XSci

Spectral Lead–Lag and Cost-Aware Allocation in Egyptian Equity Benchmarks

Louise Shaw, Khalid Saqr

Submitted by Khalid Saqr

Published November 19, 2026 · Version v1, November 19, 2026 · DOI 10.66977/xsci.2611.0035

Quantitative Finance, Signal Processing, Spectral Analysis

Abstract

This paper presents a computational framework for translating dependence between overlapping equity benchmarks into allocation rules evaluated under explicit implementation costs. The framework combines spectral coherence, phase-delay estimation, causal filtering, friction-aware allocation, IID-bootstrap wealth diagnostics, and regime-consensus Bayesian optimization. Using aligned daily observations on the EGX100 Equally Weighted Index and the EGX30, the analysis finds strong contemporaneous return co-movement and horizon-specific synchronization. A coherent medium-horizon region appears near an 84-trading-day cycle; under the stated phase convention, its estimated delay is consistent with an EGX100EWI lead of roughly 2-3 trading days. Regime-consensus optimization selects a shorter 40-day cycle with zero additional execution lag. These estimates answer different questions: the spectral result describes frequency-specific synchronization, whereas the selected parameter maximizes the stated in-sample objective. IID-bootstrap summaries show a narrower wealth distribution for the overlay, but its median and fifth-percentile terminal wealth are below buy-and-hold EGX30. The findings therefore characterize a risk-return trade-off rather than higher terminal wealth or out-of-sample predictive performance.

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Review reports

xPeerd (AI review)

November 19, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript presents a computational framework for detecting frequency-specific dependence between the EGX30 and the EGX100 Equally Weighted Index and translating that dependence into a cost-aware allocation overlay. The paper’s clearest strengths are its careful distinction between descriptive synchronization and performance claims, its transparent acknowledgment that the backtest is in-sample, and its relatively interpretable workflow linking coherence, phase-delay estimation, causal filtering, friction-aware portfolio construction, bootstrap diagnostics, and Bayesian parameter search. The abstract already states an appropriately cautious core result: the overlay narrows the wealth distribution but delivers lower median and fifth-percentile terminal wealth than buy-and-hold EGX30, so the contribution is a risk-return characterization rather than evidence of superior terminal performance.

The main weaknesses concern evidential strength, validation design, and inferential scope. The manuscript repeatedly relies on in-sample selection and evaluation, admits that the same windows are used for optimization and reporting, and uses IID bootstrap resampling that does not preserve serial dependence. These are important limitations because the paper’s signal-generation pipeline is rich enough to invite overfitting even if the authors describe it prudently. The paper is coherent and generally methodologically honest, but its empirical claims should be narrowed further unless stronger out-of-sample validation, robustness checks, and dependence-preserving resampling are added. I do not see strong paper-mill or fabrication signals; the manuscript is internally consistent, the limitations are openly disclosed, and the data/code availability statements improve credibility.

Potential Major Revisions

  1. Strengthen the validation design and reduce in-sample circularity.

The most important concern is that the parameter-selection process and the reported performance assessment are not separated. The manuscript states in Section 2.5 that “parameter selection uses an objective aggregated over three dated calendar windows” and later acknowledges that “the reported pair is therefore the best observed evaluated candidate, not an exhaustive maximum over all 486 possible pairs” and that “the performance summary is in-sample rather than an independent validation.” This is an appropriate disclosure, but it also sharply limits the evidential status of the empirical findings.

The discussion reinforces the same issue: “Because the same calendar windows contribute to parameter selection and reported backtest results, the analysis tests the workflow in-sample rather than establishing out-of-sample predictive structure.” The conclusion is similarly restrained: “Independent evaluation is needed before making claims about the rule’s performance beyond this sample.”

These statements are commendably honest, but they also imply that any strategic-performance interpretation is preliminary. A major revision should therefore add at least one genuinely external evaluation layer: walk-forward testing, rolling-origin re-estimation, or a final untouched holdout segment. Without this, the framework is best framed as a methodological demonstration rather than as evidence that the detected phase relation can support a practical tactical-allocation rule.

