acceptodds
Under review as a conference paper at ICLR 2027

When Connectomic Wiring Hinders Imitation: Interface Constraints and the Latency of Sensory Access

Abstract

Fly connectomes are increasingly proposed as architectural priors for neural controllers, with reports that a policy structured by the wiring diagram learns better than random graphs. We test this on four connectomes (male and female ventral nerve cords, two brains) with 14 null models, two input/output (IO) designs and three motor tasks. Under gradient-based imitation the real wiring never outperforms a random graph. With a dense trainable IO we find no consistent effect of topology; with a biologically wired IO (per-leg sensing and actuation, commands through descending neurons) the real wiring is worse, error rises monotonically with structural fidelity, and the effect replicates in the other sex and on a hexapod robot. Hubs, modularity, reciprocity and spectral properties do not explain the penalty; the scarcity of direct afferent→efferent edges does. Degree-preserving swaps that add such edges bring the connectome to the level of a degree-matched random graph, sham swaps do not, and only sensory→motor shortcuts help. The penalty is unchanged under a teacher with no causal dependence on other legs, halves when the teacher tolerates two to three ticks of sensory delay (the connectome's afferent-to-motor path length), and lies in the slow, gait component of the target. The wiring diagram withholds one-tick paths from sensory populations whose fast fluctuations predict the gait; an accessibility–demand model ranks 27 graph variants (ρ = 0.92). Under our implementation the published positive result does not survive an Erdős–Rényi baseline.

Primary area:
applications to neuroscience & cognitive science
Keywords:
connectome, inductive bias, imitation learning, embodied control

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_qmtcOpenReview ↗
Rating
1
Confidence
4
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper tests whether biological fly-connectome wiring is beneficial when used as a fixed graph prior for a trainable neural controller. It studies male/female ventral-nerve-cord and brain graph variants, a family of degree-, flow-, module- and reciprocity-preserving null graphs, and two different input/output interfaces: a dense trainable interface and a biologically wired interface that reads sensory afferents and actuates motor-neuron groups. Under dense I/O, real wiring has no consistent benefit; under the biologically wired interface, preserving more native structure worsens imitation of a global expert, including across additional tasks and a hexapod check. Re-targeting and carefully controlled shortcut interventions implicate limited short-latency sensory-to-motor access rather than conventional global graph statistics. Teacher-locality/delay controls, frequency decomposition, a 27-variant accessibility–demand diagnostic and bounded-gain linearized propositions develop this explanation. The analysis is primarily about imitation loss under the specified interfaces, not successful autonomous locomotion.

Critical strengths
  1. Exceptionally discriminating graph controls for a counterintuitive negative result. The authors do not stop at comparing a connectome to an Erdős–Rényi graph: they use degree-preserving rewires, flow-block controls, modular and reciprocal nulls, sign/weight variants and interventions that specifically increase afferent-to-motor shortcuts while preserving important edge statistics (Secs. 3.2, 4.2–4.4; Table 2). On the MaleCNS VNC biological-interface task, the real graph reaches 0.206 validation MSE versus 0.176 for degree-preserving and 0.162 for ER (lower is better). Sham and matched swap controls make the shortcut explanation more credible than a mere topology/performance correlation.
  2. A multi-angle causal account that states its conditions and remaining residuals. The teacher-locality intervention finds that the gap is not simply explained by what the expert causally reads, while tolerated sensory delay reduces the penalty and its excess error lies predominantly below 50 Hz (Sec. 4.7). A predictive accessibility–demand statistic orders 27 variants with a reported Spearman correlation around 0.92 (Appendix E), and the paper explicitly limits the accompanying propositions to linearized bounded-gain students. Reproduction caveats concerning FlyGM and the lack of a closed-loop success claim are stated instead of hidden.
Critical weaknesses
  1. The downstream embodiment evidence is much weaker than the imitation evidence. The main result concerns validation action MSE against fixed teachers. Appendix B reports 100% falls for the tested graph-controller variants in a clean-command closed-loop flybody setting, versus substantially lower fall rates for the reference expert/MLP. Thus the measurements do not show that the compared biological or random graphs support viable locomotion, and an imitation-error ranking need not predict closed-loop control. This is a substantial boundary on the relevance of the result to embodied policy design.
  2. The explanation remains conditional on interface, optimization and architectural choices. The biologically wired read-in/read-out scheme, three message-passing updates per control step, recurrence, fixed motor readout groups and a global-distillation objective create a particular access bottleneck. Shortcut and teacher-delay interventions isolate meaningful contributions, but do not fully exclude learnability and temporal-compensation effects in a different controller. The theoretical propositions concern linearized, uncorrelated-input, bounded-gain students, not the trained nonlinear graph policies. The comparison with the positive published FlyGM result is necessarily qualified because its code and exact training setup were unavailable (Secs. 4.5, 6; Appendix F). Figure/presentation concern (secondary): Figure 1 squeezes four comparisons into very small panels; Fig. 2 has a crowded legend and compact axis/category labels; and Fig. 4 combines six plots with many similar solid/dashed curves. These layouts make the decisive null-model and shortcut comparisons laborious to verify without zooming. Enlarging panels, simplifying legends and separating key contrasts would materially improve readability, but figure quality alone is not proof of causal unsoundness.
Questions for authors
  1. Temporal compute versus structural access (assessment-critical). If message-passing depth per control step or the recurrent horizon is varied at matched computational budgets, does the connectome-to-null gap shrink as predicted by the sensory-access interpretation? Can the same ablation be performed when teacher targets are based only on the student’s available sensory channels? A robustness result would clarify whether the reported bottleneck is intrinsic to the graph or specific to the chosen interface dynamics.
  2. Relationship between imitation MSE and usable control (assessment-critical). Given the closed-loop failures documented in Appendix B, can the authors provide a behavioral evaluation that isolates whether the same wiring order persists among controllers able to execute nontrivial locomotion, or show why the reported imitation gaps are the right success measure for the claimed architectural-prior setting? The answer would materially affect the paper’s practical significance, without invalidating the within-setup imitation analysis.
5 comments
AuthorsOpenReview ↗

Response (1/4)

We sincerely thank the reviewer for a careful and accurate summary, for describing the graph controls as "exceptionally discriminating", and for two well-posed, assessment-critical questions. We have answered both with new experiments and address every weakness point by point, in four parts: (1) a factual correction and Q1; (2) Q2 and the embodiment evidence; (3) the conditions of the explanation; (4) figures and a summary of changes.

A factual correction first. The controller performs one message-passing update per control step, not three (Sec. 3.3: "one control step computes M = WH …"). Three updates per step is an ablation (Sec. 4.3, Appendix F), and it does not reduce the gap. The revision states the default in bold in Sec. 3.3 so it cannot be misread. This bears directly on Q1.

