Early Screening and Treatment of Women With Prediabetes in Pregnancy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Early Screening and Treatment of Women With Prediabetes in Pregnancy (NCT01552213), a randomized na study. The primary outcome is Number of Patients With a Diagnosis of Gestational Diabetes at 26 Weeks Gestation..

2. Clinical Question

The registry describes a randomized trial intended to examine whether medical nutrition therapy for pregnant women with prediabetes could affect impaired glucose tolerance later in pregnancy and perinatal outcomes. The posted primary endpoint is narrower: a diagnosis of gestational diabetes at 26 weeks, based on the criteria stated in the record. The primary result therefore addresses the recorded diagnosis at that time point, rather than every possible measure of glucose regulation or pregnancy outcome.

The registry record does not report detailed eligibility criteria, how prediabetes was defined for enrollment, or participant characteristics. It also does not report whether screening and treatment were applied in a way that could be separated from routine clinical care. Those omissions limit how specifically the trial population and care context can be described.

3. Trial Design

The study is recorded as a randomized, parallel-group trial with no masking. Its status is completed. The registry lists Stanford University as the sponsor and gives the study start as 2012-03 and primary completion as 2014-09. The trial title concerns early screening and treatment of women with prediabetes in pregnancy; the registry's primary endpoint concerns gestational diabetes diagnosis at 26 weeks of gestation.

The treatment group received regular dietician visits, exercise guidance, self blood glucose monitoring, and insulin therapy if determined necessary. The minimum intervention control group had a single visit with a dietician or health educator, followed by routine care per provider. The record does not give further details about visit schedules, treatment adherence, or how decisions about insulin were made.

For the primary endpoint, the posted group summaries include 42 participants in the treatment group and 41 in the control group. These are the denominators shown for that outcome; they should not be taken as an account of all participants enrolled or as evidence about why outcome data may differ from enrollment. The registry enrollment is 95. Reasons for any difference between enrollment and the endpoint denominators are not reported in the registry record.

The record does not report the randomization sequence method, allocation concealment, the original sample-size justification, or the trial's prespecified statistical analysis plan. Although the study is marked as unmasked, the implications of that design feature for outcome assessment cannot be established from the record alone. No specific conclusion about protocol adherence, deviations, or analysis populations is warranted from the available details.

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 Number of Patients With a Diagnosis of Gestational Diabetes at 26 Weeks Gestation., measured over 26 weeks of gestation.

The primary endpoint is the number of participants with a diagnosis of gestational diabetes at 26 weeks of gestation. The registry describes diagnosis as based on criteria recommended by the ADA: an oral glucose tolerance test with one abnormal value, with fasting glucose at least 92, one-hour glucose at least 180, or two-hour glucose at least 153. These thresholds define the event being counted in the posted primary result.

A participant count is a binary-outcome summary: each participant is classified according to whether the endpoint occurred. Comparing the proportions with the diagnosis in the randomized groups gives a direct summary of how often the recorded outcome was observed under the two care strategies. The endpoint is clinically relevant to the trial's stated aim of assessing impaired glucose tolerance later in pregnancy, but it is not a complete summary of maternal or infant health, nor does it capture glucose values outside the stated diagnostic criteria.

The use of a specified gestational time point makes the question concrete, but also confines the result to that assessment. The registry record does not describe how missing tests, measurements taken outside the specified time, or borderline values were handled. It also does not report a broader primary outcome combining diagnosis with severity or other outcomes.

7. Results Posted in the Registry

• Treatment for Glucose Intolerance: 45.2% (19/42) versus 56.1% (23/41) on control; risk difference -10.9 percentage points (95% CI -32.2 to 10.5), risk ratio 0.81 (0.53–1.24); unadjusted two-proportion z-test p = 0.322.

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.

Number of Participants With Excessive Gestational Weight Gain

• 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:
  • Treatment for Glucose Intolerance: 17.1% (6/35) versus 16.7% (6/36) on control; risk difference 0.5 percentage points (95% CI -17.0 to 17.9), risk ratio 1.03 (0.37–2.89); unadjusted two-proportion z-test p = 0.957.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment for Glucose Intolerance and the control. The interval gives the range of effects that remain compatible with the data.

