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Under review as a conference paper at ICLR 2027

TokAudit: Auditing What Extra Capacity Buys in Time-Series Tokenizers

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Abstract

Tokenizer capacity is usually treated as a scalar budget, but reconstruction error does not reveal what extra capacity preserves. We introduce TokAudit, a measurement framework for auditing marginal capacity increases by separating reconstruction gains into latent-structure and observation-noise components, benchmarking their allocation against a matched reference, and measuring downstream utility independently. Across the tested tokenizer constructions, most of what extra capacity buys in reconstruction is observation noise rather than latent structure, while learned codecs are usually less noise-oriented than the matched reference. More noise-oriented allocation is also associated with smaller downstream utility gains, but this relationship is population-dependent. TokAudit therefore separates capacity growth, reconstruction composition, and task utility, reframing tokenizer scaling as an auditable allocation problem.

Primary area:
datasets and benchmarks
Keywords:
time-series tokenization, discrete representation learning, quantization, tokenizer capacity, rate-distortion, time-series forecasting

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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_tqu5OpenReview ↗
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Paper summary

The paper introduces TokAudit, a framework for auditing capacity transitions in time-series tokenizers. In settings with known latent states and resampleable observation noise, it separates marginal reconstruction gains into state- and noise-related components, compares them with a matched reference, and evaluates downstream utility separately. The main result is that most additional reconstruction gain comes from observation noise in the tested settings. The reference-relative results and the link between noise allocation and utility are less consistent across populations.

Critical strengths
  1. The paper formulates a useful measurement problem by separating nominal capacity, realized occupancy, the composition of reconstruction gains, and downstream utility. The explicit ledger and conditional-mean formulation make the measurement target clear, and help avoid treating lower reconstruction error as direct evidence of a more useful representation.
  2. The matched training contrast provides a useful controlled demonstration that TokAudit can distinguish representations with similar reconstruction gains and occupancy, but different state–noise allocations.
  3. The paper includes a fairly thorough set of calibration and robustness checks, including finite-replica validation, analytic controls, tokenizer controls, and alternative dynamics and readers.
Critical weaknesses
  1. The practical value of the audit beyond characterization is still unclear. The pooled cross-generator allocation–utility association disappears after conditioning on ladder position and realized occupancy, and the paper does not show clear gains for utility prediction or capacity selection. The matched contrast shows that TokAudit can detect differences missed by reconstruction and occupancy, but it is not yet clear when those differences are useful in practice.
  2. The interpretation of the matched reference is also somewhat unclear. The measured codecs are deterministic, while the Gaussian reference includes test-channel randomness in its noise-related account. As a result, the reference-relative excess may reflect both allocation differences and the deterministic-versus-stochastic mismatch. The paper notes this distinction, but its impact on the “below-reference” interpretation is not fully resolved.
Questions for authors
  1. How should “below the reference” be interpreted when the reference noise account also includes test-channel randomness? To what extent could this reflect the deterministic-versus-stochastic difference rather than observation-noise allocation alone?
  2. Beyond the matched contrast, what decisions or conclusions does TokAudit enable that cannot be obtained from reconstruction, occupancy, and utility diagnostics alone?
  3. The main correlation interval resamples initialization seeds, while the test panels are fixed. How sensitive is the result to the choice of test panels or data-generation seed?
1 comment

Thank you for recognizing the measurement formulation and the matched contrast. The revision strengthens that contrast with independent confirmation and adds direct evidence addressing the reference and panel-sensitivity questions.

