet another inference from a null difference and should therefore be interpreted cautiously. As with the generalization functions, we will use a Bayes factor analysis to quantify the strength of evidence for the null.
Overall, the manuscript addresses a meaningful question and the multi-experiment structure is useful. The evidence is incomplete for the broad claim that implicit recalibration is insensitive to strategy type. The study would make a clearer contribution if the authors narrowed the claims, strengthened the generalization analyses, and treated null effects with appropriate inferential tools.
Based on the reviewers’ comments and the additional analyses they have suggested, we think we will be able to place our conclusions on a firmer empirical footing while also tightening and narrowing them. In the revised manuscript, we will strengthen the generalization analyses, use more appropriate inferential tools for interpreting null effects, and temper our broader claims about the insensitivity of implicit recalibration to strategy type. We will also more explicitly acknowledge the limitations of the present experiments, especially Experiment 3.
