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Evaluating Generative Time-Series Models on Data with Point Masses
Jian Xu
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Abstract
Abstract:Many of the series that generative time-series models are benchmarked on place a large probability mass on a single value --- it does not rain, no ride is requested, no part is ordered. We report what happens when such data is evaluated carefully. First, the standard rolling-origin protocol can score a model on a window whose atom structure bears no resemblance to the dataset: on one benchmark the dataset is $42\%$ zeros and the evaluation windows are $13\%$, on another $47\%$ against $5\%$. This is not a cosmetic problem --- it reversed one of our own conclusions, turning the strongest occurrence model in our study into what looked like a cautionary tale. Second, we give a control in which CRPS is invariant \emph{by construction} while the temporal coupling is destroyed, which measures exactly how much that coupling contributes to a chosen statistic. Third, benchmarking seven models on a matched protocol over five seeds, an autoregressive hurdle beats a conditional flow on five of six datasets, by up to a factor of $153$, while the flow's own occurrence statistics vary by up to $62\%$ across training seeds and every baseline is deterministic. Finally, the model ordering is not the same under five different occurrence statistics, and the two that do not share a construction agree with each other least.
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- Source: https://arxiv.org/abs/2608.09692v1
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Evaluating Generative Time-Series Models on Data with Point Masses Jian Xu1,2 1RIKEN iTHEMS, Wako, Japan. 2RIKEN Center for Advanced Intelligence Project (AIP), Tokyo, Japan. E-mail: jian.xu@riken.jpPreprint, . This work has not been peer reviewed. Abstract Many of the series that generative time-series models are benchmarked on place a large probability mass on a single value — it does not rain, no ride is requested, no part is ordered. We report what happens when such data is evaluated carefully. First, the standard rolling-origin protocol can score a model on a window whose atom structure bears no resemblance to the dataset: on one benchmark the dataset is 42%42\% zeros and the evaluation windows are 13%13\%, on another 47%47\% against 5%5\%. This is not a cosmetic problem — it reversed one of our own conclusions, turning the strongest occurrence model in our study into what looked like a cautionary tale. Second, we give a control in which CRPS is invariant by construction while the temporal coupling is destroyed, which measures exactly how much that coupling contributes to a chosen statistic. Third, benchmarking seven models on a matched protocol over five seeds, an autoregressive hurdle beats a conditional flow on five of six datasets, by up to a factor of 153153, while the flow’s own occurrence statistics vary by up to 62%62\% across training seeds and every baseline is deterministic. Finally, the model ordering is not the same under five different occurrence statistics, and the two that do not share a construction agree with each other least. Index Terms: Generative models, time series analysis, performance evaluation, intermittent demand, flow matching. I Introduction A large share of the time series that generative models are trained and evaluated on take one particular value with positive probability. It does not rain on most days; no ride is requested in most hours; no spare part is ordered in most months; a solar panel produces nothing at night. In several of the datasets that the recent generative time-series literature reports on, between a quarter and nine tenths of all observations are exactly zero (Table I). The data law is a mixture: an atom at zero, and a continuous distribution over the positive part. The models are not built that way. Flow matching with data-dependent priors [9], residual-expert flows [30], stochastic flow matching [13], VQ-latent transport [11] and their diffusion predecessors [24, 26] all transport an absolutely continuous source distribution with a learned map. Under the regularity conditions ODE-based flow models are usually analysed with — a velocity field Lipschitz in the state and integrable in time, so that the time-11 flow map is a diffeomorphism — the pushforward of an absolutely continuous law is again absolutely continuous, and Prmodel(Yt=c)=0for every c∈ℝ. _model(Y_t=c)=0 every c . (1) Continuity of the map alone would not give this — a continuous map can collapse a set to a point — but invertibility does, and the model we study is an ODE-based flow [9] integrated with a fixed-step solver, so its sampler realises an invertible map by construction. Diffusion samplers reach the same place by a different route: the exact reverse-time limit can converge to a singular