XSci (AI review)

October 2, 2026

Referee Report

Manuscript: "Comparative Analysis of LSTM vs. Transformer Models for Volatility Forecasting: A Theoretical Review with Applications to VIX and Cryptocurrency Markets"

Field: Quantitative finance / financial econometrics with machine-learning methodology

Recommendation: Major revision

Summary and Recommendation

This manuscript asks which of two deep-learning architectures a quantitative researcher should select for volatility forecasting, and answers by comparing LSTM networks and Transformers along architectural rather than purely empirical dimensions. The paper enumerates six stylized facts of financial volatility, sets out the mathematical structure of each architecture and tabulates eleven comparative properties in Table 3.1, derives five verbal predictions in Section 3.4, applies those predictions to daily VIX and hourly cryptocurrency settings using results reported in approximately six prior studies, surveys hybrid and sparse-attention designs together with five open problems, and closes with a decision matrix and practitioner checklist. The central conclusions are that neither architecture dominates universally, that sample efficiency is the primary differentiator, that LSTMs are preferable for small, noisy, or latency-sensitive applications, and that hybrid LSTM-attention designs occupy the middle ground.

The question is worth asking and the organising instinct is sound. A literature that has accumulated many pairwise accuracy tables and little mechanistic understanding would benefit from exactly the kind of synthesis attempted here, and anchoring that synthesis in the stylized facts that any volatility model must accommodate is the right way to make it legible to a finance readership. Table 3.1 and the Section 6.2 checklist are artefacts practitioners would consult, and the refusal to declare a universal winner is more useful than most of the comparisons the paper surveys. Three families of problem nonetheless prevent publication in the current form. The evidentiary foundation is largely unverifiable: five of the six studies on which the entire empirical argument rests could not be located, and the parameters populating the stylized-facts chapter carry no citations. The analytical framework contains technical errors, unspecified mechanisms, and internally inconsistent thresholds, and its two-case design cannot identify the factors it nominates. And the paper's positioning overstates what it delivers while omitting the econometric benchmarks and economic interpretation its intended audience will expect. Major revision is required, and in this reviewer's judgement the first of these families must be resolved before the others can usefully be assessed.

Major Concern Category 1: The Evidentiary Foundation Cannot Currently Be Verified

1.1 The empirical evidence base could not be located, and one identifier belongs to an unrelated paper

Because Section 1.4 states explicitly that the authors conduct no original backtesting or coding, every quantitative claim in the paper is an attribution, and the six studies cited in Sections 4.1.3 and 4.2.3 therefore constitute the whole of its evidence. In preparing this report, each was searched by title, by author and year, by journal and volume, and by topic. The clearest result concerns Patel and Shah (2023), cited as arXiv:2303.12345: that identifier resolves to a cosmology paper on the Hubble tension subsequently published in Physics Letters B, with no author named Patel or Shah. This matters disproportionately, because that source supplies the entire sample-size ladder underpinning Prediction 3, the thresholds in Section 3.5, two rows of Table 4.1, and the Section 6.2 checklist. Searches for the remaining five returned no matching record: a 2019 Journal of Financial Data Science article by Liu, Zhang and Wang comparing LSTM with Transformer, a 2021 Applied Economics Letters article by Chen and Ge on hybrid LSTM-attention VIX forecasting, a 2022 Journal of Financial Data Science article by Li, Wang and Zhang on long memory in the VIX, a 2022 Digital Finance article by Wang, Chen and Liu on Transformers for Bitcoin volatility, and a 2023 Digital Finance article by Kim and Lee on noise sensitivity. Negative search results are not proof of non-existence, and indexing gaps or title changes between preprint and publication can defeat a search, so the appropriate request is that the authors resolve the matter definitively by supplying a DOI for every cited work, correcting the arXiv identifier, and providing for each study a short methodological description covering asset, sample window, target variable, horizon, train-test split, model configurations and test statistic. Where a source cannot be substantiated, the dependent claims and the table rows and checklist lines resting on them should be withdrawn, and the authors should consider what survives on the remainder.

