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Under review as a conference paper at ICLR 2027

Identifying Neural Source Dynamics from Unknown Local Interventions

Abstract

Electroencephalography (EEG) observes brain-source activity through a linear forward model computed from head anatomy, which tells where each source appears at the scalp but not how sources drive one another. Where baseline activity reaches only part of the source space, these dynamics stay unidentified however many trials or sensors are recorded. We show that local interventions with unknown targets and strengths can supply this missing information. For linear source dynamics with known initializations, a one-step change to how one source receives input makes the contrast with matched baseline EEG rank one: the forward model identifies the changed source and calibrates its response history, and these histories, combined with initialization responses, determine the source dynamics without baseline reachability and without identifying the interventions. We establish sufficient identification conditions, a closed-form estimator and an error bound. In simulated EEG on four anatomies derived from magnetic resonance imaging (MRI), where baseline activity reaches four of twelve sources, unknown interventions recover the dynamics in 32/32 systems, whereas baseline-only estimators succeed in none, even with an invertible forward model, and explicitly constructed alternative dynamics reproduce every baseline mean. When baseline data suffice, our estimator is also more reliable than a matched spectral method.

Primary area:
applications to neuroscience & cognitive science
Keywords:
causal representation learning, identifiability, unknown interventions, neural dynamics, electroencephalography, system identification

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_CxT2OpenReview ↗
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Paper summary

This paper proposes an intervention-based identification framework—supported by rigorous mathematical derivation—to address the challenge traditional system identification methods face in reconstructing a complete dynamic system when state-space coverage is insufficient. The theoretical approach offers a degree of novelty, and experimental results provide preliminary validation.

Critical strengths
  1. The paper addresses the issue of system identifiability when the baseline state fails to cover the entire source space, noting that simply increasing the number of trials or sensors does not necessarily eliminate structural unidentifiability; the research motivation is well-founded.
  2. The authors construct a rank-one matrix based on the response difference between the intervention and baseline conditions; they identify the intervention target and calibrate the response history using the known lead-field, subsequently recovering the state transition matrix by exploiting shift relationships within the observation matrix. The entire process rests on a clear mathematical foundation rather than relying solely on black-box neural networks.
  3. The paper establishes sufficient conditions for identifiability, separately discussing source space coverage, intervention exposure, anatomical distinguishability, and temporal observability; it also provides bounds on conditional stability, aiding the understanding of the factors contributing to the method's success or failure.
Critical weaknesses
  1. The real-world EEG experiments primarily validate the transferability and reproducibility of spatial responses but do not actually reconstruct the neural source dynamics matrix F, consequently, they are insufficient to demonstrate that the method can achieve the core functions proposed in the paper within a real neural system.
  2. The method is relatively sensitive to non-local interventions and forward model mismatches, and its identification performance depends on the extent of intervention coverage and the numerical conditioning of the response history. Its reliability in larger-scale scenarios, under real-world noise, and in complex intervention environments remains to be verified.
Questions for authors
  1. The most significant theoretical results in this paper rely on a specific intervention mechanism. The authors represent the system as shown in Equation 1, implying that the intervention alters only a single row of the state transition matrix—meaning it changes the input-reception rule for just one neural source—and that this change persists for only one time step before the system immediately reverts to its original dynamics. While this assumption is reasonable for theoretical derivation, a clear gap remains between it and actual neural stimulation processes. Real-world electrical stimulation, optogenetic stimulation, or other neural interventions may simultaneously affect multiple neural sources, introduce direct external inputs, and induce sustained physiological changes. In such cases, observed response differences cannot necessarily be attributed to a change in a single input-reception row, nor does the rank-one structure necessarily hold. (1) In existing neural intervention experiments, which specific stimulation mechanisms can be reasonably approximated as a single-step change in the input-reception rule of a single neural source? (2) Do the existing identification theorems still hold when an intervention affects multiple neural sources simultaneously or when the intervention effects persist over multiple time steps? (3) Is it possible to establish a more systematic quantitative relationship between the degree of non-locality of the intervention and the error in dynamic recovery, and to clearly define the boundaries where the method fails?
  2. The primary contribution of this paper is the use of unknown local interventions to recover neurally derived dynamic relationships that are unidentifiable from baseline data. However, the paper's analysis of real EEG data focuses primarily on the transferability of spatial response patterns across different stimulus intensities and the impact of trial averaging on the reproducibility of dipole fitting. The authors explicitly acknowledge that these analyses neither recover the true neurodynamic matrix F nor validate the accuracy of the initial state mapping K. The authors should more clearly distinguish between what is validated by the real EEG experiments and the capabilities claimed by the theoretical method, avoiding the conflation of spatial response validation with the validation of neurodynamic identification.
2 comments
AuthorsOpenReview ↗

Response to Reviewer CxT2

We thank the reviewer for the positive assessment and for questions that sharpen the scope of the paper. Section numbers refer to the revised PDF, where new text is in blue.

W1/Q2. What the real recordings establish. We agree. Each claim of the paper rests on a different kind of evidence:

ClaimEvidenceEstablished
Identifiability beyond baseline reachabilityTheorem 1; exact checks to 10−1310^{-13}within the model
Finite-sample recoveryfour MRI-derived leadfields; 900 new casesin simulation
Repeatable sensor directionLocalize-MI recordings, eleven siteson real recordings
Neural FF, KK and interventionsnot tested hereneeds a perturbation experiment (J.3)

The recorded direction is measured on injected-current responses, that is on the stimulation artifact and not on neural responses. Its repeatability is the spatial prerequisite for calibration and for artifact correction. Recovery of the dynamics rests on the theory and the simulations.