  1. Clarify the epistemic status of the lead-lag claim and avoid over-reading phase delay as actionable predictability.

The manuscript is careful in some places, but the phrasing still risks implying more than the evidence establishes. In the abstract, the paper claims that “a coherent medium-horizon region appears near an 84-trading-day cycle; under the stated phase convention, its estimated delay is consistent with an EGX100EWI lead of roughly 2–3 trading days.” In Results, the same point appears as: “the estimated phase-delay profile remains near zero for short cycles and becomes negative in the medium-horizon region, reaching approximately −2 to −3 trading days around that band. Under the phase convention defined above, this estimate is consistent with an EGX100EWI lead at that frequency.”

However, the manuscript also states that “the global cross-correlation does not independently confirm the frequency-specific phase delay.” This creates a tension: the phase-based lead is the central interpretive novelty, but independent corroboration appears limited. The discussion is appropriately cautious when it notes that comparisons with broader literature “motivate further testing; they do not establish causal transmission in the present sample.”

A major revision should tighten the language throughout the paper so that phase delay is consistently described as a frequency-domain synchronization feature rather than predictive evidence per se. The authors should also add robustness checks showing whether the 84-day feature persists under alternative segment lengths, tapers, overlap settings, and nearby band definitions. Otherwise, the lead-lag interpretation may be too sensitive to methodological choices.

  1. Address model-selection risk created by a flexible pipeline.

The workflow combines several tuning-sensitive components: Welch estimation, candidate-cycle identification, adaptive band-pass design, execution lag selection, transaction costs, and a consensus objective optimized by Bayesian search. Section 2.5 defines the search over T ∈ {40, …, 120} and ℓ ∈ {0, …, 5}, while noting that only 60 objective evaluations with 15 random initializations are used. This is computationally reasonable, but it increases sensitivity to search path and score-surface irregularities.

The manuscript itself notes that “the reported pair is the best observed evaluated candidate; the apparent neighboring high-score region is descriptive rather than an uncertainty interval.” That is precisely why a major revision should quantify selection uncertainty more explicitly. Examples include repeated optimization with different seeds, stability analysis of the selected pair, or reporting the top-k candidate regions rather than only the best observed pair. At present, the chosen 40-day cycle with zero lag may reflect the objective’s local geometry more than robust structural signal.

  1. Reconsider the inferential value of the IID bootstrap.

Section 2.4 is admirably explicit: “Because this bootstrap resamples single-period returns independently, its output is a marginal distributional diagnostic” and “does not provide time-series-valid probabilities of outperformance under serial dependence or regime persistence.” The Results section likewise states that the reported frequencies are “conditional frequencies under the specified IID resampling scheme, not predictive probabilities under serial dependence.”

This transparency is a strength, but the paper still gives these diagnostics substantial visual and interpretive weight. Because the strategy’s purpose depends on dynamic structure, an IID bootstrap is a weak approximation for the question the manuscript wants to answer. A major revision should either (a) downgrade these results more strongly in the narrative, or (b) add block bootstrap, stationary bootstrap, or another dependence-preserving resampling procedure. That would better align the diagnostic method with the serially ordered phenomenon under study.

  1. Expand the economic rationale for the allocation rule.

The target rule in Section 2.3 is very simple: “the market is fully held when the filtered slope is positive and half held otherwise.” That simplicity helps interpretability, but the manuscript gives limited economic justification for why the underweight state is fixed at 1/2 rather than cash, a lower bound, or a continuously scaled exposure. Since the strategy underperforms buy-and-hold in median and fifth-percentile terminal wealth, the exact exposure architecture matters materially. The paper should explain whether 1 and 1/2 were chosen ex ante for institutional plausibility, turnover control, drawdown management, or convenience. If not, readers may suspect hidden specification arbitrariness.

  1. Sharpen the contribution claim relative to novelty.

The introduction says that “the paper contributes to computational economics through an integrated procedure for identifying and evaluating cross-benchmark dependence.” This is plausible, but the actual novelty appears to lie less in any single methodological component and more in the combination and application to Egyptian equity benchmarks. The conclusion also states that “the contribution is methodological and interpretive.” A major revision should make this narrower contribution explicit. As written, the framing sometimes approaches a broader methodological innovation claim than the evidence supports. The paper would be stronger if it clearly positioned itself as an application-driven synthesis with a transparent empirical workflow.