law, but the truncation at t=ϵ>0t=ε>0 and the finite step size used in practice leave the output continuous. A model is therefore being asked to reproduce, on more than half of the observations in some of these datasets, a feature it cannot represent. The scores used to judge it are marginal — CRPS per timestep, or a distributional distance computed on pooled windows — and are not obviously able to detect the difference between a genuine atom and a thin spike of continuous mass near zero. This paper began as a test of the hypothesis those two facts suggest: that continuous-state models are systematically handicapped on data with a point mass, and that an explicit occurrence process would fix it. Neither part survived contact with the experiments. Across six datasets the flow is ahead of every explicit occurrence model on one dataset only, and an autoregressive occurrence hurdle — a logistic classifier rolled out one step at a time — beats it on the other five, on rideshare by a factor of 153153. The empirical gap is real; what is not supported is that a continuous state is its cause, or that closing it requires a new generative model. What the experiments did produce is a set of problems with the measurement, and they are the contribution of this paper. We distinguish two kinds of statement throughout. The evaluation-level findings — what a protocol measures, what a marginal score can support — follow from the definitions and apply to any generative model scored this way. The model-level findings are empirical claims about one family of conditional flows on six datasets; we do not read them as properties of continuous-state generative modelling in general. • The evaluation window need not resemble the dataset. The standard rolling-origin protocol scores a model on the final H steps of each series. Where the atom process is non-stationary, those steps can be unrepresentative by a wide margin: covid_deaths is 42%42\% zeros as a dataset and 13%13\% in its evaluation windows, rideshare 47%47\% against 5%5\%. We show below that this inverted one of our own findings (Sec. IV-A). • A control under which CRPS cannot move. Permuting the sample index independently at each horizon step leaves every per-step predictive marginal — and therefore CRPS — unchanged by construction, while destroying the coupling that carries the occurrence statistics. It measures exactly how much the model’s trajectory coupling contributes to a chosen statistic (Sec. IV-B). • A benchmark over five seeds, and the model that wins it. An autoregressive occurrence hurdle beats the flow on five of six datasets, by up to 153×153×; the flow’s own occurrence statistics move by up to 62%62\% across training seeds while every baseline is deterministic; and the model ordering changes with the choice of occurrence statistic (Sec. V, Sec. V-A). Substituting the conventional semi-Markov occurrence process into the flow, however, makes the relevant statistic worse on five of six datasets: the occurrence model that works here is the autoregressive one, and which explicit process is substituted matters more than whether one is. I Related work I-A Generative models for time series Adversarial models [27, 7] were displaced by diffusion — autoregressive over the horizon [14], conditioned on the observed part [21], or decomposed into interpretable components [28] — and more recently by flow matching [12], which is now the default for probabilistic forecasting and unconditional generation of time series. Work in this line has concentrated on the transport: TSFlow [9] replaces the isotropic source with a Gaussian-process prior matched to the temporal structure of the data; PrismFlow [30] attributes the spectral contraction of a single global velocity estimator to incompatible conditional velocities and adds Koopman-inspired residual experts; TimeFlow [13] restores with an SDE the randomness an ODE formulation discards; SDFlow [11] moves the transport into a frozen VQ latent space. On the diffusion side the forward operator has been adapted to the spectral profile of time series [24] and to time-varying uncertainty [26]. All of these are continuous-state in the sense of Eq. 1, all report on overlapping subsets of the datasets in Table I, and none of them discusses the atom. I-B Intermittent series, occurrence processes and censoring Outside generative modelling the point mass defines a mature subfield, and the baselines of Sec. V are taken directly from it. Croston’s method [3] splits demand occurrence from demand size, with a standard bias correction [20], neural variants [10] and a probabilistic treatment via deep renewal processes [23]; even the accuracy measures used there need care on intermittent data [6]. In hydrology, chain-dependent weather generators have paired a Markov chain for wet/dry occurrence with a distribution for the amounts since Katz [8] and Richardson [15], with Stern and Coe [19] fitting non-stationary