acceptodds
Withdrawn from ICLR 2027

Agentification of Nuclear Sensing Domains for Collective Spectral Reasoning

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Modern machine learning methods have substantially advanced sensing by enabling increasingly sophisticated interpretation of acquired signals. Yet most existing approaches represent a sensing domain as a single computational object, producing monolithic vectors or sequences while leaving decomposition of the domain implicit. I introduce agentification, a learning paradigm in which a structured sensing domain is explicitly decomposed into localized subdomains and each subdomain is instantiated as a computational agent with explicit responsibility for local observation, learning, inference, and, optionally, interaction. Agentification therefore goes beyond partitioning by transforming domain components into computational entities that independently learn local behavior and contribute locally generated evidence to collective inference. I instantiate this paradigm in gamma-ray spectroscopy by transforming a 1,024-channel spectrum into 1,024 spectral agents, each using a Gaussian process to learn normal background behavior and quantify anomalous local observations. This setting targets a central nuclear-security challenge: weak source-induced counts can be masked by naturally fluctuating radiation background. The detector is source agnostic: Cs-137 and Co-60 response functions are used only to generate controlled evaluation anomalies and are never supplied to the inference framework. Across ten repeated 70/30 holdouts, agentification improves source-agnostic AUC over PCA, a nonlinear autoencoder, and the strongest monolithic baseline in the weakest source regime, while the advantage diminishes or reverses as anomalies become stronger. Agent-level evidence also provides intrinsic spectral localization, with channel-level localization AUCs of 0.718/0.789 for Cs-137/Co-60 at the weakest tested level and 0.842/0.883 at the strongest. Under partial sensing-domain degradation, agentification remains competitive and can reverse the intact-domain ordering under substantial contiguous channel loss. Simple neighboring-agent communication is not consistently beneficial, demonstrating that agent formation and communication are distinct design dimensions. These results establish agentification as a general approach for transforming structured sensing observations into populations of locally responsible computational entities and provide a computational foundation for Agentic Nuclear Sensing Systems (ANSS).

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Agentification, Collective Reasoning, Nuclear Sensing, Gamma-Ray Spectroscopy

Reviews

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

This paper proposes “agentification,” an approach that decomposes a structured sensing domain into computational agents with responsibility for local learning and inference. Specifically, a 1,024-channel gamma-ray spectrum is assigned to 1,024 agents, each of which uses a Gaussian process to model the unusualness of background counts in its channel. Local responses are standardized and transformed into anomaly scores, which are aggregated using an equally weighted combination of the mean over all channels and the mean over the top 10%. The evaluation uses 100 measured background spectra and Poisson source injections based on Cs-137 and Co-60 detector response functions, with ten repeated 70/30 holdouts. The method achieves higher mean ROC AUC than PCA, a global residual detector, and an autoencoder in the weak-anomaly regime, while its advantage disappears for stronger anomalies. The paper also evaluates channel ranking using local evidence, robustness to partial channel loss, and the effects of simple neighboring-agent communication. Distinctive aspects include the absence of source response templates from the inference procedure and the treatment of communication as a design choice separate from agent formation.

Critical strengths
  1. Detection and inspection of local supporting evidence are integrated into the same computational structure. The overall score is constructed from channel-specific anomaly scores, allowing the evidence used by the detector to be inspected directly in the spectral domain. Table 2 reports localization AUCs of 0.7176 and 0.7885 for Cs-137 and Co-60, respectively, even at the weakest source level. These results support the claim that the local scores contain ranking information about the locations of injected source counts. This does not guarantee accurate region boundaries or physical source localization, but it has practical value for making detection results inspectable. The authors also appropriately acknowledge the limitations of boundary estimation for weak signals.
  2. The paper reports conditions in which its advantage disappears, along with negative results for communication. The methods share the same background splits and source realizations, which is an appropriate basis for comparison. Table 1 limits the advantage of GP-Agent to weak anomalies and reports that the global residual detector performs better at, for example, α=0.10\alpha=0.10. The paper also reports performance degradation from neighboring-agent communication. The reversal under contiguous channel loss in Table 3 is another interesting observation for understanding the conditions under which the method may be useful. These results provide useful evidence about conditional design advantages rather than suggesting universal superiority.
Critical weaknesses
  1. The central contribution of “agentification” is not sufficiently distinguished from the baselines or from the effects of the individual components. The formulation in Equations (3)–(5), consisting of domain partitioning, local models, and aggregation, is broad enough to include the global residual baseline itself. Specifically, that baseline can be written as
gi(xi)=(xi−μiσi)2,Sresidual=1D∑igi(xi).g_i(x_i)=\left(\frac{x_i-\mu_i}{\sigma_i}\right)^2,\qquad S_{\mathrm{residual}}=\sqrt{\frac{1}{D}\sum_i g_i(x_i)}.

