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Under review as a conference paper at ICLR 2027

When Learned Compression Loses Identity: Stage-Resolved Diagnostics for Exact-Entity Conditional Generation

Abstract

Learned compression is effective when task-valid variation can be discarded without identity loss, but can become a misaligned inductive bias when correctness depends on exact, non-substitutable categorical identity. Existing evidence does not determine where exact identity is lost, while comparisons that jointly change representation and corruption cannot attribute failure to either factor. We study personalized multi-day mobility generation as an identity-sensitive testbed, where recent user history conditions future visits over a known location vocabulary, yet models may produce structurally plausible sequences with the wrong locations for that user. An ordered representation–corruption intervention with stage-specific probes localizes identity loss and tests alternative explanations. The diagnosis reveals two distinct mechanisms: vector quantization aliases exact locations before diffusion, whereas continuous autoencoding preserves near-perfect clean reconstruction yet loses prefix-specific identity access during Gaussian latent denoising. Guided by this diagnosis, NADI instantiates the native-mask endpoint through native-space absorbing diffusion and achieves the highest composite objective across all four datasets in the primary evaluation. More broadly, reconstruction fidelity alone does not establish the suitability of a generative representation: for exact, non-substitutable entities, representation and corruption should be judged by whether condition-supplied identity distinctions remain accessible throughout generation.

Primary area:
generative models
Keywords:
Learned Compression, Conditional Generation, Diffusion Models, Identity-Preserving Generation, Human Mobility Generation

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_LWTGOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies when learned compression harms exact-entity generation, using personalized mobility as a test case. It proposes NADI, which directly generates location categories and improves composite scores across four datasets.

Critical strengths

S1: The problem is well motivated. A trajectory that looks realistic but visits the wrong places is of limited use for personalized generation. S2: The experiments show that near-perfect reconstruction can coexist with poor location recovery during generation. This is useful evidence that reconstruction quality alone is insufficient for choosing a generative representation.

Critical weaknesses

W1: The paper does not establish which task or data properties predict compression failure. This limitation reduces its guidance beyond the tested settings. W2: The experiments do not fully separate representation problems from model-specific conditioning failures.

Questions for authors

Q1: Within the evaluated datasets, which observable properties best explain the differences in identity recovery across representations? Can the existing results provide practical guidance on when removing learned compression is likely to help? Q2: What evidence shows that poor identity recovery comes from the compressed representation rather than the model’s limited use of user history?

4 comments
AuthorsOpenReview ↗

Response to Reviewer LWTG (1/2): representation versus history use, observable properties, and practical guidance

We thank the reviewer for two precise questions. Our answers rest on new experiments and narrow the paper's claims. The second comment gives the supporting tables and their place in the revised PDF.

W2 and Q2. Does poor identity recovery come from the representation or from limited use of history? It depends on the pathway.

Original CONT+AE: limited use of history. The reviewer's alternative is correct for this model. Under a history swap even its time-of-day profile barely changes, and only 34–51% of its windows follow the source user's visitation profile, where 50% means ignoring the history. We remove it from the evidence for compression loss.

VQ: the representation. VQ uses the condition, since its time-of-day profile moves with the history (own − swapped +.13 to +.28). Its codes, however, merge exact locations. Mapping each code to its most frequent location recovers only .06–.19 of visits on the three large vocabularies, which we call code purity (Table 18). Even a per-location codebook with K ≥ |V| collapses on TKY, where 93.6% of the locations seen in training share a code (three seeds, Appendix L).

Continuous latent: the readout. A repaired latent model (latent-point) applies the native-embedding model's denoiser and conditioning path to a frozen, standardized per-visit autoencoder latent. It follows the source user in 97–100% of windows (Table 3), and its autoencoder reconstructs 99.4–100% of visits (Table 17). It still loses beyond-prefix locations, the real future locations absent from the 7-day prefix. Their own−swapped recall, the recall under the user's own history minus that under another user's, is .042 / .002 on NYC / TKY. A categorical readout on the same latent recovers them (.562 / .467), and a point readout on native embeddings loses them too (.014 / .001, Table 2b). In a leak-free forecasting setting on a strict time split, without the given length and weekdays, the contrast persists, with non-overlapping seed ranges on NYC, TKY and YJ (Table 27).

Poor identity recovery therefore comes from the compressed representation when the learned code is not one-to-one, that is, when one code stands for several locations, and in continuous pathways from the point readout, whether or not the space is compressed. Within period, a categorical readout recovers about as much from the learned latent as from native embeddings. In forecasting on YJ, native embeddings keep more of this identity (.085 against .031).

W1 and Q1. Which properties explain the differences, and when does removing learned compression help?