1.2 The review protocol and the empirical parameters of Section 2 are undocumented

Section 1.4 describes the work as resting on "a systematic review of existing literature," and Section 1.5 reports that a search of Scopus, Web of Science and arXiv yielded approximately 120 relevant papers, of which 85 percent report only accuracy comparisons, 12 percent discuss architectural properties "in any depth," and 5 percent offer actionable guidance. These three figures establish the gap the paper claims to fill, yet no execution date, database field, document-type filter, deduplication procedure, screening count, coding rubric, or study list is supplied, and the stated Boolean string would not retrieve work using "realized volatility," "attention," or named architectures such as Informer or PatchTST without the literal token "Transformer." The same silence surrounds the quantitative inputs to the framework itself. Across Sections 2.1 through 2.7 and again in Sections 4.1.1 and 4.2.1, the manuscript asserts autocorrelations of 0.2 to 0.3 for squared equity returns and 0.85 and 0.40 for VIX and cryptocurrency, long-run means of 15 to 20 and 50 to 80 percent, a mean-reversion speed of 0.05 to 0.10, Hurst exponents of 0.6 to 0.7, 0.7 to 0.9, 0.65, 0.52 and 0.53, regime counts of five to ten per decade and ten to twenty per year, and an effective LSTM memory of 200 to 500 steps, without a single supporting citation. Several of these are estimator-dependent in ways that bear directly on the argument, since Prediction 1 conditions on H exceeding 0.65 and the paper's own VIX estimate is exactly 0.65. There is also a deeper difficulty: the framework treats long memory and regime-shift frequency as independent axes, yet the econometric literature has shown that regime switching and occasional structural breaks generate autocorrelation patterns difficult to distinguish from genuine long memory, which would mean the two axes are not separately identified and that the reported Hurst differences between the two markets may partly reflect the reported regime-frequency differences. The revision should either supply the full systematic-review apparatus or reframe the paper honestly as a critical review and delete the percentages, and should source every numerical claim to a study and estimator.

1.3 Cross-study comparisons are not commensurable and no forecast-comparison inference is applied

The paper's central empirical move is to place results from six studies side by side and read a pattern off them, but the figures are not on a common footing. The VIX results are in index points and the cryptocurrency results in annualised percentage volatility, yet Table 4.1 presents them in adjacent rows; the three VIX studies use different windows with different crisis content, so an RMSE of 2.01 over a sample including 1990 to 2003 is not comparable with 2.10 over 2004 to 2018; and no forecast horizon, train-test split, or evaluation scheme is reported for any study. More fundamentally, the estimand itself differs in kind. In the VIX setting the target appears to be the level of an observable, model-free, risk-neutral index that differs from physical-measure volatility by a time-varying variance risk premium; in the cryptocurrency setting it is an unnamed realized-volatility estimator of a latent integrated variance whose own estimation error enters the evaluation metric. These are different statistical problems, and the noise contrast the paper attributes to market structure is partly a property of the sampling frequency and estimator chosen, which are never stated. Nor is annualisation reconciled between a 252-day convention for the VIX and a continuously traded crypto market. On the inference side, the manuscript reports p-values inherited from source studies without identifying the tests that produced them, and applies none of the apparatus a finance readership expects for predictive-accuracy comparison. The sharpest version of this concern is self-referential: Section 1.2 criticises the literature for reporting only RMSE, MAE and QLIKE, yet every quantitative claim in Section 4 is an RMSE comparison and QLIKE, though named in the Abstract, is never defined or computed. Since proxy-robust loss functions can rank models differently from non-robust ones when volatility is replaced by a noisy proxy, a synthesis built entirely on RMSE may be delivering proxy-driven rather than model-driven rankings.

1.4 Acknowledged limitations are neutralised rather than incorporated

Section 4.4 is the most intellectually serious passage in the paper, identifying publication bias, asymmetric hyperparameter tuning effort, computational constraints, data snooping and limited generalisability as threats to the evidence base. It then concludes that "despite these limitations, the convergence of theoretical predictions and empirical evidence across multiple studies supports the robust conclusions in Section 4.3." This inverts the logic, because convergence between prediction and evidence is precisely what publication bias and undisclosed model search would be expected to manufacture, and the word "robust" is applied to conclusions drawn from six studies, five reporting a single asset, with VIX effect sizes of a few hundredths of an index point. The limitations then disappear: no row of Table 4.1, no line of the Section 4.3 matrix, and no item in the Section 6.2 checklist is qualified or assigned a confidence level on their account, and the four limitations of Section 6.3 are listed in single sentences without connection to any specific finding. A limitations section performs its function only when it changes what a reader believes about particular claims. The revision should delete or invert the convergence sentence, trace each limitation to the conclusions it threatens, and annotate the decision guidance to distinguish recommendations supported by multiple independent studies from those resting on one, and those following from architectural necessity from those resting on reported accuracy.