Potential Minor Revisions

  1. Typographic, grammatical, and style issues
Location Issue Comment
Title page / author block Style inconsistency “KNOWDYN Ltd, N17GU London, United Kingdom” appears compressed and may need standard postal formatting or institutional style normalization.
Abstract Overlong sentence structure The sentence beginning “Using aligned daily observations on the EGX100 Equally Weighted Index and the EGX30...” is dense and could be split for readability.
Introduction, p. 1 Repetition / heaviness The phrase “The present study...” appears multiple times in close proximity, which slightly reduces stylistic economy.
Section 2.1, p. 2 Notational density The notation around equations (1)–(4) is correct but visually crowded; brief prose interpretation after each main expression would improve readability.
Section 2.2, p. 3 Possible rendering artifact “X(f b )Y ∗ (f )” appears to contain PDF extraction spacing artifacts around the Fourier notation. The typeset version should be checked carefully.
Figure captions Caption informativeness Several figure captions are accurate but terse. For example, Figures 5–7 could specify the exact sample horizon or key parameter settings directly in the caption.
Discussion, p. 10 Slight conceptual redundancy The manuscript reiterates several times that the analysis is in-sample. This is substantively good, but minor stylistic compression would improve flow.
References Capitalization inconsistency Several titles in the references use inconsistent capitalization conventions, e.g., “Do gulf stock markets share time varying connectedness” and “The impact of covid-19...” These should match the target journal style.
  1. Formatting issues
Location Issue Comment
Equations and symbols throughout Symbol explanation Some symbols are defined correctly but not always re-anchored in prose when reused later, increasing reader burden in Sections 2.3–2.5.
Figure integration Cross-reference support The narrative references Figures 2–7, but the paper would benefit from more direct interpretation immediately under each figure in the surrounding text.
Section hierarchy Balance Section 2 is methodologically detailed, whereas the Introduction is somewhat literature-heavy. Rebalancing could improve pacing.
End matter Reproducibility placement Data Availability and Code Availability are useful and should perhaps be moved earlier or mentioned in Methods to reinforce reproducibility.
  1. AI content analysis for this post-2021 manuscript

Estimated percentage of AI-generated content: 18–32%

This is only a stylistic estimate, not a forensic determination. My estimate is driven by the manuscript’s highly regular sentence rhythm, polished hedge language, and repeated metadiscursive clarification patterns. Examples include formulaic balancing statements such as “These estimates answer different questions,” “The findings therefore characterize a risk-return trade-off,” and “they do not establish causal transmission or out-of-sample predictive value.”

Highlighted AI-susceptible sections

Location Quoted example Why it appears AI-susceptible
Abstract “These estimates answer different questions: the spectral result describes frequency-specific synchronization, whereas the selected parameter maximizes the stated in-sample objective.” Highly balanced explanatory prose with polished contrast structure.
Introduction, p. 2 “Its computational design links detection, signal translation, execution, and evaluation.” Compact enumerative phrasing common in AI-assisted scientific editing.
Discussion, p. 9 “It converts descriptive spectral evidence into an interpretable decision rule for an in-sample backtest.” Very smooth summary compression, stylistically generic.
Conclusion, p. 11 “The contribution is methodological and interpretive.” Crisp, abstract framing statement with editorial polish.

Assessed epistemic impact

The likely impact, if AI assistance was used, appears low to moderate and concentrated in exposition rather than in the core technical content. I do not see obvious signs that technical claims, equations, or citations are incoherent in the way paper-mill outputs often are. On the contrary, the manuscript repeatedly self-limits its claims and openly notes methodological constraints, which argues against deceptive inflation. The main epistemic risk is not AI use itself, but that polished language may make the results appear stronger or more settled than their validation design justifies. So the appropriate response is not suspicion of fraud, but stricter demand for external validation and robustness analysis.

  1. Anti-fraud / coherence screening

I do not detect strong paper-mill traits. The manuscript fits a recognizable computational-finance paradigm: aligned daily index returns, spectral dependence analysis, causal filter construction, transaction-cost-aware backtesting, and bootstrap diagnostics. The internal logic is coherent, the limitations are explicitly admitted, and reproducibility is partly supported through stated data and code availability.

That said, one warning is warranted: the methodological sophistication of the pipeline exceeds the strength of the validation evidence. This is not evidence of fabrication, but it does create a presentational asymmetry in which a complex workflow may appear more confirmatory than it is. The authors should reduce that asymmetry by adding stronger out-of-sample and robustness checks.