Code injectivity predicts where learned compression fails. It is a property of the trained encoder, which a two-stage pipeline can measure before training the generator. The paper's VQ has code purity .40 / .06 / .19 / .07 on HK / NYC / TKY / YJ (three seeds, Table 18), and its beyond-prefix own−swapped recall is about zero on all four datasets. Codebook design matters as well as vocabulary size. Purity is only .40 on HK's 91 stations, while a per-location codebook makes HK nearly injective (.987) and VQ then matches NADI.

The share of the target identity in the user's own history, a data property that needs no model. For each window we measure the share of beyond-prefix targets that the user visited during the training period. On the main split it is 1.00, because test futures were training data, and this is where the output effect is largest. In the forecasting setting it is .63 / .28 / .31 / .48 on HK / NYC / TKY / YJ. Within every dataset, users with a higher share gain more from a categorical readout, monotonically across quintiles and after controlling for activity and history size (Spearman +.14 to +.52 across users, Table 29). Across datasets the comparison is descriptive. On HK, popular locations alone reach Recall@10 = .95 in the forecasting setting, so the gain stays small despite the highest share.

Practical guidance (Appendix M). First, check code injectivity, since removing or replacing learned compression helps when the code is not injective on the entities that matter. Second, a continuous latent that reconstructs well need not be abandoned. On the main split, reading it out categorically recovers most of what NADI recovers in native space (TKY .467 against .535, Table 2a), and the history share above estimates how much this helps. Third, before attributing a failure to the representation, run a history-swap test and evaluate prefix and beyond-prefix targets separately. As the reviewer notes in S2, reconstruction accuracy cannot replace these checks.

AuthorsOpenReview ↗

Response to Reviewer LWTG (2/2): factorial and within-dataset results, and where each result is in the revision

Q2, factorial check (Table 2b). Own−swapped recall of beyond-prefix locations on NYC / TKY, three seeds. All pathways share hyperparameters and pass checks of condition use and convergence. In latent-cat, a categorical head on the denoiser's state replaces the autoencoder's decoder as the readout, while diffusion still runs in the compressed latent and each step's prediction is re-encoded by the frozen encoder.

Main splitPoint readoutCategorical readout
Learned latent.042 / .002.562 / .467
Native embedding.014 / .001.489 / .301
Native tokens, absorbing–.631 / .596
Forecasting settingPoint readoutCategorical readout
Learned latent.000 / −.001.030 / .023
Native embedding.003 / .001.030 / .021
Native tokens, absorbing (NADI)–.020 / .023

Absorbing corruption adds beyond-prefix identity on the main split (.631 / .596 against .489 / .301 for native embeddings) but none in the forecasting setting (.020 / .023 against .030 / .021).

Q1, within-dataset test (Table 29). Gain of a categorical over a point readout in the recall of beyond-prefix targets under the user's own history, forecasting setting, three seeds:

HKNYCTKYYJ
Users2,8538071,7352,998
Share, lowest → highest user quintile.23 → .98.04 → .49.06 → .50.32 → .70
Gain, lowest → highest user quintile+.014 → +.030+.006 → +.069+.009 → +.047+.027 → +.044
Spearman across users [95% CI]+.14 [.09, .18]+.52 [.46, .57]+.42 [.38, .46]+.24 [.20, .27]

In an OLS regression that controls for activity and history size, the coefficient of the share is +.041 to +.096, with intervals excluding zero. The gain comes mostly from revisits, the beyond-prefix places the user visited during the training period. On TKY, recall of revisits is .106 with a categorical readout against .029 with a point readout, while first visits are recovered by neither (.010 and .005, Table 28).

Where the other results are in the revised PDF.

  • Q2: the linear probe on latent-point's denoiser states, Appendix E.2. On NYC the states contain the beyond-prefix identity (top-1 .33–.36 across seeds) that the point readout loses (.04). On TKY the regression-trained denoiser barely forms it (.01–.05).
  • Q2: the VQ code audit over three checkpoints (Appendix E.3, Table 18) and the per-location codebook (Appendix L).
  • Q2: the readout contrast in the forecasting setting, Section 4.6 and Appendix I.1 (Tables 27 and 28).
  • Q1: the dataset properties and the checklist, Appendix M (Table 34). The Limitations now state that the history share predicts the gain within each dataset but is only descriptive across datasets.
  • Changes requested by the other reviewers, such as the split overlap and simple baselines, are in our response to Reviewer GmoT.

Thank you for the additional experiments. They address our concern about the CONT+AE model. With the same continuous latent representation, directly predicting location categories helps the model use a user’s history to recover more of the target locations that were absent from the seven-day prefix. This shows that compression alone cannot explain the original model’s low recall.

For discrete codes, the HK result is informative. Once the codebook assigns distinct codes to nearly all stations, VQ performs about as well as NADI. Prior work on generative retrieval has already shown that when an encoder assigns the same code to different entities, the model has difficulty distinguishing those entities from the code alone. We therefore see the main contribution of this experiment as quantifying the impact of code collisions on mobility generation.

