Randomized Study of Daytime vs. Delayed Eating: Effect on Weight and Metabolism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Study of Daytime vs. Delayed Eating: Effect on Weight and Metabolism (NCT04414644), a randomized na study. The primary outcome is Body Mass Changes Between the Daytime vs. Delayed Eating Conditions.

2. Clinical Question

This is a question about the contrast between two eating schedules under the study conditions, not simply about whether body mass changed over time. The primary outcome is expressed as a pre-post change in kilograms for each condition. The registry reports a mean change for each condition and a mean difference comparing delayed with daytime eating.

The study also assessed respiratory quotient and energy expenditure as secondary outcomes. These provide additional metabolic measures, but they do not replace the primary body-mass question. The registry lists the study as completed and randomized, with no masking. Details about how the randomization sequence was generated or concealed are not reported in the registry record.

3. Trial Design

The registry describes a randomized, unmasked crossover study of eating timing. In a crossover design, participants experience more than one study condition, so each participant can contribute outcome information under both conditions. Here, the registry states that all participants included in outcome analyses completed both the daytime and delayed eating conditions. The analyzed groups therefore represent condition-specific observations from participants who experienced both schedules, rather than separate sets of people assigned permanently to one condition.

The daytime schedule placed study-provided meals and snacks between 0800 and 1900; the delayed schedule placed them between 1200 and 2300. Condition sequence labels describe a 2 week washout between conditions. The registry does not report further details about the washout rationale or whether effects from the first condition could persist into the next.

Enrollment was 17. The primary and secondary outcome summaries each report 12 participants per condition. The registry says that 12 participants completed both conditions and were included in analyses. It does not provide a full accounting of the difference between enrollment and the analyzed population, such as participant flow by reason for non-completion.

For each outcome, changes were calculated from baseline to 8 weeks, the end of that condition. The primary measure was body mass change in kilograms. The secondary measures were respiratory quotient change and energy expenditure change. The registry gives mean changes and standard deviations by condition, along with unadjusted comparisons. It does not list reported analyses in the results record. Details of the statistical model, including how the crossover structure, condition sequence, or possible period effects were handled, are not reported in the registry record.

The study is listed as randomized, with no masking, and its phase is listed as not applicable. The registry records the study as completed. Original design assumptions—including the planned sample size and its justification—are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All participants completed both eating conditions in a cross-over design and are included in the analyses for the outcomes for each eating condition.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All participants complete all of the eating conditions and washout period, so they are included as one group in the baseline analysis population.

6. Primary Endpoint

The registry lists the primary outcome as Body Mass Changes Between the Daytime vs. Delayed Eating Conditions, measured over pre-post changes between the daytime and delayed eating conditions; change for each condition is calculated from measures at baseline and 8 weeks (end of condition).

The primary endpoint is change in body mass, measured in kilograms, from baseline to the end of each 8-week eating condition. The registry reports the mean and standard deviation of those changes for the daytime and delayed conditions. It also reports a mean difference comparing the delayed condition with the daytime condition.

Change from baseline is used to describe how the measure shifted during each condition, rather than only comparing body mass at one measurement time. The paired crossover structure means participants contributed measurements under both schedules, which can allow a within-person comparison. However, the registry does not report the exact statistical model used to estimate the comparison, so it is not possible to establish from the record whether the reported comparison fully accounts for pairing, sequence, or period effects.

The direction of the comparison matters. The daytime condition had a mean change of -1.1 kg, while the delayed condition had a mean change of 0.2 kg. The reported mean difference for delayed versus daytime eating was 1.3 kg. These are average changes in this analyzed group under the study conditions; they do not describe every participant’s response. The standard deviations of 1.6 kg and 1.3 kg describe variation in observed changes within each condition.

Body mass was chosen as the primary outcome in a study whose stated purpose included assessing effects on body mass, adiposity, and energy metabolism. The registry does not report a primary measure of adiposity among the posted outcomes. The record therefore supports interpretation of the listed body-mass outcome, but not conclusions about every component of the broader study purpose.

