Bystander Fatigue and CPR Quality Using Continuous Compressions Versus 30:2 Compressions to Ventilation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bystander Fatigue and CPR Quality Using Continuous Compressions Versus 30:2 Compressions to Ventilation (NCT01397656), a randomized na study. The primary outcome is CPR Quality.

2. Clinical Question

The practical statistical question is a comparison of compression performance under the two approaches in a randomized crossover study. Because participants crossed from one approach to the other, the observations arise from a within-participant sequence rather than a conventional trial with separate groups assigned permanently to different treatments. The registry lists both sequence orders: CPR 30:2 followed by continuous compressions, and continuous compressions followed by CPR 30:2.

The posted comparison reports a mean difference in the count of compressions over 2 inches, with continuous compressions as the comparison condition and CPR 30:2 as the reference. That difference is an estimate of the contrast between the posted summary means. The registry record does not report a crossover-specific statistical analysis, such as an analysis that accounts for pairing or sequence. The interpretation therefore needs to distinguish the observed summary contrast from any stronger claim about a causal effect adjusted for the crossover structure.

3. Trial Design

The registry identifies this study as randomized, unmasked and crossover. Enrollment is 63, and the record marks the study completed. The recorded start is 2011-07 and primary completion is 2011-08. The sponsor is Ottawa Hospital Research Institute. The phase is listed as NA.

Each participant performed CPR using both approaches in a sequence. One sequence began with CPR 30:2 and then crossed over to continuous compressions; the other began with continuous compressions and then crossed over to CPR 30:2. The posted primary outcome timeframe is five minutes. This structure differs from a parallel-group design, in which each participant would contribute data under just one assigned condition. In a crossover study, observations under the two approaches can be paired within participants, while order and possible carryover may also matter to analysis.

The study objectives specify comparison of achieved compression frequency and depth, as well as participant-rated exertion. The registry’s primary outcome is CPR quality, described as the count of compressions at a depth over 2 inches during five minutes. Secondary outcomes are heart rate, blood pressure and the Borg Rating of Perceived Exertion Scale. Heart rate and blood pressure are recorded in beats per minute and mmHg, respectively; the exertion scale is recorded in units on a scale.

The posted summary statistics give 62 observations for CPR 30:2 and 63 for continuous compressions for the primary outcome. The record does not explain why the number of observations differs from the enrollment figure or describe exclusions, missing observations, or the analysis population. It lists no reported analyses. The original protocol’s statistical plan, including its planned handling of the crossover structure, is not reported in the registry record. Consequently, the posted group summaries and unadjusted comparison should not be mistaken for a documented account of every analysis planned or conducted by the investigators.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as CPR Quality, measured over 5 minutes.

The primary endpoint is the mean count of chest compressions reaching a depth over 2 inches during a five-minute CPR period. The registry classifies it as a continuous measure and reports a mean and standard deviation for each approach. The endpoint therefore combines two features into a count: compressions must occur during the stated observation period and must exceed the stated depth threshold.

This measure addresses a specific dimension of CPR performance. Compression depth is part of the study’s stated interest in CPR quality, and counting compressions above a threshold focuses on compressions that meet the registry’s chosen depth criterion. It is not a direct measure of every aspect of CPR quality: the registry describes compression frequency separately in the study objectives, while the posted primary outcome is the count meeting the depth threshold. The endpoint also does not itself represent a patient outcome. The study record describes a comparison of bystander performance and exertion, not a measure of survival or recovery.

The posted mean for CPR 30:2 is 324.9 compressions, with a standard deviation of 120.0; for continuous compressions, the mean is 381.5, with a standard deviation of 68.5. The registry gives the timeframe as five minutes. These summaries describe the recorded distributions under each approach, but they do not convey the participant-level pairing created by the crossover. Nor do the means alone show how individual participants’ compression counts changed between conditions.