For continuous representations, the new analysis helps explain which users within a dataset benefit most from directly predicting location categories. Our remaining concern is how to tell, on a new dataset, when removing compression is worthwhile and when changing the readout is enough. We therefore maintain our rating of 2 (Weak Reject).

AuthorsOpenReview ↗

Response to Reviewer LWTG: code collisions, and when to remove compression or change the readout

We thank the reviewer for the follow-up and agree with both readings. In this round, we updated the revised PDF in the following places. Appendix E.3 relates the VQ audit to code collisions in generative retrieval. A new Table 29b compares native embeddings with the learned latent, both read out categorically, user by user in leak-free forecasting, on all four datasets over three seeds. Appendix M now ends with a procedure for a new dataset, and the Conclusion states its core.

Code collisions. The effect of collisions is indeed known from generative retrieval, where items that share an identifier cannot be told apart from it alone. This is why TIGER (Rajput et al., 2023, cited in Section 1) appends an extra token to colliding semantic IDs. Appendix E.3 now presents the VQ experiment as quantifying collisions in mobility generation. Two observations go beyond the known effect. First, collisions persist on a large vocabulary even when the codebook has as many codes as locations. On TKY, training collapses to 3,076 codes in use, 93.6% of the locations seen in training share a code, and doubling the codebook does not help. The collisions are therefore not only a consequence of too few codes. Second, they fall on the entities that carry identity. On the three large vocabularies, 97.5–99.8% of visits to highly user-specific locations share a code whose majority label is another location (Table 18).

When to remove compression and when to change the readout. We summarize the procedure of Appendix M in four steps. Step 1 needs no model and Step 2 only the trained encoder, so in a two-stage pipeline both precede the generator. Step 3 sets the default generator, and Step 4 costs one additional training run.

Step 1: before any training, estimate how much the choice can matter. Two quantities computed from the data indicate how much beyond-prefix identity, that is, real future locations absent from the 7-day prefix, any pathway can draw from the history. One is the history share, the fraction of a user's beyond-prefix targets that the user visited during the training period. The other is the Recall@10 of a reference that samples popular locations by hour. When this reference is already high, as on HK (.951, Table 34), no pathway recovers beyond-prefix identity in forecasting (Table 27), so the choice can rest on other criteria.

Step 2: check whether the code is one-to-one on the entities that matter. If it is not, changing the readout cannot help, because a categorical head cannot separate locations that share a code. Compression should then be removed or replaced by a one-to-one code. In our data, a continuous per-visit latent serves on every vocabulary, whereas a per-location codebook serves only on a small one. The original VQ fails this check, and its own−swapped recall of beyond-prefix locations, the recall under the user's own history minus that under another user's, is at most .011 on every dataset (Table 2a). Once a per-location codebook makes the HK code nearly one-to-one (6.2% of stations share a code), VQ matches NADI.

Step 3: if the code is one-to-one, change the readout first. The continuous latent passes Step 2, and its autoencoder reconstructs 98.9–100% of visits to locations that are rare for the user (Table 17). A categorical readout in this latent matches native embeddings within .01 or exceeds them in five of the six comparisons where any beyond-prefix identity is recovered. These are the within-period setting, where test futures lie in the training period, on NYC (.562 against .571), TKY (.467 against .380) and YJ (.108 against .087, Table 2a), and forecasting on NYC (.030 against .030) and TKY (.023 against .021, Table 27).

Step 4: when the history share is high, confirm with one paired run. One trains the native pathway with the latent pathway's settings and removes compression only if it recovers more beyond-prefix identity, with seed ranges that do not overlap. Forecasting on YJ is the one case where this holds (.078–.089 against .026–.036, Table 27). The gain comes almost entirely from revisits to locations in the user's training history (+.160 against +.052), and Table 29b shows that it grows with the history share, from .033 to .088 across user quintiles (Table 29b, Spearman +.41, 95% CI +.37 to +.44), and the trend holds after controlling for activity and history size. On NYC and TKY the two pathways stay within .002 in every quintile, so the learned latent can be kept. Neither reconstruction, which is best on YJ (.998 for rare visits), nor the history share, which indicates how much the choice can matter, shows in advance whether the pathways differ, so the paired run remains the test.

Reviewer_GmoTOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper asks why some generative models fail when the output must be exact items, such as a specific user's specific locations. The test task: given one week of a user's past trips, generate their next week of trips. The paper argues that compressing locations into learned codes, either discrete codes (VQ) or continuous latents from an autoencoder, loses the user's identity. It builds a "ladder" of three models: diffusion on autoencoder latents, then diffusion directly on location embeddings, then masked diffusion directly on location tokens. It uses several probes, including swapping in another user's history to see whether the output changes. It concludes that VQ mixes up locations before diffusion even starts, while the autoencoder rebuilds locations well but ignores the user's history during generation. The final model, NADI (masked diffusion on raw tokens), gets the best overall score on four datasets.

