Randomized Translational Study to Examine the Effects of Shared Care in Management of Gestational Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Translational Study to Examine the Effects of Shared Care in Management of Gestational Diabetes (NCT01565564), a randomized na study. The primary outcome is The Rate of Macrosomia..

2. Clinical Question

The study addresses whether organizing gestational diabetes care across a local prenatal network is associated with a different frequency of macrosomia than usual care. Because the study is randomized, its intended comparison is between assigned care strategies rather than between groups formed only by participant choice. Random assignment can help make groups comparable on average, but the registry record does not describe how the sequence was generated, concealed, or implemented. Therefore, the available record alone cannot establish whether every aspect of the randomization process was protected from bias.

The primary endpoint concerns a birth outcome, measured at delivery, and is reported as the number of participants with the event. A secondary endpoint is pregnancy-induced hypertension during the period from enrolment through after delivery. These outcomes describe different aspects of pregnancy and should not be treated as interchangeable evidence. The posted results allow a statistical comparison for the named outcomes, but they do not report the broader economic or sustainability findings included in the study's stated questions.

3. Trial Design

The registry describes a completed randomized, single-masked, parallel-group study sponsored by Tianjin Women and Children's Health Center. Its title identifies a three-tier prenatal care network in Tianjin, China, and its condition is gestational diabetes mellitus. The enrollment field reports 948 participants. The registry lists the shared care and usual care arms, but the arm descriptions are blank, so the content of usual care and the practical distinction between the strategies are not reported in the registry record.

The shared care intervention is described as shared glycaemic control care within the local three-tier antenatal care network and is classified as behavioral. The record does not state which person or group was masked, or how masking was maintained. It also does not describe allocation concealment, the random sequence method, crossover or contamination, or how care was implemented across the network. These details are important for understanding the contrast participants actually received, but they are not reported in the registry record.

The primary outcome is the rate of macrosomia at the time of birth, with macrosomia defined as birthweight at least 4000 grams. The secondary outcome listed is the rate of pregnancy-induced hypertension, measured from enrolment at 24-28 gestational weeks until after delivery, an average of 12 weeks. The primary outcome counts and comparison use 361 participants in usual care and 339 in shared care; those group denominators do not account for the full enrollment figure. A participant-flow explanation, including the number randomized to each arm and any exclusions from the outcome analyses, is not reported in the registry record.

The record lists a start in 2010-09, primary completion in 2013-06, and study status as completed. It identifies two posted outcome measures and no reported analyses. The study's own planned sample-size rationale, primary analysis plan, and details of follow-up are not reported in the registry record. Thus, the registry supports a description of the broad randomized comparison and the posted endpoint counts, but not a complete reconstruction of trial conduct.

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:

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 The Rate of Macrosomia., measured over At the time of birth..

The primary endpoint is the rate of macrosomia at birth. The registry defines macrosomia as birthweight at least 4000 grams and specifies the time of birth as the measurement point. The result is presented as the number of participants meeting that definition among the participants listed in each arm. This makes the endpoint a binary outcome: each participant is either counted as having macrosomia or not counted as having it.

Birthweight is used to identify the event because it gives an operational definition that can be applied to deliveries in both randomized groups. A prespecified threshold can make outcome classification more consistent than a subjective description, although the registry record does not state who measured birthweight, how measurements were checked, or whether outcome assessors were masked. The endpoint is also clinically interpretable as an event count, but it captures only one outcome at birth and does not summarize every possible maternal or infant outcome.

The posted counts are 63 participants among 361 in usual care and 38 among 339 in shared care. The registry comparison expresses the difference as a risk difference, with the shared care arm contrasted against usual care. The estimate is negative, which indicates that the observed event frequency was lower in the shared care group in this posted comparison. This is a description of the trial's posted data, not proof that the care strategy caused the difference. The record does not provide participant-level data, the measurement procedures, or a detailed account of missing outcome data, so the endpoint result cannot by itself address those sources of uncertainty.

