Specimen Pooling for Efficient Use of Biospecimens in Studies of Time to a Common Event

Abstract

For case-control studies that rely on expensive assays for biomarkers, specimen pooling offers a cost-effective and efficient way to estimate individual-level odds ratios. Pooling helps to conserve irreplaceable biospecimens for the future, mitigates limit-of-detection problems, and enables inclusion of individuals who have limited available volumes of biospecimen. Pooling can also allow the study of a panel of biomarkers under a fixed assay budget. Here, we extend this method for application to discrete-time survival studies. Assuming a proportional odds logistic model for risk of a common outcome, we propose a design strategy that forms pooling sets within those experiencing the outcome at the same event time. We show that the proposed design enables a cost-effective analysis to assess the association of a biomarker with the outcome. Because the standard likelihood is slightly misspecified for the proposed pooling strategy under a nonnull biomarker effect, the proposed approach produces slightly biased estimates of exposure odds ratios. We explore the extent of this bias via simulations and illustrate the method by revisiting a data set relating polychlorinated biphenyls and 1,1-dichloro-2,2-bis(p-chlorophenyl)ethylene to time to pregnancy.

Specimen pooling has been used in a variety of settings dating back to World War II (1), and a growing body of literature provides relevant techniques (2–5). Pooling helps to conserve stored, often irreplaceable, biospecimens and frequently can serve to decrease the proportion of values falling below the limit of detection (6–8). We consider a scenario in which an expensive assay is needed for exposure (e.g., that for dioxin) and/or specimens are limited in volume, but the outcome is inexpensive to measure. The idea is to assign participants to appropriate pooling sets, combine small representative aliquots from individuals in the pooling sets, and assay the pooled specimens. For a case-control study, cases and controls are separately partitioned to form appropriate pooling sets (5). A modified logistic regression analysis allows efficient estimation of the individual-level exposure effect while providing substantial reduction in assay cost.

We extend the approach for application to screening for exposure effects in studies of a discrete survival-time outcome. Discrete survival-time outcomes arise in epidemiologic applications when the time to an event of interest is either truly discrete, as in the time (in menstrual cycles) from initiation of a pregnancy attempt to conception, called time to pregnancy (TTP), or when continuous event-time outcomes are grouped. Assuming a discrete-time logistic model relating TTP to the exposure, we describe a strategy and an accompanying analytical approach which, in TTP studies, allows testing of the fecundability odds ratio associated with untransformed exposures. Because the standard likelihood is misspecified for the proposed pooling strategy under a nonnull exposure effect, the proposed approach produces slightly biased estimates of the exposure odds ratio. We use simulations to evaluate performance under a range of hypotheses. Our motivating example is a study of possible effects of serum levels of chemical exposures on fecundability as measured by TTP. We illustrate our approach by comparing results from a published TTP study that used individually measured exposures (9) with results derived by using pseudopooled measurements. The ideal application of the proposed approach is for testing exposure effects, whereas estimation of the effect via the proposed approach assumes logit linearity in the untransformed exposure levels and even then is subject to some bias. We explore these and other issues in the discussion.

MATERIALS AND METHODS

Notation and background

Discrete survival-time outcomes are frequently studied in epidemiologic and clinical applications. Examples include the number of menstrual cycles from time of initiation of a pregnancy attempt to conception, the grade in which a student drops out, and others. Consider n individuals with outcome times T₁, T₂, … , T_N where T can take only integer values: T = 1, 2, … , M or T > M, and M is a time beyond which the event times are treated as censored. Let U₁, U₂, … , U_N denote the corresponding exposures. For TTP, this would typically be blood or urine collected early in pregnancy (retrospective study) or when contraception is discontinued (prospective study). We assume that T is inexpensive to measure with possible right censoring only, and U is expensive to measure or biospecimens are available in limited amount. We assume a discrete-time logistic model (i.e., a discrete-time Cox model) between U and T:

(1)

The β_0k parameters are important in this model because, as in the case of a TTP study, they permit underlying heterogeneity in risk among participants by allowing the baseline risk to decline over time.

Proposed stratified design and proposed analytic model

Weinberg and Umbach (5) proposed a pooling approach for case-control studies that allows efficient estimation of the exposure odds ratio by using pooled exposure levels instead of individual exposure levels (Web Appendix 1 available at http://aje.oxfordjournals.org/). A study with a discrete-time outcome can be thought of as a sequence of nested, case-control studies, where the controls at T = k (those at risk but still not conceiving at time k) become the participants in a new case-control study at T = k + 1. As such, a repeated application of Weinberg and Umbach's approach in each cycle is possible by randomly forming pooling groups among the cases and separately among the controls in each cycle. However, this is clearly not an ideal strategy; for example, data from a woman not conceiving until cycle 10 would have to be mixed and measured in 10 different pools, so this approach is inefficient in this context (Web Appendix 2).

