Effect of a Fixed Pramlintide: Insulin Dose Ratio on Postprandial Glucose in Type 1 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of a Fixed Pramlintide: Insulin Dose Ratio on Postprandial Glucose in Type 1 Diabetes Mellitus (NCT02500979), a randomized phase 1 study. The primary outcome is Efficacy of Pramlintide by Measurement of 24-hour Tissue Mean Weighted Glucose (MWG) Obtained With Continuous Glucose Monitoring (CGM).

2. Clinical Question

3. Trial Design

This was a randomized, single-blind, placebo-controlled, two-way crossover Phase I study. The title identifies the comparison as pramlintide and insulin co-administered in a fixed-dose ratio versus placebo and insulin in people with type 1 diabetes and inadequate glycemic control. A crossover design compares study conditions within participants across periods, rather than assigning each participant to only one condition. This can make within-participant comparisons informative, although the registry record does not report the period sequence details, washout arrangements, or which people were masked.

The interventions listed were pramlintide acetate, placebo, lispro insulin U-100, and regular insulin U-100. The described primary arms were pramlintide with regular insulin and placebo with regular insulin. The study summary describes basal-bolus subcutaneous insulin and simultaneous delivery by two separate pumps. The numerical fixed-dose ratio, treatment duration within each period, and detailed administration schedule are not reported in the registry record.

The registry record lists enrollment of 34, gives the study status as completed, and records a start date of 2015-08-17 and primary completion date of 2016-08-05. It says that 33 subjects were correctly randomized and that 26 met the stated Full Analysis Set criterion of having at least one efficacy assessment in each crossover period. The arm-level efficacy summaries also give 26.0 for each condition; these are crossover-period summaries, not a statement that each condition had a separate parallel group.

The registry record identifies a linear mixed-effects model for the sponsor-reported primary comparison. Further details of that model, including its covariance structure and any adjustment terms, 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: Eligible study subjects were males and females, aged ≥18 years and ≤70 years at the time of screening with a prior diagnosis of type 1 diabetes mellitus (T1DM) and an HbA1c value of ≥7.2% and ≤9.0% at screening.

Period 1

Reasons for not completing this period:

Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: Of the 33 correctly randomized subjects, 26 (76.5%) had at least 1 efficacy assessment available from each of the 2 crossover periods and were included in the Full Analysis Set.

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: Safety Analysis Set: All randomized subjects receiving any infused study treatment. Subjects were analyzed according to the treatment sequence they received.

6. Primary Endpoint

The registry lists the primary outcome as Efficacy of Pramlintide by Measurement of 24-hour Tissue Mean Weighted Glucose (MWG) Obtained With Continuous Glucose Monitoring (CGM), measured over 24 h.

The primary endpoint was 24-hour tissue mean weighted glucose, measured using continuous glucose monitoring and reported in mg/dL. The registry definition describes it as the total area under the 24-hour tissue-glucose curve divided by the actual time span in that period. In practical terms, this creates a time-averaged summary of the glucose readings collected across the monitoring interval, rather than relying on a single measurement or one meal-time value.

As a continuous outcome, the measure can express differences in average glucose on its measurement scale. Continuous glucose monitoring is relevant to the stated question because the study aimed to compare the glucose profile over a full day, including variation across time, rather than only a laboratory value at one moment. As a general statistical point, an average over time can be useful when the research question concerns an overall profile; it can also conceal the timing or pattern of changes that may be important to other questions. The registry lists several such additional measures as secondary outcomes.

The reported arm summaries are least-squares means, with standard errors as their dispersion measure. The Full Analysis Set definition requires an efficacy assessment in both crossover periods. The registry record does not report the planned handling of missing monitor readings, the detailed analysis formula, or whether the endpoint was transformed before analysis.

7. Results Posted in the Registry

• Pramlintide & Regular Insulin: mean 152.20 versus 173.80 on control; difference -21.60 (95% CI -44.25 to 1.05), standardized effect d = -0.52; z-test p = 0.062.

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.

