acceptodds
Under review as a conference paper at ICLR 2027

Fast Neural Mass Model Inversion via Amortized Inference

Abstract

Understanding how brain regions influence one another through effective connectivity (EC) is important for explaining brain function. Dynamic Causal Modeling (DCM) estimates these interactions using biologically grounded generative models, but requires iterative model inversion for each observation. We investigate whether this inversion can be amortized by training neural networks on simulated brain dynamics and then reusing the learned inverse model for new observations. We evaluate two amortized estimators: an EC temporal convolutional network (EC-TCN) for constrained connectivity recovery, and SparseGraphInverse, a shared edge-scoring model designed to scale to larger networks. We test these models using (1) whole-brain Jansen–Rit simulations, (2) an independent benchmark generated using the Statistical Parametric Mapping version 12 (SPM) ERP DCM forward model, and (3) auditory EEG. We further examine how recovery changes as the number of potential connections increases. In particular, we distinguish between identifying the target regions whose incoming coupling changes between conditions and identifying which source–target connections carry these changes. On the 200-case SPM benchmark, EC-TCN reaches an area under the precision-recall curve (AUPRC) of (five training seeds), 37% above DCM (; 95% CI –), with lower magnitude error ( versus ) and better-calibrated 95% intervals ( versus coverage). Inference takes ms per case (batch of 200) versus s for DCM, roughly faster. Amortized inversion can therefore provide fast, EC recovery when the set of possible connections is constrained.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Effective connectivity, dynamic causal modeling, amortized inference, neural mass models, electroencephalography, temporal convolutional networks

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_aq1UOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper uses amortized inference to accelerate neural mass model inversion, estimating condition-dependent changes in effective connectivity from EEG observations. The authors trained EC-TCN and SparseGraphInverse on simulated data for inference in constrained candidate sets and larger connectivity spaces, respectively, reducing the computational cost of per-case iterative optimization through direct prediction. The paper evaluates the accuracy, computational efficiency, and scalability of these methods and reveals differences between target localization and source attribution. Scaling experiments show that edge localization deteriorates as the candidate connectivity space expands. With the total number of candidate connections held fixed, increasing the number of candidate sources per target reduces edge-level recovery while target localization remains accurate. This indicates that the identifiability among candidate sources is an issue that needs to be addressed when expanding the scale of connectivity inference. Experiments show that within a constrained candidate connectivity space, amortized inference can improve connectivity recovery accuracy and significantly reduce the computational cost of repeated inference. Real EEG experiments support the application of the model without the need for retraining.

Critical strengths
  1. By examining target localization separately from source attribution, the paper shows why accurately identifying affected brain regions does not necessarily imply reliable recovery of individual connections. This distinction helps researchers evaluate connectivity inference methods without mistaking strong target-level performance for accurate edge-level recovery. It also provides a more specific basis for investigating where inference fails.
  2. The paper compares detection performance, magnitude error, uncertainty calibration, and inference cost, providing practical guidance for choosing connectivity estimators.
Critical weaknesses
  1. The efficiency advantage of amortized inversion is already established in prior work, and the two networks in this paper primarily serve to implement and evaluate this approach. Therefore, the paper’s novelty largely depends on the distinction between target localization and source attribution. However, the authors have not sufficiently explained what this observation adds to existing understanding of identifiability in neural inverse problems, or what specific guidance it provides for designing connectivity inference methods. This leaves me with reservations about the depth of the paper’s contribution.
  2. Controls involving a widened EC-TCN, alternative decoders, and a linear probe indicate that difficulty in source attribution is not unique to SparseGraphInverse. However, some controls share a temporal encoder, and the paper lacks a systematic analysis of training sample size. Therefore, the existing results do not sufficiently distinguish ambiguity inherent in the observations from estimation errors due to representation learning and training. The source-attribution bottleneck is the paper’s most important finding, and the incomplete explanation of its causes limits both its scientific significance and its generalizability.
  3. Although EC-TCN outperforms DCM on the SPM benchmark, it is not the strongest estimator in the reported comparisons. Table 7 shows that Random Forest achieves a higher AUPRC than EC-TCN (0.628 vs. 0.593), while Ridge obtains nearly identical magnitude estimation error (0.318 vs. 0.316) and better interval coverage (0.945 vs. 0.932). These results suggest that much of the performance improvement over DCM may come from replacing iterative inversion with supervised prediction rather than from the proposed architecture. More importantly, EC-TCN does not establish a clear advantage over substantially simpler estimators on its central connectivity recovery task. This weakens the methodological contribution and raises questions about whether the additional neural architecture and multi-head training design are necessary.
  4. The real-data experiment reveals a substantial limitation of the proposed approach. On the 63 admitted participants, EC-TCN and DCM exhibit almost no correlation in their edge-level estimates (participant-level ρ = 0.03; group-level ρ = −0.04), with sign agreement of only 0.51. This indicates that the two methods produce substantially different conclusions about which directed connections change and in what direction. Moving to mechanism-family comparisons does not resolve this issue, as EC-TCN favors bidirectional and forward modulation, whereas DCM favors the combined family. Furthermore, the comparison involves different statistical quantities: averaged classification probabilities for EC-TCN and random-effects model-selection probabilities for DCM. Consequently, the real-EEG experiment demonstrates computational applicability but does not establish reliable connectivity inference. This considerably limits the practical significance of the proposed approach for neuroscientific analysis.
Questions for authors