  1. Interpreting “below reference.” It means a smaller marginal noise-related share than the specified Gaussian test channel at the corresponding realized occupancies. Because that channel includes its own randomness, the excess is not a pure physical-noise difference or a distance from an optimum. We tested whether determinism alone accounts for the pattern using a fixed uniform quantizer selected on validation occupancy and measured on the same states and noise replay. Learned codecs lie below reference on 51/54 transitions, whereas the deterministic quantizer does so on 1/54. Median shares are 0.940/0.999 and median excesses −0.044/+0.016 (Appendix B.6). A post-hoc reference recalculation at the learned test rates changes no sign. Determinism is therefore not sufficient to explain the learned-codec pattern, although this control does not isolate the magnitude of the channel-randomness contribution. The matched-composition evidence itself does not depend on the Gaussian reference.
  2. Conclusions beyond the matched contrast. The new error comparison explains a concrete disagreement: M = D_s + V, so increasing output variance can worsen single-draw state error while conditional-mean fidelity improves. This occurs on 56/64 repetition-level confirmation transitions and 50/54 initialization-aggregated sweep transitions, with both intervals excluding zero on 54 and 29 (Section 5.2; Appendix G). The populations are analyzed separately. M − V is an equivalent implementation; the contribution is explaining what the individual readings mean, not claiming D_s is universally preferable. The new window bottleneck also identifies a composition boundary. For a 16-step window compressed into one token, whole/local noise shares change from 0.838/0.885 at SNR 0.1 to 0.101/0.348 at SNR 1.0, using train-fixed-scale ratios of mean gains. The post-hoc 64-dimensional reference agrees on dominance in all four cells and on the cross-SNR direction, while differing in magnitude (Section 5.3; Appendix E.8). Position-wise analysis locates the whole-input advantage mainly in additional target visibility, rather than establishing a causal temporal-modeling benefit. Finally, the submitted matched contrast now has an independent RBQ confirmation and VQ-VAE extension, each with 16 training blocks (Table 2). The noise-share changes are −0.037 and −0.056 within the declared practical matching bands. Simple error/variance diagnostics detect parts of the intervention too; the demonstrated discrimination is relative to reconstruction and occupancy. These results support diagnosis and explanation. They do not establish an incremental selection advantage: the new selection comparison chooses the same design under G_x and G_s, and the original prediction/selection limitations and capacity-conditioned association result remain explicit.
  3. Sensitivity to test panels and generation seeds. We held all 220 trained codecs and probes fixed, retained the 32-transition population, and evaluated eight fresh test splits with new signal/noise seeds. Training normalization and noise scale remain fixed, and probes are not refitted (Section 4; Appendix E.10). The endpoint has mean −0.550, SD 0.022, and range [−0.583, −0.518], compared with −0.538 on the original panels. The negative direction persists across these draws, directly addressing the panel axis omitted by the initialization-only interval. We report this separately: it measures test-panel sensitivity at fixed models, not joint uncertainty over training populations or a population-independent association.
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Paper summary

This paper introduces the TokAudit evaluation framework to address the question of whether improved reconstruction performance resulting from increased capacity in time-series tokenizers stems from enhanced representation of true state information or merely from reduced observation noise.

The framework investigates changes in a single tokenizer across different capacities, decomposing improvements in reconstruction error into gains related to latent states and those associated with noise reduction. It uses a Gaussian reference model that matches the actual token occupancy distribution for comparison. Additionally, the authors analyze the relationship between increased capacity and downstream task performance through prediction tasks.

Experiments are conducted using quantization mechanisms such as VQ-VAE, FSQ, and RBQ under various noise levels and dynamic systems. Results show that the reconstruction gain achieved by increasing tokenizer capacity primarily originates from noise-related improvements. The authors also observe that higher noise-related gains tend to correlate with lower downstream task performance, although this relationship is not consistent across different experimental settings.

Overall, the main contribution of this paper lies in providing a systematic measurement methodology for analyzing changes in tokenizer capacity, rather than proposing new time-series tokenizers or training methods.

Critical strengths

(1) The research question has practical relevance. This paper addresses a research-worthy issue in time series representation learning: whether a reduction in reconstruction error truly indicates that the tokenizer has learned more information beneficial to downstream tasks. Existing studies typically evaluate tokenizers using reconstruction error, codebook utilization, and downstream task metrics; however, these metrics make it difficult to directly interpret how the information retained by the model changes as capacity increases. The authors attempt to separately analyze reconstruction performance and downstream task performance, offering valuable insights into understanding the relationship between tokenizer capacity and representation quality.

(2) The experimental analysis is thorough, and the authors clearly explain certain conclusions that do not hold. The paper considers various quantization mechanisms, different noise levels, and partially nonlinear and seasonal time series, and tests the stability of estimators. Rather than interpreting all experimental results as supporting the initial hypothesis, the authors explicitly point out that certain statistical associations are data-dependent.Moreover, the paper documents in the appendix some experimental design and implementation biases, along with subsequent correction procedures. This transparency regarding experimental limitations and analytical adjustments is commendable.