Recommendations

  1. Reframe the paper explicitly as a methodological demonstration with exploratory empirical findings unless a genuine holdout or walk-forward validation is added.

  2. Add a dedicated robustness subsection testing sensitivity to Welch segment length, tapering/overlap choices, phase convention, band-width choice around T, transaction-cost assumptions, and optimization seed variation.

  3. Separate signal discovery from strategy validation. For example, identify spectral features on an earlier subperiod, calibrate the rule on a middle subperiod, and evaluate performance only on a final untouched subperiod.

  4. Replace or complement the IID bootstrap with dependence-preserving resampling, and report whether the qualitative risk-return conclusions survive.

  5. Provide a stronger economic rationale for the 1 versus 1/2 exposure rule and compare it with at least two nearby alternatives.

  6. Report selection uncertainty more fully: top-ranked parameter pairs, near-optimal score regions, and stability across repeated optimization runs.

  7. Maintain the manuscript’s current caution about causality and prediction, but enforce that caution uniformly in the abstract, introduction, results, and conclusion so that no sentence can be read as implying validated predictability.

  8. Keep the reproducibility assets prominent. The Data Availability and Code Availability statements are valuable and should be leveraged more centrally in the methodology narrative.

Overall, I judge the manuscript as coherent, technically serious, and potentially publishable after substantial revision, but not yet sufficiently validated for strong empirical claims about actionable lead-lag structure or performance.

Reviewer3 (AI review)

November 19, 2026

AI Review (reviewer3.com)

Overview

Cross-Benchmark Spectral Allocation Framework

Contribution

This study develops an end-to-end computational framework combining spectral coherence, causal band-pass filtering, friction-aware allocation, and regime-consensus optimization to extract and evaluate timing signals between equity benchmarks.

Horizon-Specific Lead–Lag Identification

Contribution

The authors identify frequency-specific synchronization between Egyptian equity benchmarks, demonstrating an 84-day cycle where the EGX100 Equally Weighted Index leads the EGX30 by approximately two to three trading days.

Friction-Aware Tactical Risk Diagnostics

Contribution

The analysis demonstrates that while a frequency-based tactical overlay narrows simulated terminal wealth dispersion, execution costs and timing dynamics prevent it from outperforming a buy-and-hold strategy in median terminal wealth.

Comments (13)

1. Symbol drift for cycle period, lag, turnover, and consensus score — Editorial

To prevent parameter selection from being driven by a single favorable window, a structural-

Key model quantities change symbols across the prose, Figure 1, and Figure 5 without notice: (1) the candidate cycle period and execution lag are denoted (T,ℓ)(T, \ell) in Section 2.3 and Section 2.5, (λ,τ)(\lambda, \tau) in Figure 1, and (λ,ω)(\lambda, \omega) in Figure 5 (where Panel B labels the vertical axis "Phase Lag (ω\omega)"); (2) using τ\tau for execution lag in Figure 1 conflicts with Equation (16) in Section 2.3, which defines τt=∣wt−wt−1∣\tau_t = |w_t - w_{t-1}| as portfolio turnover; and (3) Equations (28)–(29) define Φr\Phi_r as the single-window risk-adjusted score and Ψ\Psi as the multi-window geometric-mean consensus score, whereas Panel C of Figure 5 labels the vertical axis "Phi Score (Φ\Phi)" while plotting the consensus score Ψ\Psi values (0.0400.040 to 0.0700.070).

2. Parameter search domain and evaluation count mismatch Figure 5 — Editorial

Let T ∈ { 40 , . . . , 120 } denote a candidate cycle period in trading days and let ℓ ∈ { 0 , . . . , 5 } denote a candidate execution lag. For each

Section 2.5 (and Figure 1) states that the candidate cycle period is searched over T∈{40,…,120}T \in \{40, \dots, 120\} trading days (which, combined with ℓ∈{0,…,5}\ell \in \{0, \dots, 5\}, yields the stated 81×6=48681 \times 6 = 486 possible parameter pairs) using "60 objective evaluations." However, Figure 5 contradicts both specifications: in Panel A ("Bayesian Convergence"), the search trace runs for only 40 iterations (from n=1n = 1 to 4040) rather than 60; and in Panels B and C, the evaluated candidate cycle periods and fitted surface span [30,100][30, 100] trading days (with multiple evaluated points plotted between 3030 and 4040, and none above 100100) rather than [40,120][40, 120].

