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Under review as a conference paper at ICLR 2027

Causal Discovery via complexity-gated spiking neural networks

Abstract

We introduce X-SPK (Cross-channel SPiKing), a fully unsupervised, gradient-free spiking method for causal discovery in multivariate time series. Each channel is encoded by an independent fixed leaky reservoir and converted to equal-rate events; directed evidence is accumulated in a shared gate matrix via winner-take-all spike-timing plasticity and read out through the competition ratio . The underlying mechanism is geometric: if , conditioning on events of increases and concentrates 's near-future occupancy of its threshold-crossing region; this yields more threshold crossings, higher decayed trace mass, and a systematic WTA advantage in the causal direction. The method uses unified model settings with limited dataset-specific preprocessing and is evaluated on CausalRivers, Lorenz, Mackey-Glass, and TimeGraph (including non-stationary and confounded variants), reporting standard metrics against PCMCI+/GPDC, DYNOTEARS, VARLiNGAM, NeuralGC, CCM, and Rhino/RhinoLite across linear, nonlinear, and non-stationary regimes.

Primary area:
causal reasoning
Keywords:
causal discovery, time series, spiking neural networks, reservoir computing, spike-timing-dependent plasticity, unsupervised learning, graph structure learning, winner-take-all competition

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_8bfsOpenReview ↗
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Paper summary

The paper proposes X-SPK for causal discovery from multivariate time series. Each variable is processed by a fixed recurrent reservoir and converted into spikes at a shared target rate. A winner-take-all rule accumulates evidence from spike timing to score directed edges, without backpropagation. The authors provide a theoretical argument connecting event-timing asymmetry to causal direction under specific assumptions. Results show promising edge ranking on some nonlinear datasets.

Critical strengths

The combination of fixed reservoirs, equal-rate spike encoding, and competitive temporal updates provides a good way to score directed relationships without backpropagation. The self-channel competition is an useful design choice: it makes other channels compete against the target’s own recent activity when assigning credit. The comparison with a simple event-precedence score on identical reservoir features is informative. X-SPK improves AUROC on seven of eight tested TimeGraph settings, providing evidence that the competitive trace mechanism adds useful ranking information beyond the reservoir representation alone. This supports the proposed readout, although the gains in thresholded graph recovery are less consistent.

Critical weaknesses
  1. Each reservoir state is reduced to its norm and then a binary spike. The paper does not show that this preserves causal direction. Lemma 3.1 assumes the cause increases the effect’s reservoir norm, without establishing when this holds after random encoding.

  2. Winners depend only on fixed spike traces and self-bias, never on the learned weights. Training therefore accumulates discounted win counts. Synthetic pretraining changes the initial scores but not subsequent credit assignment, making its claimed role in learning causal discrimination unclear.

  3. The main proof fails in the two-variable case. It requires πij>1/(D−1)\pi_{ij}>1/(D-1), which exceeds one when D=2D=2. It also treats each true parent as the strongest external competitor, although the preceding lemma only compares it against non-causal variables. The argument therefore does not establish the result for either two-variable or general multi-parent systems.

  4. Equation 22 treats weights as cumulative counts, while Equation 7 discounts previous updates. With fixed decay, more data does not generally make the estimate concentrate as a sample average would. The later claim of asymptotically correct orientation is therefore unsupported.

5.Each target event credits only one channel, even when several variables jointly cause it. A stronger parent can suppress a weaker one, and an independent distractor can change existing edge scores. The paper does not establish when this competition preserves the causal graph.

  1. Every time step above threshold produces a spike, so sustained excursions generate repeated spikes and large traces. Equal spike rates do not remove this difference. Controls that vary persistence while keeping the causal graph fixed are needed to distinguish this effect from the proposed causal mechanism.
Questions for authors
  1. How should the proof of Theorem 3.3 be corrected for D=2D=2, where it requires πij>1\pi_{ij}>1, and for multiple parents, where a true parent need not be the strongest competitor? Does the claimed result still hold under the stated assumptions?

  2. Equation 22 omits the weight decay used in Equation 7. What guarantee holds for the actual discounted estimator, and does the claim of correct orientation with probability approaching one survive fixed decay?

  3. Under what conditions does a causal relationship in the original variables produce the reservoir-norm increase required by Lemma 3.1? Do the existing experiments distinguish this mechanism from differences in autocorrelation or above-threshold excursion duration?