Efficacy of Pramlintide by Measurement of Incremental 24-hour Tissue Glucose Area Under the Plasma Concentration-time Curve (AUC) Obtained With Continuous Glucose Monitoring (CGM)

• 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:
  • Pramlintide & Regular Insulin: mean -2,489 versus 26,243 on control; difference -28,732 (95% CI -38,100 to -19,364), standardized effect d = -1.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Pramlintide & Regular Insulin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Efficacy of Pramlintide by Measurement of Incremental 24-hour Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC)

• 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:
  • Pramlintide & Regular Insulin: mean -12.75 versus 11.18 on control; difference -23.93 (95% CI -61.36 to 13.49), standardized effect d = -0.35; z-test p = 0.210.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pramlintide & Regular Insulin and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy of Pramlintide by Measurement of Incremental 24-hour Plasma Glucagon Area Under the Plasma Concentration-time Curve (AUC)

• 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:
  • Pramlintide & Regular Insulin: mean -16.05 versus -14.95 on control; difference -1.10 (95% CI -36.05 to 33.85), standardized effect d = -0.02; z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pramlintide & Regular Insulin and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists 14 secondary outcomes spanning post-meal plasma glucose, 24-hour glucose measures, continuous glucose monitoring, time in a tissue-glucose range, and glucagon. The posted numerical comparisons cover a narrower set of those outcomes. Across the detailed secondary comparisons, the results are not uniformly aligned: some reported glucose measures show contrasts in the same general direction as the primary estimate, while others are imprecise and do not show a clear separation. The secondary endpoints use different scales and definitions, so their estimates should not be treated as interchangeable measures of one effect.

These secondary findings add context rather than replacing the primary result. An endpoint that averages glucose across a full day may differ from one focused on an incremental area under a curve, a meal period, or glucagon. Differences in measurement, units, variability, and analysis can all affect how precise an estimate is. The secondary outcomes may therefore help describe the breadth of measurements collected, but they do not independently resolve the discrepancy between the primary recalculation and the sponsor’s mixed-effects analysis.

General statistical explanation: testing many outcomes creates more opportunities for apparently notable results to arise by chance, particularly when each is assessed without an adjustment for multiplicity. The registry record does not report a multiplicity procedure or a prespecified hierarchy for interpreting the secondary outcomes. Accordingly, unadjusted secondary results carry less weight as confirmatory evidence than a clearly specified primary analysis. They are best read as supporting or exploratory information, with attention to their uncertainty and the fact that several different outcomes were considered.

The registry record does not report detailed numerical results for every listed secondary outcome in the material summarized by these analyses. Where detailed results are not available in the registry record, their magnitude and precision cannot be assessed. No overall conclusion about all secondary endpoints can be drawn from the limited set of detailed comparisons alone.

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

• Efficacy of Pramlintide by Measurement of Absolute Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC) Following Lunch
• Efficacy of Pramlintide by Measurement of Absolute Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC) Following Dinner
• Efficacy of Pramlintide by Measurement of Absolute Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC) Following Breakfast
• Efficacy of Pramlintide by Measurement of Incremental 24-hour Tissue Glucose Area Under the Plasma Concentration-time Curve (AUC) Obtained With Continuous Glucose Monitoring (CGM)
• Efficacy of Pramlintide by Measurement of Absolute 24-hour Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC)
• Efficacy of Pramlintide by Measurement of Incremental 24-hour Plasma Glucose Area Under the Plasma Concentration-time Curve (AUC)
• Efficacy of Pramlintide Measured by Percent Time Spent in the Range of >70 mg/dL to <180 mg/dL Tissue Glucose Obtained With Continuous Glucose Monitoring (CGM)
• Efficacy of Pramlintide by Measurement of Absolute 24-hour Plasma Glucagon Area Under the Plasma Concentration-time Curve (AUC)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference describe?

The primary outcome is continuous, so a difference in means expresses how far apart the two condition summaries are on the outcome’s original scale. The posted least-squares means are 173.8 mg/dL for placebo with regular insulin and 152.2 mg/dL for pramlintide with regular insulin. The sponsor-reported least-squares mean difference is -21.5 mg/dL, with the comparison expressed for pramlintide plus regular insulin relative to placebo plus regular insulin. A negative estimate indicates that the model’s estimated mean for the pramlintide condition was lower on this scale. It does not, by itself, establish why the values differ or what the difference means clinically.

