Aspirin Supplementation for Pregnancy Indicated Risk Reduction In Nulliparas (ASPIRIN): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Aspirin Supplementation for Pregnancy Indicated Risk Reduction In Nulliparas (ASPIRIN) (NCT02409680), a randomized na study. The primary outcome is Incidence of Preterm Birth.

2. Clinical Question

The registry describes the study as a randomized, double-masked, parallel-group trial. Its stated motivation was to test the possibility that low-dose aspirin could reduce preterm birth in a properly designed randomized trial. The registry also describes the intended research setting as racially, ethnically and geographically diverse, but actual participant characteristics by race, ethnicity or location are not reported in the registry record.

The primary comparison is between the intervention and placebo groups, rather than a comparison of participants who did and did not choose to take aspirin. Random allocation is intended to make the groups comparable on average at the point of assignment. The posted outcome data can therefore be read as a comparison of the groups assigned to each regimen, subject to the registry’s qualification that reported mITT counts reflect available data. Adherence and treatment received are not reported in the registry record.

3. Trial Design

The registry identifies this study as randomized, double-masked and parallel-group. Participants were assigned to low-dose aspirin or an identical-appearing placebo. The planned regimen was daily 81 mg aspirin or placebo, beginning between 6 0/7 weeks and 13 6/7 weeks of gestational age and continuing until 36 0/7 weeks of gestational age or delivery. The registry lists the phase as NA.

Enrollment was 11976. The study start date is recorded as 2016-03-23, primary completion as 2019-04-11, and status as completed. The sponsor is NICHD Global Network for Women's and Children's Health. The registry lists premature birth as the condition and identifies nulliparas in the trial title. Detailed eligibility criteria and the operational definition of nulliparity are not reported in the registry record.

The primary outcome analysis is described as modified intention-to-treat. The posted primary outcome counts are 668 among 5780.0 participants in the intervention arm and 754 among 5764.0 participants in the placebo arm. The registry cautions that available-data counts do not always represent the total population defined in the mITT group. Reasons for missing outcome data and the handling of missing observations are not reported in the registry record.

The record lists 18 outcome measures and 17 analyses. Three secondary outcomes are posted: hypertensive disorders of pregnancy, small for gestational age, and perinatal mortality. The registry record does not report the original sample-size justification, the planned statistical analysis protocol, interim analyses, allocation concealment procedures, or details of how masking was maintained. Those details should not be inferred from the randomized and double-masked labels.

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: Participants were randomly assigned (1:1, stratified by site) to receive aspirin or placebo tablets of identical appearance, via a sequence generated centrally by the data coordinating center.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified ITT; numbers reported reflect available data and therefore do not always reflect the total population defined in the mITT

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: Women who were eligible according to the modified intention-to-treat (mITT) criteria and included in the mITT analysis.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Preterm Birth, measured over At delivery.

The primary endpoint is the incidence of preterm birth, counted as participants with an event. The registry defines an event as delivery at or after 20 0/7 weeks and prior to 37 0/7 weeks. Classification is based on the actual delivery date in comparison with the projected estimated due date, without distinguishing whether a preterm delivery was indicated or spontaneous. The listed timeframe is at delivery.

This endpoint addresses the trial’s stated research question directly: whether assignment to low-dose aspirin or placebo differs in the occurrence of preterm birth. Counting participants with an event makes the outcome binary for each participant: the defined event either occurred or did not occur within the endpoint definition. The posted counts can then be compared between the randomized groups.

As a general statistical point, a clearly defined primary endpoint focuses the main trial comparison on a specific outcome and timeframe. It helps distinguish the central question from secondary outcomes, which may address related but different events. The registry’s definition also matters for interpretation: the primary outcome includes both indicated and spontaneous preterm delivery and uses the stated gestational-age boundaries. Results for a differently defined endpoint would not necessarily answer the same question.

The registry identifies the analysis population as modified intention-to-treat and notes that counts reflect available data. Thus, the denominator attached to the posted outcome is the number with available data in the relevant arm, not necessarily every participant in the population defined by the mITT description. Further details about missing observations and the mITT rules are not reported in the registry record.

7. Results Posted in the Registry

• Intervention Arm: 11.6% (668/5780) versus 13.1% (754/5764) on control; risk difference -1.5 percentage points (95% CI -2.7 to -0.3), risk ratio 0.88 (0.80–0.97); unadjusted two-proportion z-test p = 0.013.

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.

