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Under review as a conference paper at ICLR 2027

TREFIN: Interpretable Financial Forecasting through Typed State Dynamics

Abstract

An interpretable financial forecast should expose the measurable state on which it depends. We introduce TREFIN (Typed Relational Evolution for Financial Forecasting), a probabilistic framework that links asset concepts, residual dependence, and market conditions through an observed-factor measurement procedure. Concepts and a signed residual graph evolve jointly, with distinct propagation rules for directional and risk-like quantities. Future measurements supervise the predicted states, which provide the sole information interface to an asymmetric, heavy-tailed return decoder. A system-level theorem establishes invariant state domains, distributional validity, finite-horizon error propagation, and a conditional downside-scale response. On the 32-asset FinMultiTime task, the validation-calibrated model achieves the lowest mean squared and root mean squared errors and ranks among the top two methods on all six metrics in the main five-seed comparison. State diagnostics reveal how named quantities affect the forecast, while chronological evaluations and retraining expose complementary strengths and remaining calibration limitations. TREFIN makes intermediate financial states testable without giving up competitive nonlinear prediction.

Primary area:
learning on time series and dynamical systems
Keywords:
Financial Time-Series Forecasting, Interpretable Machine Learning, Signed Graph Learning, Probabilistic Forecasting, Typed State Dynamics

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_GQs2OpenReview ↗
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Paper summary

TREFIN is a probabilistic financial forecasting framework in which measurable asset concepts, a signed dependence graph, and market states form the sole interface to the return decoder. These states evolve through typed dynamics and are supervised using future measurements during training. The decoder produces asymmetric, heavy-tailed return distributions. The theoretical analysis establishes state feasibility, distributional validity, finite-horizon error propagation, and a conditional downside-scale response. Experiments report competitive forecasting performance on a 32-asset task, supplemented by state interventions, a graph-free retraining pilot, additional temporal splits, and a separately fitted cryptocurrency application.

Critical strengths

The strongest aspect is the commitment to a measurable intermediate representation without a raw-history bypass. The intermediate states have defined financial meanings and observable training targets, rather than being explanations attached after prediction. Maintaining competitive accuracy under this restriction is a worthwhile contribution, even without a large improvement over unrestricted predictors.

I also appreciate the work put into the appendix. The authors distinguish structural guarantees from empirical diagnostics and disclose several unfavorable or inconclusive results. The validity arguments make the proposed system easier to inspect, while the discussion appropriately avoids equating conditional response constraints with causal identification.

Critical weaknesses

The main remaining concern is empirical support for the learned dynamics. The reviewer package is helpful: the core mechanism is implemented, and the NoGraph variant removes graph dependence throughout the rollout rather than merely zeroing the initial input. However, this does not resolve the inconclusive evidence in Table 10 and Appendix E.3. The graph-free retraining pilot improves MSE from 6.9169 to 6.8495, while the energy-score difference has a confidence interval containing zero. One seed cannot establish that the graph is harmful, but it also cannot establish its benefit. A persistence comparison is particularly important for the concept and graph forecasts, since several measured quantities change slowly and graph estimates are carried forward between refits. I would like clearer evidence of what the learned dynamics add beyond providing an inspectable state interface.

The core training and calibration procedures are much clearer after inspecting the code, but the main comparative result remains difficult to assess. The implementation fits mean shrinkage on validation predictions after checkpoint selection, which is appropriate. In Table 4, however, TREFIN's MSE changes from 6.8542 before calibration to 6.8171 afterward, compared with 6.8415 for TEDM. It remains unclear whether competing methods receive the same calibration opportunity. The supplied package explicitly excludes baseline implementations and paper-scale experiment outputs, so it does not resolve the missing baseline adapter and training details noted in Appendix E.2. These details matter for both the small point-error advantage and the energy-score comparison.

Some passages read like internal reporting instructions or AI generated sentences rather than finished exposition. For example, " It must not be described as interval-coverage calibration." on p 37, "Results for unexecuted ... retraining ablations are not filled in by interpolation" on p 42. These words can be regarded as traces of the editing process or a strong tone of internal audit explanation. I won't let these factors affect my rating but they are a little bit strange.

Questions for authors
  1. Were the competing methods given the same validation-only mean-shrinkage calibration as TREFIN? If not, could you provide a matched comparison for the strongest baseline? My concern is the attribution of the small accuracy advantage, rather than the validity of TREFIN's calibration procedure.

  2. Do the concept and graph forecasts improve over carrying the current measured state forward? A persistence comparison, together with any additional matched graph-free retraining results, would help establish the empirical value of the dynamics. I do not expect every component to improve every metric.

  3. I appreciate the compact reviewer package and its explicit scope. Could you provide the resolved paper-scale configurations and the baseline adapter specifications needed to check Table 4, including their probabilistic heads, objectives, and calibration settings? For Table 10, the corresponding full and graph-free run configurations would also help connect the supplied implementation to the reported experiment.

6 comments
AuthorsOpenReview ↗

Response (1/4) to Weakness 2 and Question 1: equal calibration opportunity

Thank you for distinguishing the validity of mean calibration from the attribution of the accuracy gains. We agree that each competing predictor should receive the same opportunity, and have completed the matched comparison across three chronological folds with five seeds per model and fold. The complete code repository and experimental records can be found at the following Anonymous GitHub link: https://anonymous.4open.science/r/TREFIN-F7AE/.

The same validation-only calibration is applied to every listed predictor. The submitted protocol explicitly specifies mean calibration for TREFIN. The comparison below evaluates TEDM, Timer-XL and TREFIN both before and after the same procedure. Test periods are 2020–2021, 2022–2023 and 2024–March 2025, with identical test origins and five-step targets within each fold and separate training/validation periods.

After checkpoint/candidate selection, each predictor is frozen and validation ES selects ϱ∈[0.05,1]\varrho\in[0.05,1]. The transformation Xϱ(s)=X(s)+(ϱ−1)μX^{(s)}_{\varrho}=X^{(s)}+(\varrho-1)\mu preserves the predictor's innovations. Its before/after comparison therefore isolates calibration within that fixed model.

