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Under review as a conference paper at ICLR 2027

Explainable Longitudinal Prediction with Complete Fuzzy Measures and Higher-Order Feature Interactions

Abstract

Understanding longitudinal predictions requires identifying how several variables' histories jointly shape future outcomes. Explanations limited to individual variables or pairs can miss these higher-order interactions. We introduce recursive Choquet, a longitudinal model that summarizes each feature's history separately and combines the summaries through a complete fuzzy measure. Our central construction recursively learns each feature set's value from those of its immediate subsets. We prove that this construction guarantees normalization and monotonicity without restricting interaction order. We then use the Choquet integral to produce forecasts with an exact decomposition into signed feature interactions. We compare our model with boosted trees, GRU-D, and a Transformer using common prediction-explanation methods. In controlled experiments, we recover positive and negative interactions; on a higher-order synthetic data, we obtain the lowest attribution error among these predictors at every order through six under both Faith-Shap and Shapley-Taylor. Across a harmonized set of clinical cohorts containing 166,836 participants, we predict 12 biomarkers and two depression scores with standardized test mean squared error 0.5215. For depression predictions, we obtain the most stable pair and triple explanations among these predictors, with triple cosine similarity 0.677 across training seeds. Our results support higher-order interaction recovery in controlled data and repeatable clinical explanations, providing a basis for further clinical evaluation.

Primary area:
interpretability and explainable AI
Keywords:
Explainable AI, Longitudinal Data, Fuzzy Measures, Attention

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
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Paper summary

The paper develops a model that predicts future health measurements from past records and makes the attribution of feature sets explicit. It aggregates each feature’s values and combines these aggregates using a learned score for every possible feature set. The paper’s main technical proposal is a recursive rule that keeps these scores consistent with the requirement that adding a feature cannot decrease the set’s score. Experiments evaluate interaction recovery on synthetic data, as well as prediction accuracy and explanation stability on clinical health records. The proposed model recovers interactions well when the synthetic data follow its assumed structure and gives more repeatable pairwise and three-way interaction explanations on clinical data, but requires many parameters and predicts less accurately than boosted trees.

Critical strengths

The strengths of this work are not substantial: (1) the model is interpretable, i.e. it shows how individual features and combinations of features contribute to its predictions, and (2) the paper evaluates explanations on synthetic data while also providing a real-world application in the medical domain.

Critical weaknesses

Two critical weaknesses of this paper are (1) lack of novelty/significance and (2) poor quality in writing.

  1. Firstly, the paper does not clearly explain why the research matters, and the empirical results reported in Section 6 do not appear to constitute a substantial advance in machine learning. Furthermore, the theoretical novelty of Section 4 appears limited. The marginal contributions, Möbius coefficients, and Choquet decomposition are classical, while Theorem 1 follows from Möbius inversion and elementary counting. Theorem 2 combines the standard indicator-input property of the Choquet integral with straightforward error bounds; it does not establish recovery from observational longitudinal data. These results help explain the model, but neither theorem depends on the proposed recursive parameterization or longitudinal architecture. Finally, the paper does not engage well with related literature on higher-order feature interactions; only for example:

[a] Detecting Statistical Interactions from Neural Network Weights. ICLR 2018
This work identifies higher-order interactions from trained network weights and should be discussed alongside the paper’s synthetic interaction-recovery experiments.

[b] Neural Interaction Transparency (NIT): Disentangling Learned Interactions for Improved Interpretability. NeurIPS 2018
NIT learns interpretable additive models with interactions of controlled order, offering a natural comparison for assessing the benefit of retaining higher-order terms.

[c] Exploring Interpretable LSTM Neural Networks over Multi-Variable Data. ICML 2019
IMV-LSTM already uses variable-specific temporal representations to support interpretable prediction, and the paper should explain how its feature-preserving longitudinal aggregation differs from this approach.

[d] How does This Interaction Affect Me? Interpretable Attribution for Feature Interactions. NeurIPS 2020
Archipelago separates interaction detection from attribution to individual predictions, an issue that also arises in the paper’s distinction between capacity interactions and explanations of forecasts.

[e] Scalable Interpretability via Polynomials. NeurIPS 2022
SPAM uses low-rank polynomials to model higher-order interactions efficiently, making it a particularly useful comparison given the exponential size of the complete fuzzy measure.

[f] HarsanyiNet: Computing Accurate Shapley Values in a Single Forward Propagation. ICML 2023
HarsanyiNet builds Harsanyi interactions into the predictor and derives exact Shapley values from them, so the discussion of explanations obtained directly from the model could acknowledge this earlier architecture.

[g] Learning to Understand: Identifying Interactions via the Möbius Transform. NeurIPS 2024
This work studies recovery of Möbius coefficients from function evaluations under sparsity assumptions and should be discussed in connection with the paper’s complete-probe identification result and its computational cost.

[h] InstaSHAP: Interpretable Additive Models Explain Shapley Values Instantly. ICLR 2025
InstaSHAP connects generalized additive models with Shapley explanations and trains interpretable models to compute these attributions in a single forward pass, directly relating to the paper’s integration of prediction and explanation.

