Reviewer3 (AI review)

September 30, 2026

AI Review (reviewer3.com)

Comments (7)

1. Equation 5 control variable mismatch with Table 4 — Editorial

context. Following Liao et al. (2022), we use the previous month’s fund return as a proxy for recent price movements and additionally control for the logarithms of hold- ing position and holding duration. The dependent variable is the percentage change

Equation 5 on page 18 includes the control variable $\eta \log(|Holding\ period\ return_{i,f,t-1}|)$, indicating that the logarithm of the absolute holding period return is used. However, Table 4 on page 40 lists the control variable as $|Holding\ period\ return|$ without the logarithm, and the prose on page 17 only mentions controlling for 'the logarithms of holding position and holding duration' without mentioning a log transformation for the holding period return.

2. Collinearity in style estimation — Critical

trading game. To measure investment style, we estimate the following decision-level regression separately for each investor i . The idea is to isolate how investors respond to recent price movements, while controlling for return-related components that may reflect preference-based responses, especially around the return break-even point. We

In Equation 3, both the recent return and the gain dummy are determined by the contemporaneous price. When the price is close to the cost basis, these variables are highly collinear. If the true realization preference is continuous in the return rather than a step function, the continuous recent return variable will absorb this preference, biasing the style coefficient and contaminating the style measure with the disposition effect itself. The authors should use lagged returns or non-linear controls to separate these effects.

3. Over-generalization of decomposition results — Major

tive, short-horizon cases where the discontinuity is sharpest. The 10% figure in Table 7 integrates the gain-response effect over the full distribution of holding-period returns and the entire 10-week sample window, including longer horizons where the discon- tinuity is economically small. Together, the two exercises bracket the importance of

The model-based decomposition attributing only 10% of the disposition effect to realization preference is performed exclusively on a highly specific sub-sample of short-horizon trades (< 10 weeks) using daily transaction data. Short-horizon daily traders are highly active and much more likely to be driven by short-term price-contingent styles. For typical, longer-term investors, the relative importance of realization preference versus mechanical style may be completely different. Generalizing this 10% figure to the overall disposition effect in the broader population is an over-generalization. The authors should limit this claim to short-horizon trades.

4. Low cross-context explanatory power — Major

time variation from repeated participation. The strong positive association between early- and late-period CD estimates—over-time correlation of 0.30, significant at the 1% level—confirms that an investor’s style classification is not sensitive to when in their history it is measured.

The cross-context correlations of 0.16 for the Contrarian Degree and 0.187 for the disposition effect imply that the stable individual trait measured in the experiment explains only 2.5% to 3.5% of the variance in real-world trading style and disposition behavior. This extremely low explanatory power suggests that the vast majority of the variation in real-world trading behavior is driven by other, context-specific factors, which undermines the claim that the real-world disposition effect is largely driven by this stable individual trait. The authors should temper their conclusions regarding the dominance of this stable trait.

5. Accounting method disconnect — Major

tum investors apply the opposite rule. The cost basis is updated using the weighted- average method upon purchases and remains fixed during partial sales, resetting only after full liquidation.

The theoretical simulation model assumes a weighted-average cost-basis accounting method, which is standard for Chinese mutual funds but is not the standard method for US stock brokerages (which typically use FIFO, LIFO, or specific identification). Since the mechanical effect relies on how the cost basis evolves over partial sales, the simulation results may not generalize to the US stock brokerage dataset used for external validation. The authors should show that the mechanical effect holds under FIFO accounting.

6. Lagged snapshot measurement error — Minor

The dummy variable

In the field regressions, the selling decision during month t is regressed on the gain status at the end of month t-1. Because fund prices change daily, the actual gain status at the moment of sale during month t may differ from the month-end snapshot. This measurement error introduces attenuation bias, which likely artificially depresses the estimated baseline disposition effect and inflates the apparent role of the style interaction. The authors should use daily transaction-level data to determine the exact gain status at the time of trade.

7. Portfolio rebalancing confound — Minor

gree (CD), inferred using the same regression-based approach. While the core method- ology remains similar to Equation 3, we adjust the specification to reflect the real-life context. Following Liao et al. (2022), we use the previous month’s fund return as a proxy for recent price movements and additionally control for the logarithms of hold- ing position and holding duration. The dependent variable is the percentage change

In the real-world mutual fund setting, investors hold portfolios of multiple funds. Standard portfolio rebalancing (buying underperforming funds and selling outperforming funds to maintain target weights) mechanically generates a positive Contrarian Degree and a positive disposition effect. The authors do not control for fund-specific portfolio rebalancing in their field regressions, meaning the documented style-disposition relationship in the field may simply reflect rational portfolio rebalancing rather than a mechanical bias. The authors should control for portfolio-level rebalancing motives.

xPeerd (AI review)

September 30, 2026

AI Review (xPeerd — DAReview)

Summary

The manuscript, titled The Mechanical Disposition Effect, argues that the observed disposition effect in investor behavior is not primarily a direct preference for realizing gains, but instead is largely a mechanical by-product of persistent investment style interacting with cost-basis accounting. The paper combines three empirical settings: a virtual trading experiment on Alipay, linked field data on real mutual-fund holdings from the same participants over 2017–2021, and an external traditional brokerage dataset. The central claim is that contrarian investors display a much stronger measured disposition effect than momentum investors, with the effect reportedly 3x to 9x larger depending on the setting. The authors further argue that a discontinuity at the zero-return threshold supports realization preference, but this explains only about 10% of the total disposition effect.

The manuscript’s main strengths are the clear central question, the ambitious cross-context design, and the effort to separate “style” from “realization preference” empirically. The paper is conceptually interesting and potentially important for behavioral finance. Its main weaknesses are identification overreach, several places where causal language exceeds what the evidence securely establishes, limited transparency in the decomposition logic behind the “10%” claim, and some underdeveloped concerns about sample selection, external validity, and measurement dependence on platform-specific accounting rules.

Potential Major Revisions

1. The paper overstates the strength of its central conclusion relative to the identification actually shown.

The manuscript states in the abstract that “much of this pattern is mechanical” and that “The disposition effect is therefore a noisy proxy for realization bias” . In the introduction, the argument is sharpened further: “We argue that a large share of the disposition effect is mechanical” and “the measured disposition effect is not a clean statistic for realization preference” . By the conclusion, the framing becomes even stronger: “Rather than an independent behavioral preference, it emerges as the mechanical footprint of how investors process and react to price changes” .

I think this wording currently goes beyond the evidence. What the paper convincingly shows is that disposition-effect measures covary strongly with the estimated Contrarian Degree and that platform accounting mechanics can amplify this relationship. What it does not fully establish is that the observed field disposition effect is predominantly mechanical in a decomposition that is model-independent. The current inference seems to depend on the validity of the style measure, the stability assumption, the cost-basis mechanism, and the specification choices used to separate gain/loss response from price-response behavior. The authors should soften claims of replacement and emergence unless they provide a more formal identification argument demonstrating under what assumptions the “mechanical” component is point-identified rather than suggestive.

2. The distinction between investment style and disposition effect is asserted well, but not fully insulated from definitional overlap.