Instead, we propose a modified design that stratifies and pools according to the outcome time. At each time T = k (k ≤ M), individuals who experience the event at time k are partitioned into pooling sets, and for each such set, equal amounts of specimens are combined to form a single pool for assay. The same pooled measurement is treated as a “case” pool for the time when its event occurred and as a “control” pool for each of the earlier event times. Individuals who are censored just after T = k, without experiencing the event, are kept together and partitioned and pooled accordingly. These sets will serve as “control” pools for times up to and including k. Pools with T > M will serve as “control” pools throughout. We call this the stratified pooling design (Figure 1).

Figure 1.

Example of proposed pooling design for discrete survival-time outcome. The cases and controls at each outcome time are identified. Case pools at each time are enclosed in the black boxes. Case pools at later times are reused as control pools at earlier event times.

As in Weinberg and Umbach's approach, the pooling is outcome-dependent; but control pools are formed within strata based on their later event times. Hence, when the TTP is associated with the exposure (β₁ ≠ 0), the odds that a pool is a case pool versus a control pool are no longer a simple exponential function in the pooled exposure level as in Weinberg and Umbach's approach (Web Appendix 1, Equation 2 and Web Appendix 3). Consequently, the model based on the stratified design does not directly lend itself to analysis by a generalized linear model. Nevertheless, we use a generalized linear model based on the ideal design of randomly formed control pools to analyze the data obtained from the stratified design. Under the null hypothesis of no association (β₁ = 0), the stratified design is equivalent to the ideal design, so the model is correctly specified, which implies that a generalized linear model based on the ideal design can validly be used to test the association between the outcome and the exposure by using the stratified design. We use the same generalized linear model to estimate a nonnull β₁. We outline the model and the analytic approach below.

Similar to Weinberg and Umbach's approach, we assume that the measured level of exposure in the pooled specimen is the average of exposures of those in the pool. If subjects {1,2, … g} constituted a pool with individually measured exposures u₁, u₂, … , u_g, then the measured exposure in the pooled specimen is (10). For ease of notation, we use in this development. The logistic model based on the ideal design extends the model (Web Appendix 1, Equation 2) for pooled measure v, as follows:

(2)

where , β_0k is the baseline log odds for the event at time k given one is unexposed and at risk, and r_gk denotes the number of case sets of size g at time k divided by the number of control sets of size g at time k. The variable is declared as an offset (which forces its coefficient to be 1), the pool size “g” is entered as a covariate, and the model is fit with no intercept. Multiple pool sizes may be used, but all pool sizes must be present at each time to avoid infinities in the offset. That is, if a pool size appears in 1 stratum, it must be present in all strata. As an example, if pool sizes of 2 and 3, but not 4, are used in 1 cycle, then pools of sizes 2 and 3, but not 4, must be present at all other cycles. The interpretation of the exposure effect parameter β₁ is exactly the same as the parameter in equation 1 for individually assayed measurements, namely the estimated exposure effect is the log odds ratio associated with a unit change in an individual's exposure. For a sample size of n and pool size of g, the number of specimens that must be analyzed reduces to approximately n/g compared with n for individual analysis. Also, if 1 unit of specimen is needed for assay, then for pooled analysis, each subject need only provide a much smaller (1/g) unit of specimen for the pooled analysis. We call the application of equation 2 following a stratified design, a pooled analysis.

Assuming no unmeasured confounders, pooled analysis will be valid for inference about β₁ under the null (H₀: β₁ = 0 vs. H₁: β₁ ≠ 0). However, when β₁ ≠ 0, pooling within event times creates dependency among the individual exposure values within pools. Hence, for the stratified pooling design, equation 2 is misspecified (Web Appendix 3) if U is related to risk and consequently estimation is biased. We explore this issue by using simulations in the next section. To accommodate confounders (categorical or continuous), we extend the model as in Weinberg and Umbach's approach. In addition to the sum of exposures, we include the sum of confounders as an additional term in the model, whether they are measured in a pooled assay or measured individually (Web Appendix 4, Equation 2). Categorical (but not continuous) effect modifiers must be anticipated and accounted for in the pooling design by additionally stratifying the pooling sets and the analysis based on the levels of the effect modifier. Continuous effect modifiers can be categorized and handled similarly. Details are provided in the Web Appendices.

SIMULATIONS

When the exposure has an effect on risk (β₁ ≠ 0), as mentioned above, application of equation 2 is not strictly valid for data based on the stratified pooling design. Although logistic regression itself is biased and, hence, so is the usual analysis, we expect the pooling design to exacerbate the problem. We performed simulations to assess the performance of our approach. Detailed descriptions of the simulations are in Web Appendix 5.

