Intermittent Fasting for the Treatment of Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Intermittent Fasting for the Treatment of Type 2 Diabetes Mellitus (NCT05860413), a randomized na study. The primary outcome is Retention.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-masked, parallel-group behavioral trial. The study is marked completed, with enrollment of 57. Its start date is 2023-01-24, and its primary completion date is 2025-05-20. The phase is listed as not applicable. The sponsor is the University of Kansas Medical Center.

Participants were assigned to one of two programs: intermittent energy restriction (IER) or time-restricted eating (TRE). IER is described as a very-low energy diet of 550-800 kcal/d on 2-3 days per week. TRE is described as eating within an 8-hour period. The registry identifies both as behavioral interventions and specifies a parallel model, in which the arms are distinct groups rather than successive treatment periods.

The primary outcome is retention over 52 weeks, reported as a count of participants. The outcome description frames retention as the percentage of participants who completed the program, but the posted arm results are counts: 21 for IER and 24 for TRE. The denominators shown for the arms are 29 and 28, respectively. The record lists HbA1c and postprandial glucose as secondary outcomes. Numerical results for these secondary measures are not reported in the registry record.

The registry labels masking as double, but does not describe who was masked or how masking was maintained in these behavioral programs. Details of sequence generation, allocation concealment, adherence monitoring, the analysis population, and the original statistical design assumptions 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.

Before assignment: 57 participants were enrolled and randomized.

Overall Study

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.

6. Primary Endpoint

The registry lists the primary outcome as Retention, measured over 52 weeks.

Retention is the primary endpoint. In this trial, it is used as a feasibility measure: the outcome description defines feasibility in terms of whether participants completed the program over one year. The time frame is 52 weeks. The posted arm values are counts of participants, not percentages, even though the endpoint description refers to the percentage completing.

Retention can help describe whether participants remained in a study long enough to complete its planned follow-up. It is not itself a measure of glycemic change, adherence to every element of the program, or diabetes remission. A participant counted as retained may or may not have followed the intervention exactly; the registry record does not define retention beyond the completion description, nor does it report a separate adherence measure.

The posted counts are 21 in IER and 24 in TRE, with arm denominators of 29 and 28. These figures describe the observed completion outcome in this trial. The record does not provide reasons for non-completion or the timing of withdrawals. HbA1c and postprandial glucose are listed as secondary outcomes, but their results are not reported in the registry record. Accordingly, the primary retention result addresses feasibility as recorded, not whether either program changed glycemia.

7. Results Posted in the Registry

• Time-restricted Eating (TRE): 85.7% (24/28) versus 72.4% (21/29) on control; risk difference 13.3 percentage points (95% CI -7.5 to 34.1), risk ratio 1.18 (0.90–1.55); unadjusted two-proportion z-test p = 0.218.

8. Statistical Interpretation

9. Statistical Methods Explained

The main statistical comparison uses a binary outcome: each participant either counts as retained or does not, according to the study's completion definition. For a binary outcome, a group result can be expressed as a count, a proportion, or a contrast between groups. The registry provides the counts and denominators for retention and reports a risk-difference comparison.

What does a risk difference express?

A risk difference subtracts the outcome proportion in one group from the outcome proportion in the other. The posted comparison is TRE relative to IER, and its estimate is 0.133. A positive value indicates a greater observed proportion in the first-named group, TRE, under this ordering. The size of the estimate is on the absolute proportion scale, not a relative scale. This makes it conceptually different from a risk ratio or odds ratio.

The comparison also includes a confidence interval, from -0.075 to 0.341. The interval represents a range of estimates compatible with the observed data under the method's assumptions; it is not a range containing a known true effect with certainty. Because this interval includes zero, the data do not precisely distinguish a positive difference from no difference or a negative difference. The interval is an important complement to the point estimate, since the point estimate alone does not convey sampling uncertainty.

How should the p-value be read?

The unadjusted p-value is 0.218. In general, a p-value describes how unusual results at least as extreme as the observed result would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry's planning illustration names a two-sided significance level of 0.05. The reported p-value is larger than that level, but this does not demonstrate equivalence or prove that the programs have the same retention.