Incidence of Hypertensive Disorders of Pregnancy

• 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:
  • Intervention Arm: 6.1% (352/5780) versus 5.6% (325/5764) on control; risk difference 0.5 percentage points (95% CI -0.4 to 1.3), risk ratio 1.08 (0.93–1.25); unadjusted two-proportion z-test p = 0.302.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention Arm and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Small for Gestational Age (SGA)

• 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:
  • Intervention Arm: 27.4% (1506/5492) versus 28.6% (1564/5467) on control; risk difference -1.2 percentage points (95% CI -2.9 to 0.5), risk ratio 0.96 (0.90–1.02); unadjusted two-proportion z-test p = 0.167.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention Arm and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Perinatal Mortality

• 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:
  • Intervention Arm: 4.6% (264/5779) versus 5.4% (309/5763) on control; risk difference -0.8 percentage points (95% CI -1.6 to -0.0), risk ratio 0.85 (0.73–1.00); unadjusted two-proportion z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Intervention Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the three posted secondary endpoints, the overall pattern is not uniform. The estimated direction differs by outcome, and the reported confidence intervals do not show a similarly clear separation from the null across all three. This is a less consistent pattern than the primary endpoint result, but it does not by itself establish that the primary result is unrelated to the secondary outcomes. Each endpoint measures a different event and has its own timing and available-data denominator.

The secondary outcomes are hypertensive disorders of pregnancy, small for gestational age, and perinatal mortality. Their purpose is to add information beyond the primary endpoint, not to redefine the primary question. The results may be considered alongside the primary finding, but they should not be treated as three additional independent confirmations of it. Per-endpoint estimates and their interpretations are recorded with the outcome results rather than repeated.

The registry reports 18 outcome measures and 17 analyses, but the number of measures alone does not reveal which outcomes were planned as confirmatory, how the testing order was set, or whether statistical adjustment was used. Multiplicity adjustment and a prespecified hierarchy are not reported in the registry record. As a general statistical point, examining multiple outcomes creates more opportunities for apparently notable findings to arise by chance. Unadjusted secondary p-values therefore warrant more caution than the primary result, especially when they are considered outside a prespecified testing strategy.

The secondary outcomes can help readers understand whether the observed primary pattern appears alongside other recorded pregnancy and perinatal outcomes. They cannot, without further planned analyses and context, explain the primary result or establish a mechanism. Their role is complementary and exploratory in interpretation unless the registry record documents a stronger confirmatory plan, which it does not.

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

• Incidence of Hypertensive Disorders of Pregnancy
• Incidence of Small for Gestational Age (SGA)
• Incidence of Perinatal Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the registry definition of preterm birth or did not. The posted arm results are event counts and denominators. A risk is the event count divided by the number of participants contributing outcome data; a risk ratio compares those risks, while a risk difference subtracts one risk from the other. These are general descriptions of the measures, not additional trial results.

What does the sponsor’s risk ratio describe?

The registry reports a Cochran-Mantel-Haenszel risk ratio of 0.89 for the intervention arm relative to the placebo arm. A risk ratio of 1 would represent equal risks; values below 1 represent a lower estimated risk in the intervention group, and values above 1 a higher estimated risk. The reported 95% confidence interval is 0.81 to 0.98, and the reported p-value is 0.012. The method name indicates the sponsor used a Cochran-Mantel-Haenszel procedure. The registry record does not specify the strata or adjustment variables used, so no particular stratification scheme should be assumed.

What does the recalculated risk difference add?

The posted summary counts can also be used for a simple unadjusted risk-difference comparison. The recalculated estimate is -0.015, with a 95% confidence interval from -0.027 to -0.003 and an unadjusted p-value of 0.013. A risk difference reports an absolute contrast on the risk scale, whereas a risk ratio reports a relative contrast. Each answers a related but distinct descriptive question. The recalculation does not reproduce the sponsor’s analysis method and does not replace it.

As a general statistical point, an unadjusted comparison does not account for any grouping or covariates that may be part of a stratified analysis. It is useful as a check on the broad direction and scale implied by the posted counts, but the sponsor’s reported analysis remains the trial’s own reported result. Since the registry does not flag a discrepancy, the two results can be described as directionally consistent while retaining their methodological distinction.

How should p-values be read?

A p-value describes how unusual data at least as incompatible with a specified null model would be, if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The sponsor’s primary p-value is 0.012; the simple unadjusted recalculation gives 0.013. Both are reported alongside estimates and confidence intervals because a p-value alone does not convey the range of effect sizes compatible with the data.

