Sitagliptin Therapy to Improve Outcomes After Islet Autotransplant: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Sitagliptin Therapy to Improve Outcomes After Islet Autotransplant (NCT01186562), a randomized phase 4 study. The primary outcome is Insulin Independence.

2. Clinical Question

The practical statistical question is whether the posted comparison estimates a clear difference between the groups, and how much uncertainty remains around that estimate. The trial enrolled 83 participants, while the primary outcome is reported for 50 in the sitagliptin arm and 29 in the placebo arm. Because the outcome population is explicitly tied to return for follow-up, those arm counts should not be treated as the enrollment totals. The registry does not report why some enrolled participants are absent from the primary outcome counts or how missing outcomes were handled.

The primary endpoint addresses insulin independence rather than a laboratory measure alone. It therefore summarizes a clinically relevant status at the stated follow-up time. The posted result is a comparison between randomized groups, but interpretation still depends on the outcome definition, the participants contributing data, and the uncertainty shown in the comparison interval. The registry record does not report a more detailed definition of insulin independence or the original analysis plan.

3. Trial Design

This was a phase 4, randomized, parallel-group, placebo-controlled intervention study sponsored by the University of Minnesota. The official title describes a double-blind study of sitagliptin 100 mg/day for 1 year, while the registry’s masking field specifies triple masking. These descriptions are both part of the record; it does not explain which roles were masked or how masking was maintained.

The study tested sitagliptin after pancreatectomy and autologous islet transplantation in people with chronic pancreatitis. Its stated purpose was to assess the effect of sitagliptin on the need for insulin following those procedures. The comparator was placebo. The arm descriptions contain no further details about treatment administration, adherence, co-interventions, or procedures for managing treatment discontinuation, so those aspects are not reported in the registry record.

Enrollment was 83, and the study status is completed. The record lists a start of 2010-08 and primary completion of 2015-07. The primary endpoint is insulin independence at 12 months. The registry also posts follow-up measures at 18 months and C-peptide outcomes at 12 and 18 months. These additional outcomes broaden the description of insulin-related status and pancreatic endocrine function, but they do not change which outcome the record identifies as primary.

The primary outcome population is described as patients who returned for study follow-up. Its arm counts are 50 for sitagliptin and 29 for placebo. Those counts differ from the total enrollment and should be read as the numbers contributing to this posted endpoint, not as a complete account of participant flow. The record does not provide a participant-flow diagram, reasons for nonattendance, or the original sample-size justification. It also does not report the trial’s prespecified statistical model, analysis population, or handling of missing outcomes. The trial’s design labels establish randomization, masking, and a parallel comparison, but the registry record does not provide enough detail to reconstruct all operational or analytical decisions.

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: N's reflect patients that returned for study follow up.

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 Insulin Independence, measured over 12 months.

The primary endpoint is insulin independence, expressed as the percentage of participants who were insulin independent at 12 months. The registry describes it as the percentage of patients insulin independent and states that the reported counts reflect patients who returned for study follow-up. The endpoint is binary at the participant level: each person contributes to the status of being insulin independent or not, and the arm-level percentage summarizes those statuses.

This measure is relevant to the trial’s stated question because the study was designed to assess sitagliptin in relation to the need for insulin after pancreatectomy and islet autotransplantation. Reporting a percentage allows the two randomized groups to be compared on the proportion reaching the defined status at the stated time. It is different from a continuous laboratory measure, such as C-peptide, which captures a measured quantity rather than whether a participant meets a status definition.

The registry does not give the operational criteria used to classify insulin independence, such as how insulin use was assessed or whether the status had to be sustained. That definition is important when interpreting an endpoint because different assessment rules can classify participants differently. The record also does not explain whether the 12-month assessment had a visit window or how an unobserved status was handled. The reported percentages therefore describe the posted follow-up data, while the exact endpoint rules and missing-data procedures are not reported in the registry record.

7. Results Posted in the Registry

• Sitagliptin: 42.0% (21/50) versus 44.8% (13/29) on control; risk difference -2.8 percentage points (95% CI -25.5 to 19.9), risk ratio 0.94 (0.56–1.57); unadjusted two-proportion z-test p = 0.807.

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.