Mean Hemoglobin A1C Value at Delivery

• 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:
  • Treatment for Glucose Intolerance: mean 5.50 versus 5.80 on control; difference -0.30 (95% CI -0.49 to -0.11), standardized effect d = -0.85; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Treatment for Glucose Intolerance than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Fasting Triglyceride Level

• 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:
  • Treatment for Glucose Intolerance: mean 181.00 versus 177.50 on control; difference 3.50 (95% CI -22.70 to 29.70), standardized effect d = 0.06; z-test p = 0.793.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment for Glucose Intolerance and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains: delivery mode, gestational weight gain, laboratory measures, hypertensive conditions, postpartum glucose tolerance, and insulin use. The record lists 14 secondary outcomes as posted. These measures broaden the descriptive picture beyond the primary diagnosis at 26 weeks, but they assess different outcomes, time points, and participant subsets. They should not be treated as interchangeable evidence about the primary endpoint.

Across the outcomes with numerical results available, the pattern is not a single uniform signal that can be summarized as a common treatment effect. Some endpoints are counts and others are means, and the reported results have different degrees of uncertainty. That overall pattern does not establish that the intervention changed all aspects of maternal or perinatal outcomes, nor does it establish that no differences occurred. The primary comparison remains the direct answer to the trial's principal posted question.

Secondary findings generally carry less confirmatory weight when many outcomes are examined. The registry does not report a multiplicity adjustment, a complete prespecified hierarchy, or which secondary outcomes were designated as confirmatory. When many separate comparisons are considered, an isolated small p-value can arise by chance more readily than when a single analysis is planned. This general concern is one reason to interpret secondary results alongside their intervals, the endpoint definitions, and the full analysis context rather than as stand-alone conclusions.

Outcome-specific denominators also vary, and the record does not explain all differences in available data. As a result, apparent patterns across endpoints may reflect both real differences in outcomes and differences in who contributed data to each analysis. Without information on missingness and analysis populations, comparisons across endpoints should remain descriptive.

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

• Number of Participants With Different Modes of Delivery
• Number of Participants With Excessive Gestational Weight Gain
• Mean Hemoglobin A1C Value at Delivery
• Mean Fasting Triglyceride Level
• Number of Patients With Gestational Hypertension
• Number of Patients With Pre-eclampsia
• Mean Level of Postpartum Oral Glucose-tolerance-test at 6 Weeks Postpartum
• Number of Participants With Need for Insulin Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count of participants meeting a diagnostic definition. For this kind of binary outcome, a group proportion describes the share of participants with the event, while a risk ratio compares those proportions. A risk ratio of 1 would indicate equal proportions; a value below 1 indicates a lower observed proportion in the treatment group relative to control, and a value above 1 indicates a higher observed proportion. This is general statistical interpretation. The registry reports a risk ratio of 0.80 for the primary comparison.

The reported primary method is Chi-squared, and the reported measure is a risk ratio with a 95% confidence interval. A Chi-squared test evaluates whether the observed pattern of event and non-event counts is compatible with equal proportions under its assumptions. A p-value summarizes how surprising the data would be under a specified null hypothesis and test procedure. It is not the probability that the null hypothesis is true, and it does not describe the size or clinical importance of an effect.

The recalculated risk difference is an unadjusted contrast between the observed group proportions. Risk difference and risk ratio describe the same binary data on different scales: the risk difference is expressed as a difference in proportions, whereas the risk ratio is expressed as a relative comparison. Both measures need an uncertainty interval to show how much precision the data provide. The registry's reported analysis remains the source for the sponsor's stated method and estimate; the recalculation is a simple unadjusted calculation from the posted summaries.

For a confidence interval, the general interpretation is that the method produces intervals that cover the underlying parameter at the stated rate over repeated studies under the model assumptions. A single interval does not mean there is a 95% probability that the true value lies inside it. Its practical value is to show a set of effect sizes compatible with the observations and method. The primary interval spans the null value for both the risk-ratio and risk-difference scales, so the posted result does not distinguish the observed group contrast from no difference at the conventional level.

Other posted outcomes use different statistical summaries. Counts of participants with events are binary outcomes, while means such as hemoglobin A1C and fasting triglyceride level are continuous outcomes. For a mean, the standard deviation describes participant-to-participant spread within a group; it is not the same as the uncertainty in the estimated mean. A mean difference compares the reported group means. The registry's reported analyses for the continuous outcomes use two-sided t-tests. As a general matter, a t-test compares means while accounting for within-group variability and the amount of data, subject to its assumptions.