Basic model

A mixed exposure was generated in which 20% of the population had no exposure and 80% were exposed. Exposed subjects had a lognormal exposure U with E(ln(U)) = 0 and Var(ln(U)) = 1. The event times were generated by using the model given in equation 1. We simulated 1,000 studies, each with 500 women, for an exposure-only model with β₁ taking on various values: 0 (null), ±0.105, ±0.288, and ±0.350. The negative values reflect a 10%, 25%, and 30% reduction in the odds with 1 unit change in the exposure, respectively, and the positive values reflect an 11%, 33%, and 42% increase in the odds, respectively. Parameter estimates, model-based standard errors, empirical standard errors, and empirical coverages for 95% confidence intervals for β₁ are summarized in Table 1.

Table 1.

Results Based on 1,000 Simulated Data Sets for Estimation and Testing of the Exposure^a Risk Parameter (Lognormal Odds Ratio) β Using the Proposed Pooling Design With Pooled Logistic Model and Data From 500 Individuals

β1	Estimates	Pool Sizeb
		1	2	3	4	5	6
0	Mean of	0.002	0.003	0.003	0.002	0.002	0.002
	Empirical standard errorc of	0.029	0.029	0.030	0.030	0.030	0.031
	Model-based standard errord of	0.029	0.030	0.030	0.030	0.031	0.031
	Type I errore (α = 0.05)	0.051	0.047	0.046	0.051	0.042	0.046
	Coverage (nominal = 0.95)f	0.956	0.957	0.959	0.959	0.962	0.957
−0.105	Mean of	−0.107	−0.107	−0.105	−0.105	−0.105	−0.105
	Empirical standard error of	0.034	0.035	0.035	0.035	0.035	0.036
	Model-based standard error of	0.034	0.034	0.035	0.035	0.035	0.036
	Power	0.932	0.920	0.919	0.918	0.911	0.908
	Coverage (nominal = 0.95)	0.957	0.950	0.944	0.956	0.953	0.952
−0.288	Mean of	−0.292	−0.278	−0.266	−0.258	−0.252	−0.244
	Empirical standard error of	0.048	0.046	0.046	0.045	0.046	0.047
	Model-based standard error of	0.048	0.048	0.048	0.048	0.049	0.050
	Power	1.000	1.000	1.000	1.000	1.000	1.000
	Coverage (nominal = 0.95)	0.949	0.938	0.903	0.887	0.859	0.819
−0.350	Mean of	−0.353	−0.331	−0.315	−0.302	−0.290	−0.285
	Empirical standard error of	0.053	0.050	0.050	0.049	0.050	0.052
	Model-based standard error of	0.052	0.052	0.052	0.052	0.053	0.054
	Power	1.000	1.000	1.000	1.000	1.000	1.000
	Coverage (nominal = 0.95)	0.942	0.933	0.890	0.831	0.756	0.726
0.105	Mean of	0.112	0.112	0.112	0.112	0.112	0.112
	Empirical standard error of	0.035	0.035	0.036	0.037	0.037	0.037
	Model-based standard error of	0.035	0.036	0.036	0.037	0.037	0.037
	Power	0.923	0.922	0.916	0.911	0.907	0.910
	Coverage (nominal = 0.95)	0.950	0.954	0.958	0.951	0.952	0.955
0.288	Mean of	0.293	0.287	0.284	0.283	0.280	0.278
	Empirical standard error of	0.048	0.051	0.051	0.055	0.056	0.057
	Model-based standard error of	0.049	0.050	0.051	0.053	0.054	0.055
	Power	1.000	1.000	1.000	1.000	1.000	1.000
	Coverage (nominal = 0.95)	0.957	0.947	0.943	0.934	0.928	0.927
0.350	Mean of	0.356	0.349	0.343	0.341	0.335	0.333
	Empirical standard error of	0.056	0.058	0.060	0.062	0.064	0.066
	Model-based standard error of	0.053	0.055	0.057	0.059	0.060	0.062
	Power	1.000	1.000	1.000	1.000	1.000	1.000
	Coverage (nominal = 0.95)	0.934	0.936	0.930	0.925	0.914	0.911

^a Exposure is a mixture of 20% individuals without exposure and 80% with lognormally distributed exposure with mean 0 and unit variance.

^b Pool size of 1 is the standard analysis based on unpooled or individual exposure measurements. Other pool sizes refer to the predominant value of g, with singletons included to allow for numbers of events observed that may not be multiples of g.

^c Square root of the empirical variance from 1,000 simulated data sets.

^d Square root of the average model-based variance.

^e Type I error and power based on likelihood ratio tests.

^f Nominal 95% confidence intervals were calculated by using model-based standard errors (Wald intervals).

