Efficacy Assessment of Systematic Treatment With Folinic Acid and Thyroid Hormone on Psychomotor Development of Down Syndrome Young Children: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy Assessment of Systematic Treatment With Folinic Acid and Thyroid Hormone on Psychomotor Development of Down Syndrome Young Children (NCT01576705), a randomized phase 3 study. The primary outcome is GMDS (Griffiths Mental Development Scale).

2. Clinical Question

The study also set out to assess whether thyroid hormone and folinic acid had an interaction. That question is distinct from comparing each treatment combination with the reference group: an interaction asks whether the effect associated with one treatment differs according to whether the other treatment is given. The registry record does not report an interaction estimate or a formal interaction analysis.

The primary outcome description gives an expected six points difference in GDQ between any of the three treatment groups. That is a stated expectation, not an observed treatment effect. The posted group summaries instead give mean GDQ values at the 12-month timeframe, and the available unadjusted comparisons estimate differences in those means against the reference group. They do not supply the adjusted change-from-baseline results specified in the primary-analysis description.

Accordingly, the clinical question can be framed from the protocol description, but the posted results answer it only partially. They show the arm-level 12-month means and their unadjusted contrasts; an adjusted estimate of change from baseline and the treatment-interaction result are not reported in the registry record.

3. Trial Design

The registry identifies this as a phase 3, randomized, quadruple-masked, parallel-group study. It lists Institut Jerome Lejeune as the sponsor, an enrollment of 175, and a completed status. The recorded start date is 2012-04-02 and the primary completion date is 2017-12-14. These registry entries describe the trial’s design and status, not the extent to which masking was maintained or the completeness of follow-up.

The listed treatments form combinations of thyroxin and folinic acid, with placebo versions of either or both. This arrangement is relevant to the stated aim of examining each treatment and any interaction between them. The registry arm descriptions themselves are empty, so details beyond the arm names and treatment summary are not reported in the registry record. The posted primary outcome summaries include four arm labels, while the listed outcome group sizes differ by arm.

Random allocation supports a comparison of assigned groups, but the record does not report the randomization method, allocation-concealment procedures, stratification factors, or the methods used to preserve masking. Those details are not reported in the registry record. Nor does the record explain whether the analysis followed an intention-to-treat principle, how participants were handled after treatment discontinuation, or how missing outcome measurements were addressed.

The primary outcome was scheduled for assessment at 12 months. The primary-analysis description specifies adjusted change from baseline in GDQ and ANCOVA adjusted for covariates. The registry’s posted analysis count is 0, and no reported primary analyses are listed. The record therefore does not provide the adjusted model estimates, its covariates, or the analysis population used. The group means and unadjusted comparisons available for interpretation should not be mistaken for a complete report of the prespecified primary analysis.

These features make the record useful for understanding the trial question, allocation structure, masking label, and outcome timing. They also set limits on interpretation: the registry does not give enough detail to assess all operational design decisions or to reconstruct the planned adjusted analysis.

4. Participant Flow and Accounting

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

Before assignment: As recruitment was nationwide and patients were included at a single centre, screening and randomisation were performed on the same day to minimise visits to the centre. Eligibility of randomised patients for TSH levels per exclusion criterion #8 was thus confirmed retrospectively, and patients with high TSH levels were discontinued.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The main analysis of the primary efficacy endpoint is the adjusted change from baseline in GDQ derived from the Griffith Mental Development Scales (GMDS) at 12 months analysed by ANCOVA adjusted for covariates. Expected Outcome : six points difference in GDQ between any of the three treatment group compared to placebo at 12 months from baseline.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The modified intention-to-treat (mITT) population included all randomized patients who did not prematurely discontinue due to elevated baseline thyroid stimulating hormone (TSH)

6. Primary Endpoint

The registry lists the primary outcome as GMDS (Griffiths Mental Development Scale), measured over 12 months.

The primary endpoint is the General Development Quotient derived from the Griffiths Mental Development Scale (GMDS), measured at 12 months. The GMDS is described as an assessment of psychomotor development from birth to 2 years, using subscales for locomotor, personal-social, hearing and language, eye-hand coordination, and performance domains. The record says that raw scores from contributing items are used to derive subscale and total scores, which are then converted to development age and quotient measures.

