Decision letter | A quantitative framework for whole-body coordination reveals specific deficits in freely walking ataxic mice

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A quantitative framework for whole-body coordination reveals specific deficits in freely walking ataxic mice

Decision letter

Affiliation details

Champalimaud Foundation, Portugal
Indira M Raman, Reviewing editor, Northwestern University, United States

eLife posts the editorial decision letter and author response on a selection of the published articles (subject to the approval of the authors). An edited version of the letter sent to the authors after peer review is shown, indicating the substantive concerns or comments; minor concerns are not usually shown. Reviewers have the opportunity to discuss the decision before the letter is sent (see review process). Similarly, the author response typically shows only responses to the major concerns raised by the reviewers.

[Editors’ note: this article was originally rejected after discussions between the reviewers, but the authors were invited to resubmit after an appeal against the decision.]

Thank you for choosing to send your work entitled "A quantitative framework for whole-body coordination reveals specific deficits in freely walking ataxic mice" for consideration at eLife. Your full submission has been evaluated by Eve Marder (Senior Editor) and three peer reviewers, one of whom is a member of our Board of Reviewing Editors, and the decision was reached after discussions between the reviewers. Based on our discussions and the individual reviews below, we regret to inform you that your work will not be considered further for publication in eLife.

All the reviewers find that the study is very interesting and that the method presented for monitoring locomotion in relation to the cerebellar motor function and other motor functions is potentially strong. There are, however, concerns whether the automation procedure is making correct assessments of the locomotor parameters, that gaits are not taken into accounts in the description, that there is a lack of statistical evaluation of intra-limb coordination, and that the differences in full body movements may not account completely for the phenotype. To meet these concerns would require substantial reanalysis of the data and reconsidering the main conclusions of the study. Even with a new analysis there is a feeling that the results presented will mainly be a technical advance rather than a conceptual advance for cerebellar motor function or the locomotor field at large. The reasons for this are that there already are cerebellar specific mutants that have been analyzed in similar ways and that the locomotor data in wild-type are confirmative and lacking gait parameters. For these reasons the manuscript as presently configured is not suitable as a regular paper in eLife. The details of the concerns and suggestions for improvements are detailed in the attached review reports.

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Reviewer #1:

The paper of Machado et al. introduces a camera-based motion capture system for the analysis of walking movements in the mouse. The heart of the system is machine learning operating on resampled images of high speed cameras for mice walking in a glass corridor. To illustrate its applicability, the paper compares the walking movements of wildtype and Purkinje cell degeneration (pcd) mice.

In general, for a paper introducing a novel analysis tool, I think it must be assessed whether the method provides measurements of highly useful parameters, with high explanatory value, that goes well beyond what has been attainable before. For instance, there was a very recent paper by Hoogland et al. (2015, Curr Biol.) introducing a method that is closely related to the present one (camera-based, measuring the paw positions as well as the whole body angle) and other measurement systems applied to locomotion exist in abundance, typically published alongside main scientific findings (for example, Kiehn 2013). To be clear, I think the authors have made a very careful and high-quality job, but I am doubtful that the advances provided here represent a major leap rather than a minor incremental change to the state-of-the art.

The paper promises to demonstrate a tool that can be used to monitor whole body coordination and 3D limb kinematics. But I find that the analysis of the whole body coordination boils down to computing the angle of the mid-body axis by utilizing the recorded position of the nose and tail, which is not particularly useful from a neuroscience perspective, as the angle is determined by the interplay of a very large number of muscles that could potentially change in different ways in a large number of deficits. In addition, data on the whole body movement is already provided in the solution of Hoogland et al. (2015). I also find that the stated monitoring of the 3D limb kinematics boils down to a monitoring of the 3D spatial position of the paw. But each position could theoretically be accomplished by many different configurations in the muscles of the limb, and the latter is the type of information that one would need to obtain a useful tool. Figure 3H seem at first glance to indicate that there is indeed some information on the limb joints – however, when I read the paper and the Methods, there are no indications that the joints are actually measured. Hence, I assume that the joint angles are computed out of the 3D paw data, which is problematic. First, if these angles are not measured but computed, the authors must explain where the data in their Figure 3H comes from. For the paper as a whole, this is a major problem since the main applicability of this setup would be if the user could actually track joint angles. Relying on computational models to deduce the 3D limb kinematics is very different from actually measuring it, and reduces the value of this method.