See weaknesses. Others:

  1. Compared with existing studies on amortized inversion of neural generative models and identifiability, what specific new insights does the distinction between target localization and source attribution provide?
  2. What is the main motivation for choosing EC-TCN and SparseGraphInverse? Do these architectures have properties necessary to study this problem, or do they serve as representative implementations of amortized inference? Given the existing baselines and architecture and decoder controls, which conclusions depend on the specific designs of these two models, and which can be generalized to other estimators?
7 comments
AuthorsOpenReview ↗

Response W1

We do not claim a new theory of identifiability. What the paper adds is a specific, testable failure in a neural inverse problem, plus diagnostics to detect it.

What the observation adds. A model can rank directed connections well and still not know which region sent the signal. At 1,394 candidate connections, edge AUPRC was about 12 times the base rate and target AUPRC was 0.992. Yet given the true target, the correct source was ranked first in 0.047 of cases, against a random-source baseline of 0.051. Finding the target alone moves every connection that enters that region up the ranking, including the true one. An edge-level score can therefore make directed connectivity recovery look better than it is. Our contribution is to show this in a neural mass model and to separate the two abilities.

Our experiments provide the following:

  1. We report source accuracy given the true target, with its random-source baseline, next to edge AUPRC. Edge AUPRC alone cannot separate target from source recovery.
  2. We test the simulator before the decoder. Swap the source of a modulated connection while keeping the target fixed, and check whether the observation changes more than the noise does. With identical regional dynamics it changed by 0.6%, about the same as redrawing the process noise, so no decoder could be expected to succeed. A 1% error in global coupling changes the signal by 5.4%.
  3. We check whether a better decoder helps, and where. When regional dynamics differed (spread 0.1), a decoder that compares source and target waveforms directly raised source accuracy from 54% to 81% at 100 candidates, against 46% for random selection, so decoder design mattered there.
  4. We also check the measurement model. That advantage disappeared when the same simulations were passed through a template head model with sensor noise. The measurement process can therefore be the more immediate constraint, and decoder improvements alone would not help.

All the above indicate whether a recovery failure should be addressed by changing the generator, the decoder or the measurement process, before more is spent on the inverse model. We will state these guidelines explicitly in the updated PDF.

AuthorsOpenReview ↗

Response W2

We added analyses that separate ambiguity in the observations from estimation error, and they are reported in our response to Reviewer 8kAe (W1/Q1). Here is how they address each point.

Training sample size. We added fixed-N learning curves at 500 candidate connections, from 1,000 to 10,000 training cases, with five seeds (table in that response). With identical regional dynamics, source accuracy given the true target stays at the random-source baseline for both decoders. With regional spread 0.1, both improve with data: at 10,000 cases the pair decoder is 45 percentage points above the baseline and SparseGraphInverse is 7 points above.

Shared temporal encoder. The pair decoder is a different architecture. It processes source and target waveforms jointly before any pooling, and it still stays at the baseline with identical regions (+0.004 at 10,000 cases). We also trained a random forest on hand-built features (the mean and standard deviation over time of each region's waveform and firing rate), which uses no learned temporal representation. At 100 and 500 candidate connections, its source accuracy minus the random-source baseline is −0.005 and +0.008 with identical regions, and +0.072 and +0.025 with regional spread 0.1 (five seeds, 3,500 training cases). So the failure does not depend on the learned representation of SparseGraphInverse.

Ambiguity without a learned inverse. The nearest-signature analysis in the same response uses no trained network. Changing the source changes the simulated EEG by a median of 0.6%, about as much as redrawing the noise. Source recovery is 40% when the nuisance parameters are known exactly, against a random-source baseline of 14%, and falls to 13% at 2% error.

Estimator and measurement effects. When regional dynamics differ, more data and the pair decoder help, so the estimator matters there. The pair decoder differs from SparseGraphInverse in three ways (waveform comparison before pooling, the standard-condition firing rate, and sampling of competing-source negatives), so its advantage measures all three together. When the same simulations are passed through a template head model with sensor noise, the pair decoder's source gain disappears, so the measurement process is a further constraint.