Q1. Temporal compute versus structural access. We varied every form of temporal compute we could, one at a time, connectome vs DP, 3 seeds each:

VariationExtra computeGap (p)
default: 1 update per tick, d = 16, BPTT 32, 3,000 updates–0.030
3 message-passing updates per tick, expert (batch 8)3× per tick0.037 (0.02)
3 updates per tick, local teacher (batch 8; 1-update comparator 0.027)3× per tick0.030
BPTT window 128 instead of 32 (batch 4: samples per update matched)same per update0.027 (0.001)
node width d = 32 (batch 8)more per tick0.029 (0.002)
3× more updates (9,000)3× in total0.035 (0.002)
teacher tolerates 2–3 ticks of sensory delay (local teacher)none0.012 (reduction p = 3×10⁻⁴)

The pattern answers the question directly. Every form of added compute (depth per tick, recurrent horizon, width, training time) lowers every graph's error but leaves the connectome−DP gap in place. The one manipulation that more than halves the gap adds no compute at all: it gives the student time, by letting the target lag the sensory input. So the bottleneck is not a shortage of computation. It is when sensory information can reach the motor neurons, relative to when the target needs it, which is the structural-access reading.

On matched budgets: we increased depth with everything else fixed, which gives the deeper model more compute than the default. A matched-budget version would take compute away elsewhere (e.g. width) and give it less. Since more compute did not shrink the gap, we see no reason to expect less compute to do so. The BPTT-128 row is matched in samples per update, and it also leaves the gap.

We agree with the reviewer's implicit point: within-tick depth reaches as far as a two-tick delay in hops, yet only the delay helps, so a pure hop-count account is insufficient. The paper says so and keeps latency as a hypothesis (general response, point 3).

Q1, second part: teacher targets based only on the student's available channels. This is exactly the design of our teacher-side test (Sec. 4.7, Appendix I). We distilled the expert into two teachers: a global teacher that reads only the channels the bio-wired student can access, and a local teacher in which each leg's actuators depend only on that leg's 29 channels and the command. The gap is 0.028 and 0.030, against 0.030 for the expert. The ablations were then repeated under the local teacher:

  • three sub-updates per tick: gap 0.030 (vs 0.027 for one update): no reduction;
  • 2–3 ticks of tolerated sensory delay: gap 0.027 → 0.012: more than halved;
  • weight-matched cross-leg sensory→motor swaps: connectome 0.136 → 0.110 (p = 0.002; DP 0.106); descending→motor swaps: 0.131 (p = 0.30, no effect), as under the expert.

So the bottleneck is not created by asking the student to imitate information it cannot reach. Given the interface, it is intrinsic to the graph's path structure: it moves only when the sensory→motor paths change, or when the target gives the student time to use longer paths.

AuthorsOpenReview ↗

Response (2/4)

Q2 and Weakness 1. Imitation MSE versus usable control. We agree that this is the main boundary of the result. The revised abstract now ends: "Our claims concern imitation error: in closed loop, biologically wired controllers fall on the fly body whatever their graph, and on the hexapod RL fine-tuning leaves all graphs indistinguishable." We answer the question in three steps.

(a) The fly body cannot rank graphs in closed loop. We had reported closed-loop failure only for the connectome. DP fails equally: both fall in 100% of episodes after BC, after six DAgger rounds and after 40 PPO iterations (164k steps; returns 34 vs 38). For reference: expert 4% falls, MLP after BC+PPO 17%, dense-IO connectome GNN after BC+PPO 33%. A graph controller can therefore locomote on the fly body, but not with the bio-wired interface, and Appendix B now says so for both graphs.

(b) Behavioural evaluation among controllers that do locomote. On the hexapod, every graph variant walks after behaviour cloning, without falls under clean conditions, pushes, 1.5× body mass and 20 ms observation delay. The imitation ordering is reproduced there (connectome worst; p = 0.014 vs ER). Closed-loop speed error is saturated (0.004 for every graph), except under observation delay, where the connectome is slightly best (0.034 vs DP 0.042, ER 0.046; p = 0.025 vs ER, 0.16 vs DP).

(c) New: closed-loop RL with the same body and interface. We fine-tuned every BC controller with recurrent PPO (150 iterations, 614k steps; reward for tracking the commanded speed and yaw rate, −1 on a fall). Deterministic evaluation against the commanded velocity, mean over 3 seeds (Appendix L, Table 9):

Controllerspeed err BC → PPOyaw err BC → PPOreward BC → PPO
connectome0.095 → 0.0560.138 → 0.1990.942 → 1.003
DP0.095 → 0.0500.136 → 0.2020.948 → 1.021
ER0.095 → 0.0380.134 → 0.2280.955 → 0.959

Every graph controller gains about 5% in reward, none falls under any perturbation, and connectome, DP and ER are indistinguishable on every metric (p > 0.1). The connectome's small advantage under delay after BC does not survive fine-tuning.

Answer to Q2. Among controllers that execute nontrivial locomotion, the imitation ordering does not persist as a behavioural difference: after BC the graphs are equal (saturated), and after RL they are equal too. Importantly, no connectome benefit appears in closed loop either. The two settings therefore agree on what matters for the paper's question: the wiring is not a useful prior, whether training is by imitation or by reward. The revision states this, and also that the imitation penalty itself has no closed-loop counterpart on the hexapod.

Why imitation error is the right measure for the claim we make.

  1. It is the setting of the positive claim we test. The connectome advantage reported by FlyGM concerns gradient-based learning of a pretrained policy's behaviour; testing it requires the same objective.
  2. It is how large controllers are initialised. Our own fly pipeline, like most for high-dimensional bodies, is BC followed by RL. A prior that makes imitation harder gives RL a worse starting point; on the fly body, where RL from scratch is out of reach, that starting point decides the outcome.
  3. It allows causal inference. Imitation error has low seed variance (s.d. 0.005 against a 0.030 gap), which is what makes the sham-controlled interventions decisive. Closed-loop metrics are saturated at failure on the fly body and saturated at success on the hexapod, so they cannot resolve differences of this size.

We therefore claim what imitation error can support, a within-setup statement about the wiring as a prior for gradient-based imitation, and we report the closed-loop results in full alongside it.

AuthorsOpenReview ↗

Response (3/4)

Weakness 2. The explanation is conditional on interface, optimisation and architecture. We agree that every result holds under stated conditions, and the revision states them. We take each condition the reviewer lists in turn and give the evidence on how far the result depends on it.

  • The biologically wired interface. We see the interface dependence as the finding rather than a limitation. Under a dense interface the wiring makes no difference; under the interface by which the real VNC meets the body, it is harmful, and the interventions identify the feature of the wiring that causes the harm. The bio-wired interface is not an arbitrary choice: it encodes the anatomy (each leg's sensors enter that leg's sensory neurons; each leg's muscles are driven by that leg's motor neurons). The same interface rule gives the same ordering in two animals of different sex and on a second body.

  • "Three message-passing updates per control step." As corrected in part 1, the default is one; three is an ablation, and it leaves the gap (0.037 vs 0.030).