Q1(1). Which stimulation mechanisms fit the model? The identification result needs less than Eq. 1 suggests: a rank-one contrast with a source-specific response history. A brief focal additive pulse with unknown target and amplitude gives the same structure, so labeling, calibration, column completion and the shift solve are unchanged (§4.1, Appendix A.7). At matched contrast SNR, Direct without any change recovers 26/32 and 32/32 systems at 4,608 and 18,432 episodes, against 24/32 and 32/32 for receiving-row changes (Appendix B.9). When both mechanisms act together, reversing the sign of the initialization separates them exactly (Appendix F). The closest existing schedule is a paired-pulse design: a conditioning stimulus sets the initial state, a brief focal test stimulus perturbs one source, and matched episodes omit the test stimulus. It exists noninvasively (paired-pulse TMS-EEG) and with intracerebral stimulation and scalp EEG, where the stimulated contact is known (323 sessions in 36 patients). Whole-brain models observed through a leadfield have been fitted to these recordings and to TMS-evoked EEG (Momi et al., 2023, 2025). Dynamic clamp gives direct control of a state-dependent current, and J.3 lists what such an experiment has to establish.

Q1(2). Multiple sources or persistent effects. Persistent effects are covered through a different contrast: comparing durations that differ by one transition, at equal elapsed time, gives a rank-one contrast with the same response history, OT((F+De)ℓ+1−F(F+De)ℓ)Rs=(OTej)(ve⊤(F+De)ℓRs)O_T\big((F+D_e)^{\ell+1}-F(F+D_e)^\ell\big)R_s=(O_Te_j)\big(v_e^\top(F+D_e)^\ell R_s\big). Recovery is exact without noise for durations up to three transitions, and with noise longer durations need more trials (Appendix A.7, Proposition 7). A change in a second source makes the contrast rank two and falls outside the theorem. The data reveal this case before it affects recovery (next point).

Q1(3), W2. Non-locality against recovery, and where the method stops. We varied the coefficient of a second, neighbouring row relative to the primary one (80 systems, 98,304 trial equivalents). A test on the data compares each contrast's second singular value with a noise replicate built from two halves of the same trials (Appendix B.6).

Second row / primary coefficient00.0250.050.10.20.5
Systems recovered (of 80)80807967180
Detected by the data test1.2% (false alarms)92.5%100%100%100%100%

The effect is a bias: a fourfold budget changes one count (67 to 68). The method tolerates a second row of up to 5% of the primary coefficient, recovery degrades from 10%, and every violation that harms recovery is detected.

W2. Forward-model mismatch, noise, scale and reliability.

  • Forward model. The sensitivity the review notes came from one step of the estimator, which replaced the measured first block of each response history with the supplied leadfield. Keeping the measured block gives 154/160 recoveries at a 5° pattern error in every column (exact leadfield: 155/160; as submitted: 37/160). A twofold skull-conductivity error gives 13/16 and 14/16, against 14/16 with the nominal head model. The remaining requirement is correct source labels (Appendix I.7).
  • Noise. In the joint test of the general response (point 4) the noise is recorded EEG background, and the corrected estimator recovers 30/32 and 31/32 systems (Appendix J.5.3).
  • Scale. With repeats per condition held fixed, which is 4 and 16 times the budget, Direct recovers 77/80 systems at 24 sources and 60/80 at 48 (Spectral-local: 65/80 and 19/80). At the fixed budget of 98,304 trial equivalents it recovers 42/80 at 24 sources and none at 48 (Appendix B.7).
  • Reliability. On 800 unselected new cases Direct recovers 91.4% (general response, point 3; Appendix B.8).

We would be glad to run any further check and to hear what else would strengthen the paper.

Thank you for addressing my questions—best of luck to you!

Reviewer_furdOpenReview ↗
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Paper summary

The research paper investigates how to identify the linear source dynamics F under the known anatomical forward mapping L and the known initialization mapping K, by matching the baseline and the average response of the intervention. The intervention only changes one receiving row in a discrete transition, and the target points and coefficients are unknown. The key observation is that the difference satisfies ΔH_e = (O_T e_(j_e ) )(v_e^⊤ R_s ): nonzero differences give the direction of the single-source response history; the first sensor block matches with the known, non-proportional leadfield column, thereby restoring the target points and scale. If the initialization and the exposed target points jointly cover all the sources, and the time observation stack has full column rank, then O_T can be completed first, and F can be obtained through time shifting, without requiring the baseline reachability matrix to be full rank. The authors simulated the dynamics on four MRI anatomical mappings, demonstrating the recovery when the baseline mean only covers 4/12 sources, the comparison with Spectral-local when the reachability is complete, and the boundaries of noise, scale, intervention non-locality, and forward model error. The real EEG analysis was for the spatial response of injected current artifacts, which was not regarded as the verification of neural F recovery.

Critical strengths

The identification of objects and the handling of indistinguishable boundaries are accurately carried out. What the paper truly needs to restore is the historical column, rather than the unknown intervention parameters. The sufficient condition of Theorem 1 does not misappropriate the complete baseline reachability. The appendix also distinguishes the ambiguity of coordinate transformation from the absence of dynamic excitation, and gives the baseline equivalent class ΔFR=0 under the reversible L, and demonstrates that response propagation can be restored with fewer target points, thus not mislabeling the coverage conditions of this algorithm as universally necessary conditions. These complementary positive and negative results constitute a credible theoretical contribution.

