RCT: Can a Single Counseling Phone Call Improve Contraception After an Abortion?: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for RCT: Can a Single Counseling Phone Call Improve Contraception After an Abortion? (NCT01199952), a randomized na study. The primary outcome is Number of Participants Using an Effective Contraceptive Method 6 Weeks After Abortion.

2. Clinical Question

The trial asked whether a counseling call after an abortion was associated with a difference in use of an effective contraceptive method at six weeks. The study focused on women who chose combined hormonal contraception (CHC) on the day of their abortion. The primary comparison was between participants assigned to a call and participants assigned to no call.

The clinical question is about a specific short-term outcome and a particular population: participants who had selected CHC. It is not a comparison of all contraceptive options, nor does the primary endpoint measure longer-term continuation. The registry also lists secondary aims concerning common concerns and logistical problems, reasons for discontinuation or method change, and feasibility of follow-up calls. Detailed results for those aims are not reported in the registry record.

3. Trial Design

The registry describes a randomized, controlled trial with two groups: a control group and an intervention group. Allocation is listed as randomized, and masking is listed as none. The registry records an enrollment of 207 participants. The posted arm counts are 103 in control and 104 in intervention.

Participants in the intervention group were intended to receive a counseling phone call after abortion. The arm description says the call took place three to four weeks after enrollment, while the study summary describes a three-week educational call after abortion. The control arm description says participants did not receive a counseling call one month after enrollment. These descriptions establish the intended contrast but do not resolve the exact timing wording into a single protocol detail.

The study summary says all participants would be contacted six weeks after abortion to assess and compare method use. The primary outcome is recorded at six weeks after the abortion procedure. The registry lists the study as completed, with a start date of 2011-03-21 and primary completion in 2013-01. The phase is listed as NA.

The registry record does not report the trial's original sample-size justification or detailed statistical plan. The stated planning illustrations are based on the observed effect, rather than on a reported original design calculation. The registry lists zero posted analyses, although it includes group outcome counts and a comparison summary. The record does not establish whether the posted comparison was the prespecified primary analysis or describe any adjusted analysis.

The trial's findings apply most directly to participants represented by this study: women selecting CHC following surgical abortion in the stated setting. The record does not report enough detail to assess how closely the enrolled participants reflected other populations or settings.

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

Analysis population for the primary outcome, as defined in the registry: study sample is female only since study is birth control selected following surgical abortion

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 number of baseline participants matches the Participant Flow, n=207

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Using an Effective Contraceptive Method 6 Weeks After Abortion, measured over 6 weeks after abortion procedure.

The primary endpoint is the number of participants using an effective contraceptive method six weeks after the abortion procedure. The registry's primary outcome title and description define the endpoint as a count of participants, and the outcome type is binary: each participant either met the endpoint definition or did not.

This measure was chosen to address the trial's stated question about contraceptive use after a brief counseling intervention. The six-week assessment followed the intervention call planned for approximately three weeks after abortion, leaving time to assess method use in the following weeks. That rationale is described in the study summary. The endpoint is an assessment at a particular follow-up time, not a measure of uninterrupted use throughout the period or of later continuation.

The posted counts are 55 participants in the control group and 55 in the intervention group. The arm denominators are 103 and 104, respectively. A count alone does not account for the differing group sizes, so the comparison statistics also describe the contrast between groups. The registry does not provide a detailed operational definition of which methods qualified as effective, nor does it report how missing six-week assessments were handled.

The outcome is relevant to the stated primary aim, but it does not by itself describe participants' reasons for choosing, starting, stopping, or changing methods. Those concerns were listed among the secondary aims; detailed secondary results are not reported in the registry record.

7. Results Posted in the Registry

• Intervention: 52.9% (55/104) versus 53.4% (55/103) on control; risk difference -0.5 percentage points (95% CI -14.1 to 13.1), risk ratio 0.99 (0.77–1.28); unadjusted two-proportion z-test p = 0.941.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either used an effective contraceptive method at the six-week assessment or did not. A count is reported for each arm, together with each arm's denominator. The comparison can be described using several measures of association, including a risk difference, a relative risk, and an odds ratio. These measures express the contrast in different ways and should not be treated as interchangeable.

What does a risk difference describe?

A risk difference compares the outcome proportions in the two groups by subtracting one group's proportion from the other's. It is expressed on the same absolute scale as the outcome probability. A value of zero corresponds to no difference on that scale; a positive or negative value indicates the direction of the contrast according to the ordering of groups used in the analysis. The posted risk-difference estimate is close to zero, and its confidence interval extends to both sides of zero.

