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Under review as a conference paper at ICLR 2027

Time versus Space: A Systematic Empirical Study of Information Allocation in Large-Scale Traffic Forecasting

Abstract

Spatio-temporal traffic forecasting has largely focused on increasingly sophisticated graph-based models, implicitly assuming that spatial information is the primary source of predictive power. We revisit this assumption by asking a fundamental question: given a fixed observation budget, is forecasting accuracy improved more by allocating observations to temporal depth or spatial breadth? We answer this through a systematic empirical study of this trade-off in large-scale traffic forecasting, showing that predictive performance is determined primarily by whether the input covers one complete daily cycle of the target sensor, while additional spatial information provides only marginal benefit. We further explain this finding by showing that, under typical benchmark resolutions, congestion propagation between neighbouring sensors is faster than the observation interval, leaving little exploitable lead–lag information for graph-based models. On a high-resolution freeway corridor where propagation is resolved, physically relevant neighbourhoods instead become indispensable as traffic approaches capacity. These insights naturally lead to a simple graph-free temporal-only forecasting recipe that combines long-context temporal modelling with lightweight adaptive gating for atypical conditions, achieving state-of-the-art average accuracy on all four LargeST subsets. The principle is established with a lightweight model trained from scratch and transfers to an off-the-shelf pretrained time-series foundation model with only lightweight adaptation. Our findings indicate that predictive information is far more effectively captured through temporal depth than additional spatial observations, providing a new perspective on how spatio-temporal models should allocate their capacity.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Traffic Forecasting, Spatio-Temporal Prediction, Empirical Analysis

Reviews

Among:
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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_W53eOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper asks whether traffic forecasting benefits more from a longer history of the target sensor ("temporal depth") or from the recent history of more sensors ("spatial breadth"). On the four LargeST subsets with traffic flow at 15-minute intervals, it measures the forecasting error over a grid of history lengths TT and neighbour counts NN using ridge regression and a small MLP-Mixer. It reports that the largest gain comes when the history covers one full day, that neighbours do not help as much, and that congestion usually reaches adjacent sensors within one 15-minute interval. On a freeway corridor with 30-second speed data from FT-AED, nearby sensors do help when traffic is "near capacity". Finally, the paper proposes a model without spatial input, based on an adapted TimesFM with a historical-average prior and a gate for atypical traffic, which reaches the lowest average MAE on all four LargeST subsets.

Critical strengths

1. The paper studies where the accuracy of traffic forecasts comes from, instead of proposing another model. Most traffic forecasting models are graph-based and assume that data from other sensors is the main source of accuracy. The paper checks this assumption directly. Such studies are rare, and their results show where model developers should spend their effort, which is more useful than a small gain on a benchmark. Some results are surprising and useful: Table 2 shows that random sensors recover most of the gain of the nearest ones, and Figure 2 makes the trade-off between history length and the number of neighbours easy to see.

2. The analysis is careful, and the paper states its limitations openly. It uses two models of different complexity (ridge regression and an MLP-Mixer), an ablation study that replaces the nearest sensors with random ones, and an analysis of the "lead–lag information" between adjacent sensors based on traffic-flow theory. It also reports the cases where other sensors do help, namely "sudden-onset events" and traffic "near capacity" when the data are recorded every 30 seconds. The weaknesses below concern how well the experiments support the main conclusion, and I would like to see this study improved and published.

Critical weaknesses

1. The evidence does not show that spatial information adds little once the history is long.

The central claim is that "once the target's history spans one daily cycle, additional spatial observations add little unique information" (lines 471-472). However, the paper's own experiments do not establish it:

  • The results of ridge regression contradict it. At T≥96T \geq 96, ridge regression still gains 0.5-0.9 MAE from neighbours (lines 248-251), which is comparable to the gain of the temporal-only recipe over Graph WaveNet on San Diego (0.75 MAE).
  • The MLP-Mixer gains almost nothing from neighbours at T≥96T \geq 96, but it becomes unstable with many neighbours (Appendix B.4), which the paper attributes to the "estimation and optimization cost" of many inputs (lines 891-892). Therefore, the lack of gain may be a limitation of this model and may not hold for the data.
  • No graph model is trained with a long history (lines 483-484), and the only baseline that reads one day of all sensors, RPMixer, outperforms the temporal-only recipe on San Diego (17.25 vs 17.43 MAE, Table 4). Moreover, SBATransformer [1] uses data from all sensors with a 96-step input and reports lower MAE than the paper's best model on all four subsets at every horizon (e.g., 15.92/17.69/19.77 vs 15.96/18.55/20.69 at horizons 3/6/12 on GBA). Its evaluation pipeline may differ, but the authors' research log in the supplementary material mentions this work and notes that comparing a 512-step recipe with 12-step graph models favours the recipe (FINDINGS.md:656-659). However, the paper mentions neither SBATransformer nor this unequal comparison.