7. Results Posted in the Registry

• Delayed Eating Condition: mean 0.20 versus -1.10 on control; difference 1.30 (95% CI 0.13 to 2.47), standardized effect d = 0.89; z-test p = 0.029.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Respiratory Quotient Changes in the Daytime vs Delayed Eating Conditions

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Delayed Eating Condition: mean -0.02 versus -0.01 on control; difference -0.01 (95% CI -0.05 to 0.03), standardized effect d = -0.18; z-test p = 0.668.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed Eating Condition and the control. The interval gives the range of effects that remain compatible with the data.

Energy Expenditure Changes Between the Daytime and Delayed Eating Conditions

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Delayed Eating Condition: mean 24.35 versus -93.66 on control; difference 118.01 (95% CI 0.68 to 235.34), standardized effect d = 0.80; z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Delayed Eating Condition than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes add metabolic measures to the body-mass comparison, but their pattern is not uniform. The respiratory quotient estimate is close to zero relative to its uncertainty, whereas the energy expenditure estimate is positive with a confidence interval that approaches zero at its lower end. Together, these findings do not form a uniformly clear signal across all measured outcomes.

The primary body-mass comparison is the main result because it was designated as the primary endpoint. Secondary outcomes can provide context about other measured processes, but they do not automatically validate or explain the primary result. The registry does not report a formal analysis linking changes in respiratory quotient or energy expenditure to the body-mass result, so the measures should not be interpreted as evidence of a particular mechanism.

The secondary p-values are unadjusted. When multiple outcomes are examined, the chance of at least one apparently notable result can increase, even if no real effect exists for any outcome. Without a reported multiplicity plan, the secondary p-values carry less confirmatory weight than a prespecified primary analysis would. The energy expenditure p-value is close to a conventional threshold, but that alone does not establish a robust secondary finding. The respiratory quotient result likewise should not be framed as proof of no difference; its interval includes effects in both directions.

All outcomes are based on the same 12 participants completing both conditions, and all are changes from baseline to the end of each 8-week condition. This shared participant set means the outcome summaries are not independent replications of the primary comparison. The registry does not report whether the secondary outcomes were prespecified in a hierarchy, how their analyses accounted for the crossover, or whether any broader multiplicity adjustment was planned. Their main value is descriptive: they show what the posted metabolic measurements looked like in this small analyzed group, while leaving substantial uncertainty about precision and inferential status.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Respiratory Quotient Changes in the Daytime vs Delayed Eating Conditions
• Energy Expenditure Changes Between the Daytime and Delayed Eating Conditions

9. Statistical Interpretation

10. Statistical Methods Explained

What do the means and standard deviations describe?

Each outcome is continuous, so the registry reports a mean change and a standard deviation for each eating condition. The mean is the average observed change in the analyzed participants. The standard deviation describes how dispersed participant changes were around that average. A mean is not a description of what happened to every participant, and the standard deviation is not a confidence interval for the mean.

For body mass, the mean change was -1.1 kg in the daytime condition and 0.2 kg in the delayed condition. The standard deviations were 1.6 kg and 1.3 kg, respectively. For respiratory quotient, the reported means were -0.012 and -0.021, with standard deviations of 0.038 and 0.062. For energy expenditure, the mean changes were -93.66 kcal/day and 24.35 kcal/day, with standard deviations of 97.74 and 182.9. These are condition-specific summaries; the comparison estimates address the contrast between conditions.

What does the mean difference represent?

The registry presents the comparisons as delayed condition minus daytime condition. A positive estimate therefore means that the delayed-condition change was higher than the daytime-condition change on the outcome’s measurement scale. For body mass, the reported difference was 1.3 kg. For respiratory quotient, it was -0.009. For energy expenditure, it was 118.0 kcal/day. The sign must be interpreted together with the direction of the subtraction and the scale of the outcome.

In a crossover study, the two sets of condition observations come from participants who experienced both conditions. A comparison that accounts for this pairing may differ in precision from a comparison that treats condition groups as unrelated. The registry identifies the crossover design and reports the number included in each condition, but the model or calculation used for the comparison is not reported in the registry record. It is therefore not appropriate to assert that a particular paired test, mixed model, or adjustment was used.

How should a confidence interval be read?

