acceptodds
Under review as a conference paper at ICLR 2027

Xbank: Cross-Bank Transfer of Transaction Foundation Models

Abstract

Self-supervised learning enables banks to derive reusable representations from customer transaction histories. However, the large datasets needed for pretraining typically remain proprietary, limiting opportunities to study how these representations transfer across institutions. We introduce , a dataset comprising around 91.5 million daily-aggregated transaction records from 378,305 corporate clients, with 13 categorical features, two numerical features, and three monthly product-propensity targets. Together with the Multimodal Banking Dataset (), which contains transaction histories for approximately 1.5 million corporate clients, supports a benchmark for cross-bank transfer of frozen representations. We evaluate five models spanning contrastive, autoregressive, masked-modelling, and temporal point-process objectives. By evaluating -pretrained encoders on raw transactions, their daily aggregates, and , we isolate the effect of aggregation within the source institution and assess cross-bank transfer at the same aggregation level under each dataset’s native evaluation protocol. To handle unknown field correspondences, we propose a dictionary-free schema-alignment method based on semi-relaxed Fused Gromov-Wasserstein optimization. It combines statistical column profiles with within-bank feature dependencies, accommodates schemas of different sizes, and determines a fixed mapping before evaluation without using downstream labels. Together, these contributions provide a framework for studying the transfer of transaction representations across banks with heterogeneous data schemas.

Primary area:
datasets and benchmarks
Keywords:
transaction data, cross-institution transfer, event sequences, self-supervised learning, dataset shift, schema matching, optimal transport, benchmark dataset, banking

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_vPYDOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper introduced XBANK, an anonymized corpus of 91.5M daily-aggregated corporate-client transaction rows. built a nested benchmark examining aggregation changes and cross-bank transfer, and a dictionary-free schema-alignment protocol based on semi-relaxed Fused Gromov-Wasserstein optimization.

Critical strengths
  • This paper introduced XBANK, an anonymized corpus of 91.5M daily-aggregated corporate-client transaction rows, which together with MBD forms the a pair of industrial-scale banking datasets with distinct schemas.
  • Applied Fused Gromov-Wasserstein assignment to XBANK and MBD, and showed better performance than simple Hungarian-assignment column matcher.
Critical weaknesses
  • Banks may not be able to share data or models because of privacy and legal constraints. Even if they can, their customers may behave quite differently. The paper does not say whether XBANK and MBD cover overlapping customer populations, or explain why a representation learned from one should transfer to the other. If the datasets come from the same financial institution, why can’t they share feature names or a common schema? If they come from different institutions, how does the method deal with differences in their customers? How to make sure all the inputs needed from the frozen representation are available in the new dataset? Without a clearer account of the setting, it is hard to see the use case for XBANK or why these datasets are needed to test transfer learning.

  • The title frames the paper around transaction foundation models, but the paper does not explain why XBANK and MBD make a suitable benchmark for them. Nor is it clear that any of the five models evaluated are transaction foundation models. Applying FGW to the two datasets does not, on its own, seem like a strong methodological contribution. A public B2B transaction dataset is valuable, but the paper needs to say more clearly what XBANK makes possible for transfer learning or foundational model that existing datasets do not especially.

Questions for authors
  1. What is the intended use case for cross-bank transfer? What would each bank need to share in practice, and why is XBANK useful for studying that setting?
  2. Does the method assume that all features needed to compute the frozen representation are available in the new dataset? If so, how likely is that to hold across banks with different data collection practices and schemas? What happens when some features are missing?
  3. Do XBANK and MBD contain the same clients, or different client populations? If the populations differ, how does the approach handle differences in customer behavior? Could those differences cause the feature-matching step to fail?
  4. How were the combination weights in Section 5 hand-tuned? Were they chosen using a separate validation set or fixed before evaluating the reported results? It would help to show how sensitive the results are to these weights, to rule out cherry-picking.
  5. Can the authors explain the finding that aggregation shift does not uniformly degrade performance? Is there evidence that this result holds beyond the particular distributions in XBANK and MBD? If it's mainly due to the separate normalization, what should researchers take away from it when designing future methods or benchmarks?
  6. What makes this a benchmark for transaction foundation models specifically? How do the five evaluated models test the capabilities implied by that framing, rather than transfer learning?
2 comments

Thank you for pushing on the practical setting and the foundation-model framing — both deserve a clearer account than the original submission gave.