As a result, the main comparison changes two factors at once: the recipe uses 512 steps and no spatial input, while the graph baselines use 12 steps and spatial input. At an equal history of 12 steps, the graph model wins (18.18 MAE for Graph WaveNet vs 21.20 for the 12-step MLP-Mixer, Table 16), and at an equal long history, which is what the central claim is about, no such comparison exists.

2. The conclusions rest on a single type of data.

All forecasting results use 15-minute traffic flow from LargeST, and the "nonlinear allocation plane" is measured only on San Diego (line 483). According to the paper's own explanation, whether other sensors help depends on how often the data are recorded: they help little at 15-minute intervals (LargeST), where congestion reaches the next sensor within one time step, but they do help at 30-second intervals (FT-AED). METR-LA and PEMS-BAY, the most common benchmarks, use 5-minute intervals, which lie between these two settings, but the paper leaves them for future work (Section 6). Without them, statements such as "predictive information is far more effectively captured through temporal depth than additional spatial observations" (lines 30-32) claim more than the experiments show.

Moreover, the abstract states that performance "is determined primarily by whether the input covers one complete daily cycle" (lines 18-20). Yet the recipe still improves by 0.80 MAE when its history grows from one day to 5.3 days (18.23 vs 17.43, Table 14). This is larger than the gain from adding the four nearest sensors in Table 2 (0.54 MAE) and ten times larger than the gain from attention over other sensors on top of the adapted TimesFM (at most 0.08 MAE, line 257).

3. Sections 4.3, 4.4 and 5 are hard to follow.

Unlike Sections 3-4.2, these sections put several analyses into long paragraphs, use terms defined only in the appendix, and read like an unedited draft. Section 4.3 mixes three different analyses, and its text does not match Figure 3. Table 3 cannot be understood without Appendix H. Section 5 reports its main results through many numbers in the text, uses the gate before introducing it, and leaves the MLP-Mixer, which the paper calls its main evidence, out of Table 4. I suggest splitting Section 4.3 into parts with one claim and one figure each, defining all terms of Table 3 in the main text, and building Section 5 around one table that includes the MLP-Mixer.

4. Some choices were made on the test set, and key results cannot be verified.

  • The forecasting recipe never uses the validation split. According to the authors' research log, all its numbers are test results (FINDINGS.md:24-25), including the sweep that selected the 512-step history (FINDINGS.md:101-115) and the decision to keep the calendar embeddings (FINDINGS.md:128-140). The paper does not disclose this.
  • The retrained Graph WaveNet and STID use early stopping on test windows (scripts/e1_baselines.py:166,226), although Appendix A.3 states that early stopping uses validation data.
  • The FT-AED study (Section 4.4, Appendix H), the only experiment where neighbours clearly help, has no code in the supplementary material.
  • Section 4.2 states that random sensors give the same benefit as the nearest ones "at every history length" (lines 265-266), but this ablation study was run only at T=48T = 48 and T=512T = 512 (scripts/modal_grid.py:64).

[1] Chen et al. "Towards Scalable and Structured Spatiotemporal Forecasting," 2025

Questions for authors
  1. How does a model that reads other sensors, such as Graph WaveNet or PatchSTG, perform when trained with 96 or 512 steps of history, and how does the recipe compare with SBATransformer under the same evaluation pipeline?
  2. Can at least the errors of ridge regression over the grid of history lengths and numbers of neighbours (the "allocation plane", Figure 2, left) and the analysis of the "lead–lag information" between adjacent sensors (Section 4.3) be repeated on METR-LA or PEMS-BAY? As an optional suggestion, the datasets from [2] seem to fit this study well: they cover city road networks with up to 100,000 road segments and real road connectivity, with speed and volume at 5-minute resolution. Since adjacent road segments in a city are close to each other, these data could show whether spatial input becomes useful when congestion takes longer than one time step to reach the next segment.

[2] Velikonivtsev et al. "Metropolis-Scale Road Network Datasets for Fine-Grained Urban Traffic Modeling," 2026

Reviewer_hD2SOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies input allocation for large-scale traffic forecasting: given a fixed observation budget, should a model use longer target-sensor histories or observations from more sensors? The authors compare temporal depth and spatial breadth using residual ridge regression and a patch mixer trained from scratch. Random-sensor controls, propagation-lag analyses, and high-resolution traffic experiments further examine when spatial inputs provide additional predictive value. In the tested LargeST settings, extending the target history to cover one daily cycle produces substantial gains. Additional spatial inputs offer comparatively limited improvements, particularly for the nonlinear probe. These observations motivate a graph-free forecasting recipe combining TimesFM adaptation, calendar features, a historical-average (HA) prior, and context gating. The gated model achieves the lowest average mean absolute error (MAE) on all four LargeST subsets in Table 4. The paper’s central contribution is its formulation and empirical investigation of the input-allocation problem.