The core experiment can distinguish between insufficient information and numerical estimation failure. Partially reachable systems have a clear block structure, unexposed controls, and alternative dynamics that maintain the mean of all protocols; known reversible forward mappings and full budget baselines cannot compensate for the unexcited directions. The full reachable comparison uses the same information and paired uncertainty according to seed clustering, retains invalid results, rather than only reporting successful cases. The physical forward mismatch experiment actively reveals that "correct labels" do not mean "correct dynamics". The evidence supports the identification conclusions within the model, rather than just the failure of a certain baseline.

Critical weaknesses

The key bridges related to neural experiments have not been verified yet, limiting the applicability of the contributions. The actual use requires the simultaneous establishment of: the calibrated source state K, the accurate L, the changes in the receiving row of a single discrete transfer, and the available first artifact-free transfer samples. The authors explicitly admit that continuous-time local modulation usually does not maintain the discrete-time single-line structure, the stimulus position does not equal the known source state, and the real EEG part has not verified these conditions. This belongs to the acknowledged application limitations, not a theoretical error. Its impact has quantitative basis: merely changing the assumed skull conductivity, the precise response and all correct labels still show a median F error of 11.17%–27.52%, and all non-nominal conditions do not reach the joint success threshold. Therefore, the current contribution is more suitable as a controlled model identification method, but not sufficient to support the reliable deployment of actual EEG.

The transferability of "reliable recovery" under limited budgets is still weaker than the intuitive perception of the main success rate. For the new seed group with the same 12 sources and 98,304 trial equivalents setting, Direct decreased from 155/160 in the main confirmation to 63/80; even with 48 sources increased to 1,572,864 trial equivalents, it remained at 60/80. The authors have associated some failures with weak exposure and fully reported the results, but the main stability boundary depends on the unknown true historical error and condition number, and the numerical validity and exposure gating do not provide a certificate of the correctness of the recovery. For example, even in the unexposed control, there was a limited and over-gating fit that still achieved a F error of 74.79%. Here, it is not accusing the gating of violating its 5% test level, but emphasizing that the identification theorem and the reliable output for a single unknown system still have a distance from the Direct relative to Spectral-local.

Appendix J.2 indicates that K for coordinate initialization can be estimated by the first baseline sample, but the current experiment treats it as an exact input. Can we, with the existing 12-source system and budget, replace K with this described noisy calibration result, report target/ amplitude errors and F recovery changes? This is a limited verification of the "known initialization can be easily obtained" argument, not requiring new data, new biological experiments or new methods; if the cost is small and the recovery is stable, it will substantially enhance the applicability evaluation.

For the main confirmation and new seed 12-source group, can we use the existing results to conduct stratified diagnosis according to the same pre-described exposure/observation condition indicators, explain the difference between 155/160 and 63/80, and explain whether the advantage of Direct relative to Spectral-local still holds in the weak exposure part? This requires analyzing the existing results, not requiring an expansion of the experimental scale; it will change my judgment on the reliability breadth of the limited budget.

Questions for authors

see Weakness

5 comments
AuthorsOpenReview ↗

Response to Reviewer furd, Part 1/2

We thank the reviewer for a precise reading and for the distinction between identification and deployment. The review names two analyses that would change its assessment. Both are done, and both support the method: estimating KK from noisy data leaves Direct's outcome unchanged in all 640 paired fits, and the diagnosis of the cohort gap was followed by a prospective test on 900 new cases. The conductivity failure behind the applicability concern is resolved as well, by spatial calibration from the data (point 4, in Part 2). Section numbers refer to the revised PDF, where new text is in blue.

1. Replacing the exact KK with the noisy calibration of J.2 (Appendix J.4). For each initialization, the label and amplitude are estimated from the trial-averaged first baseline sample by the same leadfield matching used for intervention targets, with no additional trials. On the main 12-source confirmation (160 cases):

Trial equivalentsDirect successes, exact / estimated KKKK labels correctMaximum amplitude error
6,14469 / 69160/1600.14%
24,576126 / 126160/1600.07%
98,304155 / 155160/1600.035%
393,216160 / 160160/1600.017%

Direct's outcome is identical in all 640 paired fits and Spectral-local's changes in one (39 to 40 at 6,144), so the argument of J.2 holds for single-source initializations. An initialization that spreads over several sources leaves recovery unaffected when its pattern is known. An unmodelled spread of 5% still gives 31/32 recoveries under partial reachability with the measured first block of point 4 (Appendix I.7). At 10% under full reachability Spectral-local degrades less than Direct (135/160 against 122/160).

2. Stratified diagnosis of 155/160 against 63/80, and a prospective test (Appendix B.8).

  • Why the cohorts differ. Exposure does not depend on anatomy, so the 160 and 80 cases are 40 and 20 independent systems on four anatomies each. Three fresh systems have minimum exposure below 0.01; the main cohort has none. Both estimators fail on these 12 cases, and without them Direct recovers 63/68 fresh cases (92.6%), against 155/160 (96.9%).
  • Whether Direct's advantage holds in the weak-exposure part. That part carries too little information for any estimator, the distinction the review itself draws for the main experiment: on new data 5/102 (Direct) and 2/102 (Spectral-local) among the cases the flag marks. Direct's advantage lies in poorly conditioned systems. By quartile of the observed baseline-Hankel σq\sigma_q over both cohorts (post hoc), the worst quartile gives Direct 39/60 and Spectral-local 21/60 (+30.0 pp, seed-cluster CI [15.8, 44.1]); the others are tied (179/180 and 177/180). At 48 sources, where the review cites 60/80 for Direct, Spectral-local recovers 19/80 from the same data.
  • Diagnosis without ground truth, tested on new data. We fixed a flag computed from the data alone, a smallest leading contrast singular value below 0.02, and ran 200 unselected new systems and 25 low-exposure systems, each on four anatomies. All three predictions held: all 44 truly weak cases are flagged, and unflagged cases are recovered in 730/762 (95.8%, [94.1, 97.0]). On the 800 unselected cases Direct recovers 731 (91.4%, [89.2, 93.1]) and Spectral-local 689 (86.1%), a paired difference of +5.25 pp with seed-cluster CI [3.25, 7.5]. The revision reports all three cohorts and uses 91.4% as the reliability figure (§6.3; Table 8).