You raise a fair question about the intended use case for cross-bank transfer, and why two banks would ever need this rather than simply sharing data. The setting we have in mind is deploying a frozen, pretrained transaction encoder at a bank that took no part in its pretraining. What actually crosses the institutional boundary is (1) the frozen model weights pretrained only on the public MBD corpus, and (2) column-level statistical summaries of the source bank's pretraining schema (cardinality, entropy, quantiles). The receiving bank runs the frozen encoder locally on its own data and trains its own lightweight downstream classifier (LightGBM/MLP) on its own labels. Two competing banks generally have no legal or commercial basis to exchange raw transaction data, but a published checkpoint and a column-level statistical description are comparatively low-risk to produce. XBANK matters for studying exactly this scenario because it is a second institution with its own schema and its own targets, released publicly alongside MBD, which makes the scenario testable by outside researchers, not only internally at a bank.

You ask whether the method assumes every feature needed for the frozen representation is available at the new institution. It is not. Section 5 explicitly handles the case where no admissible XBANK column exists for an MBD field — "if Aj=∅A_j = \emptyset, Yj is left unfilled". This as an outcome of the matching step. Unfilled fields are zero-filled, following the MBD adapter's own absent-columns convention.

Do XBANK and MBD cover the same customer population? Both datasets consist exclusively of corporate clients — XBANK comprises roughly 378K clients "of a major commercial bank," and MBD is a separately published dataset covering roughly 1.5M clients — and the two come from different, unaffiliated institutions. Verifying customer-level overlap between two banks' corporate client bases is not something either institution can do or disclose. We'd also stress that the corporate segment is, in our view, the most commercially important one for studying cross-bank transfer: corporate clients carry disproportionate transaction volume and revenue relative to their numbers. The representation that transfers well here has practical value. This also answers the related question of why the two institutions don't simply share feature names or a common schema: XBANK and MBD are maintained independently by separate organizations with no coordinated schema design, which is precisely why a schema-alignment step is needed.

Regarding how the combination weights in Section 5 were chosen, and how sensitive the results are to them: in the updated manuscript, the passport-distance sub-weights use equal weighting (1/4 per categorical component, 1/3 per numeric component), but the FGW combination weight — which balances the passport (statistical-shape) term against the structural (within-bank) term — is no longer fixed a priori. We select it empirically: we intentionally inject noise into a held-out field with a known ground-truth correspondence, sweep α\alpha across its range, and measure the fraction of correctly restored field correspondences at each value (Appendix A2). The masked MBD-to-MBD recovery experiment (across raw-to-raw, daily-to-daily, and daily-to-raw settings) evaluated with the optimal α\alpha selected by this sweep.

Finally, to clarify what distinguishes this benchmark as one for transaction foundation models: all five architectures are pretrained once, purely self-supervised, on unlabeled transaction sequences, with no task-specific labels entering pretraining, and are then used strictly as frozen feature extractors (Section 4.4). The same frozen checkpoint is reused across four MBD targets, three XBANK targets, two aggregation levels, two independent institutions, and two downstream probe families (LightGBM, MLP), without the pretrained weights ever being touched again. That reuse — a single pretrained asset applied across many downstream tasks and domains without retraining — is the operational property a foundation model is meant to have, which is also why foundation model Chronos-2 fits naturally into the same comparison. This is what separates the setting from ordinary transfer learning: nothing is adapted to the target site. The benchmark's three stress tests (aggregation shift, institution shift, and schema shift without a dictionary) were chosen because they are the specific modes a reusable pretrained asset must survive.

Thank you for providing the cross-bank transfer scenario. Could you provide real-world use cases or concrete examples that support its practical relevance? Given privacy concerns, even sharing a frozen, pretrained encoder between two banks may require additional privacy-preserving measures. This scenario may be more realistic in non-financial settings.