Under the null, the parameter estimates showed no bias, and type I error rates reflected the nominal rate of 0.05. The average model-based standard error was close to the empirical standard error of the estimates. Coverage of confidence intervals was close to the nominal level of 95% for both pooled and individualized analyses. Similarly good performance of the pooled results was observed for β₁ = ±0.105, 0.288, and across pool sizes up to 4. However, the pooled data–based estimates for the larger effect sizes, with β₁ = −0.288 and ±0.350, were biased towards the null, especially for the larger pool sizes. Because of the different distributions of the number of events across time for positive and negative β_1’s, the bias was smaller for the positive than for the negative β_1’s. The powers for likelihood ratio tests for pooled analyses were comparable to those for a standard analysis. Similar (but somewhat better) behavior was observed for a standard normally distributed exposure (Web Table 1).

Adjusting for a confounder

A mixed exposure was generated in which 20% of the population had no exposure and 80% were exposed. The level of exposure among the exposed depended on a binary confounder, W, with prevalence = 0.3. Exposed individuals had a lognormal exposure U with E(ln(U)) = 0.3 × W and Var(ln(U)) = 1 in each of the W strata. The event times were generated by using the model in Web Appendix 4, Equation 1. We show the results for β₁ = 0, −0.105, and the confounder coefficient γ = −0.223 (Table 2), reflecting a one-fifth reduction in the event odds associated with the confounder for 1,000 simulations, each with data from 1,000 individuals.

Table 2.

Results Based on 1,000 Simulated Data Sets for Estimation and Testing of Risk Parameters (Lognormal Odds Ratio) β for a Continuous Exposure and γ for a Dichotomous Confounder^a Under the Proposed Pooling Design With the Pooled Logistic Model and Data from 1,000 Individuals

Parameters	Estimates	Pool Sizeb
		1	2	3	4	5	6
β1 = 0	Mean of	0.001	0.001	0.001	0.001	0.001	0.001
	Empirical standard errorc of	0.019	0.019	0.019	0.019	0.020	0.020
	Model-based standard errord of	0.018	0.018	0.018	0.018	0.018	0.019
	Type I errore (a = 0.05)	0.056	0.056	0.063	0.060	0.060	0.055
	Coverage (nominal = 0.95)f	0.942	0.949	0.939	0.942	0.942	0.943
γ = −0.223	Mean of	−0.224	−0.224	−0.224	−0.224	−0.224	−0.225
	Empirical standard error of	0.087	0.088	0.088	0.088	0.089	0.091
	Model-based standard error of	0.087	0.087	0.088	0.088	0.088	0.089
	Power	0.738	0.735	0.731	0.736	0.728	0.727
	Coverage (nominal = 0.95)	0.952	0.955	0.958	0.952	0.947	0.947
β1 = −0.105	Mean of	−0.106	−0.104	−0.102	−0.101	−0.099	−0.098
	Empirical standard error of	0.022	0.022	0.022	0.022	0.022	0.021
	Model-based standard error of	0.023	0.023	0.023	0.023	0.023	0.023
	Power	1.000	1.000	0.999	1.000	1.000	1.000
	Coverage (nominal = 0.95)	0.955	0.955	0.951	0.947	0.935	0.937
γ = −0.223	Mean of	−0.223	−0.219	−0.215	−0.213	−0.207	−0.205
	Empirical standard error of	0.091	0.092	0.092	0.093	0.093	0.094
	Model-based standard error of	0.088	0.089	0.090	0.090	0.091	0.092
	Power	0.724	0.710	0.688	0.670	0.627	0.627
	Coverage (nominal = 0.95)	0.946	0.946	0.939	0.949	0.948	0.939

^a Model with exposure and a binary confounder. The confounder W is Bernoulli with P (W = 1) = 0.3. The exposure U is lognormal with E(ln(U)) = 0.3 × W and Var(ln(U)) = 1 in each of the W strata. Negative confounder effect is assumed.

^b Pool size of 1 is standard analysis based on unpooled or individual exposure measurements. Other pool sizes refer to the predominant value of g, with singletons included to allow for numbers of events observed that may not be multiples of g.

^c Square root of the empirical variance from 1,000 simulated data sets.

^d Square root of the average model-based variance.

^e Type I error and power based on likelihood ratio tests.

^f Nominal 95% confidence intervals were calculated by using model-based standard errors (Wald intervals).

The estimates of both β₁ and γ from pooled analyses were generally comparable to the estimates from standard analyses in terms of bias, empirical variance, model-based variance, type I error, power, and coverage. The evident good behavior of the type I error documents that control for confounding was effective. The performance of the pooled analysis showed very little bias for pool sizes up to 4 but deteriorated slightly for larger pool sizes, resulting in bias towards the null and lower power. The performance worsened for larger effect sizes, but the estimates from pools of sizes 2 and 3 were comparable to those from the standard analysis (results not shown). We performed additional simulations with a continuous confounder. For a standard normal confounder, properties of the estimates were similar to those for a binary confounder (Web Table 2). For the normal confounder with mean = 0 and a larger variance of 7, whereas the model-based standard error was comparable to the empirical standard error, the estimates were more biased, resulting in less than nominal coverage (Web Table 3).