Over-dispersion matters in settings where observed variability exceeds what a chosen statistical model expects. A model that understates variability can produce intervals that are too narrow and p-values that are too small. This is a general statistical concern; the posted primary endpoint is a binary comparison, and the registry does not report an over-dispersion assessment or a model-based adjustment for it. The available record also does not describe adjustment for covariates, clustering, repeated measurements, or other departures from a simple group comparison.

The registry does not report whether the primary analysis followed an intention-to-treat principle, whether participants were analyzed according to assigned group, or whether a per-protocol or other analysis population was used. It does not report how missing outcome values were handled. Those details can affect the meaning of an estimate, particularly when endpoint data are not available for every enrolled participant. The endpoint summaries should therefore be interpreted as the posted data, without assuming a particular missing-data or population strategy.

The record lists 15 outcome measures and 14 analyses, but a complete prespecified testing sequence is not reported. Testing several outcomes can increase the chance of at least one apparently notable result if each is considered separately. A multiplicity adjustment can be used to control that broader error rate, but whether any adjustment was planned or applied is not reported in the registry record. Consequently, isolated secondary p-values should not be treated as definitive evidence without context about prespecification and the full set of analyses.

The planning illustrations are distinct from the trial's original design. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation, with the effect to detect set to a stated fraction of the observed effect. These assumptions are known for the illustrations, but the trial's own original sample-size assumptions and justification are not reported in the registry record. Such calculations are planning aids, not descriptions of the study's actual analysis method.

11. Confidence Intervals and Precision

The primary risk-ratio estimate is 0.80, and its 95% confidence interval runs from 0.53 to 1.24. The span includes the null value of 1 and reaches both below and above it. In plain terms, the posted data are compatible with a lower relative frequency of diagnosis in the treatment group, little or no relative difference, or a higher relative frequency. The point estimate alone does not capture this uncertainty.

On the risk-difference scale, the recalculated estimate is -0.109, with an interval from -0.322 to 0.105. Because this interval includes zero, it also accommodates no difference in observed proportions. These two intervals use distinct effect scales and should not be read as if their values were directly interchangeable. Both communicate uncertainty around the observed comparison.

A confidence interval is more informative than a p-value alone because it conveys both direction and precision. Here the primary interval is broad enough to leave room for materially different contrasts. The record does not report a prespecified threshold for a clinically important difference, so the interval cannot be classified against such a threshold. Statistical uncertainty also does not resolve possible uncertainty arising from missing data, outcome assessment, or other design features that are not described.

The secondary continuous outcomes have their own precision, reflected in the reported group spreads and recalculated mean-difference intervals where available. Those estimates address different questions and should not be used to narrow uncertainty about the primary diagnosis endpoint. Their interpretation remains limited by the outcome-specific denominators and the absence of further analysis details in the registry record.

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 illustrations report participants per arm for the binary and continuous outcomes in this trial; there are no time-to-event illustrations reporting total event counts. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. These are planning assumptions for the illustrations; the trial's own original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect. The 90% power column gives the corresponding planning target for a 90% chance. Power is a property of a planned study under specified assumptions, not a measure of certainty about the result after data have been observed.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. That pattern follows because smaller effects are harder to distinguish from random variation with the same design assumptions. The calculations are illustrations based on the observed effect, rather than a reconstruction of the actual trial design or a guarantee that a future study would achieve its target.

This is not observed power. Observed power is not a useful substitute for examining the estimate and its confidence interval after a study is complete. The planning figures should instead be read as conditional design illustrations, whose relevance depends on whether their assumed effect size and other assumptions are appropriate for a future study.

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 = 0.561; treatment proportion p₁ = 0.452; average p̄ = 0.507.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3858.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7029 = 0.5915.
4. n = (1.3858 + 0.5915)² / (-0.1086)² = 331.5, rounded up to 332 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 <- 0.560975609756098                          # control proportion
p1 <- 0.452380952380952                          # 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(1552213)
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 = 332 (80% power), 444 (90% power)
 75% of observed effect: n per arm = 590 (80% power), 789 (90% power)
 50% of observed effect: n per arm = 1,324 (80% power), 1,772 (90% power)
power.prop.test: 331.5 
Simulated power at n = 332 per arm: 0.795 (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 the primary comparison using a Chi-squared analysis and a risk ratio of 0.80, with a 95% confidence interval from 0.53 to 1.24 and p = 0.32. The simple unadjusted recalculation from the posted counts gives a risk ratio of 0.806, with an interval from 0.525 to 1.238, and p = 0.322. The differences are consistent with the registry's rounded presentation. The record does not flag a discrepancy for the primary analysis.