Least-squares means are model-based estimates, rather than necessarily simple arithmetic averages of all recorded observations. A model can account for features of the design, but the registry record does not report the full specification. The reported analysis is identified as a linear mixed-effects model; the exact fixed effects, random effects, covariance structure, and handling of period or sequence are not reported in the registry record.

Why does the crossover design matter?

General statistical explanation: in a crossover study, participants receive more than one study condition in different periods. Observations from the same participant can be correlated because they share participant characteristics. A suitable analysis can use this within-participant information and account for the study structure. If that relationship is ignored, a simple comparison based only on separate arm summaries may not have the same uncertainty estimate as an analysis that uses participant-level data and the crossover structure.

The recalculated primary mean difference is -21.6 mg/dL. Its 95% confidence interval extends from -44.25 to 1.046, and its unadjusted p-value is 0.062. This recalculation uses posted summary statistics and is not the sponsor’s mixed-effects model. The sponsor-reported estimate is -21.5 mg/dL, with a 95% confidence interval from -37.8 to -5.2. The discrepancy flag indicates that these results do not match closely enough to treat the summary-based calculation as a reproduction of the sponsor’s analysis. The sponsor’s own analysis takes precedence.

What does a confidence interval convey?

General statistical explanation: a confidence interval describes the range of estimates compatible with the data and the specified statistical procedure, under its assumptions. A narrower interval indicates greater precision on the same scale; a wider interval indicates more uncertainty about the estimated difference. The interval is not a range containing every participant’s response, and it does not show the distribution of individual outcomes.

For the primary recalculation, the interval includes zero, while the sponsor-reported interval does not. That contrast is one part of the observed discrepancy. It should not be resolved by selecting whichever result is more favorable; the registry’s sponsor-reported model is the analysis to prioritize, while the recalculation is a transparent but simplified check based on the arm summaries.

What role does the p-value play?

General statistical explanation: a p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions held. 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 primary recalculation has an unadjusted p-value of 0.062. The sponsor’s reported model result is presented with its own estimate and confidence interval; its p-value is not restated because the numerical value has more than three decimal places.

The distinction between adjusted and unadjusted analysis matters in a study with repeated measurements and multiple endpoints. The posted primary result is from a linear mixed-effects model, while the simple recalculation is unadjusted. The registry record does not report a multiplicity adjustment for the primary or secondary outcomes, nor does it report an overall testing strategy. The displayed unadjusted secondary comparisons should therefore not be treated as if they were a single confirmatory family of tests.

Why can over-dispersion matter?

General statistical explanation: dispersion describes variability in measurements around a summary. If variability is greater than a model assumes, standard errors can be too small and confidence intervals too narrow; if it is lower, the reverse can occur. The primary outcome is reported with standard errors, and the recalculated pooled standard deviation is marked as approximate. These summary quantities do not provide enough information to evaluate the full distribution or diagnose model fit. Participant-level data and model diagnostics are not reported in the registry record.

The secondary outcomes include continuous area-under-the-curve measures and a percentage of time in a stated tissue-glucose range. These measures have different units and answer different questions, so their numerical estimates should not be compared directly with the primary mean difference. Some secondary analyses have sponsor-reported model results and others do not. The registry record does not report a common model specification across all secondary endpoints.

Finally, the study’s original design assumptions, including any planned sample-size justification, are not reported in the registry record. A separate planning illustration based on observed effects can show how assumed effect sizes relate to hypothetical sample sizes, but it cannot establish what the original investigators planned or whether the completed study had adequate precision for every outcome.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is a least-squares mean difference of -21.5 mg/dL, with a 95% confidence interval from -37.8 to -5.2. The interval places the model’s estimated difference on the lower side of zero across the reported bounds. Its width also shows that the data are compatible with a range of possible differences, not just the single point estimate. The interval concerns the estimated group-level contrast; it does not describe the range of individual participant measurements.

