The trade stops making sense when its backward recursion turns concave. Cui, Li, Li and Shi scale an entropy penalty by the squared wealth gap, keeping their long-only mean-variance rule convex only while a scalar continuation coefficient stays positive at every rebalancing date. A fixed temperature preserves convexity at any temperature, though it gives up that scalar recursion. In monthly industry data, the positivity test fails in 55 of 72 rolling windows at 0.01.

Why scale the temperature?

The paper tackles multi-period Markowitz mean-variance selection with no shorting. Over T=6 periods, the investor minimizes terminal-wealth variance subject to a target mean d. Entropy regularization comes from reinforcement learning (Wang and Zhou 2020 in continuous time); it randomizes allocations for exploration. There is no new return forecast here. The advance is a solvable long-only recursion after entropy enters the problem.

The authors begin with the discrete-time, pre-commitment problem. Its standard embedding makes control quadratic in y_t, the gap between current wealth and a shifted target. Cui and coauthors showed in 2014 how the no-shorting problem stays tractable: with a positive gap, risky holdings are s_t y_t K_t, where K_t is a nonnegative portfolio vector independent of wealth. At zero or below, risky holdings vanish. Backward induction needs just one scalar continuation coefficient C_t and one vector K_t per date.

Putting a fixed temperature on a distribution over the nonnegative orthant looks natural. It also spoils that reduction. The orthant's normalizing integral varies with the state, leaving a value function that is no longer quadratic. Proposition 2.1 establishes the failure at the last date. In the simulation, dividing the final-stage value by q²y² gives a ratio of about 0.4502 throughout the unconstrained case. With no shorting and a fixed temperature, it rises from 0.2529 at y=0.05 to 0.4611 at y=2.

The proposed temperature is q_t² y_t² τ, and randomness applies only to K. The ratio is flat again, at about 0.4650. C_t then equals minus 2τ times the log of the integral of exp(minus h_t/τ) over K; h_t is the stage loss. Entropy changes C_t directly, so a negative coefficient makes the positive-gap branch concave. Theorem 3.2 proves that a sufficiently small τ keeps every C_t positive. With the additional conditions 0 < C_0 < 1 and d > q_0x_0, the authors obtain a closed-form multiplier and recover the original solution as temperature goes to zero.

The tests comprise a four-asset, six-period lognormal-mixture simulation and a rolling test of ten value-weighted Fama-French industries. The industry data are monthly, from January 1975 to December 2025. Each 180-month training window yields 175 overlapping six-month paths. The paper reports 72 non-overlapping six-month test episodes, beginning in January 1990 and ending in July 2025, with a target terminal mean of 1.10.

The coefficient can fail early

In the simulation, the minimum coefficient goes from 0.6376 at τ=10⁻⁴ to 0.6615 at τ=10⁻³, then falls to 0.1432 at τ=0.015. At τ=0.0225, C_1 = -0.1298 breaks the recursion at an interior date, before C_0 can be formed. The authors put it plainly: "positivity is a genuinely recursive requirement, not merely a condition on the initial continuation coefficient."

Industry data tighten the limit. Every one of the 72 windows remains positive through τ=5×10⁻³. At 7.5×10⁻³, 69 survive, although the worst coefficient has reached -0.0574. At 10⁻², just 17 survive. Positivity has therefore failed in 55 of 72 industry windows at a temperature where the simulation's minimum coefficient remains 0.4061. Proposition 3.3 supplies a checkable bound: the smallest second-moment determinant across dates must reach at least (2πe(1−Δ)/n)^n, with 0 < Δ < 1. We did not see the empirical section evaluate it. Instead, the algorithm stops when a coefficient is nonpositive, lowers τ and starts again. A desk needs the full backward pass, with every C_t checked before it trades.

What reaches the market

The derived policy is randomized. The reported trades are not: as the authors say up front, every backtest takes the mode, the argmin of stage loss. Entropy affects the coefficients and multiplier rather than randomizing an actual allocation. In simulation, the mode policy has a Sharpe-like ratio of 0.7220 at τ=10⁻⁴, 10⁻³ and 10⁻²; terminal mean runs from 1.1228 to 1.1926. Three identical Sharpe figures suggest to us that τ changes composition very little there. It mostly adjusts leverage in the simulation, while industry Sharpe moves from 0.2458 to 0.2814.

The target can still be missed. The regularized multiplier, the authors write, "need not enforce the terminal mean constraint exactly." Simulation overshoots by 0.0126 at τ=10⁻³. Every empirical row falls short of 1.10, including the ETO benchmarks. Those benchmarks have no entropy and miss by -0.0299 to -0.0309, pointing to out-of-sample estimation as the shared cause.

Does the benchmark edge hold?

The abstract stresses structure; the empirical section also claims performance. The authors favor target error in the comparison: -0.0091 at τ=10⁻³ is "substantially smaller in magnitude than those of the three ETO benchmarks", whose errors are around -0.03. They say the mode policy "produces economically reasonable outcomes." At τ=10⁻³, it records mean 1.0909, variance 0.0648, target error -0.0091, 5% wealth quantile 0.7055, wealth CVaR 0.3177 and Sharpe 0.2791. The best benchmark row, ETO-FF3, has 1.0691, 0.0393, -0.0309, 0.8261, 0.4782 and 0.2488, respectively. The mode gets nearer the target and earns a higher Sharpe, alongside 65% more variance. Its 5% wealth quantile is 0.7055 against 0.8261; wealth CVaR is 0.3177 against 0.4782.

Temperature selection happens on the test episodes. Seven values appear across the same 72 episodes, with Sharpe spanning 0.2458 to 0.2814. At τ=10⁻⁴, Sharpe trails ETO-FF3's 0.2488. The authors acknowledge that "recursive convexity alone does not determine the economically preferred temperature" and leave data-driven selection for future work. They defend the grid as a menu because "the temperature materially changes the balance between target tracking and risk reduction." A reader can use a menu to choose a risk level. Yet τ=10⁻³ has the smallest target error on the same 72 episodes used to assess it, making the row picked for that error an ex-post choice. The grid's top Sharpe, 0.2814, occurs at τ=2.5×10⁻³, with target error widened to -0.0234. We found no standard errors for the comparisons.

Costs and dependence also matter. We did not find transaction costs mentioned anywhere, so the reported figures should be read as gross. The theory assumes returns independent across periods, whereas the 175 training paths cut from one 180-month window share most of their months.

The risk ratio has a naming issue, too. Simulation prose calls it "Sharpe-like"; tables call it a Sharpe ratio. We did not find a formula or an annualization for six-month terminal wealth.

Our substitute run

We cannot trade Fama-French industry portfolios, and our build cannot reproduce the paper's method as specified. Our substitute is closer to the classical no-shorting baseline that the paper starts from; it uses daily US sector ETFs and cash. We chose both the daily frequency and the ETF universe ourselves. This run does not test the authors' claim, and the industry figures above do not carry over to it. A version choosing τ from trailing data and still beating the benchmarks' roughly -0.03 target error after costs would change our view.