For secondary outcomes, the sponsor's reported p-values and the simple recalculations are not identical in every case. For example, the hemoglobin A1C comparison has a recalculated p-value of 0.001 and a reported p-value of 0.01; the fasting triglyceride comparison has a recalculated p-value of 0.793 and a reported p-value of 0.75. The registry does not explain these differences, so their cause should not be inferred. The recalculations use the posted summary statistics and are unadjusted; they may not reproduce all details of the sponsor's analysis.

For interpretation, the registry's reported analysis is the trial's own stated result. Recalculated quantities provide a transparent check based on the summaries, not a replacement for the analysis method or any information not reported in the record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 15 outcome measures and 14 analyses. It does not report a multiplicity adjustment, a family of outcomes used to define a single error rate, or a prespecified hierarchy specifying which comparisons should receive confirmatory emphasis. Without those details, the reported p-values for secondary outcomes are best treated as nominal results rather than as evidence that has been adjusted for the full set of possible comparisons.

Multiplicity is a general statistical issue: when many hypotheses are tested, the chance of at least one small p-value under a broad no-effect scenario increases unless the testing approach accounts for the number or structure of comparisons. This does not mean that any particular secondary finding is false. It means that p-values should be interpreted in the context of how many analyses were considered and whether the analyses were prespecified. The registry record does not provide enough information to resolve that context.

Missing-data handling is also not reported in the registry record. Outcome denominators vary, and the primary outcome denominators do not account for the full registry enrollment. The reasons for the differences, the number or pattern of missing observations for each endpoint, and any imputation or sensitivity analyses are not reported. It is therefore not possible to determine whether the observed summaries could be affected by missingness or to assess the direction of any such effect.

The record does not state whether the analyses used an intention-to-treat population, a per-protocol population, or another defined group. Nor does it report whether participants were analyzed by randomized assignment. These choices influence how a comparison is interpreted, especially when treatment adherence, crossover, or missing assessments may occur. Such details are not reported and should not be assumed.

The registry reports Chi-squared testing for the primary binary outcome and two-sided t-tests for the listed continuous comparisons, but does not provide a full statistical analysis plan or adjustment details. The absence of these reporting elements limits assessment of prespecification and robustness; it does not by itself demonstrate that the analyses were improperly conducted.

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 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: intrauterine fetal demise (2.2%).

The adverse-event summary lists serious events among 50 participants at risk in the treatment group and among 45 participants at risk in the minimum intervention control group. It records zero serious events in the treatment group and one in the control group. The registry's top serious-event term is “Intrauterine Fetal Demise,” listed as 2.2%. The record does not provide further event-level detail or clarify how that term relates to the group-level summary, so the percentage should be read as reported rather than independently interpreted.

The summary lists zero other adverse events in both groups. Death counts are not reported in the registry record. The adverse-event denominators differ from the primary endpoint denominators, and the record does not explain why. These safety summaries are counts from the registry, not a basis for estimating comparative risk with precision or attributing an event to treatment.

Rare events are especially difficult to compare in a trial of this size, and a small count does not rule out events that were not observed. Conversely, an event occurring in a group does not establish that the assigned care caused it. The available safety information is limited to the posted counts and term, without detailed severity, timing, relatedness assessments, or fuller context.

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

The primary result describes the frequency of a gestational diabetes diagnosis at 26 weeks in the two randomized groups, as recorded in the registry. The posted estimate favors fewer diagnoses in the treatment group, but its confidence interval includes no difference and also includes values in the opposite direction. The data therefore do not provide a precise, definitive estimate of the group contrast.

This finding does not prove that the groups were equivalent, and it does not show that treatment had no effect. A result that is not statistically significant can reflect a small or absent effect, limited precision, or both. The confidence interval is essential because it shows the range of contrasts compatible with the data and analysis; it is not limited to the point estimate.