As a general statistical point, a mean is a compact description of the average count, while a standard deviation describes variation among observations around that mean. Neither one tells whether all observations were similar or whether a smaller number of observations had especially high or low values. Interpreting the endpoint therefore requires both the contrast and its uncertainty, as well as attention to the crossover design and the threshold-based definition.

7. Results Posted in the Registry

• CPR With Continuous Compressions: mean 381.50 versus 324.90 on control; difference 56.60 (95% CI 22.27 to 90.93), standardized effect d = 0.58; z-test p = 0.001.

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.

Heart Rate

• 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:
  • CPR With Continuous Compressions: mean 82.40 versus 82.80 on control; difference -0.40 (95% CI -5.87 to 5.07), standardized effect d = -0.03; z-test p = 0.886.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CPR With Continuous Compressions and the control. The interval gives the range of effects that remain compatible with the data.

Blood Pressure

• 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:
  • CPR With Continuous Compressions: mean 110.30 versus 109.80 on control; difference 0.50 (95% CI -3.39 to 4.39), standardized effect d = 0.05; z-test p = 0.801.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CPR With Continuous Compressions and the control. The interval gives the range of effects that remain compatible with the data.

Borg Rating of Perceived Exertion 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:
  • CPR With Continuous Compressions: mean 11.60 versus 11.00 on control; difference 0.60 (95% CI -0.38 to 1.58), standardized effect d = 0.21; z-test p = 0.232.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CPR With Continuous Compressions and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of participants’ response to the CPR periods: heart rate, blood pressure and perceived exertion. Across these measures, the posted comparisons do not show the same clear separation as the primary depth-based count. Each secondary confidence interval includes zero, and each corresponding unadjusted p-value is above 0.05. That pattern means the available summaries do not provide clear evidence of a difference in these measures; it does not establish that the approaches produce identical values.

These secondary outcomes help contextualize the primary finding, but they do not directly measure the same feature. The primary endpoint counts compressions exceeding a depth threshold. Heart rate and blood pressure describe physiological measures, while the Borg scale records perceived exertion. A higher count of compressions over 2 inches need not imply a corresponding difference in these other measures. The record does not provide a model linking the outcomes or a combined measure of quality.

Secondary results deserve less weight than a prespecified primary result when their analysis plan is unclear and multiple outcomes are considered. Looking across multiple outcomes creates more opportunities for a seemingly notable result to arise by chance. An adjustment or a clearly defined hierarchy can address some of that interpretive problem, but the registry record does not report a multiplicity procedure or a hierarchy for the secondary analyses. It lists no reported analyses.

The secondary confidence intervals are therefore important alongside their p-values. They show the range of contrasts compatible with the posted calculations, while the lack of a reported crossover-specific analysis leaves uncertainty about how within-participant pairing was handled. These outcomes should be read as supportive descriptive information, not as decisive confirmation or contradiction of the primary comparison. The overall pattern is that the primary depth-threshold count differs in the posted unadjusted comparison, whereas the secondary summaries are inconclusive about differences in heart rate, blood pressure and perceived exertion.

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

• Heart Rate
• Blood Pressure
• Borg Rating of Perceived Exertion Scale

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents continuous outcomes as means and standard deviations. This is a common way to describe measurements on a numerical scale: the mean locates the average, and the standard deviation gives a sense of variation around that average. For the primary endpoint, the quantity is a count, even though it is analysed as a continuous measure. A mean difference then expresses the contrast between the two posted averages in the original count scale.

What does the mean difference describe?

The primary comparison is reported as a mean difference of 56.6 compressions, calculated as the continuous-compression mean relative to the CPR 30:2 mean. A positive value means the posted mean is higher for continuous compressions in this contrast. The means are 381.5 and 324.9, respectively. This is an unadjusted comparison based on the posted summary statistics. It is not an adjustment for participant characteristics, order, or other factors, and the registry does not report a separate analysis plan.

These quantities describe the outcome in its original units, which can make the direction and scale of a contrast easier to understand than a standardized effect. A standardized effect expresses a difference relative to variability; it can help compare measures with different units, but it does not directly answer how many compressions separate the posted means. The record includes a standardized effect calculation, but the primary interpretation does not require it.