Insulin Independence

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Sitagliptin: 36.0% (18/50) versus 44.4% (12/27) on control; risk difference -8.4 percentage points (95% CI -31.4 to 14.5), risk ratio 0.81 (0.46–1.42); unadjusted two-proportion z-test p = 0.468.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

Area Under the Curve (AUC) C-peptide (ng/dL*Min)

• 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 errors.
• Result:
  • Sitagliptin: mean 273.00 versus 273.00 on control; difference 0.00 (95% CI -65.86 to 65.86), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

AUC C-peptide

• 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:
  • Sitagliptin: mean 274.00 versus 235.00 on control; difference 39.00 (95% CI 26.69 to 51.31), standardized effect d = 1.72; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Sitagliptin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes extend the picture beyond insulin independence at 12 months, with a later insulin-independence assessment and C-peptide measures at 12 and 18 months. Across these outcomes, the pattern is not uniformly aligned in direction or timing: the later insulin-independence comparison points in the same general direction as the primary estimate, the 12-month AUC C-peptide means are equal as posted, and the 18-month AUC C-peptide comparison favors a higher mean in the sitagliptin arm. These differences in pattern underline that distinct outcomes and follow-up times do not necessarily tell an identical story.

These results can provide context for the primary endpoint but should not be combined informally into a single conclusion. Insulin independence is a participant status, whereas C-peptide is a continuous laboratory measure. They are related to the broader question of insulin-related function, but they are not interchangeable outcomes. A difference in a laboratory measure does not automatically imply a difference in the primary clinical status, and the registry does not report an analysis establishing a relationship between these outcomes.

The posted secondary comparisons are unadjusted, and the record lists no reported analyses for them. When many outcomes and time points are considered, selective emphasis on an isolated result can overstate how conclusive it is. Multiplicity procedures can control the interpretation of a family of tests, but no such procedure is reported. In addition, the secondary outcomes have their own follow-up counts, which vary across measures. The record does not explain these differences or give a complete account of missing observations.

Accordingly, the secondary results are most useful as descriptive context and as a reason to examine the outcome-specific tables and intervals. They do not overturn the primary result, and they do not by themselves establish a coherent treatment effect across all measures. The registry’s limited analysis details and lack of a reported multiplicity plan further support cautious interpretation. The full pattern is informative, but its evidential weight is lower than a prespecified, fully described confirmatory analysis would carry.

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

• Insulin Independence
• Area Under the Curve (AUC) C-peptide (ng/dL*Min)
• AUC C-peptide
• Acute C-peptide Response (ACR) to Glucose
• Acute C-peptide Response (ACR) to Glucose

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary percentage: each participant is classified according to insulin-independence status, and the result is summarized within each randomized arm. For a binary outcome, an arm percentage describes the proportion of participants with the event of interest. A between-arm risk difference expresses the absolute difference between those proportions, with the comparison defined as sitagliptin relative to placebo. A negative estimate means the posted proportion is lower in the sitagliptin arm; it does not, by itself, establish that the true difference is negative.

What does the interval communicate?

A confidence interval presents a range of values that are compatible with the observed data under the assumptions of the interval procedure. It communicates uncertainty around an estimate rather than giving a second estimate or a guarantee about the true value. If an interval for a difference includes zero, the data do not rule out no group difference at the interval’s stated confidence level. The registry does not state the confidence level or method used for the posted primary interval, so the interval can be described by its reported limits without assigning a level that the record does not give.

The primary interval extends from -0.255 to 0.199 around a risk-difference estimate of -0.028. This spread indicates that the estimate is imprecise: the observed data do not narrow the possible group difference to a small range around the point estimate. Interval width is affected by the amount of information available, including outcome frequencies and the number of participants contributing data. Here, the posted primary outcome includes 50 sitagliptin participants and 29 placebo participants. The unequal endpoint counts are visible in the record, but the record does not state why they differ or describe any adjustment for the imbalance.

How should the p-value be read?

The unadjusted p-value is 0.807. In general, a p-value summarizes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the test assumptions held. A larger p-value is not proof that the groups are identical, and a smaller p-value would not establish clinical importance. The primary p-value is labeled unadjusted. The registry does not report the precise test, any covariate adjustment, or a multiplicity strategy for the primary and secondary outcomes. It is therefore appropriate to report the value as posted and avoid attributing it to an unreported model.

Risk differences are useful because they show an absolute contrast in the event proportions. Other measures, such as a risk ratio or odds ratio, express a relative contrast and can answer a different descriptive question. The registry includes relative measures in the comparison data, but the primary interpretation emphasizes the risk difference because it is the posted absolute comparison. These measures can differ in appearance and scale while describing the same underlying two-arm outcome; they should not be treated as interchangeable.

Why can outcome dispersion matter?