7. Results Posted in the Registry

• The Shared Care Arm: 11.2% (38/339) versus 17.5% (63/361) on control; risk difference -6.2 percentage points (95% CI -11.4 to -1.1), risk ratio 0.64 (0.44–0.93); unadjusted two-proportion z-test p = 0.019.

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.

The Rate of Pregnancy-induced Hypertension.

• 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:
  • The Shared Care Arm: 8.0% (27/339) versus 4.4% (16/361) on control; risk difference 3.5 percentage points (95% CI -0.0 to 7.1), risk ratio 1.80 (0.99–3.28); unadjusted two-proportion z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between The Shared Care Arm and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoint is pregnancy-induced hypertension, measured from enrolment at 24-28 gestational weeks until after delivery, an average of 12 weeks. Its comparison points in the opposite direction from the primary macrosomia estimate: the recorded event count and estimated risk difference are higher in shared care. The secondary confidence interval includes zero, and the unadjusted p-value is 0.052. This pattern is not a clear demonstration of a difference, but neither does it show that the groups are equivalent.

The primary and secondary findings address distinct outcomes. A directionally different secondary result does not erase or validate the primary finding, and the primary result does not establish a pattern across all maternal and infant outcomes. The registry lists one secondary outcome, but the study summary also names cost-effectiveness and sustainability as research questions. Results for those questions are not reported in the registry record. The posted endpoint evidence therefore covers only part of the stated research agenda.

Secondary results generally carry less confirmatory weight than a prespecified primary result, particularly when the analysis plan and hierarchy of outcomes are not available. Testing multiple outcomes can increase the chance of finding an apparently notable result by chance. Adjustments for multiplicity, a prespecified ordering of tests, or a clear exploratory designation can guide interpretation, but none is reported in the registry record. The unadjusted secondary p-value should therefore be treated as one piece of evidence rather than as a standalone conclusion.

The registry does not report whether the secondary endpoint was prespecified in a protocol, how it was measured, or whether there were additional secondary outcomes that were not posted. This limits assessment of selective reporting and the total number of comparisons considered. The secondary estimate is also subject to the same uncertainties about participant flow and analysis populations as the primary estimate. Accordingly, the overall secondary pattern is suggestive of uncertainty and differing outcome directions, not a coherent, complete account of the intervention's effects.

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

• The Rate of Pregnancy-induced Hypertension.

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: participants are counted as having macrosomia or not having macrosomia, using the registry definition of birthweight at least 4000 grams. For a binary outcome, a risk is the number of participants with the event divided by the number assessed in that group. The comparison reported is a risk difference, which subtracts the usual-care risk from the shared-care risk. A negative difference means the observed risk is lower in shared care. The record also supplies relative measures, but the main interpretation can be understood from the risk difference and the arm-specific event counts without treating any one effect scale as uniquely sufficient.

The risk difference is an absolute comparison: it describes how far apart the event frequencies are on the risk scale. A relative risk instead compares one group's risk with the other's as a ratio, and an odds ratio compares the odds of the event. These measures answer related but not identical questions, and their numerical sizes are not interchangeable. All effect measures are estimates from the observed sample. The registry's posted primary comparison is unadjusted, so it is not a model-based estimate controlling for covariates.

The unadjusted p-value assesses how compatible the observed data are with a null hypothesis of no group difference under the analysis assumptions. It does not quantify the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A small p-value can accompany a modest difference, while a larger p-value can result when an estimate is imprecise. For the primary comparison, the unadjusted p-value is 0.019. The registry does not state whether any other testing plan, adjustment, or confirmatory threshold was used.

A confidence interval gives an estimate together with a range of values that are reasonably compatible with the data under the chosen statistical method. For a risk difference, zero represents no absolute difference. If the interval crosses zero, the data do not clearly rule out no difference at the interval's confidence level. If it does not cross zero, the interval supports a difference under that method, but it does not remove the possibility of bias, confounding from implementation problems, or selective reporting. The registry does not identify the interval construction method, so interpretation should not assume a particular model beyond the posted result.

