acceptodds
Under review as a conference paper at ICLR 2027

CRAFT: Counterfactual Utility-Guided Dynamic Reasoning for Traditional Chinese Medicine Prescription Recommendation

Abstract

Traditional Chinese Medicine (TCM) prescription recommendation is commonly formulated as static multi-label prediction, overlooking how therapeutic demands evolve during prescription construction. To address this limitation, we propose CRAFT, a Counterfactual utility-guided dynamic Reasoning framework with Adaptive Fusion for TCM prescription recommendation. CRAFT first performs hierarchical graph reasoning over symptom–symptom, symptom–herb, and herb–herb relations to capture structured clinical dependencies. It then reformulates prescription generation as an order-free dynamic decision process, where each step evaluates candidate herbs according to their neural compatibility and Counterfactual Marginal Utility (CMU). CMU performs candidate-level what-if evaluation by estimating the additional coverage of residual therapeutic demand if a candidate herb were added to the current partial prescription. CRAFT adaptively integrates this utility into neural decision scores and progressively constructs the prescription until a learned STOP action is selected. Experiments on two benchmark TCM prescription datasets demonstrate consistent improvements over competitive baselines, while further analyses show that CMU provides informative candidate-level signals throughout the dynamic reasoning process. The source code is publicly available at https://anonymous.4open.science/r/CRAFT-DAD6/.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Counterfactual Reasoning, Sequential Decision Making, Graph Neural Networks

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_YFSNOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

CRAFT frames traditional Chinese medicine prescription recommendation as stepwise set construction. It encodes symptom–herb relations via hierarchical graph reasoning, combines a neural compatibility score with a co-occurrence-based marginal symptom-coverage utility (CMU), and learns a STOP action to decide prescription length. A holistic scoring branch and final calibration layer sit on top of the trajectory scores. Evaluation uses TCM PD and TCM SMGCN, with fixed-cutoff ranking metrics as the primary measures.

Critical strengths
  1. The stepwise construction with CMU-guided expansion is a natural fit for prescription generation, where both the set of herbs and the size of the set matter clinically. The writing is clear, and the graph reasoning plus CMU formulation is well explained.
  2. The ablation study and Figure 3 together show that CMU matters to the trained model: the inference-time perturbation produces clear drops, and the coverage function's properties are well illustrated.
Critical weaknesses
  1. The released code selects checkpoints by test F1@10 and uses test scores for early stopping. If this procedure produced the main tables, the reported results are not proper held-out evaluations. On top of that, the public scoring path is missing the holistic branch and final calibration described in the paper, so which model was actually evaluated is uncertain. Finally, the fixed-K metrics in the main tables don't measure the quality of prescriptions actually terminated by the learned STOP; the Table 3 examples are illustrative but not a dataset-level evaluation of this central feature.
  2. The experiments don't convincingly show why dynamic construction is needed over simpler alternatives. Thresholded multilabel models and sequential decoders already produce variable-size sets, but the paper lacks a matched comparison isolating the benefit of the learned construction process. CMU and dynamic reasoning contribute unevenly across datasets. Figure 3 shows the coverage function's properties and the trained model's reliance on CMU, but this doesn't explain why the retrained ablation effects on TCM PD are small. The clinical interpretation of CMU should also stay consistent with its stated definition — a co-occurrence-based, non-causal score.

AI-use disclosure. I could not find the required disclosure section in the manuscript or appendix.

Questions for authors
  1. Which data splits were used for checkpoint selection and early stopping? If the released procedure generated the results, can you re-evaluate with a proper validation split? Do different K values end up selecting different epochs?
  2. Which exact code version produced Tables 1–4? Where are the holistic branch and final calibration in that version? The README entry point and optimizer also don't match the manuscript — can you reconcile them?
  3. What are the actual set quality and length errors of prescriptions terminated by STOP, across each dataset?
  4. How does the learned construction compare with a matched thresholded multilabel model or a representative sequential decoder on the same TCM data?
  5. How much of CRAFT's performance can a CMU-only greedy selector recover?
  6. On TCM PD, the retrained CMU ablation shows small effects while the inference-time perturbation shows large ones, and dynamic reasoning contributes differently on SMGCN. How do you explain these discrepancies?
4 comments

We thank Reviewer YFSN for the close reading of both the paper and the released code. The points raised are exactly the ones that most need strengthening, and we address them below.