  1. There are too many issues with the paper's clarity for it to be readable by the ICLR audience, e.g.:
  • In the Abstract, the sentence "Across a harmonized set of clinical cohorts containing 166,836 participants, we predict 12 biomarkers and two depression scores with standardized test mean squared error 0.5215." is not informative: why is "harmonized" or the number of participants important? What are these biomarkers? This value of "0.5215" is not informative without a baseline comparison. Further, "we obtain the most stable pair and triple explanations among these predictors, with triple cosine similarity 0.677 across training seeds" the most stable compared to what? What is this cosine similarity measuring?
  • The introduction has no references to the literature, which makes its contribution to machine learning research unclear.
  • zijz_{ij} in Equation 1 is not explained.
  • In "The main model uses softmax weights.", it is unclear what are the non-main models and how do "softmax" weights look like.
  • Section 3 could start by stating what the goal of this method is, and revisiting "Why?" at each point of describing "what" and "how" it was done.
  • Proposition 1 is not understandable; each of the terms "monotone," "capacity," and "parameters" should be better explained.
  • L163 writes about "biomarkers" and "depression scores," but the reader does not know what they mean at this point.
  • L168 "they are not changes in clinical outcome units" is unclear.
  • Section 5 is too verbose, and much of it could have been stated in the Appendix, making space for actual results.
  • There are too many numeric values appearing in the text of Section 6 without a clear explanation for why they matter, e.g. "MSE of 0.51492, compared with 0.52148" or "with cosine similarities from −0.036 to 0.066".
Questions for authors

I don't think answers to any question could affect my assessment for this work.

5 comments

Thank you for the expert reading and for the specific references. Your comments led to many of the largest revisions. We agree with several of your points, and we changed the paper rather than argue them. The contribution we now claim is the combination of three things: longitudinal summaries that keep each feature's name, a headroom-scaled complete capacity, and a common evaluation of prediction explanations across model families. Section and table numbers refer to the revised PDF.

1. Novelty and significance

We now explain why the research matters. The introduction starts from a concrete problem, with references. Clinicians often need to know which combinations of risk factors drive a forecast. Sequence models only allow post hoc interaction attributions, and those can change when the model is retrained. Our own data quantify this: a Transformer's triple attributions agree across retraining seeds with a cosine similarity of only 0.10, and different predictors barely agree on triples at all (cosine -0.04 to 0.07). A model whose interactions are part of the prediction is one way to address this.

Here is what we claim now, and what we no longer claim:

  • We state the measured trade-off plainly, including the parts against us. Our error is about 3 percent higher than that of boosted trees. Pair-level capacities are more accurate and cheaper in this cohort. And the clinical data support few high-order sets. So we now present the complete measure as an exploratory diagnostic for higher-order structure, not as a better clinical predictor and not as a calibrated test.
  • On synthetic data with known interactions up to sixth order, our explanations are at least 11 times closer to the truth, at every order, than those of 15 comparison predictors. We also say that part of this comes from fitting the generator better. It is therefore controlled recovery within the Choquet family, not an explanation advantage at matched prediction error.

On the theory, we agree with your assessment. The set-gain identities and the complete-probe result are classical consequences of Mobius inversion and the indicator property of the Choquet integral. We have:

  • renamed them from theorems to lemmas;
  • cited Grabisch, and Denneberg and Grabisch, for them;
  • moved the proofs to the appendix;
  • and said explicitly that we state them only because they determine how the reported quantities should be read.

The only formal result tied to our parameterization is Proposition 1, the validity and one-to-one property of the headroom-scaled recursion. We now support it with a direct comparison against the clipped iChIMP construction (Section 6.2). We also narrowed that claim. Headroom scaling avoids hard clipping and the dead increments of a ReLU; it does not give a larger class of capacities, and it does not guarantee that every parameter receives an informative gradient. The comparison supports an optimization benefit in the settings we tested. A softplus variant of iChIMP essentially matches our static recovery and clinical prediction, and we did not evaluate its clinical stability.

On recovery from observational data, you are right that Lemma 2 does not establish recovery from observational longitudinal data, and we now say so right after the lemma. To make the point concrete, we added an identifiability diagnostic on the clinical training data (Section 4.2, Appendix B.4, Tables 5 and 6). A set value receives direct evidence only if the set appears on some participant's sorted chain. The diagnostic uses the summaries of one representative fitted model.

  • This holds for 89 percent of pairs and 70 percent of triples, but for only 5.9 percent of all 2 million proper sets.
  • For the 122 sets through order three that have at least 1,000 supporting landmarks, the design is reasonably conditioned, with a condition number of about 102.
  • It becomes rank deficient once all supported triples are included.

The favorable conditioning therefore concerns those selected columns only. It does not establish identifiability of the full jointly learned model. So most high-order clinical set values are shaped by the recursion rather than by the data, and we list this as a limitation.

2. Related literature

Thank you for the list. We checked each reference, and we now discuss all eight in Related work, with a comparison table in Appendix A.3 (Table 4). Where a method could be run in our protocol, we ran it (Appendix G).

  • [a] We ran NID (ICLR 2018) on the signed synthetic generator. It ranks the planted pairs first to third and the planted triple second to fifth. It gives no signs, though, so the negative pair is ranked only by strength (Table 37).
  • [b] We discuss NIT (NeurIPS 2018) as a neural model with controlled interaction order. We did not run NIT itself. The question it raises, whether keeping higher orders helps, is tested with k-additive capacities, EBM, and SPAM in the same protocol.
  • [c] We discuss IMV-LSTM (ICML 2019): it keeps a separate state for each variable and reports variable importance, not set interactions. We also ran an IMV-LSTM-style model on the synthetic data. No official implementation exists for our longitudinal setting, so we label it as our own adaptation. It fits the generators poorly, so its results say little about the original method.
  • [d] We discuss Archipelago (NeurIPS 2020) alongside our separation of capacity coefficients from explanations of final predictions.
  • [e] We ran SPAM (NeurIPS 2022) at order 2 and 3 on both synthetic generators and on the clinical data. SPAM of order 2 predicts better than our model (0.5074 against 0.5215), but its pair explanations are much less stable across seeds (cosine 0.226 against 0.778). SPAM of order 3 also predicts better (0.5098), and its triple explanations are much less stable (cosine 0.047 against 0.677).
  • [f] We agree that HarsanyiNet (ICML 2023) is the closest in spirit, and we now say so. The difference is that our coefficients form a normalized monotone capacity over named longitudinal summaries, with every set enumerated. We ran a HarsanyiNet-style model on the synthetic data, again labeled as our own adaptation. It also fits poorly, so we do not read the result as a verdict on HarsanyiNet itself.
  • [g] We discuss Kang et al. (NeurIPS 2024) next to our complete-probe result. Sparse Mobius recovery from queries is a natural route past the cost of enumerating every set.
  • [h] We discuss InstaSHAP (ICLR 2025) next to explanations obtained in one pass from interpretable additive models.