General statistical interpretation also depends on the analysis method, the outcome definition, and how missing observations were handled. Those details are not reported in the registry record. The posted p-value is described as unadjusted, and no multiplicity procedure is described. A reader should not assume that the result was adjusted for other outcomes or analyses.

What are relative measures?

Risk ratios and odds ratios express between-group contrasts on relative scales. A risk ratio compares outcome proportions; an odds ratio compares outcome odds. These measures can appear more or less dramatic than an absolute risk difference because their scales differ. The record includes relative summaries as well as the risk difference, but the primary interpretation centers on the risk difference and its interval. For a modest trial with a binary endpoint, relative measures can also have substantial uncertainty, and should not be treated as a separate confirmation of a result.

In general, odds are not the same thing as probability, and an odds ratio is not interchangeable with a risk ratio. Neither a relative measure nor an absolute measure resolves uncertainty caused by a limited amount of outcome information. The arm counts and interval are therefore central to understanding how much the posted comparison can support.

What does the recalculated label mean?

A recalculated comparison is a simple, unadjusted calculation based on the arm-level summary statistics in the registry. It does not use participant-level records or account for covariates unless those are explicitly included in the method. Here, no discrepancy is flagged between the recalculation and a sponsor result, but the record lists no analyses. The recalculated summary should not be mistaken for a full statistical analysis plan or a more detailed sponsor analysis.

Randomization is intended, in general, to reduce systematic differences between assigned groups, but a randomized label alone does not describe the implementation or guarantee balance in every characteristic. The registry record does not report the randomization procedure, allocation concealment, baseline characteristics, or whether the primary analysis followed assignment regardless of intervention adherence. Those omissions limit assessment of the assumptions underlying a causal comparison.

Why can over-dispersion matter?

Over-dispersion is a general issue for outcomes in which variability is greater than a simple model expects. It can make standard errors too small if a model assumes less variation than the data contain, leading to confidence intervals that are too narrow and tests that are too optimistic. For a binary retention outcome, the relevant model and variance assumptions depend on the analysis approach. The registry record does not report a model or an over-dispersion assessment, so no specific conclusion about over-dispersion can be drawn for this comparison.

Finally, the study's stated aims include glycemia and possible remission, but the posted primary result is retention. HbA1c and postprandial glucose appear as secondary outcome names without numerical estimates. Statistical methods for those endpoints cannot be evaluated from the record, and the retention analysis cannot be used as a substitute for them.

10. Confidence Intervals and Precision

The precision of the primary comparison is conveyed most directly by its confidence interval. For TRE relative to IER, the posted risk-difference estimate is 0.133, and the interval extends from -0.075 to 0.341. A confidence interval describes the uncertainty around an estimate under the statistical method's assumptions. It does not guarantee that the true difference lies within its endpoints, nor does it describe the range of individual participant outcomes.

The interval includes zero. That means the observed data do not rule out no difference under this interval-based analysis. It also extends to estimates on either side of zero, indicating uncertainty about the direction and size of the underlying difference. The positive point estimate alone should not be read as a precise finding of higher retention with TRE. The unadjusted p-value of 0.218 is consistent with the uncertainty conveyed by the interval, but the p-value and interval answer different statistical questions.

Precision is influenced by the number of outcome observations, the distribution of outcomes across groups, and the analysis method. General statistical reasoning suggests that limited information about a binary outcome can leave a wide range of effects compatible with the data. The registry's observed counts are 21 retained in IER and 24 in TRE, with denominators of 29 and 28. These counts are useful context for the interval but do not justify calculating a new precision measure beyond what is posted.

The record does not report a prespecified precision target, a margin for equivalence, or an interval for secondary outcome results. Therefore, the available interval should be interpreted as uncertainty around the retention comparison only. It does not quantify uncertainty in HbA1c, postprandial glucose, or remission outcomes.

11. 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 sample-size figures are planning illustrations based on the observed retention effect, not the trial's original design assumptions. They report participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planned effect to detect is expressed as a stated fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column indicates the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under those planning assumptions, if that effect were the true one. The 90% power column expresses the analogous planning target at 90% power. These are design calculations, not predictions that a future study will obtain a particular result. The record does not report the trial's own original sample-size justification or design assumptions.

