Metabolic Analysis for Treatment Choice in Gestational Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Metabolic Analysis for Treatment Choice in Gestational Diabetes Mellitus (NCT03029702), a randomized phase 4 study. The primary outcome is Proportion of Women Who Are Eligible, Screened, Enroll and Remain in the Study.

2. Clinical Question

The clinical rationale in the registry is that GDM can arise through differing metabolic mechanisms, while usual treatment choice may involve provider and patient preference and trial and error. The trial therefore asks whether assigning treatment according to the GDM mechanism is feasible within a randomized study, as reflected in recruitment and retention, and also posts secondary measures related to treatment consistency and glucose control. This distinction matters: the primary result concerns participants’ progress through the study, not whether an individualized strategy improves maternal or infant health. The registry lists maternal and neonatal outcomes among secondary measures, but results for most of those outcomes are not reported in the registry record.

3. Trial Design

This was a phase 4 randomized, single-masked, parallel-group study, with 54 participants enrolled. The registry status is completed. Participants were allocated to usual care or individualized treatment, with 27 participants in each arm. The two arms used the same listed treatment options—insulin, glyburide, and metformin—but differed in the stated basis for treatment choice. In usual care, participants received standard counseling and a prescribed treatment. In individualized treatment, therapy was matched to the participant’s GDM mechanism after standard counseling.

The registry gives a study start date of 2018-02-28 and a primary completion date of 2023-08-31. The primary endpoint timeframe is through study completion, described as an average of 16 weeks. One secondary measure has a timeframe of 2 weeks after treatment initiation, while maternal glucose control is assessed at delivery. Other listed secondary outcomes include treatment consistency, remaining on the same treatment, cesarean delivery, hypertensive diseases in pregnancy, birthweight, neonatal lean body mass, and cord blood glucose.

The registry does not report the sequence-generation procedure, allocation concealment method, masking details, eligibility criteria, or the identity of the person or group masked. It also does not report how the individualized matching algorithm operationalized each metabolic mechanism. The original sample-size justification, planned statistical analysis protocol, and any interim analyses are not reported in the registry record. These omissions limit how fully the design can be reconstructed from the registry, even though the broad randomized, parallel structure and arm definitions are stated.

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

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 Proportion of Women Who Are Eligible, Screened, Enroll and Remain in the Study, measured over Through study completion, an average of 16 weeks.

The primary endpoint is described as the proportion of women who are eligible, screened, enroll, and remain in the study. Its stated timeframe extends through study completion, an average of 16 weeks. The measure is relevant to a study whose overall goal is to investigate an individualized treatment approach: the ability to recruit participants and retain them through follow-up is important when assessing whether such a strategy can be studied in practice.

There is a distinction between the endpoint’s wording and the posted data format. The registry labels the measure as a proportion, but gives the unit as participants and the parameter as a count. The arm results are counts, with 25 of 27 participants in usual care and 26 of 27 in individualized treatment represented in the posted results. The registry does not separately define the stages in the endpoint—eligibility, screening, enrollment, and remaining in the study—or provide stage-specific counts. Accordingly, the results can be read as posted participant counts, but they do not support a detailed breakdown of where participants entered or left the study process.

This endpoint is not a direct measure of glycemic control, pregnancy outcome, or treatment benefit. Those topics appear among secondary outcomes. The primary measure instead describes study participation and retention, which should be kept distinct from the clinical outcomes the study was intended to investigate.

7. Results Posted in the Registry

• Individualized Treatment: 96.3% (26/27) versus 92.6% (25/27) on control; risk difference 3.7 percentage points (95% CI -8.5 to 15.9), risk ratio 1.04 (0.91–1.18); unadjusted two-proportion z-test p = 0.552.

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.