There are also some statements made about the analysis of pcd mice, claiming that this analysis supports that the cerebellum provides an internal model. But there is no evidence here that the cerebellum provides an internal model of any kind. What is seen here is only that block of the normal information processing pathway of various motor systems perturbs the capability of the central nervous system to rely on internal models. On the other hand, all biological motor control is feed-forward in nature, as it needs to deal with long delays, and feed-forward control can be solved only by using internal models. So the only thing learned from this study is that the normal function of the central nervous system in locomotion is dependent on a normally operating cerebellum. The internal models could be generated elsewhere, with the perturbed Purkinje cells destroying the capacity of the system as a whole by removing an otherwise permissive signal to any other system hypothetically responsible for generating/providing the internal model.

Reviewer #2:

The authors developed a very nice method to quantify motor performance during free locomotion in mice. They show that in cerebellar ataxia coordination rather than individual movements are affected. This is an elegant and thorough study, but a number of points require attention:

1) The authors used Purkinje cell degeneration (pcd) mice to test for cerebellar ataxia. Pcd mice start to lose their Purkinje cells during early adulthood – however, later on, other defects appear e.g. the loss of thalamic neurons after P50 and subsequently more widespread neurodegeneration (see Fernandez-Gonzalez, Science 2002 and references cited therein). The use of pcd mice at ages varying between p41 and p154, therefore, is expected to result in heterogeneous stages of neurodegeneration. This is not addressed experimentally. Therefore, the authors have to present their data separately for different age groups – especially for mice younger than p50 (no extra-cerebellar neurodegeneration expected) and older (including thalamic and maybe even more neurodegeneration).

2) Dependence of gait parameters of individual limbs on weight and speed.

The authors provide an elegant analysis of the correlations between weight, speed and specific parameters of single-limb movements. As expected, many (if not all) parameters depend on speed. The effect of weight, however, is more prominent in some parameters than in others (e.g. compare Figures 2C and 2E). The authors conclude that, given body weight and speed, they can make reasonably accurate predictions for single-limb movement parameters. However, the authors do not directly disentangle the impact of body weight vs. speed for each parameter. In other words, how much of the variation is explained by either one? Were there also gender- and/or age-related differences, or were these fully explained by variations in body weight (see Figure 2–figure supplement 2)?

3) Impact of speed for analyzing individual limb gait parameters in pcd mice.

The authors show in Figure 3 that pcd mice make smaller, slower steps than wildtype littermates. They argue that, despite the actual values being different from controls, individual limb parameters are largely in line with those from control mice at similar speed and with similar weight. This is an important finding, but it would be informative to show the impact of body weight alone. In other words: it seems that the (on-axis) trajectory of single limbs is not really different between pcd and control mice, but what about the timing?

In addition, the off-axis movements do seem to be affected, but it is not fully clear to me to what extent corrections for body size and speed have been applied here. In the Discussion, I feel that a better balance between the preserved on-axis parameters and the affected off-axis parameters in the discussion would be warranted.

4) I feel that the remark "the failure of existing systems to quantitatively capture gait ataxia" (in the subsection “Interlimb and whole-body coordination are specifically impaired in pcd”) is a bit too strong and does not acknowledge the merits of previous quantifications (e.g. Erasmus Ladder and transparent disk treadmill, which both can also quantify interlimb coordination). Although the authors show that the trajectory of individual limbs is not grossly affected in pcd mice, the speed is (Figure 3A). And the speed is in turn related to the velocity of single limbs (Figure 2E). Thus, without neglecting the importance of the current study, stating that previous studies were not able to quantitate features of gait ataxia or interlimb coordination is in my opinion too strong. For possibilities of transparent disk treadmill to study interlimb coordination, please refer to Hoogland et al., 2015, Current Biol). Here, the level of ataxia in tottering is not only quantified (including interlimb coordination), but also related to the level of complex spike synchrony. Please discuss this neurobiological mechanism upfront as well as the advantages and disadvantages of the technical possibilities of this disk treadmill system with respect to the current locomouse technology.