For the architectures and training sizes we tested, the failure with identical regions reflects weak source information in the observation. With regional differences, recovery depends on the decoder, training size and the measurement process. We will state this in the updated PDF.

AuthorsOpenReview ↗

Response W3

We agree that EC-TCN is not the strongest estimator on every metric, and that the advantage over the evaluated DCM configuration extends to simpler supervised estimators.

Random forest has the highest detection AUPRC, ridge has near-nominal coverage and a magnitude error close to EC-TCN's, and none of the learned estimators separates the six connections from the base rate by more than 0.07. Much of the improvement over DCM therefore comes from replacing per-observation inversion with supervised prediction, and not from the EC-TCN architecture.

We tested whether the extra design choices help, and they do not. A graph-augmented variant of EC-TCN reached pooled AUPRC 0.404, well below EC-TCN's 0.593. In the Jansen–Rit experiment, removing the auxiliary six-class family head gave pooled AUPRC 0.920 against 0.905 with it, so the multi-head family training is not necessary for recovery.

Our contribution is the controlled characterization of what supervised amortized estimators recover from neural mass model data and where they fail. The baseline comparisons support this: improved gain recovery is not specific to EC-TCN, and across all estimators it does not extend to the extrinsic connections, a distinction hidden in the pooled score. We will present EC-TCN as one representative task-specific estimator and give the simpler baselines greater prominence in the updated PDF.

Reviewer_KhiAOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper investigates amortized inference for effective connectivity estimation in neural mass models (NMMs), aiming to replace computationally expensive, observation-specific Dynamic Causal Modeling (DCM) inversion with a learned inverse mapping.

The authors introduce two neural estimators: EC-TCN, a temporal convolutional network designed to recover connectivity changes within a constrained set of candidate connections, and SparseGraphInverse, a shared edge-scoring architecture intended to extend inference to larger connectivity spaces. Both models are trained on simulated neural dynamics with known connectivity parameters.

The study evaluates these approaches through three experimental settings: (1) synthetic EEG generated using a whole-brain Jansen–Rit neural mass model, including controlled distribution shifts; (2) an independent synthetic benchmark generated using the SPM DCM forward model, where EC-TCN is compared against conventional DCM and several machine learning baselines; and (3) real auditory EEG recordings, where simulation-trained estimators are applied without retraining.

The results suggest that amortized inference can substantially reduce computational costs while achieving competitive or improved parameter recovery within constrained connectivity spaces. However, the scaling experiments reveal a pronounced deterioration in edge-level localization as the candidate connectivity space expands, despite relatively preserved target-region identification. The authors interpret this discrepancy as evidence that distinguishing among competing incoming connections constitutes a fundamental bottleneck for effective connectivity inference.

Overall, the paper presents an empirical investigation of the computational advantages and identifiability limitations of amortized neural mass model inversion.

Critical strengths

S1. A scientifically meaningful problem with a relatively systematic experimental investigation

The paper addresses an important problem in computational neuroscience: whether directed effective connectivity can be reliably recovered from neural observations, particularly as the dimensionality of the candidate connectivity space increases.

I appreciate that the authors do not restrict their evaluation to predictive performance or computational efficiency. Instead, they investigate how connectivity recovery deteriorates under different distribution shifts and increasing candidate-space complexity.

The distinction between target-region localization and source-specific edge attribution is particularly valuable. The observation that target-level recovery remains relatively robust while source attribution deteriorates provides a potentially meaningful insight into the limitations of effective connectivity inference.

This analysis is more scientifically informative than a conventional demonstration that a learned estimator outperforms an iterative baseline.

S2. Multiple validation settings and explicit examination of failure modes

The experimental evaluation is relatively comprehensive, incorporating controlled Jansen–Rit simulations, an independently generated SPM DCM benchmark, and real auditory EEG recordings.

The inclusion of distribution-shift experiments, uncertainty calibration, computational comparisons, and candidate-space scaling analyses strengthens the empirical characterization of the proposed approach.

I particularly appreciate the authors’ attempt to distinguish failures attributable to model architecture from those potentially arising from the underlying inverse problem. The additional controls involving candidate selection, decoder architecture, and observation richness demonstrate an effort to investigate the mechanisms underlying performance degradation rather than merely reporting aggregate performance metrics.

Although these experiments do not fully resolve the identifiability question, they constitute a substantive strength of the paper.

Critical weaknesses

W1. Insufficient methodological novelty and unclear justification for amortized inference

My primary concern is that the methodological contribution of the proposed amortized inference framework is not sufficiently distinguished from existing simulation-based inference approaches.

The central strategy—generating observation–parameter pairs from a mechanistic simulator and training a neural network to approximate the inverse mapping—is already well established in simulation-based inference and amortized parameter estimation.