Proportion of Participants With Consistent GDM Mechanism Before and and After Treatment Initiation

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Individualized Treatment: 77.8% (21/27) versus 81.5% (22/27) on control; risk difference -3.7 percentage points (95% CI -25.2 to 17.8), risk ratio 0.95 (0.73–1.25); unadjusted two-proportion z-test p = 0.735.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Individualized Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Women Who Remain on Same Treatment During Study

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Individualized Treatment: 96.3% (26/27) versus 92.6% (25/27) on control; risk difference 3.7 percentage points (95% CI -8.5 to 15.9), risk ratio 1.04 (0.91–1.18); unadjusted two-proportion z-test p = 0.552.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Individualized Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Maternal Glucose Control

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Individualized Treatment: 81.5% (22/27) versus 74.1% (20/27) on control; risk difference 7.4 percentage points (95% CI -14.7 to 29.5), risk ratio 1.10 (0.83–1.47); unadjusted two-proportion z-test p = 0.513.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Individualized Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results with numerical comparisons cover three distinct aspects: consistency of the GDM mechanism before and after treatment initiation, remaining on the same treatment, and maternal glucose control at delivery. Their estimated directions are mixed rather than consistently favoring one arm. The reported intervals are broad and include no difference, and the registry’s listed Fisher Exact p-values are 0.9, 0.9, and 0.8 for those outcomes. Taken together, these results do not show a clear pattern of separation between usual care and individualized treatment in the posted secondary comparisons.

These outcomes provide context for the primary participation result but do not transform it into a clinical efficacy result. The primary endpoint concerns eligibility, screening, enrollment, and retention; the secondary measures address treatment processes and glucose control. The trial’s rationale also concerns maternal and neonatal outcomes, but results for most of the listed outcomes—including cesarean delivery, hypertensive diseases in pregnancy, birthweight, neonatal lean body mass, and cord blood glucose—are not reported in the registry record.

Secondary findings generally carry less weight than a prespecified primary result because many outcomes create multiple opportunities to observe apparently notable differences. If multiple comparisons are examined without adjustment, the chance of at least one seemingly unusual result can increase. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints, so their p-values should be treated as exploratory rather than independent confirmation. Their value lies in describing the range of outcomes recorded and identifying questions that require adequately planned follow-up, not in establishing a definitive overall treatment effect.

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

• Proportion of Participants With Consistent GDM Mechanism Before and and After Treatment Initiation
• Proportion of Women Who Remain on Same Treatment During Study
• Maternal Glucose Control
• Proportion of Participants Who Deliver by Primary Cesarean
• Proportion of Participants Who Developed Hypertensive Diseases in Pregnancy
• Birthweight
• Neonatal Lean Body Mass
• Cord Blood Glucose

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the study as randomized and parallel, with usual care as the control arm and individualized treatment as the comparison arm. The calculations associated with the posted counts are unadjusted comparisons of two groups. They do not account for covariates, stratification, or other adjustments; such adjustments are not described in the registry record.

What does a risk difference express?

A risk difference expresses the difference between the proportions experiencing the stated event in the two arms. Here, the positive primary estimate means the posted event proportion is higher in the individualized-treatment arm than in usual care, according to the event coding used for the calculation. The estimate is expressed on the probability scale, so zero corresponds to equal proportions. For the primary endpoint, the recalculated estimate is 0.037. This is a direct, unadjusted comparison and should not be interpreted as an adjusted treatment effect.

The registry’s primary endpoint wording refers to a proportion, but its unit and posted arm values are participant counts. The calculated comparison uses the counts and arm sizes recorded for the analysis. That operational detail is important: the statistical contrast is only as clear as the outcome definition and coding. The registry does not provide additional stage-specific definitions for eligibility, screening, enrollment, or retention.

How should the p-values be understood?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The unadjusted recalculated p-value for the primary endpoint is 0.552. The registry-reported analysis names Fisher Exact and gives p = 0.9. Fisher’s exact test is a method for comparing categorical outcomes in small samples; it calculates a probability-based test result from the observed cell counts under its null hypothesis. The registry does not report the corresponding estimated contrast or interval for that analysis.

A p-value above a conventional threshold does not demonstrate equivalence or prove that no difference exists. The estimate and its confidence interval provide complementary information about direction, magnitude, and uncertainty. When enrollment is limited and outcome counts are close, the data may be compatible with a range of possible underlying differences.

What does a confidence interval add?

A confidence interval gives a range of effect estimates compatible with the observed data under the method used. In repeated use of the same procedure under its assumptions, intervals constructed at the stated confidence level would cover the true parameter at that rate. It is not a probability statement about the particular fixed effect after observing the data. For the primary risk difference, the interval extends from -0.085 to 0.159. Because it includes zero, the data are compatible with no difference as well as with differences in either direction. Its width also indicates limited precision.

