Humans underestimate their body mass in microgravity: evidence from reaching movements during spaceflight
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eLife Assessment
This paper undertakes an important investigation to determine whether movement slowing in microgravity is due to a strategic conservative approach or rather due to an underestimation of the mass of the arm. While the experimental dataset is unique and the coupled experimental and computational analyses comprehensive, the authors present incomplete results to support the claim that movement slowing is due to mass underestimation. Further analysis is needed to rule out alternative explanations.
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Abstract
Abstract
Astronauts consistently exhibit slower movements in microgravity, even during tasks requiring rapid responses. The sensorimotor mechanisms underlying this general slowing remain debated. Two competing hypotheses have been proposed: either the sensorimotor system adopts a conservative control strategy for safety and postural stability, or the system underestimates body mass due to reduced inputs from proprioceptive receptors. To resolve the debate, we studied twelve taikonauts aboard the China Space Station performing a classical hand-reaching task. Compared to their pre-flight performance and to an age-matched control group, participants showed increased movement durations and altered kinematic profiles in microgravity. Model-based analyses of motor control parameters revealed that these changes stemmed from reduced initial force generation in the feedforward control phase followed by compensatory feedback-based corrections. These findings support the body mass underestimation hypothesis while refuting the strategic slowing hypothesis. Importantly, sensory estimate of bodily property in microgravity is biased but evaded from sensorimotor adaptation, calling for an extension of existing theories of motor learning.
Article activity feed
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eLife Assessment
This paper undertakes an important investigation to determine whether movement slowing in microgravity is due to a strategic conservative approach or rather due to an underestimation of the mass of the arm. While the experimental dataset is unique and the coupled experimental and computational analyses comprehensive, the authors present incomplete results to support the claim that movement slowing is due to mass underestimation. Further analysis is needed to rule out alternative explanations.
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Reviewer #1 (Public review):
Summary:
This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.
Strengths:
The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current form.
Weaknesses:
(1…
Reviewer #1 (Public review):
Summary:
This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.
Strengths:
The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current form.
Weaknesses:
(1) First, the hypothesis of a strategic and conservative slowdown implicitly assumes a similar cost function, which cannot be guaranteed, tested, or verified. For example, previous work has suggested that changing the ratio between the state and control weight matrices produced an alteration in movement kinematics similar to that presented here, without changing the estimated mass parameter (Crevecoeur et al., 2010, J Neurophysiol, 104 (3), 1301-1313). Thus, the hypothesis of conservative slowing cannot be rejected. Such a strategy could vary with effective mass (thus showing a statistical effect), but the possibility that the data reflect a combination of both mechanisms (strategic slowing and mass misestimation) remains open.
(2) The main strength of the article is the presence of directional effects expected under the hypothesis of mass estimation error. However, the article lacks a clear demonstration of such an effect: indeed, although there appears to be a significant effect of direction, I was not sure that this effect matched the model's predictions. A directional effect is not sufficient because the model makes clear quantitative predictions about how this effect should vary across directions. In the absence of a quantitative match between the model and the data, the authors' claims regarding the role of misestimating the effective mass remain unsupported.
In general, both the hypotheses of slowing motion (out of caution) and misestimating mass have been put forward in the past, and the added value of this article lies in demonstrating that the effect depended on direction. However, (1) a conservative strategy with a different cost function can also explain the data, and (2) the quantitative match between the directional effect and the model's predictions has not been established.
Specific points:
(1) I noted a lack of presentation of raw kinematic traces, which would be necessary to convince me that the directional effect was related to effective mass as stated.
(2) The presentation and justification of the model require substantial improvement; the reason for their presence in the supplementary material is unclear, as there is space to present the modelling work in detail in the main text. Regarding the model, some choices require justification: for example, why did the authors ignore the nonlinear Coriolis and centripetal terms?
(3) The increase in the proportion of trials with subcomponents is interesting, but the explanatory power of this observation is limited, as the initial percentage was already quite high (from 60-70% during the initial study to 70-85% in flight). This suggests that the potential effect of effective mass only explains a small increase in a trend already present in the initial study. A more critical assessment of this result is warranted.
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Reviewer #2 (Public review):
This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.
Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model tends to add confidence to the proposed conclusions. That being said, I have several comments that could be addressed to consolidate interpretations and improve clarity.
Main comments:
(1) Mass underestimation
a) While this interpretation is supported by data and analyses, it is not clear whether this gives …
Reviewer #2 (Public review):
This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.
Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model tends to add confidence to the proposed conclusions. That being said, I have several comments that could be addressed to consolidate interpretations and improve clarity.