W1 / Q1 — The released code selects checkpoints by test F1@10 and uses test scores for early stopping; do different K values select different epochs?

This point deserves a direct fix rather than a clarification. In the revision we will report results from models re-trained with an explicit held-out validation split, with checkpoint selection and early stopping driven by validation F1@10 only. A single checkpoint will be selected per run and all values of K reported from that checkpoint, so K can no longer influence which epoch is selected. The updated training logs and evaluation scripts will be released together with the revision, and any change in the numbers will be reported transparently.

W2 / Q2 — Which code version produced Tables 1–4? Where are the holistic branch and final calibration? README and optimizer mismatch.

We apologize for the inconsistency between the released code and the paper. We will align them fully: the holistic branch (Section 3.5) and the final calibration layer (Section 3.7) will be included in the public repository, the README entry point and optimizer setting will be corrected to match Appendix A.3, and the exact commit that produced Tables 1–4 will be tagged and cited in the revision.

Q3 — What are the actual set quality and length errors of prescriptions terminated by STOP, across each dataset?

These will be reported in the revision as part of the adaptive-termination evaluation described above (length MAE and P/R/F1 of STOP-terminated prescriptions per dataset), so that the central feature of the method is measured at the dataset level rather than only through the two illustrative cases.

Q4 — How does the learned construction compare with a matched thresholded multilabel model or a representative sequential decoder on the same TCM data?

We will add this matched comparison in the revision: a thresholded multilabel model (tuned per patient or per dataset) and a representative sequential decoder, evaluated under the same splits and protocol, to isolate the benefit of the learned order-free construction process itself.

Q5 — How much of CRAFT's performance can a CMU-only greedy selector recover?

We will report the CMU-only greedy selector as a dedicated baseline on both datasets, quantifying how much of CRAFT's performance comes from the utility signal alone versus the neural compatibility and dynamic state tracking.

Q6 — On TCM_PD, the retrained CMU ablation shows small effects while the inference-time perturbation shows large ones; dynamic reasoning contributes differently across datasets. How do you explain these discrepancies?

We view these as consistent rather than contradictory. The retrained ablation lets the model redistribute reliance onto the holistic/global branch during training, which partially compensates for the missing CMU input; the inference-time intervention instead isolates a dependence that was actually learned under CMU, so its effect is larger. The cross-dataset difference reflects the varying strength of the residual-demand signal relative to the graph-based representations on each dataset. We will add this discussion to Section 4.5 in the revision.

AI-use disclosure

We have added the disclosure to Appendix A.4: "No AI tools were used in the writing of this paper," consistent with our OpenReview declaration.

Additional Response (1/2): Implementation Consistency and Evaluation Reliability

We thank the reviewer for carefully examining our released implementation. We would like to clarify the code-version discrepancy and report the results of our completed re-evaluation.

1. Clarification regarding the released code (W1/Q2)

We acknowledge that the previously released repository snapshot was not synchronized with the full architecture and evaluation procedure described in the manuscript.

In particular, the released version does not contain the complete holistic prescription branch, dynamic–global fusion, or final inference calibration. Its checkpoint-selection procedure also relies on test-set metrics.

We apologize for this inconsistency. We agree that the released implementation, in its current form, is insufficient to reproduce the complete method described in the paper.

We are preparing an updated repository release containing the complete model implementation, training and inference entry points, configuration files, and evaluation scripts.

Importantly, we distinguish this code-release issue from the results of our newly conducted experiments. The revised results are obtained using an explicit validation-based evaluation protocol, as described below.

We will also provide a code-to-result mapping identifying the implementation, checkpoints, and logs associated with the revised experimental results. Until this provenance is fully documented, we do not claim that the existing public snapshot reproduces all results in Tables 1–4.

2. Revised validation protocol (W1/Q1)

We conducted new experiments on both datasets using three random seeds (2021, 2022, and 2023).

The original training partitions were divided into fitting and validation subsets, while preserving the original test sets.

DatasetFitValidationTest
TCM_PD18,6382,07113,056
TCM_SMGCN20,6252,2923,443

Model optimization and training-derived association statistics use the fitting data.

Checkpoint selection and early stopping are based exclusively on validation Micro-F1@10.

A single checkpoint is selected for each run and subsequently used to evaluate all recommendation cutoffs (K = 5, 10, and 20).

Therefore, different values of K do not select different epochs in the revised experiments.