How should a confidence interval be read?

A confidence interval expresses uncertainty around an estimate under the statistical method used to construct it. The primary interval runs from 22.27 to 90.93 compressions, around the estimate of 56.6. It provides a range of values compatible with the data and calculation, rather than a guarantee that the true contrast lies within those particular limits. A wider interval indicates less precision than a narrower interval on the same scale. The interval does not resolve whether the method properly uses the paired crossover observations; that depends on the analysis, which is not reported in the registry record.

The secondary intervals are also useful even when they include zero. An interval containing zero means the posted results are compatible with no difference as well as with contrasts in either direction covered by the interval. It does not establish equivalence or rule out a meaningful difference. A formal equivalence or non-inferiority conclusion would require a specified margin and a suitable analysis, neither of which is reported in the registry record.

What does the p-value add?

The primary unadjusted p-value is 0.001. In general, a p-value describes how unusual data at least as incompatible with a null hypothesis would be if that null and the calculation assumptions were correct. It is not the probability that the null is true, nor a measure of the importance of the observed difference. The p-value should be considered alongside the effect estimate, its interval, the outcome definition and the design. The registry does not document the analysis that produced an investigator-reported p-value; it lists no reported analyses.

The secondary unadjusted p-values are 0.886, 0.801 and 0.232. These results alone should not be used to assert that the secondary measures are the same under both approaches. Their intervals and the limited precision of the comparisons matter, and the record does not report an adjustment for making multiple comparisons.

Why does the crossover design matter?

In a crossover design, each participant experiences both conditions. The two measurements from a participant may be more alike than measurements from different participants. A paired analysis uses this within-participant relationship, usually by analysing each participant’s change between conditions or through another model that represents repeated observations. Such methods can yield different standard errors from an analysis treating condition summaries as independent.

The posted comparison contains group counts and marginal means and standard deviations, but not the within-participant differences or their variability. The registry record does not state whether the comparison incorporates pairing, order, or carryover. A simple calculation from the separate summary statistics cannot reconstruct those participant-level features. Accordingly, the unadjusted estimate is useful as a description of the posted summaries but cannot be assumed to be the definitive crossover analysis.

Order can matter because performance in a later period might be affected by practice, fatigue or experience in an earlier period. This is a general consideration for crossover trials, not a claim that such effects occurred in this study. The record identifies the two sequence orders but does not report a test or adjustment for order or carryover. It also does not report washout details. These omissions limit what can be concluded about how the crossover was handled statistically.

What do standard deviations and over-dispersion mean?

Standard deviation describes the spread of observed values around the mean. The primary standard deviation is 120.0 for CPR 30:2 and 68.5 for continuous compressions. The larger value indicates more variability in the posted CPR 30:2 outcome distribution, as summarized by that measure. It does not show the shape of the distribution, identify outliers, or establish why variability differs.

As a general statistical concept, over-dispersion occurs when data vary more than a model’s assumptions allow. For count outcomes, a simple model may assume a particular relationship between the average and variability; if actual variability is greater, standard errors can be too small and intervals too narrow unless the analysis accounts for it. The registry supplies means and standard deviations but does not report a count-distribution model, diagnostic checks, or an over-dispersion assessment. It would therefore be inappropriate to claim that over-dispersion was present or that it was handled in a particular way.

For a mean-based comparison, the scale of the endpoint and the variability are both relevant. A count of compressions over a fixed period may be skewed or otherwise depart from a normal distribution; whether that matters depends on the data and analysis. The registry does not report the participant-level distributions or diagnostic analyses. General concerns about count data should be treated as questions for interpretation, not as evidence that the posted means are invalid.