  • Recurrence. The GRU node update is one controller class. The same ordering appears with very different dynamics: a frozen rate model with a trained readout (T2 MSE: connectome 0.78 vs ER 0.65; T3 explained variance: 0.115 vs 0.161), a DMN-style rate model with trained neuron parameters (0.143 vs DP 0.189, p = 0.004), and new versions of both models tied by cell type (GNN gap 0.039; tied DMN 0.145 vs DP 0.200, p = 0.005). A four-times longer gradient horizon leaves the gap at 0.027.

  • Fixed motor readout groups. The weight-matched shortcut swaps keep the readout groups exactly as they are and still remove the penalty (0.171 vs sham 0.200). The readout groups alone therefore do not cause it; what matters is the paths from sensors to those groups.

  • Global-distillation objective. The objective was varied: local teacher (no cross-leg dependence, gap 0.030), global teacher restricted to accessible channels (0.028), smoothed expert (0.018), delayed teachers (0.023 / 0.012 / 0.012), an analytic tripod clock on the hexapod (p = 0.014), and recorded fly kinematics (T3). The connectome is worst in every case. Two further objectives are not distillation: an evolution strategy on the ball task, where the connectome module (0.04 ± 0.12) is indistinguishable from its rewired version (0.07 ± 0.04), and the new PPO fine-tuning on the hexapod, where all graphs are equal.

  • Learnability and temporal compensation. We tested these directly: 3× longer training (gap 0.035; relative to DP it grows from 17% to 23%), BPTT 128, three sub-updates per tick, double width, no descriptors, and RL fine-tuning. None closes the gap. We agree that a controller class outside those we test could compensate differently, and the Limitations say so.

  • Linearised propositions. We agree, and Appendix G scopes them explicitly to idealised linear students with uncorrelated inputs and bounded gain, assumptions the trained controllers do not satisfy. The propositions motivate the accessibility statistic; the statistic is then tested empirically on the trained nonlinear controllers, where it ranks 27 graph variants by imitation error (Spearman ρ = 0.92). No conclusion about trained policies rests on the propositions alone.

  • FlyGM comparison. We agree that it is necessarily qualified, because FlyGM's code is not public, and the paper says so in Sec. 4.5, the Limitations and Appendix H. The part of our argument that does not depend on implementation details is the null-model one. On FlyWire, DP underperforms the connectome in the reported direction (0.182 vs 0.170, p = 0.11), but ER matches it (0.168, p = 0.49). FlyWire has 29–43% afferent neurons with no output; DP rewiring keeps them output-less and scrambles the afferent→efferent flow, whereas ER does not. Unit-weight baselines, as in FlyGM, give the same ordering. A released implementation could change our numbers, but not this argument about the null model.

Reviewer_NsXhOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper examines whether fly connectome wiring provides a useful architectural prior for imitation learning. Under biologically constrained input-output (IO) mappings, the real connectome performs worse than randomized graphs. Controlled rewiring experiments show that adding direct sensory-to-motor connections removes much of the performance gap. The authors further investigate this result through sensory accessibility and latency.

Critical strengths

Comprehensive structural interventions. The authors systematically examine various graph properties through controlled rewiring, targeted connectivity changes, and sham controls, providing strong evidence for the role of sensory-to-motor connectivity in the performance gap. Broad experimental comparisons. The paper examines four Drosophila connectomes and considers a range of random graph baselines, IO configurations, and neural dynamics. Useful methodological findings. The results show how IO constraints and the choice of random graph baselines affect the evaluation of connectome-based architectures. The paper also makes a useful distinction between imitation accuracy and closed-loop control performance.

Critical weaknesses

The effects of normalization and subgraph extraction remain unclear. Row normalization removes differences in total absolute incoming weight across neurons, while extracting the VNC may discard external inputs and alter the relative strength of retained connections. It would be helpful to quantify the discarded inputs and test whether the performance ordering holds under alternative normalization schemes. Limited statistical reliability across random graph instances. Most experiments use only three seeds, with each seed controlling graph sampling, model initialization, and data order. This makes it difficult to separate structural variability from training variability. More independent graph samples and separate estimates of between-graph and within-graph variance would strengthen the results. The sensory latency explanation remains incomplete. Delaying the teacher's sensory inputs reduces the performance gap, but the evidence is relatively weak (p = 0.10). Additional within-tick message-passing steps also fail to reduce the gap. Since delaying the teacher changes the prediction target, it would be useful to examine whether target predictability or initial hidden-state transients contribute to these results. Limited analysis of architecture and training sensitivity. The 32-dimensional, four-layer experiment changes two factors simultaneously and uses only one seed. The real connectome's validation error is also still decreasing at the end of training. Separate tests of node-state dimensionality, trainable node descriptors, and longer training would help clarify how much the gap depends on these choices.

Questions for authors

Same as the weaknesses.

3 comments
AuthorsOpenReview ↗

Response (1/3)

We sincerely thank the reviewer for four specific and testable concerns. We addressed each with new analysis or new runs, in three parts: (1) normalisation and subgraph extraction; (2) graph-sampling variance and the latency explanation; (3) architecture and training sensitivity. All p-values are Welch tests over 3 seeds unless stated; the new numbers are in the robustness appendix (Appendix F, Table 4).

Subgraph extraction (quantified). We measured, for every retained neuron, the share of its synaptic input that comes from neurons outside the extracted thoracic VNC:

Retained neuronsInput lost by extraction
all21%
motor neurons4.6%
intrinsic (interneurons)8.7%
afferents (sensory and descending)62.7%

The loss is small where it matters for the mechanism, on the motor neurons and the interneurons that would carry sensory→motor paths. The large loss falls on afferents, and it is mostly input to descending neurons, whose dendrites lie in the brain; 57% of all outside input comes from central-brain intrinsic neurons. In the bio-wired interface this brain input is replaced by the command encoder onto the descending neurons, so it is modelled, not silently dropped. Two further observations argue against extraction as the cause: the brain graphs (MaleCNS brain; FlyWire with optic lobes, 138k neurons), which are far less truncated, show no connectome advantage under dense IO either; and the female VNC (BANC), extracted from an independent reconstruction, reproduces the ladder almost exactly (0.203 / 0.172 / 0.162 vs male 0.206 / 0.176 / 0.162). These numbers are now in Sec. 3.1.

Normalisation. Row normalisation is the standard rate-model convention and is applied identically to every graph. We agree that it removes differences in total input across neurons. Its interaction with synapse weighting was already tested with unit-weight graphs (connectome 0.202, DP 0.169, ER 0.161: same ordering). As suggested, we added two operators that keep differences in total input:

  • symmetric normalisation D_in^(-1/2) |W| D_out^(-1/2) with signs kept;
  • global normalisation: raw synapse counts divided by the graph's mean row sum, so every graph has mean input 1 while every neuron keeps its relative total input (row-sum p90/median: connectome 6.9, ER 1.4).
OperatorconnDPERgap (p)
row (default)0.2060.1760.1620.030 (0.002)
symmetric0.1980.1670.1620.032 (6×10⁻⁶)
global0.2020.1730.1620.029 (0.001)

The gap and the ordering are unchanged under both. We considered, and deliberately did not use, spectral-radius scaling of raw counts. The connectome's spectral radius is set by its closed excitatory loops, so matching radii shrinks its typical input about tenfold relative to ER (median row input 0.25 vs 2.7). That would create a new confound in the connectome's disfavour rather than remove one. The global normalisation matches the mean input instead, which keeps the comparison fair.

