A stochastic neuronal model predicts random search behaviors at multiple spatial scales in C. elegans

Essential revisions: 1) Results, second paragraph: The claim that this study represents "a 10-fold improvement over previously published tracking systems" seems to be a stretch. In some sense, centerline-tracking experiments operate at a much finer resolution than tracking a single dot on a worm, with papers such as Brown, et al.,

PNAS (2013) tracking many more worms with more detail and higher resolution. I agree that the authors appear to have done a fine job at spot tracking, but we don't believe that they have a claim to novelty here.

None of the published centerline tracking papers cite the spatial resolution of the method, so the argument against our claim to novelty seems to be unfounded. However, we are willing to limit this claim to measurement oftangential velocityand have adjusted the manuscript accordingly (Introduction, last paragraph). Note that our demonstration of higher velocity resolution than other methods is significant because it provides with an explanation for why we obtained a lower value of mean dwell time in the forward state than previous studies (subsection “Wild type locomotion”, first paragraph).

In preparing this manuscript, we reviewed all C. elegans centerline tracking papers, including Brown et al., PNAS (2013) cited above, and the complete set of the Stephens/Bialek papers. As far as we can tell, none of them presents an explicit statement of spatial resolution or the information needed to compute spatial resolution (pixel size on the camera chip, and overall optical magnification), nor do any of them show data from motionless worms (Figure 1—figure supplement 1), which would at least yield an estimate of resolution in the limiting case of no worm movement. Thus, we find no basis in the literature for the referee’s statement that centerline methods have higher spatial resolution.

Whereas we agree that centerline tracking is superior when the worm’s posture is the key datum, here our focus is on tangential velocity, for which centerline tracking is not the most direct measure possible. As we noted in the main text of the paper (Results, end of first paragraph), the centerline method computes tangential velocity by following virtual points rather than physical marks on the body. This is done by fitting a spline to the worm’s boundary, breaking the spline into a fixed number of segments, and computing the velocity of segment endpoints. The spline method is inaccurate because the tail of the worm, being faint, is differentially resolved from frame to frame. As a result, the length of the spline, and thus the distance between segment endpoints varies significantly (e.g. Figure 1B of Karbowski et al., 2008; Figure 2 of Cronin et al., 2005 where centerline head and tail are chopped off and misaligned in comparison to real worm; Figure 1 panel B of Karbowski et al. 2006). Thus the spline method adds segmentation noise to the velocity measurements. In contrast, the spot tracking method follows a sharply defined, high-contrast mark that is essentially unaffected by image segmentation noise. Our literature review revealed only one other C. elegans tracking paper that cites the accuracy of spot of tracking. Here the tracking object is a fluorescent neuron and the resolution is given as 5 µm (Guo, 2009). This paper is the basis of our statement that our method affords a 10-fold improvement, as the stage encoders we used had a resolution of 0.5 µm. Our dead worm experiments verify that encoder precision is the limiting factor in the overall spatial resolution.

2) The authors should address the Stephens et al. (2011) paper in a different manner than they do here (particularly in the Discussion section, fifth paragraph).

We agree with the reviewers’ main points (see details below): (i) Worm's do not slip under our conditions, nor under those of Stephens et al. (ii) Thrust can be produced when phase velocity is zero. (iii) Midpoint tracking is a useful simplified description of the system. The main force of this critique is thus the request to distinguish our work from Stephens' in a different manner – by using the thought experiment in which phase velocity is substituted for tangential velocity when fitting and analyzing our Markov model. Would the two definitions of velocity yield the same results? We have now adopted this excellent suggestion in the Discussion (fourth paragraph).

To begin with, the statement that the "mathematical relationship between tangential velocity and phase velocity (so defined) has not been delineated, but is likely to be complex" largely due to slippage between the worm and the substrate seems an overstatement.

We have removed the quoted statement, and the discussion of slippage. (As point of fact, however, we did not say that the complexity of the relationship between tangential and phase velocities is due to the possibility of slippage. Rather, this complexity is due the fact that tangential velocity in the worm is fully determined by thrust, and the higher order components of the worm’s shape, which are capable of generating thrust, are ignored by definition in computing phase velocity.)