We also added iChIMP and EBM as direct comparisons.

3. Clarity

Thank you for the precise list. We addressed every item.

  • We rewrote the abstract. It now names the cohorts (CARDIA and WHI) and the outcomes, and says what the cosine measures: agreement of signed triple attributions across training seeds. Every number now comes with its comparison (for example 0.68 against 0.05 to 0.45), and the abstract states the accuracy cost.
  • The introduction now has references. It cites work on the clinical motivation, sequence models, interaction attribution methods, interpretable interaction models, and fuzzy measures.
  • z_ij in Equation 1 is now defined as the scalar summary, between 0 and 1, of participant i's history of feature j up to the landmark; it is the Choquet input for feature j. The weights, elapsed time, and transform are also defined.
  • For "The main model uses softmax weights", the softmax formula is now given. We also say that mean, sigmoid, and power-mean weights were the alternatives compared on validation data (Appendix E.2).
  • Section 3 now states its goal and the "why". It opens with the goal and three requirements (identity, validity, and exactness), and points each requirement to the subsection that addresses it. A new paragraph explains why we summarize features separately, with a direct test against a joint encoder.
  • For Proposition 1, "capacity" and "monotone" are now defined in Section 3.2, before the proposition. A plain-language reading follows it: any real-valued choice of the parameters gives a valid capacity, and every capacity with strict increases can be reached, so training needs no constraints.
  • On biomarkers and depression scores, the introduction now states the clinical task, and Section 5.3 describes the 21 inputs (ten measured biomarkers and eleven diet components) and the 14 outcomes.
  • We replaced "not changes in clinical outcome units" with an explicit statement of how a set term translates into outcome units through the decoder (end of Section 3.4).
  • We condensed Section 5 to the goal, data, and metric of each experiment. Preparation details and hardware moved to Appendices D and E.5.
  • For the numbers in Section 6, we removed five-decimal values from the text and tried to pair each remaining number with its comparison and its meaning, for example "about 3 percent higher than trees". The example you quote, cosine -0.036 to 0.066, is now explained as disagreement between predictors on triples, and it is used to make the point that stability is not correctness.

Thank you again for the detailed reading.

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Paper summary

This paper addresses the interpretability of high-order feature interactions in longitudinal prediction tasks and proposes the Recursive Choquet model. Its core contribution lies in constructing a prediction modeling framework that supports structured and exact decomposition.

Critical strengths
  1. The model preserves variable identities from raw temporal features to the aggregation layer. The paper distinguishes between set values, marginal gains and pure interaction coefficients to avoid conceptual ambiguity.

  2. This parameterization constructs set values via the maxima over subsets. Theoretical proofs are provided to support the representational capacity and validity of the model design.

Critical weaknesses
  1. While the paper demonstrates that the full Recursive Choquet model bears high empirical computational overhead, it lacks a formal mathematical derivation of its theoretical time complexity for both the training and inference stages.

  2. Current benchmarks mainly consist of classic black‑box time‑series baselines and internal model ablations. I would like the authors to add experimental comparisons or theoretical comparative discussions against more recent advanced methods relevant to this work.

Questions for authors

Please refer to Weakness.

4 comments

Thank you for the review and for the two clear requests. We addressed both with a new derivation and with new experiments. Section and table numbers refer to the revised PDF.

W1. Time complexity for training and inference

We added a formal derivation in Appendix B.5, summarized in Section 3.5, and checked it against measurements. Here n is the number of features (21 in the clinical model), and there are 42 capacities (14 outcomes times 3 time functions).

  • To build one capacity, we process sets in increasing size. A set of size k takes a maximum over its k immediate subsets, followed by one sigmoid and one update. Summed over all sizes, this is n times 2^(n-1), minus n, subset values examined, and 2^n minus 2 sigmoid evaluations. So building all capacities takes time on the order of 42 times n times 2^(n-1), and memory on the order of 42 times 2^n. Backpropagation has the same order.
  • In training, one optimizer step costs the construction above, plus a per-participant part for a batch of B participants with T visits each. That part covers the time summaries (n times T), one sort (n log n), and one lookup per chain set and capacity (42 times n). The exponential part is paid once per step and is shared by the whole batch.
  • At inference, each participant only needs the n sets on its sorted chain. So once the table is computed after training, prediction computes the per-participant part only, with no exponential term. Storing the table still takes exponential memory.
  • For explanations, all interaction coefficients of one capacity follow from the fast Mobius transform in n times 2^n operations.
  • As a check against the reported numbers, the formulas reproduce the parameter count exactly: 42 times (2^21 minus 2), plus 489 other parameters, gives 88,080,789. They also reproduce the reported number of directed additions.
  • We also measured the cost. Table 8 times construction from 12 to 24 features. As predicted, peak memory roughly quadruples with every two added features, and the time follows the operation count from 16 to 22 features. At 24 features, one forward and backward pass through the construction takes 7.7 seconds and 25 GB; optimizer states and the participant batch come on top of that. With the table cached, inference averages 0.009 ms per history, against 0.087 ms when the table is rebuilt for every batch. These are averages over GPU batches, not the end-to-end latency for a single patient.
  • Table 7 compares these costs with k-additive Choquet, GRU-D, and the Transformer. We estimate the practical limit at about 24 features on one 48 GB GPU. Beyond that, a restricted or sparse capacity is needed, and the paper now says so.