The relative risk and odds ratio are alternative ways to express a binary-outcome comparison. Relative risk compares event proportions, while the odds ratio compares the odds of the event. These measures can be useful for different purposes, but neither removes uncertainty or resolves limitations in outcome definition. In small datasets, relative measures may be especially sensitive to a small number of participants, and their interpretation depends on which event is coded as the outcome.

What does the registry analysis contribute?

The registry lists a Fisher Exact p-value for the primary measure and for the three secondary measures with numerical results in the record. It does not give an adjusted model, analysis population definition, missing-data procedure, or fuller statistical plan. The registry’s analysis results should therefore be read as limited reporting rather than as a complete account of every analytical decision. The recalculations are simple unadjusted comparisons of the posted summary counts, not a replacement for a prespecified sponsor analysis.

The presence of randomization supports a planned comparison between the assigned groups, but interpretation still depends on follow-up, outcome definitions, and analysis populations. The registry does not report whether all randomized participants were included in each outcome analysis, whether missing observations occurred, or how participants were analyzed if treatment changed. These details are important to understanding what an arm comparison represents.

Why can binary outcomes be difficult to interpret in small studies?

For a binary endpoint, each participant contributes an event or a non-event under the coding used. When the number of participants is limited, one or a few outcomes can materially affect the estimated proportion and the comparison. The interval may consequently be wide even when the point estimate appears straightforward. This is a general feature of binary data, not evidence that any particular result is wrong. The registry’s arm sizes are 27 participants each, so the estimates should be read with their uncertainty rather than as definitive population values.

Finally, the trial’s primary endpoint is about participation and retention, while the proposed clinical rationale concerns treatment matching and outcomes of pregnancy. Statistical evidence on the former does not automatically answer the latter. The secondary outcomes offer some information about treatment process and glucose control, but their reported comparisons are also imprecise, and most listed outcomes lack posted numerical results.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.037, with a confidence interval from -0.085 to 0.159. The interval crosses zero, the value corresponding to no difference between arms. It therefore includes both a negative contrast and a positive contrast, rather than identifying one direction with precision. Its width signals substantial uncertainty around the point estimate.

The interval should be read as a range of effect sizes reasonably compatible with the data and the method, not as a guarantee that the true effect lies within these exact limits. The posted arm sizes are 27 participants in each group, and the observed counts are close. With binary outcomes and limited group sizes, estimates can be imprecise; small changes in the observed event counts can affect the calculated proportions and their contrast.

The same caution applies to secondary comparisons. Their intervals also extend across zero: mechanism consistency has an estimated risk difference of -0.037, with limits -0.252 and 0.178; remaining on the same treatment has an estimate of 0.037, with limits -0.085 and 0.159; and maternal glucose control has an estimate of 0.074, with limits -0.147 and 0.295. These ranges include no difference and allow effects in both directions. They do not support precise ranking of the strategies on these outcomes.

Statistical uncertainty is distinct from clinical importance. The registry does not state a threshold for a clinically meaningful difference, so the intervals cannot be classified against a prespecified clinical margin. The result is best described as inconclusive about the size and direction of between-arm differences, rather than as proof of equality.

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 the trial’s original design assumptions. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. The figures are participants per arm for these binary outcomes; they are not total event counts. The registry’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned chance of detecting the specified effect under the stated assumptions if that effect were the true one. The 90% power column uses a higher target chance of detection under the same general framework. These are design-planning quantities, not guarantees about a future study’s result. The values change with the assumed effect: planning for 75% of the observed effect requires more participants per arm than planning for 100%, and planning for 50% requires still more. Smaller effects are harder to distinguish from random variation, so they require larger groups to reach a given power target.

For example, the primary comparison’s planning illustration ranges from 600 participants per arm for planning around 100% of the observed effect at 80% power to 2,774 per arm for 50% of the observed effect at 80% power. The corresponding 90% figures are 802 and 3,713 participants per arm. These calculations are hypothetical planning aids, not a recommendation about a particular future study. They depend on the observed effect, which is uncertain in a small trial. This is not observed power; it does not measure the probability that the completed trial detected its true effect.