If the paper is interested in modeling the animal's neural control of motion, then shouldn't the model be more concerned about the dynamics actually being controlled – in this case, the postural dynamics?

We could just as easily argue that from the perspective of the command neurons, what is being controlled is the presence or absence of thrust, and its direction.

And while it is indeed theoretically possible to produce thrust without advancing the phase, the collection of papers from Stephens et al.show that the worms' dynamics lie almost entirely on a manifold of remarkably small dimension, showing that these types of potential postural changes occur only rarely.

Shape components 3 and 4 account for approximately 30% of the shape variance (Stephens et al., 2008, Figure 2B), so it is hard to see how they can be characterized as “rare.” Moreover, these two components meet necessary and sufficient conditions for generating thrust: a gradient of curvature along the worm’s centerline (Gray 1946; Gray 1953; Gray 1964); Thus there are non-rare components that are generating thrust.

Moreover, the authors themselves admit (in the subsection “

Wild type locomotion”, fifth paragraph) that "on an agar surface, the worm moves without slipping."

Yes, we do believe that slip is generally minimal. Now, we no longer use slippage as a means of illustrating the differences between the two methods of analyzing behavior.

In addition, the authors state that the Stephens et al.(2010) paper shows that postural modeling does not accurately model the worm when its center of mass trajectory follows an arc.

We are not saying that postural modeling – defined in terms of all shape components – is inaccurate; we are actually making a much more restricted assertion. We are merely saying that phase velocity, because it is based on components 1 and 2 alone, is not necessarily an accurate measure of tangential velocity. In particular, this mismatch is accentuated in arcs, including omega turns, where other thrust producing shape components are strongly engaged.

In fact, the cited paper shows the necessity of looking at arcing trajectories between reorientation events and not just using a run-and-tumble analogy from bacteria, showing that shape-space dynamics form a predictive relationship with foraging trajectories.

We agree with this point. The work by Iino and colleagues (Iino, 2009) has shown that spatial orientation behavior is the product of two mechanisms: run-and-tumble (klinokinesis) and weathervaning (klinotaxis). However, klinotaxis, being deterministic rather than random, is outside the scope of the paper. We now make it clear that the type of chemotaxis modeled here is “random-walk chemotaxis” (Discussion, first paragraph).

All this being said, we are not disputing the authors' modeling choice of only using the midpoint of the worm's body. We have no arguments that there is utility in using a simplified description of a system to gain quantitative insight, but we want to see the authors distinguish themselves from the Stephens (2011) paper differently, focusing instead on the fundamental difference of modeling via a hidden Markov model instead of fitting parameters in a set of deterministic/stochastic differential equations. The choice of measuring Euclidean velocity instead of phase velocity is a modeling choice. Put another way, if someone with comparable amounts of shape-space data were to fit a hidden Markov model of your form to their data using phase velocity instead of velocity, would they likely obtain the same results?

We would not get the same results (rate constants, weights, etc.) because thrust (hence movement) can be generated even when phase velocity is zero (see point (ii) of agreement above). Thus some of the pauses identified phase velocity, would not be identified as pauses by tangential velocity because the worm is still moving. Would all pauses in tangential velocity be detected by the phase velocity method? We speculate that this is mainly true, because when tangential velocity is zero, net thrust is zero, so none of the shape components are generating thrust, including components 1 and 2.

3) In Figure 4, could the result that there is no postural stereotypy entering into state $\mathrm{X}$ be the result of an over-zealous "pause" caller. Specifically, this model calls many more things pauses than other approaches because of the nature of the sub-frame-resolution hidden Markov fit. What do these plots look like if only the longest visits to the $\mathrm{X}$ states are included?

We tested for this possibility by reanalyzing the average posture at $\mathrm{FX}$ transitions after eliminating all but long pauses, and found a similar lack of postural preference at $\mathrm{FX}$ transitions. This result held for any minimum pause duration up to 2 s; longer dwells in state $\mathrm{X}$ were too rare to analyze. We have added this result to the text (subsection “Wild type locomotion”, last paragraph).

4) Is there any evidence that the time scales of neural activity in C. elegans' motor neurons can be as short as the pause states being predicted? Although the model is supposed to be an abstraction of what's occurring in the worm's nervous system, one should expect to predict reasonable numbers for this nonetheless.