A confidence interval conveys uncertainty in an estimated comparison. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. If an interval includes zero for a difference, the data are compatible with no difference as well as with effects on either side of zero at the interval’s confidence level. If it lies entirely on one side of zero, the range of estimates represented by that interval has a consistent direction. This general description does not replace details about the statistical method used.

The primary body-mass interval is reported entirely above zero. The respiratory quotient interval includes zero. The energy expenditure interval is reported zero but has a lower limit close to zero. The energy expenditure result is therefore less decisive in practical interpretation than the point estimate alone might suggest. Confidence intervals do not state the probability that a particular fixed value is true, and they do not account for design or measurement limitations that are not incorporated into the analysis.

What does a p-value add?

An unadjusted p-value describes how unusual a test statistic at least as extreme as the observed one would be under a specified null hypothesis and the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The registry reports unadjusted p-values of 0.029 for body mass, 0.668 for respiratory quotient, and 0.049 for energy expenditure. The record does not report whether the analyses were prespecified or how multiplicity was addressed.

Because several outcomes were evaluated, the p-values should not be read as if each were the sole planned test. Unadjusted results do not account for the possibility of finding a small p-value by chance across multiple tests. This concern is particularly relevant to secondary outcomes. The registry does not report a multiplicity procedure or a hierarchy of confirmatory hypotheses.

Why does over-dispersion matter in general?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if the model does not allow for the extra variability. The outcomes in this record are continuous and summarized with standard deviations; no over-dispersion assessment or model diagnostics are reported. It would therefore be speculative to claim that over-dispersion occurred or that a particular correction was needed. The general lesson is that model assumptions affect uncertainty estimates, and the registry’s limited methods detail prevents a full diagnostic assessment.

What is known about the analysis plan?

The registry reports mean outcomes, standard deviations, comparison estimates, confidence intervals, and unadjusted p-values. It does not report detailed model specifications, assumptions, analysis populations beyond the statement that 12 participants completed both conditions, missing-data procedures, or interim analyses. A statistical plan and original sample-size justification are not reported in the registry record. The posted summaries allow a descriptive reading of the effects and their uncertainty, but not a complete audit of the analysis.

11. Confidence Intervals and Precision

The body-mass comparison is estimated as 1.3 kg, with a confidence interval reported from 0.134 to 2.466 kg. The interval lies above zero, but its width indicates that the compatible effect estimates range from a relatively small positive difference to a larger one. The mean difference alone therefore gives an incomplete account of uncertainty. The analysis includes 12 participants who completed both conditions, so precision is limited by the size of the analyzed group.

For respiratory quotient, the estimate is -0.009 and the confidence interval runs from -0.050 to 0.032. Since zero lies within that range, the data are compatible with effects in either direction as well as little or no difference. The point estimate should not be treated as a precise indication of the direction or magnitude of a condition contrast.

The energy expenditure estimate is 118.0 kcal/day, with a confidence interval from 0.677 to 235.3 kcal/day. The lower bound is close to zero relative to the interval’s overall span, while the upper bound allows a substantially larger positive difference. This is a broad range of plausible estimates, rather than a precise estimate centered tightly around the point value.

In general, confidence intervals reflect sampling uncertainty under the analysis method and its assumptions. They do not capture every source of uncertainty, including possible attrition bias, carryover, measurement limitations, or unreported analysis choices. The registry does not specify the confidence level or detailed method used to construct the intervals. The results should therefore be read with the reported ranges and design limitations in view, rather than as exact descriptions of effects that would necessarily recur in another study.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, not the original trial’s design justification. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. Original design assumptions for the trial are not reported in the registry record.

For the primary body-mass comparison, planning for 100% of the observed effect gives 20 participants per arm for 80% power and 27 participants per arm for 90% power. Planning for 75% of the observed effect gives 36 participants per arm for 80% power and 47 participants per arm for 90% power. Planning for 50% of the observed effect gives 79 participants per arm for 80% power and 106 participants per arm for 90% power.

In plain language, the 80% power column gives the illustrative number of participants per arm needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% column describes the corresponding planning target for a higher chance of detection. These are planning calculations, not observed power.