It can therefore also be interpreted as having a channel-specific background model and local evidence. Retaining the individual gig_i values would allow channel-level evidence to be displayed for this baseline as well. Thus, even accepting the authors’ definition in terms of localized responsibility and inference, the operational criterion that makes the baseline “monolithic” and the proposed method “agentified” remains insufficiently specified. My concern is not the use of the term “agent,” but whether this distinction corresponds to a testable algorithmic difference or prediction. Furthermore, the proposed method simultaneously introduces GP modeling, empirical negative log likelihood, median/MAD standardization, a saturating transformation, and aggregation emphasizing the top 10% of scores. The experiments do not establish whether the improvements in Table 1 arise from the local model or the particular aggregation scheme. At minimum, comparisons against a local residual detector using the same aggregation and a GP detector using only the global mean would be important. Localization should likewise be compared against local residual scores using the same metric. The application contribution would also be clearer with a discussion of domain-specific background-modeling approaches, such as the NMF methods in Bandstra et al. (2023). This concern directly affects both the central claim of a new learning paradigm and the interpretation of the reported performance improvements. 2. The evidence is insufficient to assess the reliability and practical significance of the improvements. At the three weakest source levels, GP-Agent improves mean AUC over the strongest baseline by approximately 0.015–0.020. These differences are promising, but the means and standard deviations in Table 1 do not characterize the uncertainty of the paired performance differences. Overlapping standard deviations do not establish the absence of a difference, just as higher means alone do not establish a reliable advantage. The ten holdouts reuse the same 100 background spectra and should not be treated as ten independent experiments. An uncertainty analysis should account for the dependence induced by reusing the original background spectra and the injected examples derived from them. Moreover, the AUC at the weakest source level is 0.5569. A relative improvement does not by itself establish useful detection performance. Detection rates at a specified false-alarm rate are not reported, making it difficult to assess the practical significance of the results for the stated nuclear-security motivation. The restriction to 100 backgrounds and synthetic injections from two source response functions is a legitimate limitation that the authors acknowledge. I am not requiring a large new measurement campaign during the rebuttal period. However, uncertainty analyses using the existing data and sufficient implementation details for reproduction are needed. In particular, the empirical probability estimator, the precise definition of the GP response, handling of zero MAD, and treatment of previously unobserved count values could materially affect the results.

Questions for authors

The following questions concern issues whose answers could materially affect my assessment.

  1. Are there comparisons that distinguish agentification from the choice of aggregation? Please specify a testable criterion that distinguishes the global residual baseline from the formulation in Equations (3)–(5). Could you also compare a local residual detector using the same top-10% aggregation with a GP detector using only the global mean? Comparing localization AUC against local residual scores would also help establish the method-specific benefit. Please clarify which data and criteria were used to select the top-10% fraction and the mixing weight of 0.5.
  2. How stable are the performance differences in the weak-source regime? Please provide the paired AUC differences for each split and an uncertainty analysis that accounts for reuse of the original background data. It is important not to assume that the ten splits are independent observations. Could you also assess sensitivity to the random source-injection realizations? In addition, could you report detection rates at fixed false-alarm rates that can reasonably be estimated with the available sample size, together with the threshold-selection procedure? I am not requesting precise estimates at extremely low false-alarm rates from this dataset alone.
  3. Can you provide the implementation details needed to reproduce the results? Please specify the estimator for pi(q)p_i(q), ϵ\epsilon, the GP mean, noise and kernel parameter settings, the exact definition of the response rir_i, and the handling of zero MAD and previously unobserved counts. Are implementation files or supplementary materials available during review that also specify the split and injection random seeds, autoencoder training settings, and aggregation procedure under channel loss? Validation on independent source-present measurements is an important direction for future work. The questions above primarily concern interpreting and verifying the currently reported results.
1 comment
  1. An operational distinction and controlled ablations

The reviewer is correct that the basic partition/local-score/aggregation equations also describe established feature-wise anomaly detectors. Section 3.1 now states this limitation explicitly. What changes in the revised learned-communication configuration is the inference dependency: the conditional score for channel i depends not just on x_i, but on the simultaneously observed selected nonlocal channels x_{N_i} (Sections 4.7–4.8). Table 1 compares learned conditional fusion to independent GP pooling, self-only fusion, and a degree-matched random nonlocal graph while holding local evidence and pooling fixed. The effect is modest and weaker in reverse chronology; it is not a claim that agents are mathematically necessary.