Random allocation is intended to create comparison groups that are similar on average in factors that could affect outcomes. In a well-conducted randomized study, this helps support causal interpretation of group differences. However, randomization alone does not guarantee that the groups remain comparable after assignment. Loss to follow-up, nonadherence, crossover, incomplete outcome measurement, and deviations from the analysis plan can influence results. The registry record does not report sequence generation, concealment, adherence, participant flow, or analysis population, so those protections cannot be evaluated from the posted information.

The primary comparison uses group denominators of 361 for usual care and 339 for shared care, with the event counts reported for each. A denominator matters because the same event count has a different meaning depending on how many participants were assessed. When outcomes are missing, analysis choices can also affect the comparison. For example, an analysis limited to participants with recorded outcomes may differ from an analysis that retains everyone as randomized, depending on why outcomes are missing. The registry does not report missing-data methods or explain how the listed denominators were selected. It is therefore not possible to determine whether the analysis followed an intention-to-treat principle or another population definition.

The registry identifies the trial as single-masked, but does not name who was masked. Masking can reduce the influence of expectations on care, reporting, measurement, or decisions about outcome classification, depending on who is unaware of group assignment. For a birthweight threshold outcome, an objective measurement may limit some forms of subjective assessment, but the measurement and adjudication procedures are not reported. No inference about the success or failure of masking can be made from the registry label alone.

The sample-size planning illustration uses the observed effect as its starting point. It assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is a stated fraction of the observed effect. For non-time-to-event outcomes such as these event counts, the planning values are participants per arm. The figures are illustrations based on the posted effect, not evidence about the trial's original sample-size justification. The registry does not report the original design assumptions or any prespecified target effect.

Power is the probability that a specified statistical procedure will reject its null hypothesis under a particular assumed effect and assumptions. Planning for 80% power or 90% power means selecting a sample size intended to give that probability if the assumptions are met. It does not indicate the probability that the observed result is true, nor does it describe the probability that this completed trial reached a particular conclusion. The planning illustration is sensitive to the assumed effect: detecting a smaller effect generally requires more participants, all else equal. The original trial's own power calculation is not reported in the registry record.

The secondary outcome uses the same broad binary-outcome approach, with pregnancy-induced hypertension as the event and the posted group counts as the basis of the comparison. Its unadjusted p-value and confidence interval must be read in the context of its secondary status and the lack of a reported multiplicity plan. Repeated testing across several outcomes can increase the chance of at least one apparently notable result, depending on the testing strategy. The record gives one posted secondary outcome, but does not provide a full protocol outcome list or explain whether other outcomes were measured, withheld, or analyzed. General statistical caution about multiple testing therefore applies, but the registry does not permit a definitive assessment of the full testing burden.

Over-dispersion is a concern in some statistical models when observed variability exceeds what a simple model expects. It is especially relevant to count outcomes or clustered data, where participants within a site or provider may have more similar outcomes than participants across sites. This trial involved a three-tier care network, but the registry does not report a model accounting for provider or network clustering, nor does it provide evidence that a particular over-dispersion problem occurred. This is a general consideration, not a claim that the posted estimates are known to be affected by it.

In general, an analysis plan helps readers distinguish prespecified confirmatory outcomes from exploratory analyses and understand how missing data, clustering, and multiple tests were handled. The registry record reports zero analyses and no adjusted analyses. It does not provide a protocol or statistical analysis plan. Consequently, the posted estimates can be described and their uncertainty discussed, but the analytical decisions behind them cannot be fully audited.

11. Confidence Intervals and Precision

The primary risk-difference estimate is accompanied by a confidence interval that lies entirely below zero. This direction is consistent with fewer recorded macrosomia events in shared care than in usual care. The interval also makes clear that the exact size of the difference is uncertain: an estimate is not a fixed quantity known without error, and plausible values span a range. The unadjusted p-value of 0.019 gives a related test-based summary, but it does not replace the interval or describe the clinical importance of the result.