3. Opposite lag-sign conventions for cross-correlation between text and Figure 4 — Editorial

Under this lag convention, positive k indicates that EGX100EWI leads EGX30.

In Section 2.2, Equation (11) defines the normalized time-domain cross-correlation as ϱxy(k)=∑t∈Ik(xt−xˉ)(yt−k−yˉ)Nkσxσy\varrho_{xy}(k) = \frac{\sum_{t \in I_k} (x_t - \bar{x})(y_{t-k} - \bar{y})}{N_k \sigma_x \sigma_y}, where xtx_t is the demeaned EGX30 return and yty_t is the demeaned EGX100EWI return, and the accompanying text explicitly states that "positive kk indicates that EGX100EWI leads EGX30." However, in the lower-right panel of Figure 4 ("Global Time-Domain Cross-Correlation (CCF)"), the horizontal axis is labeled "Lag Interval (Days) [+ = EGX30 Leads]", assigning the opposite directional meaning to positive lags.

4. Coherence and phase estimates lack statistical significance bounds — Major

peak before conversion to a delay. Dominant cyclical relations are identified from local maxima of C xy ( f ) subject to a minimum coherence threshold of 0 . 2, and the strongest peaks are ranked by coherence. This threshold screens out visually negligible comovement; it is not a formal significance test. Candidate peaks are compared with the time-domain cross-correlation as a

With a sample spanning roughly four years (~1,000 trading days) and a Welch segment length of L=252L = 252 with 50% overlap, the spectral estimates rely on only around 7 overlapping segments, under which sample magnitude-squared coherence is substantially upward biased and phase variance can be large. Without null significance thresholds for coherence or confidence intervals on the phase delay d(f)d(f) at T≈84T \approx 84 days, the analysis cannot distinguish a genuine 2–3 day lead from finite-sample estimation noise.

5. Unnecessary surrogate approximation on a 486-point grid — Major

where Geval\mathcal{G}_{\text{eval}} is the set of parameter pairs actually evaluated by Gaussian-process Bayesian optimization, using 60 objective evaluations and 15 random initializations [28]. The reported pair is therefore the best observed evaluated candidate, not an exhaustive maximum over all 486 possible pairs.

The discrete candidate space consists of only 81×6=48681 \times 6 = 486 parameter pairs, for which a fourth-order linear recursion over ~1,000 observations takes less than a second to evaluate exhaustively. Sampling only 60 points via Bayesian optimization introduces avoidable approximation uncertainty, and Figure 5A stops at iteration 40 rather than the 60 evaluations stated in the text.

6. One-sided causal Butterworth filter introduces unaccounted phase distortion — Critical

The filtered component c t is generated by a Butterworth band-pass filter implemented in one- sided form using SciPy’s butter(..., btype=’band’) and lfilter [27].

The framework motivates signal extraction via spectral phase delay, yet uses a one-sided IIR Butterworth filter (lfilter) that inherently introduces a frequency-dependent non-linear phase delay (group delay) across the pass band. Because this internal filter lag is not quantified or reconciled with the 2–3 day spectral lead and execution lag ℓ\ell, it is unclear what effective time displacement the causal slope signal mtm_t actually represents.

7. Historical backtest metrics defined in methods are omitted from results — Major

and annualized volatility and Sharpe performance are reported in the standard form σann(q)=252 sd(qt)\sigma_{\text{ann}}(q) = \sqrt{252}\,\text{sd}(q_t), SR(q)=252 E[qt]sd(qt)\text{SR}(q) = \sqrt{252}\,\frac{\mathbb{E}[q_t]}{\text{sd}(q_t)}

Equation (19) and Equation (20) formally define the realized historical wealth indices WtB,WtSW_t^B, W_t^S, annualized volatility σann(q)\sigma_{\text{ann}}(q), and Sharpe ratio SR(q)\text{SR}(q), yet none of these realized in-sample values are reported anywhere in Section 3. Reporting the actual historical performance alongside the IID bootstrap summaries is essential for evaluating what the strategy achieved on the realized data.