W2. Comparison with more recent methods

We added both experiments and discussion (Section 5, Table 1, Appendix G). iChIMP [1], the restricted capacities, EBM [2, 3], and SPAM [4] go through the same prediction-explanation protocol as the original baselines. NID [5] is evaluated separately, by how it ranks the planted interactions, and the two adapted neural models [6, 7] are evaluated on synthetic data only.

  • iChIMP [1] is the closest learned fuzzy-measure construction. We used it in its published form and with a softplus increment, as a drop-in replacement for our capacity (Section 6.2).
  • Restricted k-additive Choquet capacities of order 1 to 3, including an exact 2-additive class.
  • EBM, also known as GA2M [2, 3], with automatic pair selection.
  • SPAM [4] of order 2 and 3, a scalable higher-order interaction model.
  • NID [5], which detects interactions from network weights, on the synthetic data.
  • HarsanyiNet-style [6] and IMV-LSTM-style [7] models on the synthetic data. Neither has an official implementation for our longitudinal setting, so these are our own adaptations. They fit the generators poorly, and we say in the paper that their results should not be read as a verdict on the original methods.

The main findings are:

  • On the higher-order synthetic generator, our attribution error is at least 11 times lower than that of the 15 external comparison predictors, at every order from one to six. Our own progressive ablation is not counted among them; its gap is much smaller. Part of the advantage comes from fitting the generator better. On the pair-only generator, the picture reverses as expected: the exact 2-additive class is best at orders one and two. We report both results.
  • NID ranks the planted pairs first to third and the planted triple second to fifth. It gives no signs, though, so it cannot tell synergy from redundancy (Table 37).
  • In clinical prediction on imputation 1, SPAM [4] of order 2 is the most accurate interpretable model (0.5074, against 0.5215 for ours and 0.5045 for boosted trees). However, its pair explanations are much less stable across training seeds (cosine 0.226, against 0.778 for ours). SPAM of order 3 also predicts better than our model (0.5098), and its triple explanations are much less stable (cosine 0.047, against 0.677).
  • The published iChIMP form [1] is more stable than ours on clinical triples (0.797), but it predicts worse and clips 39 percent of its set values at one, where they receive no gradient. We did not evaluate the clinical stability of the softplus iChIMP variant, so we make no stability claim against it.
  • Taken together, these comparisons clarify the trade-offs. They do not show that our model is better on every criterion.

We also added discussion of NIT [8], Archipelago [9], Kang et al. on Mobius recovery (NeurIPS 2024) [10], and InstaSHAP (ICLR 2025) [11] to Related work. A new table in Appendix A.3 (Table 4) compares all of these methods on interaction order, exactness, monotonicity, temporal identity, and cost.

Thank you again for the helpful suggestions.

AuthorsOpenReview ↗

References

[1] Islam, M. A., Anderson, D. T., Pinar, A., Havens, T. C., Scott, G. J., and Keller, J. M. (2020). Enabling Explainable Fusion in Deep Learning with Fuzzy Integral Neural Networks. IEEE Transactions on Fuzzy Systems, 28(7), 1291-1300.

[2] Lou, Y., Caruana, R., Gehrke, J., and Hooker, G. (2013). Accurate Intelligible Models with Pairwise Interactions. Proceedings of the 19th ACM SIGKDD International Conference on Knowledge Discovery and Data Mining, 623-631.

[3] Nori, H., Jenkins, S., Koch, P., and Caruana, R. (2019). InterpretML: A Unified Framework for Machine Learning Interpretability. arXiv preprint arXiv:1909.09223.

[4] Dubey, A., Radenovic, F., and Mahajan, D. (2022). Scalable Interpretability via Polynomials. Advances in Neural Information Processing Systems (NeurIPS 2022).

[5] Tsang, M., Cheng, D., and Liu, Y. (2018). Detecting Statistical Interactions from Neural Network Weights. International Conference on Learning Representations (ICLR 2018).

[6] Chen, L., Lou, S., Zhang, K., Huang, J., and Zhang, Q. (2023). HarsanyiNet: Computing Accurate Shapley Values in a Single Forward Propagation. Proceedings of the 40th International Conference on Machine Learning, 202, 4804-4825.

[7] Guo, T., Lin, T., and Antulov-Fantulin, N. (2019). Exploring Interpretable LSTM Neural Networks over Multi-Variable Data. Proceedings of the 36th International Conference on Machine Learning, 97, 2494-2504.

[8] Tsang, M., Liu, H., Purushotham, S., Murali, P., and Liu, Y. (2018). Neural Interaction Transparency (NIT): Disentangling Learned Interactions for Improved Interpretability. Advances in Neural Information Processing Systems (NeurIPS 2018).

[9] Tsang, M., Rambhatla, S., and Liu, Y. (2020). How Does This Interaction Affect Me? Interpretable Attribution for Feature Interactions. Advances in Neural Information Processing Systems (NeurIPS 2020).

[10] Kang, J. S., Erginbas, Y. E., Butler, L., Pedarsani, R., and Ramchandran, K. (2024). Learning to Understand: Identifying Interactions via the Möbius Transform. Advances in Neural Information Processing Systems (NeurIPS 2024).

[11] Enouen, J., and Liu, Y. (2025). InstaSHAP: Interpretable Additive Models Explain Shapley Values Instantly. International Conference on Learning Representations (ICLR 2025).

Thank you for the thorough response and substantial revisions; the new complexity analysis, empirical measurements, and comparisons directly address my main concerns.