The simple recalculation gives a different 95% confidence interval, from -44.25 to 1.046, around a mean difference of -21.6 mg/dL. Because this interval includes zero while the sponsor-reported interval does not, the choice of analysis changes the inferential reading. The sponsor’s own analysis takes precedence, but the disagreement is relevant to transparency: the summary-based calculation is not an independent reconstruction of the mixed-effects result.

General statistical explanation: confidence intervals reflect both the observed data and the analysis assumptions. A crossover analysis may use within-participant relationships that are not represented in an unadjusted calculation from arm-level summaries. Without the participant-level data and full model specification, it is not possible to determine exactly which modeling features account for the different intervals. Those details are not reported in the registry record.

The standard errors for the two primary arm summaries are 8.17. Similar arm-level standard errors do not guarantee identical uncertainty for the between-condition contrast under different analysis methods. Precision of a contrast also depends on the analysis structure and, in a crossover design, the within-participant information. The confidence interval is therefore more informative than reading the arm summaries in isolation.

The registry record reports a Full Analysis Set of 26 participants with efficacy assessments in both crossover periods. This defines the analyzed population but does not by itself explain the extent or pattern of missing measurements. Missing-data handling is not reported in the registry record. The interval should consequently be understood as conditional on the stated analysis and its available data, not as a complete account of uncertainty from every possible source.

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 figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The registry record’s original sample-size justification is not reported. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers the stated fraction of the observed effect as the effect to detect.

For the primary outcome, the row for planning for 100% of the observed effect lists 59 participants per arm for 80% power and 79 participants per arm for 90% power. Planning for 75% of the observed effect lists 104 participants per arm for 80% power and 139 participants per arm for 90% power. Planning for 50% of the observed effect lists 234 participants per arm for 80% power and 313 participants per arm for 90% power.

In plain language, the 80% power column gives the number of participants per arm that the stated planning calculation associates with an 80% chance of detecting the assumed effect under its assumptions, if that effect and the model assumptions are correct. The 90% column gives the corresponding planning number for a higher target chance of detection. These are hypothetical planning quantities, not results about the chance that the completed study detected an effect. This is not observed power.

The smaller the effect chosen for planning, the more participants the illustration requires. That pattern appears across the listed rows: detecting a smaller fraction of the observed effect requires larger per-arm figures. The values are per arm, not a total for the study. They are also not a reconstruction of the original crossover design calculation; the registry record does not report the assumptions used for that design, and the illustration’s stated assumptions should be read as its own planning framework.

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 = -21.600; pooled standard deviation σ = 41.659.
2. n = 2 × (1.96 + 0.842)² × 41.659² / -21.600² = 58.4, rounded up to 59 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 <- -21.6                      # observed difference in means
sigma <- 41.658989426053                     # 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(2500979)
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 = 59 (80% power), 79 (90% power)
 75% of observed effect: n per arm = 104 (80% power), 139 (90% power)
 50% of observed effect: n per arm = 234 (80% power), 313 (90% power)
power.t.test: 59.4 
Simulated power at n = 59 per arm: 0.796 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a linear mixed-effects model and reports a least-squares mean difference of -21.5 mg/dL, with a 95% confidence interval from -37.8 to -5.2. The recalculation from the posted arm summaries is an unadjusted mean difference of -21.6 mg/dL, with a 95% confidence interval from -44.25 to 1.046 and an unadjusted p-value of 0.062. These estimates are close in point value but their reported uncertainty and inferential readings differ.

The recalculation is a simple check using summary statistics, not a replication of the sponsor’s analysis. It cannot account for participant-level pairing or other features of the mixed-effects model that are not represented in the arm summaries. The registry record does not provide the full model specification or participant-level data needed to reproduce the sponsor’s result.

Because the discrepancy is flagged, the sponsor’s own analysis takes precedence for interpretation of the primary comparison. The recalculation remains useful as a reminder that different analysis approaches can yield different intervals even when point estimates are similar. Neither result alone establishes clinical importance, and the sponsor-reported model result should be understood within the population and outcome defined in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary outcome and lists 14 secondary outcomes. It does not report whether the primary endpoint was selected through a formal hierarchy, whether any interim analyses were conducted, or whether a multiplicity adjustment was used for the collection of secondary tests. Those features are important because testing several outcomes can increase the chance of at least one apparently unusual result under a null model. The unadjusted p-values for individual secondary comparisons do not account for that broader testing context.