8. Inconsistency between text and Figure 5 parameter search bounds — Major

Let

The text specifies the candidate cycle period domain as T∈{40,…,120}T \in \{40, \dots, 120\} trading days, and concludes that the optimum is at the boundary T∗=40T^* = 40. However, Figure 5 (Panels B and C) plots the evaluated parameter domain over T∈[30,100]T \in [30, 100] trading days, leaving it ambiguous which search space was actually used and whether cycles below 40 days were tested or excluded.

9. Comparing optimized 40-day rule without reporting 84-day backtest metrics — Major

The diagnostic backtest uses a medium-horizon band corresponding to periods between 60 and 100 trading days, centered on the coherent 84-day cycle. The local

The paper describes a diagnostic backtest centered on the 84-day spectral cycle (60–100 day pass band) in Section 2.3, but never reports its performance metrics, consensus score, or wealth distribution in Section 3. Without showing the performance of the 84-day cycle with a 2–3 day lag, the reader cannot directly compare the spectral candidate against the selected (40,0)(40, 0) configuration.

10. Exact sample size and regime observation counts are omitted — Critical

Let Pt(30)P_t^{(30)} denote the closing value of the EGX30 index and let Pt(100)P_t^{(100)} denote the closing value of the EGX100 Equally Weighted Index on the common trading-day support t=1,…,Nt = 1, \dots, N, where the sample is formed by the inner alignment of the two daily series.

The manuscript defines the aligned trading-day support as t=1,…,Nt = 1, \dots, N and partitions it into three calendar windows R1,R2,R3\mathcal{R}_1, \mathcal{R}_2, \mathcal{R}_3, but never reports the integer value of NN, the effective trimmed length TST_S, or the sample sizes within each window. Reporting these exact observation counts is necessary to assess the statistical reliability of the Welch spectral averages and the empirical 5% tail quantiles (CVaR0.05,r\text{CVaR}_{0.05,r}) in each window.

11. Inconsistent finite-difference and padding rules between optimization and backtest — Major

which serves as a causal momentum proxy. In the optimization layer, the same local slope is implemented numerically by the discrete gradient operator applied to c t , which is equivalent to a first-order finite-difference representation up to endpoint conventions. At each decision date

In the optimization layer, the slope mtm_t is computed using a discrete gradient operator (central difference in the interior, which uses ct+1c_{t+1} and is not strictly causal) and undefined leading positions are padded with 1/21/2, whereas the diagnostic backtest uses backward differences mt=ct−ct−1m_t = c_t - c_{t-1} and trims leading positions. Even though ℓ∗=0\ell^* = 0 is selected, using a non-causal central difference operator during parameter search means the objective Ψ(T,ℓ)\Psi(T, \ell) is not evaluating the strictly causal rule defined in Equation (13).

12. Absence of a passive 75%-exposure or constant-mix benchmark — Major

EGX100EWI. The target portfolio weight is defined by w ∗ t =    1 , if m t > 0 , 1 2 , if m t ≤ 0 , (14) so that the market is fully held when the filtered slope is positive and half held otherwise. If

Because the strategy switches strictly between wt=1w_t = 1 and wt=0.5w_t = 0.5, its average market exposure is mechanically around 0.75, which naturally reduces return variance and terminal wealth dispersion during a strong bull market (where EGX30 tripled) regardless of any cyclical timing skill. Without benchmarking against a static fractional exposure (e.g., a constant 75% weight in EGX30) or random switching of equal turnover, it is impossible to tell whether the narrower wealth distribution reflects genuine cyclical conditioning or simple deleveraging.

13. Unpaired bootstrap resampling distorts comparative dominance frequency — Major

trimming for alignment and lag. For each replication m = 1 , . . . , M , daily returns are resampled with replacement from either the benchmark sequence { r (30) t } or the strategy sequence { n t } , and cumulative wealth is formed as

In Section 2.4, daily returns appear to be resampled independently from the benchmark sequence {rt(30)}\{r_t^{(30)}\} and the strategy sequence {nt}\{n_t\}, rather than resampling paired dates (rt(30),nt)(r_t^{(30)}, n_t) jointly. Because ntn_t is either 1.0rt(30)1.0 r_t^{(30)} or 0.5rt(30)0.5 r_t^{(30)} minus turnover costs on the exact same market day, unpaired resampling breaks the strong contemporaneous coupling between the overlay and the index, invalidating the reported 3.1% comparative frequency (Strat > B&H) and the median delta in Figure 7.