FoldModel/adapterMSE before / after (×104\times10^4)ES before / after (×102\times10^2)
1TEDM11.5255 ± 0.0142 / 6.8296 ± 0.000314.8430 ± 0.0031 / 10.5919 ± 0.0005
1Timer-XL6.9732 ± 0.0247 / 6.8352 ± 0.00089.3447 ± 0.0184 / 9.2117 ± 0.0026
1TREFIN6.8542 ± 0.0414 / 6.8171 ± 0.00669.0060 ± 0.0359 / 8.9744 ± 0.0160
2TEDM7.2998 ± 0.0061 / 4.0795 ± 0.000012.8252 ± 0.0034 / 9.1533 ± 0.0011
2Timer-XL4.1431 ± 0.0082 / 4.0761 ± 0.00087.7901 ± 0.0089 / 7.7254 ± 0.0011
2TREFIN4.0897 ± 0.0068 / 4.0781 ± 0.00227.6502 ± 0.0044 / 7.6372 ± 0.0028
3TEDM5.9792 ± 0.0034 / 3.4004 ± 0.000011.7795 ± 0.0028 / 8.4141 ± 0.0005
3Timer-XL3.4420 ± 0.0098 / 3.3905 ± 0.00137.0745 ± 0.0124 / 7.0099 ± 0.0021
3TREFIN3.3895 ± 0.0022 / 3.3899 ± 0.00077.0087 ± 0.0062 / 7.0101 ± 0.0054

Entries are mean ± sample SD over five seeds. TEDM uses native stochastic scenarios; Timer-XL uses a centered joint training-residual adapter; testing uses 256 scenarios. The table identifies the task adapters used for these comparisons, with their inputs, objectives, candidate budgets and pinned source revisions specified in the revised paper.

TREFIN retains strongly competitive prediction under equal calibration opportunity. It has lower MSE than both comparators in folds 1 and 3 and lower ES in folds 1 and 2. Its MSE is 0.049% above Timer-XL in fold 2, and its ES is 0.0024% above Timer-XL in fold 3. The same three-fold, five-seed protocol is complete for TimeXer and TimeMixer++, with all six main predictive metrics reported.

An additional native-implementation comparison applies identical calibration opportunity to nine further implementations on fold 1. TREFIN's calibrated MSE is 6.8171±0.00666.8171\pm0.0066, versus 6.8260±0.00696.8260\pm0.0069 for the closest native point comparator, MASTER-style, (MSE ×104\times10^4).

We provide the complete cross-period comparisons, native implementations, before/after calibration results and adapter specifications in Table 2‾\underline{\text{Table 2}}, Appendices G.1-G.3, Tables 15 and 17‾\underline{\text{Appendices G.1-G.3, Tables 15 and 17}} and Fig. 10‾\underline{\text{Fig. 10}} of the revised paper. These results support the central contribution: a measured, inspectable state interface together with strongly competitive predictive performance.

AuthorsOpenReview ↗

Response (2/4) to Weakness 1 and Question 2: persistence and matched graph retraining

Thank you for identifying persistence and matched retraining as complementary tests of the learned dynamics. We appreciate your observation that different components need not improve every metric; the completed experiments distinguish concept prediction, the complete graph pathway and the incremental effect of graph updates.

Concept evolution improves aggregate prediction beyond persistence. We compare C^h=C0\widehat C_h=C_0 and A^h=A0\widehat A_h=A_0 against the same measured future targets, test origins and five original seeds in each fold. Lead zero is excluded; concept MAE uses robust-standardized units.

FoldOverall concept MAE reductionImproved coordinates /26Lead-5 graph IoU: learned / persistence
14.64%120.5851 / 0.6791
26.82%150.6394 / 0.7359
39.12%170.6252 / 0.6999

Overall concept MAE averages equally over coordinates, future leads, assets, origins and seeds; each coordinate count uses its MAE averaged over leads 1–5. Learned concepts improve aggregate error in every period, with heterogeneous gains across the named quantities.

Graph persistence has higher IoU at every evaluated lead and lower continuous graph MAE in all three folds. Both forecasts use the same target, refitted every five observations and held between refits; lead 5 crosses a refit. IoU uses strict ∣Aij∣>0.05|A_{ij}|>0.05 off diagonal, with empty unions zero.

We summarize these results in Fig. 4‾\underline{\text{Fig. 4}} of the revised paper and report every future lead and all 26 coordinates, including continuous graph errors, in Appendix H.3, Tables 28-29 and Fig. 13‾\underline{\text{Appendix H.3, Tables 28-29 and Fig. 13}}.

The explicit graph pathway contributes after the remaining parameters adapt. TREFIN uses signed, continuous graph weights in typed concept propagation, decoder features ACAC and joint-return precision. The additional Full/NoGraph comparisons retrain from initialization on fold 1 with seeds 1/7/19/37/73, identical prepared data, AdamW, batch 64, a 20-epoch cap and patience 6. Validation ES selects checkpoints; all receive the same validation-only mean calibration ϱ∈[.05,1]\varrho\in[.05,1].

NoGraph zeros AA at initialization, every transition and decoding and removes graph-target loss, retaining the market state's residual-dependence summary. The selected protocol gives each variant four nominal validation candidates; Full selects rF=.05r_F=.05, and NoGraph selects λC=.10\lambda_C=.10 with λA=0\lambda_A=0. Choices are frozen before five-seed evaluation.

Entries are mean ± sample SD; concept MAE averages future leads 1–5.

ProtocolVariantMSE (×104\times10^4)ES (×102\times10^2)Concept MAE
FixedFull6.8174 ± 0.00658.9752 ± 0.01800.4923 ± 0.0037
FixedNoGraph6.8268 ± 0.00929.0569 ± 0.02970.5140 ± 0.0205
SelectedFull6.8170 ± 0.00558.9754 ± 0.01910.4925 ± 0.0047
SelectedNoGraph6.8268 ± 0.00939.0569 ± 0.02960.5141 ± 0.0205

Full has lower mean MSE, ES and concept MAE under both protocols, including when each variant selects its own configuration. The complete five-variant study is reported in Appendix H, Table 21 and Fig. 11‾\underline{\text{Appendix H, Table 21 and Fig. 11}} of the revised paper. The original single-seed pilot remains separate in Appendix E.3, Table 8‾\underline{\text{Appendix E.3, Table 8}}.

Graph updating has period-dependent predictive effects. The additional three-fold Full/FrozenGraph study retains Ah=A0A_h=A_0 in every FrozenGraph transition and decoder while retraining other active parameters. Each fold/variant uses calibrated seed-1 validation ES to select among the same four nominal candidates; the inactive slow-refresh candidate duplicates FrozenGraph's base and is evaluated once. All six choices are frozen before testing; each selected model receives the same validation-only positive mean calibration before five-seed evaluation.

Full has lower mean MSE in folds 1 and 3 and lower mean ES in fold 3. FrozenGraph has lower concept and continuous graph MAE in all three folds. Mean continuous graph MAE for Full/FrozenGraph is 0.0083/0.0056, 0.0069/0.0038 and 0.0071/0.0042 in folds 1–3. These results test updating the signed weights while both models retain the initial relational information; Full/NoGraph separately tests the complete graph pathway.

We provide all prediction/state metrics, selected runs and paired results in Table 3‾\underline{\text{Table 3}} and Appendix H.2, Tables 25-27 and Fig. 12‾\underline{\text{Appendix H.2, Tables 25-27 and Fig. 12}} of the revised paper. This study retains its own selected checkpoints, separately from the original persistence cohort.

AuthorsOpenReview ↗

Response (3/4) to Weakness 2 and Question 3: resolved configurations and baseline adapters

Thank you for asking for the configurations and adapter specifications that connect the implementation to each reported experiment. We have organized the resolved settings by experiment family so that the original comparison, the graph-free pilot and the matched retraining studies can each be checked against their own protocol.

