A Study to Investigate the Efficacy and Safety of Canagliflozin in Children and Adolescents (>=10 to <18 Years) With Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Investigate the Efficacy and Safety of Canagliflozin in Children and Adolescents (>=10 to <18 Years) With Type 2 Diabetes Mellitus (NCT03170518), a randomized phase 3 study. The primary outcome is Change From Baseline in Glycated Hemoglobin (HbA1c) at Week 26.

2. Clinical Question

The registry identifies this as a Phase 3 study with randomized allocation, double masking, and a parallel-group design. Its stated purpose was to assess the effect of canagliflozin relative to placebo on HbA1c after 26 weeks of treatment and to assess overall safety and tolerability. The key estimate is a between-group difference in change, not a direct description of every participant’s experience or a comparison of each canagliflozin dose separately.

3. Trial Design

This Phase 3 trial was randomized, multicenter, double-blind, parallel-group, and placebo-controlled. The registry reports 171 participants enrolled. The study record lists a start date of 2017-07-21, a primary completion date of 2023-09-20, and a status of completed. These dates describe the registry record and do not, by themselves, explain why the study took that length of time.

Before the double-blind phase, participants received matching placebo once daily during a 2-week single-blind run-in. During the first 12 weeks of the double-blind treatment phase, the description specifies canagliflozin 100 mg or matching placebo once daily. It also indicates that treatment assignment at Week 13 depended on HbA1c and estimated glomerular filtration rate criteria, but the posted arm description is incomplete. The full later-dose procedure is not reported in the registry record, so no further detail about that step can be inferred from the available description.

The primary endpoint was change in HbA1c at Week 26, with baseline identified as Day 1. The primary analysis combined the canagliflozin 100 mg and 300 mg groups and compared that combined group with placebo. The reported analysis population was the full analysis set, defined by random assignment, receipt of at least one dose, and a baseline HbA1c measurement. In the posted primary outcome results, the placebo group had 87 participants and the combined canagliflozin group had 84.

The registry also lists secondary outcomes assessed at Week 26 and Week 52, including fasting plasma glucose, HbA1c thresholds, rescue therapy, body weight, body mass index, and lipid measures. Not every endpoint has numerical results posted in the information analyzed. The original protocol’s detailed sample-size rationale, original design assumptions, interim-analysis plan, and full statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all participants who were randomly assigned to a treatment group, received at least one dose of study agent and had a baseline HbA1c measurement.

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 Change From Baseline in Glycated Hemoglobin (HbA1c) at Week 26, measured over Baseline (Day 1) and Week 26.

The primary endpoint was change from baseline in glycated hemoglobin, or HbA1c, at Week 26. The measurement is expressed as percent HbA1c, and baseline was Day 1. A change score describes how the measure moved during follow-up relative to each participant’s starting measurement. The treatment comparison then estimates the difference between the groups’ average changes.

HbA1c is used in diabetes research as an indicator of blood glucose exposure over a longer period than a single glucose measurement. This makes it a relevant continuous outcome for assessing a treatment’s effect on glycemic control over the trial’s primary follow-up interval. A continuous measure also retains information about the amount of change, rather than reducing the outcome to whether each participant crossed one chosen threshold.

The registry reports least-squares means for the groups and a least-squares mean difference from an ANCOVA analysis. The analysis description for the endpoint specifies a pattern mixture model with multiple imputation and says that the combined canagliflozin 100 mg and 300 mg population was planned for analysis. Thus, the primary estimate is about that combined group versus placebo; it does not establish separate estimates for the two doses. The full analysis set required random assignment, at least one dose, and a baseline HbA1c measurement.

The endpoint is a laboratory measure and does not, by itself, describe symptoms, quality of life, complications, or other clinical outcomes. Those questions require their own outcomes and evidence. The registry lists several secondary measures, but the primary statistical result addresses only the Week 26 HbA1c change.

7. Results Posted in the Registry

• Canagliflozin 100/300 mg: mean -0.37 versus 0.39 on control; difference -0.76 (95% CI -1.29 to -0.23), standardized effect d = -0.43; z-test p = 0.005.

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.