General statistical explanation: multiplicity procedures can control the overall error rate across a defined family of tests or organize testing through a prespecified sequence. Without a reported plan, a reader cannot know which outcomes were intended as confirmatory, how results across outcomes were meant to be interpreted, or whether any adjustment was intended. The registry record does not report a statistical analysis plan that answers these questions. The secondary outcomes should therefore be interpreted cautiously and not treated as a set of independent confirmations.

The primary analysis population is described as the Full Analysis Set: among 33 correctly randomized subjects, 26 had at least one efficacy assessment available from each of the two crossover periods and were included. This establishes the stated inclusion criterion for that analysis. It does not explain why other correctly randomized subjects were not included, the amount or timing of missing measurements, or whether readings were missing within an otherwise included period. These details are not reported in the registry record.

The registry record also does not report the method used to handle missing data, any sensitivity analyses for missingness, or how incomplete continuous glucose monitoring records were treated. General statistical explanation: missing-data methods can affect estimates if the likelihood of missingness is related to observed or unobserved outcomes. Without the analysis details, the robustness of the primary and secondary results to missing data cannot be evaluated from the recorded information alone.

Likewise, the original sample-size justification and interim-analysis plans are not reported in the registry record. The planning illustration based on observed effects is separate from those missing design details and cannot be used to infer them.

16. 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 1% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list zero affected participants in each condition: 0 of 28 at risk for placebo with regular insulin and 0 of 32 at risk for pramlintide with regular insulin. No serious adverse event terms are listed. The registry record does not report death counts, so deaths should be described as not reported in the registry record rather than interpreted as zero.

For other adverse events, the record lists 9 affected among 28 at risk for placebo with regular insulin and 22 affected among 32 at risk for pramlintide with regular insulin. These are counts of participants affected, not counts of every event episode. The adverse-event risk groups do not match the primary Full Analysis Set definition, and the registry record does not explain the difference in denominators.

These figures are descriptive. They do not establish that a condition caused an event, and they do not provide event severity, duration, relatedness, or a detailed breakdown of non-serious event types. General statistical explanation: safety counts are most informative when read with clear definitions of the event, the population at risk, the observation period, and how relatedness was assessed. Several of those details are not reported in the registry record, so the numbers alone provide a limited safety summary.

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

The posted primary result describes a model-based difference in 24-hour tissue mean weighted glucose between pramlintide plus regular insulin and placebo plus regular insulin in the recorded study population. The sponsor-reported estimate is -21.5 mg/dL, with a 95% confidence interval from -37.8 to -5.2. The direction of the estimate is toward a lower mean weighted glucose in the pramlintide condition. The registry record’s analysis and population definition are essential context for that statement.

This result does not, on its own, establish that the regimen works, that it is preferable for an individual, or that it has a favorable overall benefit-harm balance. It does not provide a treatment recommendation. A continuous glucose summary is one outcome among the broader set of efficacy and safety measures. It cannot answer every question about glucose patterns, clinical outcomes, safety, or longer-term experience.

The result also does not show how much individual participants changed, whether all participants had changes in the same direction, or how the difference varied across meals and time of day. The 24-hour mean compresses repeated monitor readings into one summary. The registry record does not report participant-level distributions or enough detailed analysis information to address those questions.

The contrast between the sponsor’s model-based result and the simple recalculation is another limit on interpretation. The recalculated interval includes zero, while the sponsor-reported interval does not. Since the analyses differ, the sponsor’s own analysis takes precedence, but a reader cannot independently reconstruct it from the registry record’s summary statistics alone. Full model details and participant-level data are not reported.

Finally, the study is a Phase I crossover study with a Full Analysis Set of 26 participants meeting the stated requirement for assessments in both periods. The registry record does not establish how broadly these findings apply beyond that analysis population, and it does not report the original sample-size assumptions. The result should be read as evidence about the specified endpoint in this study, not as a complete assessment of efficacy, safety, or generalizability.