Resolved TREFIN configuration. The original fold-1 comparison uses seeds 1/7/19/37/73, training 2009–2017, validation 2018–2019, testing 2020–2021, horizon 5 and embargo 5. The common settings are:

ComponentResolved setting
MeasurementsConcepts at 5/21/63/126 rows; graph window 126, refit stride 5; market window 21
WidthsHidden 64; lead embedding 12; graph embedding 24
TransitionStep .20; damping [.12,.90]; diffusion cap .15; forcing cap .40; graph refresh .10; residual scale .01
Decoderqϵ=.02q_\epsilon=.02; νmin⁡=2.1\nu_{\min}=2.1; mean-bound multiplier 5; scale floor .05; risk-strength cap 1
Auxiliary lossesλC=.25\lambda_C=.25, λA=.08\lambda_A=.08; monotonicity .01; sensitivity .10; radius target .995
OptimizationAdamW; learning rate .001; weight decay .0001; cosine period 20; norm clip 1; batch 64
SelectionMaximum 20 epochs; patience 6; validation-ES improvement 10−610^{-6}
ScenariosTrain/validation/test 16/64/256; evaluation RNG seed 271828
CalibrationPositive mean scalar [.05,1]; validation ES; tolerance 10−510^{-5}; frozen dynamics and shape

Graph-penalty selection uses rolling training windows and candidates [.01,.03,.1,.3]; the realized selection is .10 in all resolved paper-scale runs. Prepared metadata retains the selected value, fitted scales and projection bounds alongside input hashes and exact split indices.

We document the TREFIN splits and common configuration in Appendix E.2, Tables 6-7‾\underline{\text{Appendix E.2, Tables 6-7}} of the revised paper. In Appendix J, Table 32‾\underline{\text{Appendix J, Table 32}}, panels A-B record the selected backbone training runs, panel C records calibration scalars, and panel D records the original pilot.

The original Full/NoGraph pilot is documented in its own setting. Both runs use fold 1, seed 1, the same prepared data and the uncalibrated configuration. Full completes 11 epochs and selects epoch 5 (validation ES .06359918); NoGraph completes 10 and selects epoch 4 (validation ES .06402534). NoGraph adds ablation_variant: NoGraph, zeroing the graph at initialization, every transition and decoding. Its pilot configuration retains λA=.08\lambda_A=.08, a parameter-independent graph-target term. The uncalibrated Full/NoGraph MSE is 6.9169/6.8495 (×104\times10^4), and ES is 9.0526/9.0557 (×102\times10^2).

The revised paper records this single-seed pilot separately from the five-seed structural studies in Appendix E.3, Table 8‾\underline{\text{Appendix E.3, Table 8}} and Appendix J, Table 32, panel D‾\underline{\text{Appendix J, Table 32, panel D}}.

The five-variant and three-fold Full/FrozenGraph studies each retain their own resolved configurations. Full/FrozenGraph freezes all six validation choices before testing: 21 unique search fits, 24 additional selected fits and 30 final evaluations. FrozenGraph omits its parameter-constant graph-target loss and uses the augmented gain matrix with graph row (0,1)(0,1); gain coefficient .1 and target .995 remain unchanged. The protocol and selected runs are documented in Appendix H.2, Table 26‾\underline{\text{Appendix H.2, Table 26}} of the revised paper.

Baseline results are tied to their actual adapters and selection procedures. The specifications identify inputs, predictive heads, objectives, candidate budgets, scenario construction and calibration for every comparator in the matched studies. TEDM uses its native stochastic sampler; Timer-XL uses centered joint training residuals. Native implementations are distinguished from pinned backbone adapters, and each comparison uses the common validation-only calibration described in our preceding response.

We provide these specifications and selected-run records in Appendices G.1 and G.3‾\underline{\text{Appendices G.1 and G.3}} and Appendix J, Table 32‾\underline{\text{Appendix J, Table 32}} of the revised paper. We have prepared the original resolved TREFIN and pilot configurations, preparation hashes, pinned baseline sources, launch commands, selection records and per-origin losses for the planned public code release.

Reviewer_Hh3tOpenReview ↗
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Paper summary

This paper proposes TREFIN, a probabilistic return-forecasting model whose only input is a measured financial state. At each origin, an exponentially weighted ridge regression on Fama–French factors produces 26 per-asset concepts (multi-scale momentum, semivariances, jump share, illiquidity, flow, factor betas), a signed graph from Graphical-Lasso partial correlations of factor residuals, and a 3-dimensional market state. Concepts and graph evolve jointly for H=5 steps with a "typed" damping–diffusion update (signed Laplacian for directional coordinates, unsigned Laplacian for risk-like ones), and future measurements supervise this path. An asymmetric Student-t decoder generates cross-sectional return scenarios, and risk coordinates enter the downside scale only through a positive channel. A system-level theorem states state invariance, distributional validity, a finite-horizon error bound, and direct downside-scale monotonicity. On a 32-asset FinMultiTime panel, the validation-calibrated model reports the best MSE/RMSE and top-two ranks on all six metrics.

The design question is well motivated. The signed/unsigned typing of diffusion is a clean idea, the decoder is valid by construction, and the measurement pipeline is specified in unusual detail with train-only fitting and purged splits. The paper also reports its own weaknesses openly (undercoverage, negative msIC in fold 2, the graph-free pilot, large structural sensitivity constants).

However, the empirical evidence does not support the main claims well. The headline ranking depends on a post-hoc mean shrinkage applied only to TREFIN, the margin over TEDM is 0.36% with no significance test, and naive and econometric baselines are missing. The baseline numbers come from a separate host whose inputs, probabilistic adapters, and tuning budgets are not documented. The central components (typed diffusion, path supervision, graph) are not ablated with retraining, and the only retraining ablation favors removing the graph on point metrics. The theorem mostly restates the construction, and its error bound is vacuous at the reported constants.