Adjusting for an effect modifier

We simulated a binary effect modifier with prevalence 0.3 by using the model in Web Appendix 4, Equation 3. The exposure distribution of the individuals was as described in the previous section. We considered studies of 1,500 women, and Table 3 shows the results for exposure main effect β₁ = 0 or ±0.1, effect modifier main effect η = −0.05, and interaction parameter θ = −0.223. Effect modifier–stratified pooling strategy turns the effect modifier into a design variable. Hence, η is not identifiable from the pooled analysis. In our simulations, both β₁ and θ were estimated well. Confidence interval coverage for β₁ and θ were generally in line with the nominal 0.95, except those for θ when β₁ was negative and pool sizes exceeded 2.

Table 3.

Results Based on 1,000 Simulated Data Sets for Estimation and Testing of Risk Parameters (Lognormal Odds Ratio) β, η, and θ for Effect Modification by a Dichotomous Effect Modifier^a and Data From 1,500 Individuals

Parameters	Estimates	Pool Sizeb
		1	2	3	4	5	6
β1 = 0	Mean of	0.000	0.000	0.000	0.000	0.000	0.000
	Empirical standard errorc of	0.020	0.020	0.021	0.021	0.021	0.021
	Model-based standard errord of	0.020	0.020	0.020	0.020	0.020	0.021
	Type I errore (α = 0.05)	0.055	0.056	0.062	0.058	0.062	0.059
	Coverage (nominal = 0.95)f	0.952	0.948	0.949	0.943	0.944	0.948
θ = −0.223	Mean of	−0.228	−0.221	−0.214	−0.209	−0.204	−0.203
	Empirical standard error of	0.049	0.048	0.048	0.048	0.049	0.049
	Model-based standard error of	0.050	0.050	0.050	0.051	0.052	0.053
	Power	1.000	1.000	1.000	0.997	0.997	0.996
	Coverage (nominal = 0.95)	0.954	0.957	0.939	0.952	0.936	0.931
β1 = −0.10	Mean of	−0.100	−0.100	−0.099	−0.098	−0.098	−0.098
	Empirical standard error of	0.022	0.023	0.022	0.023	0.023	0.024
	Model-based standard error of	0.023	0.023	0.023	0.024	0.024	0.024
	Power	0.997	0.997	0.997	0.994	0.994	0.994
	Coverage (nominal = 0.95)	0.954	0.958	0.953	0.950	0.958	0.938
θ = −0.223	Mean of	−0.225	−0.209	−0.197	−0.186	−0.179	−0.172
	Empirical standard error of	0.059	0.058	0.058	0.057	0.057	0.060
	Model-based standard error of	0.058	0.059	0.059	0.059	0.060	0.062
	Power	0.992	0.977	0.964	0.928	0.923	0.890
	Coverage (nominal = 0.95)	0.952	0.941	0.922	0.890	0.865	0.838
β1 = 0.10	Mean of	0.101	0.100	0.100	0.100	0.100	0.100
	Empirical standard error of	0.023	0.023	0.024	0.024	0.024	0.025
	Model-based standard error of	0.023	0.023	0.024	0.024	0.024	0.024
	Power	0.998	0.999	0.999	0.999	0.999	0.999
	Coverage (nominal = 0.95)	0.958	0.951	0.944	0.952	0.951	0.953
θ = −0.223	Mean of	−0.226	−0.225	−0.224	−0.222	−0.221	−0.222
	Empirical standard error of	0.045	0.045	0.045	0.045	0.046	0.047
	Model-based standard error of	0.044	0.045	0.045	0.046	0.046	0.047
	Power	1.000	1.000	1.000	1.000	0.999	1.000
	Coverage (nominal = 0.95)	0.955	0.952	0.947	0.952	0.947	0.953

^a Exposure and binary effect modifier. The effect modifier W is Bernoulli with P (W = 1) = 0.3. The exposure U is lognormal with E(ln(U)) = 0.3 × W and Var(ln(U)) = 1 in each of the W strata. Negative main effect (−0.05) of effect modifier. η = −0.05 was used for these simulations.

^b Pool size = 1 means standard analysis based on unpooled or individual exposure measurements. Other pool sizes refer to the predominant value of g, with singletons included to allow for numbers of events observed that may not be multiples of g.

^c Square root of the empirical variance from 1,000 simulated data sets.

^d Square root of the average model-based variance.

^e Type I error and power based on likelihood ratio tests.

^f Nominal 95% confidence intervals were calculated by using model-based standard errors (Wald intervals).