Percentage of Participants Who Received Rescue Therapy

• 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:
  • Canagliflozin 100/300 mg: 11.9% (10/84) versus 46.0% (40/87) on control; risk difference -34.1 percentage points (95% CI -46.6 to -21.5), risk ratio 0.26 (0.14–0.48); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Canagliflozin 100/300 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering several domains: glycemic measures, use and timing of rescue therapy, body weight and body mass index, and blood lipid measures. This range can provide context for the primary HbA1c result, but secondary outcomes do not replace the prespecified primary question. Their interpretation depends on each endpoint’s definition, analysis, follow-up, and missing-data handling.

For rescue therapy, the posted percentages are 46.0% in the placebo group and 11.9% in the combined canagliflozin group. The unadjusted comparison is reported as p < 0.001. This pattern is directionally consistent with a separation between groups in the trial’s overall glycemic outcome, but rescue therapy is a distinct outcome and depends on the protocol’s criteria for starting it. Those criteria and the primary analysis’s handling of rescue are not reported in the registry record. The registry does not list a sponsor-reported analysis for this secondary endpoint.

Detailed numerical results for the other listed secondary outcomes are not reported in the registry record. It is therefore not possible to describe a complete pattern across all secondary results or to assess their estimates and precision. The existence of an endpoint in the outcome list should not be mistaken for a posted numerical result.

Unadjusted secondary results carry less weight because the trial lists multiple outcomes and the registry does not report a multiplicity adjustment or testing hierarchy. When many endpoints are evaluated, a small p-value can arise even if no corresponding effect exists, simply because many tests are considered. This general issue does not negate a secondary finding, but it means that a nominal p-value should be interpreted cautiously unless the analysis plan specifies how the family of tests was controlled.

The secondary outcomes can help describe how the trial assessed dimensions beyond HbA1c, but they do not independently establish the primary result’s meaning. The strongest statistical interpretation remains anchored to the reported primary endpoint and its model-based comparison. Secondary evidence should be treated as supporting context only to the extent that its methods and results are sufficiently reported.

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

• Change From Baseline in Fasting Plasma Glucose (FPG) at Weeks 26 and 52
• Percentage of Participants With HbA1c Less Than (<)7.5 Percent (%), <7%, and <6.5% at Weeks 26 and 52
• Percentage of Participants Who Received Rescue Therapy
• Time to Rescue Therapy
• Percent Change From Baseline in Body Weight at Weeks 26 and 52
• Change From Baseline in Body Mass Index (BMI) at Weeks 26 and 52
• Percent Change From Baseline in Fasting Plasma Lipids Levels at Weeks 26 and 52
• Percent Change From Baseline in LDL-C to HDL-C Ratio and Non-HDL-C to LDL-C Ratio at Weeks 26 and 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: HbA1c change is measured on a numerical scale, and the reported group summaries are least-squares means with standard errors. Continuous outcomes can preserve differences in magnitude across participants, but their analysis depends on how the model represents group effects, baseline values, and missing observations. The registry names ANCOVA as the sponsor’s reported comparison method and separately describes the primary endpoint as analyzed with a pattern mixture model using multiple imputation.

What does ANCOVA contribute?

Analysis of covariance, or ANCOVA, estimates a treatment-group contrast while accounting for one or more other variables included in the model. In a baseline-adjusted clinical trial analysis, this approach commonly uses the baseline measurement to improve precision and account for chance baseline differences. The registry reports an ANCOVA least-squares mean difference of -0.76 for the primary comparison. The complete list of model terms, covariates, and implementation details is not reported in the registry record, so those features should not be presumed.

A least-squares mean is a model-based group estimate, not necessarily the raw arithmetic average of all observed values. It is calculated from the fitted analysis model. The least-squares mean difference expresses the model-based contrast between the groups. The registry’s primary values of 0.39 for placebo and -0.37 for combined canagliflozin are also identified as least-squares means, and the sponsor-reported comparison gives the difference between groups.

Why use multiple imputation?

Some participants may have missing endpoint measurements. Multiple imputation is a general statistical approach that replaces each missing value with several plausible values, analyzes each completed dataset, and combines results so that uncertainty about the missing values is reflected in the final inference. The registry states that a pattern mixture model with multiple imputation was used for the primary outcome. Pattern mixture approaches are general methods for examining missingness patterns and how outcome distributions may differ across them. The registry record does not report the imputation model’s variables, the number of imputed datasets, the assumptions for missing outcomes, or any sensitivity analyses. Those details therefore cannot be evaluated from the posted description.