The primary endpoint is a diagnosis at a specified gestational time point using the thresholds in the registry. It is not a direct summary of every aspect of glucose tolerance, treatment burden, maternal health, delivery, or infant outcomes. Secondary measures can add context, but their presence does not transform the primary result into a comprehensive evaluation of all potential benefits and harms.

The record's limited information on eligibility, missing data, analysis populations, and the original statistical plan also constrains interpretation. The findings describe the posted outcome summaries and analyses, not necessarily every participant's course or every outcome considered by investigators. Any application beyond the specific trial population and care strategies would require evidence about how closely those circumstances match.

No treatment recommendation follows from these statistics alone. The result is most accurately read as an uncertain comparison in this completed randomized trial, with the uncertainty and reporting gaps considered alongside the observed group summaries.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a p-value are not enough to characterize a clinical comparison. The primary estimate is directionally below the null on the risk-ratio scale, but the confidence interval extends across the null and into the opposite direction. Reading the interval helps distinguish the observed point estimate from what the data can establish with precision.

It also shows the importance of keeping endpoint definitions in view. The primary question concerns a diagnosis at 26 weeks under specific glucose thresholds, while the listed secondary outcomes span different clinical domains and measurement types. A collection of outcomes can describe a broader trial, but it does not automatically create a single unified effect or answer every question about care.

The trial is randomized and parallel, yet important elements needed to evaluate the analysis are not reported in the registry record. Allocation methods, missing-data handling, analysis populations, multiplicity procedures, and the original sample-size justification are absent. Statistical interpretation depends not only on the test result, but also on how the study was planned and how the reported data relate to the randomized groups.

Finally, planning illustrations based on an observed effect should not be confused with evidence about the completed study's power. Their assumptions are explicit, but they are separate from the original design. This distinction helps prevent retrospective calculations from being mistaken for trial-planning decisions or for proof that an uncertain result is conclusive.

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 registry record leaves several trial-specific questions unanswered. It does not report detailed eligibility criteria, participant characteristics, the operational definition of prediabetes, or the screening procedures used to identify participants. Without these details, the degree to which the enrolled group represents a clearly defined clinical population cannot be assessed from the record.

The trial is unmasked, but the registry does not describe who knew treatment assignments during outcome assessment or whether the primary diagnosis was assessed in a way that could be influenced by knowledge of group. It also does not provide the randomization sequence method or allocation concealment details. These omissions prevent a fuller assessment of conduct and potential sources of bias; they do not establish that bias occurred.

The outcome denominators vary, and the record does not explain missing observations, exclusions, or analysis populations. It does not describe adherence, crossovers, deviations from assigned care, or how insulin decisions were operationalized. The record also lacks a complete statistical analysis plan, multiplicity details, and a trial-specific sample-size justification. These limitations affect assessment of robustness, prespecification, and precision.

The primary endpoint is a diagnosis at one gestational time point, and the posted summary does not describe the trajectory of glucose measurements or the severity of impairment. The outcome list includes additional maternal and perinatal measures, but the registry's short descriptions do not provide comprehensive definitions or full analytic context for all of them. Safety reporting is also limited to aggregate counts and a listed serious-event term, with no further event-level information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Early Screening and Treatment of Women With Prediabetes in Pregnancy — NCT01552213.
• Registry record last updated 2019-01-16; status last verified 2018-07.
• Results first posted 2019-01-16.
• 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 describes a completed, randomized, unmasked, parallel-group trial of treatment for glucose intolerance compared with minimum intervention control among pregnant women with prediabetes. The primary outcome is the number of participants diagnosed with gestational diabetes at 26 weeks of gestation. The treatment strategy included dietician visits, exercise, glucose self-monitoring, and insulin if considered necessary; the control strategy included a single educational visit followed by routine care.

The posted primary estimate is a risk ratio of 0.80 with a 95% confidence interval from 0.53 to 1.24 and p = 0.32. The interval includes no difference and allows effects in either direction, so the result remains uncertain. Secondary and safety summaries provide additional information, but interpretation is limited by missing reporting on analysis populations, missing data, multiplicity, and several design details.

The registry does not report the original sample-size justification or a complete statistical analysis plan. Planning illustrations based on the observed effects are separate from that original design and should be read only under their stated assumptions.