The test set is not used for checkpoint selection or early stopping.

3. Updated experimental results

The revised three-seed CRAFT results are:

DatasetMacro-F1@10
TCM_PD0.2454 ± 0.0004
TCM_SMGCN0.2516 ± 0.0005

These results replace the previous single-run estimates when evaluating CRAFT under the corrected validation protocol.

We acknowledge that the previous test-based checkpoint selection was methodologically inappropriate, and we do not use those original test-selected results as evidence of held-out generalization.

4. Reproducibility and reporting

We will distinguish revised experimental results from historical baseline results, and document the corresponding training configurations, checkpoint-selection procedure, and evaluation scripts.

We also acknowledge that correcting the public repository and establishing complete provenance for

Additional Response (1/2): Implementation Consistency and Evaluation Reliability

We thank the reviewer for carefully examining our released implementation. We would like to clarify the code-version discrepancy and report the results of our completed re-evaluation.

1. Clarification regarding the released code (W1/Q2)

We acknowledge that the previously released repository snapshot was not synchronized with the full architecture and evaluation procedure described in the manuscript.

In particular, the released version does not contain the complete holistic prescription branch, dynamic–global fusion, or final inference calibration. Its checkpoint-selection procedure also relies on test-set metrics.

We apologize for this inconsistency. We agree that the released implementation, in its current form, is insufficient to reproduce the complete method described in the paper.

We are preparing an updated repository release containing the complete model implementation, training and inference entry points, configuration files, and evaluation scripts.

Importantly, we distinguish this code-release issue from the results of our newly conducted experiments. The revised results are obtained using an explicit validation-based evaluation protocol, as described below.

We will also provide a code-to-result mapping identifying the implementation, checkpoints, and logs associated with the revised experimental results. Until this provenance is fully documented, we do not claim that the existing public snapshot reproduces all results in Tables 1–4.

2. Revised validation protocol (W1/Q1)

We conducted new experiments on both datasets using three random seeds (2021, 2022, and 2023).

The original training partitions were divided into fitting and validation subsets, while preserving the original test sets.

DatasetFitValidationTest
TCM_PD18,6382,07113,056
TCM_SMGCN20,6252,2923,443

Model optimization and training-derived association statistics use the fitting data.

Checkpoint selection and early stopping are based exclusively on validation Micro-F1@10.

A single checkpoint is selected for each run and subsequently used to evaluate all recommendation cutoffs (K = 5, 10, and 20).

Therefore, different values of K do not select different epochs in the revised experiments.

The test set is not used for checkpoint selection or early stopping.

3. Updated experimental results

The revised three-seed CRAFT results are:

DatasetMacro-F1@10
TCM_PD0.2454 ± 0.0004
TCM_SMGCN0.2516 ± 0.0005

These results replace the previous single-run estimates when evaluating CRAFT under the corrected validation protocol.

We acknowledge that the previous test-based checkpoint selection was methodologically inappropriate, and we do not use those original test-selected results as evidence of held-out generalization.

4. Reproducibility and reporting

We will distinguish revised experimental results from historical baseline results, and document the corresponding training configurations, checkpoint-selection procedure, and evaluation scripts.

We also acknowledge that correcting the public repository and establishing complete provenance for

Thank you for the response and the additional experiments. I still have reservations about the method’s overall contribution to prescription recommendation and the strength of the evidence for its benefits. In my view, the paper falls short of the ICLR bar, so I’ll keep my original rating.

I also noticed that Part 1 of your November 18 response appears to have been posted twice, and I haven’t seen Part 2 in the thread.

Reviewer_xTy2OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

CRAFT reformulates TCM prescription recommendation from one-shot multi-label prediction into an order-free dynamic decision process. A hierarchical graph reasoning stage encodes symptom–symptom, symptom–herb, and herb–herb relations built from the training set. At each step, a candidate herb is scored by a neural compatibility term plus a Counterfactual Marginal Utility (CMU): the marginal coverage of residual symptom evidence if the candidate were added, computed from an empirical-Bayes-smoothed co-occurrence prior. A Softplus gate fuses CMU into the score without auxiliary supervision; a GRU updates the prescription state; a learned STOP action terminates construction. Training uses a set-valued multi-positive softmax over all remaining ground-truth herbs plus a frequency-weighted prescription-level BCE. On TCM_PD and TCM_SMGCN, CRAFT improves over six baselines on most of nine P/R/F1@K metrics. A utility-validity study (pairwise AUC 0.894), a diminishing-return analysis, and an inference-time intervention experiment (Normal > Zero > Shuffled > Reversed) characterize CMU's contribution. Ablations isolate six components. Code is anonymously available.