occurrence chains to reproduce dry-spell lengths — the statistic we use throughout — and Wilks [25] extending it to multiple sites. Where the atom comes from the observation process instead — detection limits, saturation, clipping — the setting is censored regression [22, 1]. What none of this provides is joint trajectory generation: it works with marginal or low-order conditional forecasts and is absent from the benchmarks the generative models report on. Running the two families against each other on the same windows is one contribution of this paper. I-C Evaluating generative time series Reported comparisons rest on CRPS — a strictly proper score, but a marginal one [4] — and, for unconditional generation, on a discriminative score and Context-FID [7], a Fréchet distance in the representation space of a contrastive encoder [29]. Both are marginal or pooled. Scores that are sensitive to dependence exist — the energy score [4] and, more sharply for correlation structure, the variogram score [18] — and we report both, but neither isolates the contribution of the coupling from that of the marginals. The control of Sec. IV-B does, and it is the inverse of a familiar operation: the Schaake shuffle [2] and ensemble copula coupling [16, 17] impose a rank dependence on samples that were postprocessed marginally, whereas we remove the dependence a model produced while holding those marginals fixed. Used forward it is a correction; used backward it is a measurement. I Atoms in time-series benchmarks Table I reports, for datasets drawn from the GluonTS and Monash repositories [5], the fraction of exact zeros and two descriptors of the atom process: the calendar-unexplained occurrence entropy s=H(Z∣calendar)/H(Z),Zt=Yt=0,s=H(Z )\,/\,H(Z), Z_t=1\Y_t=0\, (2) estimated with a cross-fitted logistic model on calendar harmonics, and the over-dispersion of the zero-run law relative to a geometric distribution, ϕ=Var(L)/([L]2−[L]),ϕ=1 for geometric.φ=Var(L)\,/\, (E[L]^2-E[L] ), φ=1 for geometric. (3) Both are computed from the raw data, with no model and no access to the test split. Neither turns out to predict which datasets a flow struggles on (Section V); we report them because they are the two natural candidates and because ruling them out is itself informative. TABLE I: Atom mass and two data-only descriptors. s is the share of occurrence uncertainty the calendar cannot explain (Eq. 2); ϕφ is the over-dispersion of the zero-run law (Eq. 3). Neither predicts which datasets the flow struggles on (Sec. V). Dataset Pr(Y=0) (Y=0) s ϕφ car_parts 0.94 1.00 0.72 weather† 0.62 1.00 1.88 temp_rain† 0.57 0.66 7.93 solar 0.50 0.15 0.02 rideshare 0.47 0.93 1.47 covid‡ 0.42 0.65 0.43 uber 0.31 0.98 30.7 electricity 0.01 — — traffic 0.00 — — †mixed: these interleave rain series with temperature and pressure series that have no atom (74%74\% of weather’s series have Pr(Y=0)<0.01 (Y=0)<0.01); we use the Pr(Y=0)≥0.3 (Y=0)≥ 0.3 subset throughout. ‡excluded from Sec. V, see Sec. IV-A. IV Two evaluation problems IV-A The evaluation window need not resemble the dataset The standard protocol forecasts the final H steps of each series. When the atom process is non-stationary, those windows can be unrepresentative of the dataset by a wide margin. On covid_deaths the dataset is 42.3%42.3\% zeros while the evaluation windows are 13.1%13.1\%; on rideshare it is 46.9%46.9\% against 5.3%5.3\% (Fig. 1). Any statement about atom behaviour measured under this protocol on these datasets is therefore measured on a regime the dataset barely contains. Figure 1: How far the evaluation window departs from the dataset it is drawn from. Zero is agreement. Under the rolling-origin protocol rideshare’s windows are 4242 points short of the dataset’s zero rate, so the protocol is not testing the atom behaviour it appears to. A series-wise split fixes that case but not covid, whose zeros belong to the pre-outbreak period, and introduces a departure of its own on car_parts. A series-wise split — hold out whole series, draw windows across their full time axis — removes the problem where the atom process is stationary in time: on rideshare the evaluation-window zero rate moves from 5.3%5.3\% to 59.1%59.1\%. It does not rescue covid_deaths (14.1%14.1\%), whose zeros are an artefact of the pre-outbreak period rather than a recurring process; we exclude it below and state the reason rather than reporting a number that cannot mean what it appears to. IV-B A control under which CRPS cannot move CRPS is a function of the per-timestep predictive marginals alone, so it is often argued that it cannot see temporal structure. We make this measurable. Given samples Y^1:H(1:K) Y^(1:K)_1:H for a window, permute the sample index independently at each step h: Y~h(k)=Y^h(πh(k)),πh∼Unif(K) i.i.d. Y^(k)_h= Y^( _h(k))_h, _h ( S_K) i.i.d. (4) The multiset of values proposed at each (window,h)(window,h) is unchanged, so every per-step