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 = 0.926; treatment proportion p₁ = 0.963; average p̄ = 0.944.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3239 = 0.6349.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3229 = 0.2717.
4. n = (0.6349 + 0.2717)² / (0.0370)² = 599.3, rounded up to 600 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 <- 0.925925925925926                          # control proportion
p1 <- 0.962962962962963                          # 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(3029702)
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 = 600 (80% power), 802 (90% power)
 75% of observed effect: n per arm = 1,150 (80% power), 1,539 (90% power)
 50% of observed effect: n per arm = 2,774 (80% power), 3,713 (90% power)
power.prop.test: 599.3 
Simulated power at n = 600 per arm: 0.804 (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. Analyses Reported by the Sponsor

The registry reports a Fisher Exact analysis with p = 0.9 for the primary endpoint. The unadjusted recalculation from the posted arm counts gives a risk difference of 0.037, a confidence interval from -0.085 to 0.159, and p = 0.552. These entries are not reported in identical form: the registry analysis gives a test method and p-value, while the recalculation also supplies a between-arm effect estimate and interval. The registry associates its reported analysis with the usual-care group and does not provide a contrast estimate alongside that p-value.

The registry does not explain whether the sponsor’s analysis and the recalculation use the same outcome coding, analysis population, or exact testing setup. The different p-values should therefore not be treated as a direct contradiction without those details. The discrepancy indicator is false, but that does not fill in the missing analysis specifications. The recalculation is a transparent, simple comparison of the posted summary counts; it does not replace the registry-reported analysis or establish which analysis was prespecified. The sponsor’s full statistical plan, including any rationale for its test and analysis population, is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes and reports numerical analyses for three of them in the record. It does not report whether the trial used a formal hierarchy for testing these outcomes, an adjustment for multiple comparisons, or a distinction between confirmatory and exploratory analyses. When many outcomes are tested, interpreting each p-value as if it were the only test can overstate the evidence. A multiplicity plan can control how the overall error rate is handled, but no such plan is reported in the registry record.

The record also does not report a missing-data strategy. It gives participant counts for the primary endpoint and selected secondary measures, but does not state whether any observations were missing, how missing outcomes were classified, or whether any imputation or sensitivity analysis was performed. No analysis population—such as all randomized participants or participants with complete outcome data—is defined in the statistical information reported. The handling of treatment changes and any departures from assigned treatment is also not reported.

These omissions matter because the interpretation of an arm comparison depends on who contributed data and how incomplete follow-up was addressed. They do not establish that missing data or protocol deviations occurred; they mean that the registry does not describe these aspects. Similarly, no interim analyses, stopping rules, or original statistical analysis plan are reported in the registry record. Without those details, it is not possible to assess whether the posted analyses follow a prespecified testing strategy or to reconstruct the full inferential framework.

The completed status and enrollment count describe the study’s overall record, but they do not supply the missing methodological details. The estimates and p-values should therefore be read as the results reported, with uncertainty about unreported analytical decisions kept distinct from the observed counts themselves.

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 0% reporting threshold.

The registry reports zero serious adverse events among 27 participants in usual care and zero among 27 participants in individualized treatment. It also reports zero other adverse events in each arm and zero deaths in both arms. No serious adverse-event terms are listed.

These are event counts over the recorded study period, not proof that an arm has no risk. With a limited number of participants and a finite follow-up period, an absence of recorded events can coexist with uncertainty about uncommon events or events outside the observation period. The registry does not provide further detail about adverse-event definitions, severity grading, relatedness, or collection procedures. The figures describe what was posted and should not be interpreted as a comprehensive safety comparison or as evidence that either treatment strategy is risk-free.

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

The results show that the posted primary participation counts were close across the two randomized groups: 25 participants in usual care and 26 in individualized treatment, out of 27 in each arm. The unadjusted risk-difference estimate is small, but its confidence interval is broad and includes zero. The data do not establish a clear difference in study participation and retention, and they do not precisely rule out differences in either direction.

That conclusion is limited to the endpoint as recorded. It is not a conclusion about whether matching treatment to GDM mechanism improves glucose control, pregnancy outcomes, or infant outcomes. The primary endpoint is about the study process, while those clinical outcomes are secondary. For the secondary comparisons with posted numerical results, the estimates are uncertain and do not form a consistent pattern. Numerical results for most of the maternal and neonatal outcomes listed in the registry are not reported in the registry record.

A result that is not statistically distinguishable from zero does not establish that the treatment strategies are equivalent. Equivalence requires a defined margin and an analysis designed to assess whether the uncertainty interval falls within that margin. The registry does not report such a margin. Nor does a p-value above a conventional threshold establish that the approaches have no effect. The findings are better described as inconclusive and imprecise for between-arm differences.