For a binary outcome, uncertainty depends on the observed event proportions and the number of people contributing data. With continuous outcomes, the spread of measurements also affects the precision of a mean comparison. Greater variability, often described as over-dispersion when it exceeds what a model assumes, can make standard errors too small if the model does not account for it. This is a general statistical point. The registry does not report an over-dispersion assessment or a model for the primary binary outcome, so it is not possible to say whether that issue arose in this trial.

The secondary C-peptide measures are continuous outcomes, and their summary statistics use different dispersion labels: the 12-month AUC C-peptide result reports standard errors, while the 18-month AUC C-peptide result reports standard deviations. A standard deviation describes spread among individual measurements; a standard error describes uncertainty in an estimated mean. They answer different questions and should not be read as if they were the same quantity. The registry does not report the model or procedure underlying the posted secondary comparisons. The displayed estimates and p-values therefore provide descriptive and unadjusted comparison information, not a full account of the trial’s analysis.

What information is missing about the analysis?

The registry lists zero reported analyses for the primary outcome and no reported analyses for the posted secondary outcomes. This does not mean that no analysis was conducted; it means that an analysis description is not reported in the registry record. Details such as the prespecified analysis population, the treatment of missing outcomes, adjustment for baseline variables, and the statistical test or model are not reported. The trial’s original sample-size assumptions and justification are also not reported in the registry record. Those gaps limit the ability to assess whether the posted summaries match a prespecified analysis plan.

Randomization is intended, in general, to make the treatment groups comparable at assignment, reducing systematic confounding on average. It does not ensure that every group remains comparable among participants with observed follow-up if outcome availability is related to participant characteristics or outcomes. Because the primary outcome population is restricted in the description to people returning for follow-up and the record does not explain missingness, the randomization label alone cannot resolve concerns about the observed endpoint population.

Finally, the posted p-values for secondary outcomes are unadjusted. When multiple outcomes or time points are examined, the chance of observing a seemingly notable result somewhere among them can increase. A multiplicity strategy can address that issue, but the registry does not report one. The secondary findings should therefore be read as exploratory context rather than as a set of independent confirmatory tests.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -0.028, with reported limits of -0.255 and 0.199. The interval includes no difference and spans values in both directions. Its breadth means the point estimate alone gives an incomplete picture: the posted data are compatible with a range of possible differences, and the result does not pin down the size or direction with precision.

Precision is influenced by how many participants contribute outcomes and by the frequency of the event. The primary endpoint counts are 50 for sitagliptin and 29 for placebo. The registry notes that the counts reflect patients returning for follow-up, but does not provide reasons for unavailable outcomes or describe how they were handled. The enrollment of 83 should therefore not be mistaken for the number contributing to this endpoint. The record also does not identify the confidence level or construction method for the reported interval.

The unadjusted p-value of 0.807 is consistent with substantial uncertainty in the primary comparison, but it does not replace the interval or demonstrate equivalence. An absence of a small p-value is not evidence that all clinically relevant differences have been excluded. Conversely, the range of the interval should not be interpreted as a set of equally likely effects. It is an uncertainty summary conditioned on the method and assumptions used.

The secondary comparisons have their own intervals and differing follow-up counts, so their precision cannot be assumed to match that of the primary endpoint. In particular, different outcome types and dispersion summaries affect how uncertainty is expressed. The registry record does not report the methods needed to evaluate whether the intervals account for all design features. The tables and plots should be read as summaries of the posted data, with the primary interval providing the most direct view of uncertainty for the main question.

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 sample-size table is a planning illustration based on the observed effect, not a reconstruction of the trial’s original design. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect. For this binary outcome, the table reports participants per arm, not total events. The note that time-to-event tables give total events does not apply to this endpoint.

The columns for 80% power and 90% power show the planned number of participants per arm that would be required, under those assumptions, to have the stated probability of detecting the effect used for that row when the specified statistical model and assumptions hold. They are not counts observed in this trial. The trial’s own original sample-size justification and design assumptions are not reported in the registry record. These figures are planning illustrations, not observed power.

Read down the rows as increasingly conservative planning scenarios: detecting a smaller fraction of the observed effect requires more participants per arm. The same general relationship applies when comparing the 80% and 90% power columns: seeking a higher chance of detecting the stated effect calls for a larger planned sample under the same assumptions. Because the illustration uses the observed effect as its starting point, it is sensitive to the uncertainty in that estimate. The primary comparison’s interval is broad, so the observed effect should not be treated as a known underlying effect for future planning.