  4. Do the gate weights affect any later credit assignments in the implementation? If not, how does synthetic pretraining improve causal discrimination beyond changing the initial edge scores?

1 comment
AuthorsOpenReview ↗

Corrected proof and the exact zero-lag condition (persistence ordering)

Thank you. Your points are precise and four identify real errors: Theorem 3.3 at D=2 and with several parents, Eq. 22, the description of the gate, and the persistence confound.

1. Lemma 3.1 (does thresholding preserve direction?) Not unconditionally, and the appendix does not prove it. We replace it by an explicit assumption (A4): the cause raises the effect's spike probability lag by lag, and a channel with no causal path to the target stays at its base rate. We make no claim for arbitrary nonlinear or inhibitory encodings.

2. Gate weights and pretraining. You are right. The winner at a firing of j is the argmax of the decayed traces (plus a self bias) and never reads W, so W is a write-only accumulator of decayed win counts. More training cannot change who wins; pretraining only shifts the initial W. We describe X-SPK as a decayed precedence statistic with competitive credit, not as a system that learns its dynamics, and report pretraining as an optional prior with an ablation.

3. Theorem 3.3. Both objections hold. At D=2, pi_ij = pi_ji = 1, so "pi_ij > 1/(D-1)" is false. The trace-dominance lemma beats only non-causal externals, so it fails when j has another parent of equal or larger elevation. And "self is independent of the externals" fails, since i's spikes drive j's own. Revision (new appendix): the theorem is stated for D >= 3, i a leading parent of j and j not upstream of i; a swap-coupling lemma conditional on self losing replaces the false step; the conclusion is that i beats j in win probability and, in the population limit, in the thresholded ratio W_ij/W_jj. Two assumptions are idealizations: self-decoupling and comparable self-predictability q_j <= q_i. Self-decoupling fails in part: over 168 unidirectional true edges the Spearman correlation between the target's self trace and the parent's trace at the target's firings has mean 0.11 but ranges from -0.53 (Lorenz) to 0.43-0.70 (TimeGraph c-series). At D=2 it reduces to q_j < q_i; several parents are covered only for a leading parent.

4. Eq. 22 vs Eq. 7. Agreed. Eq. 7 applies a column decay (1 - lambda), lambda = 5e-4, at every firing of j; Eq. 22 omits it. We replace Eq. 22 by the decayed sum; W_ij and W_jj share the discounts, so the ratio compares equally discounted counts. "Orientation probability -> 1" is restricted to N_j << 1/lambda = 2000 firings (about 100 here; omitted factor about 0.95).

5. One credited channel per event. A stated limit: credit is a shared budget, so a strong parent can suppress a weaker one. The competition is an explaining-away heuristic tested empirically, not guaranteed.

6. Persistence. You are right, and the issue is larger than posed. Mechanism: channels fire equally often, so at lag 0 a pair differs only in clustering. In our SCM (effect = cause + independent noise) the cause keeps long bursts (about 4.3 spikes), a fast-noise effect is fragmented (1.5-2), and the gate credits the persistent channel. The effect's first spike is not later (-0.3 steps), so our original explanation (a noisier effect spikes later) is withdrawn. Condition: at zero lag direction is correct when the observed cause is more persistent than the observed effect and reversed otherwise (exact: the effect's autocorrelation is a variance-weighted average of the cause's and the noise's). At fixed SNR it falls from 0.95 to 0.25 (driver AR 0.9) and from 0.80 to 0.05 (AR 0.5) as the effect's noise becomes as coherent as the cause; a plain autocorrelation comparison matches X-SPK at zero lag. Benchmarks: that ordering, with no adjacency information, matches or beats X-SPK's off-diagonal AUROC on Lorenz (1.00 vs 1.00) and Mackey-Glass (0.98/0.84/0.58/0.79/0.69 vs 0.65/0.66/0.57/0.69/0.52 across the five topologies): the source is the more persistent channel on 86-100% of true edges (68% in one), so these benchmarks are persistence-sortable like varsortability. We add the baseline everywhere. TimeGraph is not explained by it (0.41-0.48 vs 0.54-0.74) but is weak evidence (5 windows per set). Where precedence helps: with lag >= 1 inside the trace memory it is an independent cue (white driver, L=1-2: 0.90-1.00 vs 0.50-0.70 for autocorrelation rules), but this is not a comparison with a lead-lag baseline, and we claim no advantage beyond persistence. What stands: the repaired theorem and the identifying condition give a checkable account of when direction is right, and the condition correctly predicts the reversal (0.95 to 0.25). Given event times, the competition recovers direction irrespective of response waveform (AUROC 1.00 at lag 2, robust to 20% missed and 20% false events), which is what the event interface is for.