The study was randomized and included 54 participants, which provides a structured comparison but leaves limited information for estimating uncommon binary outcomes precisely. The absence of reported adverse events is also confined to the registry’s recorded counts and follow-up. Overall, the record documents a completed comparison and several outcome summaries, but it does not settle the broader clinical question motivating the study. Further interpretation depends on clearer outcome definitions, fuller reporting, and evidence with adequate precision for the clinical outcomes of interest.

18. Why This Trial Matters Statistically

This study raises a useful statistical question about individualized treatment: can a treatment strategy based on a participant’s metabolic mechanism be evaluated against usual care in a randomized design? The two arms used the same listed medications but differed in the stated basis for choosing therapy. That design makes the comparison about the strategy for treatment selection, rather than a comparison of one named drug with another.

The primary endpoint also highlights the difference between feasibility and clinical efficacy. Recruitment and retention are important for determining whether a study can be conducted and followed through. They are not substitutes for outcomes such as maternal glucose control or pregnancy and neonatal outcomes. Keeping those questions separate prevents a favorable or similar participation count from being interpreted as evidence about clinical benefit.

Statistically, the posted risk difference and its interval illustrate why point estimates should not be read in isolation. A single estimate can look close to zero while its uncertainty still permits effects in either direction. The sample-size illustrations make a related point: when the target is a smaller effect, substantially more participants per arm are needed under the stated planning assumptions. These calculations do not revise the completed study; they help explain why small trials can provide limited precision.

The record also illustrates the importance of complete statistical reporting. Outcome definitions, analysis populations, missing-data handling, multiplicity plans, and original sample-size assumptions are not reported in the registry record. Those details help readers distinguish prespecified confirmatory analyses from exploratory comparisons and understand exactly which participants and outcomes inform each estimate. The posted results are informative as a record of the observed data, but the gaps constrain how far the findings can be generalized or interpreted.

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 main limitation for interpretation is the small enrollment: 54 participants, with 27 in each arm. The confidence intervals are broad for the primary and secondary binary comparisons, so the data provide limited precision for differences between strategies. This is especially relevant for outcomes that may be uncommon, for which a small number of events can substantially influence an estimated proportion.

The primary endpoint’s description combines eligibility, screening, enrollment, and retention, while the posted outcome is reported as a participant count. The registry does not provide stage-specific counts or additional operational definitions. This makes it difficult to determine which part of the study process the recorded arm values most directly represent. The distinction between a proportion label and count-based reporting should be kept in view when interpreting the contrast.

Other limitations arise from incomplete reporting rather than evidence of a specific flaw. The registry does not report the details of randomization, masking, matching procedures, analysis populations, missing-data handling, multiplicity control, interim analyses, or the original sample-size rationale. It also does not provide numerical results for most listed maternal and neonatal secondary outcomes. These omissions limit assessment of the trial’s execution and the breadth of its clinical findings.

The registry identifies the study as single-masked but does not specify who was masked. The treatment options are listed, but the record does not give further details about treatment selection in usual care or how metabolic matching was implemented. The posted results therefore support interpretation of the stated arm strategy and available counts, but not a detailed appraisal of adherence, crossover, or the matching process.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Metabolic Analysis for Treatment Choice in Gestational Diabetes Mellitus — NCT03029702.
• Registry record last updated 2024-11-29; status last verified 2024-11.
• Results first posted 2024-11-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03029702 is a completed phase 4 randomized, single-masked, parallel-group study of usual care versus treatment individualized to GDM mechanism. It enrolled 54 participants, with 27 in each arm, and listed insulin, glyburide, and metformin as treatment options.

The primary endpoint concerns eligibility, screening, enrollment, and remaining in the study through completion, described as an average of 16 weeks. The posted counts are 25 in usual care and 26 in individualized treatment. The recalculated risk difference is 0.037, with a confidence interval from -0.085 to 0.159 and an unadjusted p-value of 0.552. The interval includes no difference and indicates limited precision.

Numerical secondary results cover mechanism consistency, remaining on the same treatment, and maternal glucose control; their comparisons are uncertain. Results for most listed maternal and neonatal outcomes are not reported in the registry record. The registry reports zero serious adverse events, other adverse events, and deaths in each arm. Important details of the statistical plan and analysis handling are not reported in the registry record.