Section 3.5 directly addresses this concern and states: “Equation 3 isolates how investors adjust their position in response to recent market movements after removing any direct response to whether a position is at a gain or a loss. The Contrarian Degree is therefore conceptually and econometrically distinct from the disposition effect” . This is an important defense, but it remains incomplete.

The reason is that gain/loss status itself is partly generated by earlier price paths and trade timing, and the CD measure is also extracted from trading responses to recent returns. So although the variables are not identical by definition, they may still be tightly structurally entangled. This matters because the paper’s strongest claims rely on interpreting the style–disposition association as revealing mechanism rather than a related manifestation of the same underlying dynamic behavior. The cross-context validation helps, especially the claim that “experimentally classified contrarian investors exhibit a significantly stronger disposition effect in the field” , but more is needed. I would recommend placebo-style tests, alternative style measures not built directly on recent return response, and a falsification exercise showing that style predicts some outcomes but not others if the interpretation is correct.

3. The sample-selection rules may materially shape the magnitude and interpretation of the results.

In the field data, the paper “exclude[s] investor-month-fund observations if there is no selling record within the investor-month” and retains only investors with “no less than 100 valid fund-month observations to ensure active participation” . In the brokerage extension, investors are restricted to “at least 10 active trades” . These filters may be reasonable for estimation precision, but they also narrow the paper toward active traders whose behavior may not represent the broader investor population.

This is especially important because the manuscript itself notes that the sample likely contains unusually active users: “our sample consists of investors who participate the trading games multiple times, and they are expected to trade more actively” . That admission raises an external-validity issue. If the estimated mechanical component is strongest among active, platform-engaged, return-salient users, then the paper should not generalize too broadly to “the disposition effect” as a universal phenomenon. I would want a dedicated robustness subsection quantifying how results change under looser inclusion thresholds, including lower-activity investors, or weighting schemes that better approximate the full platform population.

4. The paper’s decomposition of realization preference versus mechanical effect needs much more methodological transparency.

The manuscript claims: “responses to return status per se account for only around 10% of the overall disposition effect” , and the abstract similarly says the zero-return discontinuity “explains only about 10% of the effect” . This is potentially one of the most important quantitative contributions, but in the currently visible text the underlying decomposition is not sufficiently transparent.

A reader needs to know exactly how the 10% number is constructed, how sensitive it is to bandwidth or specification choices around the zero threshold, what identifying assumptions are required, and whether alternative thresholds or smoothing choices materially change the inference. Because this number is central to the paper’s headline conclusion, it should not appear as a relatively compressed statement. It needs to be unpacked, stress-tested, and made replicable in the main text or a clearly signposted appendix.

5. The accounting-rule dependence is central, but the paper underdevelops how platform-specific this mechanism is.

The field data section acknowledges a very specific cost-basis rule: “Alipay implements a common way that updates cost basis according to the weighted average cost only when extra purchase is made. Namely, when an investor sells partially its fund shares, the cost basis does not change. The cost basis resets after a full liquidation” . The appendix then formalizes the mechanism around this rule: “The platform reports a displayed cost basis Ct computed as a weighted-average purchase price” and this basis “is updated only upon purchases and remains unchanged during partial sales” .

This is analytically useful, but it also means the proposed mechanism may be highly sensitive to institutional accounting conventions. The authors should directly discuss whether the argument survives under FIFO, LIFO, tax-lot selection, or investor-side private reference points that differ from displayed platform basis. Without such analysis, the general claim that the disposition effect is largely mechanical may be too dependent on a specific platform implementation.

6. Some causal and near-deterministic language should be moderated.

Section 3.3 says, “investment style is a key, even determinant, predictor of the strength of the disposition effect” . The conclusion states that “the aggregate disposition effect thus largely reflects the composition of investment styles in the market rather than a universally shared irrationality” . I think “determinant” is too strong unless the authors can show that most plausible omitted channels have been bounded away. The paper clearly establishes predictive power and a plausible mechanism; that is not the same as establishing dominance in a causal sense.

Relatedly, Section 4 argues that interventions focused on realization decisions “are likely to be ineffective” if the bias is downstream of stable trading rules . That policy statement is stronger than the evidence warrants. The paper does not test interventions, and persistence of style does not imply non-malleability of realization responses. Such claims should be recast as hypotheses or implications rather than direct policy conclusions.

7. The anti-fraud / coherence check is broadly reassuring, but some claims still need tighter evidentiary anchoring.

I do not see obvious paper-mill traits such as meaningless jargon, fabricated-sounding concepts, or incoherent structure. The manuscript is coherent, technically framed, and anchored in a recognizable behavioral-finance paradigm. The experimental-field linkage and the brokerage replication are also conceptually aligned. That said, several claims are presented with high confidence while relying on compressed explanation, especially the “10%” decomposition and the breadth of the generalization from one platform’s accounting environment to the disposition effect as a broader construct. These features do not suggest fraud, but they do suggest a need for greater evidentiary discipline before publication.

Potential Minor Revisions

1. Typographic, spacing, and formatting issues

The uploaded text appears to contain frequent encoding or PDF extraction artifacts, for example broken hyphenation and symbol corruption such as “re￾alizing,” “mo￾mentum,” “dis￾position,” and arrow/symbol replacements like “↑” and “→” appearing inside prose and equations. Examples appear throughout the manuscript, including the abstract and introduction, and in tables and appendix material. For example, “price￾contingent trading styles alone can generate disposition-effect-like behavior” and “the effect is up to nine times stronger for contrarian than mo￾mentum investors” appear with broken character rendering in the abstract . Similar artifacts occur in the appendix equations and notes, such as “Ut ↘ Pt / Ct→ ↑ 1” and in Table C.1 where negative signs and arrows appear corrupted .

These may stem from extraction rather than the source PDF, but they must be checked carefully in the final manuscript files, especially equations, table notes, minus signs, superscripts, and subscripts.

2. Some prose could be tightened to reduce rhetorical excess.

Phrases such as “canonical interpretation,” “primitive behavioral bias,” and “universally shared irrationality” are rhetorically effective but slightly overstated for a paper that is ultimately making an empirical identification argument under assumptions. Examples appear in the introduction and conclusion . I would recommend a more measured tone in places where the contribution is reinterpretation rather than outright refutation.

3. Section transitions are clear but occasionally repetitive.

The paper repeatedly states variants of the same high-level claim: that style shapes cost basis, which shapes gain/loss realization, which shapes the measured disposition effect. This appears in the introduction, Section 3, Section 4, and conclusion . Some repetition is useful, but parts could be condensed to create room for more design transparency or robustness discussion.

4. Clarify the practical meaning of coefficients for non-specialist readers.

For example, Table 3 is summarized as a gain-loss asymmetry “about 13 pps higher for contrarians” with a “baseline disposition effect of about 4 pps” for momentum investors . Those interpretations are useful, but similar plain-language interpretation should be consistently provided for the main field estimates, not just selected experimental ones.