Main comments:
(1) Mass underestimation
a) While this interpretation is supported by data and analyses, it is not clear whether this gives a complete picture of the underlying phenomena. The two hypotheses (i.e., mass underestimation vs deliberate speed reduction) can only be distinguished in terms of velocity/acceleration patterns, which should display specific changes during the flight with a mass underestimation. The experimental data generally shows the expected changes but for the 45{degree sign} condition, no changes are observed during flight compared to the pre- and post-phases (Figure 4). In Figure 5E, only a change in the primary submovement peak velocity is observed for 45{degree sign}, but this finding relies on a more involved decomposition procedure. It suggests that there is something specific about 45{degree sign} (beyond its low effective mass). In such planar movements, 45{degree sign} often corresponds to a movement which is close to single-joint, whereas 90{degree sign} and 135{degree sign} involve multi-joint movements. If so, the increased proportion of submovements in 90{degree sign} and 135{degree sign} could indicate that participants had more difficulties in coordinating multi-joint movements during flight. Besides inertia, Coriolis and centripetal effects may be non-negligible in such fast planar reaching (Hollerbach & Flash, Biol Cyber, 1982) and, interestingly, they would also be affected by a mass underestimation (thus, this is not necessarily incompatible with the author's view; yet predicting the effects of a mass underestimation on Coriolis/centripetal torques would require a two-link arm model). Overall, I found the discrepancy between the 45{degree sign} direction and the other directions under-exploited in the current version of the article. In sum, could the corrective submovements be due to a misestimation of Coriolis/centripetal torques in the multi-joint dynamics (caused specifically -or not- by a mass underestimation)?
b) Additionally, since the taikonauts are tested after 2 or 3 weeks in flight, one could also assume that neuromuscular deconditioning explains (at least in part) the general decrease in movement speed. Can the authors explain how to rule out this alternative interpretation? For instance, weaker muscles could account for slower movements within a classical time-effort trade-off (as more neural effort would be needed to generate a similar amount of muscle force, thereby suggesting a purposive slowing down of movement). Therefore, could the observed results (slowing down + more submovements) be explained by some neuromuscular deconditioning combined with a difficulty in coordinating multi-joint movements in weightlessness (due to a misestimation or Coriolis/centripetal torques) provide an alternative explanation for the results?
(2) Modelling
a) The model description should be improved as it is currently a mix of discrete time and continuous time formulations. Moreover, an infinite-horizon cost function is used, but I thought the authors used a finite-horizon formulation with the prefixed duration provided by the movement utility maximization framework of Shadmehr et al. (Curr Biol, 2016). Furthermore, was the mass underestimation reflected both in the utility model and the optimal control model? If so, did the authors really compute the feedback control gain with the underestimated mass but simulate the system with the real mass? This is important because the mass appears both in the utility framework and in the LQ framework. Given the current interpretations, the feedforward command is assumed to be erroneous, and the feedback command would allow for motor corrections. Therefore, it could be clarified whether the feedback command also misestimates the mass or not, which may affect its efficiency. For instance, if both feedforward and feedback motor commands are based on wrong internal models (e.g., due to the mass underestimation), one may wonder how the astronauts would execute accurate goal-directed movements.
b) The model seems to be deterministic in its current form (no motor and sensory noise). Since the framework developed by Todorov (2005) is used, sensorimotor noise could have been readily considered. One could also assume that motor and sensory noise increase in microgravity, and the model could inform on how microgravity affects the number of submovements or endpoint variance due to sensorimotor noise changes, for instance.
c) Finally, how does the model distinguish the feedforward and feedback components of the motor command that are discussed in the paper, given that the model only yields a feedback control law? Does 'feedforward' refer to the motor plan here (i.e., the prefixed duration and arguably the precomputed feedback gain)?
(3) Brevity of movements and speed-accuracy trade-off
The tested movements are much faster (average duration approx. 350 ms) than similar self-paced movements that have been studied in other works (e.g., Wang et al., J Neurophysiology, 2016; Berret et al., PLOS Comp Biol, 2021, where movements can last about 900-1000 ms). This is consistent with the instructions to reach quickly and accurately, in line with a speed-accuracy trade-off. Was this instruction given to highlight the inertial effects related to the arm's anisotropy? One may however, wonder if the same results would hold for slower self-paced movements (are they also with reduced speed compared to Earth performance?). Moreover, a few other important questions might need to be addressed for completeness: how to ensure that astronauts did remember this instruction during the flight? (could the control group move faster because they better remembered the instruction?). Did the taikonauts perform the experiment on their own during the flight, or did one taikonaut assume the role of the experimenter?
(4) No learning effect
This is a surprising effect, as mentioned by the authors. Other studies conducted in microgravity have indeed revealed an optimal adaptation of motor patterns in a few dozen trials (e.g., Gaveau et al., eLife, 2016). Perhaps the difference is again related to single-joint versus multi-joint movements. This should be better discussed given the impact of this claim. Typically, why would a "sensory bias of bodily property" persist in microgravity and be a "fundamental constraint of the sensorimotor system"?
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Reviewer #3 (Public review):
Summary:
The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for an increased number of corrective submovements in weightlessness. …
Reviewer #3 (Public review):
Summary:
The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for an increased number of corrective submovements in weightlessness. They contend that this provides conclusive evidence to accept the hypothesis of an underestimation of body mass.
Strengths:
In my opinion, the study provides a valuable contribution, the theoretical aspects are well presented through simulations, the statistical analyses are meticulous, the applicable literature is comprehensively considered and cited, and the manuscript is well written.