AuthorsOpenReview ↗

Response (2/3)

Graph-sampling vs training variance. We sincerely appreciate this suggestion. Two points.

  • Already implicit in the design. Connectome runs involve no graph sampling, so their spread across seeds (s.d. 0.005) is pure training variance. The DP spread, which combines both sources, is also 0.005. Between-graph variance is therefore small next to the 0.030 gap.
  • Now estimated separately, as requested. We decoupled the graph seed from the training seed and ran, for DP and ER, five graph samples at one initialisation and one graph at five initialisations:
Nulls.d. across graphss.d. across initialisations
DP0.00130.0055
ER0.00090.0009

Both components are an order of magnitude below the 0.030 gap, and for DP the graph component is the smaller one. The connectome−DP difference is therefore not an artefact of which random graphs were drawn (Appendix F).

The latency explanation. We agree that it is incomplete, and the revision presents it as a hypothesis (general response, point 3). On the possibilities the reviewer raises:

  • Initial hidden-state transients: ruled out. We re-evaluated all main checkpoints with the first steps of every validation episode excluded from the error:
Steps excludedconnDPERgap
00.2060.1760.1620.031
160.2110.1800.1660.031
320.2200.1880.1730.032
640.2410.2070.1900.034

Every graph's error rises later in the episode (steady walking is harder than the start), and the gap grows slightly, so it does not come from the initial transient.

  • Target predictability: a fair alternative, tested. Delayed targets are easier for every graph (DP 0.114 → 0.092 from L = 0 to L = 3), which is why we report the gap, and the gap also shrinks in relative terms: (conn − DP)/DP is 25%, 24%, 17% and 15% for L = 0–3. A ridge regression shows that delayed targets are not more predictable from the current observation (validation R² 0.827, 0.831, 0.832, 0.830), but are more predictable from the last five observations (0.843, 0.860, 0.873, 0.874). A delay-tolerant target is one that recent history predicts, which is the same thing as a target the student has time to route through its interneurons. We therefore now describe predictability and latency as two descriptions of one effect rather than rival explanations, and we no longer present the delay result as discriminating between them (Sec. 4.7, Appendix I).

  • Statistical weakness: addressed. With three more seeds per condition (n = 6; n = 3 at one tick), the gap is 0.027, 0.023, 0.012 and 0.012 at 0–3 ticks of delay; the reduction from L = 0 to L = 3 is 0.016 ± 0.003 (p = 3×10⁻⁴; it was p = 0.10 at n = 3).

  • Within-tick message passing. We agree this is the observation that keeps latency a hypothesis: three sub-updates per tick, which give the current observation the same two-edge reach as a two-tick delay, do not reduce the gap (expert: 0.037 vs 0.030; local teacher: 0.030 vs 0.027). The delayed target depends on observations the recurrent state has already integrated over several ticks, which within-tick depth does not supply; the paper states that a pure hop-count account is insufficient.

AuthorsOpenReview ↗

Response (3/3)

Architecture and training sensitivity. We sincerely appreciate these suggestions. One clarification first: depth alone was already varied at fixed width. Three sub-updates per tick do not reduce the gap, either under the local teacher (3 seeds: 0.030 vs 0.027 for one update at the same batch size; Appendix I) or under the expert (Sec. 4.3; now 3 seeds: connectome 0.183 vs DP 0.146, gap 0.037, p = 0.02, against 0.030 for one update at the same batch size).

We agree that the 32-channel / 4-hop run confounded width with depth and was a single seed. It was meant as a check of FlyGM's configuration; the revision replaces it with separate tests, each connectome vs DP over 3 seeds:

Change (one factor at a time)connDPgap (p)
default (d = 16, descriptors, 3,000 updates)0.2060.1760.030
node width d = 32 (batch 8; batch-8 d = 16 comparator: 0.206 / 0.176)0.2020.1740.029 (0.002)
no per-neuron descriptors0.2110.1740.037 (0.009)
3× longer training (9,000 updates)0.1860.1510.035 (0.002)
BPTT window 128 (batch 4, same samples per update)0.2050.1780.027 (0.001)
three sub-updates per tick (batch 8)0.1830.1460.037 (0.02)

What each row shows:

  • Node-state dimensionality. Doubling the width changes neither graph's error noticeably and leaves the gap at 0.029.
  • Trainable node descriptors. Removing them hurts the connectome slightly more than DP (gap 0.037 vs 0.030). Descriptors therefore partly compensate for the wiring; they do not create the penalty. With descriptors tied by cell type instead (reply to R1), the gap is 0.039.
  • Longer training. The connectome's curve was indeed still falling at 3,000 updates. With three times as many updates every graph improves, but the gap does not close: it is 0.035, and relative to DP it grows from 17% to 23%. The connectome is not merely slower to converge.
  • Gradient horizon and depth. A four-times longer BPTT window and three sub-updates per tick each leave the gap in place.

Across all of these, and across the normalisation and tying variants, the gap stays between 0.027 and 0.039 and is significant every time. We conclude that the penalty does not depend on these architectural and training choices within the range we can test.

We thank the reviewer again. Each of the four concerns led to a concrete test, and we hope the results resolve them. We would be grateful if the reviewer would take the new evidence into account in the final assessment, and we are happy to run further checks during the discussion.

Reviewer_eaYWOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The authors tests different fly connectomes as a design prior across different tasks (IO, motor) against null graph models. They claim that there's no consistent benefit of this prior in their tested imitation learning settings and observe higher error under biologically constrained IO. The authors suggest that limited direct connections for sensory to motor connectivity accounts for most of this penalty. They also propose a measure of how well a graph's routing suits the imitation task and find that it closely aligns with the observed error.

Critical strengths
  1. In-depth experiments and informative negative findings: the authors did in depth analysis across 14 null models and connectome settings. Targeted interventions further identify sensor to motor connectivity as an important contributor to the observed imitation performance gap.
Critical weaknesses
  1. Teacher-student mismatch: The authors find that under bio-wired IO the connectome student has higher imitation error than random graphs and conclude that the connectome is a "weak or negative prior for control." However, for every teacher, including "local" ones, the teacher is a dense zero-latency MLP, so students are scored on how closely they align with an MLP. This supports that the connectome is a poor student for distilling an MLP, not that the connectome is a poor prior for control. Also, in Appendix B, the bio-wire connectome fails in 100% of cases, and the results for the random-graph variants are not reported, so it is unclear whether the gaps are faithful to actual walking performance.