Questions. Q1, Q2: see 3 and 4. Q3: see 1 and 6. Q4: see 2.

Reviewer_T1sROpenReview ↗
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Paper summary

The paper proposes a method for learning the causal graph among the channels of a multivariate time series. Each channel is passed through its own fixed random reservoir, and the reservoir activity is turned into a spike train by firing whenever the activity exceeds a high quantile, so all channels spike at the same rate. A matrix of nonnegative gates is then updated online: whenever a channel spikes, the channel that spiked most recently before it, according to a decaying trace, wins a competition and has its gate toward that channel increased. An edge is declared when a channel's gate toward another, relative to that channel's self-gate, exceeds a fixed threshold. The full pipeline also includes pretraining the gates on synthetic linear time series generated from random graphs, a second refinement pass, and a hyperparameter search over thirteen parameters.

The theoretical part argues that if one channel causes another, the effect tends to spike shortly after the cause more often than the reverse, and that the expected gate increment along the true direction is therefore larger than along the reverse direction. A further remark and corollary address when cycles cannot persist. Experiments on chaotic and synthetic systems, a river-discharge benchmark and a brain-network simulation compare the method with standard constraint-based, score-based, linear non-Gaussian and neural Granger-causality baselines, and the paper claims that the method dominates in nonlinear and chaotic regimes.

I need to emphasize two points that I elaborate below. First, with the fixed threshold used for the headline numbers, the method outputs the complete graph on every synthetic benchmark for which these numbers are reported, and on the real benchmark the numbers coincide with those of a domain mask that forbids uphill edges. Second, the theory gives no guarantee about the graph the method outputs: the single theorem compares the expected increments of a true edge and its reverse under assumptions that are unproven or admitted to fail, and says nothing about the thresholded quantity that decides edges or about non-edges.

Critical strengths
  1. The underlying idea is simple and readable: turn each channel into events and credit the channel whose events most often precede another's.

  2. The appendix openly reports several diagnostics that cut against the main text, such as the equal-budget rerun of the neural baseline, the lead-lag control, and the density mismatch. However, these do not reach the main-text claims, and disclosing a problem in the appendix does not fix it.

Critical weaknesses
  1. The headline F1 and SHD are those of the complete graph. Predicting every possible edge reproduces the reported F1 and SHD exactly, with zero variance, on Lorenz (0.909, SHD 1), all five Mackey-Glass topologies, every TimeGraph row and Netsim. The paper admits this for TimeGraph and Netsim, but presents Lorenz and Mackey-Glass as wins (lines 300-304). The ablations print identical F1 for the same reason, which the paper reads as robustness of the threshold (lines 1036-1037). The complete graph, the trivial competitor for F1, is never reported. These numbers carry no information beyond the number of nodes and edges.

  2. The real-data result is the elevation mask. On CausalRivers, predicting every downhill edge reproduces the reported F1 and SHD at all six graph sizes, and a random ranking inside the mask matches the reported AUROC within 0.03 at every size except the smallest. The paper does not say whether the baselines get the mask. If they do not, the largest margin in the paper comes from the prior and not from the method.

  3. The pipeline is tuned on the test benchmarks. The thirteen hyperparameters, including the edge threshold, were chosen by a 150-trial search against the true graphs of the same benchmarks that are reported (lines 887-892), and the synthetic pretraining graphs are built to mimic the river topology (lines 877-879). "Fully unsupervised" (line 11) does not describe this pipeline.

  4. The appendix retracts the main claim.

    • With the same tuning budget, the neural Granger baseline beats the method on 5 of 14 datasets, and only one Mackey-Glass topology remains an uncontested win (lines 664-668, 772-789).
    • A plain count of how often one channel's spikes precede another's, with no learning, comes within 0.07 AUROC of the method on 6 of 8 TimeGraph configurations and beats it on one.
    • What remains of "dominates nonlinear and chaotic regimes" is an AUROC lead on a three-node system, one Mackey-Glass topology and two small TimeGraph configurations.
  5. The ablation of the trace is degenerate by construction. Without the trace, the self-gate wins every competition, so no edge is ever credited. Chance-level AUROC is then what any constant score gives, and it says nothing about temporal credit.