Critical strengths
  1. Clear research question and informative experimental design. Placing temporal depth and spatial breadth within a common observation-budget framework provides a useful perspective on traffic forecasting. The combination of linear and nonlinear probes, together with nearest-neighbour and random-sensor controls, supports a broader analysis than a single-model performance comparison.
  2. Attention to both average performance and applicability boundaries. The paper examines aggregate errors while identifying sudden-onset events where spatial inputs remain useful. The FT-AED experiments further demonstrate that local neighbours cannot be readily replaced by distant or random sensors under high-resolution congested conditions. These findings help delineate the conditions under which temporal-only forecasting is appropriate.
  3. Clear connection between method design and failure analysis. Long histories, periodic priors, and context gating address temporal regularities, calendar structure, and HA-related failures, respectively. The analysis in Section 5.3 explains why HA improves average MAE while potentially increasing errors during atypical conditions.
  4. Potential practical value. Prioritizing daily-cycle coverage before assessing additional spatial inputs could inform the design of traffic forecasting systems. Results across four LargeST subsets, together with cross-sensor and cross-city transfer experiments, support further investigation of this approach .
Critical weaknesses
  1. Comparisons with matched temporal context and input features are missing. The main graph-based baselines in Table 4 use 12 historical steps, whereas the proposed recipe uses 512. Section 6 also acknowledges that long-input graph baselines were not evaluated. Consequently, the comparisons do not fully separate the effects of longer histories, HA, calendar features, and the removal of spatial modelling. Although PatchSTG and RPMixer are included, comparisons with a strong graph model and PatchTST/DLinear under matched history lengths and input features would strengthen the conclusions.
  2. Matching observation counts does not sufficiently control for model capacity and computational investment. Equal numbers of input scalars constrain input size but do not ensure comparable representational capacity, optimization difficulty, or computational cost. Section 3.1 explicitly distinguishes observation counts from computational costs. However, the temporal-only and graph-based models are not sufficiently matched in architecture, depth, training and inference floating-point operations (FLOPs), or training budget. Their performance differences therefore cannot be attributed directly to the relative contributions of temporal and spatial inputs. The complementary probes reduce some model-specific effects, but their findings remain conditional on the tested models and training settings. Capacity- or compute-matched comparisons, alongside training-time and network-wide inference measurements, would strengthen the interpretation.
  3. The equal-budget example does not clearly disclose the change in neighbour history length. The footnote in Section 3.1 and the setup in Section 4.1 specify 12 observations per neighbour, giving B = T + 12N. Section 4.1 subsequently describes 128 target-history steps plus three neighbours as a configuration with B = 512. Under the preceding definition, its budget would be 128 + 3 × 12 = 164. A budget of 512 requires each neighbour to contribute 128 steps. The main text should explicitly state this change and adjust the budget expression accordingly, so readers can interpret the comparison correctly.
  4. Some bibliographic details are inaccurate. RevIN is listed as an ICLR 2021 paper, whereas its formal conference publication is ICLR 2022. The reference entry and corresponding in-text citations should be corrected. The title of Cleveland et al.’s STL paper is also incomplete. Its full title is “STL: A Seasonal-Trend Decomposition Procedure Based on Loess”. Since the paper has four authors, “et al.” should not follow the complete author list. These are minor but directly correctable reference errors.
Questions for authors
  1. How do a strong graph model, PatchTST/DLinear, and the proposed mixer compare at history lengths of 12, 96, and 512? Please match HA, calendar features, and evaluation protocols. Does temporal depth retain its advantage under these conditions?
  2. Does the relative benefit of temporal and spatial inputs persist when model capacity or training compute is matched? Could the authors report training FLOPs, training time, inference memory, and network-wide prediction throughput?
  3. How many historical steps does each neighbour contribute in the B = 512 example in Section 4.1? Please clarify its relationship to the preceding definition B = T + 12N.
  4. Could the authors correct the bibliographic entries and corresponding in-text citations? Specifically, RevIN’s conference year should be ICLR 2022, and the STL reference should include its full title and remove “et al.” after the complete four-author list.
Reviewer_BJWJOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates whether a fixed observation budget should be allocated to temporal depth or spatial breadth in large-scale traffic forecasting. It finds that covering a complete daily cycle generally provides greater benefits than adding spatial observations. Based on these findings, the authors develop a temporal-only forecasting recipe combining long-context modeling, historical-average priors, and adaptive gating, evaluated using both a lightweight model and a pretrained time-series foundation model.

Critical strengths
  1. The research question is practically relevant. Examining the relative contributions of temporal and spatial information can inform the design of efficient traffic forecasting models.

