acceptodds
Under review as a conference paper at ICLR 2027

DARC: Dependency-Aware Relational Compiler

Abstract

Relational feature compilers summarize records linked to a prediction target, but column-wise aggregates cannot represent dependencies among source attributes. We introduce DARC, a dependency-aware relational compiler that first constructs a compact point-in-time representation from column-wise aggregates and then augments it with features derived from empirical functional dependencies. Because such features are not uniformly useful, DARC selects them on temporal folds within the training split and decides per task whether to include them at all. DARC activates dependency-aware features on 14 tasks and retains a purely aggregate representation on the rest. DARC achieves positive win–loss margins against budget-matched Canonical DFS, JUICE, and FastProp; the selected representation also transfers across six downstream predictors. Controlled collisions and real-data rewiring show that dependency features can distinguish histories with identical conventional aggregates.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Relational Database, Functional Dependency

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

The paper attempts to tackle feature compilation problem from a functional dependency perspective. Specifically, the paper identifies an edge cases where Deep Feature Synthesis is invariant to label-relevant signals, and demonstrates that the functional dependency is the key to solve this problem. Such a motivation is valid and has been brought up by recent literature. However, the proposed method doesn’t seem to tackle that problem from my understanding. Specifically, the proposed method still aggregates summary statistics for training rows by going over every single pair of columns, filter them, and construct a lookup table for the compiled feature. However, during inference, for two different histories with the same key to be looked up, they will still end up with the same compiled features, which contradicts with the edge case proposed in the motivation section.

Critical strengths

The strength of the paper is explicit modeling the functional dependency of columns in a table, which seems novel compared to recent literature. However, it doesn’t mean the idea is sounded; modeling pairwise dependency is costly to scale (see Weaknesses). While the paper is supported with an ample amount of experiments, I have concerns regarding validity of the experiments. For these reasons, I believe that the paper lacks of substantive strength to be accepted.

Critical weaknesses

The major problem of the paper is clarity, motivation, and unclear experiments. Below are some key points:

  1. The paper has problems with clarity, where non-canonical terms are randomly introduced without clarifications. Some examples include, but not limited to, determinant-dependent structure and independent selection. Some terms are prematurely introduced without any contexts such as functional-dependency hypergraph, thus leading to weak clarity.
  2. Figure 1 represents a failure of column-wise aggregation, which has been previously demonstrated in KumoRFM-2 paper [1]. It is the same concept presented in Figure 1. The authors failed to acknowledge the overlap between the proposed approach and KumoRFM-2 in achieving separation of these edge cases.
  3. The paper failed to introduce the motivation of the expanding temporal folds, and which cutoff times are chosen for these folds.
  4. The proposed method only works with categorical features or numerical features with small unique numbers due to the 5 statistics.
  5. The usage of the word hypergraph is misleading since the paper only attempts to model dependency between 2 columns, which should just be a pairwise dependency.
  6. The method fails to tell apart the two histories presented in Figure 1 since the the 5 statistics are order-agnostic and computed based on the past records in the table. In other word, during inference, if two different history sequences are presented, the proposed approach won’t be able to tell them apart either since they just retrieve the computed metrics from the look-up table.
  7. The number of dependency scales with the square of number of columns in a table, which means the model is far from scalable.
  8. Why does Table 1 have JUICE implemented differently from the version report in its official paper (which causes suspiciously lower performance)?

[1] Hudovernik et al. KumoRFM-2: Scaling Foundation Models for Relational Learning. 2026.

Questions for authors
  1. Appendix A.1. is poorly written with unclear experiment details. Could the authors elaborate more the experiment settings in this section?
  2. Appendix A.2. looks confusing. If I understand correctly, we’re having features constructed for badges computed already. The paper attempts to shuffle names, which shouldn’t change the summary statistics that are constructed for badges either. In other words, the proposed method should yield the same result with DFS, but the paper states that the proposed method can yield positive FDHG distance. How is it possible? Also this question shares the same concern with Weakness 6.
  3. What are the motivations for picking the 5 summary statistics?
Reviewer_K4VCOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies feature engineering for machine learning on relational databases. The task is to predict a label for an entity, such as a user or an item, from its linked records across several tables. Common tools, called feature compilers (e.g., Deep Feature Synthesis, or DFS), turn these records into a fixed set of summary features, one column at a time. The authors argue that this misses dependencies between columns (X -> A). Their main contribution is DARC. DARC builds a compact "Base" of column-wise aggregates, adds functional-dependency (FDHG) features such as confidence, entropy and margin of p(A | x), and decides per task whether to use them, using only training data. On 51 RelBench/DBInfer tasks, DARC beats budget-matched Canonical DFS (28/4/9), JUICE (30/1/7) and FastProp (20/1/15), and the chosen representation transfers across six downstream predictors.