  6. The theory does not cover the output graph.

    • The central claim, that a cause's spikes precede its effect's more often than the reverse, is never proved: the promised derivation is not in the appendix (lines 172-173).
    • The theorem is stated with no assumptions in the main text (line 203). Its proof needs mixing, an exchangeability approximation, a lag-by-lag assumption, and an inequality the authors say holds only "on the majority of tested edges" (lines 1196-1197).
    • With two channels, the theorem's conclusion is exactly the strict form of that inequality.
    • The theorem says nothing about the thresholded ratio that decides edges, or about non-edges.
    • The acyclicity corollary only says that an acyclic graph has no cycles.
    • The complexity and MDL framing is cosmetic.
  7. The baselines are questionable.

    • PCMCI+ with the GPDC test is reliably below random AUROC on Lorenz and all Mackey-Glass topologies, which suggests inverted scores.
    • "Rhino" in every table is a Lasso-VAR stand-in.
    • The larger graphs have no nonlinear baseline.
    • Prior reservoir-based causal discovery and event coincidence analysis are not cited. The paper's directional statistic is that analysis's trigger coincidence rate.
Questions for authors
  1. For which rows does the fixed-threshold output coincide with the complete graph? Please add the complete-graph and empty-graph rows to every results table (for CausalRivers, the masked complete graph), and correct the main-text claims on Lorenz and Mackey-Glass accordingly.

  2. Do the baselines receive the elevation mask and the same preprocessing on CausalRivers? Please report the method without the mask and without synthetic pretraining, at all graph sizes.

  3. How do the results change when the hyperparameters, including the edge threshold, are chosen without access to the true graphs of the reported benchmarks? For example, choose them on held-out benchmarks only.

  4. Which main-text claims survive the equal-budget and longer-lag reruns in the appendix? Please move those results to the main text and revise the "dominates" claim (line 299).

  5. How does the method compare with the untrained lead-lag count on Lorenz, Mackey-Glass and CausalRivers, and with that count computed on the raw signals rather than the reservoir spikes?

  6. Please state the main theorem with all of its assumptions, and say which of them were checked on which data. With two channels, what does the theorem add to the assumed inequality? How does it relate to the ratio that actually decides edges? Where is the proof of the lemma on spike precedence?

  7. Why is PCMCI+ with GPDC consistently below random AUROC? How are continuous edge scores extracted from each baseline?

  8. How many ensemble members does each reported number use? Please report single-initialization results.

  9. Please relabel "Rhino" as the Lasso-VAR proxy it is, add a nonlinear baseline on the larger graphs, and position the method against reservoir-based causal discovery and event coincidence analysis.

Typos (not counted against the paper):

  • "Equation equation 1" and similar, throughout (lines 85, 145, 177, 198, ...).
  • Line 278: "PCMCI+/PCMCI+/GPDC (Runge et al., 2019)" --> "PCMCI+ and PCMCI+/GPDC (Runge, 2020)".
  • Table 1: "|E| ≈ 5" for Lorenz --> "|E| = 5"; please list the edges.
  • Table 6: the selected trace decay 0.688 lies outside its own search range [0.70, 0.98].
1 comment
AuthorsOpenReview ↗

Metric audit and corrections: what the evidence supports after the fixes

Thank you for an unusually careful review. We checked your numerical claims against our raw files; the main ones are correct and we concede them. Checking also exposed an error in our metric code. Numbers below are from the corrected analysis.

1. Metric error. AUROC/AUPRC flattened the score matrix including the diagonal: always zero for X-SPK, often nonzero for baselines (self-links). This favoured X-SPK. We now score off-diagonal pairs only and recompute all tables (X-SPK's AUROC drops 0.01-0.10). PCMCI+'s below-chance AUROC (0.42 at D=5) is this artifact, not score inversion (0.48 off-diagonal, 0.52 transposed).

2. Complete graph. Confirmed: on Lorenz, all Mackey-Glass topologies, every TimeGraph set, Netsim and the Tigramite benchmark, thresholded F1/SHD equal the complete graph's with zero variance (42 of 50 dataset rows). Presenting them as wins was wrong. We add empty- and complete-graph rows everywhere and report these datasets by AUROC/AUPRC. The permutation-null readout predicts 22-37% of pairs and is below the complete graph's F1 on Lorenz and Mackey-Glass.