18. Why This Trial Matters Statistically

This study illustrates why analysis details matter when reading a clinical trial result. The same primary outcome and similar point estimates are associated with different confidence intervals under the sponsor-reported mixed-effects analysis and the simple recalculation from summary statistics. In a crossover design, measurements within a participant can be related, so the analysis structure can affect uncertainty. The registry record identifies the sponsor’s model but does not report enough detail to reproduce it fully.

It also demonstrates the distinction between a primary outcome and a large collection of secondary questions. The primary endpoint summarizes the 24-hour tissue-glucose profile, while secondary measures consider post-meal glucose, other glucose summaries, time in a range, and glucagon. These outcomes provide different perspectives, but numerous unadjusted comparisons do not automatically amount to multiple independent confirmations. Without a reported multiplicity strategy, the secondary results require cautious interpretation.

Precision is another key issue. The primary estimate is not the whole result: the confidence interval communicates uncertainty around it, and the disagreement between the two analysis approaches changes the interval’s relationship to zero. Reporting the estimate, interval, analysis method, and analysis population together supports a more disciplined interpretation than relying on a single point value.

Finally, the registry record distinguishes the efficacy analysis population from the adverse-event risk groups and gives a specific definition for the Full Analysis Set. Keeping these populations and denominators separate avoids treating unlike counts as though they describe the same participants or analysis. The record also makes clear that observed-effect planning illustrations are not the original design justification. These distinctions are central to transparent statistical reading.

19. 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.

The primary analysis is based on a Full Analysis Set of 26 participants who had at least one efficacy assessment in each crossover period. The registry record states that 33 subjects were correctly randomized but does not explain the exclusions from the Full Analysis Set or report a sensitivity analysis for those not included. The effect of missing efficacy data on the result therefore cannot be assessed from the registry record.

The sponsor’s primary model is identified as a linear mixed-effects model, but the model specification is not reported. Details such as covariance structure, period and sequence terms, and any additional adjustments are not reported in the registry record. The summary-based recalculation differs in its confidence interval and unadjusted inference; without participant-level data, the source of that difference cannot be isolated.

The study is a Phase I crossover study, and the record does not report the numerical fixed-dose ratio, detailed period schedule, washout details, or which parties were masked. These omissions limit evaluation of the treatment sequence and operational features from the registry record. No assumptions about those design details should be inferred from the title alone.

The registry record lists 14 secondary outcomes but does not report a multiplicity adjustment or hierarchy for their interpretation. That makes secondary findings less suitable as stand-alone confirmatory evidence. The record also does not report the original sample-size justification, interim analyses, or a statistical analysis plan that would clarify the intended testing strategy.

Safety reporting is limited to affected-participant counts and the serious-event summary. Death counts are not reported in the registry record, and details such as event relatedness and the observation window are not stated. These limits constrain conclusions about safety and the reach of the efficacy findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of a Fixed Pramlintide: Insulin Dose Ratio on Postprandial Glucose in Type 1 Diabetes Mellitus — NCT02500979.
• Registry record last updated 2018-11-02; status last verified 2018-03.
• Results first posted 2018-11-02.
• 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.

23. Record Summary

The registry record describes a completed, randomized, single-blind, placebo-controlled, two-way crossover Phase I study of pramlintide with regular insulin versus placebo with regular insulin in type 1 diabetes. Enrollment is listed as 34, and the primary endpoint was 24-hour tissue mean weighted glucose measured by continuous glucose monitoring.

The sponsor-reported primary analysis is a linear mixed-effects model with a least-squares mean difference of -21.5 mg/dL and a 95% confidence interval from -37.8 to -5.2. The unadjusted recalculation differs, so the sponsor’s own analysis takes precedence. The Full Analysis Set included 26 participants with at least one efficacy assessment in each crossover period.

The registry record lists multiple secondary outcomes and adverse-event counts, but does not report multiplicity procedures, the original sample-size justification, detailed missing-data methods, or full model specifications. These omissions limit independent reconstruction and broader interpretation.