5. Table and note presentation should be standardized.

The table notes are generally informative, but some are dense and may benefit from formatting standardization. For instance, Table 1’s note is long and combines variable definitions, sample restrictions, and timing conventions in a single block . Table 2–4 notes are clearer, but notation and dummy-variable descriptions should be made visually uniform across tables .

6. AI content analysis

Estimated percentage of AI-generated content: low to moderate, approximately 10–20%.

Reasoning: the manuscript is coherent, domain-specific, and methodologically structured in a way that is typical of contemporary economics working papers. However, some passages use highly polished, somewhat uniform explanatory prose and repeated rhetorical framing, especially in the introduction and conclusion, that could reflect either careful human drafting or partial AI-assisted editing. Examples include broad-scope formulations such as “what looks like a primitive bias may be the predictable outcome of deeper, stable decision rules” and the repeated stylized contrasts between “mechanical” and “preference-based” channels across sections .

Highlighted sections with possible AI-assisted polishing:

• Abstract and opening introduction, where claims are compressed into strong, balanced, high-fluency formulations
• Concluding section, especially the paragraph beginning “Rather than an independent behavioral preference...”
• Transitional interpretive prose in Sections 4–5, where explanatory structure is very smooth and repetitive

Assessed epistemic impact: limited if AI was used only for language polishing; more serious if AI contributed to econometric interpretation or overconfident causal phrasing. The key issue is not authorship of prose but whether polished language masks assumptions that should be made explicit. In this manuscript, that risk is most visible in the confidence with which the “mechanical” interpretation is generalized.

Recommendations

1. Reframe the headline contribution more carefully. I would recommend changing the strongest claims from “the disposition effect is therefore a noisy proxy for realization bias” to a more conditional statement, such as: the measured disposition effect substantially reflects investment-style-induced mechanics under the observed trading and accounting environment. That would remain strong while better matching the evidence.

2. Add a dedicated identification subsection. This should explicitly state:

• what is observed,
• what is estimated,
• what assumptions are required to interpret the style–disposition link mechanically,
• what part of the argument is descriptive,
• what part is causal,
• and what would falsify the interpretation.

3. Expand the decomposition behind the “10%” realization-preference estimate. Put the estimator, bandwidth choices, graphical evidence, robustness checks, and uncertainty intervals in the main text or a prominently referenced appendix. This is too important to leave underexplained.

4. Strengthen robustness against definitional entanglement. Consider:

• alternative style proxies,
• out-of-sample prediction exercises,
• placebo outcomes,
• subgroup tests where accounting mechanics should matter less or more,
• and alternative gain/loss definitions.

5. Address external validity much more directly. The field sample is platform-specific, mutual-fund-specific, and selected on participation intensity. A stronger discussion is needed on whether the findings generalize to stocks, less active investors, different market structures, and other cost-basis conventions.

6. Analyze sensitivity to accounting rules. Since the mechanical channel hinges on weighted-average cost with no basis updating on partial sales, I would strongly recommend simulations or conceptual comparisons under alternative accounting conventions.

7. Moderate policy implications. Claims that certain debiasing interventions are “likely to be ineffective” should be softened unless directly tested. The paper can motivate that conjecture without presenting it as a near-conclusion.

8. Improve presentation quality. Carefully inspect the source manuscript for encoding issues, symbols, and equation rendering. Even if these are only extraction artifacts, journal submission files should be checked line by line in equations, tables, and appendices.

Overall recommendation

My assessment is that this is a promising and potentially important manuscript with a genuinely interesting reinterpretation of a classic behavioral-finance result. However, in its current form, the paper’s strongest conclusions are stated more forcefully than the available identification warrants. I would recommend major revision before the work is ready for a high-level submission.

XSci (AI review)

September 30, 2026

Referee Report

Manuscript: "The Mechanical Disposition Effect" Field: Behavioral / household finance Recommendation: Major revision required

Summary and Recommendation

This manuscript challenges the canonical reading of the disposition effect, arguing that much of it is mechanical: stable price-contingent investment styles interact with weighted-average cost-basis accounting to determine whether sales fall in gain or loss states, so that the measured statistic is not a clean read on realization preference. The authors estimate an investor-level Contrarian Degree from per-investor regressions of trading intensity on recent price changes while conditioning on gain status, and relate it to Odean (1998) disposition measures in three settings: a virtual trading game embedded in Alipay, from which 50,000 multi-session participants yield 4,527,250 decision-level observations; those same participants' Alipay equity mutual fund holdings over January 2017 to October 2021, comprising 12,071,776 investor-fund-month observations; and the Barber and Odean (2000) discount brokerage data for January 1991 to December 1996. Contrarians constitute roughly 86%, 76% and 63% of investors across the three settings and display markedly stronger disposition effects, which the authors characterize as up to nine times larger. Section 4 documents persistence in both style and the bias, and Section 5 documents a discontinuity in daily selling at the zero-return threshold in a transaction-level sample of 915,063 observations, which a model-based decomposition credits with roughly 10% of the total effect.

The paper is a serious contribution to an important question, and several of its elements are genuine assets. Linking an elicitation instrument to the same individuals' administrative holdings is a design few researchers can obtain, and the cross-context prediction in column (3) of Table 4 is the most informative single test in the paper. The replication in external brokerage data reflects good practice rather than reliance on proprietary evidence. The zero-return discontinuity in Table 6 stands on its own merits: given that Ben-David and Hirshleifer (2012) found no such jump, documenting one in a high-frequency setting with a salient displayed reference point adds to the evidence on realization utility whatever one concludes about the main thesis. The authors are also commendably candid, anticipating the strongest objection to their design in Section 3.5 and explicitly reconciling the two apparently discordant magnitudes in Section 5. The reviewer nonetheless recommends major revision. The concerns below concentrate on three areas: whether the Contrarian Degree measures what the paper claims, whether the outcome and the samples on which it is estimated support the inference drawn, and whether the mechanism and the headline magnitudes are established rather than asserted. None appears fatal to the underlying idea, and most of the remedies involve exercises the authors can run with the data already in hand.

Major Concern Category 1: The Construction and Interpretation of the Contrarian Degree

1.1 The conditioning in Equation 3 does not econometrically separate style from the disposition effect

Section 3.5 offers three defenses against the charge that style and the disposition effect are observationally equivalent, and the first bears most of the weight: because Equation 3 includes the gain dummy, the absolute session return and their interaction, the recent-return coefficient is said to isolate the response to price movements after removing any direct response to gain-loss status. This argument is weaker than it appears for a reason internal to the paper's own mechanism. The authors' thesis is precisely that recent returns and gain status are not independent, since for a contrarian an up-move both triggers a sale and moves the position into the gain region through a cost basis that prior purchases in down states have depressed. Including gain status additively and interacting it only with the absolute session return imposes a particular functional form on this nuisance component, and any curvature not captured by that form loads onto the coefficient of interest. This matters concretely because Ben-David and Hirshleifer (2012) document a distinctly non-monotone, V-shaped selling schedule in exactly this domain. The concern is sharpened by the fact that the dependent variable in Equation 3 is turnover, which includes sales, so the same transactions that determine the numerators of the proportion of gains and losses realized also determine the style coefficient. Because both objects are estimated from the same short per-investor series, their estimation errors are mechanically correlated: an investor whose realized sequence happened to concentrate sales after up-moves will appear both more contrarian and more disposition-prone with no underlying trait difference. Notably, column (3) of Table 4, which uses experimentally inferred style, shows the interaction falling from 7.558 to 3.059 and the main gain coefficient becoming statistically indistinguishable from zero at 0.400 with a standard error of 0.339. That attenuation is consistent with the concern raised here and deserves discussion rather than the current characterization that results are qualitatively unchanged. A split-sample construction, estimating style from odd-numbered sessions or the pre-2020 subperiod and disposition from the complement, would resolve the issue directly, and the infrastructure already exists in Section 4.1.