marginal — and hence CRPS — is invariant by construction, while the coupling that carries the run-length law is destroyed. We compute the empirical CRPS exactly, evaluating |X−X′|E|X-X | with the closed form for the mean absolute pairwise difference of a sorted sample rather than from a random pairing; the measured difference under Eq. 4 is then 0 to floating-point precision on every dataset. (A pairing-based estimator of the second term is not invariant even though CRPS is, and reports a spurious difference of order 10−210^-2 — a detail worth stating because it is easy to mistake for a real effect.) What the control licenses is narrower than “the part of the temporal structure CRPS cannot see”: it is an exact within-model measurement of the contribution that the model’s trajectory coupling makes to a chosen statistic, with the predictive marginals held fixed. It does not enumerate everything a marginal score misses, and a model whose zero-run error is unchanged by decorrelation may still have learned autocorrelation, seasonality, or magnitude–occurrence coupling that this statistic does not register. Within that scope it gives a reference point a model must beat: if decorrelating its own samples does not worsen a statistic, the coupling it learned contributes nothing to that statistic. Fig. 2 shows it for two datasets and the last row of Table I for all six. On uber and car_parts the decorrelated flow is better than the flow, and on rideshare the two are within 12%12\%; the learned coupling pays for itself only on rain, weather and solar. Figure 2: Zero-run-length CCDFs. On rain the flow tracks the data and its decorrelated version does not, so the learned coupling is doing work. On rideshare the flow is far below the data at every length — its dry spells average 5.85.8 steps against 26.726.7 — and is indistinguishable from its own decorrelated samples, so the learned coupling contributes nothing to the zero-run statistic. CRPS is identical for the dashed and dotted curves by construction. V Benchmark and a negative result We compare, on identical windows and with an identical threshold protocol (threshold selected on a validation half, test-optimal threshold reported as a diagnostic upper bound): a conditional flow [9]; global and per-series Markov occurrence chains; a negative-binomial semi-Markov occurrence process; autoregressive and non-autoregressive hurdle models with a learned occurrence classifier; and a hybrid that keeps the flow’s own positive magnitudes and replaces only its zero pattern with the semi-Markov process. TABLE I: Zero-run-length W1W_1 (lower is better) under the series-wise protocol, identical windows and thresholds for every row. The flow is mean ± s.d. over five training seeds; the occurrence baselines carry no training stochasticity (closed-form transitions, fixed random_state) and are therefore reported once. Ctrl is the flow’s own decorrelated version (Eq. 4) — what a model must beat for its trajectory coupling to contribute positively to this statistic. rain solar uber ridesh weath c.parts Flow .33 ±.11 .71 ±.44 .24 ±.09 19.8 ± 1.4 .52 ±.23 .37 ±.03 Markov, global .84 2.60 1.38 3.69 .73 .57 Markov, series .22 2.63 .15 4.79 .19 .45 NB semi-Markov .90 2.58 .46 3.36 .62 1.04 Hurdle, non-AR 1.06 5.01 .21 9.50 .90 .23 Hurdle, AR .31 1.23 .08 .13 .10 .05 Hybrid .92 2.61 .46 3.38 .59 1.05 Ctrl: decorrelated 1.12 .93 .35 21.0 1.37 .28 CRPS on the same samples Flow 3.03 5.50 3.10 3.11 1.81 .43 Markov, global 4.48 25.4 9.83 2.74 1.79 .38 Markov, series 4.23 25.2 8.61 2.86 1.81 .40 NB semi-Markov 4.41 25.6 10.2 2.78 1.80 .41 Hurdle, non-AR 3.96 34.9 8.70 2.58 1.80 .36 Hurdle, AR 4.01 20.4 8.79 2.27 1.76 .36 Hybrid 3.87 24.3 7.00 3.25 1.78 .44 Three observations follow from Table I. An autoregressive hurdle dominates. A learned occurrence classifier rolled out one step at a time is the best model on five of the six datasets, and not narrowly: on rideshare it reaches 0.130.13 against the flow’s 19.819.8, a factor of 153153. It is also the best or second-best model under the spectral, spell-quantile and survival statistics of Sec. V-A. The lower panel of Table I shows why this is not simply a better model: on rain, solar and uber the flow has the best CRPS of the seven while being beaten or matched on the occurrence statistics, and on solar it is ahead on both. The two families of number do not order the models the same way, which is the situation a practitioner is actually in. We report this arm prominently because we initially omitted it: under the rolling-origin protocol its rollout drifts and it looks like a cautionary tale about exposure bias, and we had written it up as one. Under the series-wise protocol — where the evaluation windows actually contain the atom — it is the strongest occurrence model we tested. The earlier reading was an artefact of the evaluation windows of Sec. IV-A, which is a second, uncomfortable instance of this