3. The gate and the reliability of a single fit. We agree: the gate and the flag are rejection tests for acquisitions that carry too little information, and the revision describes them that way (§5.1, Appendix C.4). For a single unknown system the prospective test gives the numbers above: every truly weak acquisition is rejected, and 95.8% of the accepted ones are recovered. The flag catches every weak-exposure failure, 37 of Direct's 69 failures in the unselected cohort; the other 32 occur mainly in poorly conditioned systems (Appendix B.8). The 74.79% case the review cites is one of 32 controls with one unexposed source. It passes the gate because a noise direction happens to match the missing target, and the paper gives it as the example of why the gate rejects and does not certify (Appendix C.4).

AuthorsOpenReview ↗

Response to Reviewer furd, Part 2/2

4. The four bridges to a neural experiment. We adopt the review's characterization of the contribution as a controlled identification method (introduction; §6.4). Each bridge the review lists is now specified by a measured requirement, a check on the data, or a correction in the estimator.

  • KK is calibrated from the data (point 1).
  • LL: the conductivity failure the review cites had two causes, and both are removed. Appendix I combined the exact KK with the mismatched LL, so the two used different source units, and calibrating KK with the fitting leadfield aligns them (I.5). The estimator also replaced the first block of each recovered response history with the supplied leadfield, although the data measure that block; keeping it lets the data calibrate the spatial patterns (I.7). On the same noisy acquisitions the joint criterion is then met in 13, 13, 14 and 14 of 16 systems at half, −25%, +50% and twice the nominal conductivity, against 14/16 at the nominal value (originally 0, 1, 0 and 0).
  • The single-row change in one transition: the construction also covers a focal additive pulse and, through duration-increment contrasts, persistent changes (A.7). A second changed row is detected from the data at 2.5% of the primary coefficient, before it affects recovery (B.6).
  • Continuous time, without correction: a local pulse centred a time tct_c before the next sample has spread to other sources when it is recorded, which biases the estimate once tct_c exceeds about 0.05Δt0.05\Delta t (J.5.1).
  • Continuous time, with correction: the offset is set by the stimulus trigger, and an estimator step that uses it recovers 32/32 systems for every offset up to 0.35Δt0.35\Delta t, without noise and at 73,728 trial equivalents (28 to 31 of 32 at 18,432). The requirement is an offset known to about 0.05Δt0.05\Delta t and no larger than a third of a step.
  • First post-intervention samples: a stimulation artifact with a repeatable topography is projected out. With the topography estimated from 5% of the budget, recovery equals clean data when the calibration records are free of neural response (J.5.2), and Localize-MI shows that such a topography is repeatable in real recordings. With an injective leadfield the first sample is not needed (D.3.1); with fewer sensors than sources it is a requirement of the design.

The review asks about these conditions holding together. With recorded EEG background, a quarter-step pulse lag, a 5° leadfield-pattern error, KK calibrated from the data and a 5% initialization leak at once, the corrected estimator recovers 30/32 and 31/32 systems at 18,432 and 73,728 trial equivalents (ideal model: 32/32; Appendix J.5.3). The artifact projection is evaluated separately.

5. Relation to prior work. The closest prior work is the interventional state space model of Nejatbakhsh & Wang (ICML 2025), which the revision now discusses (§2, Appendix J.7). It learns an injective observation map together with the dynamics and identifies them up to permutation, scaling and shift, from hard interventions that cut a latent variable from its past. Here the leadfield is known, so sources carry anatomical labels and units without that ambiguity, with fewer sensors than sources. The interventions are soft: the perturbed source keeps its dependence on the past, a case the concurrent nonlinear extension of that model lists as a limitation (Tolle et al., 2026). That work motivates interventions by noting that unperturbed activity stays in a low-dimensional subspace. Our theorem turns this into rank conditions under which soft interventions identify the dynamics that baseline responses leave undetermined.

Reassessment. The review states that its main concern is "not a theoretical error" and that the evidence supports the identification conclusions within the model. Both analyses it asked for are done and support the method, and the forward-model failure behind the applicability concern is brought to the nominal level. If a concern remains, we would be glad to hear which one and to address it during the discussion. Otherwise we would be grateful if you would reconsider the soundness score and the rating.

On the ethics flag. The review flags the paper for ethics review without stating a concern. The study uses simulations and the public Localize-MI dataset, with no new human or animal data, and we would be glad to address the specific concern behind the flag.

Dear Reviewer furd, thank you again for your detailed review. As the discussion period ends soon, we wanted to kindly check whether our response has addressed your concerns. In your review you mentioned two analyses that would inform your assessment, and we have reported both in Part 1 of our response. Part 2 addresses each of the four bridges to a neural experiment that you listed, including the conductivity mismatch, and the relation to prior work. We would be very glad to clarify anything that remains open.

Reviewer_pSWjOpenReview ↗
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Paper summary

The paper studies recovery of linear source dynamics from EEG when baseline activity explores only part of the source space. Unknown local interventions reveal source response histories, which a known leadfield identifies and calibrates. Combining these histories with baseline responses allows recovery under explicit rank conditions. The paper provides an estimator, a stability bound, and simulation results.