Missing-data methods matter because observed outcomes may not represent participants without measurements. An analysis that depends on assumptions about unobserved values can change when those assumptions change. Multiple imputation does not make missing observations known; it provides a structured way to use assumptions and carry imputation uncertainty into estimates. Whether those assumptions are plausible requires more detail than the registry reports.

What is the unadjusted re-calculation?

The re-calculation is a simple, unadjusted comparison reconstructed from posted summary statistics. It uses the group-level means and standard errors to estimate the mean difference and a corresponding test. It is not a recreation of the sponsor’s ANCOVA or pattern mixture model. It does not account for model covariates or the details of the missing-data procedure unless those are encoded in the posted summaries. It is best read as a check on the direction and approximate strength of the group contrast, not as a replacement for the sponsor’s analysis.

The pooled standard deviation used in the continuous-outcome re-calculation is described as approximate. Such a quantity can help express the scale of a difference relative to variability, but a standardized effect is not the primary endpoint and is not a direct clinical threshold. It also depends on the variability estimate. The posted primary estimate itself is in percentage points of HbA1c and is easier to interpret in the endpoint’s original units.

How should the p-values be understood?

A p-value summarizes how incompatible the observed data are with a specified null model, assuming that model and its conditions hold. Smaller values indicate greater incompatibility with that null model; they do not quantify the probability that a result occurred “by chance,” the probability that a treatment has an effect, or the size of the difference. The sponsor reports p = 0.002 for the ANCOVA comparison, while the unadjusted summary-statistic calculation reports p = 0.005. Their difference is unsurprising when methods and information used in the calculations differ, and the values should not be treated as competing estimates from the same analysis.

For a binary outcome such as receipt of rescue therapy, the group summaries are percentages of participants and the comparison can be expressed as a risk difference. This is a difference between proportions, not a difference in means. The registry reports an unadjusted p-value for that endpoint, but no sponsor analysis is listed for it. Risk differences, relative risks, and odds ratios answer related but distinct questions; the chosen measure affects how a binary contrast is communicated.

Multiplicity is a general issue when a study assesses many outcomes or makes many comparisons. Repeated testing can increase the chance of at least one small p-value under a collection of null hypotheses. Whether and how the study addressed multiplicity is not reported in the registry record. The primary result should therefore be distinguished from secondary findings, and the unadjusted secondary p-value should be viewed with less weight than a result interpreted under a prespecified multiplicity strategy.

Finally, the planning calculations associated with the posted effect are illustrations, not evidence about the trial’s original design. The registry record does not report the original sample-size justification or its assumptions. General power calculations estimate the sample size that would be needed under stated assumptions to detect a chosen effect with a chosen probability; they do not describe the probability that this completed trial detected an effect after the results are known.

11. Confidence Intervals and Precision

The sponsor-reported primary difference is -0.76 percentage points, with a 95% confidence interval from -1.25 to -0.27. The interval is a measure of statistical precision: under the model and its assumptions, it gives a range of values compatible with the observed data at the stated confidence level. It includes values representing a more negative difference and values closer to zero. It does not mean that there is a 95% probability that the true effect lies in this particular interval.

Because the entire reported interval is below zero, the result is statistically distinguishable from no difference under the reported ANCOVA analysis at the conventional 5% level. The interval’s width also matters: even though it does not include zero, it allows a range of magnitudes. Statistical evidence against a zero difference is not the same as certainty about the exact size of the effect or its clinical importance.

The unadjusted re-calculation also gives an estimate of -0.76, but its interval is derived from summary statistics rather than the sponsor’s model. The re-calculation and sponsor analysis should not be collapsed into a single interval or described as if they use identical assumptions. The posted information does not provide all details needed to assess the model-based uncertainty independently, including the complete ANCOVA specification and the missing-data sensitivity analyses.

Precision is affected by the amount of information available, variability in the outcome, and the analysis model. The primary analysis includes 87 participants in the placebo group and 84 in the combined canagliflozin group. These group sizes do not, on their own, determine precision; the observed variability and analytic treatment of the data also contribute. The standard errors reported for the group least-squares means are 0.191 for placebo and 0.194 for combined canagliflozin. They describe uncertainty around the respective model-based means, not the between-group interval directly.