To our knowledge, there is only one report of voltage recordings from body wall muscle motor neurons in C. elegans (Liu, 2014). Interestingly, these motor neurons, which happen to be in the pool of reverse motor neurons, exhibit distinct up and down states. Theoretically, the down states could be pauses of the state-$\mathrm{X}$ type in our model when they coincide with down states in forward motor neurons, whereas the up states could be pauses of the state-$\mathrm{Y}$ type in our model when they coincide with up states in forward motor neurons. Unfortunately, no simultaneous recordings of reverse and forward neurons were made so it is impossible to determine the duration of possible pause states. The Liu paper is now referenced in the third paragraph of the subsection “The Stochastic Switch Model”.

5) In the first paragraph of the subsection “Wild type locomotion” the authors claim that their "tracking system is capable of revealing briefer visits" to the pause state and that this is the reason why their measured dwell time is much shorter than previously measured. Again, we are not yet convinced that this method is much more accurate than the posture tracking used in Stephens et al.

(2011) to measure the forward dwell time. The Stephens paper, however, uses a slightly different definition of the dwell time, using cessation of the forward phase velocity instead. Although the paper here does not measure phase velocity, they could measure the dwell time between visits to the reversal state (i.e. ignoring $\mathrm{F}$->$\mathrm{P}$->$\mathrm{F}$ type transitions). What happens if this definition is used? Does the same result emerge?

We have added this calculation to the text. The resulting mean dwell time in the forward state using the standard fixed velocity threshold of 0.5 mm/s and ignoring $\mathrm{FPF}$ transitions was 9.13 ± 0.15 s. which matches the value obtained by others using the same threshold (8.98 ± 0.57 s) (Rakowski, 2013). This result has been added to the text (subsection “Wild type locomotion”, first paragraph).

6) A more general comment is that we would like to understand more what type of neural activity the authors would predict based on their model, connectome data, and polarity results from papers such as Rakowski (2013) despite imaging in a freely-behaving worm being well outside of the scope of this paper (although not nearly as impossible as the authors seem to suggest in the Discussion section). If this experiment were performed, what is the most likely neural instantiation of this model that is consistent with the current literature? The strength of this model is that it makes an attempt at getting at how this circuit may actually function. Accordingly, if possible, a concrete prediction or predictions to this end would greatly increase the value of this paper to researchers and could guide experimentalists performing imaging in freely-behaving animals in their measurements and analysis.

This is a great idea! We have now included a paragraph of predictions in the Discussion (fifth paragraph).

[Editors’ note: the author responses to the previous round of peer review follow.]

Consensus review:

The authors present a kinematic analysis of random local search behavior in C. elegans. The then use a Hidden Markov Model to quantitatively model such searches based their kinematic analyses. They then identify this HMM with known aspects of the worm connectome to understand the neural implementation of switches between different behavioral states. In particular, the model contains two populations of neurons, each controlling either forward or reverse locomotion, with the overall network resulting in four possible behaviors: forward, reverse, and two pause states. They perform a maximum likelihood fit of the model to measured time series, making predictions about the effect of neural ablations, the sign and strength of synaptic connections, effects of perturbations to membrane potentials. Moreover, they phenomenologically model a potential underlying neural mechanism for different search modalities. The subject matter of the paper is definitely one of broad interest, and if the model is correct it would provide us with a substantive understanding into the neural implementation of the forward/pause/reversal/pause(?) dynamics it would be a major contribution. However, the reviewers are not fully convinced that the model is the simplest possible explanation of the animal's behavior and that the

authors have shown that a clear connection can be drawn to neural correlates. Enthusiasm for the subject matter and the potential neural correlates vs. concerns about the appropriateness of the approach and its rigor were weighed differently by the reviewers initially, but in consultation the concerns predominated. The detailed reviews of the expert reviewers are appended but their concerns are summarized below. 1) The model is not adequately placed within the context of previous work in the field. There have been other papers attempting to understand both exploitation/exploration behavioral generation (e.g. Flavell et al., Cell, 2013) and forward/reversing dynamics (e.g. Stephens, PNAS, 2011).

The requested context is now provided in the Introduction.

