A daily ETF scenario engine should beat historical simulation on VaR and ES before it gets to set portfolio weights. That is the most useful thing to build from this survey. Start with a few ETFs. The best tail-risk figure the authors report clears that hurdle by very little.

How the 131-study survey divides the work

Zhang, Duan, Zou, Feng and Xiao reduced 2,568 records to 604 after screening titles and abstracts. Reviewing the full texts left 131 studies, published or posted between 2021 and early 2026. The survey organizes them along two axes.

The first is the task. Extrapolation uses a history to generate plausible future paths; imputation fills gaps in a series. Synthesis generates entirely new paths from noise, with the option of conditioning on a regime or volatility target. Model family supplies the second axis. The paper identifies six: classical statistics, discriminative deep nets, GANs, diffusion models, foundation models, and controllable or text-conditioned generators such as TimeWeaver and T2S. The task counts are 54, 29 and 47. They add to 130 rather than the stated 131, leaving an internal inconsistency in the table.

Risk and scarce data carry most of the argument. Any historical window contains few crashes. A generator that captures fat tails and volatility clustering could therefore supply stress scenarios unavailable in that history. For practitioners, the main deliverable is a five-row evaluation checklist: pointwise accuracy, distributional fidelity, stylized facts, downstream utility and privacy. The authors give pointwise error a low rating for financial validity. Their conclusion here is fair: no single metric suffices, and financial validity requires distributional fidelity alongside economic logic and practical use. Every performance figure comes from other work. The survey conducts no experiments itself.

Our ETF engine is still running

We could not test the paper's method: a survey offers no single method to reproduce. Instead, we selected a compact generative model to implement its framework for synthesizing asset returns. Our engine uses daily returns from US-listed equity, Treasury-bond and gold ETFs. It reproduces none of the reviewed architectures. Nor does it test any trading result reported by the authors.

We left the order-book branch out entirely. As the survey notes, its diffusion and large-market-model simulators were evaluated on at most two stocks or single datasets. TRADES, for instance, reports predictive-score gains of 3.27- and 3.48-point on two names. That is too little evidence to justify building an execution simulator. Our run remains in progress, and we report no results here.

Does Tail-GAN clear the historical-simulation hurdle?

Of the reviewed models, Tail-GAN comes closest to a risk desk's needs. The Acerbi-Székely function scores its discriminator on VaR and ES, making tail outcomes dominate the generator's gradient. The survey gives these out-of-sample relative errors for VaR/ES across buy-and-hold, mean-reversion and trend-following strategies:

Keep the whole row in view.

Most of the gain comes against a neural baseline whose error is about 2.5 times that of history. The improvement over the baseline a risk manager would actually use is 0.3 points.

The score-based distributional test also calls for care. For dynamic strategies, the survey reports rejection rates of 21.3% for Tail-GAN, 11.4% for WGAN and 0% for historical simulation. Those results cover a different scope from the error figures above. The authors prefer the higher rejection rate, arguing that the synthetic distribution differs from the test set "in the way real markets are." A goodness-of-fit test would usually count 0% rejection in a model's favour. Before accepting 21.3% as a pass, we would check the direction against the original Tail-GAN paper.

Five names, little time

The headline sample comprises five names: AAPL, AMZN, GOOG, JPM and QQQ. Its period is 2019-11 to 2019-12, which the survey describes as a one-month training window. Reaching the S&P 500 required eigenportfolio dimensionality reduction, which reduces the dimensions the model has to handle. Tail-GAN(Eig) then recorded 25.6% error, versus 25.9% for historical simulation. The survey itself describes that gap as much smaller.

The defence is that Tail-GAN addresses a different failure. Sample-dominated Wasserstein and cross-entropy losses structurally miss tail events, explaining vanilla WGAN's 26.9% error. On this reading, Tail-GAN competes with other generators on tail behaviour and makes no claim to replace historical simulation. That objective is exactly why historical simulation remains the benchmark to beat.

The authors acknowledge both limits and deserve credit for it. Their candour extends elsewhere: they describe diffusion's advantage over GANs in macro simulation as "a within-paper claim rather than a cross-paper empirical fact." They also identify the source of CSDI's reported 40 to 65% improvement over probabilistic baselines and 5 to 20% over deterministic ones. Those gains come from healthcare and environmental data.

None of this establishes a result for a stock, bond and gold mix. Single stocks dominate the test universe. For Tail-GAN, the survey reports only the 2019-11 to 2019-12 training window, and we found no crisis-period result in it. An ETF engine must reproduce bond-equity correlation flips. Five equities over a short window cannot demonstrate that ability.

The missing tolerances

The metrics are specified precisely. The survey gives the Hill tail estimator and uses the absolute-return ACF to measure clustering. For leverage, it specifies L(τ) = Corr(r_t, r²_{t+τ}) < 0 for small τ. Cross-asset fit is measured by the Frobenius norm between correlation matrices. Tolerances remain unspecified: the synthetic tail index should match history "closely", but we found neither a threshold nor a choice of k for the Hill estimator.

The data split requires another decision. FinTSB and FinTSBridge use 7:1:2; TSGBench and CTBench use 9:0:1, leaving no validation slice. The survey permits either hidden Markov models or variance thresholds for partitioning regimes. Those choices will carve up crisis windows differently. We chose US-listed ETFs partly to avoid a problem the survey identifies: forward-padding assets traded across different exchange hours produces flat-line correlations.

Before the allocator gets involved

For daily ETFs, the checklist translates into a chronological sequence of hurdles. Synthetic VaR and ES must improve on historical simulation's error on held-out dates. The survey's own evidence sets that margin at 0.3-point. Within a crisis partition, the Frobenius gap between correlation matrices must not grow relative to the blended sample. Mean-variance and risk-parity weights derived from synthetic paths should preserve the signs of historical risk premia, a test MacroSynth reportedly passed. The survey backtests no ETF strategy. We claim none on its behalf.

We have encountered this hurdle before. In an earlier note on a Treasury normalizing flow, historical simulation continued to win on unseen dates after we tightened the scales. A generator beating historical simulation by more than 0.3 points in a crisis window excluded from its training would change our view.