Major Concern Category 2: The Analytical Framework Is Internally Inconsistent and Cannot Identify Its Own Mechanisms

2.1 The theoretical predictions are validated against the literature from which they appear to derive

Sections 4.1.3 and 4.2.3 conclude that the empirical evidence supports, and in the cryptocurrency case strongly supports, the five predictions of Section 3.4, and this corroboration is the logical spine of the paper. The inference appears circular. Prediction 3's thresholds of 5,000 and 20,000 observations are not derived from any stated property of attention estimation or sample complexity, and Section 1.5 has already reported Patel and Shah's sample-size finding several pages before the predictions are stated, so the thresholds read as having been read off the evidence rather than deduced in advance. Prediction 1's threshold of H greater than 0.65 coincides exactly with the Hurst exponent the paper assigns to daily VIX, rendering it unfalsifiable within the paper's own two-market design. The second difficulty is more concrete: Prediction 1 asserts that Transformers should outperform LSTMs for the VIX, yet Section 4.1.3 reports the LSTM winning in two of three studies, with only Li et al. showing a Transformer edge of 0.03 RMSE points reported without a test. The synthesis nonetheless declares the prediction supported. At best the evidence supports a conjunction of Predictions 1 and 3 in which sample size overrides long memory, but that is a post-hoc rescue requiring the relative weights to be specified in advance, and the paper never states what would have counted as a refutation. A compact simulation study, which Section 5.5 itself proposes and which involves no market data and so falls within the declared scope, would convert these conjectures into genuinely testable propositions.

2.2 Several technical characterisations of the architectures appear incorrect

Because the manuscript offers no original evidence, the accuracy of its formal statements is its substance, and four items in Section 3 require correction. The parameter count for multi-head attention is given as O(h·d²) where h is the number of heads, but under the paper's own definition of d_k as d/h the concatenated projections total 4d² independent of head count, which matters because parameter count underpins the sample-efficiency argument and the hybrid's claimed economy in Section 5.1. More consequentially, Section 3.3 justifies the Transformer's noise sensitivity by asserting that "a single noisy observation can receive high attention if its value is extreme," whereas under scaled dot-product attention as written in Section 3.2 the weight depends on the query-key inner product, not on the magnitude of the value; an extreme value does not thereby attract attention. Since noise robustness is Prediction 4 and occupies a row in Table 3.1, a row in Table 4.1, a line in the Section 4.3 matrix, a line in the Section 6.2 checklist and finding 4 in Section 6.1, the stated mechanism must be replaced with a correct one, and the complementary claim that the forget gate filters noise likewise needs derivation, particularly as the forget gate governs retention of the prior cell state rather than admission of new input. Section 2.5 further describes the LSTM hidden state as evolving "via a differential equation," though the recursion in Section 3.1 is a difference equation whose decay factor is learned and input-dependent, which weakens the "state must decay" entry in Table 3.1 since a forget gate can in principle approach zero within a single step. Finally, the 200 to 500 step effective-memory range is uncited despite being the basis for the claimed Transformer advantage under long memory, and the symbol h denotes both the LSTM hidden dimension and the number of attention heads, a collision that propagates into the complexity expressions.