How do relative measures differ?

A relative risk compares the probability of the outcome in one group with the probability in the other. An odds ratio compares the odds rather than the probabilities. For either relative measure, a value of one represents no relative difference. These measures can give a different numerical impression from an absolute risk difference, especially when an outcome is not rare. The registry includes relative-measure summaries, but the primary interpretation remains anchored to the endpoint and the posted group counts. No adjusted relative estimates are reported.

What does the p-value say?

The unadjusted p-value is 0.941. In general, a p-value describes how unusual data at least as incompatible with a specified no-difference model would be, if that model and the test assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. A large p-value does not demonstrate that effects are absent or that groups are equivalent. It indicates that this comparison does not provide strong evidence against the no-difference model under the analysis used.

The registry does not report the exact test procedure used for the posted p-value, so it should not be assigned to a particular test or set of assumptions. The comparison is described as unadjusted; no adjustment for baseline variables is listed. Random allocation is intended to support a fair comparison, but the record does not provide baseline characteristics or enough detail to evaluate balance in this trial.

Why does the confidence interval matter?

A confidence interval gives a range of values compatible with the observed data and the interval's statistical procedure. In repeated use of the same procedure under its assumptions, intervals constructed in this way have a specified coverage property. An interval is not a guarantee that the true effect lies within its particular limits, and it is not a range of all possible individual responses. Here, the reported interval for the risk difference crosses zero, so the data are compatible with no difference as well as with effects on either side. Its breadth is important: it conveys uncertainty about the magnitude, not merely whether a threshold for statistical significance was crossed.

For binary outcomes, the precision of estimates depends on the number of participants and outcome events in the groups, as well as on the distribution of outcomes. A study with limited information can yield an estimate near zero but still have an interval broad enough to include effects that may matter. The registry does not report a precision target or a prespecified clinically important difference, so the interval cannot be judged against a stated decision threshold.

What can be inferred from randomization?

Random allocation can support causal interpretation by balancing, on average, measured and unmeasured baseline characteristics across groups. That protection depends on implementation, follow-up, outcome measurement, and analysis. The record states that the study was randomized but does not report the allocation sequence method, concealment procedures, participant flow, or analysis population. These details are not reported in the registry record. The lack of masking is recorded; the record does not explain whether outcome assessment could have been influenced by knowledge of assignment.

The registry's design field lists a single-group model while its allocation and arm descriptions identify randomized control and intervention groups. The record does not explain this classification. The group-level comparison should therefore be interpreted from the stated arms and posted outcomes, while recognizing that the record does not reconcile the design labels.

General statistical principle: over-dispersion is relevant when count data vary more than a chosen model assumes. It is not an issue to infer from these results because the primary endpoint is recorded as a binary participant outcome, not as a rate or count of repeated events. No over-dispersion assessment is reported.

10. Confidence Intervals and Precision

The precision of the primary comparison is conveyed by the confidence interval around the risk-difference estimate. The interval extends from a negative value to a positive value, crossing the value that represents no difference. Thus the posted data are compatible with possible effects in either direction. The point estimate is close to no difference, but the interval is more informative about uncertainty than the point estimate alone.

A confidence interval is not a measure of how many participants had the outcome, nor does it give a probability that the true effect lies within the particular interval. As a general statistical explanation, a confidence interval is produced by a procedure that, under its assumptions, captures the true parameter at a stated rate over repeated samples. The registry does not state the interval method or its confidence level, so those details are not reported in the registry record.

The group counts are 55 participants in each arm, with denominators of 103 in control and 104 in intervention. Those data support a comparison but do not make the estimate highly precise merely because the counts match. Precision depends on the information in all observed outcomes and on the statistical method. The posted interval indicates substantial uncertainty about the size and direction of the difference.

The record does not report a prespecified margin for a clinically important difference, so it is not possible to assess whether the interval rules out differences that investigators considered important. Nor does it report a target interval width or a design-based precision objective. The conclusion should remain calibrated: the comparison did not identify a clear difference, while the interval leaves uncertainty rather than establishing equivalence.

11. 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 events. They are illustrations calculated from the observed effect, using a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row represents planning for a stated fraction of the observed effect. These are planning illustrations, not observed power.