XSci (AI review)

November 19, 2026

Summary

The manuscript asks whether dependence between two overlapping Egyptian benchmarks, the EGX30 and the EGX100 Equally Weighted Index, carries horizon-specific timing information that can be traded. Welch coherence and phase on aligned daily returns give an implied delay; a causal Butterworth band-pass signal from EGX100EWI returns drives a two-state weight on the EGX30 under a 40 basis point friction; parameters are chosen by Bayesian optimization of a geometric-mean score over three calendar windows, and outcomes assessed by an IID bootstrap. Reported are a coherent region near an 84-day cycle implying an EGX100EWI lead of 2–3 days, a selected 40-day cycle with zero execution lag, and an overlay with narrower wealth dispersion but lower median (2.39x versus 3.34x) and fifth-percentile (1.42x versus 1.68x) terminal wealth than the benchmark.

Contribution and Significance

The contribution is an applied pipeline rather than a method or a finding: Welch coherence and phase, a SciPy Butterworth filter, GP Bayesian optimization and an IID bootstrap, all off the shelf, with no estimator derived and no new data. What is new is the object of study, the phase relation between two benchmarks of one under-studied exchange. Against the closest cited work — the multi-resolution comovement analyses of Dewandaru et al. [31,32], Rehman et al. [33] and Smolo et al. [37] — it substitutes Welch coherence for wavelets and adds friction accounting: a change of application, not an advance.

The economics is largely absent. EGX30 is cap-weighted and blue-chip, EGX100EWI broad and equally weighted, yet the manuscript never reports their constituent overlap or liquidity gap, and never asks whether a 2–3 day phase relation between a liquid and an illiquid portfolio could be mechanical. The literature bearing on this is uncited: Lo and MacKinlay (1990), "An Econometric Analysis of Nonsynchronous Trading," Journal of Econometrics 45(1–2), 181–211; Lo and MacKinlay (1990), "When Are Contrarian Profits Due to Stock Market Overreaction?", Review of Financial Studies 3(2), 175–205; and Chordia and Swaminathan (2000), "Trading Volume and Cross-Autocorrelations in Stock Returns," Journal of Finance 55(2), 913–935.

Strengths

  • The manuscript is unusually candid: it labels the backtest in-sample (Sections 2.5, 4) and notes that the cross-correlogram "does not independently confirm the frequency-specific phase delay" (Section 3).
  • Section 2.3 and Equations (12), (15)–(18) pin down the filter recursion, lag, turnover and cost conventions precisely enough to reproduce.
  • Frictions enter the selection objective itself (Equations (18), (25)–(29)) rather than being applied after the fact.
  • The authors report a negative result — Figure 7's inset shows the overlay beating buy-and-hold in 3.1% of simulations — and deposit data and notebook (Zenodo record 19697766).

Recommendation

Reject for the leading journals of the field. The advance over prior work is too small: standard components, one market, two series, the economic question unengaged. Independently, the evidence does not convincingly support either empirical claim the paper rests on — the 84-day phase relation has no measure of its precision and sits inside a single Fourier bin, and the selected 40-day cycle is a corner solution produced by a bandwidth artefact in Equation (24). The candour about what has not been established is genuine, but the disclaimers describe what is missing rather than supply it.

Major Concerns

  1. The spectral result has no measure of precision, and its resolution cannot support the claim (Section 2.2, Equations (6)–(10); Figure 4). With L = min{252, N}, the Welch frequency grid is k/252, so the resolvable medium-horizon periods are 126, 84, 63 and 50.4 days. The "coherent region near 80 to 90 trading days" is thus exactly one bin, 252/3 = 84: the reported cycle length reflects the segment length, not a localized feature. Neither N, the sample dates, nor the segment count is reported, and no confidence band is given for coherence or delay. With coherence near 0.85 and roughly seven 50%-overlapping segments in a four-year daily sample, the standard phase-error expression gives about 0.11 radians, or 1.5 days at an 84-day period, so the claimed 2–3 day lead lies within two standard errors of zero; Figure 4's own cross-correlogram is flat within ±0.1 at every nonzero lag. The 0.2 screening threshold compounds this: for seven segments the 5% null coherence level is near 0.39, so peaks marked "dominant coherent cycles" include values indistinguishable from noise. Confidence bands, a null level corrected for the number of frequencies examined, and stability of the peak to L are all needed.