2.3 The regime-shift mechanism central to the cryptocurrency recommendation is never specified

The proposition that attention "resets" after a structural break appears in Section 2.5, in Table 3.1, as Prediction 2, in Section 4.2.2, as the attributed explanation of Wang et al.'s result in Section 4.2.3, in Table 4.1, in the Section 4.3 matrix and as finding 3 in Section 6.1, and it is the sole justification for the paper's cryptocurrency recommendation. No mechanism is given. A mechanism would need to explain how a model trained to minimise average loss over a sample containing many regimes learns a query-key geometry that concentrates attention on observations following an unobserved, unlabelled break. Sinusoidal positional encoding, which Section 3.2 presents as the default, represents absolute position and provides no regime representation; the capacity to attend to the recent past exists, but so does the capacity of an LSTM forget gate to do the same, and no argument is offered that attention does it better. Section 5.2 moreover concedes that practical sequence lengths require a sliding window, which is itself a crude form of the recency behaviour being attributed to learned attention. There is also tension with the paper's own sample-efficiency argument: if localising attention after a break requires observing many breaks, as Section 4.1.2 implies, then the mechanism is in-sample pattern recognition over historical regimes rather than adaptation to novel ones, and the 2020 and 2022 episodes the paper cites are precisely cases where novelty was the issue. The authors should supply a derivation, a supporting citation, or an explicit demotion to conjecture; a simulation using the Markov-switching framework they already cite would settle the question directly.

2.4 The sample-size thresholds and market predictions are mutually inconsistent

Sample size is identified in Section 6.1 as the primary differentiator, yet its thresholds take at least four incompatible values. The Abstract and Table 3.1 give 500 to 1,000 observations for LSTM and 10,000 to 50,000 for Transformer; Prediction 3 and Section 3.5 use 5,000 and 20,000, leaving the interval between them unassigned; Section 6.2's checklist asks only about 20,000; and Table 4.1, the paper's own evidence summary, records a Transformer advantage for the VIX at 5,000 and for Bitcoin at 8,000, both below the Abstract's floor and far below the checklist's threshold. Section 4.1.3 compounds this by placing the VIX crossover at T greater than 5,000 when Chen and Ge are described as using 5,040 observations and finding the Transformer losing, so the crossover on the paper's own numbers lies somewhere between 5,040 and 7,812. A practitioner with 15,000 hourly observations is told to use an LSTM by Section 6.2 and a Transformer by Table 4.1. The same unreconciled quality affects the cryptocurrency case, where Prediction 2 favours the Transformer on regime frequency and Prediction 4 favours the LSTM on noise, both apply, and no arbitration rule is offered; and where the Abstract asserts that Transformers excel at long-range dependence "particularly in high-frequency cryptocurrency data" while Section 2.7 records "Transformer advantage for VIX; neither for crypto" and Section 6.1 describes a Hurst exponent of 0.52 as "only moderate" after two earlier sections called it near-random-walk. A single set of thresholds should be derived transparently from the assembled evidence, presented with explicit uncertainty, and propagated consistently to every recommendation.

2.5 The two-case design confounds every factor the analysis seeks to isolate

The five predictions each nominate a single operative cause, and Section 4 tests them by comparing two settings that differ simultaneously on all of them. Daily VIX and hourly cryptocurrency differ in frequency, asset class, long memory, signal-to-noise ratio, regime-shift frequency by roughly two orders of magnitude, typical sample size, market structure and the kind of object being forecast. Any performance difference between them is therefore consistent with any of eight explanations, and the design cannot attribute it to one; in the cryptocurrency case it cannot even adjudicate between two of the paper's own predictions that point in opposite directions. The only sources in the evidence base containing identifying variation are Patel and Shah, who vary sample size with the asset held fixed, and Kim and Lee, who vary noise with the asset held fixed, and the paper's most defensible conclusions rest on those two studies rather than on the headline contrast. That should be stated, with the weight on the two-case comparison correspondingly reduced. The constructive route is either to expand the case set so that factors vary independently, adding for instance a low-frequency high-noise setting and a high-frequency low-noise setting, or to run the factorial simulation the paper itself proposes, manipulating Hurst exponent, regime intensity, noise variance and sample size with everything else held fixed. Without one of these, Table 4.1 and the Section 6.2 checklist extrapolate from two observations.