You state that “Unfilled fields are zero-filled, following the MBD adapter’s own absent-columns convention.” It would be helpful to quantify the impact of missing features on the approach’s performance.

The response does not address my earlier question: “If the populations differ, how does the approach handle differences in customer behavior? Could those differences cause the feature-matching step to fail?”

Overall, I appreciate the authors’ efforts to clarify these points. However, the concerns above remain unresolved, so I will maintain my original score.

Reviewer_h1uAOpenReview ↗
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Informativeness
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Paper summary

This paper introduces a large-scale corporate banking transaction dataset, XBANK, containing 91.5 million daily-aggregated records from ~378K clients, to investigate the transferability of transaction foundation models across financial institutions. The authors establish a benchmark using MBD and XBANK, evaluating five self-supervised models under different aggregation levels and institutional settings. They also propose a dictionary-free schema alignment protocol to address heterogeneous feature schemas. Experimental results show that daily aggregation slightly improves performance for most models, while the proposed alignment improves ROC-AUC in most cases but shows mixed effects on top-k prediction metrics.

Critical strengths
  • The paper addresses a practically important and well-motivated problem of transferring pretrained transaction models across financial institutions with heterogeneous data schemas and aggregation levels.

  • The introduction of a large-scale corporate banking dataset is a valuable contribution, since the availability of public financial transaction datasets is limited.

  • The evaluation covers five self-supervised architectures with different learning objectives and investigates both aggregation effects and schema alignment, providing useful empirical observations about the robustness of transaction representations.

Critical weaknesses
  • Given that its main contribution is on a novel benchmark construction with validation, the experiment and reproducibility could be strengthened. The aggregation analysis is confounded by separately fitted amount normalization. More importantly, the lack of publicly accessible XBANK data and benchmark code during review limits independent verification of the proposed benchmark and its results.

  • The evaluation does not fully substantiate the claimed decomposition of the cross-bank transfer gap. Since MBD and XBANK have different prediction targets, class distributions, and evaluation protocols, the institution-shift component cannot be directly quantified, limiting the conclusions about cross-bank transferability.

  • The methodological contribution and experimental validation of the proposed schema alignment remain limited. Although the FGW-based approach improves ROC-AUC, the efficacy of its individual components is not sufficiently validated. Further, quantitative accuracy for the described schema recovery experiment is not clearly provided.

Questions for authors

Please see weaknesses

1 comment

Thank you for recognizing the scale and practical relevance of XBANK. Below we address each point of your comments.

On the concern that fixed-amount normalization, the calendar history window, and truncation to the most recent 500 events might confound the comparison between raw and daily-aggregated inputs: updated Section 7 ("Aggregation is confounded with rescaling") now states this directly. Amount normalization is refit separately on each rendering's post-aggregation sums, so the two renderings sit on measurably different effective scales. “We cannot tell whether this improvement reflects this rescaling or aggregation itself. Disentangling the two would require holding the amount channel's scale and the covered time span fixed across both renderings.” We flag this as an open limitation.

We share your concern about the data and code being inaccessible during review. Unfortunately, this follows from the conference's double-blind policy, which prohibits links that could reveal the authors' identities, including to our GitHub repository or Zenodo listing.

You raise a fair concern about isolating the institution-shift effect from differences in targets, class distributions, and evaluation protocols between MBD and XBANK. We address this with the revised benchmark design, though one related confound remains open, as noted below. We add a second pretraining arm (conditions D and E, Table 3), both evaluated under daily aggregation so that only the institution varies between them, giving Δinst=M(D)−M(E)\Delta_{\mathrm{inst}}=M(D)-M(E) as a direct, matched-aggregation measure of the institution-shift component. One confound remains open: MBD's and XBANK's targets still differ in identity and base rate, so raw PR-AUC under Δinst\Delta_{\mathrm{inst}} still mixes the institution effect with this prevalence difference (Section 7); we mitigate this by relying on ROC-AUC, which is less sensitive to prevalence, for the institution-effect claim. We'd add, though, that differing targets and evaluation protocols are not an artifact of our design but a property of the task itself: any institution adopting a representation trained elsewhere inherits a different product catalogue and evaluation regime by construction, so a fully "clean" institution effect, isolated from these differences, would not correspond to any deployment a practitioner actually faces.