The smaller the effect a future study aims to detect, the more participants the calculation requires. That pattern appears in the increasing estimates as the planning target moves from 100% to 75% and 50% of the observed effect. Since the study is a crossover, its actual design differs from the equal-allocation two-arm planning setup described for these illustrations. The figures should not be interpreted as a direct reconstruction of the trial’s intended or optimal enrollment.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.300; pooled standard deviation σ = 1.458.
2. n = 2 × (1.96 + 0.842)² × 1.458² / 1.300² = 19.7, rounded up to 20 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 1.3                      # observed difference in means
sigma <- 1.45773797371133                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4414644)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 20 (80% power), 27 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 47 (90% power)
 50% of observed effect: n per arm = 79 (80% power), 106 (90% power)
power.t.test: 20.7 
Simulated power at n = 20 per arm: 0.787 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry reports one primary outcome and two secondary outcomes, with unadjusted p-values for the comparisons. It does not report a procedure for adjusting for multiple testing, a hierarchy governing interpretation of the outcomes, or which outcomes were designated as confirmatory versus exploratory beyond the primary and secondary labels. As a result, the secondary p-values should be interpreted cautiously. The record does not establish whether multiplicity was considered in the original statistical plan.

Missing-data information is limited. Enrollment was 17, while the record states that 12 participants completed both conditions and were included in outcome analyses. A full participant-flow account, reasons for non-completion, and the amount or pattern of missing outcome data are not reported in the registry record. The record also does not describe imputation, complete-case rules beyond the stated completed-participant population, or sensitivity analyses for missing data.

The analysis population is described as participants who completed both eating conditions. Although the outcome summaries report 12 participants for each condition, the registry does not provide a separate accounting of randomized participants by sequence or explain how participants who did not complete both conditions were treated. It is not possible to determine whether the analyses followed an intention-to-treat principle or another prespecified population definition.

Because this is a crossover design, relevant analysis details include handling of paired observations, period effects, treatment sequence, and possible carryover between conditions. The registry describes a 2 week washout in the sequence labels, but does not report how the analysis addressed these design features. Interim analyses, stopping rules, and other components of a statistical analysis plan are not reported in the registry record. These omissions do not invalidate the posted summaries, but they limit assessment of how robustly the analysis reflects the design and how missingness or multiple testing may affect interpretation.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

The registry lists serious adverse events and other adverse events by condition sequence. In the group assigned to daytime eating followed by a 2 week washout and delayed eating, 9 participants were at risk, with 0 serious adverse events, 0 other adverse events, and 0 deaths reported. In the group assigned to delayed eating followed by a 2 week washout and daytime eating, 8 participants were at risk, with 0 serious adverse events, 0 other adverse events, and 0 deaths reported.

These figures describe the events recorded in the registry for the listed groups. Zero reported events does not establish that no events occurred outside the registry’s definitions or observation process, nor does it establish that a study condition is free of risk. The groups are small, and the record does not report further detail about event collection, follow-up duration for safety, or attribution. The figures should be read as the posted event counts, not as a broad safety conclusion.

16. What the Result Does, and Does Not, Mean

The posted primary result indicates a difference in average body-mass change between the two eating conditions in the analyzed participants. The daytime condition had a mean change of -1.1 kg; the delayed condition had a mean change of 0.2 kg; and the reported delayed-minus-daytime comparison was 1.3 kg. The confidence interval lies above zero, while still allowing a range of possible effect sizes. This is evidence about the observed study contrast, not a precise forecast for any individual.

The result does not show that every participant’s body mass changed in the same direction. Group means and standard deviations conceal individual variation. Nor does it show what would happen outside this study’s setting, with different participants, eating schedules, durations, or levels of control over other behaviors. The record’s stated purpose mentions control of eating and sleep timing, caloric intake, and exercise, but the posted statistics alone cannot demonstrate how fully each factor was controlled.

The study enrolled 17 participants, while 12 completed both conditions and were included in outcome analyses. That limited analyzed sample and the absence of a detailed accounting of non-completion make it difficult to assess how broadly the results apply or whether attrition influenced the estimate. The registry also does not report enough statistical-method detail to verify how the crossover structure was handled.