As a general point, the null value depends on the effect measure: it is 1 for a risk ratio and 0 for a risk difference. A confidence interval that excludes the relevant null value is consistent with a two-sided test reaching a conventional statistical threshold, but it does not prove that the estimate is exact or free from bias. The primary analysis is the sponsor-reported Cochran-Mantel-Haenszel result, not a decision made solely from the recalculated p-value.

Why distinguish the analysis population?

The primary endpoint is described as modified intention-to-treat, and the registry explicitly says that reported counts reflect available data and may not always reflect the total population defined in the mITT group. The displayed denominators are therefore important to interpretation. The record does not describe the mITT inclusion rules beyond that note, nor does it explain how missing primary outcomes were handled. Missing-data assumptions can affect estimates if availability is related to outcome or group assignment; whether that occurred cannot be assessed from the registry record.

The group denominators differ from the total enrollment, and the registry itself warns that outcome counts are based on available data. This is not enough information to infer why a participant lacks an outcome value, whether missingness differed by arm, or what result would have been observed for missing participants. Such details are not reported in the registry record.

How do secondary analyses differ from the primary test?

The registry lists secondary analyses using the same named Cochran-Mantel-Haenszel method and risk-ratio measure. These outcomes include hypertensive disorders of pregnancy, small for gestational age, and perinatal mortality. Their results add context about outcomes beyond the primary endpoint, but the registry record does not report whether the secondary outcomes were adjusted for multiple testing. As a general statistical principle, testing several outcomes increases the opportunity for at least one result to appear notable by chance. Unadjusted secondary p-values consequently carry less confirmatory weight than a single primary analysis.

The listed primary analysis is a superiority analysis. The registry does not report the full statistical analysis plan, including any planned covariates, subgroup analyses, sensitivity analyses, or interim monitoring. These details should not be inferred from the method label or the posted results.

11. Confidence Intervals and Precision

The sponsor’s primary risk-ratio estimate is 0.89, with a 95% confidence interval from 0.81 to 0.98. The interval conveys uncertainty about the estimated relative effect: values across that range are compatible with the data under the analysis assumptions. It is not a guarantee that the true effect lies in that particular interval, and it does not describe the range of individual outcomes.

The simple unadjusted risk-difference recalculation is -0.015, with a 95% confidence interval from -0.027 to -0.003. This interval expresses uncertainty on an absolute-risk scale. Its negative values indicate that the estimates in the interval favor a lower observed event proportion in the intervention group under the stated subtraction order. The risk-ratio interval and risk-difference interval cannot be compared as if they used the same units.

As a general statistical explanation, confidence intervals are affected by both the amount of information in the data and the variability of the outcome. More precise estimates tend to have narrower intervals, while less precise estimates tend to have wider ones. An interval should be interpreted alongside the point estimate, endpoint definition, analysis population and method. It should not be read as proof that every value in the interval is equally likely.

The sponsor’s interval excludes the risk-ratio null value of 1, while the unadjusted interval excludes the risk-difference null value of 0. Those interval statements are consistent with the corresponding reported p-values, but do not remove uncertainty about the magnitude or generalizability of the effect. Available-data analysis and unreported details of missingness are additional limits on what precision alone can establish.

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

The 80% power column gives the estimated participants per arm for a planning scenario designed to have an 80% chance of detecting the selected effect if that effect and the calculation assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. Power is a property of a planned design under specified assumptions; it is not the probability that the observed result is true and does not establish whether the trial succeeded.

The rows that plan for 100%, 75% and 50% of the observed effect illustrate how the required sample size changes when the target effect changes. Smaller effects require more participants to distinguish them from the null with the same planned power and significance level. The plotted curve should be read as another display of that relationship, rather than as an additional analysis of the trial’s observed result.

These figures are planning illustrations generated from the observed effect, not observed power and not a reconstruction of the trial’s original design. They should not be used to claim that the trial had a particular probability of detecting its observed result. The registry record does not report the original assumptions used to set enrollment.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.131; treatment proportion p₁ = 0.116; average p̄ = 0.123.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4648 = 0.9110.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4647 = 0.3911.
4. n = (0.9110 + 0.3911)² / (-0.0152)² = 7,298.4, rounded up to 7,299 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 <- 0.130811936155448                          # control proportion
p1 <- 0.115570934256055                          # 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(2409680)
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 = 7,299 (80% power), 9,770 (90% power)
 75% of observed effect: n per arm = 13,148 (80% power), 17,601 (90% power)
 50% of observed effect: n per arm = 29,970 (80% power), 40,120 (90% power)
power.prop.test: 7298.4 
Simulated power at n = 7,299 per arm: 0.800 (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 sponsor-reported primary result is a Cochran-Mantel-Haenszel risk ratio of 0.89, with a 95% confidence interval from 0.81 to 0.98 and p = 0.012. This is the analysis reported by the registry for the trial. It compares risk on a relative scale and is the result to use when describing the sponsor’s own primary analysis.