1.2 Mechanical portfolio rebalancing offers an alternative source of measured contrarianism

A second and independent concern is that the Contrarian Degree may register nothing more than portfolio rebalancing. The dependent variable in Equation 3 is signed turnover and the regressor is the market return since the previous decision, while Section 2.2.1 establishes that each period brings an exogenous inflow of 1,000 CNY in cash and Table 1 reports a mean risky share of 55.09% with a standard deviation of 35.57%. Consider an investor who simply targets a stable risky share. When the index rises, the risky position appreciates and restoring the target requires trimming risky assets or directing the new cash entirely to the cash account; when the index falls, the opposite holds. Both responses generate negative covariance between signed turnover and the recent return, and hence a positive Contrarian Degree, with no price-contingent belief, preference or rule of thumb involved. The same force operates in the field specification, where the dependent variable is the percentage change in the number of fund shares held and an outperforming fund grows as a portfolio share. This alternative is not a technicality: it predicts a large contrarian majority in every setting, which is what the authors find and what footnote 6 flags as at odds with prior U.S. evidence, and it predicts a positive association between the Contrarian Degree and measured disposition through the same cost-basis channel the authors identify. The interpretive difference is substantial, since under the rebalancing reading the disposition effect is not the footprint of a behavioural decision rule at all, and the policy conclusion in Section 6 about tailoring interventions to investors' underlying responses to price changes would not follow. Three diagnostics appear available: re-estimating the measure with the change in the risky share as the outcome, so a pure rebalancer registers zero by construction; controlling for the lagged deviation of the realized risky share from the investor's own average; and examining whether the measure is systematically related to within-investor risky-share volatility.

1.3 Features of the elicitation instrument may manufacture the contrarian classification

The experiment carries the identification burden because Sections 3.5 and 6 both argue that style elicited there is credible for being free of field confounds. Three design features work against that interpretation, and all push toward apparent contrarianism. The first is that price paths are drawn from a single, strongly mean-reverting series: Section 2.2.1 states that each of 160 paths comes from the SSE Composite over 2011 to 2018, a window dominated by the 2014-2015 boom and subsequent crash. An investor who has learned the statistical properties of the displayed series, or who simply responds to the visual salience of a chart that reverts, will trade against recent moves, which is Bayesian updating about a mean-reverting process rather than a stable trait. Because random assignment across paths is a design feature, this is testable: if measured contrarianism is higher among participants assigned paths with more negative serial correlation, the measure is partly a response to the assigned data-generating process. The second feature is that the game is unincentivized, with an imaginary endowment and a median decision time of 4.37 seconds per Table 1. Section 2.2.2 reads six seconds as evidence that participants digest new information, but a four-second median decision on a hypothetical portfolio is at least equally consistent with low-effort heuristic play, and a bounded interface with a visible reverting chart is precisely where a buy-the-dip heuristic would dominate. The third is that the instrument is branded as a personality test whose report, per Section 2.2, covers overconfidence, loss aversion, overoptimism and risk seeking. Participants therefore know they are assessed on named behavioural dimensions, one of which is the construct most closely tied to the disposition effect, and because they may play repeatedly and receive feedback between sessions, later behaviour may partly respond to the instrument's own output, which would contaminate the persistence tests. Reporting whether results differ for first-time versus repeat players, using the alternative sample described in footnote 4, would help considerably.

1.4 The binary style split discards the test the mechanism itself implies

Throughout the paper, a continuous measure is reduced to its sign. Tables 3 through 6 and A.1 all interact gain status with a contrarian dummy, Figures 2, 3, 4 and 7 present two groups, and Table 7 decomposes separately for two groups; the continuous measure appears only in the distributional plots and in Figure 5. This forgoes the natural test of the mechanism. Appendix C is explicitly monotone in trading intensity, parameterizing a trading-intensity factor over three values, and Table C.1 shows the simulated disposition effect rising with that factor. The mechanism therefore delivers a dose-response prediction, and a two-point contrast cannot distinguish it from a threshold or a non-monotone relationship. Reporting disposition by deciles of the measure, and a specification interacting gain status with the continuous measure, would convert the central test from a comparison of means into a genuine test of shape. The split is also unbalanced in ways that make the momentum group fragile. With roughly 14% of experimental participants classified as momentum, and with Figure B.3 describing a unimodal distribution peaking near zero, the momentum group consists largely of investors whose sign is determined by estimation noise. This shows in the results: the momentum gain coefficient is positive at 4.901 in the experiment, negative at −2.563 in the field, and positive at 20.259 in Table A.1 column (5), an inconsistency that is never reconciled and that suggests the classification is not isolating a stable type. Reporting the distribution of t-statistics on the individual style coefficients, and restricting the main analysis to precisely estimated investors, would let readers judge how much of the momentum group is signal.

Major Concern Category 2: Outcome Measurement and the Samples on Which It Is Estimated

2.1 Experimental gain status is not computed against the cost basis the mechanism requires

Appendix C.3 is explicit that the mechanism runs through a displayed cost basis computed as a volume-weighted average of past purchase prices, updated only on purchases and invariant to partial sales, and Proposition C.1 follows from contrarian purchases placing large weights on low prices in that average. In the experiment, however, Sections 2.2.1 and 2.2.2 indicate that performance is measured by paper profits over accumulated cash inflow, where that inflow is 10,000 plus 1,000 times the period number. Table 1 confirms the distinction by reporting a market return since inception of 1.55% and a separate session return of 0.38%. A return on cumulated contributions is not a return relative to a weighted-average purchase price, and it is mechanically dampened by the cash position, so an investor holding a low risky share registers a session return near zero regardless of the index path. Gain status in the experiment therefore partly reflects portfolio composition, which is itself the object responding to recent returns, so the conditioning in Equation 3 is conditioning on an outcome of the process being measured. More fundamentally, the experiment cannot test the Appendix C channel, because that channel concerns the distribution of price over cost basis at sale times and the experiment measures a different object. This undermines the parallelism the paper draws between Table 3 and Table 4 and the cross-context correlation of 0.187 in Figure 6, both of which require the two settings to measure the same construct. The remedy appears tractable: the game records the full sequence of prices and trades, so a weighted-average cost basis satisfying the Appendix C convention can be reconstructed period by period. Reporting the experimental results under that definition, along with the correlation between the two definitions of gain status, would either validate the current approach or reveal an informative divergence.