Critical strengths

S1 — A transparent, leakage-aware utility signal with a convincing interventional validation. CMU is computed exclusively from training-set co-occurrence statistics (explicitly stated twice), requires no auxiliary supervision, and degrades gracefully under the Normal > Zero > Shuffled > Reversed intervention — evidence that the model exploits the signal's candidate-specific structure, not merely its presence. This design, and its validation protocol, is the paper's real contribution and is reusable beyond TCM.

S2 — Honest and complete reporting of the empirical layer. The negative R@5 improvement is disclosed rather than hidden; both ablation anomalies (graph reasoning nearly free on TCM_PD; coverage removal improving F1@20 on TCM_SMGCN) are acknowledged with appropriately hedged interpretation; the subgroup analysis explicitly refrains from over-attribution; all graphs and statistics are training-set-only. Arithmetic is exact throughout (I verified all improvement rows, F1 consistency, and subgroup counts). This reporting discipline makes the claims auditable.

Critical weaknesses

W1 — The central advertised mechanism is never evaluated. Adaptive termination via the learned STOP action motivates the entire formulation (fixed top-K is listed as a core limitation of prior work), yet every quantitative result uses fixed K ∈ {5, 10, 20}; no length-calibration metric, no comparison of adaptive-length prescriptions against baselines with oracle K, and only two cherry-picked cases illustrate stopping. As submitted, Contribution 1 is an architectural claim without evidence.

W2 — The empirical edge is statistically unestablished on one dataset and the protocol is opaque. On TCM_SMGCN the improvements are 0.48–1.05% F1 with a negative R@5, reported from a single seed with no variance; the baseline provenance (re-run versus copied) is undisclosed; there is no validation split and the early-stopping monitor is unspecified, leaving a potential test-set leakage channel; and the trivial co-occurrence-prior baseline that would isolate CMU's contribution is missing. Each item is fixable, but together they leave the headline improvements unverified.

Questions for authors

Q1 (clarification, affects Contribution 1). What is the predicted prescription length distribution versus the ground-truth distribution, and how does the adaptive-length output compare with baselines given oracle K per patient? Without this, how should a reader weigh the STOP mechanism?

Q2 (clarification, affects Table 1). Were all baseline numbers re-run under your splits and protocol, or copied from prior papers? If re-run, with what seeds and hyperparameter sources?

Q3 (clarification, affects Section 4.2). What is the validation protocol: which split drives early stopping and checkpoint selection, given that both datasets are described as train/test only?

Q4 (clarification, affects significance). Can you report mean ± std over at least three seeds for CRAFT and the strongest baseline on TCM_SMGCN?

Q5 (clarification, affects Table 4 and Fig. 3(b)). On which dataset and split are the 86,324 decision steps and the intervention curves computed, and why does the Normal F1@5 (0.262) match neither dataset's Table 1 value?

Q6 (clarification, affects reproducibility). What are κ, γ, β₀, ξ, b_min, b_max, and ε, the formal definition of the consensus score c̃(h), and the population over which μ_d and σ_d are estimated?

Q7 (suggestion, future work). A comparison with PrescDRL (which you cite) and a raw co-occurrence-prior ranking baseline would clarify the marginal contribution of dynamic reasoning over the prior alone.

7 comments

We thank Reviewer xTy2 for the careful and constructive review, especially the detailed audit summarized in S1 and S2. We address each weakness and question below; several points require new experiments, which we will complete and report in the revision and updated repository.

W1 / Q1 — The central advertised mechanism (learned STOP / adaptive termination) is never evaluated; all results use fixed K.

We agree that Contribution 1 cannot rest on an unevaluated mechanism. In the revision we will report a dedicated evaluation of adaptive termination: (i) the predicted prescription-length distribution against the ground-truth distribution; (ii) length MAE per dataset; (iii) P/R/F1 of STOP-terminated prescriptions evaluated at their own adaptive lengths, without any fixed cutoff; and (iv) a comparison of the strongest baseline given oracle per-patient K against CRAFT's adaptive termination. Together these directly quantify the value of the learned STOP action.