paper’s own first finding. The flow’s atom statistics are seed-unstable; the baselines’ are not. Over five training seeds evaluated on identical held-out series and windows, the flow’s run-length error has a relative spread of 7%7\% to 62%62\%; on solar the seeds range over a factor of four. Every occurrence baseline here is deterministic: the transition probabilities are closed-form and the one learned component has a fixed seed. A single-run number for a flow on these statistics is not reportable at the margins these comparisons are decided by, and the papers we drew the model from report one. The obvious fix is not one, but the obvious fix was the wrong one. The hybrid keeps the flow’s magnitudes and substitutes an explicit occurrence process, isolating that component. With a semi-Markov occurrence process it improves on the flow on rideshare alone and is worse on the other five. That is the result we would have reported had we stopped there. Table I shows why it is the wrong conclusion to draw: the occurrence process that works is not the semi-Markov one but the autoregressive classifier, and a hybrid built on that component is the natural next experiment rather than a closed question. Comparing each flow against its own decorrelated version isolates the value of the coupling it learned, with the marginals held fixed. Averaged over seeds, the coupling pays for itself on rain (3.4×3.4×), weather (2.6×2.6×), uber (1.5×1.5×) and solar (1.3×1.3×), is neutral on rideshare (1.06×1.06×), and is actively harmful on car_parts (0.82×0.82×); the occurrence ACF gives the same ordering. An earlier three-seed version of this table put uber and car_parts both on the harmful side — with five seeds only car_parts remains there, which is itself an illustration of the previous paragraph. V-A Does the conclusion survive a change of statistic? Everything above is measured with the Wasserstein distance between zero-run length laws. That is one hand-built statistic, and a reader is entitled to ask whether the picture is an artefact of it. We therefore repeat the comparison under four more, in two groups. Spell quantiles (mean relative error at the 5050th, 9090th and 9999th percentile) and the sup-norm between run-length survival functions are further summaries of the same object, so they corroborate the W1W_1 rather than test it independently: the W1W_1 weights how far misplaced mass moved, the sup-norm weights how much mass is misplaced, and a model can do well on one and badly on the other. The occurrence autocorrelation and the normalised occurrence periodogram are independent of the run-length construction — they read the same binary process through a second-order and a spectral lens, and are defined for windows containing no completed spell. We also report the two transition rates of the occurrence chain. TABLE I: Mean rank across the six datasets under each occurrence statistic (1 = best of seven models), five seeds. The ordering is not the same under every statistic, and the two that do not share the run-length construction (ACF, spectrum) agree with each other less than either agrees with W1W_1. run-length family independent Model W1W_1 spellQ survS ACF spec Flow 3.2 2.7 2.8 2.0 3.0 Markov, global 5.3 4.2 4.5 5.8 4.7 Markov, series 3.3 3.0 3.0 4.7 2.7 NB semi-Markov 4.8 4.3 4.3 4.7 4.7 Hurdle, non-AR 4.5 4.5 4.3 3.5 4.8 Hurdle, AR 1.3 1.2 1.2 2.2 1.3 Hybrid 5.5 5.2 5.0 5.2 5.0 Rank correlation between orderings, averaged over datasets: W1W_1–survS +0.92+0.92, W1W_1–spellQ +0.84+0.84, W1W_1–spec +0.79+0.79, W1W_1–ACF +0.55+0.55, ACF–spec +0.45+0.45. VI Conclusion A conditional flow is beaten on five of six atom-bearing datasets — on rideshare by a factor of 153153 — by an autoregressive occurrence hurdle with no generative machinery to speak of, yet it has the best CRPS of the seven models on three of those same datasets, so which model is better depends on which family of number one reads and on which occurrence statistic within the second family. Three things follow that do not depend on the hypothesis we started from or on the model family we tested: report the atom rate of the evaluation windows, since the standard protocol can differ from the dataset by forty points and inverted the ranking of the best baseline in this study before we caught it; compare a model against its own decorrelated samples before crediting it with temporal structure, which costs one permutation, holds CRPS fixed by construction, and reveals cases where the learned coupling contributes little or negatively; and report a spread, since this flow’s occurrence statistics move by up to 62%62\% across training seeds while every occurrence baseline here is deterministic. References [1] T. Amemiya (1984) Tobit models: a survey. Journal of econometrics 24 (1-2), p. 3–61. Cited by: §I-B. [2] M. Clark, S. Gangopadhyay, L. Hay, B. Rajagopalan, and R. 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