In sum, the reported summaries support a readable comparison of average counts, while the confidence interval and p-value describe uncertainty under their calculation assumptions. The randomized crossover structure makes paired analysis especially relevant, but the statistical plan, participant-level paired data and reported investigator analyses are not available in the registry record. Those limits should remain explicit when interpreting the numerical contrast.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 56.6 compressions, and its confidence interval extends from 22.27 to 90.93. The interval is entirely above zero, consistent with the positive direction of the posted difference. Its width shows that the precise size of the contrast is uncertain: the data and calculation are compatible with a range of positive differences rather than a single exact value. The unadjusted p-value is 0.001, but statistical evidence against a zero contrast does not eliminate uncertainty about the magnitude.

Precision depends on more than the number of observations. It is also influenced by variability, the analysis method and, in this crossover study, the relation between measurements from the same participant. The registry reports standard deviations of 120.0 and 68.5 for the primary groups, but does not report the standard deviation of within-participant differences or describe a paired analysis. The displayed interval may therefore not represent the precision of a crossover-adjusted estimate.

The secondary confidence intervals include zero: heart rate, -5.874 to 5.074; blood pressure, -3.393 to 4.393; and perceived exertion, -0.384 to 1.584. These intervals do not establish that the effects are exactly zero. Rather, they indicate that the posted comparisons retain uncertainty across values on both sides of zero. A conclusion of equivalence would require a prespecified acceptable range and an analysis designed to assess it; neither is reported in the registry record.

Confidence intervals are conditional on the statistical method and assumptions used. The record does not describe the construction method for the intervals or the original analysis plan. They should be read as precision summaries for the posted comparisons, not as a substitute for a documented crossover analysis.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning estimates translate an assumed effect into an illustrative number of participants per arm. They are not the observed enrollment and do not describe the original trial design. For continuous outcomes, the estimates are participants per arm, not total events. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between two arms and a normal approximation. It considers effects equal to 100%, 75% or 50% of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column represents the number of participants per arm that the planning calculation estimates would give an 80% chance of detecting the chosen effect under those assumptions, if that effect were the true effect. The 90% column uses a higher target chance of detection and therefore generally calls for more participants per arm. These are planning probabilities under a model, not guarantees about a future study. The values change with the endpoint and with the fraction of the observed effect selected for planning.

For the primary outcome, planning for 100% of the observed effect gives 47 participants per arm for 80% power and 63 participants per arm for 90% power. Planning for 75% gives 83 and 111; planning for 50% gives 187 and 250. The pattern illustrates a general principle: smaller effects are harder to distinguish from random variation, so detecting them with the same power requires more participants. The secondary outcomes have their own planning estimates because their observed effects and variability differ.

These estimates are not observed power. They are hypothetical planning illustrations derived from the posted observed effect and stated assumptions; they do not establish whether the completed trial was adequately designed, nor do they measure the probability that its result is true. The registry does not report the investigators’ original sample-size justification, so the planning calculations should not be read as evidence of what guided 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 56.600; pooled standard deviation σ = 97.502.
2. n = 2 × (1.96 + 0.842)² × 97.502² / 56.600² = 46.6, rounded up to 47 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 <- 56.6                      # observed difference in means
sigma <- 97.5021158828157                     # 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(1397656)
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 = 47 (80% power), 63 (90% power)
 75% of observed effect: n per arm = 83 (80% power), 111 (90% power)
 50% of observed effect: n per arm = 187 (80% power), 250 (90% power)
power.t.test: 47.6 
Simulated power at n = 47 per arm: 0.791 (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 registry identifies a primary outcome and three secondary outcomes. The primary endpoint is the count of compressions over 2 inches during five minutes. The secondary endpoints are heart rate, blood pressure and Borg Rating of Perceived Exertion Scale. Considering several outcomes creates a multiplicity issue: the more comparisons examined, the greater the chance that at least one may appear notable by chance if no true effects exist. This is a general statistical concern, not evidence that any particular result in this study is false.