  1. Aggregation choices and alternative baselines

The top-10% fraction and equal mean/top-tail weighting are fixed heuristic choices; the revision does not claim they are optimal or that they were established by an independent hyperparameter search. A mean-only versus mixed-pooling audit returned identical background test-score rankings (Spearman ρ = 1.0), so we do not attribute the observed AUC improvements to top-tail pooling (Section 6.2). The supplement retains comparisons to PCA, standardized residuals, and an autoencoder (Appendix A.1), plus a separate HBOS/empirical-tail analysis (Appendix A.5). The main paper adds a matched global shrinkage-covariance Mahalanobis baseline (Section 6.1), which outperforms learned fusion at selected weak strengths. The empirical-tail method is COPOD-inspired, not a verified implementation of published COPOD. A matched official COPOD evaluation and a full GP-versus-residual top-tail factorial ablation remain useful further work.

  1. Weak-source effect sizes, uncertainty, and false alarms:

I agree that the original α = 0.005 AUC of 0.5569 versus 0.5421 is near chance and not, alone, evidence of practical utility. Supplementary Table A1 and its accompanying text now give paired descriptive standard deviations for the original small AUC gains (+0.0148, +0.0197, +0.0196 at α = 0.005, 0.010, 0.020), while explicitly acknowledging repeated use of the same 100 backgrounds. In the follow-up chronological study, Table 2 reports 30-seed paired injection percentile intervals and ΔTPR at a retrospectively selected 10% FPR. At α = 0.20, reverse ΔTPR is −0.0136 versus self-only and −0.0282 versus random-graph fusion despite favorable ΔAUC. The calibrated 550/150/300 protocol in Section 6.1 yields learned-fusion realized source-free FPRs of 5.73% forward and 28.19% reverse at a nominal 10% target (Mahalanobis: 8.81% and 17.62%). Table 4 separately reports 30-seed detection-fraction gains of +3.82, +2.16, +3.28, and +1.99 percentage points over independent GP, residual, self-only, and random-graph controls, respectively; these are spectrum-level synthetic-injection comparisons, not independent field encounters. These findings sharply limit fixed-threshold claims.

  1. Reproducibility, GP response, and source-injection protocol:

Section 4.3 now specifies the chronological smoothed count-frequency estimator: p_hat_i(q) = [n_i(q) + 0.5] / [N + 0.5 |G_i|] on an integer grid of at most 80 values; GP training targets −log(max(p_hat_i(q), realmin)) with a constant mean basis and squared-exponential covariance in MATLAB fitrgp. The local output r_i is the predicted negative-log-frequency surrogate, standardized by the median and a robust scale max(1.4826 MAD, 0.05), then transformed to bounded evidence (Sections 4.3–4.4). Counts outside the grid use GP prediction/extrapolation, with a standardized squared-residual fallback if fitting/prediction fails. Sections 4.7–4.8 detail partner selection (up to three nonadjacent background-correlated channels with |C_ij| ≥ 0.15), ridge fit (λ = 5), and evidence fusion (γ = 0.35). Section 5.1 specifies chronology, synthetic Poisson additions, and the 30-versus-10-versus-30 seed protocols by table. The learned GP hyperparameters are optimized by the library; no environment-independent exact length-scale specification is asserted. Although implementation and output files exist in the research record, the revised paper does not claim that anonymized code, every seed, or a complete executable reproduction package has already been publicly posted.

  1. Localization baselines and radiation-specific related work:

Supplementary Appendix A.2 reports the ability of GP evidence to rank channels receiving synthetic injected counts, but a matched comparison against residual-score and autoencoder reconstruction-error localization maps has not been verified. Accordingly, the revision does not claim superior localization. The radiation-background discussion cites Bandstra et al. (2023) on gamma-ray background/anomaly learning; no new NMF head-to-head experiment is implied. These are limitations to the breadth of the current evidence, not findings we seek to obscure.