The separate recalculation uses only the posted arm counts and denominators to obtain an unadjusted risk difference of -0.015, with a 95% confidence interval from -0.027 to -0.003 and an unadjusted p-value of 0.013. It is a straightforward summary-statistic comparison, not an attempt to recreate the Cochran-Mantel-Haenszel procedure. The risk ratio and risk difference have different scales, and the methods differ, so their numerical estimates should not be expected to match.

Both analyses point in the same direction for the primary outcome, and the registry does not flag a discrepancy. The sponsor’s result should remain distinct from the recalculation: one is the analysis reported for the trial, while the other is an unadjusted check based on posted summary data. If a discrepancy were flagged, the sponsor’s own analysis would take precedence; no such discrepancy is flagged in this record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and three secondary endpoints, and records 18 outcome measures and 17 analyses. It reports results for the primary outcome and the secondary outcomes discussed in the results. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a rule for controlling the overall chance of false-positive findings across outcomes. Consequently, the secondary results should not be read as if each were a separate confirmatory test with no relation to the others.

As a general statistical point, multiplicity arises when several hypotheses are tested. Even when each test uses a conventional threshold, the chance of at least one nominally notable result can increase across a set of tests. Adjustment methods or a prespecified hierarchy can address that issue, but no such plan is reported in the registry record. This does not invalidate the posted results; it affects how strongly secondary p-values can support confirmatory conclusions.

The primary population is labeled modified intention-to-treat. The registry says that counts reflect available data and do not always represent the total population defined in the mITT group. The record does not report detailed inclusion rules for this population, the number or reasons for missing observations by outcome, or the method used to handle missing data. It also does not provide sensitivity analyses assessing alternative assumptions about missing outcomes. These omissions limit assessment of whether available-case results could differ from results for the full defined population.

The primary endpoint description specifies delivery at or after 20 0/7 weeks and prior to 37 0/7 weeks, with classification based on actual delivery date relative to projected estimated due date. The registry gives this definition but does not report further adjudication procedures or how uncertain dates were managed. The analysis plan, subgroup strategy, interim analyses, and original sample-size justification are also not reported in the registry record. Those absent details should remain open questions rather than be inferred from the reported estimates.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: neonatal death up to 28 days (3.2%), fetal loss (2.7%), pre-eclampsia or eclampsia (2.5%), hypertension admission or medical visit before delivery (2.0%), other (1.0%).

The registry reports serious adverse-event figures separately for the intervention and placebo arms. For the intervention arm, 832 participants were affected among 5943 at risk; the placebo arm reports 857 affected among 5936 at risk. Death counts are recorded as 9 and 12, respectively. The registry lists serious-event terms including neonatal death up to 28 days, fetal loss, pre-eclampsia or eclampsia, hypertension admission or medical visit before delivery, other, and preterm labour or preterm birth evaluation before delivery. The listed term percentages are part of the registry record and describe the recorded serious-event terms.

These figures are safety summaries, not a randomized comparison designed in the same way as the primary efficacy analysis. The registry record does not provide enough detail to determine whether each event was judged related to assigned treatment, how events were collected, or whether event categories overlap. Death counts should not be interpreted as deaths caused by either assigned regimen. The figures should be read as reported adverse-event information, not as proof of comparative safety or harm.

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

The primary analysis reports a lower estimated risk of preterm birth in the aspirin-assigned group than in the placebo-assigned group. The sponsor’s risk-ratio estimate is 0.89, with a 95% confidence interval from 0.81 to 0.98 and p = 0.012. The simple unadjusted recalculation from the posted counts also points in that direction, while expressing the contrast as a risk difference. These findings describe the observed trial comparison and its statistical uncertainty.

They do not show that the estimated effect is identical for every participant, nor do they explain why the groups differed. The interval indicates that the effect is estimated with uncertainty; it does not provide certainty about a single true magnitude. The available-data qualification also matters: the registry says the reported counts do not always reflect the total population defined in the mITT group, and missing-data details are not reported.