5) The authors show (in Figure 5) that tail lateral movements of control mice have a sinusoidal appearance, related to the stride phase. This movement is largely exaggerated in pcd mice. Whereas the lateral movements in control mice are coupled to the stride phase, in the pcd mice there seems to be more of a coupling to the time. The tail movements could be either a compensatory mechanism to counteract imbalance due to improper limb control or they could be affected themselves, contributing to further imbalance. Currently, the variations in tail movements are not really taken into account. Could the authors provide a more solid analysis showing whether tail movements are compensatory or affected by themselves?

6) In the Discussion, the authors mention that previous studies lack the fine-grained detail used in this work and therefore focused on "markers for global motor dysfunction [but] they lack specificity" (subsection “A quantitative framework for locomotor coordination”). Now that the authors have developed such a beautiful system: what is the effect of cerebellar ataxia? How does this separate from other motor dysfunctions (e.g. muscular dystrophy)?

7) In Figure 4, the authors showed the step-cycle for four limb movements by indicating the stance onset for each paw (Figure 4A) and the support pattern (Figure 4C). However, I find it still difficult to understand the phase relationship between limbs with regard to swing and stance phase. For example, to what extent does the onset of the swing phase of the forelimb occur during the swing or stance phase of the ipsilateral hindlimb? In order to have a better interpretation of inter-limb coordination, it might be worthwhile to add an additional figure with swing and stance phase indicated for each individual limb.

Reviewer #3:

The authors of this study have developed an automated kinematic analysis of locomotion in mice. They use it for locomotor analysis in freely moving wild-type mice. A detailed description of locomotor parameters allowed them to create a mathematical model to predict most of the parameters knowing just the walking speed and the body size of the animal. They extend this analysis to a mouse model for Purkinje cell degeneration (pcd). They conclude that the traditional locomotor parameters (stride length, cadence, intra-limb coordination) and forward trajectories are not different in wild-type mice and pcd mice. In contrast they conclude that the whole-body coordination is specifically impaired in pcd mice. Furthermore, a specific description of nose and tail oscillations in pcd mice were modeled as passive consequences of the forward motion of the hindlimbs. The main conclusions from the study are: a) only by studying whole-body coordination will it be possible to reveal the ataxic locomotor phenotype, and b) the observed locomotor changes are consistent with the hypothesis that the cerebellum provides a forward model for motor control. Although I find the study of great interest there are a number of issues that are problematic for the interpretation of the data. The authors will have to address these issues to avoid making incorrect statements about the findings and the method used.

1) The authors make a big deal out of using machine learning as an 'objective' way of measuring locomotor parameters. But there seems to be a lot of noise in the detection. This is seen in Figure 1E. Where is the level set for step onset and offset? Figure 2A is an even stronger case. At very low speed (<0.4) the stride length varies with a factor of 10 from 1 cm to 10 cm. 10 cm long stride lengths are not common at these speeds in mice. It must be a detection mistake. Also there are many values with very low stride lengths spread over all speeds. One would like to know how much irrelevant noise that the automated procedure introduces for example by showing traces from the low speed locomotion with 1 cm and 10 cm stride lengths. Everything in Figure 2 is known from many previous studies of rodent locomotion – so there is nothing new about it except that the authors have analyzed a large amount of steps.

2) The authors make a point out of not seeing any intralimb differences between wild-type and pcd mice. Looking at Figure 3 this referee is not convinced, and it seems that this statement that is likely to be wrong. There seems to be clear differences in almost all parameters. Statistical tests will be needed to support the claims.