2.2 The sell indicator pools marginal trims with the position closures the theory concerns

The paper's argument is about which trades enter the sale sample, so it matters that the sale indicator corresponds to realization in the economically relevant sense. In the experiment the indicator marks any reduction in the risky position; in the field, Section 2.3 defines it as a reduction in the number of shares relative to the previous month and states that it includes both partial and complete redemption. Under the platform's accounting convention described in footnote 5, a partial sale leaves the cost basis unchanged and the mental account open, and only full liquidation resets it. Realization utility as modelled by Barberis and Xiong (2012) and Ingersoll and Jin (2013), the theory tested in Section 5, is a theory about closing positions, so a modest trim and a full redemption are economically distinct events that the current definition pools. Two consequences follow. The disposition statistics throughout the paper are weighted toward marginal position adjustments, which under the rebalancing concern above may be partly mechanical for reasons unrelated to style. And the realization-preference test is weakened, since a discontinuity in the probability of any reduction is a weaker test than a discontinuity in the probability of full liquidation, which is the event generating the utility burst the theory posits. Reporting the main results separately for full liquidations and partial trims, in both the monthly panel and the transaction-level sample, appears feasible given share-level data and the identifiability of liquidation through the cost-basis reset. If the style gradient concentrates in trims while the discontinuity concentrates in liquidations, that would sharpen the paper's claim considerably rather than undermine it, since the two channels would be shown to operate on different margins.

2.3 Sample construction filters interact with the mechanism and bound the population to which estimates generalize

Section 2.3 imposes a chain of restrictions whose combination is consequential given the paper's own logic. Following Odean (1998), investor-fund-month observations are excluded if there is no selling record within the investor-month, and investors are retained only with at least 100 valid fund-month observations. Consider how the first interacts with the mechanism. A contrarian trims after price increases and a momentum investor after decreases, so conditioning on a sale having occurred is not symmetric across styles: for a contrarian the surviving months are disproportionately months in which held funds appreciated, and the surviving non-sold positions in those months are disproportionately in the gain region. Because the proportions of gains and losses realized are computed over all positions in surviving months rather than only over sold positions, the denominators as well as the numerators become style-dependent. The observed gradient is therefore partly built into the sample definition through the very channel the paper seeks to identify. The activity requirement compounds this. Table 1 reports a monthly sell probability of 0.19, far above the 5% that Chang et al. (2016) document, and while the paper attributes the difference to lower costs, easier execution, attention and multi-session selection, the implication is a sample of very active traders. Active traders are precisely those for whom the mechanical channel is strongest, since the cost basis is repeatedly re-weighted by new purchases, so the estimates are best read as an upper bound on the channel's population importance. Reporting the field results without the within-month-sale restriction, and reporting how the gradient varies as the activity threshold is relaxed to twenty and fifty observations, would clarify both issues and appropriately qualify the abstract.

2.4 The persistence evidence is described more strongly than the magnitudes support

Section 4 establishes the persistence claim, and the language is emphatic: style is described as highly persistent over time and across contexts, the association in Figure 5 as a strong positive association. The supporting numbers are an over-time correlation of 0.30 and a cross-context correlation of 0.16 for style, and 0.355 and 0.187 respectively for the disposition effect. These are modest: a correlation of 0.30 implies that early-period style accounts for 9% of the variance in late-period style, and 0.16 implies 2.6%. The inferential chain requires more than statistical significance here, because the mechanical argument holds that the bias persists because style persists. Two pieces of evidence sit uneasily together in this respect. Table 2 reports that individual fixed effects raise raw R-squared from 4.9% to 41.9%, implying that a large share of disposition variance is individual-specific, yet the style correlation of 0.30 is lower than the disposition correlation of 0.355. If style were the source of the individual component, it should be at least as persistent as the bias it generates. The paper should confront this arithmetic, ideally by reporting how much of the individual fixed-effect variance in Table 2 the Contrarian Degree spans. The deeper issue is that none of these correlations is bounded by the reliability of the underlying estimates, both of which are estimated with substantial noise from short per-investor panels. Raw correlations between two noisy estimates of the same trait are attenuated by the product of their reliabilities, so 0.30 is consistent with much higher true persistence; conversely, if the split-half estimates share estimation inputs, the correlation can be inflated. A split-half reliability coefficient for each measure, or a simple errors-in-variables correction, would let the authors state what the raw figures imply. The comparison to Sui and Wang (2025), whose 0.132 the paper cites as a benchmark, would also be more informative with reliability accounted for, since the two studies use panels of very different lengths.

Major Concern Category 3: The Mechanism, Its Magnitudes, and the Inference Supporting Them

3.1 Appendix C establishes the mechanism by assumption and reports magnitudes on a non-comparable scale

The word "mechanical" in the title is justified by Appendix C, which therefore bears a heavy burden, and as written it demonstrates an accounting identity rather than an empirically disciplined mechanism. Section C.2 defines the contrarian rule as buying if and only if the return is negative and selling if and only if it is positive, with momentum as the mirror image. The proof sketch in Section C.4 then makes plain that Proposition C.1 follows from two assumptions that are themselves the conclusion: contrarians sell only after up-moves, raising the numerator, and buy only in down states, lowering the denominator. Given a deterministic rule that sells if and only if the price just rose, a rightward shift in the ratio is immediate, and the robustness exercise varying volatility and trading intensity confirms the invariance of an algebraic implication rather than establishing anything about investors. What would make the appendix informative is calibration: parameterizing the simulation to the empirically estimated distribution of style coefficients, the observed decision frequency, the observed volatility of the underlying index and the observed turnover of about 7%, and then asking how much of the 13 percentage point interaction in Table 3 the mechanism can generate. That quantitative comparison is what the abstract claims and it is currently made nowhere. A second and more concrete problem is that the simulated magnitudes cannot be compared to the empirical ones even in principle. The note to Table C.1 defines the proportions of gains and losses realized as conditional-on-sale probabilities that sum to one by construction, so the reported difference is a rescaling of the share of sales in the gain region, whereas the empirical measures in Equations 1 and 2 have paper positions in their denominators. The simulated values of 0.406 to 0.472 are therefore not on the same scale as the empirical statistics used throughout the paper, and Section 3.5's claim that the appendix confirms quantitatively large differences cannot be evaluated. Tracking paper positions in the simulated panel and reporting standard Odean statistics would resolve this; absent that, main-text claims should be restricted to sign rather than magnitude.