The rows correspond to planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more participants to detect under otherwise similar assumptions, because they are harder to distinguish from random variation. The numbers are illustrations tied to this observed effect and the stated method; they should not be read as definitive enrollment recommendations or as proof that the observed effect is stable.

This is not observed power. Observed power calculated from an observed effect largely restates the result and does not resolve the uncertainty in the estimate. The confidence interval and the underlying counts are more informative about the precision of this trial's retention comparison.

12. 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.724; treatment proportion p₁ = 0.857; average p̄ = 0.791.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5754 = 1.1277.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5676 = 0.4777.
4. n = (1.1277 + 0.4777)² / (0.1330)² = 145.7, rounded up to 146 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
p0 <- 0.724137931034483                          # control proportion
p1 <- 0.857142857142857                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(5860413)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 146 (80% power), 195 (90% power)
 75% of observed effect: n per arm = 275 (80% power), 368 (90% power)
 50% of observed effect: n per arm = 652 (80% power), 872 (90% power)
power.prop.test: 145.7 
Simulated power at n = 146 per arm: 0.807 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists HbA1c and postprandial glucose as secondary outcomes, alongside the primary retention endpoint. It records four outcome measures and zero posted analyses. Numerical results for the secondary outcomes are not reported in the registry record. The record also does not describe additional outcomes or how outcome reporting was organized.

Multiplicity arises when several outcomes, time points, groups, or statistical tests are considered. In general, conducting many tests can increase the chance of obtaining at least one result that appears statistically notable by chance. Researchers may address this through a prespecified hierarchy or a statistical adjustment, but neither approach is described in the registry record. It is therefore not possible to determine whether the reported p-value was part of a broader family of analyses or whether any adjustment was planned.

Missing-data handling is also not reported in the registry record. The retention endpoint itself concerns completion, but the record does not explain how missing outcome measurements were handled for HbA1c or postprandial glucose, or whether a participant who did not complete follow-up contributed any partial data. No imputation method, sensitivity analysis, or assumptions about missingness are reported. These details matter because analyses can differ depending on whether missing results are treated as unavailable, estimated, or handled through a particular model.

The analysis populations are not described. The record does not state whether participants were analyzed according to randomized assignment, according to the intervention followed, or under another definition. Although the study is labeled randomized, that label does not identify which participants or observations contributed to each analysis. The registry does not report an analysis plan or an adjusted model for the retention comparison.

These absences do not establish that multiplicity or missing-data procedures were absent from the research; they mean the procedures are not reported in the registry record. Without outcome-level results and analysis details, the statistical interpretation is limited to the posted retention counts and their unadjusted comparison.

14. 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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event summary reports zero serious adverse events in IER and zero in TRE. It also reports zero deaths in each group. These are the posted counts for the groups at risk listed in the safety record: 29 for IER and 28 for TRE.

For other adverse events, the record reports 17 affected in IER and 12 affected in TRE. These figures should be read as reported event-affected counts, not as estimates of comparative risk adjusted for differences in follow-up or participant characteristics. The record does not provide event terms in the serious-event list, which is empty, and does not provide further detail about the other events in the registry record for this summary.

Zero reported serious events does not establish that serious events are impossible, and a difference in the other-event counts does not by itself establish a causal effect of either program. The safety figures are descriptive. The registry record does not report event severity details beyond the serious versus other grouping, timing, relatedness assessments, or a formal statistical comparison. They should therefore be interpreted alongside the trial's limited size and the reporting detail available, not as a complete account of safety.

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

The result answers a narrow question: how many participants were recorded as retained at 52 weeks in each intermittent-fasting arm? The counts are 21 in IER and 24 in TRE. The risk-difference estimate for TRE relative to IER is 0.133, with a confidence interval from -0.075 to 0.341 and an unadjusted p-value of 0.218. Together, these summaries indicate uncertainty about the size and direction of the retention difference.

The result does not show that the two programs are equivalent. Establishing equivalence would require a defined equivalence margin and an analysis designed to assess it; those are not reported in the registry record. Nor does the result establish that one program is superior. The point estimate is not precise enough to settle the comparison, and the interval includes zero.