  2. Some claims appear not significant. There are claims by the authors e.g. the penalty "is reduced when the teacher tolerates two to three ticks of sensory delay" that are not significant (p=0.10), yet are presented as a contribution in the abstract.

Questions for authors

See weaknesses

2 comments
AuthorsOpenReview ↗

Response (1/2)

We sincerely thank the reviewer for the positive assessment and for two pointed criticisms, which we address in two parts: (1) the teacher–student mismatch; (2) closed-loop results for random graphs and the significance of the delay claim.

Teacher–student mismatch. We agree with part of this and have changed the wording: the Discussion now says the connectome is a weak prior "for gradient-based imitation", not "for control", and the abstract states that our claims concern imitation error. However, we respectfully disagree with the narrower reading that the connectome is a poor student of an MLP specifically. The ordering appears with teachers that are not MLPs, with teachers that are not zero-latency, and with teachers that only use what the student can see:

TeacherWhat it isConnectome worst?
expert (DMPO)dense MLP policyyes, gap to DP 0.030
global MLPreads only channels the bio-wired student can accessyes, 0.028
local MLPeach leg's actuators depend only on that leg's channels and the commandyes, 0.030
delayed local MLPreacts to sensory input 1, 2 or 3 ticks lateyes, 0.023 / 0.012 / 0.012
smoothed expert10 ms exponential average of the expert's actionsyes, 0.018 (p = 0.03)
hexapod tripod gaitanalytic function of time and command, no networkyes, vs ER p = 0.014
real fly motion capture (T3)recorded kinematics, frozen core with trained readoutyes, explained variance 0.115 vs ER 0.161
real fly motion capture (T3)DMN-style rate model, neuron parameters trainedyes, 0.143 vs DP 0.189 (p = 0.004)
real fly motion capture (T3)DMN tied by cell type (new)yes, 0.145 vs DP 0.200 (p = 0.005)

Three points follow from this.

  • Not an MLP artefact. The analytic tripod clock and the recorded fly kinematics involve no network at all, and the connectome is again worst.
  • Not a zero-latency artefact. Delayed teachers are easier for the connectome in relative terms (the gap more than halves), which is what the access account predicts, but the connectome remains worst under every delay we tested.
  • Not an inaccessible-information artefact. The global and local teachers never ask the student for information it cannot see, and the gap is unchanged (0.028 and 0.030).

The table also contains a useful negative case. On T3 with the trainable bio-wired GNN, the penalty is absent (connectome 0.345, DP 0.352, ER 0.348; p = 0.32). There, the only external input during generation is the root velocity, which enters through descending neurons that every motor pool reaches within one step. The accessibility account predicts no penalty in that case, and none is observed. The penalty therefore follows the access structure of the task, not the identity of the teacher.

Finally, distilling a pretrained policy is also the setting in which a connectome advantage was reported (FlyGM), which is why it is the setting we test.

AuthorsOpenReview ↗

Response (2/2)

Closed-loop results for random graphs. Thank you; this was an omission, and it is now corrected. Under the bio-wired interface the DP controller also falls in 100% of episodes on the fly body, after BC, after six DAgger rounds and after 40 PPO iterations (164k steps); final PPO returns are 34 for the connectome and 38 for DP, episode lengths 116 and 130 steps. Appendix B now reports both. For reference, the expert falls in 4% of episodes, the MLP after BC+PPO in 17%, and the dense-IO connectome GNN after BC+PPO in 33%. The fly body therefore gives no closed-loop comparison between graphs under the bio-wired interface, and we no longer suggest that it does.

To check whether the imitation gaps are faithful to walking performance, we turned to a body on which every controller walks:

  • Hexapod, after behaviour cloning. All graph variants walk without falls under clean conditions, pushes, 1.5× body mass and 20 ms observation delay. The imitation ordering is reproduced (connectome worst, p = 0.014 vs ER). Closed-loop speed error is saturated (0.004 for every graph) except under observation delay, where the connectome is slightly best (0.034 vs DP 0.042 and ER 0.046; p = 0.025 vs ER).
  • Hexapod, new closed-loop RL. We fine-tuned every BC controller with recurrent PPO (614k steps, reward for tracking the commanded speed and yaw rate). Every graph controller raises its reward by about 5% (connectome 0.942 → 1.003, DP 0.948 → 1.021, ER 0.955 → 0.959), none falls under any perturbation, and connectome, DP and ER are indistinguishable on every metric (p > 0.1; Appendix L, Table 9).

So the reviewer's concern is partly borne out: imitation gaps between graphs do not translate into closed-loop differences on the hexapod. That does not rescue the connectome: it shows no closed-loop benefit either. The revised abstract, Appendix B and the Limitations state this boundary.

Non-significant claim in the abstract. We agree that a p = 0.10 result should not have been presented as a contribution in the abstract. We did two things:

  1. More seeds. We ran three more seeds per condition. At n = 6 (n = 3 at one tick), the connectome−DP gap is 0.027 ± 0.002, 0.023 ± 0.005, 0.012 ± 0.003 and 0.012 ± 0.002 (s.e.) at 0, 1, 2 and 3 ticks of delay. The reduction from 0 to 3 ticks is 0.016 ± 0.003 (p = 3×10⁻⁴), and relative to DP the gap falls from 24% to 13%, so it is not only that every target becomes easier.
  2. Out of the abstract anyway. The revised abstract leaves the delay result out and keeps to the sham-controlled shortcut result. Sec. 4.7 reports the delay result with its p-value and calls the latency reading a hypothesis, because three sub-updates per tick, which give the current observation the same two-edge reach as a two-tick delay, do not reduce the gap.

We thank the reviewer again for the constructive review and hope these changes address both concerns.

Reviewer_q8MfOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper considers whether a fly connectome, used as the fixed sparse graph of a message-passing controller, provides a useful inductive bias for gradient-based imitation of a locomotion policy for the body of the fly. The authors extract several fly connectomes, and train these in a gated graph network to control a fly body to walk by imitation learning. They build several null models of and interventions on the connectome to add or remove direct afferent-to-efferent edges. For body control, they consider a dense trainable encoder and decoder onto all afferent and efferent neurons, or a biologically wired interface in which each leg's sensors enter only that leg's afferents, commands enter descending neurons through a low-rank bottleneck, and each leg's actuators are read only from that leg's motor neurons.

With the dense interface, they show the connectome, degree-preserving and Erdős–Rényi graphs are statistically indistinguishable. With the biological interface, they show that imitation error grows with structural fidelity.

To test whether the scarcity of direct sensory-to-motor connections causes the penalty, the authors rewire pairs of connectome edges so that some sensory inputs reach motor neurons directly, while neurons retain their number of connections and synapse count. These swaps reduce the connectome's error (its penalty) to the level of the degree-preserving null, whereas a sham that rewires the same number of edges without creating direct connections does not reduce error. When all new direct connections come from the other legs' sensory neurons, the connectome penalty disappears; when they come from the same leg's sensory neurons, about half of it disappears; and when they come from descending neurons, it does not change. They show that this ordering of relative errors is the same across datasets.