For planning for 100% of the observed effect, the figures are 148,277 participants per arm for 80% power and 198,500 participants per arm for 90% power. For planning for 75% of the observed effect, the corresponding figures are 263,561 and 352,833 participants per arm. For planning for 50% of the observed effect, they are 592,914 and 793,743 participants per arm.

In general, the 80% power column gives the estimated participants per arm under the listed assumptions for a design intended to have an 80% chance of detecting the specified effect at the stated significance level, if that effect is the true one and the assumptions hold. The 90% column gives the analogous planning figure for a 90% chance. Higher power targets generally require more participants under otherwise unchanged assumptions.

Smaller effects require more participants to distinguish them from random variation. The fractions in the planning figures therefore illustrate how required sample size grows as the effect to detect becomes smaller relative to the observed effect. These calculations use the observed result as their starting point and are not the trial's original sample-size justification; that justification is not reported in the registry record. The planning values should not be read as evidence that the trial had a particular probability of detecting an effect.

12. 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 = 0.534; treatment proportion p₁ = 0.529; average p̄ = 0.531.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7057 = 1.3832.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7057 = 0.5939.
4. n = (1.3832 + 0.5939)² / (-0.0051)² = 148,276.5, rounded up to 148,277 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 <- 0.533980582524272                          # control proportion
p1 <- 0.528846153846154                          # 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(1199952)
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 = 148,277 (80% power), 198,500 (90% power)
 75% of observed effect: n per arm = 263,561 (80% power), 352,833 (90% power)
 50% of observed effect: n per arm = 592,914 (80% power), 793,743 (90% power)
power.prop.test: 148276.5 
Simulated power at n = 148,277 per arm: 0.799 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and one secondary outcome measure, with the secondary outcome concerning reasons for discontinuation of contraception. The study summary also describes secondary aims about common concerns and logistical problems, reasons for discontinuation or method change, and feasibility of follow-up telephone calls. Detailed findings for these aims are not reported in the registry record.

When several outcomes or comparisons are tested, the chance of at least one false-positive finding can increase. General statistical methods for addressing this include prespecifying a primary contrast, adjusting for multiple tests, or interpreting secondary analyses as exploratory. The registry does not report a multiplicity strategy, a hierarchy among secondary outcomes, or whether any adjustment was used. No conclusion about multiplicity control can therefore be drawn from the record.

The registry lists zero posted analyses, and it does not describe the analysis population, exclusions after randomization, or a plan for handling missing six-week assessments. The record does not report how many participants completed the follow-up call or whether the posted denominators represent all randomized participants, participants with available outcomes, or another analysis set. The arm denominators and outcome counts are available, but they do not resolve those methodological questions.

Missing outcome data can affect an estimate if availability is related to group assignment or to the outcome. General approaches include defining the analysis population in advance, reporting follow-up by group, and examining assumptions about missing outcomes. None of those details is reported in the registry record. It is therefore not possible to assess attrition, determine whether an intention-to-treat analysis was used, or establish whether missingness could have changed the comparison.

The record does not report a prespecified statistical analysis plan, covariate adjustment, handling of protocol deviations, or sensitivity analyses. These omissions do not establish that such procedures were absent from the conduct of the study; they mean the registry record does not document them. Interpretation should consequently stay with the posted outcome counts and unadjusted comparison rather than attributing them to an undocumented analysis strategy.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The serious adverse event figures record zero serious events in both groups. The registry lists 103 participants at risk in control and 104 at risk in intervention, with zero serious events in each group. It also records zero other adverse events in both groups and zero deaths in both groups.

These figures describe what was recorded in the registry, not proof that no adverse events occurred outside the recorded definitions or observation period. The registry does not report detailed event terms, collection procedures, or a safety observation timeframe. It also does not provide a narrative explaining how events were monitored or classified. No serious adverse event terms are listed.

As a general statistical point, zero observed events do not establish that the underlying event risk is zero. The amount of information depends on the number observed, the number at risk, and how completely events were ascertained. The figures should be read as recorded counts rather than as a comprehensive assessment of safety. They do not change the interpretation of the primary contraceptive-use endpoint.

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

The result describes a randomized comparison of counseling call versus no counseling call among women choosing CHC after surgical abortion. At six weeks, 55 participants in each group were recorded as using an effective contraceptive method. The unadjusted p-value is 0.941, and the risk-difference confidence interval crosses no difference. Together, these findings do not identify a clear difference between the groups in the posted primary outcome.