Major Concern Category 3: Positioning, Benchmarking, and Decision Relevance

3.1 The announced contributions are not delivered in the form claimed

The Abstract states that "we propose a hybrid LSTM-attention framework," but Section 5.1 describes a standard three-step design and attributes its performance to Chen and Ge, whose hybrid Section 1.5 has already listed among the paper's motivating findings; nothing in Section 5.1 is modified, extended, parameterised or evaluated by the present authors. Describing an existing architecture accurately is a legitimate function of a review, but it is not proposing one. The recurring label "theoretical," which appears in the title, Abstract, keywords and the headings of Sections 3.4, 4.1.2 and 4.2.2, likewise covers an argument containing no definitions, propositions, theorems, proofs or derived bounds; the complexity statements are recited rather than derived, and RQ2's request for conditions under which each model has a "demonstrable" advantage is met by assertion rather than demonstration. Section 5.5's fifth open problem concedes the point, identifying theoretical sample complexity as unsolved, which is to say that the paper's own central quantity has no theory behind it. This matters because contribution is the paper's differentiation strategy: if its own treatment is a verbal discussion of architectural properties, it falls within the 12 percent band it criticises rather than above it. The revision should add a short contributions paragraph stating plainly what is new, credit the hybrid architecture to its source, and either supply one formal or simulated result or substitute a more accurate descriptor such as "mechanism-oriented" for "theoretical."

3.2 The econometric benchmark literature is absent, and the prior question is never asked

The paper's structure presupposes that the practitioner's choice is between two deep-learning architectures, disposing of parametric alternatives in a single unsupported paragraph in Section 1.1. The most consequential omission is the heterogeneous autoregressive model of realized volatility, which captures the empirically relevant persistence of volatility with three averaging horizons estimated by ordinary least squares. Its absence matters twice over: it is the benchmark against which claims of forecasting improvement are conventionally judged in this literature, and its existence undercuts the paper's organising claim, since if three coefficients reproduce volatility persistence then long memory may simply not be the dimension along which the two deep architectures differ in practice, which drains much of the motivation from Prediction 1. Fractionally integrated conditional-variance models are similarly absent, and they are a direct counterexample to the Section 1.1 assertion that parametric models assume linear autocorrelation decay. Most tellingly, the paper never asks the prior question its own numbers raise: in Section 4.1.3 the gap between GARCH(1,1) at 2.45 and the better deep model at 2.10 is roughly twice the gap between the two deep models, and in Section 4.2.3 the gap between GARCH at 1.24 percent and the better deep model at 0.78 percent is several times the LSTM-Transformer gap. A reader is entitled to ask whether the architectural choice the paper spends thirty pages on is second-order relative to the paradigm choice it dismisses in a paragraph, and whether a well-specified HAR model with a leverage term would close most of the remaining distance at a fraction of the computational and governance cost.

3.3 Statistical accuracy is never connected to economic consequence

Section 1.1 locates volatility forecasting within option pricing, value-at-risk and expected-shortfall calculation, portfolio optimisation and hedging, and the Abstract promises actionable guidance, yet none of these terms reappears after the opening section and no result anywhere is expressed in economic units. The paper's VIX recommendation turns on differences of 0.18 and 0.03 index points, and a reader attempting to act on it will want to know what such a difference is worth in variance-swap mispricing, hedging profit and loss, regulatory capital under a ten-day value-at-risk, or the Sharpe ratio of a volatility-timing strategy. Without that mapping the paper cannot distinguish a difference justifying the rebuilding of a production pipeline from one that does not. The decision framework compounds this by accounting only for accuracy and feasibility, omitting the costs that dominate real model-selection choices: engineering and maintenance effort, retraining cadence and its compute budget, model-risk validation burden, failure behaviour under stress, and the organisational cost of maintaining two model families; the Section 3.5 advice keys instead on GPU memory thresholds that will date quickly. There is also the asymmetry of volatility-forecast losses, where underforecasting before a crisis and overforecasting during calm have very different consequences that squared error weights equally, and the question of whether a point forecast is the right object at all, given that value-at-risk and expected shortfall require conditional quantiles and option pricing requires a term structure. None of this demands a trading study, which Section 1.4 reasonably excludes; a single transparent economic calculation, a cost column in the decision matrix, and an explicit statement of which Section 1.1 applications the point-forecast framing actually serves would suffice.