Critical strengths
  1. The identification result is clean, with explicit conditions separating source coverage, exposure, and observability. The analysis also describes the ambiguity that remains when coverage is incomplete.
  2. The controls convincingly show that baseline failure comes from missing information. I also appreciate the clear reporting of failures under nonlocal interventions and leadfield errors.
Critical weaknesses
  1. The added value of the intervention model is unclear. A focal additive pulse also gives a contrast of the form (O_Te_j a), allowing the same source labeling and calibration. The paper acknowledges this, but I would like a clearer explanation of what the receiving-row model adds. Its experimental requirements—changing one row for exactly one transition—are restrictive and remain unvalidated.

  2. The EEG application needs stronger evidence. Complete recovery in the main partial-reachability experiment requires 18,432 episodes at the lower noise level. Appendix I also reports 0/16 successful recoveries with roughly 11–13% leadfield mismatch, even with noise-free responses and correct labels. The recorded EEG analysis measures spatial repeatability of stimulation artifacts, rather than recovery of neural dynamics. These results leave practical feasibility unresolved.

  3. The comparisons establish the information gap more strongly than estimator superiority. Baseline methods cannot recover the full system in the partial-reachability setting. The EM comparison is exploratory, has convergence problems, and excludes the intervention transition. An intervention-aware comparator would be more convincing. Direct recovery also falls from 155/160 in the main full-reachability cohort to 63/80 in a fresh cohort, suggesting sensitivity that needs further explanation.

Questions for authors
  1. What does the receiving-row intervention model add beyond focal additive pulses? The paper acknowledges that an additive pulse can produce the same source-specific response history. Could you state which identification and estimation results carry over, and clarify what additional insight follows from the state-dependent intervention model?

  2. Which experimental setting could satisfy the intervention assumptions? The model requires one receiving row to change for exactly one transition, followed by a return to baseline dynamics. Could you describe a concrete candidate protocol and explain how its locality, duration, and state dependence could be checked experimentally?

  3. Is recovery possible at a practical noise level and trial budget? Could you report the simulations’ per-trial SNR, with an explicit definition, and test budgets of hundreds to a few thousand episodes? It would help to distinguish conditions where recovery is merely identifiable from those where it is experimentally feasible.

  4. How accurate must the leadfield be for useful recovery? Appendix I shows substantial errors even when target labels remain correct. Could you quantify the leadfield-error tolerance needed to meet the recovery criterion, and distinguish sensitivity to column scaling from sensitivity to spatial-pattern errors? Would estimating calibration parameters jointly with the dynamics improve robustness?

  5. Would the advantage hold against an intervention-aware likelihood method? The current EM comparison excludes the changed transition and has convergence difficulties. Could you fit the intervention explicitly as an unknown receiving-row perturbation, and compare recovery under the same observations and trial budget? This would help separate the benefit of the data from the benefit of the proposed estimator.

  6. What explains the drop in recovery on the fresh full-reachability cohort? Direct recovery falls from 155/160 to 63/80 at the same size and budget. Could you provide a more systematic analysis of exposure strength and conditioning across cohorts? How well does the observed-data exposure gate predict eventual recovery without access to ground truth?

  7. How sensitive is the method to errors in the initialization map (K)? The paper discusses calibrating focal initializations from their first sensor sample, but the estimator takes (K) as given. Could you evaluate recovery when this calibration is estimated from noisy data, including cases where the initialization is slightly distributed across sources?

  8. What happens when the first post-intervention samples are unavailable or contaminated? These samples anchor the response history to the leadfield, but may overlap with stimulation artifacts. Could you quantify the effect of missing early samples and assess whether the alternative propagation approach can recover useful dynamics in that setting?

  9. How robust is recovery to persistent or spatially distributed interventions?

4 comments
AuthorsOpenReview ↗

Response to Reviewer pSWj, Part 1/3: W1 to W3, Q1 to Q3

We thank the reviewer for a careful review and for nine concrete questions. Tests of predictions used protocols fixed before running, and post hoc analyses are labelled. Sections refer to the revised PDF, where new text is in blue. On the three weaknesses:

  • W1. The construction uses only the rank-one response history, so it also covers focal additive pulses and persistent changes (Q1, Q2, Q9).
  • W2. Calibration from the data brings the Appendix I failure to the nominal level (Q4), and a few hundred episodes suffice at a per-trial contrast SNR of about 17 dB (Q3). The real recordings establish the spatial half of the calibration (§6.4).
  • W3. The likelihood you proposed is as accurate as Direct on the same contrasts and needs the labels and starting point that Direct supplies (Q5). The cohort drop is explained and confirmed on new cases (Q6).

Q1. What the receiving-row model adds beyond a focal additive pulse. All identification and estimation results carry over. A focal additive pulse ce=aeejc_e=a_ee_j gives

ΔHe=(OTej) ae1⊤,\Delta H_e=(O_Te_j)\,a_e\mathbf 1^\top,

with the same left factor OTejO_Te_j, the response history of source jj; the unknown amplitude aea_e only sets its scale. Labeling, scale calibration, column completion, the shift solve and the coverage condition rank⁡[K,EJ]=q\operatorname{rank}[K,E_J]=q are unchanged, and the exposure condition becomes ae≠0a_e\neq0 (§4.1, Appendix A.7). In simulation, Direct without any change recovers 26/32 systems at 4,608 episodes and 32/32 at 18,432 from additive pulses with unknown targets and amplitudes (receiving-row at the same contrast SNR: 24/32 and 32/32; Appendix B.9).