Reviewer_YddkOpenReview ↗
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Paper summary

The paper proposes a new paradigm that transforms structured sensing observation into locally responsible agents and collective inference. The motivation is that weak local evidence may be diluted when combining all evidence together for global evidence. The paper evaluates a nuclear sensing application and demonstrate that agentification could improve performance in the weakest source regimes.

Critical strengths
  • The application to nuclear sensing is interesting.
  • Simple evaluation but demonstrates that collective inference of local agents can be beneficial to certain degrees.
Critical weaknesses
  • A simple motivation study demonstrating that local evidence is diluted can consolidate the intuition of agentification.
  • It is unclear whether the benefits of the proposed paradigm extend beyond channel-level Gaussian processes. Comparisons with conventional local models or learned local representations followed by aggregation would help clarify the distinct contribution of agentification.
  • Partitioning the channels for agentification may result in additional overhead since multiple local inferences are needed. The computation trade off, especially on a bigger scale with more complex models, is limited.
Questions for authors
  • Can you provide direct evidence that whole spectrum modeling can dilute weak local evidence as a motivation study?
  • How is the proposed method different from conventional local modeling followed by aggregation.
  • Can you provide a computational tradeoff with agentification? and how might these costs scale with more channels or more complex models.
3 comments
  • Evidence for the proposed dilution motivation:

I agree that the original motivation was too broad. Uniformly averaging evidence across D channels can attenuate the contribution of a perturbation confined to k channels, but this arithmetic observation is not evidence that every whole-spectrum detector dilutes weak sources. Sections 1, 4.2, and 4.5 now present dilution as a possibility and state that it requires matched empirical testing. The global shrinkage-Mahalanobis baseline provides an informative counterexample: it outperforms learned fusion at α = 0.05 in both chronological directions and at α = 0.10 in reverse (Section 6.1; Table 3). Thus, we do not claim a general failure of global modeling.

  • Relationship to conventional local models:

The revised formulation explicitly treats independent channel-wise estimators with fixed aggregation as a degenerate case, not evidence of a new capability (Section 3.1). The additional testable operation is background-only selection of nonlocal dependency partners followed by a conditional innovation score that depends on other current channel observations (Sections 4.7–4.8). With local GP evidence and pooling held fixed, learned nonlocal selection modestly improves aggregate AUC over independent, self-only, and random-graph alternatives (Table 1). Conditional feature models could also implement such a computation; we therefore position this work as a structured framework and an empirical study of conditional cooperation rather than proof of a general new learning paradigm. Supplementary Table A4 further shows that ordinary feature-wise HBOS and empirical-tail methods are competitive in the separate low-count setting.

  • Computational cost and scaling limits:

I added an explicit complexity discussion in Sections 4.8 and 6.1. Constructing the dense training-background correlation matrix has nominal O(ND²) time cost and O(D²) storage for N training spectra and D active channels. Once up to k partners are selected for each agent, conditional inference costs O(Dk) operations per spectrum, in addition to the local GP evaluations and score pooling. This is an overhead, not a demonstrated speedup. The current implementation uses D = 1,024 and k = 3; we have not established end-to-end runtime, memory scaling, or a favorable compute-performance tradeoff at substantially larger D. Those require separate measurements and, potentially, sparse dependency-discovery methods.

Thank you for your responses. However, most of my concerns (e.g., dilution motivation empirical support, the distinction from conventional local modeling, and the computational tradeoff) are insufficiently addressed, so I am maintaining my score.

I thank the reviewer for reconsidering the submission and for clarifying the remaining concerns. I respect the decision to maintain the score.

I agree that the revised experiments do not establish universal evidence dilution in global models or demonstrate a favorable computational-efficiency tradeoff. Indeed, my shrinkage-covariance Mahalanobis baseline outperforms learned fusion at selected weak-source strengths. We have explicitly acknowledged these findings and narrowed the associated claims.

Regarding the distinction from conventional local modeling, we do not claim that independent feature-wise estimators, score aggregation, or conditional prediction are individually new. Rather, the contribution is the formulation of agentification as a structured sensing-domain architecture and the controlled evaluation of background-learned nonlocal conditional cooperation. The matched comparisons against independent, self-only, and random-graph controls provide evidence for this specific mechanism, although the improvements are modest and not universal.