The record does not report whether the investigators adjusted for multiple testing, specified a hierarchy among secondary outcomes, or designated which comparisons would be confirmatory. It lists no reported analyses. The posted secondary p-values are unadjusted. They should therefore be interpreted cautiously and not as a collection of independent confirmations. The original protocol’s multiplicity strategy is not reported in the registry record.

Missing-data handling is also not described. The record reports enrollment of 63 and outcome group counts of 62 for CPR 30:2 and 63 for continuous compressions, but does not explain the difference, identify missing observations, or state how any missing values were handled. It does not report whether all randomized participants were included in each analysis or whether any participants were excluded. The analysis population and any imputation or other missing-data procedure are not reported in the registry record.

The design makes analysis population details particularly relevant. Participants crossed between conditions, and a complete paired comparison would ordinarily require usable information under both approaches for the participant. The posted group counts alone do not establish how many complete paired records contributed to the comparison. That number is not reported in the registry record, and no total of distinct participants contributing to analyses can be inferred from the two group counts.

Finally, the registry does not report an analysis that accounts for participant-level pairing, sequence order or possible carryover. These are distinct questions from multiplicity and missing data, but all bear on how faithfully the posted estimates reflect the randomized crossover design. Without the analysis plan and participant-level accounting, the summaries are informative as posted outcome descriptions but do not fully document the inferential process.

15. Safety Results

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

Other (non-serious) adverse events

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

The adverse-event record lists two sequence groups: CPR 30:2 followed by continuous compressions, and continuous compressions followed by CPR 30:2. For each sequence, 63 participants are listed as at risk for serious adverse events and 0 as affected. The record likewise lists 63 at risk for other adverse events and 0 affected in each sequence group.

These figures mean that the registry reports zero affected participants in the displayed serious and other adverse-event categories for both sequences. They do not establish that no event of any kind occurred, nor do they provide information about event definitions, collection procedures, severity gradings beyond the listed categories, or how events were attributed to each CPR period. Those details are not reported in the registry record.

Deaths are recorded as null rather than as a numerical count. A null entry is not the same as a reported zero; the death count is not reported in the registry record. The event figures should therefore be read as registry entries for the stated categories, not as a complete safety assessment or as proof of absence of risk.

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

The posted primary result describes a higher mean count of compressions reaching a depth over 2 inches during the continuous-compression condition than during CPR 30:2. The estimated mean difference is 56.6 compressions, with a 95% confidence interval from 22.27 to 90.93 and an unadjusted p-value of 0.001. This is evidence of a difference in the specific outcome as summarized in the registry. It is not, by itself, evidence that one approach is better across all aspects of CPR.

The endpoint is a performance measure collected during a five-minute period, not a patient-centered clinical outcome. The record does not report survival, recovery, or other patient outcomes. It therefore cannot establish that the observed difference in compression counts leads to a difference in clinical outcomes. The posted summary also does not establish how compression frequency differed; frequency is described in the study objectives, but the primary posted measure is the count above a depth threshold.

The study’s crossover design means participants performed both approaches. That design can support within-person comparisons, but interpretation depends on an analysis that accounts for the pairing and any relevant order effects. The registry lists no reported analyses and does not explain whether the posted comparison uses paired information. The difference should therefore be treated as an unadjusted summary-statistic contrast, not as a fully documented causal estimate from a crossover model.

The secondary outcome summaries do not settle the broader question. Their unadjusted comparisons have confidence intervals that include zero, which leaves uncertainty about the size and direction of possible differences. No multiplicity procedure or analysis hierarchy is reported. These findings should not be turned into claims that the secondary measures are equal or that the primary result is corroborated by them.

The result also does not establish that the observed estimate will be reproduced in another population or setting. The record describes laymen aged 55 or greater and a short CPR performance assessment, but does not report detailed recruitment or setting information. Nor does it report the original sample-size justification or statistical analysis plan. The appropriate reading is consequently bounded: the posted data show a positive unadjusted contrast in a particular compression-depth count, with statistical uncertainty and design-related analytic details that remain undocumented.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its randomized crossover structure makes the distinction between marginal summaries and paired analysis consequential. Each participant performed both CPR approaches, so the relation between that participant’s observations can contribute important information. Separate means and standard deviations do not reveal that within-participant relation. The registry’s lack of a reported crossover analysis makes it important to avoid treating a simple contrast between group summaries as though it necessarily incorporated the study design.