Confidence intervals are best read as a measure of precision conditional on the statistical method and the observed data. A narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the effect's magnitude. The registry does not name the interval construction method, so the coverage properties and assumptions cannot be independently assessed from the record. Also, an interval reflects sampling uncertainty under its model; it does not include every source of uncertainty, such as outcome misclassification, incomplete follow-up, deviations from randomization, or selective outcome reporting.

For the secondary endpoint, the confidence interval includes zero and extends into positive values. This is compatible with no absolute difference and with a range of possible positive differences under the method. Its unadjusted p-value is 0.052. Neither this p-value nor the interval establishes equality between care groups. Rather, the secondary estimate is not precise enough to distinguish clearly between no difference and some effects in the positive direction.

Precision also depends on how much outcome information is available. The registry reports 361 usual-care participants and 339 shared-care participants in the primary comparison, while total enrollment is 948. The record does not explain the difference between those figures, so the effect of any missing outcomes or exclusions on precision cannot be assessed. The confidence intervals describe uncertainty in the reported comparison, not uncertainty arising from unreported participant flow or choices made during analysis.

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 planning values are participants per arm, not total events. They concern the binary outcomes in this study and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is expressed as a fraction of the observed effect. The planning entries distinguish assumptions based on 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect.

The 80% power column gives the number of participants per arm intended to provide an 80% chance of detecting the assumed effect if the planning assumptions hold. The 90% power column gives the number per arm intended to provide a 90% chance under those same assumptions. These are design calculations, not probabilities that the trial's result is correct or that a treatment has a particular effect. This is not observed power.

Because smaller effects are harder to distinguish from random variation, the planning figures increase as the assumed effect becomes smaller. The illustration starts from the effect observed in this study, so it is not independent evidence that the effect is reproducible or a suitable target for a future study. In particular, an observed effect can be unstable, and a planning result based on it may give an overly optimistic impression if the observed difference is larger than the underlying effect.

The registry does not report the trial's own original sample-size calculation, its design target, or the effect size used when enrollment was planned. These planning values should therefore be read as hypothetical illustrations of sample-size requirements under the stated assumptions, not as an explanation of why the trial enrolled 948 participants. The sample-size calculation also does not resolve missing-data, allocation, masking, or multiplicity concerns.

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 = 0.175; treatment proportion p₁ = 0.112; average p̄ = 0.143.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4955 = 0.9712.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4935 = 0.4154.
4. n = (0.9712 + 0.4154)² / (-0.0624)² = 493.4, rounded up to 494 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 <- 0.174515235457064                          # control proportion
p1 <- 0.112094395280236                          # 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(1565564)
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 = 494 (80% power), 661 (90% power)
 75% of observed effect: n per arm = 918 (80% power), 1,228 (90% power)
 50% of observed effect: n per arm = 2,153 (80% power), 2,882 (90% power)
power.prop.test: 493.4 
Simulated power at n = 494 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators test more than one outcome, comparison, subgroup, or time point. Even if every test is conducted correctly, a larger set of tests increases the chance that at least one result will appear statistically notable by chance. Approaches such as adjusting significance thresholds, defining a hierarchy, or labeling analyses exploratory can help readers interpret this issue. The registry record does not report a multiplicity strategy, a testing hierarchy, or a statistical analysis plan.

The record identifies the macrosomia rate as primary and pregnancy-induced hypertension as secondary. It also lists cost-effectiveness and sustainability among the study's research questions, but results for those questions are not reported in the registry record. Because the full protocol outcome list and analysis plan are unavailable, it is not possible to determine how many outcomes, subgroups, or time points were examined or whether the posted results represent all planned analyses. The secondary p-value is unadjusted, so it should not be interpreted as if the registry had documented control of the overall false-positive risk.