Critical strengths

1- train-only temporal protocol. All selection decisions use three expanding inner folds inside the training split (Sec. 4.1). Validation and test rows are never used for selection (Appx. B.10). Point-in-time feature construction avoids leakage. This makes the selection results credible.

2- A demonstration of the representational gap. On rel-stack/user-badge, rewiring Name values within each history keeps the full Canonical DFS vector unchanged in 100% of cases, while FDHG features change in 43.96% of them (Table 6). This shows that column-wise aggregates can miss information in real data.

Critical weaknesses

1- Most of the gain comes from the Base, not from dependency features. The gate picks Base on 34 of 51 tasks, and FD-enhanced features on only 14 (Table 2). The authors say Base "accounts for most of the selected compiler representations" (Sec. 5.3), and in Table 1 the gate picks Base on four of seven tasks. Against Base itself, DARC's net margin is small: +2 to +11 tasks across predictors (Table 4). There are no significance tests or effect sizes. So the paper's central claim, that dependency features help, rests on a small subset of tasks.

2- The baseline comparisons favor DARC. Each baseline is capped at DARC's own realized feature count Ki, which is often 1–4 columns (Table 16). JUICE is cut to its first Ki columns "in deterministic export order" (Appx. D.2), with no selection. In contrast, DARC chooses its features on training folds. Results on full, uncapped JUICE and FastProp are not shown. Results also seem to be reported on the official validation split (Sec. 5.3) rather than the RelBench test split, which makes it hard to compare with published numbers.

Questions for authors

1- (Clarification) How do DARC's results compare with full, uncapped JUICE, FastProp and Canonical DFS, and with JUICE columns chosen on the same training folds? Can you also report test-split results?

2- (Clarification) FDHG features are computed from p(A | x) pooled across all entities and use only the entity's latest x (Sec. 4.3). How does this capture the within-history dependency shown in Fig. 1? Is this why the median FDHG distance in the rewiring test is 0 (Table 6)?

3- (Clarification) On the 14 FD-enhanced tasks, how large are the gains over Base, and are they significant across seeds? Greedy selection takes a median of 2,316 s versus 25 s for Base (Table 14), so the size of the gain matters.

Reviewer_oJjfOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

DARC builds a small set of one-hop aggregates (Base). It can add features from candidate dependencies X → A, which it gets by looking up the target's latest X value in a p(A|x) table pooled over all entities. Dependencies and the final representation are selected on temporal folds inside the training split. The gate picks Base on 34 of 51 tasks, DFS on 3 and an FD variant on 14. DARC reports positive win/loss against matched DFS, JUICE and FastProp.

Critical strengths

Selection uses only training-split folds, and the 51-task, six-predictor sweep is broad. This does not offset the problems below.

Critical weaknesses
  1. Weak motivation and limited novelty. The FDHG block depends only on the target's last X value, so it cannot tell apart the two histories in Figure 1, which both end with x2. It is a fixed encoding of LAST(X), and there is no comparison against LAST(X), count encoding or target encoding. Similar group-by statistics exist in OpenFE (ICML 2023) and FeatAug (ICDE 2024). Using FDs to guide relational feature inclusion goes back to Kumar et al. (SIGMOD 2016).

  2. Small benefit from the FD part. Most tasks keep Base or DFS, and the paper says most of the gain comes from Base. Against Base, the win/loss counts are significant only for CatBoost. On brewer-dormant, the chosen FD variant is worse than Base, yet Table 1 counts it as a win.

  3. Unconvincing evaluation. Results are on the validation split only, and each seed uses a different 2,000-row subsample. Regression uses RMSE rather than RelBench's official MAE. There are no significance tests. The "matched" DFS often has far fewer features than DARC, and JUICE is truncated without selection. Against FastDFS, the only unrestricted baseline, DARC is 15/0/12, and this is not reported in the main text.

  4. Code contradicts the paper. The paper claims point-in-time features, but for training rows the FD map is fit on data up to the end of the training window (auto_fdhg.py:2170), so training rows see their own future. configs/main.yaml (4 statistics, 1 edge, TabPFN decoder) and gate.py (improve on every seed) describe a different method from Sec. 4. benchmark_tasks.csv records 24 SELECT / 26 FALLBACK, not the 14/34/3 in Table 2.

Questions for authors
  1. Can you report test-split results without subsampling, using MAE and significance tests?
  2. How does FDHG compare with adding LAST(X) or its encodings to Base?
  3. What changes if the FD map for each training row only uses data before that row's prediction time?
  4. Why is JUICE truncated rather than selected, and how were the Table 1 tasks chosen?

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

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