I acknowledge that additional computational benchmarking and broader validation are necessary to establish the generality and practical advantages of the approach. We hope the Area Chair will consider both the controlled experimental evidence and the explicitly stated limitations when evaluating the revised contribution.

I appreciate the reviewer's careful assessment and constructive feedback.

Reviewer_BJLyOpenReview ↗
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Paper summary

In this work the author proposes "agentification": dividing a structured observation into local regions, assigning each region its own learned model, and combining the resulting local evidence. The paper instantiates this idea in gamma-ray anomaly detection. Each of a spectrum's 1,024 channels receives a Gaussian-process model of background behavior. The detector converts unusual channel observations into bounded scores and combines their global mean with the mean of the highest-scoring 10%. The experiments use 100 measured background spectra and controlled source additions for Cs-137 and Co-60. The local models modestly improve detection over the strongest baseline at low source levels, provide channel-level localization, and remain competitive when channels are missing. Simple neighboring-channel communication generally does not help. The application is well motivated, but the evidence does not yet separate the proposed agent-based interpretation from established feature-wise anomaly detection or establish the broader claim of a new learning paradigm.

Critical strengths
  • The paper addresses a clear and difficult detection problem. Weak changes can disappear in background variation, so retaining localized evidence before aggregating it is a sensible idea. The motivation connects the structure of the observations to the design rather than introducing agents without a task-specific reason.
  • The source-agnostic setting is clearly stated. The source response functions generate evaluation anomalies and localization labels but are not provided to the detector. This is a useful distinction: the task is to detect unusual behavior, not classify a spectrum by matching a supplied source template.
  • The evaluation uses measured backgrounds and paired comparisons. The author preserves the held-out measured background when adding source counts, and competing methods use the same splits and source realizations. Including a simple standardized-residual detector alongside PCA and an autoencoder is also good practice; the simple baseline proves quite strong.
  • The paper reports where the method helps and where it does not. The benefit is concentrated in the weakest source regimes, while the residual detector wins at some stronger levels. The communication experiment is an honest negative result. These qualifications are more informative than a general claim that a local representation always beats a global one.
  • Localization is evaluated rather than only illustrated. At the weakest source level, channel-level AUC is about 0.718 for Cs-137 and 0.789 for Co-60. The distinction between ranking informative channels and recovering an exact anomalous region is important, and the paper acknowledges that the latter remains difficult.
  • The missing-channel experiments ask a useful robustness question. Testing random and contiguous loss is more informative than evaluating only intact spectra. The author also lets the residual baseline use the surviving channels, which avoids an unnecessarily disadvantaged comparison.
Critical weaknesses
  • The central learning contribution is not yet distinct from local anomaly models with score aggregation. In the implemented method, the partition is fixed, each channel learns independently, and the final decision combines scalar scores. Communication is optional and does not explain the main gains. Calling each local model an agent gives the computation an organizational interpretation, but the paper needs to establish what changes algorithmically or empirically compared with treating these as channel-wise estimators. The issue is not that the agents must be more complex or possess general autonomy; the author explicitly rules out that interpretation. It is that "persistent responsibility" does not yet identify a learning capability that an ordinary collection of local models lacks. I would frame the contribution as a local-model approach to weak spectral anomaly detection unless a more specific distinction can be demonstrated. The current evidence is not sufficient to establish a general new learning paradigm.

  • The related work misses close connections to feature-wise anomaly detection and its interpretability. Goldstein and Dengel (2012), Histogram-based Outlier Score (HBOS): compare against independent feature-distribution scoring to isolate what GP smoothing and aggregation add. Li et al. (2020), COPOD: Copula-Based Outlier Detection: discuss and preferably compare its empirical-tail scores and feature-level attribution in the same background-only setting.

  • The comparisons do not isolate why the detection score improves. The GP detector changes several things at once: the background model, the calibration of local scores, their bounded transformation, and the emphasis on the strongest 10% of channels. The residual baseline instead uses a global mean of squared standardized deviations. A weak localized anomaly could benefit from the different aggregation even without any agent formulation. Please compare the same mean-plus-top-tail aggregation applied to simple channel residuals or empirical likelihoods, and compare the GP scores with global-mean aggregation alone. A small table of these controls would be more informative than adding a much larger neural baseline. It would show whether the main benefit comes from local modeling, robust calibration or the final pooling rule.