The receiving-row model adds the state-dependent case, in which an intervention can be nonzero and still uninformative (ve⊤Rs=0v_e^\top R_s=0); the exposure condition and its negative control exist for this case. It also gives an experimental test of which mechanism acts: for a mixed perturbation Dez+ceD_ez+c_e, initializations of opposite sign separate the two terms exactly (Appendix F). In causal-representation-learning terms both are soft interventions, the additive pulse being a shift intervention (Rothenhäusler et al., 2015; Zhang et al., 2023).

Q2. A candidate protocol and how to check its assumptions. Because the additive case is covered, a standard paired-pulse schedule is a candidate: a conditioning stimulus sets the initial state (KK), a brief focal test stimulus at a chosen delay is the intervention, and matched episodes omit the test stimulus. It exists noninvasively (paired-pulse TMS-EEG) and with intracerebral stimulation and scalp EEG, where the stimulated contact is known (Appendix J.3); recordings of this kind exist at scale (323 sessions in 36 patients; Momi et al., 2025). Dynamic clamp is the cleanest setting for the state-dependent case. Each assumption can be checked on the data or controlled by the design:

  • Locality: the contrast is rank one. A second changed row is detected at 2.5% of the primary coefficient (Q9).
  • Single transition: the left factor is shared across insertion times, and later blocks satisfy the baseline shift relation.
  • State dependence: the parity test of Appendix F.
  • Timing: set by the stimulus trigger. A pulse centred a time tct_c before the next sample has spread to other sources when it is recorded, and an uncorrected offset above about 0.05Δt0.05\Delta t biases the estimate. An estimator step that uses the known offset recovers 32/32 systems for every offset up to 0.35Δt0.35\Delta t, without noise and at 73,728 trial equivalents (28 to 31 of 32 at 18,432). The requirement is an offset known to about 0.05Δt0.05\Delta t and no larger than a third of a step (Appendix J.5.1).

Q3. Per-trial SNR and small budgets. The contrast SNR is 20log⁡1020\log_{10} of the RMS of the noise-free single-trial contrast LFtDeFτintKLF^tD_eF^{\tau_{\rm int}}K over the RMS single-trial noise at the same samples, including propagated process noise (Appendix B.9). In Table 1 it is 6.1 dB and −6.0 dB at the two noise levels, against 22.2 and 10.1 dB for the baseline response: the simulated intervention changes the response by about one sixth of its amplitude.

We tested budgets from 384 episodes on the 32 systems of Table 1, raising the contrast SNR by a stronger intervention at unchanged noise.

Per-trial contrast SNR384 episodes1,1524,60818,432
6.1 dB (Table 1)1/322/3224/3232/32
12.1 dB6/3226/3232/32not run
16.9 dB24/3232/3232/32not run

Averaging nn repeats adds 10log⁡10n10\log_{10}n dB, so all results fall on one curve, and the budget for 75% recovery is

N75≈4,608⋅10(6.1−SNRc)/10N_{75}\approx4{,}608\cdot10^{(6.1-\mathrm{SNR}_{\rm c})/10}

episodes, where SNRc\mathrm{SNR}_{\rm c} is the per-trial contrast SNR in dB; four times that gives 32/32. The noiseless check passes in 32/32 systems, so every shortfall is a matter of budget.

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Response to Reviewer pSWj, Part 2/3: Q4, Q5

Q4. Leadfield accuracy; scale against pattern; joint calibration. Yes: estimating the calibration from the same acquisition improves robustness, and the acquisition already contains what it needs. The first block of every contrast is proportional to the true target column L:,jL_{:,j}, and the first baseline sample measures LKLK. The submitted estimator replaced this first block of the recovered response histories with the supplied leadfield, which is what turned pattern errors into bias in FF. The variant keeps the measured block, uses it as the readout for held-out reconstruction, and takes only source labels and units from the supplied leadfield. It is a one-line change (all five predictions held; Appendix I.7).

On the conductivity experiment cited in your review, with noise and 98,304 trial equivalents (systems recovered, of 16):

Conductivity relative to nominal×0.5−25%nominal+50%×2
Appendix I fits with exact KK011300
KK calibrated from the nominal leadfield (I.5)0131390
Calibrated KK and measured first block (I.7)1313141414

All rows use the same joint criterion in nominal source units. The failure had two causes. The exact KK and the mismatched LL expressed sources in different units, which calibrating KK fixes. The remaining pattern bias (about 12% at a twofold error) disappears with the measured first block. Without noise the variant recovers all 16 systems at every conductivity, and with noise its median error of FF is 2.9 to 4.9%.

  • Pattern tolerance. With a random pattern error in every column, the variant recovers 155, 154, 140 and 111 of 160 systems at 2°, 5°, 10° and 20° (exact leadfield: 155/160; as submitted: 37/160 at 5°), and 31/32 up to 5° under partial reachability. The requirement is a correct source label: the losses at 10° and 20° come from mislabelled sources, and with correct labels recovery is 140/145 and 111/126.
  • Scale. A column-scale error L^=LΛ\hat L=L\Lambda is a change of source units that scalp data cannot identify. The method returns Λ−1FΛ\Lambda^{-1}F\Lambda, with exact eigenvalues, zero pattern and signs (I.6).
  • Cost. None at the exact leadfield: the success counts are the same and the median error is 3.06% against 2.93%. The main tables use Algorithm 1 as submitted, so their numbers stand. The variant has been tested at twelve sources and has not been rerun in the other analyses.