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Paper summary

The paper proposes a Recursive Choquet model for longitudinal prediction with interpretable higher-order feature interactions. It summarizes each feature's history into a scalar, then combines summaries with a complete fuzzy measure to guarantee monotonicity and normalization. The paper evaluates on synthetic generators and a clinical cohort against boosted trees, GRU-D, and a Transformer.

Critical strengths

The signed synthetic example tests both positive and negative interactions rather than only positive planted effects. The common Faith-Shap/Shapley–Taylor protocol makes final-prediction explanations comparable across models. The clinical study includes multiple imputations and training seeds, paired prediction comparisons, and computational measurements. The lower-order ablations and imperfect higher-order stability are reported openly.

Critical weaknesses
  1. Insufficient motivation for the longitudinal design. The model summarizes each feature's history independently, then models cross-feature interactions only at the summary level. The paper never justifies why this is preferable to an end-to-end model that learns temporal and cross-feature structure jointly, such as GRU-D or a Transformer.
  2. Worst clinical prediction among compared methods. In Table 2, Recursive Choquet has the highest macro standardized MSE (0.52149), worse than boosted trees (0.50429), GRU-D (0.50761), and the Transformer (0.51559). Table 24 confirms significantly lower paired MSE for boosted trees and GRU-D. The proposed method sacrifices prediction accuracy for explanations.
  3. The model scales 2^n with the number of features n. Higher-order terms are not shown to improve clinical prediction, and Table 23 shows selection frequency dropping from 0.690 for pairs to 0.103 for five-feature interactions. The cost is therefore not justified by demonstrated benefit, and the resulting latency makes the model impractical for real applications.
  4. No comparison with state of the art, and the technical novelty is not established. Most citations predate 2020. One 2020 paper the manuscript cites, Islam et al.'s iChIMP, already constructs a measure recursively from the maximum of subset values plus a nonnegative learned increment (Eq. 10). Its public implementation uses immediate predecessors and clips at one. Eq. 3 instead scales a sigmoid increment by the remaining distance to one. The paper does not establish a representational or optimization advantage over that closely related construction. A more precise account of what is technically new, together with a direct iChIMP comparison, is needed.
  5. In the matched imputation-1 comparison, the 2-additive model improves test MSE from 0.521481 to 0.514919, reduces parameters from 88,080,789 to 10,191, and reduces training time from 3,676 to 517 seconds (Table 25). Low-order refits also have stronger internal selection stability (Appendix E.3). However, these models are excluded from the common final-prediction explanation comparison, leaving the central accuracy–explanation–cost trade-off unresolved.
  6. Presentation and consistency problems. Numerical precision is inconsistent across tables, and significant figures vary within Table 3. The hardware is stated as "3 Nvidia RTX A4000 48GB GPUs," but this type may not exists (typo?).
Questions for authors
  1. What property of Eq. 3 is unavailable in iChIMP's recursive measure construction? Could you compare their representable capacities, optimization behavior, and interaction recovery using the same temporal summaries and outcome decoder?

  2. Could you include the 1-/2-/3-additive variants and a relevant interpretable higher-order comparator in the common prediction-explanation evaluation, with explicit handling of zero interactions? What measured explanation benefit justifies the complete model's substantially greater cost and worse clinical prediction?

  3. Can the high-order terms demonstrate a reproducible clinical or predictive benefit beyond the lower-order models?

4 comments

Thank you for the detailed and specific review. Your questions shaped most of the new experiments in this revision. We ran every comparison you asked for. Some of the answers are not in our favor; we report them as they came out and narrowed our claims to match. Unless we say otherwise, the new results are secondary analyses (designed after we saw the original test results) on imputation 1 with three seeds. Section and table numbers refer to the revised PDF.

W1. Why summarize each feature history separately?

This is a fair point, and the original paper did not argue it. Section 3 now opens with the goal and three requirements, and a new paragraph, "Why separate summaries?", gives the reasons and the evidence.

  • The main reason is identity. If an encoder mixes all features in its first layer, the capacity is defined over learned mixtures, and its coefficients no longer name an interaction between, say, glucose and insulin. With separate summaries, each interaction coefficient is a property of the model rather than an approximation of it.
  • We tested the joint alternative you describe. We replaced the separate summaries with a shared GRU that reads all 21 histories together, and kept the same 2-additive capacity, decoder, and likelihood (Appendix G.1 and G.6). Test error went up from 0.5149 to 0.5207, and pair explanations became less stable across seeds (cosine 0.648 against 0.927). So in this cohort, separation did not cost accuracy.
  • Separation also keeps missing history local to one feature. Deleting 20 percent of the history raises our error by 0.87 percent, against 2.70 to 6.95 percent for the external predictors (Table 15). This shows robustness, but the comparison does not isolate separation as its cause.
  • We also state the cost. The model cannot represent temporal cross-feature effects, such as glucose rising while weight falls. When the generating interactions change over time, its error rises (Appendix F.1).

W2. Worst clinical prediction

You are right, and we now say so directly in the abstract and in Section 6.4. Over 30 fits, boosted trees are the most accurate, and our error is about 3 percent higher (0.5215 against 0.5043). The paired bootstrap favors trees and GRU-D. We added a breakdown and one attempted fix.

  • About two thirds of the gap to trees comes from four nearly static anthropometric outcomes: height, weight, BMI, and waist circumference. Without them, our error is slightly below the Transformer's (0.648 against 0.652). For glucose, we are the most accurate of the original models (Appendix D.2).
  • We tested whether the gap comes from our forced relaxation away from the last recorded value. We added a learned weight that lets the recorded value persist. It did not lower validation error (Appendix D.2), so we do not claim to know the full cause.
  • So the trade-off is real. The complete model gives up some accuracy in exchange for exact explanations, and we present it that way.

