Diffusion models will earn their portfolio compute only after someone publishes a benchmark that allows direct comparison. Wang and Ventre come close to saying so themselves.
Their paper is a literature review, and, they say, the first devoted specifically to diffusion-family generative models for financial data. It contains no experiments, reimplementation or head-to-head comparison. The text includes no performance figure produced by the authors. Every numerical item below, unless it comes from our run, is a paper count.
The contribution lies in how the review is organised. Model families give way to the financial object being generated: time series, limit order books, tabular records, and structured objects including correlation matrices, implied-volatility surfaces and yield curves. Each object sets its own test of validity. Generated correlation matrices must remain symmetric and positive semidefinite. Volatility surfaces must obey no-arbitrage across strike and maturity. Order books must keep bids below asks, observe tick sizes and leave queue sizes non-negative. A generic sample-realism score cannot express those constraints. The taxonomy therefore carries the survey's main argument rather than merely filing the papers.
Section 2 compresses the technical background into DDPM and score-SDE training with Euler-Maruyama sampling, flow matching with Euler sampling, classifier and classifier-free guidance, FiLM conditioning, and the accelerators DDIM, EDM, consistency models, DPM-Solver and UniPC. The case for diffusion in finance is structural: stable likelihood-based training, mode coverage, flexible conditioning, and forward and reverse SDEs that fit naturally alongside the Itô calculus used for price dynamics. The network learns the reverse-time score in place of a calibrated fixed drift and volatility.
What is inside Table 1?
Table 1 contains 30 representative papers. The authors call the selection illustrative rather than exhaustive. Eleven cover time series, six limit order books, seven tabular data and six structured objects. All entries date from 2023 onward. FinDiff at ICAIF 2023 is the earliest, while the latest papers carry 2026 dates, leaving a field roughly three years old. The bibliography contains 103 entries.
Equities take most of the space. The 11 time-series rows and all 6 LOB rows carry the Stock tag, accounting for 17 of the 30, while two structured rows carry it as well. Elsewhere there are 2 option rows plus one derivative-pricing row, one interest rate row and one treasury future row. Flow matching is scarce: only 2 of the 30 entries are labelled Flow, namely FlowHFT and the latent-space flow-based tabular augmentation work. Regional tags in the table are US, CN, JP, Global, Multi and Synthetic. Three of the 30 slots belong to the authors' prior work, the Financial Time Series Denoiser, DiffVolume and DiffLOB. Keep that in mind when reading the LOB section.
Several ideas justify reading beyond the taxonomy. Tiwari adds a closed-form risk-neutral score shift to the DDPM reverse dynamics, making discounted generated paths satisfy the martingale condition and imposing no-arbitrage analytically. Backhouse et al. render order books as structured images, then use inpainting to generate future book states in parallel and avoid autoregressive error accumulation. Kim et al. replace ordinary Gaussian corruption with a GBM-informed forward noising process, putting price dynamics into the destruction path itself. These are three distinct ways to place financial structure inside a generic image-model architecture.
The benchmark gap is already the authors' case
The survey says that "Many papers use proprietary data, incompatible horizons, different preprocessing choices, weak or non-overlapping baselines, and downstream tasks that are difficult to compare." Its conclusion follows directly: "the field risks producing many plausible demonstrations but little cumulative evidence." We agree. The authors also say plainly that finance has no equivalent of Inception Score or FID, leaving realism claims numerically incomparable from one paper to another.
The authors make the obvious reviewer criticism before anyone else can. Their response consists of the three open directions they identify: object-specific benchmark suites instead of ad hoc realism checks, financial scaling laws, and diffusion operating directly as a decision-maker rather than a sampler. It is the right list. Yet the survey performs no head-to-head comparison, supplies no performance figures and warns that many papers rely on weak or non-overlapping baselines.
A desk reader therefore cannot learn from this document whether diffusion beats a GARCH-style simulator, block bootstrap, normalizing flow or plain Monte Carlo at any actual decision. Claims about risk-adjusted returns in the trading and portfolio papers appear without figures. The review names "transaction-cost robustness" as an evaluation criterion and describes a turnover-constrained CVaR portfolio allocator. Figures for costs, turnover, capacity and slippage never appear.
