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Conflict of Interest Disclosure

I am an independent researcher in fintech and cryptocurrency market microstructure. I have no personal, financial, or advisory relationship with any of the authors. My prior published research overlaps thematically with this paper but is not cited herein.

Summary

This paper provides a comprehensive empirical analysis of CEX-DEX arbitrage on Ethereum, spanning 19 months (August 2023 to March 2025) and 7.2 million identified arbitrage transactions. The authors refine existing heuristics for detecting CEX-DEX arbitrage, introduce a novel empirical framework for estimating arbitrage revenue without observing the off-chain CEX leg, and analyze searcher profitability, builder integration, and market centralization. The paper estimates $233.8 million in total extracted value by 19 major searchers and documents increasing concentration, with three searchers capturing approximately three-quarters of volume and extracted value. The topic is timely and important for understanding MEV supply chain dynamics under Proposer-Builder Separation (PBS). The methodology is creative and the dataset is impressive. However, the paper suffers from several methodological limitations, incomplete parameter reporting, and conclusions that occasionally overreach the evidence.

Strengths

1. Novel empirical framework for unobserved CEX execution. The core methodological contribution (inferring CEX hedge timing from the decay pattern of gross returns around the slot time) is genuinely innovative. By identifying searcher-specific "optimal execution horizons" where information advantage maximizes before market impact erodes it, the authors construct a data-driven proxy for realized arbitrage revenue without requiring proprietary CEX trade data. This addresses a central challenge in CEX-DEX arbitrage research and is likely to be influential.

2. Expanded heuristic coverage. The authors significantly expand prior heuristics by accommodating multi-swap transactions, removing the single-swap constraint, and eliminating the gas-limit and minimum-tip filters that previously excluded integrated searcher-builder pairs. This is a meaningful improvement over Heimbach et al. (2024) and Oz et al. (2024) and increases both coverage and representativeness.

3. Rich dataset and transparency. With 8.7 million detected transactions, 7.2 million included in revenue estimation, and open-sourced Dune queries, the paper sets a high bar for empirical MEV research. The 19-month span captures multiple market regimes and the dataset is among the largest in the CEX-DEX arbitrage literature.

4. Searcher-builder integration analysis. The analysis of exclusive vs. neutral searchers, profit-sharing patterns, and the mutual reinforcement of competitive positions is empirically grounded and policy-relevant. The finding that integrated searchers retain only 10 to 15 percent of revenue while neutral searchers retain 30 to 70 percent is an important result for understanding PBS economics.

5. Builder profit correction. By combining on-chain builder profits with estimated searcher PnL, the paper corrects prior underestimates of integrated builder profitability. The finding that rsync's aggregated profit margin reaches 27 percent (versus negative on-chain margins) is a meaningful refinement of Yang et al. (2025) and Oz et al. (2024).

Weaknesses

1. The optimal execution horizon assumption is untested and potentially misspecified. The paper assumes each searcher hedges at a single, searcher-specific optimal horizon t* identified from historical trades. This is a strong homogeneity assumption: it imposes identical hedge timing across all trades for a given searcher, regardless of token liquidity, trade size, market volatility, or whether the trade is a "rush" or "patient" execution. The authors acknowledge this as a "simplified approximation" but do not quantify the approximation error. For Pattern 2 searchers trading illiquid ALT tokens, where the gross return drops abruptly within 1 to 2 seconds, a single horizon may be reasonable. For Pattern 1 searchers like Wintermute with gradual 1.5-second peaks and flat interquartile bands, the variance in actual execution timing across trades could be substantial. The paper should report the cross-trade standard deviation of individual-trade peak times (not just the median) to validate the homogeneity assumption. Without this, the revenue estimates are upper bounds with unknown tightness.

2. The markout methodology ignores hedge price impact and inventory risk costs. The gross return GR(t) is computed using CEX mid-prices at the markout horizon, not the actual execution price the searcher obtains. For Pattern 1 searchers executing large volumes in major tokens, the market impact of the CEX hedge could be significant. Almgren and Chriss (2000) and Bertsimas and Lo (1998), cited in Section 4.1, explicitly model execution costs that the paper does not incorporate. The authors state they neglect "the price impact of hedging, particularly relevant for low-liquidity tokens," but the issue is equally relevant for high-liquidity tokens at large trade sizes. Wintermute's $74.8 billion in volume with $11.36 median trade size implies many trades far exceed the median; the price impact on these large trades is material. The paper's revenue estimates are therefore upper bounds that may overstate true profitability, and the degree of overstatement is unquantified.