W2 / Q2 — Baseline provenance (re-run vs. copied) is undisclosed.

We will add a reproducibility paragraph to Section 4.1 stating, for every baseline, whether the numbers were re-run under our splits and protocol or taken from the original papers, together with the seeds used and the source of each hyperparameter setting.

Q3 — Which split drives early stopping and checkpoint selection?

We will clarify the validation protocol in Section 4.1 and Appendix A.3. To remove any ambiguity, we will re-train CRAFT and all baselines with an explicit held-out validation split, select checkpoints and early stopping on validation F1@10 only, and re-evaluate once on the test set. Any change in the numbers will be reported transparently in the revision, and the updated training logs will be released.

Q4 — Mean ± std over at least three seeds for CRAFT and the strongest baseline on TCM_SMGCN.

We will report mean ± std over three seeds for CRAFT and TCMRGCL on both datasets. If the SMGCN improvements fall within variance, we will temper the corresponding claims in the abstract and Section 4.2 accordingly.

Q5 — On which dataset/split are the 86,324 decision steps and the intervention curves computed, and why does Normal F1@5 (0.262) match neither dataset's Table 1 value?

We will clarify in Section 4.5 that the 86,324 valid decision steps are all ground-truth herb tokens across the two test sets, and that Figure 3(b) reports per-step F1 along the rollout trajectory as the recommendation set grows, which is a different quantity from the fixed-cutoff ranking metrics in Table 1. The exact evaluation protocol for Figure 3(b) will be stated explicitly.

Q6 — Values of κ, γ, β₀, ξ, b_min, b_max, ε; definition of the consensus score c̃(h); population for μ_d and σ_d.

All requested values and definitions will be added to Table 6 and Section 3.7 in the revision: the shrinkage parameter κ, the calibration coefficients γ, β₀, ξ, b_min, b_max, the numerical constant ε, the formal definition of the consensus score c̃(h), and the population over which μ_d and σ_d are estimated.

Q7 — Comparison with PrescDRL and a raw co-occurrence-prior ranking baseline.

We will add both analyses to the revision: (a) a comparison with PrescDRL, where the data regime permits a fair evaluation; (b) a symptom-conditioned co-occurrence-prior ranking baseline to isolate the marginal value of learning beyond the prior itself; and (c) a CMU-only greedy selector to quantify how much of CRAFT's performance is recoverable from the utility signal alone.

Dear Authors,

Thank you for the point-by-point response; the revision plan is specific and addresses each weakness. Three remarks.

On W1/Q1 (the learned STOP mechanism): the planned evaluation — predicted versus ground-truth prescription-length distributions, length MAE, P/R/F1 of STOP-terminated prescriptions at their adaptive lengths, and the comparison against the strongest baseline with oracle per-patient K — is the right design; the oracle-K arm isolates the value of learned termination from the utility signal itself. This item is outcome-determinative for my assessment, since Contribution 1 rests on it.

On Q3/Q4: re-training with an explicit held-out validation split, checkpoint selection on validation F1@10 only, a single test-set evaluation, and mean ± std over three seeds on both datasets will resolve the protocol ambiguity; tempering the TCM_SMGCN claims if the differences fall within variance is the right commitment.

On Q5: thank you for clarifying that the 86,324 steps are ground-truth herb tokens across both test sets and that Figure 3(b) reports per-step F1 along the rollout; please state this protocol explicitly in Section 4.5 to avoid confusion with Table 1's fixed-cutoff metrics.

The remaining items (Q2 provenance paragraph, Q6 constants and definitions, Q7 PrescDRL / co-occurrence-prior / greedy-selector baselines) are satisfiable as stated. Since the response consists of planned revisions rather than new evidence, I will hold my rating and revisit it once the revised manuscript, logs, and updated repository are available.

Response to W1 / Q1: Evaluation of Learned STOP

We thank the reviewer for emphasizing the need to directly evaluate adaptive prescription termination. We agree that fixed Top-K metrics alone cannot establish the effectiveness of the learned STOP mechanism.

We have therefore conducted additional evaluations on TCM_PD and TCM_SMGCN using three random seeds (2021, 2022, and 2023) and validation-selected checkpoints.

1. Direct evaluation of adaptive prescription generation

We evaluate prescriptions terminated by the learned STOP action without imposing a fixed recommendation length. We also introduce Dynamic Oracle-K and Calibrated Oracle-K controls.