Critical weaknesses

(1) The methodological innovation is limited; the evaluation framework primarily builds upon existing statistical analysis and information-theoretic tools. The main approach of this paper involves decomposing reconstruction error into error terms from different sources and analyzing them by aligning with reference models and downstream task metrics. However, the conditional expectations, variance decomposition, finite-sample bias correction, and Gaussian rate-distortion reference model used in this process are all built upon existing statistical analysis and information-theoretic methods.The paper organizes these analytical techniques into a unified evaluation framework, which demonstrates a certain level of systematicity, yet it does not sufficiently clarify what fundamentally new measurement capabilities arise from this combination.In particular, the paper does not propose novel tokenizer architectures, capacity allocation strategies, or training optimization methods, nor does it establish theoretical guidelines that can directly guide capacity selection. Therefore, I believe this work is more akin to an integration and empirical study of existing analytical tools, with relatively limited methodological innovation and practical technical contribution.

(2) The core analysis heavily relies on idealized data assumptions, limiting the method's applicability to real-world time series. TokAudit's requirement for state and noise decomposition assumes that the latent state can be obtained and that observation noise can be resampled while keeping the latent state unchanged. However, in real-world time series data, the true latent state is typically not directly observable, and noise may not be cleanly separable from the state. This paper primarily conducts measurements using artificially constructed state-space models with known additive Gaussian noise. While this design helps validate the analytical method, it does not sufficiently demonstrate whether the method can reliably distinguish meaningful information from noise in practical applications. Although the paper includes experiments on real time series, most analyses still rely on manually injected known noise or require predefined ways of decomposing states and residuals. In particular, the experiment in Appendix G.4 shows that when the state and residual do not satisfy the required conditional relationships, measurement results may deviate significantly from the target quantities. Therefore, the current method remains highly limited in terms of applicability to real data and interpretability of results. The authors are advised to further clarify under what real-world data conditions this framework is actually applicable.

(3) Core experiments rely too heavily on simplified tokenizers and prediction tasks, creating a significant gap from practical time series modeling scenarios. This study primarily employs four-dimensional time series inputs and uses MLP-based encoders and decoders to compare different quantization mechanisms and their capacity variations. Although these settings help control experimental variables, they still differ significantly from the Tokenizers used in practical time series foundational models. For instance, modern time series models often employ representations based on patches, convolutions, or frequency-domain transformations, and may extract complex dynamic features over extended temporal windows. In contrast, this work mainly adopts a per-time-step encoding approach. While limited experiments with larger temporal receptive fields were included, these representative Tokenizer architectures have not been fully covered. Moreover, the primary downstream evaluation relies on reading models such as Ridge regression to predict the latent state at the next time step, with performance measured by RankIC. This setup does not adequately reflect how Tokenizers are actually utilized in real-world prediction, anomaly detection, or classification tasks. Therefore, I believe the current results mainly illustrate the behavior of the simplified models tested under specific data generation mechanisms, and are insufficient to support general conclusions about the capacity scaling of time series Tokenizers.

Questions for authors

Q1. Regarding methodological innovation. The main methodology of this paper builds upon existing tools such as conditional expectation decomposition, finite-sample bias correction, and Gaussian rate-distortion analysis. Could the authors further clarify what novel and irreplaceable contributions TokAudit offers compared to directly applying these established statistical methods? In particular, which design elements within the framework provide information that existing evaluation methods cannot capture?

Q2. Regarding applicability on real-world data. TokAudit requires the ability to access latent states and resample observation noise under fixed state conditions. However, real-world time series often fail to meet these requirements. Could the authors further clarify how this framework can be reliably applied when latent states are unobservable, or when noise is temporally correlated or state-dependent? Can they provide validation on real data without relying on known noise injection?

Q3. Regarding the representativeness of the experimental models. The paper primarily uses a four-dimensional input and a relatively simple MLP tokenizer, whereas patch-based, convolutional, or frequency-domain tokenizers are commonly used in practical time series models. Could the authors further explain why the current experiments are sufficient to represent the general behavior of tokenizer capacity scaling in time series? Is it possible to validate the core conclusions on at least one tokenizer that is more representative of real-world time series foundational models?