Moreover, a direct comparison to (Rakowski et al., 2013) is needed. This work, which is cited as Ref. 12, also develops a model of the command neuron network and uses this model to predict behavioral states and the effects of ablations.

The Rakowski paper is difficult to decipher at several key respects, but as we understand the text, reviewers’ points (i) and (ii) are almost certainly over-interpretations of what the Rakowski model (RM) achieves.

(i) Prediction of behavioral states. We agree that the RM enables one to predict/compute from a given weight matrix the quantity $\mathrm{R}$ = Tf/(Tf + Tb), where Tf and Tb are, respectively, the total time the animal spends in the forward and backward states during the observation period. Note, however, that $\mathrm{R}$ is not a state. Rather, it is the steady-state probability of forward locomotion (conditional on the animal not being in the pause state). The individual behavioral states themselves – forward, backward, and stopped, in their terminology – are not represented in the mathematics. It would therefore be impossible to derive mathematical expressions for mean dwell times in these states, nor could one simulate the network in time to produce a predicted sequence of behavioral states. Thus, it is simply not true that the RM predicts behavioral states.

(ii) Prediction of ablation effects. We agree that the RM computes the effects of ablations on the quantity R, but we don’t agree it predicts them. This is for the simple reason that the model is fitted to the ablation data, so it can’t be said to predict them. It should have been tested on data to which is was not fitted.

With respect to the question of ablation effects, we must call the reviewers' attention to the fact that the ablation data in Rakowski were not analyzed for statistical significance, and the Sternberg lab has confirmed this in personal communications. The absence of statistics means that the question of which purported "effects" are real, and which are false positives of false negatives simply cannot be addressed. Rakowski’s claims related to behavioral effects of ablations should therefore be put on hold until they have been subjected to the field’s common standard of validity.

In revising our manuscript, we nevertheless made the requested direct comparison be between the two models. We added a paragraph in Discussion that is dedicated to the comparison (sixth paragraph). We chose not to mention the missing statistics.

2) The existence of two different pause states $\mathrm{X}$ and $\mathrm{Y}$ is not well supported in the data and the HMM does not have the power to confirm their existence.

This comment raises two separate questions: (a) Does the addition of a second pause state significantly improve the ability of the model to fit the data? (b) Do the two pause states correspond to “real’” physiological states? These two questions raise fundamentally different issues, which we consider separately below:

a) Does the addition of a second pause state significantly improve the ability of the model to fit the data? Yes, the second pause state improves the fit well beyond what can be attributed to the addition of two free parameters in the model (p<10^-100 by likelihood ratio test (see subsection “Wild type locomotion“, fourth paragraph and Table 1). For this test we constrained the rates into state $\mathrm{Y}$ to be $a_{\mathrm{FY}}$ = $a_{\mathrm{RY}}$ = 10^-10 s^-1, which effectively eliminates state $\mathrm{Y}$ ($p_{\mathrm{Y}}$ < 10^-18); model B in Table 1). Because the model with one pause state (model B in Table 1) is a special case of the model with two pause states (model A in Table 1), we could apply the likelihood ratio test. The likelihood ratio test is designed specifically for the purpose of comparing two models, one of which is a constrained version of the other, by comparing the reduction in likelihood in the constrained model with the reduction that can be attributed to having fewer free parameters. We further showed that there is almost no benefit in allowing direct transitions between $\mathrm{F}$ and $\mathrm{R}$ states (model C in Table 1; equivalent to the most general model with one pause state and all 6 transition rates left unconstrained). We conclude that our synaptic model with two pause states, which has 6 free parameters, fits the data far better than any similar model with only one pause state.