On the lack of quantitative validation of the schema-alignment method's field-recovery accuracy: Section 5 now defines the two signals feeding the fused objective — passport (statistical-shape) distance and within-bank structural distance — combined via a weight α\alpha, where α\alpha=0 uses only column shape and α\alpha=1 only relational structure. Rather than fixing this trade-off a priori, we select it empirically: we intentionally inject noise into a held-out field with a known ground-truth correspondence, sweep α\alpha across its range, and measure the fraction of correctly restored field correspondences at each value (Appendix A2). The recovery-accuracy question is resolved as well: with α\alpha set optimal way, Section 5 reports that the matcher correctly recovered all evaluated field correspondences in each of three settings: raw-to-raw, daily-to-daily, and daily-to-raw matching.

Reviewer_9C9QOpenReview ↗
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2
Confidence
3
Informativeness
2
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Paper summary

This paper introduces XBANK, a large-scale dataset designed to evaluate the cross-institutional transferability of foundation models for transaction data. XBANK comprises approximately 91.5 million daily-aggregated transaction records from 378,305 corporate clients, featuring 13 categorical attributes, 2 numerical attributes, and 3 predictive targets related to monthly product propensity. The authors conduct a cross-institutional evaluation of five self-supervised transaction models, CoLES, NEP, MLM, THP, and COTIC, using both XBANK and the existing Multimodal Banking Dataset. Furthermore, the authors propose a method based on semi-relaxed Fused Gromov–Wasserstein optimization, which enables the mapping of heterogeneous input patterns by integrating column-level statistical features and inter-feature dependencies, all without requiring downstream labels.

Critical strengths

This paper introduces XBANK, a large-scale, real-world dataset of banking transactions with significant research value. It encompasses approximately 378,000 corporate clients and 91.5 million daily-aggregated transaction records. The study extends its evaluation to cross-bank migration scenarios, a common challenge in practical deployments addressing real-world issues such as varying aggregation granularities and the alignment of heterogeneous data fields. Consequently, XBANK serves as a valuable data resource for research on transaction representation across different financial institutions. Under a frozen-encoder setting, the paper evaluates five distinct models, spanning contrastive learning, autoregressive prediction, masked modeling, and temporal point process modeling. Furthermore, the study reports performance based on both overall ranking metrics and the accuracy of identifying the top 5% of entities. It reveals that while pattern alignment may improve ROC-AUC scores, it can simultaneously degrade the quality of the top-ranked list, an empirical observation that offers meaningful insight into the discrepancies between different evaluation metrics.

Critical weaknesses

This paper presents a large-scale, cross-bank model evaluation dataset. However, the design of the benchmark experiments and the subsequent analysis of the results have notable shortcomings. The MBD and XBANK datasets differ in their tasks, class distributions, and evaluation protocols. Consequently, the current experimental design fails to isolate the impact of these factors from that of the change in banking institutions, making it impossible to attribute performance variations solely to the latter. The paper does not quantify the effect of shifting between institutions, and the use of aggregated experiments, which alter the normalization parameters for transaction amounts, precludes the isolation of the impact of aggregation itself. Furthermore, the discrepancy between overall ranking metrics and the quality of top-k lists has not been explicitly linked to the specific challenges inherent in cross-bank migration. The schema alignment method also lacks quantitative validation regarding the accuracy of field-mapping recovery, which hinders a distinct assessment of model transferability versus alignment quality. Finally, the absence of concrete data examples and flowcharts illustrating the construction process makes the benchmark difficult to understand.

Questions for authors
  1. Lines 256- 259, M(B)-M(C) is defined as the incremental institutional migration gap, but the prediction targets, category proportions, and evaluation protocols of MBD and XBANK are different. How do the authors distinguish the impact of institutional changes from these factors?