3. The "inventory adjustment trade" filter lacks validation. The paper excludes 683,539 transactions (7.8 percent of detected trades) as "inventory adjustments" because their markout revenue fails to cover base fees throughout the examined interval. This is a consequential filter: for SCP, it removes 142,086 of 2,188,986 trades (6.5 percent); for Caitlyn, it removes 5,750 of 12,173 trades (47.2 percent). The authors state these trades pay "much lower tips to builders" but do not establish that low tips are a reliable signal of non-arbitrage activity. Integrated searchers may pay low or zero tips to their affiliated builders (as noted in Appendix F.2, where the minimum-tip heuristic was removed precisely for this reason). The filter may systematically exclude integrated searcher trades that are genuine arbitrages but carry minimal builder payments, biasing the sample toward non-integrated searchers. A validation exercise (for example, comparing a random sample of excluded trades against known integrated-searcher transaction patterns) would strengthen confidence in the filter.

4. Pattern 3 searchers are excluded from revenue estimation without adequate justification. The paper excludes Bard, Jinx, Tristana, and Lux (2.7 percent of transactions) because their gross return curves are flat and "no clear peak-then-decay point emerges." The interpretation is that these searchers "hold their inventory and do not hedge their positions on CEX within this window." But an alternative explanation is that these searchers hedge via OTC desks, internal inventory nets, or cross-DEX arbitrage rather than CEX, in which case the markout methodology simply does not apply to them. The paper does not test this alternative. Excluding them from revenue estimation while retaining them in descriptive figures creates an inconsistency: the centralization narrative (three searchers capturing 73 percent of extracted value) is computed on a denominator that omits 2.7 percent of trades whose revenue is unknown. If Pattern 3 searchers are actually highly profitable, the concentration statistics could change materially.

5. The HHI centralization narrative lacks a benchmark or statistical test. The paper reports HHI indices for volume and extracted value and states the market is "highly centralized" by Q1 2025. But HHI is a descriptive statistic, not a test. The paper does not compare observed HHI trajectories against a null model (for example, random allocation, proportional growth, or Polya urn processes), nor does it test whether the increase in HHI is statistically significant. The "turning point" around June 2024 is identified visually, not via structural break tests. Without formal inference, the claim of "increasing centralization" is suggestive but not established.

6. The causal claim about Kayle-Titan mutual reinforcement rests on correlation, not causation. Section 7.3 reports a contemporaneous Spearman correlation of ρ = 0.74 (p < 0.0001) between Kayle's volume share in Titan blocks and Titan's market share, with lagged correlations showing predictive effects in both directions. The authors interpret this as "mutually reinforcing exclusivity partnership" and "feedback loop." But the lagged correlations (ρ = 0.655 at 1-day lag, declining to 7 days) are consistent with any persistent common driver (for example, overall CEX-DEX arbitrage volume, Ethereum price volatility, or Binance funding rate dynamics) that affects both variables simultaneously. The paper does not control for confounders or use instrumental variables to isolate causal effects. The claim that "larger Kayle flow in one day brings larger tip revenue for Titan and enlarges Titan's builder surplus, enhancing Titan's bidding power in subsequent days" is a plausible mechanism but not a demonstrated one. The reverse effect ("higher market share for Titan subsequently increases Kayle's market capture") is even harder to justify causally: Titan's market share does not directly create arbitrage opportunities for Kayle. The correlation could reflect Kayle's growth driving Titan's share, not reciprocal reinforcement.

7. The builder subsidy analysis is confounded by the Ultra Sound bid adjustment mechanism. Section 8 and Appendix G define subsidized blocks as those where both on-chain builder profit and aggregated profit are negative. But the Ultra Sound bid adjustment mechanism (introduced December 2023) systematically alters builder profits by refunding a fraction of the bid delta. The refund rate changed from 100 percent to 50 percent on March 5, 2024, creating a structural break in the profit calculation. The paper does not test whether subsidy rates differ before and after this change, or whether the apparent 15 percent reduction in subsidies after "correction" is driven by the refund rate change rather than by genuine economic behavior. Without disaggregating by refund regime, the subsidy comparison is uninterpretable.

8. The conclusion's policy implications overreach the evidence. The paper recommends shorter block times (EIP-7782), Orderflow Auctions, BuilderNet, and MEV capture/burn mechanisms as mitigations. But the paper provides no empirical analysis of these mechanisms. The claim that shorter block times "may lower the absolute value extractable" but "it is less clear that shorter block times would meaningfully shift the market structure" is speculative. The paper does not model how entry barriers or economies of scale would respond to shorter block times. Similarly, the dismissal of OFAs and BuilderNet as having "uncertain" impact on the upstream searcher market is a reasonable caution, but the paper offers no framework for evaluating this uncertainty. These recommendations read as standard MEV-literature talking points rather than conclusions derived from the paper's own analysis.

9. Standard errors and confidence intervals are not reported for key estimates. The paper reports point estimates for total extracted value ($233.8M), searcher-specific revenues, and profit margins, but provides no uncertainty quantification. Given the multiple approximations in the revenue estimation (optimal horizon assumption, mid-price instead of execution price, inventory adjustment filtering), the sampling distribution of these estimates is wide and asymmetric. Bootstrap confidence intervals or Bayesian credible intervals would communicate the reliability of the headline figures. Without them, the precision of the estimates is overstated.