A separate omission worries me more because it captures a common failure mode for generative models in finance. Synthetic data used to augment predictor training can introduce look-ahead when the generator has seen the full sample. The survey does not discuss how the reviewed papers managed train and test splits for augmentation. Sampling latency appears as a bottleneck for stress testing and path simulation, then goes unquantified. A requirement for 300 paths per rebalance across 300 names can decide whether the method is usable.
The Bagchi et al. finding comes closest to a warning label. As relayed by the survey, factor dimensionality in diffusion portfolio models governs a bias-variance tradeoff: too few factors underfit return dynamics, while too many create unstable, concentrated portfolios. The survey gives no figures for this result. Concentration is exactly what a CVaR optimiser produces when its scenario set is too clean.
Our own build
The disclosure comes before the results. This survey defines no canonical trading model, so any build requires choosing one architecture and one scenario-to-allocation rule, then accepting responsibility for both. We could not reproduce the LOB, order-flow, bid-ask or true high-frequency work. Our data comprise one-minute OHLCV bars, without quotes, book states or tick trades. We instead worked in the survey's US stock and ETF return-generation strand, where generated scenarios feed portfolio allocation. The result is an adaptation of one idea in the survey.
We rebalanced monthly from 2020-01-01 to 2024-07-01 using daily bars. Each calendar year, the universe was screened point-in-time for the top 30 US stocks and ETFs by annual dollar volume, excluding ADRs and indexes and requiring 756 trading days of history. Conditioning used lagged VIX, macro series and PCA factors, all standardised on an expanding window. PCA was fitted within each training fold, with the factor count selected through nested held-out noise-prediction loss.
A conditional variance-preserving diffusion model generated 300 joint 21-day return scenarios with 20 reverse steps. We then minimised empirical CVaR at 95%, long-only, with 10% allowed per position and one-way turnover capped at 1.0. Trades executed at the observed close. We charged 5 bps one way plus $0.004 a share.
The survey has no performance figures of its own. Our figures for that window are total return 79.32%, Sharpe 0.53, Sortino 0.65, Calmar 0.28, maximum drawdown -50.49% and volatility 33.37%.
Read the risk numbers first.
Volatility of 33.37% and a -50.49% maximum drawdown describe what a long-only portfolio of the 30 largest US names by dollar volume can do. Minimum empirical CVaR at 95% across 300 scenarios failed to alter that during 2020 or 2022. Modelled slippage is zero, flattering a monthly portfolio whose turnover cap is 1.0.
Sample length is the larger problem: 54 months, one rate cycle and one crash. A generator conditioned on VIX and macro state has perhaps two genuine regime transitions available for learning over that window. And 300 scenarios of 21-day joint returns provide a thin empirical loss distribution for estimating 95% CVaR.
Our run does not isolate the diffusion step's contribution. We did not run the obvious control, the same optimiser supplied with a bootstrap or shrinkage covariance. The result therefore says nothing about whether diffusion helped, and I would not allow it to be quoted as evidence either way. This was one automated pass, with the stated architecture, data limits and allocation rule, rather than a verdict on the authors' work.
Our missing control reproduces the survey's own complaint inside our backtest.
A reading list for the desk
The taxonomy is useful, and the reading list earns its place. Fifteen of the 30 tabulated entries appeared in refereed venues by our count of the Venue column. The other fifteen are arXiv preprints, so the underlying claims have received uneven quality control, just as the authors' framing suggests.
I want one paper built around a single, clearly specified decision, with conditional scenarios generated for that decision. It should compare against a bootstrap and a GARCH simulator over the same universe and period, net of costs, while reporting sampling time in seconds. The survey identifies no such comparison among any of the 30.
Wang and Ventre observe that many papers use "weak or non-overlapping baselines", then ask the field to "build object-specific benchmark suites". Until those suites exist, diffusion finance remains a collection of interesting constructions whose portfolio value cannot be compared.
Our backtest stops at 2024-07-01, and everything after that date is deliberately left untouched so the same strategy can be checked out of sample later.