Critical strengths

S1. A careful diagnostic design. Comparing the same model with the correct user's history vs a swapped history, on the same noisy input, is a clean way to test whether a model uses its input. The capacity sweep (making the autoencoder latent as large as the model) is a good control.

S2. Consistent results. NADI gets the best overall score on all four quite different datasets, with three training seeds for the main comparison (Table 7).

Critical weaknesses

W1. The key baseline ignores its input, so it may simply be broken. When the autoencoder model gets another user's history, its Recall@10 barely changes (−0.001, +0.004, +0.011, −0.000; Table 3), and it can identify the correct user only at chance level (about 34–50%; Table 16). A conditional model whose output doesn't depend on its condition suggests a training or design problem in this implementation. It is not proof that "continuous compression loses identity." Only one autoencoder design and one conditioning method are tested, with no attempt at stronger conditioning. The paper's main explanation is drawn from this one model.

W2. The "identity" metric can be scored without identity. On the HK dataset, the autoencoder model gets Recall@10 = 0.58 (Table 2) even though it ignores whose history it gets (Table 3). So that score can be reached from popular locations alone. Recall@10 also just checks whether the user's top-10 past places appear anywhere in the generated week, which rewards copying the past. There are no simple baselines such as "repeat last week," "sample the user's past places" or a per-user Markov model, so we can't tell how much of NADI's win is just copying.

W3. Each ladder step changes more than one thing. The step "remove compression" also swaps a separate encoder/decoder for direct embeddings and likely changes the loss and output layer. Saying 48–99% of the gain comes from "removing compression" mixes several changes together.

W4. The VQ test is set up to fail. VQ maps a whole (location, time, boundary) triple to one code, with only 256–4,096 codes for 32,000–49,000 locations. Mix-ups are then guaranteed simply because there are fewer codes than locations. This doesn't show that VQ in general fails.

W5. The data split may leak, and the wins shrink on stricter splits.

  • The main split uses the same time period and the same users for training and testing, and "does not require all test windows to occur strictly after all training windows" (Appendix C.2). Test weeks may overlap with training data.
  • On a strict time-based split (Appendix I), TransVAE beats NADI on NYC (0.786 vs 0.776).
  • On new users (Appendix J), DiffTraj beats NADI on YJ (0.866 vs 0.816).
  • All models are also told the exact length of the future and the weekday labels, which makes the task easier than real forecasting.
Questions for authors
  1. What scores do simple baselines get: popular locations, sampling the user's past places, repeating last week, and a per-user Markov model?
  2. Can the autoencoder model's problem be fixed with stronger conditioning (for example classifier-free guidance or conditioning the autoencoder on the history)? If so, isn't the issue conditioning rather than compression?
  3. In the main split, can a test week's days appear in training data for the same user? How often? What are the results with strictly non-overlapping windows?
  4. Does VQ still mix up locations if location gets its own code and the codebook is at least as large as the number of locations?
  5. Can you report seed variance for the probe results?
2 comments
AuthorsOpenReview ↗

Response to Reviewer GmoT (1/2): conditioning or compression, simple baselines, the ladder, VQ codebooks, and data leakage

We thank the reviewer for a careful review and for concrete tests. We agree with W1, W2, W3 and W5, and with W4 that the original VQ setting guaranteed aliasing.

W1 and Q2. Conditioning or compression? For the original CONT+AE it is conditioning. Under a history swap even its time-of-day profile barely changes, and only 34–51% of its windows follow the source user's visitation profile, where 50% means ignoring the history. We remove it from the evidence for compression loss. The repaired latent model, latent-point, diffuses in a frozen, standardized per-visit autoencoder latent with the native Gaussian denoiser and conditioning path. It uses the history, since 97–100% of its windows follow the source user (Table 3), and its autoencoder reconstructs 99.4–100% of visits (Table 17). It still loses beyond-prefix locations, the real future locations absent from the 7-day prefix. Their own−swapped recall, the recall under the user's own history minus that under another user's, is .054 on NYC and .000 on TKY, against .562 and .467 when a categorical head on the same latent replaces the point readout (Table 2a). Classifier-free guidance does not remove the loss, which appears with and without guidance (W3). Because latent-point already uses the history, we did not also condition its autoencoder on it. With conditioning fixed, the loss lies in the point readout, and W3 shows the same loss in native embeddings.

W2 and Q1. Simple baselines and identity metrics. We agree. Recall@10 and the composite reward copying the prefix week, which we now state as a limitation (Section 5). In the forecasting setting of W5, repeating the prefix week and the prefix Markov chain exceed all generative models in composite on all four datasets (Table 26). Both replay the input week's real timing and draw locations only from it, so they cannot generate any location outside the 7-day prefix. Their scores show what replaying the input earns, not learned user behavior, so we report them for calibration only. Identity claims therefore rest only on paired own−swapped measures, under which copying earns nothing beyond the prefix. NADI's highest-composite claim is restricted to learned baselines on the main split.