Q5 (W3). Would the advantage hold against an intervention-aware likelihood? We implemented the comparator you describe (Appendix E.5): a Gaussian quasi-likelihood on the trial-averaged blocks that fits FF together with an unknown receiving row vev_e for each condition. It models the changed transition explicitly, with correct trial counts, channel whitening and an exact Jacobian, and it receives the same observations and budget as Direct. On the 192 acquisitions of Table 1:

  • Accuracy is the same. Cell medians of eFe_F are within −2% to +5% of Direct's. Per system the likelihood is slightly better in four of five cells (median ratio 0.93 to 0.95) and slightly worse at the lowest SNR (1.05 to 1.06). At the threshold budget it recovers 28 or 29 of 32 systems against 24.
  • The comparison is stable under longer optimization, which answers the convergence concern in W3. Many fits in the main run stopped at the cap of 400 evaluations, so we extended the fits on 40 acquisitions to 6,400 evaluations. The median change in eFe_F is 0.4% from the Direct start and 1.1% from a generic start, and at most one success changes in a cell of eight.
  • It depends on Direct. It needs the intervention labels, which Direct provides in closed form (correct in 192/192). Started from Direct it never converged to a wrong solution; from a generic start it did so once in 40. Refinement from Direct helps most systems and hurts at the lowest SNR.
  • Direct takes 2.6 ms per acquisition. Likelihood refinement from Direct takes a median of 129 s and three starts take 388 s, about 50,000 and 150,000 times longer.

A different estimator reaches the same accuracy from the same contrasts, so the benefit is in the data, which is the paper's claim (Theorem 1), and Direct extracts it in closed form. The revision states it this way, with likelihood refinement as an optional step at adequate SNR (§6.3). Against the matched estimators that receive identical arrays, Direct's advantage stands. Over Spectral-local it is +5.25 pp on 800 new unselected cases (seed-cluster CI [3.25, 7.5]) and +30 pp in the worst-conditioned quartile (post hoc). At larger sizes with repeats held fixed it recovers 77/80 against 65/80 at 24 sources and 60/80 against 19/80 at 48; at the fixed budget of 98,304 trial equivalents, 42/80 against 14/80 at 24 sources and 0/80 for both at 48 (§6.3, B.7, B.8).

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Response to Reviewer pSWj, Part 3/3: Q6 to Q9

Q6. The drop from 155/160 to 63/80. The difference is cohort composition, and the data predict it. Exposure does not depend on anatomy, so the cohorts contain 40 and 20 independent systems. Three fresh systems have minimum exposure below 0.01 and are recovered by neither method (0/12); the main cohort has none. Without them Direct succeeds in 63/68 against 155/160.

On how well an observed-data gate predicts recovery: post hoc, a threshold on the smallest leading singular value of the observed contrasts flags all 12 failures, and observed proxies predict success with AUC 0.95 to 0.97, as well as the true exposure does. We then fixed the threshold in a protocol and tested it on 900 new cases. All three predictions held: flagged cases are recovered in 5/102, unflagged cases in 730/762 (95.8%), and all 44 truly weak cases are flagged. On the 800 unselected cases Direct recovers 731 (91.4%, [89.2, 93.1]) and Spectral-local 689, and the paper now uses 91.4% as its reliability figure (§6.3; Appendix B.8, Table 8). The flag catches every weak-exposure failure, 37 of Direct's 69 failures in this cohort; the other 32 occur mainly in poorly conditioned systems.

Q7. Errors in KK. Calibrating KK from noisy data changes nothing. With the first-sample calibration of J.2, all labels are correct, the amplitude error is at most 0.14%, and Direct's outcome is unchanged in all 640 paired fits; Spectral-local's changes in one (Appendix J.4).

For slightly distributed initializations, recovery is unaffected if the pattern is known (155 to 157 of 160, and 32/32 under partial reachability). If K:,i=eji+ΔK:,iK_{:,i}=e_{j_i}+\Delta K_{:,i} is calibrated as a single source, the unmodelled part gives a bias of about 0.85∥ΔK:,i∥20.85\|\Delta K_{:,i}\|_2: Direct succeeds in 154/160 cases at a 5% leak and 122/160 at 10% (Spectral-local: 141/160 and 135/160, so it degrades less at 10%). For sources the baseline does not reach, the measured first block of Q4 gives 31/32 at 5% and 19/32 at 10% (as submitted: 26/32 and 0/32). The requirement is a single-source or known initialization pattern, with any unmodelled leak below about 5%.

Q8. Missing or contaminated first samples. A stimulation artifact with a fixed sensor topography is removed by projecting that topography out of the first block, at the cost of one sensor dimension. With the topography known, recovery equals clean data for artifacts up to three times the response. With the topography estimated from separate stimulation-only records that take 5% of the budget, recovery again equals clean data at the same budget (154 or 155 of 160, and 31/32). This requires a repeatable topography, which Localize-MI shows for real recordings (Appendix H), and calibration records with little neural response (tolerance in Appendix J.5.2). Without correction Direct tolerates an artifact of about 10% of the response.

If the first sample is missing and the leadfield is injective, the propagation route (Appendix D) needs neither the first block nor labels and recovers 28/32 systems at m=16m=16 and 73,728 trial equivalents (D.3.1). With m<qm<q the first sample is a requirement of the design: it ties a source the baseline does not reach to its leadfield column.

Q9. Persistent and distributed interventions. Persistent changes stay identifiable through a different contrast. For a change F+DeF+D_e lasting ℓ\ell transitions, contrasting durations ℓ+1\ell+1 and ℓ\ell at equal elapsed time gives

OT[(F+De)ℓ+1−F(F+De)ℓ]Rs=(OTej)[ve⊤(F+De)ℓRs],O_T\big[(F+D_e)^{\ell+1}-F(F+D_e)^\ell\big]R_s=(O_Te_j)\big[v_e^\top(F+D_e)^\ell R_s\big],

the same response history with exposure ve⊤(F+De)ℓRsv_e^\top(F+D_e)^\ell R_s (Appendix A.7, Proposition 7). On the 32 systems of Table 1 recovery is exact without noise for ℓ=0,…,3\ell=0,\dots,3. With noise the cost is budget: exposure falls with duration, so longer durations need more trials (Table 4).