3. CausalRivers and the mask. Confirmed. X-SPK's F1/SHD equal the masked complete graph's (exactly on all 10 subgraphs at D=5, 10; to three decimals at D=15-30). A mask-only score has off-diagonal AUROC 0.74-0.79 across D=5-30 against X-SPK's 0.76-0.85, and X-SPK's AUPRC exceeds the mask-only AUPRC at every size, but within allowed pairs its AUROC is 0.53-0.65. Only X-SPK received the mask. Without it (appendix D=5, 10; no mask and no CausalRivers preprocessing, which we did not state) X-SPK reaches 0.59/0.59 against 0.47-0.58 and 0.53-0.56 for PCMCI+, DYNOTEARS, a Lasso-VAR proxy (relabelled from "Rhino") and VAR-LiNGAM, ahead of the best baseline by 0.005 and 0.03: not a clear lead. We will state that the results largely reflect the mask and do not claim a mask-free advantage.

4. Tuning on benchmarks. Correct. The Optuna pool contained Lorenz, three Mackey-Glass topologies and two CausalRivers D=6 graphs (one realization each); one Tigramite set was held out. The stored report does not record the trial count (paper: 150; script default: 60). Re-selecting on the pool the paper describes and evaluating on 12 other datasets, the held-out configuration is lower on average (0.647 vs 0.669) and on 8 of 12 (Lorenz 1.00 to 0.93, mg_dense_hub 0.67 to 0.55, tg_c1_n8 0.56 to 0.41); one sweep seed. We will report these as the zero-shot numbers and correct Table 6 (omitted second-pass multipliers 0.595/0.725, margin 0.046), the trace-decay range ([0.55, 0.98]) and the description of pass 2 (a residual rule with reduced rate and decay, not a second sweep).

5. Persistence, lead-lag, baselines (off-diagonal AUROC, 10 seeds). X-SPK beats untrained lead-lag counts and NeuralGC on Lorenz (1.00 vs 0.60 and 0.80) and most Mackey-Glass topologies (0.52-0.69 vs 0.38-0.50 and 0.47-0.60), but a pure persistence ordering (acf5_i - acf5_j, no adjacency information) does at least as well (Lorenz 1.00; Mackey-Glass 0.98/0.84/0.58/0.79/0.69 vs X-SPK 0.65/0.66/0.57/0.69/0.52); the source is more persistent on 86-100% of true edges. We add this baseline everywhere and narrow the claim. TimeGraph (5 windows per set, weak) is not explained by persistence (0.41-0.48). On an easy lagged tanh-coupled family the raw lead-lag count beats X-SPK by 0.10-0.16. We will add event coincidence analysis (Donges et al., 2016) to related work, rerun PCMCI+/GPDC and CCM with the corrected metric, and fix your typos.

6. Mechanism and theory. At zero lag all channels fire equally often, so direction is read from spike clustering: the more persistent channel is credited as the cause. This is correct when the effect's extra variance is less persistent than the driver and reversed otherwise (0.95 to 0.25), so zero lag reduces to persistence ordering; with lag >= 1, precedence adds an independent cue. Theorem 3.3 is restated and repaired for D >= 3 and a leading parent, with explicit assumptions, one of which (self-decoupling) fails in part (see our reply to 8bfs). At D=2 it is equivalent to q_j < q_i, as you suspected. We drop the MDL claim (the gate computes no code lengths) for an Occam-style prior.

7. What stands. Beyond the concessions: X-SPK's AUPRC exceeds the mask-only score at every CausalRivers size; on Lorenz and Mackey-Glass it beats untrained lead-lag counts and NeuralGC; on TimeGraph, where persistence does not explain the results, it is ahead of NeuralGC on the mean in 6 of 7 sets (tg_c2_n6: 0.74 vs 0.59-0.61 for lead-lag counts); null data give AUROC 0.50 at every spike rate; and given event times the competition recovers direction whatever the response waveform (AUROC 1.00 at lag 2, with 20% of events missed and 20% false; see general comment). We report threshold-free metrics and do not claim state-of-the-art accuracy.

Reviewer_5rsDOpenReview ↗
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Paper summary

The paper presents a spiking model for causal discovery, i.e., to assess whether events in one time series cause events in others. To this end, a STDP-like learning rule is employed. Experiments are conduced and compared to baselines for several reference datasets, reporting favorable performance for the proposed X-SPK.