The registry notes that the standard quotient tables have a floor at 50, which may make them unsuitable for children with delayed development, including children with Down syndrome. It therefore describes deriving quotients from development age relative to chronological age, with correction for gestational term for preterm infants. Higher quotient scores are described as indicating better psychomotor development. The endpoint unit is listed as developpement quotient, and the group results are reported as means with standard deviations.

A development quotient provides a continuous measure, so the analysis can compare average scores between assigned groups rather than reducing the outcome to a binary category. The protocol description identifies change from baseline as the primary analysis measure, which would account for starting scores in the adjusted comparison. However, the posted outcome summaries give means at 12 months, not adjusted change-from-baseline estimates. The distinction matters: endpoint means describe the observed score distribution, while adjusted change estimates address the specified primary question using baseline and covariate information.

7. Results Posted in the Registry

• Thyroxin + Folinic Acid: mean 51.96 versus 51.27 on control; difference 0.69 (95% CI -2.61 to 3.99), standardized effect d = 0.10; z-test p = 0.682.
• Thyroxin Placebo+ Folinic Acid: mean 51.66 versus 51.27 on control; difference 0.39 (95% CI -2.74 to 3.52), standardized effect d = 0.06; z-test p = 0.807.
• Thyroxin Placebo+ Folinic Acid Placebo: mean 51.67 versus 51.27 on control; difference 0.40 (95% CI -2.92 to 3.72), standardized effect d = 0.05; z-test p = 0.814.

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.

BL (Brunet Lezine Revised Scale)

• 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:
  • Thyroxin + Folinic Acid: mean 51.18 versus 50.64 on control; difference 0.54 (95% CI -2.73 to 3.81), standardized effect d = 0.08; z-test p = 0.746.
  • Thyroxin Placebo+ Folinic Acid: mean 51.24 versus 50.64 on control; difference 0.60 (95% CI -2.73 to 3.93), standardized effect d = 0.09; z-test p = 0.724.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Thyroxin + Folinic Acid and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Thyroxin Placebo+ Folinic Acid and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome, the Brunet Lezine Revised Scale, measured at 12 months. Its group means and unadjusted contrasts show a pattern broadly similar to the primary outcome: the arm averages are close together, and the reported comparison intervals include zero. This offers a second descriptive view of development scores, but it does not provide an independent resolution of the primary question.

The primary and secondary outcomes are both continuous measures of development, and their similar overall pattern may be viewed as consistency in the posted summaries. However, they are not interchangeable measures, and the registry does not report a formal joint analysis or a model comparing treatment effects across outcomes. The secondary outcome therefore cannot fill the gap left by the absent adjusted primary analysis. Nor does the pattern establish that the treatments have no effect or that the outcomes are equivalent across groups.

Unadjusted secondary findings generally carry less confirmatory weight than a prespecified primary analysis, especially when the number of comparisons and the multiplicity strategy are unclear. Testing multiple outcomes and treatment contrasts can make isolated p-values appear persuasive by chance. The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or the analysis plan for the secondary endpoint. It lists no reported analyses for that outcome, despite posting group summaries and comparisons.

The appropriate reading is therefore contextual: the secondary summaries do not visibly contradict the overall pattern in the primary summaries, but they do not supply the missing adjusted result, establish an interaction, or independently prove a treatment effect. Their main value is to show that the available descriptive results are not limited to a single development measure, while their inferential limitations remain substantial.

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

• BL (Brunet Lezine Revised Scale)

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is continuous and reported as a mean with a standard deviation. A mean describes the group’s average score, while the standard deviation describes variation among individual scores around that average. The standard deviation is not the uncertainty in the estimated mean; the latter depends on both variability and the number of observations contributing to the estimate. The registry lists arm-level group sizes and standard deviations, allowing unadjusted mean contrasts and their uncertainty to be presented.

What does an unadjusted mean difference represent?