The table and any accompanying curve are best used to understand how planning requirements change with the effect size and power target, rather than as a recommendation for a future study. They do not establish that the completed trial had adequate or inadequate power according to its original plan. The record does not report that original plan, and the displayed illustration cannot fill that gap.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.448; treatment proportion p₁ = 0.420; average p̄ = 0.434.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7009 = 1.3738.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7007 = 0.5897.
4. n = (1.3738 + 0.5897)² / (-0.0283)² = 4,822.1, rounded up to 4,823 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 <- 0.448275862068966                          # control proportion
p1 <- 0.42                          # 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(1186562)
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 = 4,823 (80% power), 6,455 (90% power)
 75% of observed effect: n per arm = 8,590 (80% power), 11,499 (90% power)
 50% of observed effect: n per arm = 19,362 (80% power), 25,919 (90% power)
power.prop.test: 4822.1 
Simulated power at n = 4,823 per arm: 0.796 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry posts one primary endpoint and several secondary outcomes, including measurements at different follow-up times. It does not report a multiplicity adjustment or explain how the primary and secondary comparisons were prioritized analytically beyond identifying the primary endpoint. Without a reported strategy, the unadjusted secondary p-values should not be treated as if they were protected against the increased chance of notable findings when many comparisons are examined. The record lists no reported analyses for the secondary outcomes.

Missing data are also important to interpretation. The primary outcome description says that the reported numbers reflect patients who returned for study follow-up. The arm counts for the primary endpoint are 50 and 29, while total enrollment is 83. The registry record does not give reasons why outcome data are unavailable for other enrolled participants, state whether missingness differed by treatment arm, or describe any method for handling missing outcomes. It does not report whether the analysis used complete cases, imputation, a sensitivity analysis, or another approach. Those methods should not be inferred from the posted percentages.

The other outcome counts vary by measure and follow-up time. The registry does not provide a participant-flow account that links enrollment, treatment, follow-up attendance, and each endpoint’s analysis population. This makes it difficult to determine whether the posted secondary estimates represent the same participants or whether changes in the observed groups could affect comparisons over time.

The analysis population is not described beyond the primary outcome’s follow-up note. The record does not state whether participants were analyzed according to randomized assignment, whether there was a per-protocol analysis, or whether any participants were excluded after randomization. It also does not report the prespecified statistical model, covariate adjustments, or handling of treatment discontinuation. These omissions do not invalidate the posted results, but they limit assessment of how closely the registry summaries reflect the intended trial analysis and how robust the comparisons are to missing-data assumptions.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdomen pain (20.7%), obstruction bowel gastrointestinal (17.2%), fever constitutional symptoms (13.0%), constipation gastrointestinal (10.3%), hypoglycemia metabolic/laboratory (10.3%).

The adverse-event summary reports serious adverse events affecting 31 of 54 at-risk participants in the sitagliptin group and 26 of 29 in the placebo group. For other adverse events, it reports 54 of 54 and 29 of 29 affected, respectively. These counts describe the registry’s posted safety groups; they are not the same denominators as the primary outcome follow-up counts. The record does not explain the difference between the safety and efficacy populations.

The most frequently listed serious-event terms include Abdomen Pain (20.7%), Obstruction Bowel Gastrointestinal (17.2%), Fever Constitutional Symptoms (13.0%), Constipation Gastrointestinal (10.3%), Hypoglycemia Metabolic/Laboratory (10.3%), and Dehydration Gastrointestinal (9.3%). The record does not clearly attribute these term percentages to a particular treatment arm in the posted summary, so they should not be assigned to one arm. Death counts are not reported in the registry record.

These summaries do not provide enough detail to assess event timing, duration, severity grading beyond the serious-event category, or causal attribution. The counts should be read as descriptive safety reporting, not as a comparison adjusted for follow-up or other factors. The registry record does not report a detailed safety-analysis method or definitions beyond the posted categories.

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

The primary finding is a comparison of observed insulin-independence percentages at 12 months among participants represented in the follow-up data. The reported percentages are 42.0% for sitagliptin and 45.0% for placebo. The risk-difference estimate is -0.028, its interval includes differences in either direction, and the unadjusted p-value is 0.807. The appropriate statistical reading is that the estimate is uncertain and does not precisely establish the size or direction of a difference in this outcome.