Weaknesses:
Nevertheless, I am of the opinion that the interpretation of the observations leaves room for other possible explanations of the observed phenomenon, thus weakening the strength of the arguments.
First, I would like to point out an apparent (at least to me) divergence between the predictions and the observed data. Figures 1 and S1 show that the difference between predicted values for the 3 movement directions is almost linear, with predictions for 90º midway between predictions for 45º and 135º. The effective mass at 90º appears to be much closer to that of 45º than to that of 135º (Figure S1A). But the data shown in Figure 2 and Figure 3 indicate that movements at 90º and 135º are grouped together in terms of reaction time, movement duration, and peak acceleration, while both differ significantly from those values for movements at 45º.
Furthermore, in Figure 4, the change in peak acceleration time and relative time to peak acceleration between 1g and 0g appears to be greater for 90º than for 135º, which appears to me to be at least superficially in contradiction with the predictions from Figure S1. If the effective mass is the key parameter, wouldn't one expect as much difference between 90º and 135º as between 90º and 45º? It is true that peak speed (Figure 3B) and peak speed time (Figure 4B) appear to follow the ordering according to effective mass, but is there a mathematical explanation as to why the ordering is respected for velocity but not acceleration? These inconsistencies weaken the author's conclusions and should be addressed.
Then, to strengthen the conclusions, I feel that the following points would need to be addressed:
(1) The authors model the movement control through equations that derive the input control variable in terms of the force acting on the hand and treat the arm as a second-order low-pass filter (Equation 13). Underestimation of the mass in the computation of a feedforward command would lead to a lower-than-expected displacement to that command. But it is not clear if and how the authors account for a potential modification of the time constants of the 2nd order system. The CNS does not effectuate movements with pure torque generators. Muscles have elastic properties that depend on their tonic excitation level, reflex feedback, and other parameters. Indeed, Fisk et al.* showed variations of movement characteristics consistent with lower muscle tone, lower bandwidth, and lower damping ratio in 0g compared to 1g. Could the variations in the response to the initial feedforward command be explained by a misrepresentation of the limbs' damping and natural frequency, leading to greater uncertainty about the consequences of the initial command? This would still be an argument for unadapted feedforward control of the movement, leading to the need for more corrective movements. But it would not necessarily reflect an underestimation of body mass.
*Fisk, J. O. H. N., Lackner, J. R., & DiZio, P. A. U. L. (1993). Gravitoinertial force level influences arm movement control. Journal of neurophysiology, 69(2), 504-511.
(2) The movements were measured by having the subjects slide their finger on the surface of a touch screen. In weightlessness, the implications of this contact are expected to be quite different than those on the ground. In weightlessness, the taikonauts would need to actively press downward to maintain contact with the screen, while on Earth, gravity will do the work. The tangential forces that resist movement due to friction might therefore be different in 0g. This could be particularly relevant given that the effect of friction would interact with the limb in a direction-dependent fashion, given the anisotropy of the equivalent mass at the fingertip evoked by the authors. Is there some way to discount or control for these potential effects?
(3) The carefully crafted modelling of the limb neglects, nevertheless, the potential instability of the base of the arm. While the taikonauts were able to use their left arm to stabilize their bodies, it is not clear to what extent active stabilization with the contralateral limb can reproduce the stability of the human body seated in a chair in Earth gravity. Unintended motion of the shoulder could account for a smaller-than-expected displacement of the hand in response to the initial feedforward command and/or greater propensity for errors (with a greater need for corrective submovements) in 0g. The direction of movement with respect to the anchoring point could lead to the dependence of the observed effects on movement direction. Could this be tested in some way, e.g., by testing subjects on the ground while standing on an unstable base of support or sitting on a swing, with the same requirement to stabilize the torso using the contralateral arm?
The arguments for an underestimation of body mass would be strengthened if the authors could address these points in some way.
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Author response:
Reviewer #1 (Public review):
Summary:
This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.
Strengths:
The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current …
Author response:
Reviewer #1 (Public review):
Summary:
This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.
Strengths:
The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current form.
Weaknesses:
(1) First, the hypothesis of a strategic and conservative slow down implicitly assumes a similar cost function, which cannot be guaranteed, tested, or verified. For example, previous work has suggested that changing the ratio between the state and control weight matrices produced an alteration in movement kinematics similar to that presented here, without changing the estimated mass parameter (Crevecoeur et al., 2010, J Neurophysiol, 104 (3), 1301-1313). Thus, the hypothesis of conservative slowing cannot be rejected. Such a strategy could vary with effective mass (thus showing a statistical effect), but the possibility that the data reflect a combination of both mechanisms (strategic slowing and mass misestimation) remains open.
We test whether changing the ratio between the state and control weight matrices can generate the observed effect. As shown in Author response image 1 and Author response image 2, the cost function change cannot produce a reduced peak velocity/acceleration and their timing advance simultaneously, but a mass estimation change can. In other words, using mass underestimation alone can explain the two key findings, amplitude reduction and timing advance. Yes, we cannot exclude the possibility of a change in cost function on top of the mass underestimation, but the principle of Occam’s Razor would support to adhering to a simple explanation, i.e., using body mass underestimation to explain the key findings. We will include our exploration on possible changes in cost function in the revision (in the Supplemental Materials).