10. The "upper-bound" framing is inconsistently applied. The paper states that estimated PnL is "an upper-bound estimate" due to unobserved hedge costs, but then treats point estimates as exact in subsequent analyses (HHI calculations, profit margin comparisons, builder subsidy corrections). If the estimates are upper bounds, the HHI and concentration statistics computed from them are also upper-bound-dependent. The paper does not conduct sensitivity analysis (for example, assuming hedge costs of 5 bps, 10 bps, or 20 bps) to show how robust the centralization and profitability conclusions are to estimation error. A single "upper-bound" disclaimer is insufficient when the bounds are never quantified.

Recommendation

Minor revisions required. The paper makes a significant empirical contribution and the methodology is innovative. The issues identified are limitations rather than fatal flaws, but they should be addressed to prevent overstatement of the evidence.

Before resubmission, the authors should:

1. Quantify the optimal execution horizon assumption. Report cross-trade standard deviations of individual-trade peak times for each searcher. If heterogeneity is high, consider searcher-size- or token-liquidity-specific horizons rather than a single horizon per searcher.

2. Bound the hedge price impact error. Provide a sensitivity analysis assuming CEX execution at the bid-ask spread (not mid-price) and incorporating estimated market impact for large trades. Report how total extracted value and searcher rankings change under conservative execution cost assumptions.

3. Validate the inventory adjustment filter. Compare a random sample of excluded trades against known integrated-searcher patterns to test whether the filter systematically removes genuine arbitrages.

4. Include Pattern 3 searchers in sensitivity analysis. Estimate revenue for Pattern 3 searchers under alternative assumptions (for example, they hedge at +10 seconds, or their revenue equals the flat gross return level) and report how concentration statistics change.

5. Formalize the centralization test. Apply a structural break test (Bai-Perron, ICSS) to the HHI time series, or compare observed HHI against a null model of random allocation. Report whether the June 2024 "turning point" is statistically identified.

6. Cautiously reframe the Kayle-Titan causal claims. Replace "mutually reinforcing" and "feedback loop" with "strongly correlated" and "consistent with mutual reinforcement." Acknowledge confounding by common drivers and state that causal identification requires further research.

7. Disaggregate builder subsidy analysis by Ultra Sound refund regime. Test whether subsidy rates differ before and after March 5, 2024, and report whether the "correction" effect is robust to the refund rate change.

8. Add uncertainty quantification. Report bootstrap 95 percent confidence intervals for total extracted value, searcher-specific revenues, and HHI indices. State the sensitivity of headline figures to estimation assumptions.

9. Tighten policy recommendations. Remove speculative claims about EIP-7782 and OFAs unless supported by the paper's own analysis. Focus recommendations on what the data directly show: the scale of CEX-DEX extraction, the profit-sharing asymmetry between integrated and neutral searchers, and the need for transparency in searcher-builder arrangements.

10. Report estimation software and version. State whether the analysis used Python (pandas, numpy), R, Dune SQL, or other tools, and cite versions. This aids replication and allows readers to verify the heuristics implementation.

Guidance for Authors: Literature Engagement

The paper's literature review is comprehensive but could be tightened thematically. Three clusters would improve coherence:

(a) CEX-DEX arbitrage identification and measurement: Heimbach et al. (2024), Oz et al. (2024), Chan et al. (2023), Chen et al. (2023).

(b) MEV supply chain and PBS economics: Daian et al. (2019), Yang et al. (2025), Gupta et al. (2023), Wahrstätter et al. (2023), Wu et al. (2024).

(c) Market microstructure and optimal execution: Almgren and Chriss (2000), Bertsimas and Lo (1998), Barclay and Warner (1993), Korajczyk and Murphy (2019).

The current review mixes these freely. Separating them would clarify how the paper bridges arbitrage detection (cluster a), blockchain infrastructure (cluster b), and traditional finance execution theory (cluster c).

For the Editor

This is a strong empirical paper with a novel methodology. The dataset is impressive and the findings on searcher-builder integration are policy-relevant. The issues identified above are standard limitations for pioneering empirical work in an opaque market and do not undermine the paper's core contribution. With minor revisions to bound estimation error, formalize centralization tests, and cautiously reframe causal claims, this paper would be suitable for publication in a top-tier venue in blockchain economics or financial market microstructure.

Final Note to the Authors

The CEX-DEX arbitrage space is "the darkest part of the MEV dark forest," and your empirical framework for illuminating it is a significant methodological advance. The scale of extraction ($233.8M) and the concentration of rewards among integrated searcher-builder pairs are findings that should inform protocol design and regulatory attention. Addressing the limitations above (particularly quantifying the estimation error bounds and formalizing the centralization tests) will make this a landmark paper in the MEV literature. I encourage you to undertake these revisions and resubmit.

Competing interests

The author declares that they have no competing interests.

Use of Artificial Intelligence (AI)

The author declares that they used generative AI to come up with new ideas for their review.