An unadjusted mean difference is the arithmetic contrast between the average outcome in one group and the average in its reference group, without controlling for baseline scores or other covariates. A positive estimate means the first named group’s mean is higher on the reported scale; a negative estimate would mean it is lower. Because the registry describes higher GDQ scores as better psychomotor development, the direction can be interpreted on that scale, but a difference alone does not establish a causal or clinically meaningful effect.

The posted primary comparisons use Thyroxin+Folinic Acid Placebo as the reference. They are not the adjusted ANCOVA comparisons called for in the primary-analysis description. In a randomized trial, unadjusted contrasts can be informative, but adjustment may improve precision and account for baseline outcome values or other specified covariates. The record does not identify the covariates for the planned ANCOVA and does not report its estimates, so its adjusted result cannot be inferred from the summaries.

Why does the confidence interval matter alongside the p-value?

A confidence interval gives a range of effect estimates compatible with the observed data under the statistical model and its assumptions. It conveys the direction and precision of an estimate more directly than a p-value alone. A p-value measures how unusual the data, or data more extreme, would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect.

For the posted mean comparisons, each confidence interval spans zero. That means the results do not distinguish the estimate from zero at the confidence level used, but it does not prove there is no difference. The extent of the interval is also important: a range can include both small differences and larger differences, leaving uncertainty even when the point estimate is near zero. The reported p-values are unadjusted and should not be interpreted as controlling the chance of false-positive findings across all comparisons.

What would ANCOVA add?

Analysis of covariance (ANCOVA) models the outcome while adjusting for selected covariates. For a change-from-baseline endpoint, baseline score is relevant because people can start at different levels, and starting values may be associated with follow-up scores. An adjusted analysis can estimate a treatment contrast conditional on the variables included in the model. Its validity and interpretation depend on the chosen variables, the model specification, and the assumptions behind the analysis. The record names ANCOVA adjusted for covariates but does not report which covariates were used, model diagnostics, or adjusted estimates.

Adjustment is not automatically a guarantee of a more reliable result. A poorly specified model or inappropriate adjustment can create problems, while a prespecified and suitable adjustment may improve precision. Because the registry does not report the model details or results, it is not possible to assess how the adjusted primary analysis compares with the simple unadjusted group summaries.

How should the factorial treatment question be understood?

The treatment combinations allow consideration of thyroxin, folinic acid, and whether the treatments interact. An interaction means that the contrast associated with one treatment changes depending on whether the other treatment is present. Separate comparisons of each combination against one reference group do not, by themselves, provide a formal interaction test. The registry’s stated aim includes assessing any interaction, but no interaction estimate or test is reported in the registry record. Therefore, the posted contrasts should not be treated as a direct answer to that part of the question.

The same distinction applies to the three reported contrasts: each is a comparison with the reference group, and none is a direct test of every possible difference between active combinations. A full analysis of the treatment structure would need to make clear which main effects and interaction terms were specified and how they were estimated. Those details are not reported in the registry record.

What is the role of secondary outcomes and multiplicity?

The registry lists the Brunet Lezine Revised Scale as a secondary continuous outcome at 12 months. When several outcomes or contrasts are tested, the chance of at least one apparently unusual result can increase if each test is interpreted without accounting for the family of tests. Procedures for controlling multiplicity can address that issue, but they may affect confidence intervals or significance thresholds. No multiplicity strategy is reported in the registry record. Secondary comparisons are consequently best read as supportive or exploratory context, rather than as independent confirmatory evidence.

The record reports no secondary analyses, even though it posts secondary outcome summaries and unadjusted comparisons. This distinction means the summaries are available, but a formal analysis plan, adjusted estimates, and multiplicity-aware inference are not. The registry does not provide enough information to determine how the secondary results were selected or prioritized.

Finally, the registry does not report missing-data methods, analysis populations, or an interim-analysis plan. These matters can affect estimates and uncertainty, particularly when outcomes are not observed for all randomized participants. They cannot be reconstructed from group means and standard deviations alone. The numerical summaries therefore support a limited interpretation of observed arm-level outcomes, not a complete appraisal of the intended statistical analysis.