b) Do the two pause states correspond to “real’” physiological states? This is subtle question because “real” physiological state is not easily defined. Therefore, for the purpose of this rebuttal we will consider the strongest version of this question, which we infer to be the question that the reviewer is asking: Does the model have the power to confirm the hypothesis that state $\mathrm{X}$ corresponds to both pools of command neurons being “OFF”, whereas state $\mathrm{Y}$ corresponds to both pools being “ON”? Our answer is no, and we do not make this claim. Instead, we propose this as a working hypothesis that provides a useful framework in which to interpret results but which will need to be tested directly by physiological experiments when and if such experiments become technically feasible. In support of the working hypothesis, it is important to note that it is consistent with experimental observations beyond the well-known result that the forward command neurons promote forward locomotion and reverse command neurons promote reverse locomotion. It has also been shown that genetic ablation or silencing of both pools of command neurons induces long pauses (subsection “The Stochastic Switch Model, seventh paragraph), as expected for state $\mathrm{X}$, and that worms pause when forward and reverse motor neurons simultaneously enter their activated state (in the eighth paragraph of the aforementioned subsection). Although the latter results are for the motor neurons, not the command neurons that drive them, the gap junction synapses known to exist between the command neurons and their motor neuron targets makes it reasonable to hypothesize that both pools of command neurons are also co-activated during these pauses, as expected for state $\mathrm{Y}$. Thus, there is sufficient experimental evidence to justify proposing our working hypothesis. Additional evidence that states $\mathrm{X}$ and $\mathrm{Y}$ are “real” by physiological criteria comes from our results showing that the two states have different properties. State $\mathrm{Y}$ is intimately associated with the termination of reverse locomotion, whereas state $\mathrm{X}$ is associated with the end of forward locomotion (Figure 3). Because worms typically end reverse locomotion with a ventral bend, state $\mathrm{Y}$ is associated with this posture (Figure 4), whereas state $\mathrm{X}$ has no strong postural preference. The two states also have different mean dwell times (Figure 2—figure supplement 3), and state $\mathrm{Y}$ almost always leads into state $\mathrm{F}$, whereas state $\mathrm{X}$ can exit to either state $\mathrm{F}$ or $\mathrm{R}$ (Figure 3). Thus, pauses that follow reverse locomotion are different from pauses that follow forward locomotion, and can therefore be regarded as two different states of the system. It remains to be shown experimentally how closely the states of the model correspond to activity states of the command neurons

We have made three changes to the manuscript which we hope will limit the risk that other readers will over-interpret what we are claiming with respect to the possible association of states of the model with activity states of the command neurons:

A) We have rewritten the paragraphs that explain the model assumptions and the possible relationships between the four states of the model and the activity states of the command neurons (subsection “The Stochastic Switch Model”, third, seventh and eighth paragraphs).

B) The title has been changed from “A stochastic neuronal flip-flop circuit regulates random search during foraging behavior,” to “A stochastic neuronal model predicts random search behaviors at multiple spatial scales in C. elegans.”

C) We have re-stated the primary conclusion of the paper (Discussion, fourth paragraph): “Nevertheless, the predictive and explanatory successes of the model demonstrate the utility of present conceptualization of the network.”

3) The mapping of the HMM onto the underlying neuronal network is not convincing. In particular there little data in this paper or in any of the citations to support the contention that pause state $\mathrm{X}$ = all command neurons off and pause state $\mathrm{Y}$ = all command neurons on.

As noted in response to critique 2, this is an assumption, not a contention, and we have taken steps to clarify this point in the Discussion.

Mapping synaptic weights onto coupling in the HMM is not rigorous.

We understand this statement to mean that we have not provided an equation for computing synaptic strength, as would be measured electrophysiologically in pairwise recordings quantifying synaptic currents, in terms of synaptic weights (w) as defined in the Stochastic Switch Model. We agree. As requested below, we have relaxed claims to have demonstrated prediction of synaptic weights in the electrophysiological sense of the term.

For the paper to be suitable for eLife the following extensive changes would have to be made.

1) Relax the claims about the model's prediction of synaptic weights.

We have relaxed these claims by pointing out that the term “synaptic weight” has different meanings in the neural-network versus the electrophysiological literature (neither field, of course, can be said to own the term). We now relax our claims by explicitly stating that the Stochastic Switch Model does not predict the magnitude of synaptic conductances (subsection “Synaptic weights in the stochastic switch model”, second paragraph). But it does predict aspects of functional connectivity, such as excitation or inhibition, because weights in the model are signed quantities. We also relax our claims of correspondence between the model and the electrophysiology by noting that our method of testing the model carries with it the assumption that functional connectivity between populations of neurons reflects the connectivity between the neurons in those pools that have the greatest effects on behavior (e.g. in ablations).