Critical strengths

The paper provides detailed experiments and comprehensive results. The spiking model proposed is argued to be biologically plausible and superior to baseline models in many regimes.

Critical weaknesses

The approach and the central ideas of the paper are not explained at all:

  • what does it mean to recover a "directed graph" from time series?
  • What does "causal discovery" from data even mean?
  • Can you even detect causality from data? It seems to me all you can detect is correlation Furthermore, the used model cannot be understood from the explanations either as many terms are not explained ("Optuna search"? "pass-2-refinement", ...), since it is assumed that even very technical and specialized ones, are known to readers. This makes the main paper very hard to read and understand. in addition, the impact of the results may be evident to people in that particular community, but not to others, in particular not to me.
Questions for authors
  • What is the added value of the spike encoding and the STDP learning rule?
  • What is the merit of the presented benchmarks, as they almost all seem to be explicitly constructed toy models?
  • The model contains many parameters, what actual values were used and how were these selected?

I realize that some of these questions are addressed in the appendix, but this must go to the main text!

1 comment
AuthorsOpenReview ↗

Plain-language explanation, parameter selection, and what the evidence supports

Thank you. Your central complaint, that the main text assumes specialist vocabulary and never says what problem is solved, is fair; we will fix it in the main text, not the appendix.

1. What does "recovering a directed graph from a time series" mean? We observe D quantities over time, e.g. the water level at D river gauges. The goal is a "who influences whom" diagram: one node per quantity and an arrow i -> j when changes in i are followed by changes in j. "Directed" means "the upstream gauge drives the downstream one" differs from the reverse. We will add a subsection, "What causal discovery means here", with this example and a three-node picture.

2. Causation or only correlation? Correlation alone cannot give direction. The method uses the one asymmetry observational series carry: causes come before effects. It scores how often one series' events precede another's, which is evidence for a direction only under the usual assumptions (the cause raises the chance of an event in the effect; no unobserved common driver). Otherwise the output is a lead-lag graph, not a causal graph; the Introduction will say so. A caveat from the other reviews: at zero lag the direction we read is which series is more persistent (longer bursts), and a plain autocorrelation comparison does as well, as with varsortability. The paper will state this condition and report such baselines in every table.

3. Why spikes and a STDP-like rule? See our general comment for what we defend and concede. In short: each series becomes binary events (when a small random recurrent network, a "reservoir", is unusually active), and a local competition rule credits, at each event of series j, the series whose recent events best precede it. 4. Are the benchmarks toys? Ground truth exists mainly for simulated and known-mechanism physical systems; we use both (Lorenz, Mackey-Glass, TimeGraph; CausalRivers, a real river network). Other reviews found problems we confirm. (a) In the main CausalRivers table only X-SPK got an elevation prior (upstream-to-downstream pairs only). The prior alone has AUROC 0.74-0.79 against X-SPK's 0.76-0.85, F1/SHD equal the masked complete graph's, and within the allowed pairs X-SPK's AUROC is 0.53-0.65: the results largely reflect the prior. (b) Without it (appendix, D=5 and 10) X-SPK reaches about 0.59 against 0.47-0.58 for baselines, not a clear lead. (c) Our AUROC code scored the diagonal of the score matrix, which favours X-SPK; we corrected it and recompute all tables off-diagonal.

5. Parameters and their selection. Table 6 moves to the main text with the three parameters it omitted (second-pass rate and decay multipliers 0.595 and 0.725; margin 0.046). Optuna is a hyperparameter search library: we evaluate proposed parameter sets on tuning datasets and keep the one closest to the ideal on four objectives (F1, AUROC, AUPRC, SHD). The selection was not held out: the pool included Lorenz, three Mackey-Glass topologies, Tigramite sets and two CausalRivers D=6 graphs, so "zero-shot transfer" was wrong for Lorenz and two of five Mackey-Glass topologies. We reran the selection on the pool the paper describes (150 trials, no warm start) and tested both configurations on 12 other datasets: off-diagonal AUROC is lower for the held-out configuration on average (0.647 vs 0.669) and on 8 of 12 (Lorenz 1.00 to 0.93). One sweep seed: we read the direction only. We will report the held-out numbers as the zero-shot ones.