Author response image 1.
Simulation using an altered cost function with α = 3.0. Panels A, B, and E show simulated position, velocity, and acceleration profiles, respectively, for the three movement directions. Solid lines correspond to pre- and post-exposure conditions, while dashed lines represent the in-flight condition. Panels C and D display the peak velocity and its timing across the three phases (Pre, In, Post), and Panels F and G show the corresponding peak acceleration and its timing. Note, varying the cost function, while leading to reduced peak velocity/acceleration, leads to an erroneous prediction of delayed timing of peak velocity/acceleration.
Author response image 2.
Simulation results using a cost function with α = 0.3. The format is the same as in Author response image 1. Note, this ten-fold decrease in α, while finally getting the timing of peak velocity/acceleration right (advanced or reduced), leads to an erroneous prediction of increased peak velocity/acceleration.
(2) The main strength of the article is the presence of directional effects expected under the hypothesis of mass estimation error. However, the article lacks a clear demonstration of such an effect: indeed, although there appears to be a significant effect of direction, I was not sure that this effect matched the model's predictions. A directional effect is not sufficient because the model makes clear quantitative predictions about how this effect should vary across directions. In the absence of a quantitative match between the model and the data, the authors' claims regarding the role of misestimating the effective mass remain unsupported.
Our paper does not aim to quantitatively reproduce human reaching movements in microgravity. We will make this more clearly in the revision.
(1) The model is a simplification of the actual situation. For example, the model simulates an ideal case of moving a point mass (effective mass) without friction and without considering Coriolis and centripetal torques, while the actual situation is that people move their finger across a touch screen. The two-link arm model assumes planar movements, but our participants move their hand on a table top without vertical support to constrain their movement in 2D.
(2) Our study merely uses well-established (though simplified) models to qualitatively predict the overall behavioral patterns if mass underestimation is at play. For this purpose, the results are well in line with models’ qualitative predictions: we indeed confirm that key kinematic features (peak velocity and acceleration) follow the same ranking order of movement direction conditions as predicted.
(3) Using model simulation to qualitatively predict human behavioral patterns is a common practice in motor control studies, prominent examples including the papers on optimal feedback control (Todorov, 2004 and 2005) and movement vigor (Shadmehr et al., 2016). In fact, our model was inspired by the model in the latter paper.
Citations:
Todorov, E. (2004). Optimality principles in sensorimotor control. Nature Neuroscience, 7(9), 907.
Todorov, E. (2005). Stochastic optimal control and estimation methods adapted to the noise characteristics of the sensorimotor system. Neural Computation, 17(5), 1084–1108.
Shadmehr, R., Huang, H. J., & Ahmed, A. A. (2016). A Representation of Effort in Decision-Making and Motor Control. Current Biology: CB, 26(14), 1929–1934.
In general, both the hypotheses of slowing motion (out of caution) and misestimating mass have been put forward in the past, and the added value of this article lies in demonstrating that the effect depended on direction. However, (1) a conservative strategy with a different cost function can also explain the data, and (2) the quantitative match between the directional effect and the model's predictions has not been established.
Specific points:
(1) I noted a lack of presentation of raw kinematic traces, which would be necessary to convince me that the directional effect was related to effective mass as stated.
We are happy to include exemplary speed and acceleration trajectories. One example subject’s detailed trajectories are shown below and will be included in the revision. The reduced and advanced velocity/acceleration peaks are visible in typical trials.
Author response image 3.
Hand speed profiles (upper panels), hand acceleration profiles (middle panels) and speed profiles of the primary submovements (lower panels) towards different directions from an example participant.
(2) The presentation and justification of the model require substantial improvement; the reason for their presence in the supplementary material is unclear, as there is space to present the modelling work in detail in the main text. Regarding the model, some choices require justification: for example, why did the authors ignore the nonlinear Coriolis and centripetal terms?
Response: In brief, our simulations show that Coriolis and centripetal forces, despite having some directional anisotropy, only have small effects on predicted kinematics (see our responses to Reviewer 2). We will move descriptions of the model into the main text with more justifications for using a simple model.
(3) The increase in the proportion of trials with subcomponents is interesting, but the explanatory power of this observation is limited, as the initial percentage was already quite high (from 60-70% during the initial study to 70-85% in flight). This suggests that the potential effect of effective mass only explains a small increase in a trend already present in the initial study. A more critical assessment of this result is warranted.
Response: Indeed, the percentage of submovements only increases slightly, but the more important change is that the IPI (the inter-peak interval between submovements) also increases at the same time. Moreover, it is the effect of IPI that significantly predicts the duration increase in our linear mixed model. We will highlight this fact in our revision to avoid confusion.
Reviewer #2 (Public review):
This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.
Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model tends to add confidence to the proposed conclusions. That being said, I have several comments that could be addressed to consolidate interpretations and improve clarity.