W3. Exponential cost without a demonstrated benefit

We agree that higher-order terms did not improve clinical prediction, and Section 6.6 now says so plainly. Your reading of Table 23 is also correct: internal selection stability falls with order. In response, we made three changes.

  • The cost is now derived and measured. Appendix B.5 derives time and memory for training and inference. Table 8 measures construction from 12 to 24 features. At 24 features, one forward and backward pass over all 42 capacities takes 7.7 seconds and 25 GB. So we estimate that the complete measure is practical up to about 24 features on one 48 GB GPU, and not beyond.
  • Prediction computation is not exponential. Each participant only uses the n sets on its sorted chain. Once the capacity table is computed after training, prediction averages 0.009 ms per history in batches on one A100 GPU. When the table is rebuilt for every batch, as in our original timing, it takes 0.087 ms. The predictions are identical (Section 3.5). The exponential cost is in training computation, parameters, and storage of the table, which also has to be kept at deployment.
  • We changed what we claim the complete model is for. It is costly and did not help clinical prediction here. So we now present it as an exploratory diagnostic for higher-order structure, followed by a restricted capacity for deployment (Discussion). A k-additive model cannot serve this purpose, because it fixes every term above order k to zero. It is not a calibrated test, though: when few high-order sets are supported by the data, weak recovery does not show that higher-order structure is absent.

W4 and Q1. iChIMP and what is new

Thank you for pointing us to iChIMP; we compared it directly. We agree that it is the closest prior construction, and we have corrected our description of it in Related work. iChIMP takes the maximum over the immediate subsets, adds a ReLU increment, and clips at one. The contributions now say that our construction belongs to the same subset-maximum family.

Here is what is different, and what it buys:

  • In terms of representation, our headroom-scaled form maps any finite parameters one-to-one onto the strictly monotone capacities (Proposition 1). Clipped iChIMP can also reach boundary capacities exactly, meaning a set equal to its subset or equal to one; ours reaches those only as a limit. So we do not claim a larger class of capacities. The difference is in optimization.
  • Clipping hurts optimization. Saturated sets all sit at one and their parameters get no gradient. A ReLU increment at zero gets no gradient either. We ran a drop-in comparison with the same temporal summaries, decoder, likelihood, and training settings (Section 6.2, Appendix G.2, Table 34):
    • With complete probes, the published iChIMP form has about five times our interaction error (0.036 against 0.0066). About 40 percent of its increments receive no gradient at convergence.
    • A softplus variant, still with clipping, matches our probe recovery (0.0065) and our clinical error (0.5216 against 0.5214). But it still clips 10.7 percent of the clinical set values at one, against 39 percent for the published form. We did not evaluate its clinical stability or attribution mass, so we make no stability claim against it.
    • In the longitudinal explanation study, both clipped forms fit the generator about 50 times less accurately, and their attribution errors are 12 to 142 times larger at every order.
  • So our claim is now narrow and, we believe, defensible. Headroom scaling avoids hard clipping and the dead increments of a ReLU, with unconstrained parameters. It is not a new class of capacities. We also do not claim that every parameter gets a useful gradient: the maximum is not differentiable at ties, and sets that the data rarely support can still be poorly informed.

W5 and Q2. Restricted models in the common comparison

We have done this. The 1-, 2-, and 3-additive models, an exact 2-additive class, a second 3-additive variant, EBM, and SPAM of order 2 and 3 now all go through the same final-prediction explanation protocol. They are evaluated on both synthetic generators and for clinical stability (Table 1, Appendix G.3 and G.4). Zero interactions are handled explicitly. Where a model cannot represent an order, its entry is shown in gray with a dagger. Its synthetic error then equals the size of the reference terms, and its clinical terms at that order arise only through the nonlinear depression likelihood.

Here is what this shows, both for and against the complete model:

  • When higher-order structure exists, only the complete models are accurate. On the higher-order generator, our attribution error is at least 11 times lower than that of the 15 external comparison predictors, at every order (our own progressive ablation is not counted among them). Restricted models are inaccurate even at the orders they can represent, because higher-order effects leak into lower-order terms. For example, the 3-additive variant's pair error is 220 times ours.
  • When it does not exist, the right restricted model wins. On the pair-only generator, the exact 2-additive class is best at orders one and two, and the restricted models' errors above order two are effectively zero. Our spurious higher-order terms stay small.
  • Part of our synthetic advantage comes from fitting the generator better. So we do not claim an explanation advantage at matched prediction error (Section 6.3).
  • Clinical stability is mixed. Our triples are more stable than those of the black-box models, both SPAM models, and the standard 3-additive model (cosine 0.677 against 0.047 to 0.450). But two models are more stable than ours. Published iChIMP (0.797) predicts worse and clips 39 percent of its set values. The 3-additive variant (0.839) puts about 500 times less weight on triples (Section 6.5). Stability across seeds is also not the same as clinical correctness, and we do not claim the latter.

To answer your last question directly: in this clinical cohort, we did not find an accuracy or explanation benefit that justifies the complete model's cost for deployment. The measured benefit is the synthetic one, namely detecting and recovering higher-order structure when it exists. That is why we now recommend the complete model as an exploratory diagnostic before choosing a restricted model.

Q3. Do the high-order terms give a reproducible clinical benefit?

Honestly, no, not in this cohort, and the paper now says so.