W3. Each ladder step changes more than one thing. We agree. The first step changed conditioning, state space and output parameterization at once, so we withdraw the 48–99% figure and remove the ladder. A controlled diagnostic path now changes one component per step, and a factorial check crosses state space with readout under shared hyperparameters and without guidance (Section 3, Table 2). The readout is the deciding factor. On NYC / TKY, own−swapped recall of beyond-prefix locations is .042 / .002 with a point readout and .562 / .467 with a categorical readout in the learned latent, and .014 / .001 against .489 / .301 in native embeddings (Table 2b, three seeds).

W4 and Q4. VQ with one code per location. VQ still aliases on a large vocabulary but not on a small one. With K = |V| or 2|V|, EMA updates and dead-code reset (three seeds, Appendix L), the HK codebook is nearly one-to-one (6.2% of locations share a code) and VQ then matches NADI (OBJ / Recall@10 .952 / .774 against .956 / .78). On TKY training collapses to 3,076 codes, and 93.6% of the locations seen in training share a code. Doubling K leaves 3,015 codes in use, and Recall@10 falls to .445 against .84 for NADI. We therefore narrow the VQ claim to learned codebooks on large vocabularies.

W5 and Q3. Overlap, strict splits, and the given length and weekdays. Yes. In 99.4–99.9% of main-split test windows, all seven future days are training targets of the same user (Appendix C.2). We therefore present it as a within-period setting, which tests retrieval of identity seen in training, and keep it for the diagnosis because every pathway can retrieve that identity and the swap comparison needs fixed output positions. For leak-free evidence we add a forecasting setting on the strict split of Appendix I, without the given length and weekdays (Section 4.6). There every pathway still uses the history (85–100% of windows follow the source user), and beyond-prefix own−swapped recall is at most .003 for point readouts but .020–.085 for categorical readouts on NYC, TKY and YJ, with non-overlapping seed ranges (Table 27). On YJ, native embeddings keep more of it than the learned latent (.085 against .031). As the reviewer notes, NADI's lead does not survive this setting. It is not the strongest learned model on any dataset (Table 26), and absorbing corruption adds no beyond-prefix identity. We therefore withdraw the masking increment of the original paper and restrict the masking claim to retrieval of identity seen in training.

Q5. Seed variance. Tables 22 and 27 now report seed ranges over three seeds for the paired probes. On NYC, TKY and YJ the ranges of point and categorical readouts do not overlap in either setting.

AuthorsOpenReview ↗

Response to Reviewer GmoT (2/2): baseline scores, seed ranges, and where each result is in the revision

W2 and Q1. Requested baselines, OBJ / Recall@10. We reproduced all four requested baselines and built the two history-based ones from the 7-day prefix and from the user's whole training history. All six copy the prefix week's arrival times and differ only in how they choose locations. Sampling prefix places, repeating last week and the prefix Markov chain use exactly the models' input, the 7-day prefix. The popular-location baseline uses the training population's hourly statistics. The training-history baselines read the user's whole training history, which in the main split contains the test days. As the reviewer suspected, on HK popular locations alone reach Recall@10 = .884 on the main split.

Main split:

HKNYCTKYYJ
Same-hour popular locations.905 / .884.799 / .037.811 / .117.825 / .107
Sample prefix places.942 / .838.874 / .561.879 / .610.943 / .973
Repeat last week.939 / .803.860 / .526.861 / .549.943 / .973
Prefix Markov chain.940 / .818.874 / .565.879 / .606.943 / .970
Sample training-history places.950 / .923.903 / .729.907 / .761.949 / .993
Training-history Markov.946 / .881.905 / .737.907 / .762.948 / .988
NADI (Table 1).953 / .776.921 / .870.926 / .846.924 / .900

On the main split the prefix Markov chain exceeds every learned baseline of Table 1 except NADI in composite and exceeds NADI on YJ.

Forecasting setting, where the baselines also reuse the prefix week's day boundaries and NADI is the mean of three seeds:

HKNYCTKYYJ
Same-hour popular locations.936 / .951.782 / .037.801 / .119.814 / .148
Sample prefix places.967 / .834.881 / .489.890 / .534.935 / .974
Repeat last week.968 / .845.886 / .526.897 / .573.936 / .979
Prefix Markov chain.967 / .830.881 / .491.890 / .534.934 / .972
Sample training-history places.967 / .853.846 / .450.859 / .506.921 / .963
Training-history Markov.965 / .830.849 / .452.861 / .504.923 / .955
NADI.872 / .601.717 / .202.766 / .296.795 / .793

The revised appendix reports only two of the six, repeat last week and the prefix Markov chain, in the forecasting setting (Table 26). Table 34 adds the forecasting Recall@10 of the popular-location baseline, and the other values appear here only.