Main comments:
(1) Mass underestimation
a) While this interpretation is supported by data and analyses, it is not clear whether this gives a complete picture of the underlying phenomena. The two hypotheses (i.e., mass underestimation vs deliberate speed reduction) can only be distinguished in terms of velocity/acceleration patterns, which should display specific changes during the flight with a mass underestimation. The experimental data generally shows the expected changes but for the 45{degree sign} condition, no changes are observed during flight compared to the pre- and post-phases (Figure 4). In Figure 5E, only a change in the primary submovement peak velocity is observed for 45{degree sign}, but this finding relies on a more involved decomposition procedure. It suggests that there is something specific about 45{degree sign} (beyond its low effective mass). In such planar movements, 45{degree sign} often corresponds to a movement which is close to single-joint, whereas 90{degree sign} and 135{degree sign} involve multi-joint movements. If so, the increased proportion of submovements in 90{degree sign} and 135{degree sign} could indicate that participants had more difficulties in coordinating multi-joint movements during flight. Besides inertia, Coriolis and centripetal effects may be non-negligible in such fast planar reaching (Hollerbach & Flash, Biol Cyber, 1982) and, interestingly, they would also be affected by a mass underestimation (thus, this is not necessarily incompatible with the author's view; yet predicting the effects of a mass underestimation on Coriolis/centripetal torques would require a two-link arm model). Overall, I found the discrepancy between the 45{degree sign} direction and the other directions under-exploited in the current version of the article. In sum, could the corrective submovements be due to a misestimation of Coriolis/centripetal torques in the multi-joint dynamics (caused specifically -or not- by a mass underestimation)?
We agree that the effect of mass underestimation is less in the 45° direction than the other two directions, possibly related to its reliance on single-joint (elbow) as opposed to two-joints (elbow and shoulder) movements. Plus, movement correction using one joint is probably easier (as also suggested by another reviewer), this possibility will be further discussed in the revision. However, we find that our model simplification (excluding Coriolis and centripetal torques) does not affect our main conclusions at all. First, we performed a simple simulation and found that, under the current optimal hand trajectory, incorporating Coriolis and centripetal torques has only a limited impact on the resulting joint torques (see simulations in Author response image 4). One reason is that we used smaller movements than Hallerbach & Flash did. In addition, we applied an optimal feedback control model to a more realistic 2-joint arm configuration. Despite its simplicity, this model produced a speed profile consistent with our current predictions and made similar predictions regarding the effects of mass underestimation (Author response image 5). We will provide a more realistic 2-joint arm model muscle dynamics in the revision to improve the simulation further, but the message will be same: including or excluding Coriolis and centripetal torques will not affect the theoretical predictions about mass underestimation. Second, as the reviewer correctly pointed out, the mass (and its underestimation) also affects these two torque terms, thus its effect on kinematic measures is not affected much even with the full model.
Author response image 4.
Joint angles and joint torque of shoulder and elbow with simulated trajectories towards different directions. A. Shoulder (green) and elbow (blue) angles change with time for the 45° movement direction. B. Components of joint interaction torques at the shoulder. Solid line: net torque at the shoulder; dotted line: shoulder inertia torque; dashed line: shoulder Coriolis and centripetal torque. C. Same plot as B for the elbow joint. D–F. Coriolis and centripetal components in the full 360° workspace, beyond three movement directions (45°, 90°, and 135°). D. Net torque. E. Inertial torque. F. Combined Coriolis and centripetal torque. Note the polar plots of Coriolis/centripetal torques (F) have a scale that is two magnitudes smaller than that of inertial torque in our simulation. All torques were simulated with the optimal movement duration. Torques were squared and integrated over each trajectory.
Author response image 5.
Comparison between simulation results from the full model with the addition of Coriolis/centripetal torques (left) and the simplified model (right). The position profiles (top) and the corresponding speed profiles low) are shown. Solid lines are for normal mass estimation and dashed lines for mass underestimation in microgravity. The three colors represent three movement directions (dark red: 45°, red: 90°, yellow: 135°). The full model used a 2-link arm model without realistic muscle dynamics yet (will include in the formal revision) thus the speed profile is not smooth. Importantly, the full model also predict the same effect of mass underestimation, i.e., reduced peak velocity/acceleration and their timing advance.
b) Additionally, since the taikonauts are tested after 2 or 3 weeks in flight, one could also assume that neuromuscular deconditioning explains (at least in part) the general decrease in movement speed. Can the authors explain how to rule out this alternative interpretation? For instance, weaker muscles could account for slower movements within a classical time-effort trade-off (as more neural effort would be needed to generate a similar amount of muscle force, thereby suggesting a purposive slowing down of movement). Therefore, could the observed results (slowing down + more submovements) be explained by some neuromuscular deconditioning combined with a difficulty in coordinating multi-joint movements in weightlessness (due to a misestimation or Coriolis/centripetal torques) provide an alternative explanation for the results?