Q4. Regarding the practical value of the newly introduced metrics. Appendix F.3 shows that incorporating state-dependent gain does not improve cross-condition prediction performance downstream; Appendix F.4 also indicates that capacity selection based on this framework is no better than directly using validation set task metrics. Could the authors further clarify how the information provided by TokAudit contributes to practical model design? Are there real-world scenarios where traditional reconstruction error, occupancy, and downstream validation metrics fail to distinguish between models, while TokAudit can clearly guide capacity selection?

Q5. Regarding interpretation of key conclusions and statistical metrics. The noise gain proportion in the paper reflects the composition of reconstruction error improvement, rather than a direct decomposition of coding capacity or mutual information. How do the authors demonstrate that the statement "additional capacity is primarily used for noise" accurately captures the actual representation behavior of the tokenizer? Furthermore, how sensitive are the current evaluation results to the choice of reference models, small total reconstruction gains, and non-Gaussian observational noise?

3 comments

Thank you for the detailed questions. TokAudit makes the composition of trained capacity gains measurable. Q1. Contribution beyond established tools. The contribution is a validated measurement capability, not a new variance identity. Reconstruction and occupancy can conceal different gain compositions: across 16 independent blocks per mechanism, consistency training changes noise shares by −0.037 [−0.043, −0.032] for RBQ and −0.056 [−0.060, −0.053] for VQ-VAE, while reconstruction-gain gaps are 0.61%/3.09% and occupancy-increment gaps are 0.000136/0.037317 bits (Table 2). Appendix E.7 specifies the practical matching bands and the different interval procedures. We recognize M − V as an equivalent computation of D_s; the contribution concerns what is measured, not an exclusive implementation. Q2. Applicability to real data. Section 3.2 distinguishes identifiable state/noise models from model-relative declarations. Antithetic replay requires conditional symmetry and independent pairs; the residual interpretation requires conditionally zero-mean noise. State-dependent or temporal noise requires the corresponding conditional or joint law. The new Student-t/AR(1) stress test demonstrates this requirement: for the higher-capacity window codec under AR(1), iid replay gives approximately −0.0015 bias against the high-budget benchmark, versus +0.0001 with joint-law replay (Appendix E.11). Natural-noise validation remains outside the established evidence.

Q3. Tokenizer representativeness. The revision adds a convolutional bottleneck compressing a 16-step, four-channel window into one token, with 192 fits (Section 5.3). Whole/local noise shares change from 0.838/0.885 at SNR 0.1 to 0.101/0.348 at SNR 1.0, using corrected-scale ratios of mean gains; a doubled-budget check preserves this boundary. This extends the evidence beyond pointwise MLPs(Appendix E.8). Q4. Practical value. TokAudit detects composition differences missed by approximately matched reconstruction/occupancy and explains why single-draw state error can worsen while conditional-mean fidelity improves (Sections 5.1–5.2). This is a concrete diagnostic capability. We keep it distinct from selection: utility was not measured in the independent confirmation units, and the new selection study chooses the same candidate under reconstruction and state gain. Task validation remains necessary. Q5. Interpretation and sensitivity. The share decomposes reconstruction improvement, not bits or mutual information. G_s measures conditional-mean fidelity, not usable state information. Reference choice affects the excess, not this decomposition. A new deterministic occupancy-matched quantizer falls below the Gaussian reference on 1/54 transitions, versus 51/54 for learned codecs, so determinism alone does not explain the pattern; channel randomness still limits its physical interpretation (Appendix B.6).

Thanks for the additional experiments. The new tokenizer and noise tests are helpful and address some of my concerns.

I still have some doubts about how well this would work on real data, especially when the state and noise aren't clearly separated. Also, I'm not sure the proposed metrics offer much benefit for actually choosing tokenizer capacity.

The paper is clearer now, and I appreciate the effort. But I'm still not fully convinced, so I'll keep my score for now.