All six are non-learned replays of real data, and their scores show how much our metrics reward replaying real visits. We therefore use them only to check our metrics. A high score here does not indicate learned mobility behavior.

Q5. Pathways of the submitted paper. Range of own−swapped Recall@10 over three seeds on the main split, on the first 4,000 test windows (all 3,518 on NYC), so values on HK, TKY and YJ differ from the submitted Table 3:

HKNYCTKYYJ
CONT+AE−.002 to +.002+.001 to +.004−.001 to +.002.000 to +.001
GAUSS.411 to .419.770 to .782.504 to .509.506 to .599
NADI.545 to .551.817 to .852.734 to .742.648 to .714

The bootstrap 95% interval of this difference contains zero in 11 of 12 CONT+AE runs, which follow the source user in 34–51% of windows, against 99–100% for GAUSS and NADI. The NADI row is part of Table 22, and the CONT+AE and GAUSS rows are reported here only.

Where the other results are in the revised PDF.

  • W1 and Q2: the history-swap test of condition use (Section 4.1, Table 3), the repaired latent model and the other pathways (Appendix E.1), and autoencoder reconstruction (Table 17).
  • W3: the controlled path and its factorial check (Section 3, Table 2) and the fixed settings of every pathway (Appendix C.4, Table 7). Appendix E.1 also relates the two readouts to diffusion for text (Diffusion-LM, CDCD).
  • W4 and Q4: the VQ code audit over three checkpoints (Appendix E.3, Table 18) and the per-location codebook (Appendix L). Even in the original VQ setting the codes keep more information about arrival time than about location, and on the three large vocabularies 97.5–99.8% of visits to highly user-specific locations share a code whose majority label is another location. The aliasing therefore goes beyond the mix-ups that fewer codes than locations would force.
  • W5 and Q3: the overlap count and the reason for the within-period setting (Appendix C.2), and the forecasting setting (Section 4.6, Appendix I.1) with performance (Table 26), the history swap and its seed ranges (Table 27) and the sources of generated visits (Table 28). On new users, NADI reaches .816 on YJ and .811 with DiffTraj's coordinate input, against .866 for DiffTraj (Appendix J). The gap therefore reflects the coordinate representation rather than missing spatial input, which the Limitations state.
  • Q5: seed ranges on the main split (Table 22) and in the forecasting setting (Table 27).
Reviewer_4G94OpenReview ↗
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3
Confidence
1
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies when learned compression is a poor choice for conditional generation whose outputs are exact categories, so that a plausible substitute still counts as an error. The testbed is personalized multi-day mobility generation: given a user's previous seven behavioral days, a model generates the following visits, each a tuple of location, arrival-time bin and day-boundary flag, with the number of visits and their day-of-week labels supplied. Location vocabularies range from 91 metro stations (HK) to about 49K venues (TKY). To locate where identity is lost, the authors build a sequential ladder that changes one factor at a time, from Gaussian diffusion in an autoencoder latent, to Gaussian diffusion on native token embeddings, to absorbing-mask diffusion on native tokens, with VQ and coordinate-based models as side controls.

The ladder is combined with clean reconstruction and VQ code-purity audits, latent-width and codebook-size sweeps, a prefix-swap test, and a probe that measures, at each corruption level, how much the matched user history raises the probability of the reference location over a swapped history. On the three large vocabularies, VQ aliases locations before diffusion (code-only decoding accuracy of 6–18%), while the continuous autoencoder reconstructs 97.6–99.9% of locations when clean but reaches Recall@10 of only 0.01–0.07 after generation and barely reacts to a swapped history. Removing the autoencoder accounts for 48–99% of the composite improvement, and masking adds gains concentrated on rare locations. The MASK endpoint, NADI, is a MaskGIT-style masked diffusion transformer with cross-attention to the encoded history, and it has the highest composite score on all four datasets.

Critical strengths
  • The problem is well posed and the failure it targets is real. Separating structural fidelity from exact identity is a useful framing, and Figure 2 and Table 1 make the point concretely. Traveller, a latent diffusion model, keeps Recall@10 of 0.448 on the 91-station HK data but drops to 0.004–0.010 on the large vocabularies, and DiffTraj stays competitive on aggregate statistics while reaching only 0.141 on NYC and 0.077 on TKY. Aggregate realism metrics would not reveal this. The broader question of whether to generate in a learned latent or in native space, and with which corruption, is also active in image and video generation which I worked on, so a careful study of it for categorical outputs is of interest beyond mobility.

  • The evaluation is broad and the paper is open about its limits. It covers four datasets with different modalities and vocabulary sizes, and reports all component metrics behind the composite. It adds horizon generalization from one to fourteen days, where NADI has the best composite in all sixteen cells, as well as a chronological split, held-out users, stability under re-weighting of the composite and six standard mobility statistics. The limitations section states plainly that the ladder is sequential rather than factorial, that several probes use a single checkpoint, that the future length is supplied, and that DiffTraj is better on held-out YJ users.