Critical strengths
  • Propagation operators typed by the financial meaning of each coordinate: The paper makes the point that a relational operator should respect what a quantity means. A negative residual edge may reverse a directional signal but should not turn volatility into "negative risk", so directional coordinates diffuse with a signed Laplacian and magnitude-like coordinates with an unsigned one (Eq. 5, Lemma 1). Because the unsigned Laplacian annihilates constants, this rule also does not depend on the sign of standardized risk coordinates. It is a simple and principled design rule that could carry over to other graph-diffusion models over heterogeneous features.
  • Interpretability as a testable state rather than a post-hoc explanation: Every concept is a registered measurement with a specified estimator, the predicted concept and graph paths are supervised by and evaluated against future measurements (Fig. 3/6), and risk coordinates are masked in both local and graph-aggregated features (Eq. 51) so that the positive downside-scale channel (Eq. 9) cannot be bypassed. This directly addresses the concept-leakage problem of soft concept bottlenecks that the paper cites (Sec. 1), and it is a useful way to frame interpretability for continuous, noisy financial quantities.
Critical weaknesses
  • The inspectable part of the model is not the part behind the headline accuracy claim: The abstract claims the model makes states testable "without giving up competitive nonlinear prediction", but the point forecast comes from an unconstrained mean head that reads the full state (Eq. 51–52, Fig. 1 caption), and its competitiveness depends on shrinking that head toward zero.
    • The interpretability guarantee covers only the direct downside-scale response, and the positive response in Fig. 2 (right) holds by Eq. 9. The paper does not analyze which concepts drive the mean or whether their signs are financially plausible.
    • Without calibration, TREFIN's MSE (6.8542) is worse than TEDM (6.8415) and about equal to Timer-XL (6.8552) (Table 1/4). The first place appears only after a validation-selected mean shrinkage ϱ that only TREFIN receives (Sec. 3.4, B.5.1). In fold 3, 4 of 5 seeds hit the lower bound 0.05 (E.4), and with raw-unit msIC ≈ 0.006 (Table 5) the zero-mean forecast (the ϱ→0 limit of TREFIN itself) is the natural reference, but it is not reported.
    • The remaining 0.36% margin over TEDM is comparable to TEDM's seed std (0.0220) and no significance claim is made (E.1). Baseline heads, objectives, and tuning budgets are not archived (E.2), and baselines are compared only on fold 1 (Table 6 caption).
  • The typed relational dynamics, the paper's central mechanism, is not shown to drive the predictions:
    • There is no retraining ablation of typed vs. single Laplacian or of λ_C=λ_A=0 (E.3). The only retraining ablation (single seed, Table 10) shows the graph-free model is better on MSE (6.8495 vs 6.9169), MAE, msIC, and msIR, and worse on ES only within a CI that includes zero; the text calls this "partial degradation" and a "useful trade-off" (p.8). Frozen-model interventions (Table 7) show that the fitted ES uses the graph and risk inputs, not that these components are needed.
    • With r_F=0.01 (C.6), the concept transition is essentially linear damping, diffusion, and common forcing. With η_A=0.10 the predicted graph keeps a 0.9^5≈0.59 weight on A_0, and graph targets are carried forward between refits (C.3). Without a persistence reference (acknowledged in E.5), the state-fidelity curves cannot separate learned evolution from decay toward the initial state.
  • The theorem mostly restates the construction, and its quantitative part is vacuous: Invariance, validity, and monotonicity follow from projection, softplus floors, Lemma 1, and the positive-weight parameterization, and the error recursion is a standard induction. With the reported structural spectral radius of 43.36–60.65 (Table 12), M^5 is on the order of 10^8, so only the trivial diameter bound remains, and the W1 extension uses a decoder Lipschitz constant L_D that is never estimated (E.6). The theory therefore does not add evidence beyond the architecture itself.
Questions for authors
  • Naive baselines: What are the MSE/RMSE/MAE of a zero (and train-mean) forecast, and the ES of a zero-mean Student-t with EWMA or DCC-GARCH covariance, on folds 1–3? Is calibrated TREFIN significantly better than the zero forecast?
  • Shrinkage fairness: If the same validation-only ϱ is applied to every baseline, how does the Table 1 ranking change?
  • Baseline protocol: For each baseline, which inputs were used (raw OHLCV, the 26 concepts, FF5 factors), which probabilistic head/loss generated the ES scenarios, and what was the tuning budget? Will baseline code be released?
  • Significance: Can you report paired tests (block bootstrap or Diebold–Mariano on per-origin losses) of TREFIN against TEDM and Timer-XL?
  • Structural ablations: Do five-seed retrainings with a single signed (or unsigned) Laplacian, with λ_C=λ_A=0, and without the graph keep the conclusions? If the graph-free advantage on point errors holds across seeds, why is the graph a core component?
  • Persistence: What are the per-lead concept errors and graph IoU of persistence (Ĉ_h=C_0, Â_h=A_0)? For how many coordinates does the learned rollout beat persistence?
8 comments
AuthorsOpenReview ↗

Response (1/5) to Weakness 1 and Question 1: mean interpretability and financial references

Thank you for examining whether the interpretable states explain the predictions themselves and for proposing direct financial references. We have added evidence addressing both the mean's computational dependence and its predictive performance. The complete code repository and experimental records can be found at the following Anonymous GitHub link: https://anonymous.4open.science/r/TREFIN-F7AE/.

The fitted mean reads the interpretable state. Its calibrated output is

μh,i=ϱairMμtanh⁡fμ[C^h,i:,(A^hC^h)i:,st,eh].\mu_{h,i}=\varrho a_i^rM_\mu\tanh f_\mu[\widehat C_{h,i:},(\widehat A_h\widehat C_h)_{i:},s_t,e_h].

History reaches this head through measured concepts, graph-mediated concepts and the market state. This is the registered point forecast and the ideal law's expectation; the implemented sampler includes numerical centering. The nonlinear readout permits conditional responses while the designated downside-risk channel retains its analytic sign guarantee. We now examine the mean directly.

Which concepts drive the mean? We evaluate all 26 concept derivatives at the evolved state, fixing the graph, other concepts, market input, lead and fitted parameters. Across five seeds, five leads, 32 origins per fold and 32 assets, this gives 25,600 derivatives per concept per fold. In fold 1, the four largest mean absolute derivatives are CMA, SMB, signed flow and 21-observation momentum. Their median/mean-absolute derivatives, in basis points per robust-standardized concept unit, are respectively -0.637/0.769, 0.661/0.744, 0.558/0.653 and -0.518/0.613. Flow-aligned and reversal-like responses have recognizable financial interpretations as conditional fitted responses. Positive mean calibration preserves these derivative signs: the identity check found zero sign mismatches and maximum discrepancy 2.62×10−102.62\times10^{-10}.

The revised paper presents the mean responses in Fig. 3‾\underline{\text{Fig. 3}} and gives all concepts and folds, pooled over the five leads, in Appendix H.4, Table 30 and Fig. 14‾\underline{\text{Appendix H.4, Table 30 and Fig. 14}}. The mean specification and sampler centering appear in Eqs. 49-50 and 90.

Naive point and joint probabilistic references. The following gives five-seed TREFIN means and deterministic point references. The training mean uses unique realized training dates, avoiding repeated labels from overlapping windows. ES evaluates the same 32-asset joint forecast at each lead.

FoldTREFIN MSEZero MSETrain-mean MSETREFIN ESEWMA-Student ES
16.81716.83606.83468.97448.9370
24.07814.07614.08077.63727.6325
33.38993.39053.39077.01016.9888

MSE is scaled by 10410^4 and ES by 10210^2. TREFIN improves on zero in folds 1 and 3; zero has lower mean MSE in fold 2. EWMA-Student has lower mean ES in all three folds. The comparison supports strongly competitive prediction together with an inspectable state interface, with performance differences reported by period.