  • We took the three- to five-feature sets that recur among the ten largest, with a consistent sign, in at least 70 percent (65 sets) or 50 percent (126 sets) of the 30 complete fits. We added them to the 2-additive model. Test error did not change (0.5151 and 0.5152, against 0.5149; Section 6.6 and Appendix G.5).
  • These stable triples are only partly reproducible. They reappear among a 3-additive fit's ten largest triples in 10 to 19 percent of cases, against 0.75 percent by chance, but with the same sign only 62 to 64 percent of the time.
  • Part of the reason lies in the data. In the representative fit, only 5.9 percent of all sets appear on any participant's sorted chain, so most high-order set values get no direct evidence (Section 4.2, Appendix B.4).

W6. Precision and hardware

Thank you for catching both. The hardware was three NVIDIA RTX A6000 GPUs with 48 GB each; A4000 was a typo (Appendix E.5). The added experiments ran on A100 GPUs, and we now say that too. On precision, we rebuilt the main explanation table with one fixed format per column, and the main text no longer quotes five-decimal values. We also tried to pair each number in the text with what it is compared against.

Thank you again for the very concrete questions. They made the paper more honest about where the complete measure helps and where it does not.

I have read the author's response to my comments.

Reviewer_qdHqOpenReview ↗
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Paper summary

The paper introduces a longitudinal Choquet model that addresses the challenge of explainable longitudinal predictions, where multiple variables and their past measurements can interact jointly to influence future predictions. This is made possible by first creating a weighted aggregation of each feature’s history and combining these aggregations using a complete, monotone fuzzy measure. In addition to longitudinal predictions, this setup facilitates explanations through signed interaction decomposition. The authors provide mathematical proofs and conduct controlled validation using synthetic data with known interactions. They also assess the performance of their model in a clinical prediction setting, where they observe more stable explanations than those produced by alternative prediction and explanation methods.

Critical strengths

Although the validation experiments in clinical settings require substantial future work and attention to practical deployment constraints, I recommend accepting the manuscript in its current form as a strong methodological contribution. The following points support my assessment:

The method facilitates both longitudinal prediction and explanation through an exact decomposition of the Choquet aggregate into signed interaction terms. This direct link between the prediction mechanism and explanation helps avoid the additional uncertainty introduced by the design choices required when post-hoc methods such as SHAP are applied to black-box models.

Preserving feature identity during temporal aggregation could make the resulting interactions easier for domain experts to assess in clinical applications.

Distinguishing capacity values, addition gains, and signed interactions avoids interpreting these quantities interchangeably. The synthetic experiments further demonstrate this point by including cases in which identical capacity values can correspond to interactions with opposite signs.

The experiments are well designed, involving distinct training, validation, calibration, and test splits; evaluating multiple instances of interactions; separating prediction error from explanation accuracy and stability; and comparing the method against common alternatives and explanation methods. Theoretical guarantees are also provided in addition to empirical evidence. The results are reported using cautious wording, with transparent reporting of unfavourable experiments and the limitations surrounding the clinical prediction experiments.

Critical weaknesses

The paper already transparently acknowledges most of its limitations, including the need for domain experts to assess the explanations and the model’s computational constraints. However, it would be valuable to comment on the sensitivity of both predictions and explanations in cohorts with small sample sizes and high-dimensional feature spaces, as these conditions are common in clinical research.

Questions for authors

Please define all the terms in equations for the general audience (for example in Equation 4).

Please consider adding intuitive analogies from the target domain (clinical setting in this case) for math-heavy parts.

3 comments

Thank you for the careful and generous review. We are glad that the separation of capacity values, gains, and signed interactions came across clearly, and that you found the experimental design and our reporting of unfavorable results useful. Below we answer your three points. All section, table, and appendix numbers refer to the revised PDF.

1. Small samples and many features

We agree that this matters for clinical research, and we added direct evidence on it. In short, the complete model is sensitive in a way that is consistent with the order-dependent error bound. So we now recommend it as an exploratory diagnostic for data sets with tens of features and enough participants, and we recommend a restricted or sparse capacity for small or high-dimensional cohorts. This is stated in a new Discussion paragraph, "Small samples and many features".

Here is what we measured.

  • Lemma 2 explains why higher orders suffer first. It bounds the error of an interaction of order k by 2 to the power k times the error in the set values. So when the set values are estimated less precisely, for example from fewer participants, the high-order interactions are the most exposed. This is a worst-case bound, not a guarantee about any particular sample size, and we do not establish a minimum sufficient sample size. We now say this right after Lemma 2.
  • With fewer participants, synthetic recovery gets worse. Cutting the training histories from 20,000 to 2,000 raises interaction error from 0.022 to 0.047.
  • For fewer participants on clinical data, we added a learning curve with 1,000, 5,000, 20,000, and 50,000 training participants (Appendix G.6, Table 42). The 2-additive model is more accurate than the complete model at every size. The difference is largest at 5,000 to 20,000 participants (about 0.011 to 0.013 in standardized MSE) and smallest at 1,000 (about 0.003).
  • Clinical refits on 70 percent subsets keep a top-ten overlap of 0.58 for pairs and 0.33 for triples, against 0.73 for pairs in the 2-additive model.
  • We also varied the number of features. With complete probes, the triple error grows by a factor of 1.6 to 2.0 when we go from 6 to 12 features (Appendix G.6, Table 43). So the growth is gradual when every set is observed. Complete probes cover every set, however, so this does not show that the model scales under sparse clinical observation.
  • We also checked which sets the data actually inform. A set value only gets direct evidence if that set appears on some participant's sorted chain. In our clinical training data, using one representative fitted model, this holds for 89 percent of pairs and 70 percent of triples, but only for 5.9 percent of all sets (Section 4.2, Appendix B.4). Most high-order set values are therefore shaped by the recursion from their subsets rather than by the data. We think this is the most important practical caveat for small cohorts, and the main text now says so.
  • The cost also grows with more features. Memory grows as 2 to the power n. On one 48 GB GPU, we estimate that the complete measure is practical up to about 24 features (Section 3.5, Appendix B.5, Table 8). Beyond that, a restricted or sparse capacity is needed.