3) A main conclusion is that the interlimb coordination changes from wild-type to pcd mice. More specifically from a trot to a walk pattern. Walking and trotting patterns have been described for tetrapods to be distinct gaits by many different studies. They are visible at different speeds of locomotion. In your experiments wild-type mice exhibited trot as unique gait used at all speeds, even at the lowest ones when the speed is below 0.2 m/s and the support limbs are three or four (Figure 4C and 4D). In contrast the pcd mutant mice exhibit only walk, reaching a maximum speed of 0.25 m/s. What is odd about this difference is that walk is clearly found in wild-type mice by all others than these investigators. I believe that it is present even in the present study but that it has been missed (how can you have trot with 3 or 4 limb on the ground?). Since the pcd mice locomote slower than the wild-type mice the change in coordination could simply be caused by a change in gait patterns that is speed dependent. It is known for many animal models (mouse as well) that the inter-limb and whole body coordination change when the animal uses different gaits. At the mechanical level different models have been used to explain the different body coordination of walking and trotting gaits (Mechanical work in terrestrial locomotion: two basic mechanisms for minimizing energy expenditure, Cavagna et al., 1977, American Journal of Physiology). Thus, most of the differences you describe between wild-type and mutant mice could be due just to the comparison of mice using two different gaits that clearly rely on different inter-limb and whole body coordination (e.g. Figure 4A, 4C, 6A and 6B). Indeed you have clear indications that walk is also expressed in wild-type mice at low speed (Figure 4A and 4C). The data should be reanalyzed to address this issue. I am convinced that if the data are reanalysed, walk will show up in wild-type mice as well. This will dramatically change the conclusion of the story.

4) The discussion about the superiority of the present method to others needs to be toned down. The general statement that the automated analysis described in the study provides a robust way for locomotor analysis avoiding "false positive findings that permeate the mouse locomotor literature" is not true and likely to offend the locomotor field at large. I strongly recommend that the authors consider gaits (walk, trot, gallop and bound) in their analysis. Since you have done an incredible work using size-matched controls, it will be helpful if the difference between wild-type and pcd mutant mice account just for the degeneration of the Purkinje cells and not for errors due to a comparison between mice using two different gaits.

5) To my knowledge pcd mice showed not only a degeneration of the Purkinje cells but also the slower degeneration of the photoreceptor cells of the retina and mitral cells of the olfactory bulb. Since you have used animals between 41 and 154 days old, could it be that a shorter range of speed is the result of a disorganization of the visual system and not only due to an impairment of the neural control of the locomotion? They walk slower because they are half blind?

[Editors’ note: what now follows is the decision letter after the authors submitted for further consideration.]

Thank you for submitting your work entitled "A quantitative framework for whole-body coordination reveals specific deficits in freely walking ataxic mice" for peer review at eLife. Your submission has been favorably evaluated by Eve Marder (Senior Editor), a Reviewing Editor, and three reviewers.

The reviewers have discussed the reviews with one another and the Reviewing Editor has drafted this decision to help you prepare a revised submission.

The reviewers all appreciated the fact that the novel LocoMouse tool permits automated analysis with high resolution of locomotion of freely walking mice, and they judged that this method has the potential to be of value to the field. They provide a number of comments for strengthening the manuscript, which are included below. These comments center on the being more explicit about the limits of the work, its interpretation (especially regarding the mutants), and comparison to other studies, providing more information about certain analyses, and addressing some points for clarity of presentation and communication. Specifically:

1) Toning down the claims about the superiority and power of the new method, perhaps providing a more explicit comparison to commercial packages.

2) Toning down the claims about providing direct evidence for forward models, perhaps simply by shifting these ideas to the Discussion.

3) Limiting the claims about changes and the lack of changes in the mutant, perhaps by focusing on the idea that one kinematic measure was preserved while others (interlimb and intralimb) were not.

4) Providing a better description of the construction of the passive model, and (if feasible) providing a physical model (or explaining why this was not done).

5) Addressing the point either experimentally or with clarification of the (apparently) very low N (=3) for the pcd mice.

6) Improving presentation of the results/figures/sequence of calling figures, as indicated in the reviews.