Power comparison for fixed sample size and a fixed number of assays

We estimated the powers for a likelihood ratio test (with a type I error rate of 0.05) for the exposure effect for a fixed sample size of 500. Figure 2A shows the power for the standard analysis (g = 1) and pooled analysis with g = 2 and 6. The power curves for g = 1, 2, and 6 are almost indistinguishable, demonstrating almost no power loss for the pooled analysis compared with individual analysis for a study with a realistic sample size.

Figure 2.

A) Power curve for fixed sample size of 500. B) Power curve for fixed number of assays of K = 300. Because the number of events in each cycle may not be divisible by g, a few singleton pools are considered in the simulations, though most of the pools are of size g (see Web Appendices for an example).

We also compared the power of pooled analysis for g = 2 and g = 6 with that of the standard analysis and fixed the number of assays, here at K = 300, rather than fixing the number of participants. Here, the standard study had 300 participants, whereas the pooled approach with g = 2 (or g = 6) incorporated specimens from 600 (or 1,800) participants. It is clear from Figure 2B that the pooled studies have substantially more power than the standard study. Hence, when assay cost dominates a study budget, pooled approaches that enroll more people and limit the number of assays can substantially outperform the standard approach.

EXAMPLE

We compared standard and pooled analysis by using data from the Collaborative Perinatal Project, which was a large study of “… the developmental consequences of complications in pregnancy and the perinatal period” (11, p. 13). Pregnant women were enrolled from 1959 to 1965 at 12 study centers across the United States and were followed through pregnancy and beyond (12). The original study investigated the association between polychlorinated biphenyls (PCBs) and 1,1-dichloro-2,2-bis(p-chlorophenyl)ethylene (DDE) with TTP (in months) by using data from 390 women, each contributing 1 pregnancy (9). We analyzed data from 388 women with full covariate information. Among them, 115 (30%) conceived in their first month at risk and 51 (13%) still had not conceived by 13 months. Early pregnancy measurements of serum PCBs and DDE were available, allowing us to compare standard analysis with reconstructed pseudopooled analysis to estimate the fecundability odds ratio.

For the pooled analysis, we considered pools of size g = 2–6 for conception in each month. We included pools of size 1 because the number of women conceiving was not always a multiple of pool size g. Because only 2 women conceived in month 10, we truncated time after the 9th month rather than the 12th for analysis, letting M = 9. Table 4 shows the TTP for these women, along with the number of pools for each scenario, (e.g., scenario 1 denoting standard analysis, scenario 2 denoting pools of sizes 2 and 1).

Table 4.

Time to Pregnancy and Pooling Configuration for 388 Women in the Collaborative Perinatal Project, United States, 1959–1965

Pooling Scenarioa	Pool Size	No. of Months to Conception										No. of Assays	Reduction, %
		1	2	3	4	5	6	7	8	9	≥10
Scenario 1	1	115	58	42	35	16	23	8	10	7	74	388
	Pr(T = k|T ≥ k)	0.30	0.21	0.20	0.20	0.12	0.19	0.08	0.11	0.09
Scenario 2	2, 1	57, 1	28, 2	20, 2	17, 1	7, 2	11, 1	3, 2	4, 2	3, 1	36, 2	202	48
Scenario 3	3, 1	38, 1	19, 1	13, 3	11, 2	5, 1	7, 2	2, 2	3, 1	2, 1	24, 2	140	64
Scenario 4	4, 1	28, 3	14, 2	10, 2	8, 3	3, 4	5, 3	1, 4	2, 2	1, 3	18, 2	118	70
Scenario 5	5, 1	22, 5	11, 3	8, 2	6, 5	3, 1	4, 3	1, 3	1, 5	1, 2	14, 4	104	73
Scenario 6	6, 1	19, 1	9, 4	6, 6	5, 5	2, 4	3, 5	1, 2	1, 4	1, 1	12, 2	93	76

^a Models are adjusted for confounders of age (continuous, centered at mean = 24.15 years, modeled as quadratic function) and smoking status (binary: yes/no).

We used a discrete-time logistic model, as did the original authors (9). For the pseudopooled analysis, we first constructed the pools of appropriate sizes by randomly partitioning the group of women who conceived in each given month. For a given partition, we constructed the pooled measurements of PCBs and DDE by adding the individual-level measurements of PCBs and DDE for the women in each pool. We also included measurements of PCBs and DDE in the same model and estimated the adjusted fecundability odds ratios by using standard and pooled analyses. We performed adjusted analyses with age, age squared, and smoking status as confounders. Tables 5 and 6 and Web Appendix 6 summarize our results.

Table 5.