The probabilistic reference is a zero-mean joint Student law with EWMA covariance, directly evaluating the requested financial alternative. Its covariance follows Qt=λQt−1+(1−λ)rtrt⊤Q_t=\lambda Q_{t-1}+(1-\lambda)r_tr_t^\top, with ridge 10−6mean⁡(diag⁡Qt)10^{-6}\operatorname{mean}(\operatorname{diag}Q_t). Validation ES selects λ∈0.90,0.94,0.97,0.99\lambda\in\\{0.90,0.94,0.97,0.99\\} and Student degrees of freedom in 3,5,8,15,30\\{3,5,8,15,30\\}: selected decays are 0.97/0.90/0.97 and degrees of freedom are 8 in all folds. Initialization uses training data; covariance updates are causal. We draw 256 joint scenarios, with independent innovations across leads.

Paired comparison with zero. Origin-grouped circular-block resampling averages seeds within each origin and keeps all assets and leads together. With 5,000 replicates and block length 20, TREFIN-minus-zero MSE differences (×106\times10^6) and 95% intervals are -1.8897 [-5.5108, 1.2325], 0.2024 [-0.7492, 1.2196], and -0.0629 [-0.1222, -0.0047]. Block lengths 5 and 10 and paired ES checks are also reported.

We report all requested MSE/RMSE/MAE and probabilistic-reference results in Appendix G.4, Table 18‾\underline{\text{Appendix G.4, Table 18}} of the revised paper; Table 19‾\underline{\text{Table 19}} gives the paired temporal comparisons and sensitivity analyses.

AuthorsOpenReview ↗

Response (2/5) to Weakness 1 and Questions 2 and 4: common calibration across three periods

Thank you for asking us to separate calibration effects from model comparisons and to evaluate the small point-error differences over shared market observations. We have completed matched five-seed comparisons in all three chronological folds and paired temporal analyses.

Every compared predictor receives the same calibration opportunity. After checkpoint selection, validation ES selects ϱ∈[0.05,1]\varrho\in[0.05,1] in Xϱ=X+(ϱ−1)μX_\varrho=X+(\varrho-1)\mu, with innovations frozen. This shifts the mean while preserving centered scenarios. We use 64 validation and 256 test scenarios; normalization, model selection and calibration use admissible training/validation data only. Each fold's selected model and calibration are saved before test evaluation.

Three-period performance. Four backbones, three folds and five seeds give 60 selected baseline models, compared with the 15 reference TREFIN fits. Test periods are 2020-2021, 2022-2023 and 2024-March 2025, with 500/496/306 common origins, 32 assets and five leads. Entries are post-calibration means ± sample SD; MSE and ES are scaled by 10410^4 and 10210^2.

FoldModelMSEES
1TEDM6.8296 ± 0.000310.5919 ± 0.0005
1Timer-XL6.8352 ± 0.00089.2117 ± 0.0026
1TimeXer6.8370 ± 0.00109.2142 ± 0.0015
1TimeMixer++6.8363 ± 0.00059.2123 ± 0.0005
1TREFIN6.8171 ± 0.00668.9744 ± 0.0160
2TEDM4.0795 ± 0.00009.1533 ± 0.0011
2Timer-XL4.0761 ± 0.00087.7254 ± 0.0011
2TimeXer4.0767 ± 0.00037.7278 ± 0.0008
2TimeMixer++4.0767 ± 0.00027.7263 ± 0.0003
2TREFIN4.0781 ± 0.00227.6372 ± 0.0028
3TEDM3.4004 ± 0.00008.4141 ± 0.0005
3Timer-XL3.3905 ± 0.00137.0099 ± 0.0021
3TimeXer3.3903 ± 0.00027.0100 ± 0.0003
3TimeMixer++3.3905 ± 0.00027.0096 ± 0.0001
3TREFIN3.3899 ± 0.00077.0101 ± 0.0054

TREFIN has the lowest mean MSE in folds 1 and 3 among these methods; fold-2 MSE is 0.049% above Timer-XL. Its mean ES is lowest in folds 1 and 2 and slightly higher, within 0.008% of TimeMixer++, in fold 3. Strongly competitive prediction persists across the three periods. Positive mean scaling leaves msIC/msIR unchanged; TREFIN's msIC is 0.0059 ± 0.0024, -0.0019 ± 0.0025 and 0.0018 ± 0.0028 across folds.

We summarize these comparisons in Table 2 and Fig. 10‾\underline{\text{Table 2 and Fig. 10}} of the revised paper and provide all six metrics before and after calibration, including RMSE, MAE, msIC and msIR, with five-seed variability in Appendix G.2, Table 15‾\underline{\text{Appendix G.2, Table 15}}.

Nine additional native comparisons. A separate fold-1 five-seed study gives ShrunkVAR, HistGB, StateMLP, RawMLP, GRU, DLinear, PatchTST-style, iTransformer-style and MASTER-style the same validation mean-shrinkage opportunity. Within this specified comparison, TREFIN's MSE/RMSE/MAE rank changes from fourth to first, ES remains first, and msIC/msIR remain fourth. Its calibrated MSE is 6.8171 ± 0.0066 versus 6.8260 ± 0.0069 for MASTER-style. These matched-implementation rankings are distinguished from original Table 5's recorded comparison.

The revised paper documents the native comparison in Appendix G.3, Tables 16-17‾\underline{\text{Appendix G.3, Tables 16-17}}; Table 17 contains every pre/post-calibration result and selected scalar.

Paired TEDM/Timer-XL analyses. We average five seed-specific losses within each origin, preserving the asset/lead grouping and each fold's chronological sequence. Comparator-minus-TREFIN differences are evaluated by circular-block bootstrap: 20-origin blocks, 10,000 replicates, percentile 95% intervals, null-centered two-sided tests with (1+k)/(B+1)(1+k)/(B+1) correction, and Holm adjustment over the six comparator-by-fold comparisons separately for each loss. MSE is primary; MAE and ES provide complementary checks. ES uses exact all-pairs distances in float64 on 256 scenarios. Additional checks use blocks 5/10 and Diebold-Mariano tests with HAC lag 20. These paired estimates complement the seed means and SDs above.

We provide all 18 loss/comparator/fold estimates, intervals, adjusted tests and temporal sensitivity results in Appendix G.5, Table 20‾\underline{\text{Appendix G.5, Table 20}} of the revised paper.

AuthorsOpenReview ↗

Response (3/5) to Weakness 1 and Question 3: baseline inputs, adapters and training budgets

Thank you for requesting specifications that make each comparison interpretable and reproducible. We now document inputs, predictive heads, objectives, candidate budgets and source identities alongside their results.

Inputs and predictive distributions. TEDM, Timer-XL, TimeXer and TimeMixer++ receive 126 observed excess-return vectors for 32 assets and forecast five future vectors. Their predictor inputs are return histories; the factor file supplies the risk-free subtraction. TREFIN uses its measured concept/factor/volume representation. This comparison evaluates those documented pipelines on shared splits and origins. Normalization is fitted only to admissible training rows.