Confidence intervals do not account automatically for every source of uncertainty. They rely on the model, the analysis population, and assumptions about the data, including missing outcomes. They also do not resolve multiplicity across several outcomes. The interval is therefore best read as a precise statement about the estimated primary comparison under the reported analysis, rather than a complete summary of all uncertainty about the study.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not a record of the trial’s original sample-size calculation. For the continuous primary endpoint and the binary rescue-therapy endpoint, the figures are participants per arm. The sample-size assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect as the effect to detect. The trial’s own design assumptions and original sample-size justification are not reported in the registry record.

The 80% power column indicates the estimated number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect at the stated significance level, if the assumed effect and model conditions hold. The 90% power column makes the corresponding illustration for a 90% chance. Greater planned power generally requires more participants, all else being equal. For the primary endpoint, the row based on 100% of the observed effect lists 87 participants per arm for 80% power and 116 for 90% power. Planning for 75% of the observed effect lists 154 per arm for 80% power and 205 for 90% power; planning for 50% lists 345 and 462, respectively.

The rescue-therapy planning display also reports participants per arm. Its row based on 100% of the observed effect lists 27 per arm for 80% power and 36 for 90% power. The smaller-effect rows require larger sample sizes: planning for 75% lists 53 and 70 participants per arm, and planning for 50% lists 126 and 168. These are endpoint-specific illustrations, and their values should not be transferred from one outcome to another.

Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants per arm as the target effect gets smaller. These figures are not observed power: they do not measure the probability that the completed trial detected its result. They are prospective illustrations reconstructed using observed results and the stated assumptions, not the documented basis for the trial’s enrollment.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.760; pooled standard deviation σ = 1.780.
2. n = 2 × (1.96 + 0.842)² × 1.780² / -0.760² = 86.1, rounded up to 87 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 <- -0.76                      # observed difference in means
sigma <- 1.77981621616211                     # 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(3170518)
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 = 87 (80% power), 116 (90% power)
 75% of observed effect: n per arm = 154 (80% power), 205 (90% power)
 50% of observed effect: n per arm = 345 (80% power), 462 (90% power)
power.t.test: 87.1 
Simulated power at n = 87 per arm: 0.803 (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 reported primary analysis is an ANCOVA comparison of the placebo and combined canagliflozin groups. It gives a least-squares mean difference of -0.76, a 95% confidence interval from -1.25 to -0.27, and p = 0.002. This is the posted model-based result for the primary endpoint and should be read as distinct from the simple unadjusted re-calculation.

The re-calculation uses posted summary statistics to estimate the unadjusted difference. It gives the same displayed point estimate, -0.76, and p = 0.005. The match in the displayed point estimate does not mean that the calculations use the same model or data handling. The re-calculation does not reproduce the sponsor’s ANCOVA or the stated pattern mixture model with multiple imputation. It is a summary-statistic check rather than a second sponsor analysis.

The two p-values differ because they come from different calculations and may reflect different treatment of baseline information, uncertainty, and missing data. The registry record does not provide enough detail to reproduce the sponsor model in full. The sponsor-reported estimate and interval are therefore the appropriate description of the trial’s posted primary analysis, while the unadjusted result offers a separate, limited check of the direction and magnitude of the contrast. Neither p-value alone establishes clinical importance.

No discrepancy is flagged between the posted primary analysis and the re-calculation. That does not make the methods interchangeable; it means the posted result and the simple check do not suggest a reversal in the estimated direction. The sponsor’s analysis remains the model-based primary result, and the re-calculation should not be used to replace it or to infer unreported details of the analysis plan.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes a primary HbA1c outcome and a broad set of secondary outcomes. The registry lists fasting plasma glucose, HbA1c thresholds, rescue therapy, time to rescue therapy, body weight, body mass index, and lipid measures among the secondary endpoints. Across a group of statistical tests, multiplicity can increase the chance of at least one apparently unusual result when all underlying effects are absent. This is a general statistical concern, not a claim that any particular posted result is false.

The registry record does not report a multiplicity-control procedure, a testing hierarchy, or whether the secondary outcomes were intended to be confirmatory or exploratory. It also does not report an interim-analysis plan. Without those details, the reported p-values cannot be interpreted as having a known study-wide error rate. The primary result is reported separately, but the record does not describe whether it was protected within a broader testing strategy.