6. Terms. Defined at first use: pass 2 is a modified update rule (lower spike rate, shorter memory, a margin the winner must beat), not a second sweep; the permutation-null readout keeps pairs whose score exceeds what time-shifted copies of the series give; F1 is the accuracy of the predicted edge set and SHD counts edge errors. The fixed threshold predicts every edge on most synthetic datasets, so F1/SHD there equal the complete graph's; we add complete-graph and empty-graph rows and report those datasets by AUROC/AUPRC.

7. Theory. The proof of the main theorem had real errors (it fails for two nodes and for several causes). We restate it with explicit assumptions, repair the proof and label the idealized assumptions (see our reply to 8bfs). We drop the acyclicity claim unless an ordering hypothesis holds, and the MDL framing (an Occam-style prior instead).

8. What holds up. (i) On Lorenz and Mackey-Glass the score beats untrained lead-lag counts on the same events (1.00 vs 0.60; 0.52-0.69 vs 0.38-0.50) and NeuralGC on Lorenz (0.80). (ii) It needs no gradient training and gives one interpretable score per ordered pair. (iii) With a lag of at least one step, precedence adds information that persistence does not, and at zero lag we state exactly when the direction is right. What does not hold up: accuracy beyond a persistence ordering, and any mask-free advantage on CausalRivers.

Comments on the paper

1 comment
AuthorsOpenReview ↗

# Comment to all reviewers: what do spikes add?

Thank you all. The three reviews share one question: what does the spike representation contribute? Our answer has a part we defend and a part we concede.

What we defend: spikes as a natural, sparse encoding. Each channel is reduced to a few binary events, thresholded at its own top-r%, so all channels fire equally often (event density cannot serve as a cue; on null data AUROC is about 0.50 at every rate). The credit-assignment gate consumes only event times, uses a local update and needs no gradient training, so what counts as an event can change without changing the competition. The motivation is that causal direction is often hidden in the bulk of the data, where channels are correlated at zero lag (financial returns for example), and reveals itself at salient events, such as a recognizable motif in the driver that the other channels then follow; a sparse event encoding keeps those moments and discards the bulk. This is a motivation, not a result. We simulated it (dense common-mode correlation, rare driver motifs, followers echoing them or responding with a different shape, lag 0-3). With strong echoed motifs every method reaches 0.94-1.00, so events show no advantage. With a different response shape, the competition step recovers direction from the true event times (AUROC 1.00 at lag 2, robust to 20% missed and 20% false events), but our norm trigger does not deliver those times (0.65-0.87), while VAR-lasso reaches 0.92-0.94. A trigger that localises responses of unknown shape is therefore the open part of the idea.

What we concede: the norm-based trigger does not take the method beyond persistence. Our events fire when the reservoir-state norm exceeds a threshold, which is an energy detector. Empirically: (i) a leaky integrator of |x| matches the reservoir (AUROC 0.66-0.68 vs 0.654); (ii) at zero lag the direction X-SPK reads is which channel is more persistent, and a plain autocorrelation comparison matches it; (iii) on Lorenz and Mackey-Glass a pure persistence ordering does at least as well as X-SPK, although X-SPK beats untrained lead-lag counts there; (iv) precedence adds information only with lag of at least one step, and we show that against autocorrelation rules, not against a lead-lag baseline. Our original hope, that a noisier effect spikes later even at zero lag, was tested and is not supported (-0.3 steps). Events that fire on completion of a recurring pattern might go further, but unsupervised reservoir-state events recover true completions at chance (0.50-0.56 vs 0.45) in our test, so this stays future work.

What changed because of your reviews (details in the individual replies): a metric error in our code (AUROC included the score diagonal, which favoured X-SPK) is corrected and all tables recomputed; the tuning pool is described as it was, with a held-out re-selection (mean off-diagonal AUROC 0.647 vs 0.669, lower on 8 of 12 datasets); thresholded F1/SHD are reported against the complete graph and the elevation-masked complete graph, which they equal; Theorem 3.3 is restated with its assumptions and the proof repaired; and the main text gets a plain-language subsection on what causal discovery means here.

What we claim after revision. X-SPK is a competitive-credit precedence statistic over rate-matched spike traces. At zero lag it reads the persistence ordering of the channels under a stated condition; with lagged coupling it adds precedence information. The spike encoding is a sparse, event-based interface; we do not claim that the norm trigger adds accuracy beyond simple persistence and lead-lag baselines.

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

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