Response: Neuromuscular deconditioning is indeed a space or microgravity effect; thanks for bringing this up as we omitted the discussion of its possible contribution in the initial submission. However, muscle weakness is less for upper-limb muscles than for postural and lower-limb muscles (Tesch et al., 2005). The handgrip strength decreases 5% to 15% after several months (Moosavi et al., 2021); shoulder and elbow muscles atrophy, though not directly measured, was estimated to be minimal (Shen et al., 2017). The muscle weakness is unlikely to play a major role here since our reaching task involves small movements (~12cm) with joint torques of a magnitude of ~2N·m. Coriolis/centripetal torques does not affect the putative mass effect (as shown above simulations). The reviewer suggests that their poor coordination in microgravity might contribute to slowing down + more submovements. Poor coordination is an umbrella term for any motor control problems, and it can explain any microgravity effect. The feedforward control changes caused by mass underestimation can also be viewed as poor coordination. If we limit it as the coordination of the two joints or coordinating Coriolis/centripetal torques, we should expect to see some trajectory curvature changes in microgravity. However, we further analyzed our reaching trajectories and found no sign of curvature increase in our large collection of reaching movements. We probably have the largest dataset of reaching movements collected in microgravity thus far, given that we had 12 taikonauts and each of them performed about 480 to 840 reaching trials during their spaceflight. We believe the probability of Type II error is quite low here. We will include descriptive statistics of these new analyses in our revision.
Citation: Tesch, P. A., Berg, H. E., Bring, D., Evans, H. J., & LeBlanc, A. D. (2005). Effects of 17-day spaceflight on knee extensor muscle function and size. European journal of applied physiology, 93(4), 463-468.
Moosavi, D., Wolovsky, D., Depompeis, A., Uher, D., Lennington, D., Bodden, R., & Garber, C. E. (2021). The effects of spaceflight microgravity on the musculoskeletal system of humans and animals, with an emphasis on exercise as a countermeasure: A systematic scoping review. Physiological Research, 70(2), 119.
Shen, H., Lim, C., Schwartz, A. G., Andreev-Andrievskiy, A., Deymier, A. C., & Thomopoulos, S. (2017). Effects of spaceflight on the muscles of the murine shoulder. The FASEB Journal, 31(12), 5466.
(2) Modelling
a) The model description should be improved as it is currently a mix of discrete time and continuous time formulations. Moreover, an infinite-horizon cost function is used, but I thought the authors used a finite-horizon formulation with the prefixed duration provided by the movement utility maximization framework of Shadmehr et al. (Curr Biol, 2016). Furthermore, was the mass underestimation reflected both in the utility model and the optimal control model? If so, did the authors really compute the feedback control gain with the underestimated mass but simulate the system with the real mass? This is important because the mass appears both in the utility framework and in the LQ framework. Given the current interpretations, the feedforward command is assumed to be erroneous, and the feedback command would allow for motor corrections. Therefore, it could be clarified whether the feedback command also misestimates the mass or not, which may affect its efficiency. For instance, if both feedforward and feedback motor commands are based on wrong internal models (e.g., due to the mass underestimation), one may wonder how the astronauts would execute accurate goal-directed movements.
b) The model seems to be deterministic in its current form (no motor and sensory noise). Since the framework developed by Todorov (2005) is used, sensorimotor noise could have been readily considered. One could also assume that motor and sensory noise increase in microgravity, and the model could inform on how microgravity affects the number of submovements or endpoint variance due to sensorimotor noise changes, for instance.
c) Finally, how does the model distinguish the feedforward and feedback components of the motor command that are discussed in the paper, given that the model only yields a feedback control law? Does 'feedforward' refer to the motor plan here (i.e., the prefixed duration and arguably the precomputed feedback gain)?
We appreciate these very helpful suggestions about our model presentation. Indeed, our initial submission did not give detailed model descriptions in the main text, due to text limits for early submissions. We actually used a finite-horizon framework throughout, with a pre-specified duration derived from the utility model. In the revision, we will make that point clear, and we will also revise the Methods section to explicitly distinguish feedforward vs. feedback components, clarify the use of mass underestimation in both utility and control models, and update the equations accordingly.
(3) Brevity of movements and speed-accuracy trade-off
The tested movements are much faster (average duration approx. 350 ms) than similar self-paced movements that have been studied in other works (e.g., Wang et al., J Neurophysiology, 2016; Berret et al., PLOS Comp Biol, 2021, where movements can last about 900-1000 ms). This is consistent with the instructions to reach quickly and accurately, in line with a speed-accuracy trade-off. Was this instruction given to highlight the inertial effects related to the arm's anisotropy? One may however, wonder if the same results would hold for slower self-paced movements (are they also with reduced speed compared to Earth performance?). Moreover, a few other important questions might need to be addressed for completeness: how to ensure that astronauts did remember this instruction during the flight? (could the control group move faster because they better remembered the instruction?). Did the taikonauts perform the experiment on their own during the flight, or did one taikonaut assume the role of the experimenter?