2) The authors need to establish firmly that tracking a single point provides an unbiased estimate of trajectory in light of Stephens, PLoS One (2010). Given their extensive data set, we presume that converting their point imaging into centerline tracking would be extremely difficult and time consuming, but the authors should at least place their analysis in this light.

The field recognizes two definitions of trajectory. One is path of the centroid (Pierce- Shimomura et al., 1999), defined as the midpoint of the smallest rectangle that can enclose the worm. The other is the path taken by one or more points on the worm’s centerline (Cronin et al., 2005); spot tracking is an instance of the latter.

Centroid trajectory. Stephens et al. are mainly concerned with the time series of postural measurements, not trajectory. The 2010 paper is an exception, but it considers only centroid trajectory. The main point of that paper is to show that the centroid trajectories of real worms can be recovered from the time series of their posture. The authors report, however, that their “eigenworm model” can be expected to do this only when the trajectory of the real worm is relatively straight. The degree of fit between real and computed trajectories is shown in the supplemental material; the fits may or may not be convincing, depending upon one’s point of view. No attempt is made by Stephens et al. to compute centerline trajectories.

Centerline trajectory. According to the theory of thrust generation in sinusoidal locomotion, established by Gray (1946, 1953) and extended to nematodes by (Gray and Lissman, 1964), the spot tracking method should provide an accurate estimate of centerline trajectory, an estimate that is probably more accurate than previous centerline methods (Cronin et al., 2005). In the case of ideal sinusoidal locomotion (no lateral slip), each segment of the body recapitulates the path of the segment ahead of it, like train cars on a sinuous track; thus the trajectory is just the path taken by the segments. On agar plates, C. elegans plows a furrow as it crawls; surface tension provides the necessary downward pressure. The walls of this furrow, which provide the lateral resistance for thrust generation, are what causes each segment to follow the one ahead of it. It is general practice in the field to dry agar plates slightly before use to reduce slip, ensuring that the body stays within the furrow, and locomotion approaches the ideal case. Under these conditions, a radially symmetric tracking perfectly centered on the body axis introduces no bias into trajectory. Bias occurs only when the center of mass of the tracking spot is eccentric to the centerline. This offset shifts the trajectory by the extent of the eccentricity and can increase/decrease the curvature maxima/minima. But in practice eccentricities were small, probably less than 1/10 of the worm’s diameter, because spots with greater eccentricities were quickly rubbed off by friction with the substrate; such recordings were discarded. Another potential problem is deformation of the spot as the worm’s body undulates, but this was almost certainly not an issue in our experiments because the long axis of the spot was small with respect to the radius of curvature of the worm. Note: The first step in Stephens’ image analysis was to compute the worm’s centerline (Stephens et al., 2008), but centerlines were used only to compute posture. They were not used to compute the centerline velocity, although this would have been possible as previously shown (Cronin et al., 2005).

Conversion of spot-tracking to centerline tracking. Centerlines can be recovered easily from spot tracking data. We have now done this for the entire wild type data set and included it in the paper (Figure 4). Our goal was to ask whether the worm adopts a particular posture as it enters the pause state, as Stephens et al. report. In this analysis we were somewhat limited by the fact that in the spot tracking method, pause posture can be delineated only up to the anterior-posterior level of the spot (approximately the midpoint). This limitation occurs because the spot’s future trajectory after the pause has not yet occurred, but it is mitigated by the fact that postures in which curvature is discontinuous do not occur in live, wild type worms. We find that pauses following reversals occur at a particular posture whereas pauses following forward locomotion do not. In contrast, Figure 5D of Stephens et al. (2008) indicates pauses occur a particular postures regardless of the direction of movement. One obvious reason for the discrepancy between the two studies is the difference in definitions of velocity used to identify the pause state. This topic is addressed in detail in the Discussion (fifth paragraph).

In summary, the eigenworm model is based on postures, not trajectories. Centroid trajectory can be recovered in the eigenworm model, but it is inaccurate unless the worm is moving comparatively straight. In contrast, the spot tracking method provides an accurate measure of centerline trajectory without significant bias.

They should also bolster their arguments that there are two behaviorally distinct pause states and discuss how they are related to the two pause states of Stephens.