The proposed EC-TCN primarily combines a conventional temporal convolutional encoder with task-specific prediction heads, while SparseGraphInverse employs shared regional embeddings and an edge-scoring MLP. Although these architectures are reasonable engineering choices, it is unclear what methodological innovation they introduce beyond applying established neural estimation techniques to a particular neural mass model inversion problem.

The substantial computational advantage over DCM is expected from replacing repeated iterative optimization with a pretrained feedforward estimator. Consequently, computational speed alone does not establish a sufficiently novel contribution.

More importantly, the paper does not clearly articulate why amortized inference is particularly necessary for investigating the scientific question of connectivity identifiability. The identifiability of neural mass model parameters is fundamentally a property of the generative model and observation process, rather than of the amortization strategy itself.

Although the paper includes comparisons with existing SBI methods, the conceptual distinction between the proposed approach and established amortized inference frameworks remains insufficiently developed.

As a result, I find the methodological contribution relatively incremental for ICLR, despite the relevance of the application.

W2. The central identifiability claim is not sufficiently disentangled from limitations of the learned inverse estimator

The most interesting result of the paper is the deterioration of source-specific connectivity recovery as the candidate space expands, despite relatively preserved target-region localization.

However, I am not convinced that the presented experiments sufficiently establish whether this deterioration reflects an intrinsic identifiability limitation of the underlying neural mass model or a limitation of the amortized estimator.

Several distinct factors could contribute to the observed failure:

  1. Structural or practical non-identifiability of the generative model.
  2. Information loss introduced by the observation process.
  3. Approximation error arising from the learned inverse mapping.
  4. Dependence on the simulation parameter distribution and associated priors.

The authors conduct useful controls involving decoder architectures, candidate selection, and observation richness. However, these experiments do not directly characterize the inverse problem independently of the learned estimator.

For example, parameter sensitivity analyses, likelihood-based identifiability assessments, or comparisons against observation-specific inference under matched generative assumptions could help establish whether the observed ambiguity is intrinsic to the generative model.

Without such evidence, the conclusion that source attribution is fundamentally constrained by neural mass model identifiability appears stronger than the experiments directly support.

This concern is further reinforced by the real-EEG evaluation. The edge-level estimates produced by EC-TCN and DCM exhibit essentially no correlation, with participant-level correlation of approximately 0.03 and sign agreement near chance.

I acknowledge that DCM is not ground truth and that disagreement between methods does not necessarily imply that either estimator is incorrect. Nevertheless, these results leave the physiological validity of the inferred connectivity unresolved.

The subsequent interpretation at the mechanism-family level is reasonable as an exploratory analysis, but it does not establish that the proposed method reliably recovers meaningful directed connectivity from real neural observations.

Consequently, the paper’s strongest scientific claim—characterizing the fundamental limits of effective connectivity recovery—is not yet sufficiently supported by evidence that separates generative identifiability from estimator-specific limitations.

Questions for authors

The following questions are intended to clarify issues that could materially affect my assessment.

Q1. What is the specific methodological contribution beyond existing amortized simulation-based inference?

The proposed framework appears to follow the established simulation-based inference paradigm of learning an inverse mapping from simulated observation–parameter pairs.

Could the authors clarify which component of EC-TCN or SparseGraphInverse constitutes a methodological contribution beyond existing amortized parameter estimation approaches?

In particular, is the intended contribution a novel inference methodology, an application of established amortized inference techniques to neural mass models, or an empirical characterization of connectivity identifiability?

A clearer distinction would help determine the appropriate standard for evaluating the paper’s novelty.

Q2. Why is amortized inference necessary for the central scientific investigation?

The paper motivates amortized inference primarily through computational efficiency. However, its most scientifically interesting findings concern the identifiability of directed connectivity.

Could the authors explain whether amortization provides any specific advantage for investigating identifiability beyond enabling faster evaluation over simulated observations?

More specifically, would the central findings concerning target localization and source attribution be expected to hold under conventional observation-specific inference using the same generative model?

If so, what aspects of these findings should be attributed specifically to the proposed amortized inference framework?

Q3. Can the authors distinguish generative non-identifiability from amortized approximation error?

The scaling experiments demonstrate that edge-level recovery deteriorates as the candidate connectivity space expands.

However, the presented results do not conclusively establish whether this deterioration arises from intrinsic ambiguity in the forward model or insufficient approximation of the inverse mapping.

Could the authors provide direct evidence that distinct connectivity configurations produce observationally indistinguishable responses under the evaluated generative model?

For example, an analysis of parameter sensitivity, local identifiability, or alternative parameter configurations yielding comparable observation likelihoods would help substantiate the proposed interpretation.

Alternatively, a comparison against observation-specific inference under matched generative assumptions would help determine whether the observed scaling failure persists independently of amortization.