Fecundability Odds Ratios Estimated From the Standard Analysis and Pooled Analysis for PCBs and DDE for Women in the Collaborative Perinatal Project, United States, 1959–1965

Scenario	Pool Size	Total PCBs (per IQR, 1.795 mg/L)				Total DDE (per IQR, 16.6 mg/L)
		Crude Fecundability OR	95% CI	Adjusteda Fecundability OR	95% CI	Crude Fecundability OR	95% CI	Adjusteda Fecundability OR	95% CI
Publishedb	1	0.89	0.79, 1.00			0.95	0.84, 1.07
Scenario 1c,d	1	0.85	0.75, 0.97	0.86	0.75, 0.98	0.93	0.82, 1.06	0.95	0.83, 1.08
Scenario 2d	2, 1	0.85	0.75, 0.97	0.86	0.76, 0.98	0.93	0.81, 1.06	0.95	0.83, 1.08
Scenario 3d	3, 1	0.84	0.73, 0.96	0.85	0.74, 0.98	0.90	0.78, 1.04	0.94	0.81, 1.09
Scenario 4d	4, 1	0.83	0.72, 0.97	0.84	0.72, 0.97	0.94	0.82, 1.07	0.96	0.84, 1.10
Scenario 5d	5, 1	0.91	0.81, 1.01	0.91	0.82, 1.01	0.91	0.79, 1.05	0.91	0.80, 1.05
Scenario 6d	6, 1	0.86	0.76, 0.98	0.87	0.76, 0.99	0.92	0.80, 1.06	0.94	0.81, 1.08

Abbreviations: CI; confidence interval; DDE, 1,1-dichloro-2,2-bis(p-chlorophenyl)ethylene; IQR, interquartile range; OR, odds ratio; PCB, polychlorinated biphenyl.

^a PCBs and DDE in the same model; no other covariates.

^b Crude fecundability odds ratio reported in Table 1 of Law et al. (Am J Epidemiol. 2005;162:1–10.) (9). Published results are based on n = 390. PCBs and DDE were rescaled by IQR.

^c Scenario 1 denotes the standard analysis based on unpooled or individual exposure measurements.

^d Scenarios 1–6 are based on n = 388.

Table 6.

Fecundability Odds Ratios Estimated From the Standard Analysis and Pooled Analysis for the Women in the Collaborative Perinatal Project, United States, 1959–1965

Parameter	Scenario (Pool Size)
	Scenario 1 (1)a (n = 388)		Scenario 2 (2,1) (n = 388)
	Adjusted Fecundability ORb	95% CI	Adjusted Fecundability ORb	95% CI
PCBs	0.967	0.899, 1.041	0.959	0.884, 1.041
DDE	0.997	0.989, 1.004	0.993	0.986, 1.001
Age	0.932	0.905, 0.960	0.920	0.893, 0.948
Age squared	1.000	0.996, 1.004	1.000	0.997, 1.003
Smoking status	0.725	0.565, 0.931	0.689	0.526, 0.903

Abbreviations: CI; confidence interval; DDE, 1,1-dichloro-2,2-bis(p-chlorophenyl)ethylene; OR, odds ratio; PCB, polychlorinated biphenyl.

^a Standard analysis based on unpooled or individual exposure measurements.

^b From a model that includes PCBs and DDE as exposures of interest and age (continuous, centered at mean = 24.15 years, modeled as quadratic function) and smoking status (binary: yes/no) as confounders.

The fecundability odds ratios estimated from the standard individual-based analyses for both exposures (n = 388; for PCBs, odds ratio = 0.85; for DDE, odds ratio = 0.93) were similar to the published results (n = 390; for PCBs, odds ratio = 0.89; for DDE, odds ratio = 0.95). The fecundability odds ratios based on reconstructed pooled analyses for the exposures were comparable to the fecundability odds ratios from standard analyses. Neither pooled nor standard analyses showed an association of DDE with TTP, with all confidence intervals including 1. In contrast, both standard and pooled analyses showed an association of PCBs with TTP in general. Confounder-adjusted analysis showed similar results for pooled and unpooled models (Table 6).

DISCUSSION

Specimen pooling is used in a wide range of applications, including estimation of disease prevalence, disease screening (1–3), genotyping (13), estimation of sensitivity and specificity of diagnostic tests (4), and estimation of exposure effect on a binary disease outcome (5, 14). Here, our goal was to extend the specimen pooling approach of Weinberg and Umbach (5) to assess exposure effect on a discrete survival-time outcome such as TTP. TTP is a well-known marker for fecundability, but TTP studies may need to rely on irreplaceable archived specimens that are also needed for other competing purposes (15). In such situations, pooling can retain statistical efficiency while conserving biospecimens.

Pooled exposure assessment has been shown to be useful for estimating individual-level odds ratios associated with exposures for data from unmatched and matched case-control studies (5, 14). The strategy we have presented here is a generalization of Weinberg and Umbach's approach for discrete-time survival outcome. TTP is a natural application because time to pregnancy is inherently discrete, as each menstrual cycle presents exactly 1 opportunity for ovulation. However, for pooling to be advantageous, the outcome under study should not be rare. Depending on the application, grouping of continuous survival times, such as in life tables, may enable the use of a pooled approach for exploring exposure effects. This approach may also be applicable to large-scale studies with existing biorepositories, registry data, or national survey data (16–18).