Critical strengths
  1. The null-model and intervention design is thorough, with many null models that preserve degree sequence, hubs, modularity, reciprocity, block structure and signs; interventions that add and that remove shortcut edges; and a sham control. It is also good to see a replication of the ordered results in a second animal, a second sex and a second body. These are pretty convincing of the importance of direct sensory-to-motor paths in preserving function.

  2. The work supplies a useful methodological lesson for the growing literature on connectome-derived: that claims of a connectome advantage should be tested against Erdős–Rényi and flow-block-preserving nulls weighted in the same way as the connectome, not only against degree-preserving rewiring. Degree-preserving rewiring retains all out-degrees, so afferents without outputs stay output-less, while it scrambles the flow from afferent to efferent neurons. On a graph with many such afferents, this null can therefore produce an apparent connectome advantage.

Critical weaknesses
  1. VERY difficult to follow! The text reads as nearly 100% LLM-generated; this is consistent with the authors’ AI use statement, but that doesn’t excuse the AI-slop style writing. Sentences compress several results into undefined terms, and a reader must reconstruct the experiments from the appendices before the main text becomes intelligible. The final two sentences of the abstract are an example:

The wiring diagram withholds one-tick paths from sensory populations that predict the target; a fitted accessibility–demand statistic ranks 27 graph variants (ρ = 0.92). Under our implementation the published positive result does not survive an Erdős–Rényi baseline. "Accessibility–demand statistic" is defined only in Appendix E, ρ is not identified as a Spearman rank correlation with imitation error, and it’s not clear what the 27 variants are. "The published positive result" cites neither the paper (FlyGM, Jin et al. 2026) nor describes the result.

  1. The mechanistic claim in the title and abstract is not settled by the evidence, as the authors note in Section 4.7. Tolerated delay halves the gap, but three sub-updates per tick, which give the current observation the same two-edge reach as a two-tick delay, leave the gap unchanged. A residual gap of 0.014 to 0.018 survives every teacher manipulation. The linear accessibility model assumes uncorrelated inputs and bounded gain, and the authors state that neither of the two assumptions holds for the trained controllers. "The latency of sensory access" therefore names a hypothesis, and the title and abstract should say so.

  2. All biologically wired graph controllers fail at the task (100% falls, Appendix B), and the MLP reaches an imitation error 24% below the best graph and 40% below the connectome. The differences among graphs are therefore differences among failing controllers, measured by an imitation loss that Appendix J shows to be unrelated to closed-loop performance. For an inductive bias for control, the decisive question is whether the connectome helps a controller trained in closed loop by reinforcement learning with the same body and interface. The paper does not test this question; the evolutionary experiment in Appendix H changes core, objective and interface at the same time.

  3. None of the trained controllers tie parameters by cell type, under which connectome-constrained models have been shown to reproduce neural dynamics. With each neuron in the graph netowrk having its own free descriptor, roughly 20,000 per-neuron parameters can compensate for the wiring, and the connectome constrains only which neurons are connected. The "DMN-style" variant learns gain and threshold for each neuron without tying them by type, so it omits the defining constraint of Lappalainen et al. (2024) and (Duan, Dong and Fiete, NeurIPS 2025): neurons of one cell type share their parameters, and each synapse strength is given by its synapse count times its sign times a scale learned for each pair of presynaptic and postsynaptic cell types. The frozen model, the only setting in which the connectome produces a walking rhythm, has homogeneous weights across all neurons.

The Discussion states that a connectome is a strong prior for predicting the animal's own neural activity, citing Lappalainen et al. (2024), but a weak prior for control. The first claim rests on a model whose parameters are tied by cell type, whereas the paper tests the second claim only with untied models. The difference between the two claims may therefore come from the model class rather than from the difference between prediction and control. The paper already assigns every neuron a cell type, for its type-block null, so a type-tied controller can be trained without new data.

Questions for authors

n/a

3 comments
AuthorsOpenReview ↗

Response (1/3)

We sincerely thank the reviewer for a detailed and constructive report, and for recognising the null-model design and the methodological lesson it carries for the connectome-architecture literature. We reply in three parts: (1) writing and the title; (2) closed-loop control; (3) type-tied parameters and the Discussion.

Writing. We sincerely appreciate this criticism; it is fair. The abstract's last two sentences are a good example of the problem: they used a statistic defined only in Appendix E (now G), did not say that ρ is a Spearman correlation with imitation error, did not say what the 27 variants are, and referred to FlyGM without citing it. The revised abstract:

Fly connectomes have been proposed as architectural priors for neural controllers, and a recent study (FlyGM; Jin et al., 2026) reports that a policy wired by the FlyWire brain learns faster than random graphs. We test this for gradient-based imitation of fly walking with four connectomes, 14 random-graph null models and two ways of attaching the graph to the body. When an unconstrained encoder and decoder connect the body to all input and output neurons, no connectome is better or worse than a random graph. When sensors and actuators are attached as in the animal (each leg's sensors to that leg's sensory neurons, its actuators read from its own motor neurons), the real wiring is worse than random graphs, and error grows the more of the real wiring is kept. This replicates in a second animal of the other sex and on a hexapod robot. The cause is the scarcity of direct sensory-to-motor connections: edge swaps that keep every neuron's degree and synapse count but add such connections remove the penalty, a sham with the same number of swaps does not, and only connections from the other legs' sensory neurons suffice. A statistic measuring how easily each motor pool reaches the sensory inputs that predict its target ranks 27 graph variants by imitation error (Spearman ρ = 0.92). In our re-implementation, FlyGM's advantage over degree-preserving rewiring does not hold against Erdős–Rényi graphs. Our claims concern imitation error: in closed loop, biologically wired controllers fall on the fly body whatever their graph, and on the hexapod RL fine-tuning leaves all graphs indistinguishable.

The rest of the paper was revised in the same way:

  • the introduction now opens with the question and the setup, followed by four plain findings instead of a dense contribution list;
  • a "setup at a glance" paragraph names the tasks, graphs, interfaces and metric before any result;
  • every term is defined where it first appears, e.g. direct mass (the share of motor-neuron synaptic input that comes directly from sensory neurons), flow block (the afferent / intrinsic / efferent block structure), sham swap and the accessibility statistic;
  • the 27 variants are listed (Appendix G: all null models, partial rewirings, both intervention types, the sham and the source-decomposed shortcuts), and ρ is identified as a Spearman correlation with imitation error;
  • Figures 1, 2 and 4 are redrawn at print size.