Reviewer #1:

1) The authors emphasize in several places that 'traditional' measures of kinematics are unimpaired in mutants. I found this to be overly-simplistic, at least based on the results presented here. As I understand it, the main consistency is in the x-axis forward paw motion, while there are changes in vertical and mediolateral paw motion and in joint angles. Changes in vertical paw trajectory and joint angles are hardly 'non-traditional', 'complex', or even '3D' and all measures are definitely 'individual-limb'. This point is made several times in the text (see points below) and seems unwarranted. I'm not saying the results aren't interesting, nor do I think that these conclusions are necessary for the impact of the paper – I just don't think that this conclusion as stated is supported.

2) On a similar point, it's not clear to me that any of their measures are really looking at within-limb coordination, at least as this is usually considered. Most of the measures relate to paw movement, whereas traditionally issues of coordination (e.g. in studies examining the role of the cerebellum, as cited in the paper) consider interactions between joints. Yet these analyses really aren't done here. They show that joint angles are apparently different in the animals, but these are for single joints as opposed to joint angle relationships (and what those angles are is unclear, see below). I don't think that the results shown here rule out a possible deficit in traditional, within-limb coordination. I think this is mainly an issue of presentation, however, rather than one of substance. As stated above, I don't think the impact of the paper relies on this conclusion and it could be made more precise without loss of significance.

3) I potentially like the analysis of nose and tail passive movements very much, but I did have a few issues with it. First, although the results are consistent with a role of the cerebellum in predictive control based on forward models, they're not really a direct demonstration thereof. A more direct demonstration might involve examining adaptations to perturbations, e.g. adding a weight to the tail and seeing that initially control animals look like mutants but then learn to predict and compensate for this, whereas mutants never do so. Also, could the results simply be interpreted as one of a limited capacity for motor control? e.g. mutants have limited capacity for producing locomotion and expend most of it on x-axis movement of the paw since it's critical for task performance, whereas other aspects of behavior are allowed to vary? I appreciate the authors are careful on this point to say that the results are 'consistent' with this idea, but alternative explanations might be considered more directly.

4) For the nose/tail passive analysis, I originally thought that this was an actual physical model, rather than the geometric model used here. It seems clear that a physical model is the better way to do this. Why wasn't it done? The geometric model, with its assumptions of lags taken from data which is actually observed, seems more indirect and therefore less compelling. Finally, as I understand it (and I might have missed it), this analysis was only done for the mutants. It would be very good to have done the same analysis for the control animals and show that the tail/nose movements are inconsistent with passive movement, e.g. it could have been that the movement of the pelvic girdle was different in controls, leading to less tail movement (even though the hindlimbs are in alternation for both controls and mutants).

Reviewer #2:

The paper by Machado et al. examines gait patterns in wildtype and Purkinje cell degeneration (pcd) mice using a novel system for tracking locomotor kinematics in freely walking mice. The authors conclude that the individual limb kinematics of pcd mice are normal when the weight and the walking speed of the mice are taken into account. In contrast, pcd mice have impaired coordination of movements across joints, limbs and body. These results are interpreted as evidence that the cerebellum provides a forward model. This is a strong paper. I commend the authors for wrestling with a complex dataset and extracting from it a number of thought-provoking findings. I personally found many of the results exciting, but I must admit that I'm not an expert in the field of locomotion or ataxia. It was not always clear if a particular result in the paper was a major advance or just confirmation of something we already knew. For this reason, I think that it's important for the authors to clarify and emphasize the significance of their results throughout the text. I've given two examples below:

1) It is remarkable that in wildtype mice, one can account for upwards of 80% of the variance in kinematic parameters like stride length, swing velocity and cadence, simply by taking into account the walking speed and the weight of the mouse. Is this a new approach? In their rebuttal, the authors mention that the Cendelin et al. (2010) paper found that all the gait differences between lurcher and control mice disappeared when they corrected for walking speed. Did Cendelin et al. make the correction using a similar modeling approach?