Timer-XL, TimeXer and TimeMixer++ are point forecasters trained by MSE. Their declared probabilistic adapter adds complete centered training-residual paths of shape 5×325\times32, preserving empirical cross-asset and cross-lead dependence; the backbone output is this law's mean. TEDM generates joint scenarios through its native diffusion sampler and uses their mean for point prediction. All use 64 validation/256 test scenarios and the same validation-selected positive mean calibration.

Task adapters and source identities.

ModelArchitecture and task adaptation
Timer-XLOfficial OpenLTM; six length-21 tokens, last-token five-step head; width 128, three layers, four heads, feed-forward width 512, dropout 0.1, instance normalization; trained from initialization.
TEDMOfficial UNet/schedule/preconditioner/sampler; width 32, two residual blocks, channel multipliers 1/2/3/4/5, attention 112/56/28/14. Window 112 plus conditioning offset 13 and one padding position consumes 126 observations; weighted denoising; EMA 0.995 every ten updates.
TimeXerOfficial multivariate model; six length-21 patches per asset, global token, cross-asset embeddings; width 128, three layers, four heads, feed-forward width 512, dropout 0.1, native normalization, five-step head; trained from initialization.
TimeMixer++Maintained PyPOTS model; two mixer blocks, widths 32/64, three periods/kernels, channel mixing/independence, reversible normalization. Factor-three downsampling gives 126/42/14; native time imaging, dual-axis attention, multiscale mixing and coarsest-scale head.

TimeMixer++ selects evaluation periods separately from each origin's own observed history, including when origins are batched. TEDM's axis-sentinel and deterministic upstream-equivalence checks verify its adapter.

Shared candidate opportunity across the four backbones. Each fold/model/seed in {1,7,19,37,73} uses one architecture and learning rates 0.001/0.0003, batch 64, a 100-complete-data-epoch cap and patience 15. Full-validation ES selects checkpoints and candidates using 498/500/496 validation origins. Timer-XL, TimeXer and TimeMixer++ use Adam/cosine scheduling; TEDM retains its native Adam/plateau schedule. The positive calibration scalar is then selected with frozen innovations. Actual updates and resolved settings are recorded in Appendix J, Table 32‾\underline{\text{Appendix J, Table 32}}, with the full protocols in Appendix G.1‾\underline{\text{Appendix G.1}} of the revised paper.

The separate nine-model native study. Fold-1 five-seed inputs are: return lags for ShrunkVAR; own lags, C0C_0, signed/absolute graph degree, s0s_0 and asset/lead indicators for HistGB; flattened C0,A0,s0C_0,A_0,s_0 for StateMLP; 126 return vectors for RawMLP, GRU, DLinear and PatchTST-/iTransformer-style models; return, volume and signed-volume-proxy histories plus market summaries and current FF5 for MASTER-style. State inputs include factor-derived concepts. Each uses centered joint training-residual scenarios. ShrunkVAR minimizes ridge MSE, HistGB squared error, and neural models MSE with AdamW (learning rate 0.001, weight decay 0.0001, batch 64, cosine scheduling, gradient clipping 1), at most 20 epochs and patience 6. Validation ES selects among two candidates per method. Full candidate grids, head dimensions and calibrations are tabulated in Appendix G.3, Tables 16-17‾\underline{\text{Appendix G.3, Tables 16-17}} of the revised paper.

Reproducibility. Resolved configurations, pinned sources/licenses, adapter code, reload checks and per-origin losses for these matched implementations are prepared for public release accompanying the paper.

Implementation references: TEDM, 1d65888c; OpenLTM, 0b300509; TimeXer, 4e938a17; PyPOTS TimeMixer++, 22715335.

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Paper summary

TREFIN forecasts returns through measured financial concepts, a residual-dependence graph, and market conditions, while also predicting the future states. It combines typed dynamics with a constrained probabilistic decoder and reports competitive results on a 32-asset task, alongside state-fidelity and calibration diagnostics.

Critical strengths
  1. Measurable prediction interface. The financial concepts are defined by explicit measurements and form part of the actual prediction path. This gives the interpretation a concrete basis beyond assigning names to hidden coordinates.

  2. Inspectable treatment of risk. The distinction between directional and risk-like propagation is sensible, and the direct downside-scale response is enforced by construction. The paper also states the limits of these guarantees clearly.

  3. Competitive forecasting accuracy. The calibrated model ranks among the top two methods on all six main metrics. This supports the case that an interpretable state interface need not incur a large loss in forecasting accuracy.

Critical weaknesses
  1. Incomplete evidence for the graph component. The graph-free retraining pilot improves point errors, and its energy-score difference has an interval spanning zero. With only one retrained seed, the benefit of the graph remains unresolved.

  2. Undercoverage of predictive intervals. The nominal 90% intervals cover only about 80% to 87% of the evaluated returns across the three periods. This is a material weakness for a method whose contribution includes probabilistic risk forecasts.

  3. Concept forecasts lack a persistence comparison. The paper measures errors against future concept values but does not establish improvement over simply carrying the current values forward. This matters because some long-window financial measurements change slowly.

Questions for authors
  1. Structural comparisons after retraining. Can the authors provide multi-seed graph-free and untyped comparisons with the same calibration procedure? This would show whether the proposed structure improves the result after the remaining components are allowed to adapt.

  2. Calibration and the risk guarantee. What explains the interval undercoverage, and how much can be corrected without changing the stated risk-response guarantee? This is important for assessing the value of the probabilistic decoder.

  3. Predictive value of named states. Can concept and graph forecasts be compared with matched persistence baselines at each lead? This would clarify whether the learned dynamics add predictive information beyond the measured starting state.

4 comments
AuthorsOpenReview ↗

Response (1/3) to Weakness 1 and Question 1: matched structural retraining

Thank you for asking whether the proposed structure remains useful when the other parameters are allowed to adapt. This distinction is central to evaluating an interpretable forecasting architecture, and we have completed additional five-seed retraining comparisons under both fixed and validation-selected configurations. The complete code repository and experimental records can be found at the following Anonymous GitHub link: https://anonymous.4open.science/r/TREFIN-F7AE/.

The complete graph pathway contributes after retraining. All five variants use fold 1, seeds 1/7/19/37/73, identical prepared data, AdamW, batch 64, a 20-epoch cap and patience 6. Checkpoints are selected by validation ES and receive the same validation-only mean calibration ϱ∈[0.05,1]\varrho\in[0.05,1].

NoGraph removes the explicit AA channel at initialization, every transition and decoding, with graph-target loss zero. It retains the market state, including its residual-dependence summary. Signed-only and unsigned-only use one transition Laplacian for all concept coordinates, leaving the decoder unchanged. No state supervision sets λC=λA=0\lambda_C=\lambda_A=0 while retaining the forward architecture.