Thanks for highlighting the brevity of movements in our experiment. Our intention in emphasizing fast movements is to rigorously test whether movement is indeed slowed down in microgravity. The observed prolonged movement duration clearly shows that microgravity affects people’s movement duration, even when they are pushed to move fast. The second reason for using fast movement is to highlight that feedforward control is affected in microgravity. Mass underestimation specifically affects feedforward control in the first place. Slow movement would inevitably have online corrections that might obscure the effect of mass underestimation. Note that movement slowing is not only observed in our speed-emphasized reaching task, but also in whole-arm pointing in other astronauts studies (Berger, 1997; Sangals, 1999), which have been quoted in our paper. We thus believe these findings are generalizable.
Regarding the consistency of instructions: all our experiments conducted in the Tiangong space station were monitored in real time by experimenters in the Control Center located in Beijing. The task instructions were presented on the initial display of the data acquisition application and ample reading time was allowed. In fact, all the pre-, in-, and post-flight test sessions were administered by the same group of experimenters with the same instruction. It is common that astronauts serve both as participants and experimenters at the same time. And, they were well trained for this type of role on the ground. Note that we had multiple pre-flight test sessions to familiarize them with the task. All these rigorous measures were in place to obtain high-quality data. We will include these experimental details and the rationales for emphasizing fast movements in the revision.
Citations:
Berger, M., Mescheriakov, S., Molokanova, E., Lechner-Steinleitner, S., Seguer, N., & Kozlovskaya, I. (1997). Pointing arm movements in short- and long-term spaceflights. Aviation, Space, and Environmental Medicine, 68(9), 781–787.
Sangals, J., Heuer, H., Manzey, D., & Lorenz, B. (1999). Changed visuomotor transformations during and after prolonged microgravity. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 129(3), 378–390.
(4) No learning effect
This is a surprising effect, as mentioned by the authors. Other studies conducted in microgravity have indeed revealed an optimal adaptation of motor patterns in a few dozen trials (e.g., Gaveau et al., eLife, 2016). Perhaps the difference is again related to single-joint versus multi-joint movements. This should be better discussed given the impact of this claim. Typically, why would a "sensory bias of bodily property" persist in microgravity and be a "fundamental constraint of the sensorimotor system"?
We believe the differences between our study and Gaveau et al.’s study cannot be simply attributed to single-joint versus multi-joint movements. One of the most salient differences is that their adaptation is about incorporating microgravity in control for minimizing effort, while our adaptation is about rightfully perceiving body mass. We will elaborate on possible reasons for the lack of learning in the light of this previous study.
We can elaborate on “sensory bias” and “fundamental constraint of the sensorimotor system”. If an inertial change is perceived (like an extra weight attached to the forearm, as in previous motor adaptation studies), people can adapt their reaching in tens of trials. In this case, sensory cues are veridical as they correctly inform about the inertial perturbation. However, in microgravity, reduced gravitational pull and proprioceptive inputs constantly inform the controller that the body mass is less than its actual magnitude. In other words, sensory cues in space are misleading for estimating body mass. The resulting sensory bias prevents the sensorimotor system from correctly adapt. Our statement was too brief in the initial submission; we will expand it in the revision.
Reviewer #3 (Public review):
Summary:
The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for an increased number of corrective submovements in weightlessness. They contend that this provides conclusive evidence to accept the hypothesis of an underestimation of body mass.
Strengths:
In my opinion, the study provides a valuable contribution, the theoretical aspects are well presented through simulations, the statistical analyses are meticulous, the applicable literature is comprehensively considered and cited, and the manuscript is well written.
Weaknesses:
Nevertheless, I am of the opinion that the interpretation of the observations leaves room for other possible explanations of the observed phenomenon, thus weakening the strength of the arguments.
First, I would like to point out an apparent (at least to me) divergence between the predictions and the observed data. Figures 1 and S1 show that the difference between predicted values for the 3 movement directions is almost linear, with predictions for 90º midway between predictions for 45º and 135º. The effective mass at 90º appears to be much closer to that of 45º than to that of 135º (Figure S1A). But the data shown in Figure 2 and Figure 3 indicate that movements at 90º and 135º are grouped together in terms of reaction time, movement duration, and peak acceleration, while both differ significantly from those values for movements at 45º.
Furthermore, in Figure 4, the change in peak acceleration time and relative time to peak acceleration between 1g and 0g appears to be greater for 90º than for 135º, which appears to me to be at least superficially in contradiction with the predictions from Figure S1. If the effective mass is the key parameter, wouldn't one expect as much difference between 90º and 135º as between 90º and 45º? It is true that peak speed (Figure 3B) and peak speed time (Figure 4B) appear to follow the ordering according to effective mass, but is there a mathematical explanation as to why the ordering is respected for velocity but not acceleration? These inconsistencies weaken the author's conclusions and should be addressed.