  • The dataset is small, and repeated holdouts do not establish independent generalization. There are 100 measured spectra, not 102,400 independent training observations; each local model receives only 70 background examples in a split. The paper acknowledges the small dataset, but the measurement provenance and independence need more detail. Were the spectra collected in separate sessions or as nearby measurements under similar conditions? If collection groups exist, a session-level or chronological split would provide a stronger test than random splitting. The ten holdouts reuse the same spectra, so their standard deviation should not be read as uncertainty from ten independent datasets. Please report paired uncertainty for the method differences, respecting the reuse of each original background spectrum and its derived source-added examples.

  • The weak-source gain is modest, and its practical detection meaning remains unclear. At the weakest level, the proposed detector has AUC 0.5569 versus 0.5421 for the residual baseline. At the next two levels, its gains are about 0.020 AUC. These may be real improvements, but both methods remain close to chance at the weakest level, and the paper does not provide paired confidence intervals for those differences. Please also show detection rates at specified false-alarm levels. Overall AUC alone does not tell us whether the extra local sensitivity helps in the part of the operating range motivating the task. The evaluation uses two controlled source-response shapes added to the same background collection. I would either add an independent source-present or changed-background test, or scope the conclusions explicitly to this controlled benchmark rather than treating it as evidence of general sensing performance.

  • The localization result needs a comparative baseline before it supports a distinctive interpretability claim. A channel-to-score map is useful, and it is valuable that the same scores participate in the decision. However, the residual detector also computes per-channel deviations before reducing them to a scalar, and an autoencoder provides per-channel reconstruction errors. Those maps can be inspected without a separate post-hoc explainer. Please compare their localization quality with the GP evidence under the same injected-count labels. The paper also says it reports precision among the strongest agents and the fraction of source counts captured, but the main quantitative localization table contains only AUC. Aggregate versions of those measures, with uncertainty, would help distinguish a generally informative anomaly map from a few favorable examples. The acknowledged difficulty of exact weak-event localization should remain visible in the overall interpretation.

Questions for authors
  • What observable learning or inference capability distinguishes agentification here from a collection of independently fitted channel-wise anomaly models?
  • Do the gains remain when simple residual or empirical-distribution scores use the same calibration and top-tail aggregation?
  • How independent are the 100 background spectra, and are the weak-source improvements supported by paired uncertainty estimates and fixed-false-alarm detection rates?
  • Does the proposed evidence map localize injected counts better than residual and reconstruction-error maps under the same evaluation?
1 comment
  1. Distinction from independent feature-wise anomaly scoring:

I agree with the reviewer’s core criticism. A set of independent channel-wise GP estimators followed by fixed pooling is a valid feature-wise anomaly detector; naming the estimators “agents” does not establish a new learning algorithm. Sections 3.1–3.2 now make this explicit. The operational addition tested here is background-learned conditional evidence: for a given channel, the conditional term changes with contemporaneous measurements at up to three selected nonlocal channels even when its own count is held fixed (Sections 4.7–4.8). A conventional conditional feature model could implement the same mathematics; our claim is an inspectable, locally assigned architecture and a measurable effect of learned cooperation, not exclusivity.

  1. Matched controls and source of improvement:

I added independent GP pooling, self-only fusion, and a random nonlocal graph with matched local GP evidence, fusion weight, and pooling (Section 4.7; Table 1). The average learned-minus-control AUC differences across seven source strengths are, respectively, +0.0356, +0.0252, and +0.0272 forward, and +0.0120, +0.0077, and +0.0064 reverse. The larger gains occur in the forward direction and are not universal. A pooling audit found identical test-score rankings for mean-only and mixed top-10% pooling (Spearman ρ = 1.0), so we do not credit the top-decile term with an AUC gain (Section 6.2). Supplementary Appendix A.4 also shows that naive neighboring-agent message passing can hurt detection.

  1. HBOS, COPOD-related scoring, and the global-model comparison:

Supplementary Appendix A.5, Table A4, reports a separate 100-spectrum chronological comparison with HBOS and an empirical two-sided marginal-tail method inspired by COPOD. At α = 0.02, 0.05, and 0.10, these feature-wise baselines match or exceed GP-Agent in several cases; we explicitly reject a claim of universal GP superiority (Section 7). We label the empirical-tail method COPOD-inspired rather than an official reproduction of COPOD. Its protocol differs from the 1,000-spectrum learned-fusion study, and a fully matched published-COPOD comparison against LearnedFused remains outstanding. The revised main paper also compares against a global shrinkage-covariance Mahalanobis detector (Section 6.1; Table 3), which wins at selected weak strengths.