The validation-selected results below are mean ± sample SD over five seeds. Concept MAE averages the 26 robust-standardized coordinates over future leads 1–5; anchored lead zero is excluded.

VariantMSE (×104\times10^4)ES (×102\times10^2)Concept MAE
Full6.8170 ± 0.00558.9754 ± 0.01910.4925 ± 0.0047
NoGraph6.8268 ± 0.00939.0569 ± 0.02960.5141 ± 0.0205
Signed-only6.8170 ± 0.00558.9756 ± 0.01930.4928 ± 0.0047
Unsigned-only6.8193 ± 0.00438.9495 ± 0.02110.4920 ± 0.0017
No state supervision6.8192 ± 0.00448.9560 ± 0.01830.7098 ± 0.0052

Every variant receives four nominal candidate slots: base (rF=.01,ηA=.10,λC=.25,λA=.08)(r_F=.01,\eta_A=.10,\lambda_C=.25,\lambda_A=.08); slow graph (ηA=.02)(\eta_A=.02); stronger dynamics (rF=.05)(r_F=.05); and weaker supervision (λC=.10,λA=.02)(\lambda_C=.10,\lambda_A=.02). Required zero losses override these settings; duplicate effective candidates are evaluated once. Calibrated seed-1 validation ES selects a configuration that is frozen for five-seed evaluation. Full and signed-only select stronger dynamics; NoGraph selects weaker concept supervision; unsigned-only and no-state-supervision select slow graph.

Full has lower mean MSE, ES and concept MAE than NoGraph under both protocols. The fixed-configuration comparison gives the same direction: Full/NoGraph MSE 6.8174/6.8268, ES 8.9752/9.0569 and concept MAE 0.4923/0.5140, with the same metric multipliers. The single-Laplacian variants retain competitive return scores, including lower selected ES for unsigned-only. Typing supplies the distinct propagation semantics of directional signals and risk magnitudes; state supervision substantially improves fidelity to the measured concepts. These are complementary contributions to an inspectable model with strongly competitive prediction.

We report both complete five-variant comparisons in Appendix H, Table 21 and Fig. 11‾\underline{\text{Appendix H, Table 21 and Fig. 11}} of the revised paper. The original uncalibrated, single-seed pilot remains separately identified in Appendix E.3, Table 8‾\underline{\text{Appendix E.3, Table 8}}.

Updating the graph is evaluated separately from removing it. Our additional three-fold Full/FrozenGraph study holds Ah=A0A_h=A_0 in every FrozenGraph transition and decoder while retraining its other active parameters. Each fold/variant uses the same four-slot validation selection and positive mean calibration before five-seed evaluation. Full has lower mean MSE in folds 1 and 3 and lower mean ES in fold 3; FrozenGraph has lower concept and continuous graph MAE in all three folds. Thus the incremental return effect of graph updating is period-dependent, while the Full/NoGraph comparison establishes the contribution of the complete graph pathway. Our persistence response gives the compact paired results.

We provide the cross-period results, selected runs and continuous graph errors in Table 3‾\underline{\text{Table 3}} and Appendix H.2, Tables 25-27 and Fig. 12‾\underline{\text{Appendix H.2, Tables 25-27 and Fig. 12}} of the revised paper.

AuthorsOpenReview ↗

Response (2/3) to Weakness 2 and Question 2: interval coverage and the risk-response guarantee

Thank you for asking how the probabilistic forecasts can provide more useful interval coverage while retaining their interpretable risk response. We have completed a direct calibration study across all three periods, keeping the original fitted state dynamics and point forecasts unchanged.

Mean calibration and interval calibration act on different parts of the forecast. Positive mean shrinkage translates scenarios and therefore adjusts mean amplitude without widening intervals. The original intervals achieve 80–87% coverage against the nominal 90% level; mean shrinkage alone does not address this discrepancy. We separately calibrate innovation scale, which directly controls interval width.

Positive innovation scaling preserves the conditional downside-scale guarantee. For all 15 fitted models, including their original mean-calibration coefficients, we use

Y~=μ+a(Y−μ),a>0.\widetilde Y=\mu+a(Y-\mu),\qquad a>0.

This preserves every point forecast and concept/graph trajectory. Both asymmetric scale parameters and their mean-correction term are multiplied by aa, while degrees of freedom and correlation structure remain fixed. For each designated risk coordinate, with the decoder graph, other states and current calibration factor held fixed,

=a\frac{\partial\sigma^-}{\partial c_j}\geq0.$$ **Coverage improves across periods without changing point accuracy.** Fixed validation 90% selects one factor per model using 256 validation scenarios and freezes it throughout testing. Causal rolling 90% uses the 126 most recent completed forecast origins: at raw origin $t$, a previous origin $u$ contributes only when $u+5\leq t$, after all five outcomes are observed. The rolling factor uses only past observations and stays fixed during the current state intervention. The window, target and bounds $[0.25,4]$ were prespecified. The following uses the original held-out scenarios and identical point forecasts. Entries are five-seed means; coverage includes sample SD. Width is in percentage points of return; ES is multiplied by $10^2$. | Fold | Calibration | 90% coverage (%) | Width | ES | |---|---|---:|---:|---:| | 1 | Original | 80.123 ± 0.289 | 5.2758 | 8.9744 | | 1 | Fixed validation 90% | 84.440 ± 0.227 | 6.0331 | 8.8940 | | 1 | Causal rolling 90% | 88.652 ± 0.071 | 7.4184 | 8.9608 | | 2 | Original | 85.795 ± 0.849 | 5.5911 | 7.6372 | | 2 | Fixed validation 90% | 92.988 ± 0.384 | 7.3419 | 7.6976 | | 2 | Causal rolling 90% | 90.422 ± 0.020 | 6.6024 | 7.6495 | | 3 | Original | 86.540 ± 0.356 | 4.8879 | 7.0101 | | 3 | Fixed validation 90% | 89.007 ± 0.280 | 5.3647 | 6.9960 | | 3 | Causal rolling 90% | 89.125 ± 0.117 | 5.4173 | 7.0009 | The causal rolling procedure brings mean coverage to 88.652%, 90.422% and 89.125%, with the associated width and ES changes shown explicitly. The fixed validation results also quantify how one frozen adjustment transfers across each test period. **Improved empirical coverage is compatible with the same measured-state interface, conditional risk response and strongly competitive point predictions.** We summarize the comparison in $\underline{\text{Table 4}}$ of the revised paper. The calibrated results with seed variability, both protocols and the preserved response are given in $\underline{\text{Appendix I, Table 31 and Eqs. 130-131}}$. Original-model results and variability are reported in $\underline{\text{Appendix G.2, Table 15}}$.
AuthorsOpenReview ↗

Response (3/3) to Weakness 3 and Question 3: predictive states beyond persistence

Thank you for proposing the measured starting state as the appropriate reference for future-state prediction. This is especially informative for long-window concepts and graphs carried between refits, and we have completed matched persistence comparisons at every future lead in all three folds.