Retention is a feasibility outcome, not a clinical measure of glycemic control. The registry's summary describes a broader interest in whether the programs could improve glycemia and potentially induce remission, but HbA1c and postprandial glucose results are not reported in the registry record. The posted retention figures therefore do not establish improvement in glycemia, remission, or any other clinical benefit. They also do not demonstrate that participants followed every aspect of their assigned program.

The study compares two intermittent-fasting approaches and does not have a posted usual-care or untreated comparison arm. It cannot, in the registry record reported, isolate the effect of intermittent fasting as a general approach compared with no fasting. The findings describe participants in this completed randomized, double-masked, parallel trial, with its recorded interventions and follow-up. The registry information does not support broader claims about populations, settings, or programs beyond those studied.

16. Why This Trial Matters Statistically

This trial is statistically informative as an example of the difference between an observed estimate and a precise conclusion. The observed retention counts favor TRE in direction, and the reported risk difference is positive. However, the confidence interval spans zero and includes a range of possible effects on both sides. The point estimate cannot be interpreted without that uncertainty.

The distinction between feasibility and clinical efficacy is also important. Retention can show whether participants completed follow-up under a study program, while HbA1c and postprandial glucose address glycemic outcomes. The registry identifies those secondary outcomes but does not report their results. This means the available primary finding is about completion, not whether glycemia changed.

The sample-size illustrations show how planning depends on the effect chosen for detection. Under the stated assumptions, smaller effects require more participants per arm. These calculations are not observed power and do not indicate that the trial was designed around those assumptions. The original sample-size rationale is not reported in the registry record.

Finally, the record illustrates why transparent reporting of analysis populations, missing-data procedures, multiplicity plans, and outcome estimates matters. Without those details, readers can describe the posted comparison and its precision, but cannot fully assess all analytic choices or the secondary outcomes. The most defensible statistical reading remains bounded to the reported retention counts and their uncertain unadjusted contrast.

17. 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 trial-specific limitations follow from the registry entries available. The primary endpoint is retention, which measures completion rather than glycemic response or remission. Although HbA1c and postprandial glucose are listed as secondary outcomes, their numerical results are not reported in the registry record. The stated broader aims therefore cannot be assessed from the posted outcome information.

The comparison is between IER and TRE, not between an intermittent-fasting program and a non-fasting or usual-care group. The result does not isolate a general effect of intermittent fasting. The posted risk-difference interval is broad and crosses zero, leaving uncertainty about the size and direction of the retention difference.

The record does not report eligibility criteria beyond the condition, baseline characteristics, adherence measures, reasons for non-completion, or the timing of withdrawals. It also does not explain who was masked, how masking was implemented, or how retention was defined beyond the completion description. Details of random sequence generation and allocation concealment are not reported in the registry record.

Analysis populations, missing-data methods, multiplicity procedures, covariate adjustment, and the original sample-size justification are also not reported. These omissions constrain the ability to assess the robustness of the statistical interpretation. The trial is marked completed, but its posted analysis count is zero; the record therefore provides limited analytic detail beyond the reported arm counts and comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Intermittent Fasting for the Treatment of Type 2 Diabetes Mellitus — NCT05860413.
• Registry record last updated 2026-09-29; status last verified 2026-05.
• Results first posted 2026-09-29.
• 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.

21. Record Summary

The registry record describes a completed randomized, double-masked, parallel behavioral trial sponsored by the University of Kansas Medical Center. Enrollment is 57. The trial began on 2023-01-24, and primary completion was recorded as 2025-05-20. The condition is type 2 diabetes.

The arms are intermittent energy restriction (IER), using a very-low energy diet of 550-800 kcal/d on 2-3 days per week, and time-restricted eating (TRE), using an 8-hour eating period. The primary outcome is retention at 52 weeks. The posted counts are 21 for IER and 24 for TRE, with denominators of 29 and 28.

The posted risk difference for TRE relative to IER is 0.133, with a confidence interval from -0.075 to 0.341 and an unadjusted p-value of 0.218. HbA1c and postprandial glucose are listed as secondary outcomes, but their numerical results are not reported in the registry record. The available primary result concerns retention and does not establish glycemic effects.