3.4 The literature window closes two years before submission

Sections 1.4 and 1.5 bound the synthesis at 2024 for a manuscript dated April 2026, and for a review, where currency is close to the whole of the value proposition, this gap requires justification. It is consequential in three ways. Section 6.3 concedes that new architectures such as Mamba and RWKV may supersede the Transformer, but neither appears in the reference list, so the limitations section acknowledges possible obsolescence without examining it; state-space models in particular combine the linear-time recurrent inference the paper assigns exclusively to LSTM with the long-range capacity it assigns exclusively to Transformer, occupying a cell of Table 3.1 the paper treats as empty, while pre-trained time-series models bear directly on the sample-efficiency finding the paper identifies as primary. More sharply, the premise that Transformers hold an advantage for long-horizon temporal dependence was contested within the search window itself by evidence that simple linear baselines match or exceed a family of Transformer variants on standard benchmarks, and this directly contradicts Prediction 1 and the long-range-dependency row of Table 3.1; a review that does not address the leading counterargument to its own organising claim will be read as having surveyed selectively. Finally, the staleness interacts with the corpus statistics, since a gap measured in 2024 may have narrowed by 2026. The search should be rerun to the submission date with the execution date reported, and Section 5 should gain a subsection treating linear baselines, state-space models and pre-trained forecasters as genuine alternatives rather than as a parenthesis in the limitations.

Minor Issues

1. Section numbering and manuscript preparation. Every top-level heading is numbered "1.", the first subsection reads "### 2. 1.1 Background," page-budget annotations such as "(0.3 page)" and "(1.5 pages)" remain in at least seven headings, timestamped chat attributions of the form "[4/27/2026 2:32 PM] George Panos:" appear mid-paragraph in five or more places, and bare name prefixes appear in Sections 1.2, 4.1.3 and 6.5. Beyond readability, the last of these would compromise anonymity under double-blind review. A typographical error also survives into a substantive conclusion, where finding 4 of Section 6.1 reads "Noise robustness favors LSIMS."

2. Equations and notation require retypesetting. The cell-state recursion in Section 3.1 is written self-referentially as C_t = f_t ⊙ C_{t-1} + i_t ⊙ C_t, with the candidate state denoted inconsistently, and the gate expressions render as "f_{-}t" and "h_{-}t-1}". The Transformer equations are similarly corrupted, including the input space, the projection dimensions, the attention expression and the positional-encoding formulas. Since Section 3 is the formal core of a paper with no empirical content, these must be corrected before typesetting.

3. Tables are not rendered as tables. Table 3.1, the Section 2.7 summary, Table 4.1, the Section 4.3 decision matrix and the Section 6.2 checklist all appear as run-together prose, and in Section 2.7 content has merged across rows so that three distinct stylized facts are indistinguishable.

4. Reported sample sizes do not reconcile with the stated windows, and one result row is duplicated. Liu et al. (2019) is given as 2004 to 2018 with 3,528 observations, which at the paper's own 252 trading days implies fourteen years rather than fifteen, and Wang et al. (2022) as 2018 to 2021 with approximately 26,000 hourly observations, which implies three years rather than four. In Section 4.2.3 the row "T < 2,000 (<3 months): LSTM RMSE 1.02%, Transformer RMSE 1.15%" appears twice, and the stated conclusion that the Transformer requires six to twelve months sits awkwardly with the ladder's own tie region at 2,000 to 5,000.

5. The mean-reversion specification admits negative variance. Section 2.2 writes the process as an Ornstein-Uhlenbeck diffusion in the variance with additive Gaussian noise, which assigns positive probability to negative variance. Heston (1993), cited two paragraphs earlier, uses a square-root diffusion precisely to avoid this; a log-variance specification is the other standard choice.

6. Autocorrelation and Hurst figures compare objects of different kinds. Section 2.1 states the mathematical characterisation for the ACF of squared returns, gives 0.2 to 0.3 for daily equities, then reports 0.85 for daily VIX, a value characteristic of a volatility level rather than squared returns. Section 2.4 states that daily equity returns have H of 0.6 to 0.7, which is difficult to reconcile with weak-form efficiency, and Section 4.1.1 reports H ≈ 0.65 for the VIX without specifying level, log or increment, or the estimator used.

7. The VIX is characterised imprecisely and the variance risk premium is never mentioned. Section 4.1.1 describes the index as "the 30-day implied volatility of S&P 500 options," whereas it is a model-free, strike-weighted expectation constructed from SPX option prices. The distinction bears on the claim in the same paragraph that the VIX is a clean target with a high signal-to-noise ratio, since a risk-neutral expectation differs from physical-measure volatility by a time-varying premium.