The result does not by itself establish how well the estimate applies to people or settings not represented in the analyzed participants. The registry describes the intended study population and motivation, but detailed participant characteristics and actual recruitment distribution by geography, race and ethnicity are not reported in the registry record. Adherence and treatment exposure are also not reported. Generalizing beyond the recorded trial comparison therefore requires information not contained in this record.

Secondary outcomes add context but have a less consistent pattern, and multiplicity handling is not reported. Serious adverse-event summaries are descriptive and do not establish treatment causation. Neither the primary result nor the safety summaries should be converted into individual medical advice. They are statistical evidence from a particular randomized comparison, with the definitions, analysis population and limitations recorded for the trial.

18. Why This Trial Matters Statistically

This trial matters statistically because it places a clearly defined pregnancy outcome at the center of a randomized comparison. The primary endpoint is specified as preterm birth, with gestational-age boundaries and a rule for determining timing from actual delivery date relative to the projected estimated due date. That definition makes the target comparison interpretable and distinguishes the primary question from related secondary outcomes.

The registry reports a substantial enrollment and posts event counts for both randomized groups. Random allocation and double masking are important design features for reducing some sources of bias in a treatment comparison, although the registry record does not provide all operational details needed to assess how those protections were implemented. The sponsor analysis and an unadjusted recalculation point in the same direction, while also illustrating why method and effect scale must be stated clearly.

The record also highlights the limits of reading a result from a registry summary alone. The primary population is modified intention-to-treat, yet counts reflect available data; details about missingness, multiplicity, the original sample-size plan and interim analyses are not reported. Secondary outcomes offer a broader view, but they do not carry the same interpretive role as the primary endpoint when the testing strategy is unknown.

For biostatistical interpretation, the value lies not in a single p-value but in the combination of trial design, endpoint definition, effect estimate, uncertainty interval, analysis population and transparency about what is unreported. The posted data allow a focused assessment of the primary comparison, while leaving important questions about analysis planning and generalizability unresolved.

19. Limitations

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

Several trial-specific limitations follow from the registry record. First, the primary analysis is modified intention-to-treat, and the record explicitly notes that outcome counts reflect available data and may not represent the full mITT population. The number and reasons for missing data, arm-specific missingness, and the method used to address missing outcomes are not reported in the registry record. The impact of missing outcome data therefore cannot be evaluated from the posted summary.

Second, the record does not provide the original sample-size justification or the full statistical analysis plan. It does not report whether interim analyses were conducted, how multiplicity across outcomes was handled, or what covariates or strata were used in the sponsor’s Cochran-Mantel-Haenszel analysis. The planning illustrations based on the observed effect cannot answer what assumptions were used when the trial was designed.

Third, the registry describes the intended setting as diverse, but actual enrollment characteristics by geography, race or ethnicity are not reported in the registry record. Detailed eligibility criteria, adherence, treatment received and procedures for maintaining masking are also not reported. These omissions limit assessment of the population represented and the practical conduct of the intervention comparison.

Finally, the posted safety figures do not provide detailed attribution or collection methods, and the record does not explain whether serious-event categories overlap. The secondary outcomes are not accompanied by a reported multiplicity plan. These limitations do not erase the recorded primary result, but they constrain how completely its robustness, safety context and transportability can be assessed from registry information alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Aspirin Supplementation for Pregnancy Indicated Risk Reduction In Nulliparas (ASPIRIN) — NCT02409680.
• Registry record last updated 2024-11-21; status last verified 2024-11.
• Results first posted 2021-09-08.
• 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 completed ASPIRIN trial is recorded as a randomized, double-masked, parallel-group study with enrollment of 11976. Participants were assigned to daily 81 mg low-dose aspirin or an identical-appearing placebo, on the stated gestational-age schedule. The primary endpoint was preterm birth at delivery, defined using gestational-age thresholds and the actual delivery date relative to the projected estimated due date.

The sponsor-reported primary analysis is a Cochran-Mantel-Haenszel risk ratio of 0.89, with a 95% confidence interval from 0.81 to 0.98 and p = 0.012. The unadjusted recalculation from posted counts gives a risk difference of -0.015, with a 95% confidence interval from -0.027 to -0.003 and p = 0.013. The registry notes that outcome counts reflect available data and may not represent the total mITT population. Three secondary outcomes and serious adverse-event summaries are also recorded. Details on missing-data handling, multiplicity, original sample-size planning and several aspects of the analysis plan are not reported in the registry record.