  2. If the fixed-amount normalization method, calendar history window, and test sample are used, does the conclusion that daily input is better than raw input still hold? Lines 211- 212, Currently, the most recent 500 records are truncated for both inputs. Does this cause the aggregated version to cover a longer historical period, thus affecting the comparison results?

3.When the source domain category vocabulary is frozen, how to deal with unknown categories of the target bank and categories that encode the same semantics and are inconsistent?

2 comments

Thank you for the careful review. In the revised paper, we replace the original nested A→B→C design with a full factorial design (Table 3, conditions A–E), adding a second pretraining arm (D, E) under daily aggregation in which only the institution varies. This yields a direct institution-shift measurement, Δinst=M(D)−M(E)\Delta_{\mathrm{inst}}=M(D)-M(E). A related confound remains open, however: MBD's and XBANK's targets still differ in identity and base rate, and Section 7 explicitly notes that Δinst\Delta_{\mathrm{inst}} conflates the institution effect with this base-rate difference when measured on raw PR-AUC; for this reason we rely on ROC-AUC, which is less sensitive to prevalence. We would add that the difference in targets and evaluation protocols is not an artifact of our experimental design but a property of the task itself: any institution adopting a representation trained elsewhere inherits a different product catalogue and a different evaluation regime by construction, so a fully "clean" institution effect isolated from these differences would not correspond to any deployment a practitioner actually faces.

We also thank the reviewer for pointing out the confound between normalization, history window, and aggregation. We caught this point after submission. Section 4.2 now states that the two renderings differ in temporal granularity and the time span covered, since the 500-event truncation means daily-aggregated histories reach further back in calendar time than raw ones. Section 7 states this limitation directly: we cannot tell whether the observed improvement reflects this rescaling or aggregation itself, and disentangling the two would require holding the amount channel's scale and the covered time span fixed across both renderings. Category vocabulary and semantic compatibility across institutions are now addressed in the closing paragraph of Section 5. We state there that the recovered mapping is column-level only and does not establish value-level correspondences: identical codes may carry different meanings across banks, and some values present in the target bank may be absent from the source bank altogether. Column matching, in other words, does not guarantee semantic compatibility between the matched columns' values, and we name this limitation as outside the scope of the matcher.

The original submission stated the ROC-AUC/top-k discrepancy as a general empirical finding without tying it to the migration setting itself. Subsection 6.1 now makes this link explicit: migration changes both the base rate of the target and the identity of borderline cases near the decision boundary. Which means that a representation transferred across institutions can preserve the global ranking it was trained for (reflected in ROC-AUC, which aggregates over the full score distribution) while reordering cases specifically at the extreme tail, where precision at top-k is measured. We argue this is not a generic metric artifact but a structural consequence of cross-bank transfer: the institution shift concentrates its damage exactly where the top-k candidate list is most exposed to it, so that we report both ROC-AUC and top-k metrics.

The original submission did not quantify the accuracy of the recovered field mapping itself. We have added a quantitative validation in Appendix A2: we intentionally inject noise into a held-out field with a known ground-truth correspondence, then sweep the α\alpha parameter governing the trade-off between the statistical and structural terms of the FGW objective, and measure the fraction of correctly restored field correspondences at each value. This gives a direct, label-free measurement of mapping-recovery accuracy, used both to select α\alpha and to report the method's recovery rate.

Following your comment, we have added new Figure 1 with the factorial benchmark design for cross-bank transfer to simplify the understanding of our approach.

Thank you for the additional experiments and for clarifying the limitations of the original design. My question is whether daily input still performs better when the calendar history window, amount normalization method, and test samples are held fixed. The response does not report this comparison, so my question remains unanswered.

Regarding the category vocabulary, the authors explain the limitations of field-level mapping. However, my original question concerns how specific category values are handled during inference. When the source bank's vocabulary is frozen, how are previously unseen categories from the target bank encoded? If two banks use different codes for the same category, does the model treat them as different categories, or are they mapped to a common representation before being fed into the model?

These two issues remain important for evaluating the experimental results. Therefore, I maintain my original rating.

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

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