This distinction is particularly important because the paper interprets the observed scaling behavior as evidence of a fundamental identifiability bottleneck.

Q4. How should the disagreement between EC-TCN and DCM on real EEG be interpreted?

The real-EEG experiments report negligible correlation between EC-TCN and DCM edge-level estimates, along with sign agreement close to chance.

While I agree that DCM should not be treated as ground truth, this discrepancy raises questions about the physiological interpretability of the inferred connectivity parameters.

Could the authors clarify what evidence supports the validity of EC-TCN’s edge-level connectivity estimates on real EEG, independently of agreement with DCM?

In particular, are there established physiological constraints, known experimental effects, or independently supported connectivity patterns that could provide additional evidence for the inferred mechanisms?

Without such validation, it remains unclear whether the simulation-trained inverse estimator recovers meaningful connectivity or primarily reflects the assumptions embedded in its training simulator.

Q5. How sensitive are the conclusions to the assumed simulation priors and parameter distributions?

The amortized estimator is trained using connectivity configurations sampled from predefined parameter distributions, including constrained candidate sets and bounded modulation magnitudes.

Consequently, its predictions may depend substantially on the assumed distribution of plausible connectivity configurations.

Could the authors clarify whether the source-attribution failure persists under alternative parameter priors, particularly those that modify the relative prevalence or magnitude of competing incoming connections?

This would help distinguish limitations imposed by the observation model from those induced by the training distribution.

7 comments
AuthorsOpenReview ↗

Response Q1

We're not claiming a new general simulation based inference method or a new neural architecture. EC-TCN and SparseGraphInverse are both task specific amortized estimators. The contribution of the paper is an empirical investigation into what these existing methods are able to recover from neural mass model data and where they fail to recover. We will revise the Introduction and contribution statements in the updated PDF to make this positioning explicit and incorporate the additional experiments reported in our responses.

Three findings support that claim. Firstly, on the independently generated SPM benchmark, learned estimators outperform the evaluated DCM configuration for excitatory gains, without a clear advantage for extrinsic connections. Random forest also outperforms EC-TCN overall, showing that this finding extends beyond our architecture (in appendix)

Second, the scaling experiments separate out target localization from source attribution. The generator level analysis explains why different sources can produce quite indistinguishable observations. Regional differences and a decoder which compares the source and target waveforms both help with source recovery in the simulation (response to Reviewer 8kAe (W1/Q1)

Third, new injected-modulation tests on two real EEG datasets show strong gain detection but weak connection detection, without establishing physiological connectivity (see response Q4).

We therefore present the paper as an application of established amortized inference techniques to neural mass models, with its main novelty in the empirical characterization of parameter recovery and connectivity identifiability insteadof a new inference methodology.

AuthorsOpenReview ↗

Response Q2

Amortization made it feasible to test recovery across thousands of simulated observations and candidate sets of up to 1,394 directed connections. A trained estimator scores a new observation in milliseconds, so we could test recovery over thousands of simulated observations, retrain across five seeds, and vary training size up to 10,000 cases with candidate sets of up to 1,394 directed connections (learning curves in our response to Reviewer 8kAe, Q1). On the SPM benchmark, frozen EC-TCN took 2.71 ms per case at batch size 200, compared with 79.13 s for the end-to-end DCM fit (321× including one-off EC-TCN training). Fitting 10,000 cases with DCM at that cost would take about 9 days for a five-region model, and we cannot run DCM for 1,394 connections (maximum of 9 connections at a time can run), so experiments of this kind are not practical with observation-specific fitting.

The evidence that source information is fragile comes from the generative model. Forward-model sensitivity and nearest-signature matching, which use no learned inverse (Table in our response to Reviewer 8kAe, Q1), show that a source swap changes the observation by about as much as a noise redraw, and that source recovery falls toward the random-source baseline once parameters are uncertain. We therefore expect source-attribution difficulty to persist under observation-specific inference with the same Jansen–Rit model, observations and parameter uncertainty. The recovery rates would depend on the estimator.

Given the true target, the correct source is ranked first as follows (200 test cases):

SettingRandom-source baselineDCMEC-TCN
All targets0.5850.6520.724
R_A1→R_STG vs R_IFG→R_STG (98 cases)0.5000.5820.561

Both are above the baseline over all targets and neither separates the two connections into right STG beyond sampling error (about ±0.05). DCM's posterior correlation between the two parameters is small (median 0.037), so the ambiguity reflects weak information, not collinearity between the parameters. We did not run a matched whole-brain comparison with observation-specific inference. The whole-brain expectation rests on the generator analyses above.

The target and source findings are properties of the generative model, its observations and its parameter uncertainty. Amortization made them cheap to measure repeatedly; it does not create them. The estimator-specific results (EC-TCN versus DCM on gains, pair decoder gains from regional spread) are properties of those estimators, and Random forest also exceeds EC-TCN, so the advantage is not specific to our architecture. We will make this distinction explicit in the updated PDF.