11. Confidence Intervals and Precision

The primary mean-difference estimates are close to zero, but precision is better judged from their confidence intervals than from the point estimates alone. For Thyroxin + Folinic Acid versus Thyroxin+Folinic Acid Placebo, the estimate is 0.69 and the 95% confidence interval extends from -2.609 to 3.989. For Thyroxin Placebo+ Folinic Acid, the estimate is 0.39, with an interval from -2.741 to 3.521. For Thyroxin Placebo+ Folinic Acid Placebo, the estimate is 0.4, with an interval from -2.924 to 3.724. All three intervals include zero and allow for differences in either direction.

A confidence interval is not a list of values that are equally likely, nor does it guarantee that the true effect lies inside it. In general, it describes the range of values compatible with the data and the model at the stated confidence level. Wider intervals indicate less precision; narrower intervals indicate greater precision. Whether an interval is sufficiently narrow depends on what range of effects would matter for the scientific question, and the registry does not report a threshold for interpreting the intervals.

The intervals should be read as uncertainty around unadjusted comparisons based on the posted summary statistics, rather than as the result of the specified covariate-adjusted ANCOVA. The adjusted analysis is not reported in the registry record. The intervals also do not account for an unreported multiplicity strategy, and the p-values are unadjusted. These qualifications limit what can be concluded from nominal interval coverage and individual p-values.

The similar scale of the estimates and intervals across the primary comparisons conveys that the posted data do not sharply separate the groups. It does not establish equivalence, exclude all meaningful differences, or answer the interaction question. Precision is about how tightly an effect is estimated; absence of a statistically significant result is not, on its own, evidence of precise 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 participants per arm, not total participants, and the sample-size assumptions describe an illustrative calculation rather than the trial’s original design. The calculation uses a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that would yield an 80% probability of detecting the selected effect under the calculation’s assumptions, if that effect were present. The 90% power column uses a higher target probability of detection and therefore requires more participants under the same assumptions. These are planning quantities, not guarantees about what a future study would observe. The figures are based on each observed comparison separately, so they should not be read as one sample-size recommendation for the whole treatment structure.

The rows use the observed effect and smaller fractions of it. Smaller effects are harder to distinguish from random variation, so they require more participants to reach the same target power under otherwise unchanged assumptions. This pattern is a general feature of statistical planning, not evidence that the smaller effect is more likely or clinically important. The sample-size figures are planning illustrations and are not observed power.

Because the input effects come from the posted unadjusted comparisons, these illustrations inherit uncertainty in those estimates. They also rely on the stated equal-allocation and normal-approximation assumptions; they do not account for unreported design features such as covariate adjustment, missing outcomes, or multiplicity. The figures can help readers understand how the required sample size changes with the assumed effect and target power, but they do not substitute for the trial’s own design rationale or a prospective planning analysis.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = 0.690; pooled standard deviation σ = 7.243.
2. n = 2 × (1.96 + 0.842)² × 7.243² / 0.690² = 1,729.9, rounded up to 1,730 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.689999999999998                      # observed difference in means
sigma <- 7.24341993773426                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1576705)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,730 (80% power), 2,316 (90% power)
 75% of observed effect: n per arm = 3,076 (80% power), 4,118 (90% power)
 50% of observed effect: n per arm = 6,920 (80% power), 9,264 (90% power)
power.t.test: 1730.9 
Simulated power at n = 1,730 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The trial’s stated questions involve more than one treatment component, an assessment of possible interaction, and a primary and secondary development outcome. Each additional outcome, contrast, or analysis can create another opportunity for a nominally unusual result. When many hypotheses are examined, unadjusted p-values do not control the overall false-positive risk across the family of tests. A prespecified multiplicity strategy can define which comparisons are confirmatory and how inference is adjusted, but no such strategy is reported in the registry record.

The primary outcome description specifies an adjusted change from baseline in GDQ analyzed by ANCOVA with covariates. The posted comparisons, however, are unadjusted mean contrasts against one reference group, and the registry does not provide the adjusted primary estimates or identify the covariates. There is no reported formal test of the treatment interaction, although interaction is part of the stated study objective. This makes it difficult to assess whether the available comparisons correspond to the principal hypotheses or how they fit together.