Critical weaknesses
  • The conclusion about Gaussian corruption depends on the CONT+AE and GAUSS pathways being reasonable implementations, and the paper gives too little detail to judge this. I could not find the noise schedule, the parameterization, the number of sampling steps, how latents or embeddings are scaled, how continuous outputs are mapped back to locations, or the KL weight of the autoencoder. Appendix C.4 says tuning covered capacity, depth and learning rate, which leaves out the settings that matter most for Gaussian diffusion on embeddings of categorical data. Work on continuous diffusion for text, such as Diffusion-LM, CDCD and Plaid, found that these models need specific choices (x0-prediction with rounding, embedding normalization, adapted noise schedules) to be competitive, and this line of work is neither cited nor discussed. Without these details and a stronger GAUSS baseline, the GAUSS to MASK gains may reflect this implementation rather than the corruption type.

  • It is not clear that the CONT+AE result concerns identity rather than a general conditioning failure of that model. Swapping the history barely changes its Recall@10, and its outputs are about equally close to the target and source users, which suggests the latent model mostly ignores its condition. The paper says its controls rule out generic conditioning failure, but the swap test only looks at locations. Does the swap change any non-identity output of CONT+AE, such as the per-user time profile? If not, the simpler reading is that this conditional latent model does not use its condition at all. The latent-width sweep addresses capacity, but not the factors pointed to by the diffusability work the paper cites, such as latent regularization and normalization.

Questions for authors

See above. I work on image and video generation and am not familiar with the mobility generation literature, so my assessment focuses on the generative modeling and diagnostic claims, and I defer to other reviewers on the choice of mobility baselines and metrics.

2 comments
AuthorsOpenReview ↗

Response to Reviewer 4G94 (1/2): implementation settings, a stronger GAUSS, CONT+AE conditioning, and the ethics flag

We thank the reviewer for pointing to the two places where our evidence was weakest. Both concerns are correct. The second comment gives the supporting tables and their place in the revised PDF.

W1. Are CONT+AE and GAUSS reasonable implementations?

Settings. Appendix C.4 (Table 7) now reports them, and the table below adds the submitted CONT+AE and GAUSS. The last column is the controlled path that replaces the ladder, and its factorial check (Table 2b) uses the same settings for all pathways. Schedules, parameterizations and step counts were fixed by design, and the search covered only width, depth and learning rate, as the reviewer notes. NADI and the absorbing pathway use a 12-step MaskGIT-style sampler.

CONT+AEGAUSSControlled path
Noise schedulecosine, T = 200cosine, T = 100cosine, T = 100
Parameterizationε-prediction, MSE, trained jointly with the autoencoderx0-prediction, cross-entropy heads (location, time bin, day boundary)x0-prediction. Point: MSE (native-point adds Diffusion-LM's rounding loss). Categorical: cross-entropy
SamplingDDPM, 200 steps50 steps, η = 150 steps, η = 1, no guidance
Scalingnonenonelatent standardized to unit variance, embeddings L2-normalized and scaled to √d
Back to locationsdecoder, argmaxargmax at every step, re-embeddeddecoded to tokens and re-embedded at every step
KL weightnone (deterministic autoencoder)–none, and the latent pathways train the autoencoder first and then freeze it
Tunedlatent width, depth, learning ratewidth, depth, learning rateGAUSS's selected values, shared

A stronger GAUSS. We now cite and discuss Diffusion-LM, CDCD, Plaid and related work (Appendix E.1). GAUSS already used x0-prediction with cross-entropy heads and re-embedded the argmax at every step, but it did not normalize its embeddings. L2-normalizing them and scaling them to √d (native-cat), with everything else unchanged, closes 44%, 63% and 71% of the GAUSS-to-MASK OBJ gap on HK, TKY and YJ, and on NYC native-cat is above MASK. GAUSS+, which adds score interpolation and self-conditioning, stays within .02 of native-cat in OBJ (Appendix E.5, Table 20, three seeds). We did not adapt the noise schedule, which the Limitations state. Much of the masking increment in the submitted Table 2 therefore reflected the GAUSS implementation, as the reviewer suspected.

What remains of the corruption effect. Beyond-prefix locations are the user's future locations absent from the 7-day prefix. In the factorial check, absorbing corruption still raises their own−swapped recall, the recall under the user's own history minus that under another user's, on the main split (NYC .631 against .489, TKY .596 against .301). The main split's test futures lie within the training period, and in a leak-free forecasting setting absorbing corruption adds none. We therefore restrict the masking claim to better retrieval of identity seen in training.