8. Several claims carry no support where support is available. The regime-shift frequency of "5–10 major events per decade" is followed by six enumerated events spanning fifteen years, and the 2010 flash crash appears in Section 2.5 but not in the Section 4.1.1 list. The assertion in Section 2.3 that cryptocurrencies display opposite leverage asymmetries is uncited yet becomes a table entry in Section 2.7. The hardware estimate in Section 5.4 that a million operations takes roughly a millisecond on a GPU is several orders of magnitude out and omits the factor d from the paper's own cost expression. The LogSparse complexity is given as O(T·log T) where the source gives O(T(log T)²).

9. Scope statements do not describe the paper, and the decision rules have gaps. Section 1.4 excludes GARCH-deep-learning hybrids although GARCH baselines are reported throughout Section 4, and excludes hybrids although Section 5.1 presents one; it excludes convolutional and temporal convolutional networks without argument, although dilated causal convolutions sit on the same trade-off frontier. RQ4 promises selection from observable characteristics yet the rules condition on noise level and regime frequency, neither of which is directly observable nor given an estimator, and "major regime shift" is never defined operationally despite Hamilton (1989) being available for the purpose. The Section 4.3 matrix omits the three-to-ten-year daily case and the three-to-twelve-month hourly case, which are plausibly the modal practitioner situations. Sections 5.5 and 6.4 overlap substantially without cross-reference, and the Abstract names three open problems where Section 5.5 lists five.

10. The reference apparatus and submission materials are incomplete. The References heading is numbered "1." and the first entry is prefixed "2." while the rest are unnumbered; no entry carries a DOI, and arXiv entries omit dates and versions. No author affiliation, ORCID or corresponding-author contact is given, and there is no data availability, funding, conflict-of-interest or generative-AI use declaration, each of which is now standard at the likely target outlets. Preprint status is not signalled in the body text, so unrefereed and peer-reviewed findings are presented as evidentially equivalent, which matters most for the source carrying the greatest argumentative weight. Finally, no out-of-sample evaluation design is reported for any cited study, and forecast combination is never considered despite the paper's deliverable being a selection rule.

Missing and Inadequately Integrated Literature

Cited but Inadequately Integrated

Several works the manuscript cites are invoked for provenance and then set aside at the point where they would do real analytical work. Gatheral, Jaisson and Rosenbaum (2018) is cited in Section 5.3 and correctly described as implying a Hurst exponent near 0.1 for log-volatility, but the implication is confined to a four-sentence open problem even though the paper's entire long-memory axis presumes persistence with H between 0.65 and 0.9; if the roughness characterisation holds, the organising variable of the framework is in question, and Bennedsen, Lunde and Pakkanen (2022) offers the natural reconciliation by constructing a class in which roughness and genuine long memory coexist. Jain and Wallace (2019) is used to treat the non-interpretability of attention as settled, and that conclusion then functions as a decisive criterion in four places, but the subsequent debate contesting the strength of the claim is not acknowledged, and the complementary proposition that LSTM gate analysis constitutes an adequate regulatory explanation is asserted without any citation at all. Vaswani et al. (2017) is cited for the architecture but not for its treatment of incremental decoding, where cached keys and values make the marginal cost of appending an observation linear rather than quadratic in context length; this materially softens the online-updating disadvantage that Table 3.1, Prediction 5 and the Section 6.2 checklist all rely on. Engle (1982), Bollerslev (1986) and Heston (1993) function only as foils, supporting an unsubstantiated claim that parametric models fail during turbulence, while Section 2.3 simultaneously concedes that the GJR extension captures the leverage asymmetry. Hamilton (1989) supplies a formal apparatus for defining regimes that the paper never uses despite regime frequency being one of two framework variables, and Chen and Ge (2021) and Patel and Shah (2023), the two most load-bearing sources, are each summarised in a handful of clauses that leave their designs unevaluable.