  1. Background independence, paired uncertainty, and operating points:

The original 100-spectrum benchmark uses ten reused random 70/30 holdouts, not ten independent datasets. The new 1,000-spectrum benchmark uses a single sequence of one-second mobile-background spectra with chronological partitions, not independent survey campaigns (Section 5.1). Main Tables 1–2 use 30 paired synthetic injection realizations on 700-training/300-test splits; Table 3 uses 10 seeds on 550-training/150-calibration/300-test splits; and Table 4 uses the latter protocol with 30 seeds. Table 2 reports injection-conditional percentile intervals and retrospectively selected 10% FPR differences; these must not be interpreted as independent-campaign confidence intervals or operationally calibrated alarm claims. On disjoint source-free test backgrounds at the nominal 10% calibration target, learned-fusion realized FPR is 5.73% forward and 28.19% reverse, while Mahalanobis yields 8.81% and 17.62% (Section 6.1). The large reverse inflation materially limits practical conclusions. The supplement reports paired descriptive variability for small original weak-source AUC differences, not survey-level uncertainty.

  1. Localization and source-specific conclusions:

Supplementary Appendix A.2, Table A2, evaluates channel ranking against retrospectively recorded injected counts (e.g., Cs-137 0.7176 and Co-60 0.7885 AUC at α = 0.005). These results show that the same local evidence used in collective scoring is inspectable by channel; they do not show exact hard-boundary recovery, physical source localization, or superiority over standardized-residual and autoencoder attribution maps. We have retained that narrower claim. A fully matched localization comparison and uncertainty summaries for top-ranked-channel precision and injected-count mass remain incomplete, and we do not present them as established results.

Comments on the paper

1 comment

General response

  • Reader's guide to the revisions::

The changed manuscript is not a replacement of the original research question. Section 3.1 now states that independent channel-wise models plus pooling are not, by themselves, evidence of a new learning capability. Sections 4.7–4.8 specify the additional conditional-inference operation. Tables 1–2 report controlled matched-cooperation comparisons; Table 3 reports the global Mahalanobis comparison; Table 4 reports weak-source recovery and realized false-positive rates. Section 7 states the failure cases and remaining validity limits. Supplementary Appendices A.1–A.5 retain the separate 100-spectrum baselines, channel-level localization, channel-loss robustness, naive communication ablation, and feature-wise low-count comparisons. Results from these distinct protocols are not pooled.

  • Overall clarification::

We thank the three reviewers for identifying an important ambiguity in the original submission: fixed channel-wise models followed by score aggregation do not, by themselves, establish a new learning capability. The revised paper therefore distinguishes (i) agentification as an explicit organization of local sensing responsibilities from (ii) the testable incremental mechanism of background-learned conditional cooperation. In the latter, an agent’s evidence may depend on its own observation and on contemporaneous observations from selected nonlocal partners. We no longer claim that this inference is unique to agent implementations or that GP models are universally superior.

  • New comparisons and scope::

The revision adds a separate 1,000-spectrum mobile-background study with forward and reverse chronological tests, matched independent, self-only, and random-graph controls, a global shrinkage-covariance Mahalanobis baseline, a disjoint background-only calibration segment for a nominal 10% false-positive rate, and paired source-injection analyses. The earlier 100-spectrum random-holdout results, localization, robustness, and naive communication ablation remain in Supplementary Appendices A.1–A.5 under explicit protocol labels. These experiments involve measured backgrounds but synthetic Cs-137/Co-60 source additions, not measured source-present field encounters.

  • What the evidence does—and does not—show:

Learned conditional fusion has modest aggregate AUC advantages over matched independent, self-only, and random-graph controls, with smaller reverse-direction gains. It loses to global shrinkage-Mahalanobis at α = 0.05 in both chronological directions and at α = 0.10 in reverse; in the separate low-count study, HBOS and an empirical-tail method are competitive with GP-Agent. Most importantly, at a nominal 10% calibration target, learned fusion produces a source-free reverse-split false-positive rate of 28.19%, compared with 17.62% for Mahalanobis. We now state these counterexamples and calibration limitations in the Abstract, Sections 6.1–7, and the Conclusion. They support further study of learned conditional cooperation, not deployment-ready alarming or a universally superior learning paradigm.

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