  2. The selected 40-day cycle is a corner solution created by Equation (24) (Section 2.5; Figure 5). Fixing a ±15-day half-width in period does not fix bandwidth in frequency: at T = 40 the band spans f from 0.0182 to 0.0400, a width of 0.0218 cycles per day, while at T = 120 it spans 0.00741 to 0.00952, a width of 0.00211 — ten times narrower. Short candidates therefore pass an order of magnitude more spectral power and give a more responsive signal, biasing the objective toward them by construction. The manuscript asserts the opposite, that the half-width "prevents the optimization from comparing filters of substantially different widths" and "provides a common comparison scale across candidate periods"; Equation (24) contradicts both. The selected T* = 40 is the lower endpoint of T ∈ {40, …, 120}, and Figure 5C shows the fitted trend still rising as T falls toward it — the signature this bias predicts. "A 40-day cycle" therefore cannot be read as an identified horizon; re-running the search at constant fractional bandwidth would show whether an interior optimum exists at all.

  3. The performance comparison is not a valid comparison (Sections 2.3, 2.4; Figures 6, 7). Equation (14) de-risks to a weight of one half, and Section 2.3 works "under a zero risk-free-rate assumption," so the uninvested half earns nothing. Over this sample the Central Bank of Egypt's overnight deposit rate ran from 16.25% at end-2022 to 27.25% through much of 2024 and near 20% in 2025; crediting the cash leg at even a conservative domestic short rate would add several points a year and could reverse the fifth-percentile gap of 1.42x against 1.68x on which the downside conclusion rests. Separately, Section 2.4 resamples "from either the benchmark sequence or the strategy sequence," that is independently, although the strategy return is by construction a near-deterministic function of the same-period benchmark return. Breaking that pairing makes the reported 3.1% frequency of the strategy beating buy-and-hold an artefact of comparing independent draws of two highly correlated series; the disclaimers address serial dependence but not this. A paired bootstrap and an interest-bearing cash leg are needed before any risk-return conclusion follows.

  4. The contribution is not placed against the literature that would explain it (Sections 1, 4). A phase relation between a liquid cap-weighted index and an illiquid equally weighted one is exactly the setting in which nonsynchronous trading and speed-of-adjustment effects generate cross-autocorrelation; the three works named above are the standard references and none is in the reference list. Non-trading effects predict that the equally weighted index should lag, not lead, and the opposite sign is reported without comment. With no constituent overlap and no liquidity measure given, the manuscript cannot say whether it has found an economic lead–lag relation, a microstructure artefact, or an identity of index construction.

Minor Comments

  1. The manuscript never says which configuration Figure 6 reports, yet the abstract and conclusion attribute its figures to "the selected overlay," while Figure 7, for the selected 40-day cycle, annotates a median gap of −0.87x rather than 3.34 − 2.39 = 0.95x.
  2. Figure 4's cross-correlogram panel is labelled "[+ = EGX30 Leads]" while the text after Equation (11) states that "positive k indicates that EGX100EWI leads EGX30."
  3. Section 3 places the −2 to −3 day phase trough at 80–90 days, whereas the phase panel of Figure 4 appears to show it at 40–60 days.
  4. Equation (20) defines annualized volatility and the Sharpe ratio, yet no value of either, no value of N, and no table of realized performance appears anywhere in the paper.
  5. The parameters are (T, ℓ) in the text, (λ, τ) in Figure 1 and (λ, ω) in Figure 5B, and the consensus score is Ψ in the text but "Consensus Φ" in Figures 5A and 5C.
  6. Section 2.5 states "60 objective evaluations and 15 random initializations," but Figure 5A's iteration axis appears to reach only about 40.
  7. Leading undefined lagged positions are dropped in the diagnostic backtest but filled with the 1/2 state in the optimization layer (Section 2.3), so the two runs are not from an identical pipeline.
  8. The recursion is causal, but the pass band and the T grid come from full-sample coherence, so "strictly causal" (Section 2.3) overstates what holds for the procedure.
  9. No sensitivity is reported for κ = 0.004 or the {1, 1/2} weight pair, and 40 basis points is not justified against Egyptian trading-cost evidence.
  10. The windows of Equation (23) partition the sample contiguously and Equation (29) is sensitive to where the boundaries fall, so an alternative partition should be reported.