We built the decomposition to answer one question: when extra capacity lowers reconstruction error, is it buying signal or noise—and is that capacity step worth taking? Real data doesn't give you the true state. No measurement does. The demand that matters is that the state model be stated and tested. TokAudit does that. On ETTm1, with a declared causal seasonal state, the audit puts 52-84% of the reconstruction error and 34-66% of the capacity gain on the noise side. The same run residual lag-one autocorrelation of 0.79-0.99—the audit warning you, before you use the number, that the declared split is imperfect. On Weather,wecant track the state , then the audit given noting to split. But that's the correct behavior; a metric that silently returns a number when its assumptions fail is worse. In the known-truth test with AR(1) noise, replaying it as iid shifts the window codec by -0.0015; replaying the correct joint law leaves it at +0.0001. Reconstruction and occupancy are just as model-dependent on real data. So the difference is that they don't say so. On selection, F.4 gives the direct answer: when you can afford full task validation, use it—it won in the tested cells. The audit earns its place when validation is unavailable, or when reconstruction and occupancy are tied. At matched reconstruction and occupancy, the noise share still separates training recipes. In a separate set of fits, candidates whose extra capacity goes disproportionately to noise gain less downstream utility (rho around -0.54), and the Beijing data show the same pattern. Validation answers which candidate performs better on the task you can measure. It does not answer what the extra capacity is doing. TokAudit answers that, and it flags when a reconstruction gain is mostly noise.

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Paper summary

The paper asks what a time-series tokenizer gains when it is trained at a higher capacity. TokAudit decomposes the resulting reduction in reconstruction error into a state component (closer recovery of a known latent state) and a noise component (more faithful reproduction of the observation noise), compares this split with a matched Gaussian reference, and measures downstream utility separately. On a small synthetic regime-switching VAR with per-time-step codecs, supplemented by several controls and a few real-data stress tests, the authors find that most of the additional gain is attributable to noise, that learned codecs usually allocate less of it to noise than the reference does, and that a larger excess noise share is associated with smaller utility gains, a relationship they describe as population-dependent.

Critical strengths

The measurement is well defined. The split into state and noise components is exact, and the estimator is validated in several ways, including known noise orderings and a closed-form quantizer. The paper is also unusually transparent. Failed criteria, inconclusive studies, protocol deviations and corrected values are reported alongside the positive results, and the authors withdrew a calibration claim when one of their own checks narrowly failed. The underlying question of what additional tokenizer capacity actually buys is relevant to the development of time-series foundation models.

Critical weaknesses
  1. In my view the headline result largely follows from the setup, and the findings specific to learned codecs do not survive the paper's own controls. The codecs are trained to reconstruct noisy observations. Once the quantization cells become finer than the noise, the noise effectively dithers the quantizer, and any further reduction in error is counted as noise gain. The paper's own results are consistent with this. The Gaussian reference attributes most of its gain to noise, the closed-form quantizer in App. C attributes essentially all of it to noise in the noisy settings, and untrained scalar binning shows the pattern even more strongly than the learned codecs (App. E.4). The findings specific to learned codecs are weaker. Scalar binning falls below the reference in only about half of its transitions and reverses the sign of the utility association, although its reader setup differs, and in the cross-generator population the association vanishes or turns positive once capacity is controlled for (App. E.1). The reference is also difficult to interpret, because it counts its own test-channel randomness as noise and therefore attributes nearly all of its gain to noise even in the absence of observation noise (App. C).

  2. The practical value of the audit is not demonstrated, and the method applies only when the noise is known. Adding the state account or the excess share to standard diagnostics worsens out-of-fold prediction of utility gain (App. F.3), the audit-based rule for selecting capacity ranks last among the rules compared, although the differences are not tested (App. F.4), and plain reconstruction gain tracks utility gain more closely than the excess share does (App. A.3). The method also requires a known latent state and resampleable noise, which is why the real-data stress tests inject synthetic noise. The ETTm1 application instead declares a state and treats strongly autocorrelated residuals as independent noise, and the authors' own known-truth simulation shows that such an account can capture only a small fraction of the intended quantity (App. G.4).

Minor comments. The interval reported for the main endpoint resamples only the seeds and holds the transitions fixed (App. B.5), whereas a Fisher-z interval for this sample size would be roughly five times wider. The paper is also difficult to follow, since most of the material needed to evaluate the claims is in a very long appendix and the text relies heavily on internal terminology ("ledger", "rung", "frozen re-read").