2. Defining the terms in the equations

Thank you. We went through the equations in Section 3 with a general reader in mind. For Equation 4 in particular, every symbol is now defined right after the equation:

  • f is the long-run level that the forecast relaxes towards.
  • The term 2C - 1 recenters the Choquet aggregate from the range 0 to 1 to the range -1 to 1.
  • b and a are the intercept and scale that put it on the standardized outcome scale.
  • h is the forecast horizon in years from the landmark.
  • kappa is a learned rate, so that r(h) rises from 0 at the landmark towards 1.

We also added a sentence at the end of Section 3.4 that explains how one set term translates into outcome units. In the same way, Equation 1 now explains z_ij, the weights, and the elapsed time, and it gives the softmax formula. A full notation table is in Appendix A.1 (Table 2).

3. Clinical analogies for the math-heavy parts

We like this suggestion very much. We added short clinical readings where the math is heaviest, and collected them in a new Appendix A.2 (Table 3). Here are some examples:

  • Summarizing each feature over time is like a clinician reading each laboratory trend separately before forming an overall judgment.
  • A capacity value v(S) says how much the forecast relies on a group of measurements together, for example glucose and insulin together for a HOMA-IR forecast.
  • The min term in the decomposition behaves like a clinical rule that needs every criterion at once.
  • G(S) asks how much adding a measurement to the panel raises the capacity on average, and d(S) asks how much of that increase is genuinely joint. Both are increments of the fitted capacity, not measured gains in clinical utility or prediction accuracy.
  • A positive interaction means synergy. A negative one means overlapping information that would otherwise be counted twice. Both describe the capacity on the transformed inputs; the contribution to an outcome also depends on the decoder.
  • In one representative fit, glucose with insulin for HOMA-IR is the most negative pair. HOMA-IR is computed from glucose and insulin, so this example illustrates how the fitted model aggregates them. It is not independent clinical validation.

We are careful to say in the text that these readings describe how the model combines its inputs. They are not causal effects of changing a clinical variable.

Clinical validation

We also agree with your remark that the clinical side needs substantial future work. The revised Limitations paragraph says that clinical use requires external validation and evaluation by clinicians and domain experts.

Thank you again for the constructive suggestions.

Thank you for your response. I appreciate the extra effort you put into discussing the "small sample, many features" case. I am satisfied with the responses. I am happy to assist the AC further in the discussion phase.

Comments on the paper

1 comment

We thank all four reviewers for their time and for detailed, constructive reviews. We have uploaded a revised paper; the main text stays within 10 pages. Below is a short summary of the main changes. Each reviewer also gets a separate point-by-point reply. New results are secondary analyses, designed after we saw the original test results, and the paper labels them that way.

  1. We narrowed and clarified our claims. The contribution is the combination of longitudinal summaries that keep each feature's identity, a headroom-scaled complete capacity, and a common evaluation of prediction explanations. The abstract, introduction, and discussion now state the trade-off plainly, including the parts against us. Our clinical error is about 3 percent higher than that of boosted trees. Pair-level capacities are more accurate and cheaper in this cohort. And the clinical data support few high-order sets. We now present the complete fuzzy measure as an exploratory diagnostic for higher-order structure, to be followed by a restricted capacity for deployment. It is not a calibrated test, and weak recovery does not show that higher-order structure is absent.

  2. We compared our construction directly with iChIMP (Section 6.2). It belongs to the same subset-maximum family. Headroom scaling avoids hard clipping and the dead increments of a ReLU. In a drop-in comparison, the published iChIMP form recovers interactions less accurately, while a softplus variant essentially matches our static recovery and clinical prediction. Both clipped forms do worse on the longitudinal synthetic task. We present this as an optimization improvement in the settings we tested, not a new class of capacities.

  3. We added many more comparators and state the scope of each (Table 1, Appendix G). Restricted k-additive capacities, EBM, SPAM of order 2 and 3, and iChIMP go through the same prediction-explanation protocol as the original baselines. NID gets a separate ranking evaluation. The HarsanyiNet-style and IMV-LSTM-style models are our own adaptations and are evaluated on synthetic data only; they fit poorly, so they say little about the original methods. Structural zeros are marked explicitly. On the higher-order generator, our attribution error is at least 11 times lower than that of the 15 external comparison predictors (our own progressive ablation is not counted among them). Part of this comes from fitting the generator better, so it is not an explanation advantage at matched prediction error. On pair-only data, the right restricted model is better.

  4. We addressed cost, scaling, and identifiability. We added a complexity derivation (Appendix B.5) and a scaling benchmark from 12 to 24 features (Table 8). Training time and storage are exponential in the number of features. With the capacity table cached, prediction averages 0.009 ms per history in GPU batches; the cached table itself still needs exponential storage. The practical limit of about 24 features refers to one 48 GB GPU. We also added a diagnostic of which clinical sets the data actually inform (Section 4.2, Appendix B.4). It uses one representative fitted model and does not establish identifiability of the full jointly learned model.

  5. We examined small samples, joint encoders, and the benefit of higher orders (Section 6.6, Appendix G.6). We added a clinical learning curve, a joint GRU encoder baseline, and a check of whether stable higher-order sets help a restricted model. They do not, and we say so.

  6. We improved the presentation. Theorems are restated as classical lemmas with citations. Section 3 opens with its goal and requirements, and every term is defined. Clinical analogies are in a new Appendix A.2; they describe how the fitted model combines its inputs, not clinical benefit or causal effects. Section 5 is condensed, and the numbers in Section 6 now come with comparisons. We also added a related-methods table (Appendix A.3).

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

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