  2. The analysis provides useful diagnostic insights. The investigation of sampling resolution, congestion propagation, and atypical events helps characterize when spatial information becomes useful.

  3. The temporal-only recipe achieves competitive accuracy. Its effectiveness across four LargeST subsets demonstrates the potential of simple models with appropriately chosen temporal context.

Critical weaknesses
  1. The fixed-budget setting is insufficiently justified. The paper does not provide concrete GPU resource measurements connecting its observation budget to practical computational constraints. Equal observation counts do not necessarily imply equal computational costs. It therefore remains unclear why an STGNN could not be used under the same GPU budget.

  2. The evaluation has limited dataset diversity. The main forecasting results cover four subsets of a single dataset, LargeST. Evaluation on additional benchmarks, particularly METR-LA and PEMS-BAY, is needed to assess the generality of the conclusions.

  3. The benefit of spatial modeling under matched long contexts remains unclear. The paper does not directly compare temporal-only models with spatial or graph-based models receiving the same long temporal history. Such comparisons are necessary to determine whether spatial modeling provides additional gains once sufficient temporal context is available.

  4. The novelty beyond prior work is unclear. SimST [1] and STID [2] have already challenged the necessity of GNNs for traffic forecasting. The paper should clarify what new insight or methodological contribution it provides beyond these findings and why its proposed recipe is necessary.

  5. The probes are too limited to support broad empirical conclusions. A systematic study should evaluate established models such as STID [2], PatchSTG [3], and Graph WaveNet [4] with T = 96 or 512, optionally incorporating historical-average priors. The authors' custom mixer-plus-neighbors probe and cross-sensor attention added to TimesFM [5], with gains of at most 0.08 MAE for the latter, provide insufficient evidence to generalize across spatial modeling approaches.

  6. The efficiency evaluation is incomplete. Despite emphasizing GPU memory constraints, the paper lacks a systematic comparison of peak GPU memory, training time, FLOPs, and space complexity. The reliance on a 48 GB GPU also requires clearer practical justification given higher-memory hardware such as the H200 with 141 GB. Comparisons with scalable spatial models, including SAGDFN [6], RAGC [7], and STGformer [8], are needed to establish the proposed approach's efficiency advantages.

References

[1] Xu Liu, Yuxuan Liang, Chao Huang, Hengchang Hu, Yushi Cao, Bryan Hooi, and Roger Zimmermann. Do We Really Need Graph Neural Networks for Traffic Forecasting? arXiv preprint arXiv:2301.12603, 2023. https://arxiv.org/abs/2301.12603

[2] Zezhi Shao, Zhao Zhang, Fei Wang, Wei Wei, and Yongjun Xu. Spatial-Temporal Identity: A Simple yet Effective Baseline for Multivariate Time Series Forecasting. CIKM, 2022. https://arxiv.org/abs/2208.05233

[3] Yuchen Fang, Yuxuan Liang, Bo Hui, Zezhi Shao, Liwei Deng, Xu Liu, Xinke Jiang, and Kai Zheng. Efficient Large-Scale Traffic Forecasting with Transformers: A Spatial Data Management Perspective. KDD, 2025. https://doi.org/10.1145/3690624.3709177

[4] Zonghan Wu, Shirui Pan, Guodong Long, Jing Jiang, and Chengqi Zhang. Graph WaveNet for Deep Spatial-Temporal Graph Modeling. IJCAI, 2019. https://doi.org/10.24963/ijcai.2019/264

[5] Abhimanyu Das, Weihao Kong, Rajat Sen, and Yichen Zhou. A Decoder-Only Foundation Model for Time-Series Forecasting. ICML, 2024. https://proceedings.mlr.press/v235/das24c.html

[6] Yue Jiang, Xiucheng Li, Yile Chen, Shuai Liu, Weilong Kong, Antonis F. Lentzakis, and Gao Cong. SAGDFN: A Scalable Adaptive Graph Diffusion Forecasting Network for Multivariate Time Series Forecasting. ICDE, 2024. https://arxiv.org/abs/2406.12282

[7] Kaiqi Wu, Weiyang Kong, Sen Zhang, Zitong Chen, and Yubao Liu. Efficient Traffic Forecasting on Large-Scale Road Network by Regularized Adaptive Graph Convolution. ICDE, 2026. https://arxiv.org/abs/2506.07179

[8] Hongjun Wang, Jiyuan Chen, Tong Pan, Zheng Dong, Lingyu Zhang, Renhe Jiang, and Xuan Song. STGformer: Efficient Spatiotemporal Graph Transformer for Traffic Forecasting. arXiv preprint arXiv:2410.00385, 2024. https://arxiv.org/abs/2410.00385

Questions for authors

NA

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