A second changed row makes the contrast rank two, and a test on the data detects it (Appendix B.6): a neighbouring-row change of 2.5% of the primary coefficient is flagged in 92.5 to 100% of systems, at 1.2 to 5% false alarms, while recovery is still 80/80 and degrades only from 10% (67/80).

Reassessment. The analyses above extend the intervention class the construction covers, bring the forward-model failure of W2 to the nominal level, and show that the requested comparator is as accurate as Direct, to within 5% in median error. On feasibility, the required budget follows from the per-trial contrast SNR by one formula, which an experimenter can evaluate from a pilot recording. If a concern remains, we would be glad to hear which one and to run a further check during the discussion. Otherwise we would be grateful if you would reconsider the rating.

Dear Reviewer pSWj, as the discussion period ends soon, we wanted to check whether our response addressed your questions. It answers each of W1 to W3 and Q1 to Q9 in three parts, including the likelihood comparison you proposed (Q5). We would be glad to clarify anything that remains open.

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General response

We thank the reviewers for their careful reading. All three accept the central result, in their words a "clean" identification result (pSWj), "a credible theoretical contribution" (furd) with "a clear mathematical foundation" (CxT2). Unknown local interventions reveal anatomically calibrated source response histories, and these identify the dynamics even when baseline responses do not span the source space and the intervention coefficients stay unidentified. Direct turns this principle into a closed-form estimator. Each point below answers a concern raised in the reviews. Every new test of a prediction used a protocol fixed before running: of the 37 predictions 32 held, and the five that did not are reported in Appendices E.5, J.5.1 and J.5.2. No claim rests on them.

1. Calibration from the data brings the leadfield failure cited in the reviews to the nominal level (furd; pSWj W2, Q4). The acquisition measures the first block of each response history, and the submitted estimator replaced it with the supplied leadfield. Keeping the measured block lets the data calibrate the spatial patterns, while anatomy supplies source labels and units. With KK calibrated from the same recordings, the variant recovers 13/16 and 14/16 systems at half and twice the nominal skull conductivity (nominal head model: 14/16; submission: 0/16), on the same noisy acquisitions and by the same joint criterion in nominal source units. A random 5° pattern error in every leadfield column leaves recovery at 154/160, against 155/160 with the exact leadfield (Appendix I.7). The variant needs no additional trials and has been tested at twelve sources.

2. Direct is as accurate as the intervention-aware likelihood pSWj requested, and it supplies the labels and the starting point that likelihood needs (pSWj W3, Q5). On the same 192 acquisitions the median dynamics errors differ by at most 5% across conditions. Direct takes 2.6 ms per acquisition; likelihood refinement started from Direct takes a median of 129 s. Direct's labels are correct in 192/192 acquisitions, and from its starting point the likelihood never converged to a wrong solution (Appendix E.5). The gain over baseline methods therefore comes from the interventional contrasts, which is the claim of the paper, and Direct is the closed-form way to use them.

3. Reliability is tested prospectively on an independent cohort (furd; pSWj Q6). On 800 unselected new cases Direct recovers 731 (91.4%, 95% CI [89.2, 93.1]) and Spectral-local 689, a gain of 5.25 percentage points with seed-cluster CI [3.25, 7.5]. The drop from 155/160 to 63/80 that both reviews cite comes from three weak-exposure systems, which neither estimator recovers. A flag computed from the data alone, with its threshold fixed before the test, marks all 44 truly weak cases among 900 new ones, and 730 of the 762 unflagged cases in the unselected cohort are recovered (95.8%; Appendix B.8).

4. The corrections work together, with recorded EEG noise (furd; CxT2 W2; pSWj W2). On the 32 partial-reachability systems of Table 1 we combined recorded prestimulus EEG background, a continuous-time pulse with a known lag of 0.25 sampling steps, a 5° leadfield-pattern error, KK calibrated from the data, and a 5% initialization leak. The combined variant keeps the measured first block and corrects for the known lag (Appendix J.5.1). It recovers 30/32 systems at 18,432 trial equivalents and 31/32 at 73,728, where the ideal model gives 32/32, with a median dynamics error of 4.6% against 3.2% (Appendix J.5.3). The dynamics are simulated, the levels were fixed in advance, and the pulse timing is taken as known. Stimulation artifacts are corrected in a separate study (Appendix J.5.2).

Changes in the revised PDF (new text in blue).

  • §2, Appendix J.7: relation to interventional state space models (Nejatbakhsh & Wang, 2025) and to recent work on unknown interventions (furd).
  • §4.1, Appendix A.7: the construction extended to focal additive pulses and, through duration-increment contrasts, to persistent changes (pSWj W1, Q9; CxT2 Q1).
  • §6.3, Appendices B.8, E.5: the prospective cohort and the likelihood comparator (points 2 and 3).
  • Introduction, Appendix J.3: the contribution stated as a controlled identification method, and what a neural experiment has to establish (CxT2 W1, Q2).
  • Appendices B.6, B.9: a data test for a second changed row (CxT2 Q1; pSWj Q9), and small budgets: at a per-trial contrast SNR of 16.9 dB, 384 episodes recover 24/32 systems and 1,152 recover 32/32 (pSWj Q3).
  • Appendices I.5 to I.7, J.4 to J.6: calibration from the data, the timing and artifact corrections, the joint test, and a table of measured tolerances (points 1 and 4).

The main comparisons use the estimator as submitted, and the calibration and timing variants are labelled as such.

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

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