This result does not prove that the groups are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty falls within that margin; neither is reported in the registry record. Nor does the result establish that sitagliptin has no effect. The interval remains compatible with a range of values, and missing outcome handling is not described. A non-significant p-value is not evidence that every meaningful difference has been excluded.

The secondary results offer additional but not definitive context. They cover different outcomes and follow-up times, and their pattern is not uniform. The registry does not report an adjustment for multiple comparisons, so individual unadjusted secondary results carry less weight as confirmatory evidence. They should be considered alongside the primary endpoint, not used selectively to replace it.

The trial’s design features—randomization, placebo control, masking, and a parallel-group structure—support a comparative framework. However, the registry record does not report the original sample-size rationale, full analysis plan, outcome definition details, participant flow, or missing-data methods. Those absences restrict what can be concluded from the posted summaries. This page describes the data and their statistical precision; it does not provide medical advice or determine what treatment is appropriate for any person.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it separates a point estimate from the uncertainty surrounding it. The primary comparison’s estimated risk difference is close to zero, but the interval is wide enough to include values on both sides of no difference. Looking only at the observed percentages or the p-value would miss the central issue: the data do not precisely estimate the size or direction of the group contrast.

It also illustrates why endpoint denominators matter. The record reports total enrollment of 83, but the primary result is based on participants who returned for follow-up, with different counts in the two arms. Randomization supports comparison at assignment, yet incomplete outcome information can complicate interpretation of the participants who contribute observed data. A clear account of participant flow and missing-data handling is therefore important when reading a posted result.

The secondary outcomes demonstrate another common challenge: different measures and time points can show different patterns. Insulin independence is a binary status, while C-peptide is continuous. These outcomes may be related conceptually, but each measures something distinct, and the registry does not report an analysis linking them. Unadjusted results across several outcomes also raise a multiplicity concern, making a prespecified analysis plan valuable for separating confirmatory from exploratory evidence.

Finally, the planning illustration is not the same as the trial’s original design calculation. It uses the observed effect and stated assumptions to show how sample-size needs change with the target effect and power. Keeping that distinction clear prevents a planning exercise from being mistaken for evidence about the trial’s achieved power or the adequacy of its original design.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations are visible in the registry record. The primary outcome population is described as participants who returned for follow-up, but no participant-flow details or reasons for missing outcomes are reported. The outcome counts differ by arm, and the registry does not describe whether missingness was related to treatment assignment, participant characteristics, or insulin-independence status. Consequently, the effect of unavailable outcome data cannot be assessed from the posted summaries alone.

The registry does not provide the operational definition of insulin independence, the assessment procedures, or the rules for classifying participants at 12 months. It also does not report the original analysis plan, the statistical test or model for the primary comparison, the analysis population, or sensitivity analyses. No multiplicity strategy is reported for the multiple secondary outcomes and follow-up times.

There is no posted detail about treatment adherence, discontinuation, or other post-randomization events that could affect interpretation. The record does not describe the roles covered by triple masking or how masking was implemented. These details cannot be inferred from the design labels or blank arm descriptions.

The secondary measures have varying sample sizes and different dispersion labels, and the record does not explain the reasons for those differences. The safety summary also uses denominators that differ from the primary endpoint counts, without a participant-flow explanation. Serious-event term percentages are not clearly assigned by arm in the summary, and deaths are not reported in the registry record. These omissions limit a detailed assessment of safety patterns and of how well the observed groups were followed across outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Sitagliptin Therapy to Improve Outcomes After Islet Autotransplant — NCT01186562.
• Registry record last updated 2017-05-31; status last verified 2017-05.
• Results first posted 2016-12-28.
• 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

The registry record describes a completed phase 4, randomized, triple-masked, parallel-group, placebo-controlled study of sitagliptin after pancreatectomy and islet autotransplantation. The official title specifies sitagliptin 100 mg/day for 1 year. Enrollment was 83, and the primary endpoint was insulin independence at 12 months.

The posted primary comparison reports 42.0% insulin independence with sitagliptin and 45.0% with placebo among participants represented in follow-up. The estimated risk difference is -0.028, with an interval from -0.255 to 0.199 and an unadjusted p-value of 0.807. The interval is broad, and the posted data do not precisely establish the direction or size of a difference.

Secondary outcomes cover insulin independence at 18 months and C-peptide measures at 12 and 18 months. Their pattern varies by measure and time point, and the registry does not report multiplicity adjustment or detailed analysis methods. The record also does not describe missing-data handling, the original sample-size justification, or a complete participant flow. Safety summaries are posted, but deaths are not reported in the registry record.