AuthorsOpenReview ↗

Response Q3

Thank you for this suggestion. Yes, both factors matter. The additional experiments show that source ambiguity and approximation error both contribute, depending on the setting. We examined them separately using forward-model analysis, learning curves, a new decoder and observation-specific inference.

Forward-model evidence. Changing the source of a modulated connection while keeping its target fixed changes the observations by a median of only 0.6%, comparable to redrawing the process noise. In comparison, a 1% change in global coupling changes the observations by 5.4%, and a 1% change in background drive by 46%. Direct matching to forward-model signatures, without a learned inverse, recovers the source in 40% of cases when global coupling, background drive and b are known exactly, but falls to 13% at 2% error, against a 14% random-source baseline. The full table is in our response to Reviewer 8kAe, Q1. This shows that source information exists, but is fragile to parameter uncertainty independently of neural-network approximation.

Approximation error. We also added a waveform-pair decoder that processes source and target waveforms jointly. With identical regional dynamics, both architectures remain close to the random-source baseline when training increases from 1,000 to 10,000 cases. With regional differences, however, the pair decoder substantially improves recovery: at 100 candidates, conditional source accuracy reaches approximately 81%, compared with 54% for SparseGraphInverse and a 46% random-source baseline. Thus, the original representation does leave useful information unrecovered in this setting. Passing the simulations through the tested template-head measurement model with sensor noise removes this source-recovery advantage.

Observation-specific inference. On the smaller benchmark generated using the SPM forward model, DCM also struggles to distinguish the two competing inputs into right STG: accuracy is 0.582 for DCM and 0.561 for EC-TCN, against a 0.500 baseline across 98 cases (see our response to Q2). This supports source-attribution difficulty beyond amortized inference within that benchmark. We have not performed a matched whole-brain DCM comparison, so the whole-brain conclusion rests on the Jansen–Rit forward-model controls.

These results give a more precise explanation of the observed failure: source recovery depends on regional dynamics, parameter uncertainty, the inverse representation and the measurement process. We will replace “fundamental identifiability bottleneck” with this supported conclusion in the updated PDF. We do not claim structural non-identifiability, which would require a formal analysis beyond the experiments reported here.

Reviewer_8kAeOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies amortized inference of condition-dependent neural-mass-model connectivity changes using EC-TCN and a shared edge-scoring model, SparseGraphInverse. It evaluates constrained recovery in Jansen-Rit dynamics, trains a separate sensor-space estimator on an SPM ERP DCM benchmark, examines candidate-space scaling, and applies frozen models to auditory EEG. On 200 SPM test cases, EC-TCN achieves mean AUPRC 0.593 versus 0.433 for the evaluated DCM configuration, with faster inference and better empirical interval coverage. The scaling study finds that identifying affected targets remains easier than identifying the particular incoming source, and the real-data analysis reports substantial disagreement between inferred edges.

Critical strengths
  1. An informative investigation of failure as the hypothesis space expands

I find the target-versus-source distinction the strongest contribution. In the fixed-N source-competition experiment, target-level AUPRC stays around 0.98–0.99 as identifying the incoming edge becomes harder (Appendix A.7.4). This says something useful about the inverse problem: a system can detect which region is affected without reliably attributing that effect to a particular source. The candidate-identity, observation-richness and alternative-decoder controls strengthen that empirical result. These controls make the source-attribution result useful for interpreting what an amortized inverse can recover.

  1. Careful reporting and several meaningful comparison controls

Several difficult results are reported clearly. The SPM experiment compares methods on the same sensor observations and uses case-level paired bootstrapping. A 40-case control increases the DCM iteration budget to convergence without removing the ranking gap. The paper also reports random forest's higher AUPRC, poor coverage outside the training range and near-zero real-data agreement at the edge level (pp. 7, 14–16). I value these results because they help define where the method is useful and prevent the speedup from being interpreted as general success at neuronal connectivity inversion.

Critical weaknesses
  1. The scaling controls do not fully distinguish an information limit from limited learning data

The source-attribution result is convincing as an empirical observation in these training regimes, but the explanation in terms of identifiability needs more separation from statistical difficulty. The candidate set increases from 11 to 1,394 while each case has only 1–10 active edges. Table 8 uses 1,000 training cases up to N = 500 and 3,500 at N = 1,394. Positive prevalence and the positive training exposure available for any individual candidate both change substantially. AUPRC depends on prevalence, and keeping the model's parameter count fixed does not hold these factors constant.