Missing data are addressed in the primary endpoint description: a pattern mixture model with multiple imputation was used. This is relevant because participants without a Week 26 measurement may differ from those with observed measurements. The registry does not give the imputation model, its assumptions, or sensitivity analyses examining departures from those assumptions. The method’s name alone is not enough to judge whether missingness could materially affect the estimate.

The full analysis set includes randomly assigned participants who received at least one dose and had a baseline HbA1c measurement. This definition identifies the population used for the primary outcome, but it is not identical to an intention-to-treat population that necessarily includes everyone randomized regardless of treatment received or baseline availability. The registry does not report enough information to describe a separate per-protocol analysis or the handling of every post-randomization event.

The original sample-size justification, the assumptions used when planning enrollment, and any prespecified procedures for missing measurements or multiplicity beyond the stated primary method are not reported in the registry record. The planning illustrations based on observed effects do not fill those gaps. These reporting limits constrain how fully the analysis can be audited and how confidently secondary results can be treated as confirmatory.

16. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pancreatitis acute (5.9%), cholelithiasis (1.5%), anaphylactic reaction (1.5%), erysipelas (1.5%), pneumonia (1.5%).

The registry reports serious adverse events separately for the placebo and two canagliflozin dose groups. There were 5 serious adverse events among 87 participants at risk in the placebo group, 7 among 67 at risk in the canagliflozin 100 mg group, and 1 among 17 at risk in the canagliflozin 300 mg group. The recorded number of deaths was 0 in each of these groups. These are counts within the registry’s stated at-risk groups, not a comparison adjusted for exposure time or other participant characteristics.

The safety groups are presented separately by dose, unlike the combined 100/300 mg group used for the primary endpoint. Their denominators differ from the primary endpoint group sizes, so the primary efficacy comparison should not be used as if it were the safety population. The registry also lists serious-event terms and percentages, including Pancreatitis Acute at 5.9%, and Cholelithiasis, Anaphylactic Reaction, Erysipelas, Pneumonia, and Diabetic Ketoacidosis at 1.5% each. The posted information does not establish that each term occurred in a particular dose group, so no group attribution should be inferred from that list.

Serious adverse event counts are a limited description of safety. They do not show all event details, timing, duration, causality assessments, or exposure-adjusted rates. Other adverse events were also reported, but the presence of an event count does not establish that treatment caused the event. The registry figures describe what was recorded during the study and should be interpreted alongside the study’s size and follow-up rather than as definitive evidence of comparative safety.

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

The primary result describes an estimated difference in Week 26 HbA1c change between participants in the combined canagliflozin 100/300 mg group and those assigned placebo. The sponsor-reported least-squares mean difference was -0.76 percentage points, with a 95% confidence interval from -1.25 to -0.27. In the reported ANCOVA analysis, the interval excludes zero and the p-value is 0.002. This is evidence of a group difference under the stated analysis, with uncertainty about its exact size.

The result does not show that every participant experienced a decrease in HbA1c, nor does it provide a separate estimate for the 100 mg and 300 mg groups. The primary outcome combined those doses. The result also does not show how HbA1c changed beyond the primary follow-up interval, or establish effects on outcomes not reported numerically in the registry.

A statistical difference is not automatically a clinically important difference. The registry record does not state a threshold for a clinically meaningful HbA1c change, so the estimate cannot be classified against such a threshold from this information alone. Nor does a p-value say how likely the result is to repeat in another study or what an individual participant’s outcome would be.

The trial’s population was children and adolescents aged 10 to under 18 years with type 2 diabetes. Results from this population do not automatically generalize to other age groups or settings. Generalizability also depends on details such as eligibility criteria and participant characteristics, many of which are not included in the information summarized in the registry record.

The secondary rescue-therapy result is a distinct piece of evidence, and the registry does not report numerical values for all other listed secondary outcomes. Safety counts are also separate from the primary efficacy estimate. None of these results alone answers every question about benefits, harms, longer-term outcomes, or comparative treatment choices. The findings should be understood as statistical results from this randomized trial, not as medical advice.