This does not establish that the intervention and control conditions are equivalent. A non-significant comparison can reflect a small true difference, limited precision, or both. The interval remains compatible with effects in either direction, and the registry does not report a prespecified equivalence margin or a clinically important difference. It is therefore not appropriate to interpret the result as proof that counseling has no effect.

The endpoint concerns use at one follow-up time. It does not establish continued use over a longer period, the reasons participants chose or changed methods, or the experience of participants who did not use CHC. The study was specifically about participants who chose CHC, and the findings should not be generalized automatically to people selecting other contraceptive methods or to other settings.

The registry describes secondary questions about concerns, logistical problems, discontinuation, method changes, and feasibility. Their results are not reported in the registry record, so the primary comparison cannot answer those questions. Similarly, the recorded zero adverse-event counts should be understood as registry counts and not as proof that no events were possible or occurred outside the recorded assessment.

A balanced reading is that the observed six-week counts were similar, while the estimate remains uncertain. The data do not support a definitive claim of benefit, harm, or equivalence. Missing details about follow-up, analysis populations, and the statistical plan further limit how fully the comparison can be evaluated.

16. Why This Trial Matters Statistically

This trial illustrates why a point estimate, a p-value, and a confidence interval answer different questions. The group counts are identical, and the unadjusted p-value is large, but neither fact alone establishes that the groups have the same underlying outcome. The confidence interval shows that uncertainty remains about both the direction and size of the difference.

It also shows why a null result should not be reduced to a binary statement of success or failure. A trial may produce an estimate close to no difference while retaining uncertainty about effects that could matter. Without a prespecified clinically important difference or equivalence margin, statistical non-significance cannot be translated into a claim of practical equivalence.

The sample-size illustrations emphasize another general point: planning requirements depend on the effect a study is designed to detect. Smaller target effects require larger samples under the same assumptions. Since the original design justification is not reported, the illustrations based on the observed effect should not be mistaken for evidence about what the investigators intended or what the trial was powered to detect.

Finally, a registry record can contain outcome counts and a comparison while leaving essential analytic details undocumented. Follow-up, missing-data handling, analysis population, multiplicity, and the specific test are all relevant to interpretation. The record supports a cautious description of the observed six-week comparison, but not a complete reconstruction of the study's statistical conduct.

17. Limitations

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

The registry record leaves several trial-specific uncertainties. It does not report the original sample-size justification, a detailed statistical analysis plan, the test used for the posted p-value, or whether any covariates were considered. The planning illustrations use the observed effect and cannot establish the intended design target.

The record does not explain the design classification that lists a single-group model alongside randomized allocation and separate control and intervention arms. It also uses different descriptions of the intervention timing: three weeks after abortion in the study summary and three to four weeks after enrollment in the arm description. The exact timing cannot be resolved from the registry wording alone.

Participant flow and missing outcome handling are not reported. The record does not state how many participants were reached at six weeks, whether all randomized participants were included in the comparison, or how unavailable outcomes were handled. The stated arm denominators and counts do not answer those questions. Baseline characteristics and allocation-concealment details are also not reported in the registry record.

The primary outcome is measured at one follow-up point, and the registry does not give a detailed definition of which contraceptive methods counted as effective. Results for the listed secondary aims are not reported. The safety record lists zero events but does not describe event ascertainment or a safety observation period. These limitations constrain assessment of the endpoint definition, completeness of follow-up, and the scope of conclusions that can be drawn.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: RCT: Can a Single Counseling Phone Call Improve Contraception After an Abortion? — NCT01199952.
• Registry record last updated 2019-09-19; status last verified 2019-08.
• Results first posted 2019-09-19.
• 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.

21. Record Summary

NCT01199952 is a completed randomized controlled trial sponsored by the University of California, San Francisco. The registry records enrollment of 207 participants and compares a counseling phone call with no call among women who chose CHC following surgical abortion. Masking is listed as none.

The primary outcome is use of an effective contraceptive method six weeks after the abortion procedure. The posted counts are 55 of 103 in control and 55 of 104 in intervention. The unadjusted p-value is 0.941, and the reported risk-difference interval crosses no difference. The record lists zero serious adverse events, zero other adverse events, and zero deaths in both groups.

The registry does not report the original sample-size justification, a detailed statistical plan, missing-data handling, or detailed results for the secondary aims. The posted comparison does not establish equivalence, and the confidence interval leaves uncertainty about the size and direction of the difference.