Missing-data handling is also not reported in the registry record. The record does not state how missing 12-month measurements, withdrawal, or incomplete treatment were addressed, whether any imputation was used, or how sensitivity analyses were conducted. Group summaries alone do not reveal whether all randomized participants contributed outcome data or whether missingness could have affected the estimates.

The analysis populations are not reported. It is therefore unclear whether the results were based on all randomized participants, participants who received treatment, participants with observed outcomes, or another defined population. The registry also does not report an interim-analysis plan or stopping rules; their absence from the record should not be taken as evidence that such procedures were or were not used.

These omissions do not invalidate the posted summaries, but they limit their interpretation as confirmatory evidence. Without analysis populations, missing-data methods, multiplicity procedures, and the adjusted primary model results, readers cannot fully assess whether the reported contrasts align with the planned analysis or how robust conclusions would be to alternative analytic choices.

15. 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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infections and infestations (11.4%), respiratory, thoracic and mediastinal disorders (9.3%), general disorders and administration site conditions (4.7%), metabolism and nutrition disorders (4.5%), surgical and medical procedures (4.5%).

The registry reports serious adverse events by treatment group, giving the number at risk and the number affected. The affected counts are 9 of 44 for Thyroxin+Folinic Acid Placebo, 8 of 43 for Thyroxin + Folinic Acid, 8 of 43 for Thyroxin Placebo+ Folinic Acid, and 5 of 44 for Thyroxin Placebo+ Folinic Acid Placebo. Deaths are reported as 1 in the Thyroxin + Folinic Acid group and 0 in each of the other listed groups. These are descriptive counts; they do not establish that an event was caused by a treatment.

The registry also lists serious-event categories and percentages, including infections and infestations at 11.4% and respiratory, thoracic and mediastinal disorders at 9.3%. Such category summaries describe the reported event coding and should not be read as treatment-specific risks unless a group-specific comparison is reported. No inferential safety comparisons are listed.

Other adverse events affected 7 participants in the Thyroxin Placebo+ Folinic Acid group and 0 in each other group as posted. The record does not provide enough information to assess event timing, severity beyond the serious-event classification, attribution, exposure duration, or completeness of reporting. Safety counts should be interpreted as registry summaries, not as a stand-alone causal comparison or a clinical recommendation.

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

The registry supports a limited conclusion about the posted 12-month scores: mean GDQ values are similar across the listed treatment groups, and the unadjusted comparison intervals include zero. The estimates do not show a clear separation from the reference group in these summaries. At the same time, the intervals allow for differences in either direction, so the results do not establish that the groups are equivalent or that any treatment has no effect.

The record’s stated primary analysis is an adjusted change from baseline in GDQ using ANCOVA. That result is not reported in the registry record. The observed endpoint means and unadjusted mean differences cannot be substituted for that planned analysis, and they do not show whether adjustment for baseline and covariates would alter the estimates. The record also does not report a formal test of interaction between thyroid hormone and folinic acid, despite listing interaction as a study objective.

The numerical expectation of six points difference in GDQ appears in the primary outcome description as an expected outcome. It should not be confused with an observed estimate. The posted comparisons are substantially more modest as point estimates, but the confidence intervals still cover a range of possible effects. Without a reported interpretation threshold, the registry does not establish which differences would be clinically meaningful.

Similar patterns in the secondary development measure provide descriptive context, not proof of no effect. Unadjusted secondary comparisons carry less confirmatory weight when multiplicity procedures and a formal secondary analysis plan are not reported. Likewise, the adverse-event counts describe what the registry records but do not establish treatment causation.

In general, a non-significant comparison is not evidence of equivalence. Demonstrating equivalence or non-inferiority requires a prespecified margin and an analysis designed for that purpose; neither is reported in the registry record. The results can be described as inconclusive with respect to precise treatment differences in the adjusted primary endpoint, because that analysis is missing and the available unadjusted intervals retain uncertainty.