(i) On the existence of two pause states. As stated above, we do not claim that the model has the power to confirm the existence of the two pause states. However, the model does provide reasons to believe such states might exist. As requested, we have reinforced these arguments, now devoting a whole new paragraph to the issue (subsection “Wild type locomotion“, fourth paragraph).

(ii) Discuss relationship to pause states of Stephens. Done. See fifth paragraph of the Discussion.

3) The authors should differentiate their work with respect to Rakowski, 2013. Does their model provide different predictions? Can they be disambiguated? It would be great if they could show this, but minimally, they should suggest what experiments should be performed in the future.

See Discussion, sixth paragraph.

4) Similarly –

what measurements should be made to distinguish $\mathrm{X}$ and $\mathrm{Y}$ pause states map onto the electrical activity of the command neuron network at least at some coarse-grained level?

See Discussion, third and fourth paragraphs.

Reviewer #3: 1) In Figure 4B, I find the excuse for omitting error bars to be relatively weak. Minimally, bootstrapped confidence intervals could be found, which would be significantly better than the current lack of any measure of variability.

Note: Figure 4 is now Figure 5.

Calculating confidence intervals would be nice for graphical representation, but was unnecessary to compute statistical significance of the differences shown in the figure, which was done using the likelihood ratio test, results of which are shown in Table 4. Computing the results shown in Table 4 was extremely time-consuming; >95% of the computation time for the entire data analysis presented in the paper was for computing the p-values in this table. Computing confidence intervals for Figure 5B (formerly Figure 4B) would require another ~10x increase in computation time, thousands of hours. Given that the confidence intervals would not be used to for the key statistical tests, which we already have done using the appropriate test, it would be an unnecessary burden to compute them.

2) In the fifth paragraph of the subsection “Genetic effects on command neuron function “and Figure 6. The claim is made that "changes in synaptic strength dominate the effects of changes in membrane potential on Δ$\mathrm{F}$ and

Δ$\mathrm{R}$." This certainly seems true for Δ$\mathrm{F}$, but both models appear to give more-or-less identical predictions here for Δ$\mathrm{R}$.

We understand the concern here to be that the ΔV and Δ$\mathrm{R}$ models make the same prediction for changes in Δ$\mathrm{R}$, meaning that the Δ$\mathrm{R}$ data cannot be used to distinguish between the two models. However, taking a step back and looking across the Δ$\mathrm{R}$ and Δ$\mathrm{F}$ data simultaneously, it can be seen that the Δ$\mathrm{R}$ model gets both patterns right, whereas the ΔV model gets only one of them right. It is this fact that we take as evidence in support of the Δ$\mathrm{R}$ model for Δ$\mathrm{F}$ and Δ$\mathrm{R}$. The text has been modified to make it more clear that we are looking across Δ$\mathrm{F}$and Δ$\mathrm{R}$ when comparing the models (subsection “Genetic effects on command neuron function”, sixth paragraph).

3) In the first paragraph of the subsection “The Stochastic Switch Model and other random search behaviors“. It is claimed that "changes are required in at least three weights to produce the full range of search behaviors." This is not actually shown anywhere in the paper, just that three weights are sufficient to induce the full range. A supplementary figure to this effect would be useful.

The revised text and figures now carefully document weight changes that are minimally required for the full range of search modes (Figure 8 including supplementals, Table 7 (new), and accompanying text (subsection “Regulation of search scale, last two paragraphs and subsection “Biased random walks”).

4) The predicted value for the dwell time in the forward state is not comparable to the rest of the literature, as a different definition is used here. What would happen if a standard definition was used? Does the same rate result?

We now report the mean dwell times for $\mathrm{F}$, $\mathrm{R}$ and $\mathrm{X}$ based on fixed velocity thresholds of ± 0.05 mm/s. $d_{\mathrm{F}}$ = 1.86 ± 0.03; $d_{\mathrm{R}}$ = 1.23 ± 0.02;$d_{\mathrm{P},0.05}$= 0.14 ± 0.001. Thus, the short dwell times in the forward state that we observed were not due to the model. We attribute them instead to the higher time resolution of our tracking hardware (subsection “Wild type locomotion”, first paragraph).