MethodTCM_PD Macro-F1TCM_SMGCN Macro-F1
Learned STOP0.1473 ± 0.00840.1510 ± 0.0190
Dynamic Oracle-K0.2045 ± 0.00840.2104 ± 0.0102
Fixed Top-100.2454 ± 0.00040.2516 ± 0.0005
Calibrated Oracle-K0.2496 ± 0.00050.2541 ± 0.0003
TCMRGCL Oracle-K0.2259 ± 0.00070.1858 ± 0.0030

2. Prescription-length analysis

MetricTCM_PDTCM_SMGCN
Ground-truth mean length6.6217.100
Predicted mean length2.7502.777
Length MAE4.5614.860
Underestimation rate78.51%81.10%
Exact-length prediction rate9.21%7.73%

The learned STOP policy tends to terminate prescription construction prematurely, resulting in substantial length underestimation.

3. Separating termination and herb-selection errors

Dynamic Oracle-K replaces the learned termination decision with the ground-truth prescription length while retaining sequential herb selection.

This improves Macro-F1 from 0.1473 to 0.2045 on TCM_PD and from 0.1510 to 0.2104 on TCM_SMGCN.

However, Dynamic Oracle-K remains below Calibrated Oracle-K, indicating that both termination decisions and sequential herb selection contribute to the performance gap.

We additionally evaluate an independently reimplemented TCMRGCL baseline with oracle prescription lengths. Oracle-K methods are diagnostic controls because ground-truth lengths are unavailable during deployment.

4. Implications for Contribution 1

We acknowledge that the current learned STOP policy does not outperform fixed Top-K recommendation. Therefore, we no longer present adaptive termination as an experimentally established performance advantage.

Importantly, this limitation should be distinguished from the state-dependent CMU reasoning mechanism and the final herb-ranking capability, which are evaluated separately.

We will revise the contribution statements and limitations discussion accordingly.

We appreciate the reviewer's suggestion, which has enabled a more complete and transparent assessment of adaptive prescription construction.

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

CRAFT models TCM prescription recommendation as a step-by-step herb selection process. It combines graph representations, a coverage-based marginal utility score, adaptive score fusion, and a learned STOP action.

Critical strengths

The paper considers dependencies between previously selected herbs and future choices.

Critical weaknesses

The main framework combines familiar ideas: graph-based representation learning, sequential set construction, coverage-based marginal gains, adaptive score fusion, and a STOP action. The paper does not clearly establish what new technical principle emerges from this combination.

Both figures devote substantial space to explaining the progression from symptoms to herb selection and prescription construction. Their roles could be more distinct.

The marginal utility is too simple to support its therapeutic interpretation. The coverage strength in Eq. (3) is estimated from symptom–herb co-occurrence in the training prescriptions. This measures prescribing association, not therapeutic benefit. A herb may frequently appear with a symptom without independently treating that symptom.

Questions for authors

See weaknesses

2 comments

"The main framework combines familiar ideas ... no new technical principle emerges. "

We thank the reviewer for the frank assessment. We have revised the introduction to position the contribution more precisely: CRAFT does not claim a new learning primitive, but (i) a reformulation of prescription recommendation as an order-free dynamic decision process with a learned STOP action, and (ii) a leakage-safe, supervision-free candidate utility signal whose candidate-specific structure is verified by intervention (Normal > Zero > Shuffled > Reversed). Reviewer xTy2 (S1) independently identifies this design and its validation protocol as the paper's reusable contribution, which we now state explicitly rather than implying a new principle.

"Both figures devote substantial space to explaining the progression from symptoms to herb selection … roles could be more distinct."

Agreed. Fig. 1 now only contrasts the two paradigms (one-shot top-K vs. dynamic construction); all architectural detail has been moved to Fig. 2. The redundant symptom-to-herb progression panels have been removed.

"The marginal utility is too simple to support its therapeutic interpretation … co-occurrence measures prescribing association, not therapeutic benefit."

We agree, and §3.3 already constrains the term "counterfactual" to candidate-level what-if evaluation rather than causal inference. We have unified the terminology throughout the abstract, introduction, and conclusion: CMU now consistently denotes prescribing-association coverage of residual symptom evidence, with no therapeutic-benefit claims. We believe the utility signal remains informative under this honest interpretation, as evidenced by its candidate-level validity (pairwise AUC 0.894) and the intervention results.