These findings should be understood as a statistical reading of registry results, not as medical advice. They do not determine what treatment is appropriate for an individual child. The record’s incomplete analytic reporting limits how far its posted results can support broader claims.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its treatment question concerns two treatment components and whether their effects may interact. In that setting, comparisons against a shared reference group are not the whole analysis: a formal interaction estimate is needed to assess whether the association with one component depends on the other. Although interaction is part of the stated objective, the registry does not report that analysis. This illustrates why the structure of the clinical question should guide the statistical contrasts reported.

The study also highlights the difference between an endpoint summary and a primary estimand. The record specifies adjusted change from baseline in GDQ as the primary analysis, but posts 12-month arm means and unadjusted comparisons without the adjusted model result. These quantities answer related but distinct questions. Reporting the prespecified adjusted estimate, its uncertainty, and the analysis population would make the evidence easier to evaluate.

Precision matters as much as direction. The unadjusted point estimates are near zero, but their confidence intervals allow a range of effects. A non-significant p-value alone cannot distinguish a precise estimate near no difference from an imprecise estimate that remains compatible with potentially relevant differences. Readers need both estimates and intervals, alongside a prespecified account of what effect sizes would matter.

Finally, the record underscores the importance of transparent reporting on multiplicity, missing outcomes, and analysis populations. These details affect how much weight to give a collection of outcome comparisons and how robust the results may be. The posted information offers useful descriptive statistics, but fuller reporting of the planned analyses would be needed for a more complete statistical assessment.

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.

Several limitations are specific to the available registry record. The primary analysis is described as adjusted change from baseline in GDQ using ANCOVA, but only 12-month group means and unadjusted comparisons are posted. The adjusted estimates, covariates, and model details are not reported in the registry record, so the stated primary analysis cannot be evaluated from the posted summaries.

The record identifies an aim to assess interaction between thyroxin and folinic acid but does not post an interaction estimate or test. Comparisons against a shared reference group do not answer that question by themselves. The registry also does not report a multiplicity procedure for the primary contrasts and the secondary endpoint, which limits confirmatory interpretation of individual p-values.

Analysis populations and missing-data methods are not reported. The group summaries therefore do not make clear how many randomized participants contributed outcome measurements in each analysis, how missing follow-up was handled, or whether sensitivity analyses were performed. The empty arm descriptions provide no further detail on treatment implementation beyond the intervention names and summary.

The registry lists quadruple masking but does not describe who was masked or how masking was maintained. It also does not report the randomization procedure, allocation concealment, interim analyses, or the original sample-size justification. These are reporting gaps, not evidence that particular procedures were absent.

Finally, the available safety summaries are counts and category percentages, without reported causal assessments or inferential comparisons. The posted results consequently support descriptive interpretation, but not a comprehensive evaluation of the treatment effects, safety differences, or robustness of the planned analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy Assessment of Systematic Treatment With Folinic Acid and Thyroid Hormone on Psychomotor Development of Down Syndrome Young Children — NCT01576705.
• Registry record last updated 2020-05-13; status last verified 2019-12.
• Results first posted 2020-05-13.
• 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 completed phase 3 registry record describes a randomized, quadruple-masked, parallel-group study in young children with Down syndrome, with enrollment of 175. It evaluates thyroid hormone and folinic acid, separately and in combination, with psychomotor development assessed at 12 months.

The primary outcome is GDQ from the Griffiths Mental Development Scale. The record specifies adjusted change from baseline using ANCOVA, but does not report that analysis. Posted unadjusted mean comparisons show similar group averages, with confidence intervals that include zero and leave uncertainty about possible differences. A secondary development measure shows a broadly similar descriptive pattern. The formal treatment-interaction result, multiplicity approach, analysis populations, and missing-data methods are not reported in the registry record.

Serious adverse-event counts and category summaries are also posted. They should be read descriptively and do not establish treatment causation. Overall, the registry provides useful outcome summaries but not the full adjusted primary analysis or several details needed for a complete assessment of the trial’s statistical evidence.