The mechanism in the title. We agree that the title must not claim more than the experiments show. We keep it, with a precise reading (general response, point 3). "Latency of sensory access" refers to how many ticks pass before a sensory population can influence a motor pool, which the path structure fixes. The sham-controlled interventions establish that this structure carries the penalty. That the error is caused by the delay as such is a hypothesis; the delayed-teacher result (now significant at n = 6, p = 3×10⁻⁴) supports it in part, and the three-sub-update result shows that a pure hop count is not the whole story. The text states it as a hypothesis, the residual gap of 0.012–0.018 that survives every teacher manipulation is reported as unexplained, and the linearised propositions are explicitly scoped to idealised students whose assumptions the trained controllers do not satisfy (Appendix G).

AuthorsOpenReview ↗

Response (2/3)

Closed-loop failure and the MLP comparison. The reviewer is right that the bio-wired controllers fail in closed loop on the fly body, and we now report this for DP as well: both fall in 100% of episodes after BC, after six DAgger rounds and after 40 PPO iterations (returns 34 vs 38). We respectfully disagree with two of the inferences drawn from it:

  • The MLP is not a like-for-like comparator. It has dense input and output: every sensor reaches every actuator within one layer. Under our account it is the limiting case of an all-shortcut architecture, so a lower imitation error is exactly what we would expect. The relevant comparison is graph against graph under the same interface, and we make no claim that graph controllers beat MLPs.
  • Appendix J (now L) does not show that imitation loss is unrelated to closed-loop performance. It shows one cross-architecture inversion: the MLP has the lowest loss and the worst closed-loop speed error. Among the graph controllers, clean closed-loop speed error is saturated (0.004 for every graph), so there it is uninformative rather than unrelated. Under 20 ms observation delay the ordering reverses (connectome best, p = 0.025 vs ER), which we reported as a single-task hint.

Closed-loop RL with the same body and interface. We agree that this is the decisive test of an inductive bias for control, and we have run it.

  • Fly body. PPO from the BC initialisation was run for the connectome and DP: neither learns to walk within 164k steps, and the returns are indistinguishable (34 vs 38). PPO from scratch on the 59-actuator fly with a 21k-node graph controller is beyond our compute; from-scratch PPO on the much smaller hexapod with an MLP did not leave the standing solution in 410k steps.
  • Hexapod (new). Every variant walks here, so closed loop can discriminate. We fine-tuned each BC checkpoint with recurrent PPO (150 iterations, 614k steps, 16 environments; reward for tracking the commanded speed and yaw rate, −1 on a fall). Evaluation is deterministic, against the commanded velocity (Appendix L, Table 9; mean over 3 seeds):
Controllerspeed err BC → PPOyaw err BC → PPOreward BC → PPO
connectome0.095 → 0.0560.138 → 0.1990.942 → 1.003
DP0.095 → 0.0500.136 → 0.2020.948 → 1.021
ER0.095 → 0.0380.134 → 0.2280.955 → 0.959
MLP (lr 3e-5)0.103 → 0.1220.140 → 0.1550.944 → 0.772

PPO trades some yaw tracking for speed tracking and raises every graph controller's reward by about 5%. No graph controller falls under any perturbation, and connectome, DP and ER are indistinguishable on every metric (p > 0.1). The connectome's small advantage under observation delay after BC does not survive fine-tuning. The MLP is unstable under the same procedure: at lr 3e-4 all three seeds lose the gait (first-update KL 1.3 vs 0.08 for the graph controllers); at 3e-5 one seed reaches the best reward of any run (1.04), one reverts to standing and one degrades.

So closed-loop RL reveals no benefit of the wiring either. Together with the imitation results, this means the wiring is not a useful prior in either setting we can test. The paper's claim is, and is now stated as, a claim about imitation; Appendix B and the Limitations point to the closed-loop results.

The ES experiment. We agree that Appendix H (now J) changes core, objective and interface at once. The revision says so and no longer uses it as evidence about gradient optimisation; it characterises the frozen-module controller only.

AuthorsOpenReview ↗

Response 3/3

Type-tied parameters. We sincerely appreciate this suggestion, and we have run it. Tying does not rescue the connectome; it widens the gap.

  • Trainable GNN, walking task (3 seeds): connectome 0.211 ± 0.004, type-block null 0.202 ± 0.001 (p = 0.035), DP 0.173 ± 0.004, ER 0.162 ± 0.001. The connectome−DP gap is 0.039 (p = 3×10⁻⁴), against 0.030 untied.
  • DMN rate model tied by type (gain, threshold and synapse scale per type), fit to real fly gait (T3; explained variance, higher is better): connectome 0.145 ± 0.013, type-block 0.157 ± 0.010, DP 0.200 ± 0.009 (p = 0.005), ER 0.182 ± 0.006. Untied, the numbers were 0.143 / – / 0.189 / 0.161, so the ordering is unchanged.

Design (Appendix F, Table 4):

  • one 8-dimensional descriptor per cell type instead of per neuron (3,625 classes: cell types, with untyped neurons grouped by superclass and hemilineage);
  • a learnable synaptic scale per (pre-type, post-type) pair, multiplying sign × synapse count, as in Lappalainen et al. (2024).

Random graphs connect many more type pairs than the connectome, which gives them more free parameters. We therefore added the type-block null, which keeps the connectome's type-pair edge counts and hence nearly its parameter set (256k pair scales vs 251k for the connectome; DP 734k, ER 623k). The type-block null beats the connectome with an almost identical parameter set, and DP and ER beat it with more parameters, so parameter count does not explain the result.

Two reasons why we did not expect, and do not find, that untied parameters explain the penalty:

  1. The penalty concerns which paths exist, and no node or type parameterisation can create a path. A motor neuron's state at tick t depends on an input neuron's observation at tick t − k only if a path of length ≤ k joins them. This holds for any node-wise update, tied or untied. The interventions that remove the penalty change exactly this path structure, with every node's degree and strength held fixed.
  2. Untied parameters favour the connectome, not the nulls. The reviewer is right that per-neuron freedom can compensate for the wiring. But the connectome loses even with that freedom; tying removes compensatory freedom, so it can only make the wiring matter more, which is what we observe. Removing the descriptors entirely points the same way: connectome 0.211 vs DP 0.174, gap 0.037 (p = 0.009) against 0.030 with descriptors. (A small correction: each descriptor is 8-dimensional, so descriptors total 172k parameters rather than about 20k.)

We agree that the DMN-style variant trained per-neuron gain and threshold without tying, and was therefore not the model of Lappalainen et al. or of Duan, Dong and Fiete (NeurIPS 2025). The revision says so, adds the tied versions above, and cites Duan et al.

On the frozen model: it uses homogeneous weights by design, to ask whether the raw wiring produces useful dynamics without training; it is the only setting with a walking rhythm, and even there the connectome is worst on the downstream task (T3 explained variance 0.115 vs ER 0.161). The tied DMN result above is the trained counterpart.