Additional Technical Clarification and New Experimental Evidence

We thank the reviewer for the critical assessment. We would like to supplement our previous response with a more precise explanation of CRAFT's methodological contribution and newly completed experimental evidence.

1. What distinguishes CRAFT from a simple combination of existing components?

We agree that graph representation learning, sequential selection, coverage functions, and STOP actions are established techniques. We do not claim that any of these components constitutes a new learning primitive.

The specific methodological contribution of CRAFT lies in introducing an explicit prescription-state-dependent marginal utility into candidate herb evaluation.

Conventional one-shot recommendation assigns each herb a score based primarily on the patient's symptoms. In contrast, CRAFT evaluates a candidate herb conditioned on both the patient symptoms and the currently selected herb set.

Thus, the same candidate can receive a different marginal utility as the prescription evolves, reflecting the residual symptom evidence not yet covered by selected herbs.

This formulation provides a structured connection between symptom evidence, prescription state, and candidate-level decisions.

We acknowledge that state-dependent coverage and marginal gains are established mathematical concepts. Our contribution is their concrete integration into the prescription recommendation setting, together with an explicit neural compatibility term and a reproducible evaluation of the resulting utility signal.

2. Does the CMU signal contribute meaningful information?

We have repeated the CMU intervention analysis using validation-selected checkpoints across two datasets and three random seeds.

The updated Macro-F1@10 results are:

InterventionTCM_PDTCM_SMGCN
Normal0.24540.2516
Zero0.03880.0441
Shuffle0.01470.0097
Reverse0.00610.0071

We additionally performed an action-only intervention, modifying CMU during sequential decisions while retaining the original final CMU-based reranking.

Under this setting, removing the dynamic CMU signal reduces Macro-F1@10 from 0.2454 to 0.1860 on TCM_PD and from 0.2516 to 0.1867 on TCM_SMGCN.

These observations show that the trained model relies on candidate-specific CMU information during inference.

However, because such interventions perturb a trained model, we do not interpret the entire performance decrease as an isolated causal effect or independent gain from sequential reasoning.

3. Is CMU merely a proxy for prescribing association?

We agree with the reviewer that symptom–herb co-occurrence does not establish therapeutic efficacy or clinical causality.

We have consequently revised the terminology to describe CMU as a measure of marginal coverage of prescribing-associated symptom evidence, rather than an estimate of therapeutic benefit.

To quantify the predictive strength of the underlying association information, we additionally evaluated a co-occurrence-prior baseline and a CMU-only greedy selector.

MethodTCM_PD F1@10TCM_SMGCN F1@10
CRAFT0.24540.2516
Co-occurrence Prior0.24300.2505
CMU-only Greedy0.24260.2501

These results demonstrate that the association prior itself is a strong predictor and that the complete architecture provides only modest additional fixed-length ranking improvements.

We do not claim otherwise. Instead, we distinguish the predictive utility of association statistics from the state-dependent mechanism used to incorporate those statistics into sequential prescription reasoning.

4. Presentation and scope of claims

We have clarified the distinct roles of the two figures: Fig. 1 contrasts one-shot recommendation with sequential prescription construction, while Fig. 2 presents the detailed architecture.

We have also narrowed our claims concerning dynamic termination. Additional evaluations show that the current learned STOP policy suffers from premature termination and does not outperform fixed Top-K recommendation. Accordingly, we no longer present adaptive termination as an established performance advantage.

In summary, we do not claim a new general-purpose learning primitive or clinical causal inference. We claim a specific, auditable formulation of state-dependent marginal-utility reasoning for prescription recommendation, while explicitly acknowledging its limited incremental ranking gains and the current limitations of learned termination.

We appreciate the reviewer's critique, which has helped us sharpen the methodological positioning and empirical scope of the paper.

Comments on the paper

1 comment
AuthorsOpenReview ↗

CRAFT (Submission 29476) — Rebuttal Draft

We thank all reviewers for the careful reading. Three concerns are shared across the reviews; we address them first with new experiments and clarifications: (C1) the checkpoint-selection / validation protocol (xTy2 Q3, YFSN Q1); (C2) evaluation of the adaptive STOP mechanism (xTy2 W1/Q1, YFSN Q3); (C3) statistical support and simple baselines (xTy2 W2/Q2/Q4/Q7, YFSN Q4/Q5). Per-reviewer responses follow.

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

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