Missing-data handling is also not reported in the registry record. Enrollment is listed as 948, while the primary outcome comparison has arm denominators of 361 and 339. The registry does not explain the participant flow, whether all randomized participants were included, why denominators differ from enrollment, or whether any outcome values were unavailable. It gives no imputation method, missingness assumption, or sensitivity analysis. Without this information, the influence of missing outcomes on the estimated group differences cannot be evaluated.

The analysis populations are not reported in the registry record. It is therefore unclear whether estimates are based on all participants as randomized, participants who received assigned care, or participants with observed outcomes. Those populations answer different questions when adherence, crossover, or follow-up is incomplete. No adjusted analyses are posted, and no subgroup analyses are reported. The absence of reported analyses does not establish that no analyses were conducted; it means their methods and results are not available in the registry record.

The registry labels the study single-masked but does not identify the masked party or explain the process. The randomization method and allocation concealment are not reported either. These omissions do not show that the methods were inadequate, but they prevent readers from judging how well bias was controlled. The record also does not report interim analyses, stopping rules, or monitoring plans, so those features cannot be assessed.

15. Safety Results

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

Other (non-serious) adverse events

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

The adverse-event record lists zero serious adverse events and zero other adverse events in each of its two groups. It lists 361 participants at risk for each category in the shared care group and 339 in the usual care group. These group denominators are reversed relative to the arm denominators in the posted primary outcome comparison. The registry does not explain this difference, so it should not be assumed to reflect the same analysis population or participant accounting.

The zero entries describe what was recorded in the adverse-event fields; they do not prove that no events occurred outside the registry's reporting process. The record does not provide definitions, collection procedures, surveillance duration, or a narrative about how adverse events were assessed. Death counts are not reported in the registry record. No serious-event terms are listed.

Safety interpretation therefore needs to remain narrow. The posted fields contain zero reported serious and other adverse events, but the details needed to assess completeness and ascertainment are absent. These entries cannot establish the absence of risk, and they should not be used to make a clinical recommendation. They are limited registry reporting, not a comprehensive safety evaluation.

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

The posted primary comparison shows fewer recorded macrosomia events in the shared care arm than in the usual care arm, and the unadjusted confidence interval excludes no difference. This is evidence of a difference in the recorded outcome under the analysis reported in the registry. It is not, by itself, proof that shared care caused the difference. Causal interpretation also depends on the conduct of randomization, follow-up, adherence, outcome ascertainment, and analysis choices, several of which are not described in the registry record.

The result does not establish how large a difference would matter in practice. Statistical evidence and practical importance are separate questions: the former concerns how compatible the observed data are with a null comparison under a method, while the latter depends on the value placed on the outcome and the broader context of care. The registry does not report an interpretation threshold for clinical importance, a formal economic analysis, or participant and clinician perspectives.

The secondary pregnancy-induced hypertension comparison is uncertain and points in a different direction. It does not establish that shared care increases that outcome, nor does it establish that there is no difference. The result has an unadjusted p-value and confidence interval that should be interpreted in light of its secondary status and the absence of a reported multiplicity plan. Neither endpoint alone represents the total balance of possible benefits and harms.

The findings also cannot be generalized automatically to settings outside the studied three-tier prenatal care network in Tianjin, China. The record does not describe participant characteristics, care implementation, or the usual-care services in enough detail to judge similarity to other populations and systems. Results for cost-effectiveness and sustainability are not reported in the registry record, despite being named as research questions. Those questions cannot be answered from the posted birth outcome counts.

Finally, the enrollment and outcome denominators are not reconciled, analysis populations are not identified, and missing-data methods are not reported. These gaps limit confidence in how completely the posted estimates represent all randomized participants. The appropriate reading is therefore specific: the registry reports an unadjusted primary outcome difference in the observed comparison, with meaningful uncertainty about its magnitude and important unanswered questions about study conduct and analysis.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares a care-delivery strategy with usual care using random allocation and a binary birth outcome. The registry provides event counts by arm and a risk-difference comparison, allowing readers to see both the observed data and an estimate of the absolute group contrast. Reporting counts alongside an effect estimate is valuable because the estimate's interpretation depends on the number of participants assessed and the number with the event.