The fixed-N source-competition experiment is a better control, and the nearly collinear forward-response signatures are useful evidence of ambiguity. However, several decoders failing on the same finite training set does not locate the limit of the observation model. A learning curve for that fixed-N setting, with performance reported relative to chance/prevalence, would show whether additional training examples change the conclusion. Direct sensitivity or likelihood analysis could support a stronger claim about the inverse problem. The paper's existing distinction between affected targets and incoming sources remains valuable even if that stronger interpretation is narrowed.

  1. The DCM advantage remains specific to the prior and calibration comparison

The DCM convergence control is helpful, but it does not match the information about the parameter distribution available to the two methods. The learned model sees hundreds of labeled examples from a sparse effect distribution and receives validation-only per-edge scale calibration. DCM uses its generative priors and native posterior uncertainty in a complete parameter model. These choices can affect both recovery and interval coverage. The precise prior/parameter mapping and a comparison with validation-calibrated DCM uncertainty would help interpret the observed coverage gap.

The SPM result is also obtained after training a separate estimator on SPM-generated observations. It shows that amortization can work in that benchmark; it does not test transfer of the JR-trained estimator to another forward model. The real-EEG results further argue for a restricted claim: the edge estimates disagree and there is no neuronal ground truth that resolves the disagreement. I am comfortable with a claim of fast inference under evaluated observation models and training distributions, but would avoid interpreting speed or simulation coverage as evidence that the real-data edges are more accurate.

Questions for authors
  1. Does the fixed-N source-competition result persist as training data increase? Please show a learning curve and performance relative to the prevalence/chance level. A forward-model sensitivity or posterior analysis would help decide whether the source ambiguity is intrinsic to the observations or partly a learning-data limitation.

  2. What generative and inversion priors, parameter transforms and inactive-effect conventions were used in the SPM comparison? How do magnitude error and coverage change when DCM uncertainty receives comparable validation-only recalibration or priors matched to the evaluated effect distribution?

  3. Section 2.1 defines the combined family as forward, backward and intrinsic modulation together, while Section 2.4.1 activates effects independently. How are forward-plus-intrinsic cases without a backward effect, and backward-plus-intrinsic cases without a forward effect, labeled? Please reconcile that rule with the 75.9% combined class and the separate real-EEG family model.

3 comments
AuthorsOpenReview ↗

Response - Q1

Q1 : Thank you for this suggestion. We added fixed-N learning curves, a new decoder and forward-model sensitivity analysis to address this question.

Estimator and regional dynamics1,000 cases3,500 cases10,000 cases
SparseGraphInverse, identical regions+.001±.003−.005±.005−.008±.010
Pair decoder, identical regions−.010±.004+.003±.006+.004±.001
SparseGraphInverse, regional spread 0.1+.040±.008+.048±.007+.066±.006
Pair decoder, regional spread 0.1+.354±.004+.409±.031+.454±.022
  1. At fixed N=500, increasing training cases from 1,000 to 10,000 leaves source attribution close to the random-source baseline with identical regional dynamics under both tested architectures. The table above reports source accuracy given the true target, minus the random-source baseline; zero means no better than the baseline. Values are mean ± standard deviation over five training seeds.

  2. Reviewer aq1U also noted that several existing controls share a temporal encoder (W2). Motivated by this concern, we added a waveform-pair decoder that processes source and target waveforms jointly before pooling. This tests whether the original model’s separate regional representations limit source recovery.

  3. Initially, all regions used the same local Jansen–Rit neural mass dynamics, while their connections followed the structural network. We then introduced regional heterogeneity so that regions could have different local dynamics, potentially making their contributions easier to distinguish. “Regional spread 0.1” refers to the heterogeneity setting used in this experiment. With these regional differences, the pair decoder’s source accuracy above the random-source baseline increases from .354±.004 to .454±.022 as training data increase from 1,000 to 10,000 cases. With identical regional dynamics, it remains close to the baseline.

  4. We also tested source identification by directly comparing observations with forward-model signatures. Across 120 cases, recovery declines as errors in global coupling, background drive and the parameter b increase (columns give the error in these parameters):

GeneratorNo error0.5% error1% error2% error5% errorRandom-source baseline
Identical regional dynamics0.400.220.200.130.120.14
Background drive varies by region0.820.550.380.250.170.14

With identical regional dynamics, accuracy exceeds the random-source baseline when these parameters are known exactly, but approaches that baseline at 2% error (0.13 against 0.14). Allowing background drive to vary across regions substantially improves recovery, although it remains sensitive to parameter uncertainty. These results show that source information exists, but its recovery depends on regional differences and knowledge of these nuisance parameters.

AuthorsOpenReview ↗

Response Q2

Thank you for asking us to clarify the parameter conventions and the fairness of the prior and calibration comparison. We added prior controls and validation-only recalibration for DCM.