Concept dynamics improve aggregate forecasting beyond persistence. We compare C^h=C0\widehat C_h=C_0 and A^h=A0\widehat A_h=A_0 with the learned trajectories using the same projected future measurements, held-out origins and five original seeds. Concept MAE uses robust-standardized coordinate units; future leads 1–5 are evaluated and anchored lead zero is excluded.

FoldOverall concept MAE reductionImproved coordinates /26Lead-5 graph IoU: learned / persistence
14.64%120.5851 / 0.6791
26.82%150.6394 / 0.7359
39.12%170.6252 / 0.6999

The overall reduction averages equally over coordinates, future leads, assets, origins and seeds. Each coordinate's improvement count uses its MAE averaged over the five future leads. Learned concepts improve aggregate MAE in every period, with heterogeneous improvements across the named financial quantities.

The revised paper summarizes these results in Fig. 4‾\underline{\text{Fig. 4}} and provides all 15 fold/lead comparisons and every one of the 26 coordinates in Appendix H.3, Tables 28-29 and Fig. 13‾\underline{\text{Appendix H.3, Tables 28-29 and Fig. 13}}, allowing slowly varying quantities to be assessed individually.

Graph reconstruction and forecasting contribution answer distinct empirical questions. Persistence has higher graph IoU at every evaluated lead and lower continuous graph MAE in all three folds. Both forecasts use the same target graph, refitted every five observations and held between refits; lead 5 crosses a refit. IoU uses strict ∣Aij∣>0.05|A_{ij}|>0.05 off diagonal and assigns empty unions zero. Both support and continuous errors are reported in Table 28‾\underline{\text{Table 28}}.

TREFIN uses signed, continuous graph weights in typed concept propagation, relational decoder features ACAC, and the signed-Laplacian contribution to joint-return precision. These computations depend on information discarded by binary support. Their predictive contribution is evaluated directly by retraining: Full/NoGraph removes the graph pathway, whereas Full/FrozenGraph retains the initial relational information and tests the incremental contribution of graph updating.

The additional Full/FrozenGraph study tests graph updates after adaptation. FrozenGraph keeps Ah=A0A_h=A_0 in every transition and decoder while retraining the other active parameters. Each fold/variant independently selects among the same four nominal configurations using calibrated seed-1 validation ES; duplicate effective candidates are evaluated once. The selected configurations are frozen before five-seed evaluation, with the same validation-only positive mean calibration.

The entries below are paired seed means ± sample SD of FrozenGraph minus Full; positive values favor Full for these errors.

FoldΔMSE (×104\times10^4)ΔES (×102\times10^2)ΔConcept MAEΔGraph MAE
10.0016 ± 0.0037-0.0284 ± 0.0098-0.0009 ± 0.0052-0.002728 ± 0.000026
2-0.0008 ± 0.0008-0.0037 ± 0.0046-0.0089 ± 0.0159-0.003086 ± 0.000007
30.0003 ± 0.00080.0048 ± 0.0106-0.0033 ± 0.0012-0.002888 ± 0.000004

Full has lower mean MSE in folds 1 and 3 and lower mean ES in fold 3. FrozenGraph has lower concept and continuous graph MAE in all three folds. The return effect of learned graph updates is period-dependent. The Full/NoGraph results in our structural response separately show lower mean MSE, ES and concept MAE for Full under both matched protocols. Together, these experiments identify the value of concept evolution, the full graph pathway and the incremental graph update without conflating their effects.

We report the complete Full/FrozenGraph prediction and state metrics, selected runs and paired results in Table 3‾\underline{\text{Table 3}} and Appendix H.2, Tables 25-27 and Fig. 12‾\underline{\text{Appendix H.2, Tables 25-27 and Fig. 12}} of the revised paper. Its selected checkpoints are distinct from the original persistence cohort above.

AuthorsOpenReview ↗

Follow-up Letter

Dear Reviewer,

Thanks for your valuable review, which has inspired us to improve our paper further. As the author-reviewer discussion period will end in about 3 days, we kindly wonder if our responses have addressed your concerns.

Following your suggestions, we have incorporated the following updates into the revised paper:

  • Added matched structural retraining. We evaluated five variants with five seeds on fold 1, using both fixed and independently validation-selected configurations. Full has lower mean MSE, energy score and concept MAE than NoGraph under both protocols. The other variants clarify the roles of typed propagation and state supervision. These results are reported in Appendix H.1, Table 21‾\underline{\text{Appendix H.1, Table 21}}.

  • Improved interval coverage while preserving the conditional risk-response guarantee. Positive innovation-scale calibration leaves point forecasts and state trajectories unchanged and preserves conditional downside-scale monotonicity. Causal rolling calibration achieves 88.65%, 90.42% and 89.13% empirical coverage for nominal 90% intervals across the three periods, as reported in Table 4 and Appendix I‾\underline{\text{Table 4 and Appendix I}}.

  • Added persistence comparisons and matched graph-update experiments across all three periods. Learned concept dynamics improve aggregate concept MAE over persistence in every fold. Together, the Full/NoGraph and five-seed Full/FrozenGraph studies distinguish the contribution of the complete graph pathway from the period-dependent effects of updating the graph. We report both graph-reconstruction and forecasting outcomes in Table 3, Fig. 4‾\underline{\text{Table 3, Fig. 4}} and Appendices H.2-H.3‾\underline{\text{Appendices H.2-H.3}}.

These revisions provide a more direct assessment of TREFIN's interpretable state dynamics, probabilistic calibration and strongly competitive predictive performance. All of the above analyses have been incorporated into the revised paper for your review.

Thank you again for your time and thoughtful suggestions. We would greatly appreciate your thoughts on these revisions and would be happy to clarify any remaining questions.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Thank you letter

Dear Area Chair and Reviewers,

Thank you for the time and care you have devoted to evaluating TREFIN, including the detailed reading of its mathematical specification, experimental results, and implementation. We appreciate your recognition of the measurable state interface, the distinction between directional and risk-like propagation, and the value of making financial predictions inspectable.

Your questions help us sharpen the central contribution: interpretability together with strongly competitive predictive performance, through financial states that participate in the actual forecasting computation. Our replies provide matched calibration for four forecasting backbones across three periods, multi-seed structural retraining, three-period comparisons of evolving and retained initial graphs, persistence references for the learned states, direct responses of the fitted mean, interval-calibration results across three periods, and an additional analytic five-step sensitivity bound around the fitted state trajectories. We have integrated this evidence into the revised main text and appendices. Each response identifies the corresponding equations, tables or figures and connects the requested evidence to the relevant architectural property. The complete code repository and experimental records can be found at the following Anonymous GitHub link: https://anonymous.4open.science/r/TREFIN-F7AE/.

We are grateful for these thoughtful suggestions and for the opportunity to make the contribution and its supporting evidence more precise.

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

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