3.2 The mechanical reading is not established against an observationally equivalent belief-based account

Section 3.2 is admirably careful that the Contrarian Degree could reflect beliefs, preferences or rules of thumb, and states that the authors remain agnostic about its psychological origins. The paper does not remain agnostic in interpretation: Section 6 states that the disposition effect emerges as the mechanical footprint of how investors react to price changes, and Section 5's title places realization preference beyond the mechanical. The difficulty is that a belief-based account generates the same pattern. If contrarian investors hold mean-reverting beliefs and sell after a price rise because they expect reversal, that sale occurs in the gain region for the same cost-basis reason, but it is caused by a belief about future returns rather than by accounting. The claims are substantively different, since beliefs are potentially correctable by information whereas an accounting artifact is not, and the paper's own language oscillates between them, referring in Section 5 to belief-driven investment style and belief-based attributes while the title asserts a mechanical reading. Distinguishing the two is feasible here, and doing so would be the paper's most convincing evidence. The accounting account makes a prediction the belief account does not: the convention described in footnote 5 implies that weighting occurs only when an investor has made multiple purchases into a position, since with a single purchase the cost basis is simply the purchase price. The style gradient should therefore be much weaker, and under the purest form of the mechanism close to absent, for positions built in a single purchase, and should strengthen with the number of purchases since the last full liquidation. Both quantities are observable in share-level data. Absent such tests, the appropriate revision is to soften the framing, since the substantive contribution — that the disposition statistic is not a clean read on realization preference — survives either reading, so little is lost and considerable credibility gained by presenting the accounting channel as one of two consistent interpretations.

3.3 The decomposition cannot bound the preference channel, and Table 7 is more heterogeneous than the text conveys

The abstract's most consequential sentence is that the discontinuity explains only about 10% of the effect, and its construction makes it an upper bound on a narrowly defined object rather than an estimate of the preference channel's importance. The decomposition removes terms related to the gain dummy from the discontinuity specification and refits, but that specification retains third-degree polynomials in the holding-period return interacted with holding length and style. Realization preference as modelled by Barberis and Xiong (2012) and Ingersoll and Jin (2013) does not operate only through a discontinuity at zero; it generates a smooth reference-dependent selling schedule of which the jump is one testable implication. Leaving the polynomials in the restricted model therefore assigns all smooth reference-dependence to the mechanical residual and credits preference only with the discontinuous part. That is a well-defined quantity but not the share attributable to realization preference, and the abstract equates the two. A version that also removes the polynomials, or that separates them into reference-dependent and residual components, would let the authors report a range. The reported numbers also merit closer discussion. Table 7 gives shares of 11.46% and 9.17% in the experiment and 6.94% and 12.28% in the field for contrarian and momentum investors respectively. The headline is a rough midpoint, but the dispersion is nearly two-fold and the ordering reverses across settings. Under the paper's own logic the preference share should be mechanically smaller for contrarians, whose denominators are inflated by the mechanical channel; the field pattern is consistent with this and the experimental pattern is not. This tension is informative and should be confronted rather than averaged away. Relatedly, the significance stars in Table 7 attach to the level difference rather than to the share, and no interval is reported for the quantity the abstract advertises, so a reader cannot tell whether about 10% is distinguishable from 20%. A delta-method or bootstrap interval is straightforward and would materially strengthen the claim. The table note also defines the share against the counterfactual rather than the total, which does not match the abstract's phrasing.

3.4 The headline magnitudes are not traceable to reported estimates with measures of uncertainty

Neither of the paper's two advertised numbers can be located in the tables in a form that permits assessment. The claim that the effect is up to nine times stronger for contrarians rests on Figure 4, whose note reports only that it plots average disposition effects in three settings; no table gives the underlying levels and no standard errors accompany the ratio. The regression evidence meanwhile implies considerably smaller ratios: Table 3 column (2) gives roughly 3.7, Table 7's fitted effects give roughly 4.1 in the experiment and 4.2 in the field, Table A.1 column (3) gives roughly 1.5, and Table 4 column (2) gives a ratio that is undefined because the momentum coefficient is negative. Not one reaches nine. A ratio of a difference to a small and imprecisely estimated denominator is in any case fragile, since the momentum baseline is estimated on a minority of participants and the ratio explodes as that baseline approaches zero. The authors should tabulate the Figure 4 levels with standard errors, report the implied ratio for each setting, and replace the abstract's formulation with either a central tendency or an explicit range attributed to its source. Relatedly, the conclusion's statement that the bias is economically small or even absent for momentum investors is in tension with Table A.1, where the momentum gain coefficient ranges from 14.727 to 20.269 percentage points and is the largest momentum estimate anywhere in the paper. In the one setting external to the authors' own platform, momentum investors display a substantial disposition effect and the style gap is close to parity. This is the paper's most important robustness result and it points toward a more qualified conclusion than the abstract states; it belongs in the main text rather than the appendix.

3.5 The inference strategy and the discontinuity design require strengthening

The paper's headline coefficients carry very large t-statistics, roughly 11 in Tables 3 and 4 and roughly 14 in Table A.1, but the clustering choices leave that precision difficult to interpret. In the experiment, standard errors are two-way clustered at the individual and game-period levels, yet Section 2.2.1 establishes eleven decision periods of which the first is dropped, so one dimension has roughly ten clusters and, in the saturated column of Table 3, coincides with a fixed-effect dimension. More importantly, that is not where the dependence lies: 160 price paths drawn from eight years of index data must overlap substantially, so participants assigned overlapping paths face identical return sequences, and market-path-year fixed effects absorb the level of this dependence but not its correlation structure. Clustering by price path would be the natural fix. In the field, clustering by investor and month omits the fund dimension, though returns are strongly correlated within funds across investors. Table 6 reports no statement of how standard errors are computed at all, which is notable for the paper's only identification-based result. The most persuasive response would be a permutation exercise exploiting the experiment's random path assignment, reassigning style labels within path cells and reporting the empirical distribution of the interaction coefficient; this is computationally feasible and would do more to establish the results than any analytical adjustment. The discontinuity design itself also departs from current practice in ways that are individually fixable but collectively leave the finding unverified. The specification is a global third-degree polynomial over a twenty-percentage-point window, which is the configuration most prone to producing spurious discontinuities through boundary behaviour of the fit, and footnote 10's higher-order alternatives are if anything more vulnerable. No density test is reported, which matters particularly because the running variable is a rounded platform-displayed return derived from a weighted-average cost basis, with Table 6 reporting a median return of 0.08% and a gain dummy mean of 0.53, so displayed returns of exactly zero are likely common and their coding directly determines the estimate. No placebo cutoffs are reported, though estimating the same jump at non-zero thresholds is the single most informative available check, and no bandwidth sensitivity is shown. Finally, the running variable is endogenous to style through the cost basis, which the authors partially address by interacting polynomials with style so that comparisons are within-style; this is sensible but should be stated explicitly as the identifying argument and defended, since readers trained in discontinuity designs will otherwise regard the design as invalid on its face.

Minor Issues

1. Table 6 Panel A appears internally inconsistent. The holding-period return is reported with mean −0.07 and standard deviation 0.42 alongside a first quartile of −2.52 and a third quartile of 2.34. A standard deviation of 0.42 cannot accompany an interquartile range of nearly five. Since the gain dummy mean of 0.53 and the median of 0.08 are mutually consistent, the standard deviation appears to be the misreported figure, and this should be checked before the discontinuity sample is interpreted.

2. Sample sizes do not reconcile across tables. Table 1 Panel C reports 12,071,776 investor-fund-month observations while Table 4 uses 9,927,327, an unexplained reduction of roughly 18%. Separately, Table 3 columns (1) to (3) use 4,527,250 observations and column (4) uses 4,456,280, a reduction of about 1.6%, whereas Section 3.2 states that the positive-holdings filter reduces the sample by about 4%. Brief caption notes identifying which filters bind in which columns would resolve both.