Questions for authors
  1. The closed-form quantizer in App. C already attributes essentially all of its gain to noise in the noisy settings, and untrained scalar binning behaves similarly. What do the noise shares of the learned codecs reveal beyond what any fine quantizer of a noisy signal would produce?
  2. Given App. F.3 and F.4, what decision would a practitioner make differently after running TokAudit?
2 comments

Thank you for the careful review. TokAudit's contribution is to make reconstruction-gain composition measurable across trained capacity transitions. Noise dominance is one empirical finding, rather than the sole basis of the framework. The submitted matched contrast already demonstrated information beyond reconstruction and occupancy; the revision strengthens that evidence.

  1. Beyond fine quantization of noisy observations. The fine-quantizer argument explains why noise dominance can occur, but does not determine the composition of a learned capacity transition. Our independent confirmation compares plain and consistency-regularized training over 16 data/initialization blocks per mechanism. At approximately matched reconstruction and occupancy, the noise-share changes are −0.037 [−0.043, −0.032] for RBQ and −0.056 [−0.060, −0.053] for VQ-VAE. Test reconstruction-gain gaps are only 0.61%/3.09%, and occupancy-increment gaps are 0.000136/0.037317 bits (Section 5.1, Table 2). Matching uses fixed practical bands; the intervals are simulation-calibrated for RBQ and finite-sample approximate Student-t for VQ-VAE (Appendix E.7). The new window bottleneck also shows that noise dominance is not inevitable: compressing 16 steps into one token gives noise shares of 0.838/0.885 at SNR 0.1 but 0.101/0.348 at SNR 1.0 for whole/local input, using ratios of mean gains (Section 5.3; Table 14). Thus the framework distinguishes both training-induced composition differences and changes across operating conditions.
  2. What does the audit enable in practice? It enables a researcher to distinguish similar reconstruction improvements by their conditional-mean state component and to explain conflicting diagnostics. With single-draw state error M and conditional output variance V, M = D_s + V. We find worsening single-draw error despite improving conditional-mean fidelity on 56/64 confirmation transitions and 50/54 sweep transitions; both intervals exclude zero on 54 and 29, respectively (Section 5.2; Appendix G). The two populations have different aggregation units and are analyzed separately. This diagnostic contribution does not depend on outperforming task validation. The negative utility-prediction and selection results delimit that separate use: neither the original study nor the new selection comparison establishes an incremental selection advantage. We retain those findings. Likewise, M − V is an equivalent implementation of the state component, and G_x ranks G_s closely; the added information is composition and explanation, not universal ranking superiority.
  3. Does the stochastic reference explain the learned-codec pattern? A new deterministic, validation-occupancy-matched uniform quantizer lies below the Gaussian reference on 1/54 transitions, versus 51/54 for learned codecs (Appendix B.6). Determinism alone therefore does not force the below-reference pattern. This control is distinct from the submitted scalar-binning experiment and does not replace its findings. Since the reference includes channel randomness, the excess remains a reference-relative descriptor, not a pure physical-noise difference or distance from an optimum. The capacity-conditioned cross-generator limitation also remains explicit.
  4. Interval, panel sensitivity and scope. The initialization-bootstrap interval conditions on the specified transitions and panels. A conventional Fisher-z interval uses a different sampling model; these transitions share capacity endpoints and are not independent sampled pairs. To examine the panel axis directly, we fixed all 220 codecs and probes and generated eight fresh test splits: correlation mean −0.550, SD 0.022, range [−0.583, −0.518], versus −0.538 originally (Section 4; Appendix E.10). This supports stability to those panel draws without claiming uncertainty over arbitrary training populations. Known or defensibly declared state/noise models remain an explicit applicability condition. The operational-state failure is retained, and the main text now presents the matched confirmation, error disagreement and window boundary together in Section 5, with their assumptions and limitations.

I thank the authors for their response and the new experiments which should improve the paper. The matched confirmation study and the deterministic quantizer control help address some of my concerns. However, my main concern is not addressed. Namely, the authors' response does not identify a concrete decision a practitioner would make differently after running TokAudit. Also, the cross-generator limitation remains. I will therefore maintain my score.

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