18. Why This Trial Matters Statistically

This trial offers a useful statistical example of how a clinical question, an endpoint, an analysis model, and a registry result fit together. The primary outcome is a continuous measure, HbA1c change, and the reported treatment contrast is a least-squares mean difference. The estimate is expressed in the original outcome scale, with a confidence interval that communicates more about precision than a p-value alone.

The record also illustrates why it matters to distinguish a sponsor-reported model-based analysis from a simple re-calculation based on posted summaries. The two estimates have the same displayed point estimate, but they are not the same analysis. ANCOVA and the stated pattern mixture model with multiple imputation involve methodological choices that a summary-statistic calculation cannot reproduce. Keeping those analyses separate prevents a convenient check from being mistaken for the trial’s primary method.

The combined dose analysis is another important interpretive feature. Combining the canagliflozin groups yields a primary comparison with placebo, but it does not answer dose-specific questions. The safety record, in contrast, presents groups separately by dose. Efficacy and safety summaries therefore need to be read with attention to which participants and groups each one represents.

The study also demonstrates how secondary endpoints can broaden the clinical description while complicating statistical interpretation. Many outcomes are listed, but detailed results are not available for all of them, and the record does not report a multiplicity strategy. An unadjusted secondary p-value has a different evidential status from a primary result analyzed under a documented plan.

Finally, observed-effect planning illustrations can show how sample size depends on the effect targeted, but they cannot stand in for the trial’s original design rationale. The distinction between a planning calculation and observed power is central to sound interpretation. Together, these features make the record valuable for understanding both what a reported estimate says and what the available reporting leaves unresolved.

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.

Several limitations are specific to the information available for this trial. The primary endpoint combines the 100 mg and 300 mg groups, so the posted primary estimate does not quantify the effect of either dose separately. The registry’s description of later treatment assignment is incomplete, which limits interpretation of the treatment regimen after the first 12 weeks. The record does not give enough detail to reconstruct the treatment course fully.

The sponsor’s primary result is reported as an ANCOVA analysis, and the endpoint description also names a pattern mixture model with multiple imputation. The full model specification, covariates, imputation details, and sensitivity analyses are not reported in the registry record. This limits independent assessment of how missing measurements and analytic assumptions affect the estimate. The unadjusted re-calculation cannot resolve those questions.

The registry does not report the original sample-size justification, multiplicity procedure, testing hierarchy, or interim-analysis plan. Without that information, the status of the secondary p-values as confirmatory or exploratory is unclear. Detailed numerical results for most listed secondary outcomes are not reported in the registry record, preventing a full assessment of consistency across outcomes.

The safety record gives counts and selected serious-event terms, but does not provide enough information to assess timing, duration, exposure-adjusted comparisons, or causal attribution. The safety group sizes differ by dose, and the primary efficacy analysis uses a combined group. These differences in populations and denominators make direct comparison across efficacy and safety summaries inappropriate without further detail.

Finally, registry results alone do not describe all participant characteristics, protocol deviations, or contextual factors that may affect generalizability. These limitations concern the scope and detail of the available record; they do not, by themselves, establish that the reported estimate is biased.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Investigate the Efficacy and Safety of Canagliflozin in Children and Adolescents (>=10 to <18 Years) With Type 2 Diabetes Mellitus — NCT03170518.
• Registry record last updated 2025-04-25; status last verified 2025-04.
• Results first posted 2025-03-12.
• 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 Phase 3 randomized, multicenter, double-blind, parallel-group, placebo-controlled study of canagliflozin in children and adolescents aged 10 to under 18 years with type 2 diabetes mellitus. It reports 171 participants enrolled and identifies the primary outcome as change from baseline in HbA1c at Week 26.

The primary analysis combined the canagliflozin 100 mg and 300 mg groups. The sponsor-reported ANCOVA least-squares mean difference versus placebo was -0.76 percentage points, with a 95% confidence interval from -1.25 to -0.27 and p = 0.002. The registry also posts a rescue-therapy outcome, while detailed numeric results for the other listed secondary outcomes are not reported in the registry record.

Serious adverse event counts are reported separately by treatment group, with 0 deaths recorded in each group. Important analysis details—including the original sample-size rationale, multiplicity procedures, and full missing-data assumptions—are not reported in the registry record. The estimates should therefore be interpreted in light of both their reported statistical precision and the limits of registry reporting.