Prediction vs. control in the Discussion. We agree: the sentence contrasted two claims tested with different model classes. It now reads: "Under the controllers we test, untied or tied by cell type (App. F), the wiring diagram is not a useful prior for gradient-based imitation; whether this differs from its value for predicting neural activity (Lappalainen et al., 2024; Duan et al., 2025) is not something our experiments separate, because those models use different parameterisations."

We thank the reviewer again. We hope the rewritten text, the closed-loop RL and the type-tied experiments address the main concerns, and we would be grateful if the reviewer would consider them in the final assessment.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General response (1/2): new experiments, writing, closed-loop control

We sincerely thank all four reviewers for their careful and constructive reports. All four credit the null-model family, the sham-controlled interventions and the replications across animals and bodies. Their criticisms fall into four groups. For each we have revised the paper and, wherever an experiment could settle the point, run it. This comment covers writing and closed-loop control; the next covers the mechanism claim and the robustness of the penalty. Each reviewer also receives a point-by-point reply.

Revised PDF. New or changed text is in blue; appendix and table numbers in our replies refer to the revision. Two appendices were inserted (D: dense-IO results, moved from the main text; F: robustness of the bio-wired penalty), so submitted Appendices D–K are now E and G–M. The main text stays within nine pages.

New experiments at a glance (3 seeds per condition unless stated)

ConcernNew experimentOutcome
closed-loop control (R1, R2, R4)recurrent PPO on the hexapod, same bio-wired interfaceevery graph +5% reward, no falls; graphs indistinguishable (p > 0.1)
cell-type tying (R1)GNN and DMN tied by cell type, plus a type-block nullgap widens (0.039 vs 0.030); ordering unchanged
delay effect significance (R2, R3)3 more seeds per delay (n = 6)reduction 0.016 ± 0.003, p = 3×10⁻⁴
normalisation, extraction (R3)two operators that keep total-input differences; extraction lossgaps 0.032 and 0.029; motor neurons lose 4.6% of input
graph vs training variance (R3)5 graphs × 1 init and 1 graph × 5 initss.d. ≤ 0.0055 against a 0.030 gap
architecture and budget (R3, R4)width, descriptors, 3× training, BPTT 128, 3 updates per tickgap 0.027–0.037 in every case

1. Writing (all reviewers; R1 most strongly). We sincerely appreciate this criticism: the submission was hard to read. Results were compressed into single sentences, and terms such as "direct mass", "flow block" and "accessibility–demand statistic" were used before they were defined. The revision rewrites the abstract and introduction in plain language, adds a "setup at a glance" paragraph (tasks, graphs, interfaces, metric), defines every term where it first appears, states one result per sentence, reduces the contributions to four plain findings, and redraws Figures 1, 2 and 4 at print size. The new abstract is in our reply to R1.

2. Imitation error vs. closed-loop control (R1, R2, R4). The paper asks whether connectome wiring is a useful prior for gradient-based imitation. That is the setting in which a connectome advantage has been reported (FlyGM's controllers are first trained by imitation), and it is what our title says. It is not a claim about closed-loop control, and the revision now says so explicitly, including in the abstract:

  • Full disclosure on the fly body. Under the bio-wired interface both the connectome and the degree-preserving (DP) controllers fall in 100% of episodes, after behaviour cloning, after six DAgger rounds and after 40 PPO iterations (164k environment steps); their final PPO returns are 34 and 38. Appendix B now reports both.
  • A body on which every controller walks. On the hexapod every graph variant walks without falling, and the imitation ordering (connectome worst) is reproduced (p = 0.014).
  • New: closed-loop RL on the hexapod with the same bio-wired interface, connectome vs DP vs ER. Recurrent PPO fine-tuning from each BC checkpoint (614k steps; reward for tracking the commanded speed and yaw rate) raises every graph controller's reward by about 5%. None falls under any perturbation, and connectome, DP and ER are indistinguishable on every metric (p > 0.1; Appendix L, Table 9). In closed loop the wiring shows neither a benefit nor a penalty.
  • We removed the two Discussion sentences that generalised from imitation to "control".
AuthorsOpenReview ↗

General response (2/2): mechanism claim and robustness

3. What the interventions establish, and what remains a hypothesis (all reviewers). The revision separates the two throughout.

  • Established: the penalty is carried by the scarcity of direct sensory→motor connections. Exact edge swaps that add such connections, while keeping every neuron's degree and in/out-strength, remove the penalty (connectome 0.206 → 0.171; DP 0.176). A sham with the same number of swaps but no new direct connections does not (0.200). Restricting the new connections by source: cross-leg sensory sources suffice (0.175), same-leg sources remove about half (0.187), and descending-neuron sources do nothing (0.203).
  • Hypothesis: that the relevant property is latency. We keep the submitted title and read "latency of sensory access" in the structural sense the interventions establish. With one propagation step per tick, a missing sensory→motor shortcut means that the other legs' sensory input reaches a motor pool only several ticks later (sensory–motor pairs within two hops: 31% for the same leg, 2.4% across legs). Whether the error arises from the delay as such, rather than from another property of short paths, is a hypothesis. The introduction says so, and the abstract makes no latency claim.
  • Delayed teacher, now at n = 6. The gap falls from 0.027 ± 0.002 to 0.023, 0.012 ± 0.003 and 0.012 ± 0.002 at one, two and three ticks of delay (s.e.; n = 3 at one tick; reduction 0.016 ± 0.003, p = 3×10⁻⁴; relative to DP 24% → 13%). Tolerated delay therefore more than halves the penalty; at n = 3 this was p = 0.10.
  • Why we still call it a hypothesis. Three sub-updates per tick give the current observation the same two-edge reach as a two-tick delay, yet they do not reduce the gap (expert: 0.037 vs 0.030; local teacher: 0.030 vs 0.027). A pure hop-count account is therefore not sufficient, and the paper says so.

4. Robustness of the penalty (R1, R3, R4). New controls, connectome vs DP, 3 seeds each (Appendix F, Table 4):

ControlconnDPgap
main result0.2060.1760.030
first 64 steps excluded from validation0.2410.2070.034
node width d=32 (batch 8; batch-8 d=16 comparator 0.206 / 0.176)0.2020.1740.029
no per-neuron descriptors0.2110.1740.037
3× longer training (9,000 updates)0.1860.1510.035
BPTT window 128 (batch 4, same samples per update)0.2050.1780.027
three updates per tick (batch 8; comparator gap 0.030)0.1830.1460.037
parameters tied by cell type (type-block null 0.202)0.2110.1730.039
symmetric normalisation0.1980.1670.032
global normalisation (counts / mean row sum)0.2020.1730.029

Every gap is significant (Welch p < 0.03), and none falls below 0.027. For the null models, the variance due to graph sampling (s.d. 0.0013 for DP, 0.0009 for ER) is an order of magnitude smaller than the gap. Added capacity, depth, gradient horizon and training time all lower every graph's error, but none of them closes the gap.

We thank the reviewers again; their questions led directly to these experiments, and we are happy to run further analyses during the discussion period.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.