W2. Does CONT+AE use its condition at all? No. The simpler reading is correct. Under a history swap its time-of-day profile barely moves (own − swapped −.001 to +.013 across the four datasets, against +.078 to +.372 for NADI), and only 34–51% of its windows follow the source user's visitation profile, where 50% means ignoring the history. We withdraw the statement that our controls rule out generic conditioning failure, and CONT+AE is no longer evidence that compression loses identity.

The repaired latent model, latent-point, keeps learned compression with a frozen per-visit autoencoder whose latent is standardized to unit variance, with no KL term, and uses GAUSS's denoiser and conditioning path. It uses the history, since 97–100% of its windows follow the source user and its time profile changes by .08–.36 under a swap (Table 3). Yet it recovers almost none of the beyond-prefix locations, whereas a categorical readout on the same latent recovers them and a point readout on native embeddings loses them too (Table 2b and second comment). The loss is therefore tied to the point readout, not to a conditioning failure. Latent normalization does not remove it, since latent-point's latent is standardized, and we state latent regularization as untested.

Ethics flag. The review gives no reason, so we summarize the relevant facts and would be glad to address a specific concern. The NYC and TKY Foursquare data and YJMob100K are public research datasets, and the HK smart-card data are used under a data-use agreement. "Identity" in the paper means the exact location class a model must generate, the object of our diagnosis rather than of a privacy attack on who a user is. The revision adds a memorization audit (Appendix I.1, Table 30, summarized in the second comment). Its Ethics Statement now covers dual use and a release policy under which nothing derived from the HK data is released.

AuthorsOpenReview ↗

Response to Reviewer 4G94 (2/2): normalization and factorial results, and where each result is in the revision

W1, normalization (Table 20). OBJ / Recall@10 on the main split over three seeds, with GAUSS and MASK as in the submitted Table 2. The OBJ seed range of native-cat is at most .012 except on NYC (.888–.925).

HKNYCTKYYJ
GAUSS.916 / .63.895 / .80.840 / .63.750 / .82
native-cat.933 / .68.910 / .86.893 / .75.884 / .91
GAUSS+.934 / .67.921 / .84.893 / .74.902 / .94
MASK (NADI).956 / .78.897 / .83.924 / .84.938 / .93

In the forecasting setting, where native-cat and NADI were both retrained, neither is consistently higher in OBJ (Table 26). They are within .002 on HK, native-cat is higher on NYC (.776 against .717), and NADI is higher on TKY and YJ (.766 against .748 and .795 against .769).

W1, factorial check (Table 2b). Own−swapped recall of beyond-prefix locations on NYC / TKY, three seeds. As in Diffusion-LM, native-point uses MSE on the clean embedding, the rounding loss and rounding at every step. The categorical pathways are trained with cross-entropy, as in CDCD and Plaid. In latent-cat, a categorical head on the denoiser's state replaces the autoencoder's decoder as the readout, while diffusion still runs in the compressed latent and each step's prediction is re-encoded by the frozen encoder.

Main splitPoint readoutCategorical readout
Learned latent.042 / .002.562 / .467
Native embedding.014 / .001.489 / .301
Native tokens, absorbing–.631 / .596
Forecasting settingPoint readoutCategorical readout
Learned latent.000 / −.001.030 / .023
Native embedding.003 / .001.030 / .021
Native tokens, absorbing (NADI)–.020 / .023

Both point-readout pathways use the condition. They follow the source user in at least 94% of windows, and their own−swapped recall of prefix locations is .49–.72 on the main split. Sampler choices do not change the loss. Without per-step rounding and with guidance scale 2 (seeds 1–2), native-point follows the source user more often (TKY 99% instead of 95%), but its beyond-prefix recall on the main split changes by at most .001. The point-readout pathways use the shared hyperparameters without a regression-specific search, and the Limitations state the untuned point readouts and noise schedule.

Where the other results are in the revised PDF.

  • W1: continuous diffusion for text (Diffusion-LM, CDCD, Plaid, self-conditioning, LD4LG, MDLM) and the definitions of the pathways, Appendix E.1.
  • W2: a linear probe on latent-point's denoiser states, Appendix E.2. On NYC the states contain the beyond-prefix identity (top-1 .33–.36 across seeds) that the point readout loses (.04), whereas on TKY the regression-trained denoiser barely forms it (.01–.05).
  • W2: latent regularization. latent-point's latent is standardized, and widening it to d_z = 256 leaves beyond-prefix recall below .01 (Appendix E.4). KL and other diffusability regularizers remain untested, which the Limitations state.
  • W2: in the forecasting setting, latent-point follows the source user in 98–100% of windows and recovers none of the beyond-prefix locations (Table 27).
  • Ethics flag: the memorization audit, Appendix I.1 (Table 30). In the forecasting setting, the share of NADI's generated days identical to one of the user's training days is .713 / .025 / .074 / .004 on HK / NYC / TKY / YJ, against .659 / .096 / .119 / .006 for the real future. It is higher only on HK, where NADI largely repeats the prefix week.

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

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