The secondary measures do not provide a complete explanation for the primary result. Their estimates have differing levels of uncertainty, and their p-values are unadjusted. The registry does not report an analysis establishing that changes in these metabolic measures mediate, cause, or otherwise explain the body-mass contrast.

Overall, the record supports a cautious description of the reported averages and their uncertainty. It does not establish a general effect for all adults, answer outcomes not posted, or justify a medical recommendation. A larger, fully reported analysis with explicit methods and participant flow would be needed to clarify the reproducibility and generalizability of the observed differences.

17. Why This Trial Matters Statistically

This study illustrates why design and analysis details matter alongside an effect estimate. A crossover trial lets the same participants experience both conditions, which can make within-person comparisons informative. It also introduces considerations that are specific to repeated conditions, including sequence and period effects and possible carryover. The registry names the crossover design and a 2 week washout, but does not report how the analysis addressed these features.

The body-mass estimate is interpretable in direction and scale, but its confidence interval is essential context. A point estimate of 1.3 kg alone can appear more definite than the range of uncertainty warrants. The secondary results further show why several outcomes should not be treated as several independent confirmations: they were measured in the same participants, and the registry does not report multiplicity adjustment.

The difference between enrollment and the analyzed group also has statistical importance. Without participant-flow details and missing-data methods, readers cannot fully judge whether the analyzed sample represents those randomized. Sample-size planning figures based on an observed estimate are useful as illustrations of how assumed effects and power targets affect required enrollment, but they are not the trial’s original design rationale and are not observed power.

More broadly, the record demonstrates the value of reporting statistical plans, analysis populations, assumptions, missing-data handling, and crossover-specific methods. Such information helps readers distinguish the numerical result from the strength of the evidence supporting it. Here, the posted summaries allow a transparent description of the estimates, while several questions needed for a complete statistical appraisal remain unanswered.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information in this record. The analyzed population is small: 12 participants completed both conditions, compared with enrollment of 17. The registry does not report a full participant-flow account or reasons for non-completion, so the possible influence of attrition cannot be assessed.

The study is a crossover, but the statistical model and treatment of paired observations are not reported. Details about sequence effects, period effects, and carryover are also absent. A 2 week washout is stated in the condition-sequence labels, but the registry does not explain the basis for that duration or report a test of residual effects.

The record does not describe missing-data procedures, sensitivity analyses, model diagnostics, or an analysis plan for the secondary outcomes. The reported p-values are unadjusted, and no multiplicity strategy is reported. These omissions make it harder to distinguish confirmatory findings from exploratory patterns, particularly for secondary outcomes.

The outcome summaries describe change over each 8-week condition, but the registry does not report posted outcomes for adiposity even though it appears in the study purpose. Nor does the record provide enough detail to evaluate how eating and sleep timing, caloric intake, and exercise were controlled in practice. The population is described as healthy adults, with obesity listed as a condition; further demographic and baseline characteristics are not included in the registry record. Consequently, the representativeness of the analyzed group and the broader applicability of the estimates cannot be assessed from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Study of Daytime vs. Delayed Eating: Effect on Weight and Metabolism — NCT04414644.
• Registry record last updated 2025-03-11; status last verified 2025-03.
• Results first posted 2025-03-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04414644 is a completed randomized, unmasked crossover study of daytime versus delayed eating, sponsored by the University of Pennsylvania. Enrollment was 17. The registry states that 12 participants completed both conditions and were included in outcome analyses. Each condition lasted 8 weeks, with a 2 week washout described between conditions.

The primary outcome was change in body mass. Mean change was -1.1 kg for daytime eating and 0.2 kg for delayed eating; the reported delayed-minus-daytime mean difference was 1.3 kg, with an unadjusted p-value of 0.029. Secondary outcomes were respiratory quotient and energy expenditure changes. The registry does not list reported analyses or provide full details of statistical methods, missing-data handling, or multiplicity procedures.

The results describe the posted outcomes in a small analyzed sample. The confidence intervals and unadjusted status of secondary results are important to interpretation. Several design and analysis details needed for a complete appraisal are not reported in the registry record.