3. The provenance and units of Table 7 are unstated. Two distinct real-life samples appear in the paper, the monthly panel and the transaction-level sample that footnote 9 notes cannot be linked to the experiment, and the table does not indicate which underlies its real-life column. The fitted effects are also on visibly inconsistent scales, 16.955 and 4.114 against 0.539 and 0.128, so stating units would prevent misreading.

4. Two robustness exercises are described without results. Footnote 4 reports that an alternative sample of 50,000 participants drawn without the five-session requirement yields qualitatively similar patterns, and footnote 10 reports that fourth- and fifth-degree polynomial specifications remain stable but are available upon request. Since the five-session filter is the paper's principal selection concern and the discontinuity is its only identification-based result, both belong in the appendix as tables.

5. The Nickell bias argument is asserted rather than demonstrated. Section 4.2 attributes the sign flip in Table 2 to bias of order minus one over T minus one, approximately −0.17, given a median panel length of seven. The panel is unbalanced with heterogeneous lengths, so a bias-corrected estimate, or a simulation under the observed length distribution, would convert a plausible conjecture into evidence.

6. Linkage and selection are not characterized. No comparison is offered between the roughly twenty million participants and the 50,000 sampled, and no linkage rate between experiment participants and field holdings is reported, though Table 5 reports 47,300 experimental against 21,712 real-life cross-sectional observations. Balance tables and a stated linkage rate would let readers assess selection at each step.

7. Random path assignment is asserted but not verified. Section 2 relies on random assignment to eliminate selection over market conditions, which is central to the experiment's claim to cleanliness, yet no balance check of participant characteristics across paths or path characteristics is reported.

8. Turnover censoring is unaddressed. Table 1 reports turnover with a mean of 6.94% and a standard deviation of 40.91% on a bounded interval, implying substantial mass at the boundaries. Reporting the share of observations at each boundary would clarify how the censoring affects the linear per-investor style estimates in Equation 3.

9. Figure and simulation notes are incomplete. The notes to Figures 3 and 7 state that dashed curves are third-order polynomial fits without indicating whether they are fitted separately on each side of zero, though the visual impression of a discontinuity depends entirely on this. Table C.1 likewise reports simulated statistics across twelve configurations without simulation standard errors or repetition counts.

10. Several presentational inconsistencies. The Section 4.3 cross-sectional specification is numbered with a stray symbol rather than as Equation 7, leaving the paper without one; Equation 4 contains no intercept though Table 3 reports constants; Equation 5 includes the logarithm of the absolute holding-period return while Table 4 reports the term without the logarithm; Section 5's descriptions in weeks do not map transparently onto Table 6's day-based windows; and the exclusion of abnormal experiment entries in Section 2.2.2 is undocumented as to criteria and magnitude.

Missing and Inadequately Integrated Literature

Cited but Inadequately Integrated

Ben-David and Hirshleifer (2012) is cited repeatedly and its specifications are followed, but the engagement is confined to its null finding on the zero-return discontinuity. Its central contribution is that the selling schedule is V-shaped in profits, with measured disposition arising from asymmetry between the branches, and this is a direct competitor to the style account: a steeper right branch produces precisely the gain-loss asymmetry the authors attribute to cost-basis mechanics. The authors should show that the style gradient survives flexible controls in the absolute holding-period return interacted with style, and should discuss whether the Contrarian Degree is capturing heterogeneity in the slopes of the V rather than in style.

Odean (1998) supplies the paper's outcome measures and its within-month-sale restriction, but the paper does not engage with that work's own discussion and testing of portfolio rebalancing as a competing explanation. Given that rebalancing is identified above as a candidate source of the Contrarian Degree itself, and that the sample restriction is a design choice with known consequences for the denominator, both deserve discussion rather than adoption by convention. Relatedly, Calvet, Campbell and Sodini (2007) is cited to justify the focus on equity mutual funds but not for its substantive documentation that households do rebalance in response to returns, which bears directly on the interpretation of the style measure.

An et al. (2024) is cited as an example of combining experimental and field data rather than for its substantive finding that the disposition effect is portfolio-driven, operating at the level of overall portfolio gain-loss status rather than position by position. Since the field setting is explicitly multi-fund while the experiment involves a single risky asset, portfolio-level reference points offer an alternative explanation for the cross-context correlation in Figure 6, and the authors should examine whether the field gradient is robust to conditioning on portfolio-level gain status. Liao et al. (2022), from which the style measure derives its spirit, likewise warrants a comparison establishing how closely the Contrarian Degree tracks the original construct, since Section 3.5 partly rests on the measure being well established. Chang, Solomon and Westerfield (2016) is engaged more thoughtfully, and the composition-based reinterpretation of its reversed delegated-asset result is testable within the authors' own data; reporting whether the observed style distribution can quantitatively reproduce that reversed sign would convert a conjecture into a result.

Several further works are cited in passing where their substance is directly relevant. Sui and Wang (2025) is used only as a numerical yardstick for the cross-context correlation, though its substantive concern with how stakes shape behaviour speaks directly to whether an unincentivized instrument can elicit a trait that governs real financial decisions. Giglio, Maggiori, Stroebel and Utkus (2021) is invoked to support the claim that individual heterogeneity is not reducible to demographics, but that work also documents substantial within-individual instability in beliefs, which is in tension with the persistence narrative. Frydman and Rangel (2014) is cited as supporting realization utility, when its finding that reducing purchase-price salience attenuates the bias is a direct test of the paper's own maintained assumption about the displayed reference point. Barberis and Xiong (2009) is listed alongside the realization-utility papers, though its result that prospect theory over annual gains and losses often fails to predict a disposition effect is a significant existing qualification to the canonical view the paper sets out to challenge, and engaging it would let the authors position their contribution more precisely.

Truly Missing Papers

Linnainmaa (2010) is not cited and is arguably the closest antecedent to the paper's central thesis. It shows that four documented retail patterns, including both the disposition effect and contrarian trading, arise largely mechanically from the price-contingent execution of limit orders, and it proposes a diagnostic for a dataset's susceptibility to this effect. The parallel is direct, since a price-contingent order generates a gain-loss asymmetry without any realization preference, and engaging with it would both sharpen the paper's framing and raise a specific confound for the brokerage replication, where limit orders were prevalent. An (2016) is likewise absent, though it formalizes and prices the V-shaped net selling propensity and shows that measured disposition is an artifact of asymmetry in a non-monotone schedule, bearing directly on whether the style measure captures style or slope asymmetry. Hartzmark (2015) documents the rank effect, whereby investors sell extreme winners and extreme losers within their portfolio, providing a salience-based non-preference account that is a natural competitor in the multi-fund field setting.