Our stratified pooling design, coupled with the pooled analytical model in equation 2, provides a valid method for testing the exposure effect on risk. However, under alternative hypothesis, the control pools at each time include groups of people having the same event time, and the pooling design is consequently not statistically equivalent to randomly grouped control pools. We pool individuals with similar outcomes, hence similar exposures. This strategy produces dependencies in the control pools, causing some bias toward the null in estimates of the coefficients as was confirmed in simulations. In a variety of settings for small effect sizes (|ln odds ratio| ≤ 0.2) or for pool size 2, the bias was negligible and the empirical coverage of confidence intervals was in line with the nominal coverage of 95%. The model-based standard errors were comparable to the empirical standard errors, suggesting that future efforts to reduce bias in the point estimates could improve the coverage of confidence intervals (Web Tables 4–19).

We also examined the pooled approach in the presence of an additional confounder or effect modifier and showed that odds ratio estimation performed well for small effect sizes. Following the proposed pooling, which stratifies on the potential effect modifier, the effect modifier becomes a design variable, and its main effect is not identifiable, but the interaction coefficient can be estimated, albeit with some bias. However, in our simulations, bias in estimating the exposure effect was detected for pool sizes of 2 only when effect measure modification was substantial. To illustrate the method, we contrasted the results of a pooled analysis and a standard analysis by using data from the Collaborative Perinatal Project (9) and showed that pooled analyses and standard analyses produced similar fecundability odds ratios for the effects of PCBs and DDE on TTP.

For simplicity, we have assumed that follow-up began at the same time for everyone in the study, but a prospective study may have late entry. Late entry can be accommodated by pooling individuals with the same entry and exit times and using the pools as control pools at appropriate times. If there are not many such individuals, they can be left unpooled.

If assay cost dominates the budget of a scientific study, then pooling offers an attractive option to reduce the assay cost. In exploratory analyses, pooling can also permit a panel of chemicals to be studied under a fixed assay budget. Pooling is most cost effective when the assay is very expensive compared with non­–assay-related costs per individual; the relative gain achievable by pooling depends on the relative burden imposed by assay-related cost. Moreover, when the specimens have already been archived (15), pooled analysis offers a conservative approach for judicious use of that archive.

Pooling requires the investigator to tolerate some important limitations. Akin to Weinberg and Umbach's approach (5), a proportional odds model is assumed for the outcome, incorporating logit linearity for the exposure. The proposed approach will allow for valid testing of exposure effect even when logit linearity does not hold. However, for estimation of the exposure effect, the pooling approach is limited to this proportional odds model, and estimates can be biased (beyond the bias implied by logistic regression itself) even when the model holds. The problem of accommodating a nonlinear transformation for pooled exposure remains unsolved. Because pooling groups are formed stratified on a particular outcome, secondary endpoints of interest cannot be easily handled.

Pooling has little effect on power and precision if the initial sample is large, but it does reduce the number of independent observations. To avoid this issue of a small effective sample size compared with the number of covariates in a multivariate model, the pool sizes used in a particular study should not be too large compared with the sample size and the number of covariates under consideration. Measurement error, especially if it is assay based and not specimen based, can exacerbate bias toward the null, as has been discussed by Weinberg and Umbach (5). For example, errors in including unequal amounts from each sample going into a given pool will contribute to measurement error (Web Table 20).

When a small proportion of samples fall below the lower limit of detection, pooling serves to further decrease this proportion. Suppose the exposure is distributed as a standard lognormal, and the lower limit of detection is 0.431. Then 20% of the individually measured exposures fall below the lower limit of detection. If random subjects are pooled in groups of 3, then only about 3.4% of pooled observations would fall below the lower limit of detection. Similar benefits accrue for upper limits of detection because pooling will tend to move the measured concentrations toward the middle. However, if a large proportion of specimens fall under the lower limit of detection, (e.g., if the population mean is below the lower limit of detection), then pooling would typically exacerbate the problem (8).

The best application of specimen pooling would probably be as a strategy to enable assessment of a panel of chemicals in relationship to a given event-time outcome. This strategy uses only a small amount of specimen from each sample, which spares sample for subsequent, more detailed, studies. Individual chemicals that are analytically flagged in the screen as risk related can subsequently be individual-level assayed for more flexible individual-level exposure-response analyses.

Despite the limitations discussed above, exposure analysis for discrete time-to-event data based on pooled specimen assays can be an effective strategy to screen for effects of exposures that are expensive to measure. Pooling spares valuable resources, both monetary and specimen, and can be an effective and cost-efficient alternative to traditional study designs.