Truly Missing Papers

The most consequential bibliographic gap is the heterogeneous autoregressive model, Corsi (2009), for the reasons set out above; alongside it, Andersen, Bollerslev, Diebold and Labys (2003) establishes the realized-volatility framework within which the cryptocurrency studies operate, and Baillie, Bollerslev and Mikkelsen (1996) provides the long-memory parametric counterexample to the Section 1.1 characterisation. On evaluation, Patton (2011) determines which loss functions yield proxy-robust rankings, Diebold and Mariano (1995) and Hansen, Lunde and Nason (2011) supply the pairwise and multi-model comparison apparatus, and Hansen and Lunde (2005) is the standard reference for the difficulty of beating simple benchmarks. On the identification problem, Diebold and Inoue (2001) and Granger and Hyung (2004) show that regime switching and occasional breaks generate apparent long memory, and Lo (1991) documents the bias of the classical rescaled-range estimator, all three bearing directly on the unsourced Hurst values; Ding, Granger and Engle (1993) is the canonical source for the autocorrelation decay figures of Section 2.1, and Cont (2001) for the stylized facts of Section 2 generally. On the machine-learning side, Zeng, Chen, Zhang and Xu (2023) is the leading challenge to the paper's premise, Nie et al. (2023) and Lim et al. (2021) are the strongest current Transformer baselines for long-horizon and interpretable forecasting respectively, Katharopoulos et al. (2020) and Dai et al. (2019) are direct counterexamples to the claim that online Transformers are infeasible, Gu and Dao (2023) is the uncited architecture named in Section 6.3, and Bengio, Simard and Frasconi (1994) is the correct source for the vanishing-gradient diagnosis. Finally, Sezer, Gudelek and Ozbayoglu (2020) is the prior systematic review against which this one should position itself, Gu, Kelly and Xiu (2020) is the methodological reference for machine learning in empirical finance, and White (2000) together with Bailey, Borwein, López de Prado and Zhu (2014) formalises the data-snooping concern that Section 4.4 raises informally.

Andersen, T. G., T. Bollerslev, F. X. Diebold, and P. Labys. 2003. Modeling and Forecasting Realized Volatility. Econometrica 71(2):579-625.
Bailey, D. H., J. M. Borwein, M. Lopez de Prado, and Q. J. Zhu. 2014. Pseudo-Mathematics and Financial Charlatanism. Notices of the AMS 61(5):458-471.
Baillie, R. T., T. Bollerslev, and H. O. Mikkelsen. 1996. Fractionally Integrated GARCH. Journal of Econometrics 74(1):3-30.
Bengio, Y., P. Simard, and P. Frasconi. 1994. Learning Long-Term Dependencies with Gradient Descent is Difficult. IEEE Transactions on Neural Networks 5(2):157-166.
Bennedsen, M., A. Lunde, and M. S. Pakkanen. 2022. Decoupling the Short- and Long-Term Behavior of Stochastic Volatility. Journal of Financial Econometrics 20(5):961-1006.
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Conclusion and Path Forward

The project behind this manuscript deserves to be completed. A review that explains the conditions under which recurrent and attention-based architectures differ, rather than tabulating that they do, would serve a field that has produced many comparisons and little understanding, and the authors' decision to organise that explanation around the stylized facts of volatility and the operational realities of deployment is the right one. The eleven-dimension comparison, the refusal to declare a universal winner, the candour of Section 4.4, and the specificity of the research agenda in Section 5.5 are all assets a revision should preserve.

The revision should proceed in three stages. The first and most urgent is verification: supply a DOI and a methodological summary for each of the six studies in Section 4, correct the arXiv identifier, source every empirical parameter in Section 2 to a study and an estimator, and withdraw any claim whose foundation cannot be substantiated. Until this is done, neither the authors nor a reader can judge what the paper establishes. The second is internal repair: correct the attention parameter count, the attention-weight mechanism, and the characterisation of LSTM dynamics; supply or demote the regime-shift mechanism; unify the sample-size thresholds into one set consistent with Table 4.1 and propagate it everywhere; resolve the conflict between Predictions 2 and 4; and either document the review protocol or reframe the paper as a critical review and delete the corpus percentages. The third is repositioning: credit the hybrid architecture to its source, replace the "theoretical" label or earn it, introduce HAR and a long-memory parametric model as benchmarks, define the estimand and horizon for each setting, connect at least one accuracy difference to an economic quantity, extend the search to the submission date, and allow the acknowledged limitations to qualify the recommendations. A compact factorial simulation over Hurst exponent, regime intensity, noise and sample size - which the authors themselves propose, which requires no market data, and which falls within their declared scope - would address the circularity, the confounding, and the missing formal content at once, and would in this reviewer's view do more than any other single addition to convert a readable survey into a contribution the intended audience could rely on.