The study also illustrates why a point estimate and a p-value are not enough. The primary estimate has an interval that excludes zero, but its precise magnitude remains uncertain. The secondary comparison is less decisive and points in the opposite direction. Considering both outcomes prevents an overly simple interpretation based on only one statistic. It also highlights why endpoint hierarchy and multiplicity plans matter when a study reports more than one outcome.

The record's limitations are statistically important as well. The enrollment figure and arm-specific outcome denominators are not reconciled, and the analysis populations, missing-data procedures, and adjustment plan are not reported. A reader can interpret the posted comparison, but cannot fully assess whether all randomized participants contributed, how incomplete data were handled, or whether the analysis followed a prespecified plan. Transparency about those items is central to evaluating the reliability of randomized trial estimates.

Finally, the sample-size illustration demonstrates the dependence of planning on the assumed effect. A smaller target difference requires more participants under otherwise similar assumptions. Because the illustration is based on the observed result rather than a documented original target, it is useful as a planning scenario but not as evidence about the trial's design rationale. Overall, the trial is a useful example of how registry results can offer a statistical signal while leaving key design and analysis questions unresolved.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record gives a broad description of the study but not enough detail to assess several features that affect interpretation. The shared care intervention is named, but its activities, delivery, duration, provider roles, and adherence measures are not described. Usual care has no arm description. Without these details, the care contrast cannot be reproduced or compared reliably with other health systems.

Randomization is recorded, but the method of sequence generation and allocation concealment is not reported in the registry record. Although the design is labeled single-masked, the masked party and procedures are not identified. The record does not explain who measured birthweight, how the threshold was applied, or whether outcome assessment was masked. These omissions limit assessment of possible selection and measurement bias.

The enrollment field reports 948, while the endpoint groups include 361 usual-care participants and 339 shared-care participants. No participant-flow account explains these denominators or reports reasons for non-inclusion. Missing-data handling and analysis population are not reported. As a result, it is not possible to determine whether the reported results reflect all participants as randomized or a subset with available outcomes.

The posted statistical analysis is unadjusted, and no analysis plan, covariate strategy, multiplicity approach, or sensitivity analysis is reported. The registry provides no information on whether network or provider clustering was considered. This is relevant in general when care is delivered through an organized network, but the record does not establish whether clustering affected the results. It also does not report interim analyses or stopping rules.

Only one secondary outcome result is posted, while the study summary also names cost-effectiveness and sustainability as research questions. Their results and methods are not reported in the registry record. The posted safety entries contain zero recorded events, but the adverse-event assessment procedures and death counts are not reported. These gaps mean that the outcome comparison is more fully described numerically than it is methodologically. They do not demonstrate that the study was improperly conducted; they restrict what can be independently evaluated from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Translational Study to Examine the Effects of Shared Care in Management of Gestational Diabetes — NCT01565564.
• Registry record last updated 2015-07-07; status last verified 2015-06.
• Results first posted 2015-06-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed, randomized, single-masked, parallel-group study of shared care versus usual care for gestational diabetes mellitus in a three-tier prenatal care network in Tianjin, China. The enrollment field is 948, and the sponsor is Tianjin Women and Children's Health Center. The primary endpoint is macrosomia at birth, defined as birthweight at least 4000 grams.

The primary comparison reports 63 events among 361 participants in usual care and 38 among 339 in shared care. Its risk-difference estimate is negative, and the unadjusted p-value is 0.019. The listed secondary outcome is pregnancy-induced hypertension; its unadjusted p-value is 0.052, and its estimate points in the opposite direction. The registry also lists cost-effectiveness and sustainability as research questions, but results for those questions are not reported in the registry record.

The record does not report the original sample-size rationale, analysis populations, missing-data methods, multiplicity plan, or a detailed participant-flow account. Thus, the posted estimates can be described, but important aspects of trial conduct and analysis remain unclear.