The primary outcome also illustrates how an endpoint definition shapes interpretation. The measure is not a general score of CPR quality; it is a count of compressions exceeding a specified depth during a defined period. A mean difference can be stated in the original count scale, but the result remains specific to that threshold and timeframe. Other dimensions, including compression frequency and exertion, require their own evidence.

The record supplies enough summary information to assess the direction, scale and nominal precision of the posted primary contrast, and it makes clear that secondary outcomes have less conclusive summaries. At the same time, it does not document the original analysis plan, multiplicity approach, missing-data handling or analysis populations. These omissions show why an estimate and p-value should not be interpreted in isolation from protocol and design information.

Finally, the planning illustrations demonstrate how strongly sample-size requirements depend on the effect selected for detection. Planning around a smaller fraction of the observed effect entails larger participant counts under the stated assumptions. That is useful for understanding future study planning, but it cannot retrospectively explain the completed trial’s enrollment because its original justification is not reported. The central statistical lesson is to separate observed summaries, inferential assumptions and planning scenarios.

18. Limitations

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

The registry provides limited detail for evaluating the crossover analysis. Although it identifies the two treatment sequences, it does not report how the comparison handles within-participant pairing, period or sequence effects, or possible carryover. The posted marginal means and standard deviations cannot recover the participant-level relationship between conditions. This limits confidence in treating the unadjusted summary contrast as the intended inferential result.

The primary endpoint measures a count above a depth threshold rather than a comprehensive measure of CPR quality. Compression frequency is included among the stated study objectives, but a frequency result is not posted among the outcomes described in the registry record. The endpoint is measured during five minutes and does not report patient outcomes. Thus its scope is narrow by design and should not be extended to outcomes it does not measure.

The outcome group counts are 62 for CPR 30:2 and 63 for continuous compressions, while enrollment is 63. The registry does not explain this difference, report the number of complete paired observations, or specify missing-data handling or analysis populations. The record also lists no reported analyses, so it is unclear whether the posted comparisons represent prespecified analyses or how they relate to any full analysis.

Other limitations arise from incomplete statistical documentation. The registry does not report the original sample-size assumptions, multiplicity adjustment, detailed model, or methods for checking distributional assumptions. The secondary outcomes have unadjusted comparisons. The adverse-event record reports zero affected participants in the listed categories but leaves deaths null, and it does not provide further event definitions or collection details. These gaps do not negate the posted summaries, but they constrain how confidently the results can be interpreted beyond their descriptive content.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bystander Fatigue and CPR Quality Using Continuous Compressions Versus 30:2 Compressions to Ventilation — NCT01397656.
• Registry record last updated 2018-11-15; status last verified 2017-06.
• Results first posted 2018-11-15.
• 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

This completed randomized, unmasked crossover study compared CPR using continuous chest compressions with CPR using a 30:2 compression-to-ventilation ratio in a population described as aged 55 or greater. Enrollment was 63. Participants followed both approaches in one of two sequence orders, and the primary outcome was the count of compressions over 2 inches during five minutes.

The posted mean count was 324.9 for CPR 30:2 and 381.5 for continuous compressions. The unadjusted mean difference was 56.6, with a 95% confidence interval from 22.27 to 90.93 and p = 0.001. Secondary outcomes were heart rate, blood pressure and perceived exertion; their posted unadjusted intervals include zero.

The registry record lists no reported analyses and does not describe crossover-specific analysis, missing-data handling, multiplicity methods or the original sample-size justification. These gaps limit interpretation of the posted comparisons as definitive inferential analyses. The primary result is specific to the depth-threshold count and does not establish effects on patient outcomes.