2) One of the main findings is that individual limb movements of pcd mice are relatively spared (when weight and walking speed are taken into account), whereas interlimb coordination is impaired. It is not clear how much of this we already knew. For example, in the subsection “Front-hind Interlimb coordination is specifically impaired in pcd”, the authors mention that previous studies in ataxic mice have failed to detect any impairments in the kinematic parameters of individual limbs. Did those studies not examine interlimb coordination as well? If the authors are the first to show that mice with cerebellar deficits have a specific impairment in locomotor coordination but not in movement of individual limbs, this is a big deal.

Additional recommendations to help make an already strong paper even stronger:

3) Drop the emphasis on forward models. The authors argue that the deficits they've uncovered point to a lack of a forward model in pcd mice. Although I found some of the evidence presented intriguing (for example the analysis of tail movements), it is far from conclusive. Furthermore, it is difficult to reconcile the normal individual limb kinematics with a faulty forward model – individual limbs are controlled by multiple agonist/antagonist muscles whose coordination requires well-calibrated forward models. I think the authors can still interpret their results in the context of forward/inverse models, but I strongly recommend that they save this interpretation for the Discussion, tone it down a bit and address the limitations. The paper would be stronger if the second paragraph of the Introduction is rewritten to highlight the main questions to be addressed in the paper, instead of offering to resolve controversies about forward vs inverse cerebellar models.

4) Analysis of variability: All the analyses are based on average data. For example, Figure 3B-E shows that there is no difference in the individual limb kinematics of pcd mice and sized-matched controls. But this is done only for the average kinematic values. Is it not possible that pcd mice might show increased trial-to-trial variability in their movements relative to sized-matched controls? How would such a finding change the authors' conclusions?

Reviewer #3:

The authors developed a machine learning algorithm to track the individual limbs as well as the nose and tail of mice in 3D during natural, voluntary locomotion. They provide a very detailed analysis of locomotion parameters in control and ataxic Purkinje cell degeneration (pcd) mice, revealing that individual limb kinematics in pcd mice are not different from control mice when accounting for the mouse's weight and speed, but that pcd mice present multi-joint and inter-limb-coordination deficits. The study has been carefully conducted and provides new and useful tools for measuring and analyzing specific features of locomotion and ataxia with unprecedented accuracy.

1) The construction of the "passive model" (Figure 5) is unclear. For example, does this model take into account the mass of the tail? Please describe in more detail how the passive prediction is calculated.

2) The authors contrast the forward model with an inverse kinematic model in the Introduction. What do they think the inverse kinematic model would predict and how does this contrast with their findings?

[Editors' note: further revisions were requested prior to acceptance, as described below.]

Thank you for resubmitting your work entitled "A quantitative framework for whole-body coordination reveals specific deficits in freely walking ataxic mice" for further consideration at eLife. Your revised article has been favorably evaluated by Eve Marder (Senior Editor), a Reviewing Editor, and three reviewers. The manuscript has been greatly improved and the revision was met with enthusiasm. There are only a few remaining issues that need to be addressed before acceptance, as outlined below:

In particular, the manual joint-angle analysis shown in Figure 3H seems limited by the single animal in each condition, and discussion among reviewers and editors led to the consensus that it could simply be dropped without major impact on the manuscript. We therefore recommend cutting this one measurement and illustration. Alternatively, if there is some reason why a single animal in each category is of value, please justify the experiment clearly. This point is explained further below.

In the subsection “Individual limb parameters”, the description makes it seem like one pcd animal and one control were used for this analysis. If so, this seems very questionable and underpowered. I'd be willing to bet that, with enough n, it would be possible to find a significant difference between two different weight matched controls. I'm not sure how the stats behave in this situation, but it's not clear to me how mixed models would be able to partition variance due to random effects (individual subjects) from the fixed effects (mutation) if there were only one animal in each group. It seems that for other comparisons with weight matched controls much larger N's are used, whereas this analysis is limited because of the need to hand mark frames. It might be easiest to simply drop this joint angle analysis – I don't think its omission would change the impact of the paper. Also, shouldn't it be ‘knee, heel, toe’? And here it's stated that the angle of the foot and arm relative to the ground are quantified – I might have missed it, but I wasn't sure where that was reported in the Results.

DOI: http://dx.doi.org/10.7554/eLife.07892.021