Indeed, the model predicts an almost equal separation between 45° and 90° and between 90° and 135°, while the data indicate that the spacing between 45° and 90° is much smaller than between 90° and 135°. We do not regard the divergence as evidence undermining our main conclusion since 1) the model is a simplification of the actual situation. For example, the model simulates an ideal case of moving a point mass (effective mass) without friction and without considering Coriolis and centripetal torques. 2) Our study does not make quantitative predictions of all the key kinematic measures; that will require model fitting and parameter estimation; instead, our study uses well-established (though simplified) models to qualitatively predict the overall behavioral pattern we would observe. For this purpose, our results are well in line with our expectations: though we did not find equal spacing between direction conditions, we do confirm that the key kinematic properties (Figure 2 and Figure 3 as questioned) follow the same ranking order of directions as predicted.
We thank the reviewer for pointing out the apparent discrepancy between model simulation and observed data. We will elaborate on the reasons behind the discrepancy in the revision.
Then, to strengthen the conclusions, I feel that the following points would need to be addressed:
(1) The authors model the movement control through equations that derive the input control variable in terms of the force acting on the hand and treat the arm as a second-order low-pass filter (Equation 13). Underestimation of the mass in the computation of a feedforward command would lead to a lower-than-expected displacement to that command. But it is not clear if and how the authors account for a potential modification of the time constants of the 2nd order system. The CNS does not effectuate movements with pure torque generators. Muscles have elastic properties that depend on their tonic excitation level, reflex feedback, and other parameters. Indeed, Fisk et al.* showed variations of movement characteristics consistent with lower muscle tone, lower bandwidth, and lower damping ratio in 0g compared to 1g. Could the variations in the response to the initial feedforward command be explained by a misrepresentation of the limbs' damping and natural frequency, leading to greater uncertainty about the consequences of the initial command? This would still be an argument for unadapted feedforward control of the movement, leading to the need for more corrective movements. But it would not necessarily reflect an underestimation of body mass.
*Fisk, J. O. H. N., Lackner, J. R., & DiZio, P. A. U. L. (1993). Gravitoinertial force level influences arm movement control. Journal of neurophysiology, 69(2), 504-511.
We agree that muscle properties, tonic excitation level, proprioception-mediated reflexes all contribute to reaching control. Fisk et al. (1993) study indeed showed that arm movement kinematics change, possibly owing to lower muscle tone and/or damping. However, reduced muscle damping and reduced spindle activity are more likely to affect feedback-based movements. Like in Fisk et al.’s study, people performed continuous arm movements with eyes closed; thus their movements largely relied on proprioceptive control. Our major findings are about the feedforward control, i.e., the reduced and “advanced” peak velocity/acceleration in discrete and ballistic reaching movements. Note that the peak acceleration happens as early as approximately 90-100ms into the movements, clearly showing that feedforward control is affected -- a different effect from Fisk et al’s findings. It is unlikely that people “advanced” their peak velocity/acceleration because they feel the need for more later corrective movements. Thus, underestimation of body mass remains the most plausible explanation.
(2) The movements were measured by having the subjects slide their finger on the surface of a touch screen. In weightlessness, the implications of this contact are expected to be quite different than those on the ground. In weightlessness, the taikonauts would need to actively press downward to maintain contact with the screen, while on Earth, gravity will do the work. The tangential forces that resist movement due to friction might therefore be different in 0g. This could be particularly relevant given that the effect of friction would interact with the limb in a direction-dependent fashion, given the anisotropy of the equivalent mass at the fingertip evoked by the authors. Is there some way to discount or control for these potential effects?
We agree that friction might play a role here, but normal interaction with a touch screen typically involves friction between 0.1 and 0.5N (e.g., Ayyildiz et al., 2018). We believe that the directional variation is even smaller than 0.1N. It is very small compared to the force used to accelerate the arm for the reaching movement (10-15N). Thus, friction anisotropy is unlikely to explain our data.
Citation: Ayyildiz M, Scaraggi M, Sirin O, Basdogan C, Persson BNJ. Contact mechanics between the human finger and a touchscreen under electroadhesion. Proc Natl Acad Sci U S A. 2018 Dec 11;115(50):12668-12673.
(3) The carefully crafted modelling of the limb neglects, nevertheless, the potential instability of the base of the arm. While the taikonauts were able to use their left arm to stabilize their bodies, it is not clear to what extent active stabilization with the contralateral limb can reproduce the stability of the human body seated in a chair in Earth gravity. Unintended motion of the shoulder could account for a smaller-than-expected displacement of the hand in response to the initial feedforward command and/or greater propensity for errors (with a greater need for corrective submovements) in 0g. The direction of movement with respect to the anchoring point could lead to the dependence of the observed effects on movement direction. Could this be tested in some way, e.g., by testing subjects on the ground while standing on an unstable base of support or sitting on a swing, with the same requirement to stabilize the torso using the contralateral arm?
Body stabilization is always a challenge for human movement studies in space. We minimized its potential confounding effects by using left-hand grasping and foot straps for postural support throughout the experiment. We would argue shoulder stability is an unlikely explanation because unexpected shoulder instability should not affect the feedforward (early) part of the ballistic reaching movement: the reduced peak acceleration and its early peak were observed at about 90-100ms after movement initiation. This effect is too early to be explained by an expected stability issue.
The arguments for an underestimation of body mass would be strengthened if the authors could address these points in some way.
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