On the experimental and mechanism side, Fischbacher, Hoffmann and Schudy (2017) is close to an experimental test of the paper's own channel, since it exogenously varies access to stop-loss and take-gain orders and traces the causal consequence for measured disposition. Imas (2016) distinguishes realized from paper losses and shows that risk-taking rises after the latter and falls after the former, which bears on the partial-versus-full redemption distinction raised above. Frydman, Hartzmark and Solomon (2018) shows that when investors sell and quickly reinvest, the original mental account is rolled into the new position so that the reference point remains tied to the old purchase price, which is an empirically supported alternative to the cost-basis convention assumed in Appendix C. Seru, Shumway and Stoffman (2010) demonstrates that apparent learning about the disposition effect is substantially attributable to attrition rather than individual improvement, which bears on the within-individual learning null and on a sample selected on repeated participation. Heimer (2016) shows that access to an investment social network nearly doubles the disposition effect, an alternative amplification channel operating without a realization preference and a relevant caution for a platform with social and gamified features.

Two methodological references should also be added. Cameron, Gelbach and Miller (2011) develops the multiway cluster-robust estimator the paper uses throughout and documents its limitations when one dimension has few clusters or coincides with the fixed effects, both of which describe the experimental specification. Calonico, Cattaneo and Titiunik (2014) is the standard reference for discontinuity estimation and inference, providing data-driven bandwidth selection and bias-corrected robust confidence intervals; implementing the local polynomial alternative would materially strengthen the paper's only identification-based result. Finally, Gneezy and Imas (2017) is the standard treatment of lab-in-the-field methodology and its external validity, addressing precisely the inferential step taken when an unincentivized in-app game is used to elicit a trait that is then used to predict real financial behaviour.

References for this section

An, L. 2016. Asset Pricing When Traders Sell Extreme Winners and Losers. The Review of Financial Studies 29:823-861.
An, L., J. Engelberg, M. Henriksson, B. Wang, and J. Williams. 2024. The Portfolio-driven Disposition Effect. The Journal of Finance 79:3459-3495.
Barberis, N., and W. Xiong. 2009. What Drives the Disposition Effect? An Analysis of a Long-Standing Preference-Based Explanation. The Journal of Finance 64:751-784.
Barberis, N., and W. Xiong. 2012. Realization Utility. Journal of Financial Economics 104:251-271.
Ben-David, I., and D. Hirshleifer. 2012. Are Investors Really Reluctant to Realize Their Losses? Trading Responses to Past Returns and the Disposition Effect. The Review of Financial Studies 25:2485-2532.
Calonico, S., M. D. Cattaneo, and R. Titiunik. 2014. Robust Nonparametric Confidence Intervals for Regression-Discontinuity Designs. Econometrica 82:2295-2326.
Calvet, L. E., J. Y. Campbell, and P. Sodini. 2007. Down or Out: Assessing the Welfare Costs of Household Investment Mistakes. Journal of Political Economy 115:707-747.
Cameron, A. C., J. B. Gelbach, and D. L. Miller. 2011. Robust Inference with Multiway Clustering. Journal of Business and Economic Statistics 29:238-249.
Chang, T. Y., D. H. Solomon, and M. M. Westerfield. 2016. Looking for Someone to Blame: Delegation, Cognitive Dissonance, and the Disposition Effect. The Journal of Finance 71:267-302.
Fischbacher, U., G. Hoffmann, and S. Schudy. 2017. The Causal Effect of Stop-Loss and Take-Gain Orders on the Disposition Effect. The Review of Financial Studies 30:2110-2129.
Frydman, C., S. M. Hartzmark, and D. H. Solomon. 2018. Rolling Mental Accounts. The Review of Financial Studies 31:362-397.
Frydman, C., and A. Rangel. 2014. Debiasing the Disposition Effect by Reducing the Saliency of Information about a Stock's Purchase Price. Journal of Economic Behavior and Organization 107:541-552.
Giglio, S., M. Maggiori, J. Stroebel, and S. Utkus. 2021. Five Facts about Beliefs and Portfolios. American Economic Review 111:1481-1522.
Gneezy, U., and A. Imas. 2017. Lab in the Field: Measuring Preferences in the Wild. In Handbook of Economic Field Experiments, Volume 1, 439-464. Elsevier.
Hartzmark, S. M. 2015. The Worst, the Best, Ignoring All the Rest: The Rank Effect and Trading Behavior. The Review of Financial Studies 28:1024-1059.
Heimer, R. Z. 2016. Peer Pressure: Social Interaction and the Disposition Effect. The Review of Financial Studies 29:3177-3209.
Imas, A. 2016. The Realization Effect: Risk-Taking after Realized versus Paper Losses. American Economic Review 106:2086-2109.
Ingersoll, J. E., and L. J. Jin. 2013. Realization Utility with Reference-Dependent Preferences. The Review of Financial Studies 26:723-767.
Liao, J., C. Peng, and N. Zhu. 2022. Extrapolative Bubbles and Trading Volume. The Review of Financial Studies 35:1682-1722.
Linnainmaa, J. T. 2010. Do Limit Orders Alter Inferences about Investor Performance and Behavior? The Journal of Finance 65:1473-1506.
Nickell, S. 1981. Biases in Dynamic Models with Fixed Effects. Econometrica 49:1417-1426.
Odean, T. 1998. Are Investors Reluctant to Realize Their Losses? The Journal of Finance 53:1775-1798.
Seru, A., T. Shumway, and N. Stoffman. 2010. Learning by Trading. The Review of Financial Studies 23:705-739.
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Conclusion and Path Forward

The central idea in this manuscript deserves to be taken seriously and is, in the reviewer's judgement, likely to be at least partly correct. The disposition effect is measured over a sale sample whose composition is endogenous to prior trading, and treating the resulting statistic as a clean read on realization preference is unwarranted. The authors have assembled data unusually well suited to making that case, and the interlinked experimental and field design is a genuine methodological advance that the paper's own framing arguably undersells. The difficulties identified above are matters of inferential discipline rather than of conception, and they cluster into three questions the revision should answer. Does the Contrarian Degree measure price-contingent style, or does it register rebalancing arithmetic, learned reversion in the assigned price paths, or the same asymmetry the disposition statistic captures? Do the outcome variable and the estimation samples correspond to the economic objects the theory concerns, given that experimental gain status is computed against cumulative contributions rather than a cost basis, that partial trims are pooled with liquidations, and that the sample selection operates through the very channel being identified? And are the mechanism and its magnitudes established, given that Appendix C proves an identity on a non-comparable scale, that the accounting and belief readings are not separated, and that neither headline number is traceable to an estimate with an interval?

Encouragingly, each question admits a concrete answer from data already in hand. Split-sample estimation of style and disposition, re-estimation of style on the change in risky share, exploitation of random path assignment to test whether measured contrarianism tracks realized path autocorrelation, reconstruction of the experimental cost basis from recorded prices and trades, separation of full liquidations from partial trims, results reported without the within-month-sale restriction and across activity thresholds, calibration of the Appendix C benchmark to observed moments with standard Odean statistics, a test of whether the style gradient strengthens with the number of purchases per position, permutation-based inference exploiting the experiment's randomization, local polynomial estimation with the standard discontinuity diagnostics, and interval estimates for the decomposition share and the style ratio would together transform the evidence. Several of these exercises may well strengthen the paper's conclusions, and where they qualify them the qualifications are likely to be interesting in their own right. The reviewer would welcome the opportunity to read a revised version.