1. Generation. Each of the 11 candidate modulations is active with probability 0.38 (about four per case; test base rate 0.35). We force 12% of cases to be fully null, and any other empty case receives one randomly chosen modulation. Active magnitudes are drawn uniformly from [0.15, 0.70] with a random sign; inactive modulations are exactly zero. These values give a moderate number of effects per case. In the Jansen–Rit benchmark, which uses the same activation scheme, retraining and testing with probabilities 0.2 and 0.55 does not change the conclusions (it will be added to the updated Appendix). All other parameters of the SPM benchmark are fixed at the posterior estimates of one real participant (ds006480, combined DCM), so only the modulations and the sensor noise vary between cases. We will state this in the main text of the updated PDF.

2. Transform and DCM priors. Both methods receive the same 65-sensor observations and are scored on the modulation b_e in SPM's matrix B. It acts on a log scale: the relevant coupling or excitatory gain is multiplied by exp(b_e), so b_e = 0 means no condition-dependent change, and active effects correspond to multipliers of about 0.50–0.86 or 1.16–2.01. DCM uses SPM's default zero-mean Gaussian prior on the modulations (variance 1/8) with no sparsity prior. Because DCM has no presence output, its AUPRC uses its posterior confidence for each modulation; alternative scores (|Ep|, |Ep|/sd, Bayesian model reduction) give AUPRC .409–.454, so the comparison does not depend on this choice. Coverage is the share of active effects with |b_e − b̂_e| ≤ 1.96 σ̂_e, where σ̂_e is the DCM posterior SD or EC-TCN's predicted SD.

3. Prior controls (will go in the updated Appendix). On the same 200 test cases:

DCM prior varianceAUPRCEC-TCN advantage [95% CI]Magnitude MAERaw 95% coverage
1/8, default.433+.169 [.134, .202].484.358
.0705, variance-matched.435+.167 [.134, .200].425.338
.03, tighter.430+.172 [.137, .207].366.271
.5, looser.414+.187 [.153, .221].687.323
EC-TCN, locked model.601.314.948

Intervals are paired case-bootstrap intervals. The variance-matched prior equals the generator's variance (.0705) but not its sparse distribution. It lowers DCM's magnitude error without improving raw coverage. A tighter prior lowers magnitude error further and lowers coverage, which is why we report both. Across all four priors and every presence score, raw or calibrated on the validation cases (best: .467), DCM AUPRC is .389–.467 and EC-TCN's advantage is +.134 to +.213.

4. Validation-only recalibration. We fitted DCM to 120 validation cases and applied the same method used for EC-TCN: a per-parameter interval scale from the 95th percentile of validation residuals. No test labels were used for any calibration choice.

MethodRecalibrated 95% coverageMean interval half-width
DCM, default prior.9281.377
DCM, variance-matched prior.9411.248
EC-TCN.948.710

Rescaling changes the interval widths but not the point estimates, so DCM's magnitude errors stay at .484 and .425. Comparable recalibration largely closes the coverage gap, but at intervals 1.8–1.9 times wider than EC-TCN's. We therefore distinguish native from recalibrated coverage and report interval width alongside coverage. The updated PDF will include these controls and the full generation, parameter and calibration details.

AuthorsOpenReview ↗

Response Q3

Both forward-plus-intrinsic and backward-plus-intrinsic cases are labeled "combined" in the 11-parameter JR experiment. The definition in Section 2.1 was too restrictive, and we will correct it.

  1. JR experiment. Effects are activated independently. Here, "combined" means intrinsic modulation together with at least one extrinsic modulation; it does not require both a forward and a backward effect. The reported 75.9% combined class follows this rule: it consists of forward-plus-intrinsic (14.7% of training cases), backward-plus-intrinsic (15.3%) and and all three (45.8%); the figures are rounded and sum to 75.9% before rounding. Under the strict definition of Section 2.1, only 45.8% of cases would be combined.

  2. Effect on recovery. Across five paired training seeds, pooled AUPRC is 0.905 with the original six labels, 0.893 with eight labels that separate these mixed cases, and 0.920 without the family-classification loss. The original grouping therefore does not inflate recovery, and removing the family loss does not lower it (connection AUPRC 0.718, 0.696 and 0.761). The family label is only an auxiliary training target.

  3. Separate recorded-EEG family model. This model samples families directly rather than deriving them from independently activated effects, and its "combined" family includes forward, backward and intrinsic modulation together. We tested it by adding injected family effects to held-out recordings, where the true family is known; it recovers them (accuracy 0.74 and 0.64 against 0.17 with permuted labels). On the unmodified recordings, however, no family stands out: the leading family depends on the generator, and odd and even trials give the same family for only 34% and 41% of participants. We therefore no longer interpret the family ranking reported in the submitted version, and the family table moves to the appendix.

We will state the two labeling rules separately in the updated PDF and correct the wording in Section 2.1.

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

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