Causal Effects in Twin Studies: the Role of Interference

Consider a twin study with a binary exposure $A$, where $A=1$ if the subject is exposed and $A=0$ if the subject is unexposed, and an outcome $Y$, and suppose first that there is no interference between subjects. In this setting each subject is considered to have two potential outcomes: $Y^{1}$, the outcome that the subject would have if, possibly counter to fact, they were to have the exposure; and $Y^{0}$, the outcome that the subject would have if, possibly counter to fact, they were to be unexposed. The observed outcome $Y$ is assumed to be equal to the potential outcome $Y^{1}$ for subjects who have exposure $A=1$, and equal to $Y^{0}$ for subjects with $A=0$. While only one potential outcome is observed for each twin—and hence the causal effect $Y^{1}-Y^{0}$ for an individual is never known—under additional assumptions (of positivity and exchangeability), the population average of these effects can be estimated from the observed data. Common targets of inference in twin studies include the average causal effect $E\big{[}Y^{1}-Y^{0}\big{]}$, where the mean is over all twins in the target population, and the average causal effect in the subgroup of twins who are discordant with their co-twin for the exposure.

Now suppose instead that there may be interference between the two twins in each pair, but not between twins from different twin pairs, so that each twin’s outcome may be impacted by their own exposure and their co-twin’s exposure. In this case, we cannot meaningfully talk about a twin’s outcome if they were to be exposed, or $Y^{1}$, since they might have one outcome if both they and their co-twin were to be exposed, and a different outcome if they were to be exposed but their co-twin were not. Thus, in this setting, each twin has 4 potential outcomes: $Y^{1,1}$, $Y^{1,0}$, $Y^{0,1}$, and $Y^{0,0}$, where we write $Y^{a,b}$ for the outcome that the twin would have if, possibly counter to fact, they were to have exposure $a$ and their co-twin were to have exposure $b$. For a twin who has exposure $A=a$ and whose co-twin has exposure $A=b$, the observed outcome $Y$ is assumed to be equal to the potential outcome $Y^{a,b}$, while the twin’s other 3 potential outcomes are not observed. There are a number of different causal effects that we can consider in this setting: of particular interest are average main effects $E\big{[}Y^{0,0}-Y^{1,0}\big{]}$ and $E\big{[}Y^{0,1}-Y^{1,1}\big{]}$, in which the subject’s own exposure is varied while their co-twin’s exposure is held constant; and average spillover effects $E\big{[}Y^{0,0}-Y^{0,1}\big{]}$ and $E\big{[}Y^{1,0}-Y^{1,1}\big{]}$, in which the subject’s own exposure is held constant while their co-twin’s exposure is varied.

Methods for estimating average main effects and average spillover effects have been studied by several authors. One body of research considers the setting of partial interference, in which there are multiple distinct groups of subjects and interference does not operate across different groups. See for example [5, 6, 23, 12, 14] for estimation of average main effects and average spillover effects under partial interference, and see [13, 12, 14] for asymptotic properties of the estimators. A different strand of the interference literature considers the setting where there is only one group, such as a single connected social network where interference could occur between any of the subjects. See for example [1, 26, 18, 16, 24]. The context that we consider here, namely independent groups of size two, falls into the first of these two frameworks. To the best of our knowledge, no previous work on partial interference demonstrated semi-parametric efficiency of an estimator. Here we derive semi-parametric efficient estimators for two models that are tailored to the setting of independent pairs.

In describing the data for a twin pair, we distinguish between those baseline covariates which are characteristics of the pair—and thus necessarily common between the two twins in a given pair—such as zygosity or parental characteristics; and baseline covariates which are characteristics of an individual twin and may or may not be the same for the two twins in a given pair. We refer to these respectively as shared covariates and individual covariates. In each twin pair, suppose that the twins have been randomly labeled as Twin 1 and Twin 2. The observed data for a given pair is $O=\big{(}C,X_{1},X_{2},A_{1},A_{2},Y_{1},Y_{2})$, where $C$ denotes the shared baseline covariates, $X_{j}$ denotes the individual baseline covariates for Twin $j$, and $A_{j}$ and $Y_{j}$ are the binary exposure and the outcome for Twin $j$. Throughout, $C$, $X_{1}$, and $X_{2}$ will refer to collections of measured baseline covariates. In some sections we will also consider factors which are unobserved; we will use notation such as $U$ or $U_{sh}$ when we refer to collections of variables at least some of which are unobserved. We assume that we observe data for $n$ twin pairs, and that the observed data $O_{1},\ldots,O_{n}$ for these $n$ pairs are independent and identically distributed.

We use the notation $Y_{j}^{a,b}$ for a potential outcome for Twin $j$: specifically, let $Y_{j}^{a,b}$ be the outcome that Twin $j$ would have if, possibly counter to fact, Twin $j$ were to have exposure $a$ and their co-twin were to have exposure $b$. Our primary targets of inference will be means of potential outcomes $E\big{[}Y^{a,b}\big{]}$ and contrasts of such parameters, where here the mean is taken over all twins in the population. We can also write the $E\big{[}Y^{a,b}\big{]}$ as $E\big{[}\frac{1}{2}\big{(}Y_{1}^{a,b}+Y_{2}^{a,b}\big{)}\big{]}$, where $\frac{1}{2}\big{(}Y_{1}^{a,b}+Y_{2}^{a,b}\big{)}$ is the average of the potential outcomes within a twin pair, and the last expectation is a mean taken over all pairs. We will often express $E\big{[}Y^{a,b}\big{]}$ this way, so that the units we work in are the independent twin pairs rather than the individual twins.

Here we review the co-twin control method for the setting where there is no interference between twins, following Sjölander et al. [21] and McGue et al. [15]; in Section 3 we compare the setting where there is interference.

The causal effect of the exposure $A_{j}$ on the outcome $Y_{j}$ may be confounded by any predictor $V$ that is a common cause of both $A_{j}$ and $Y_{j}$ (since there will be a non-causal source of association between $A_{j}$ and $Y_{j}$ via the path through $V$). Such a predictor could be a measured or unmeasured factor individual to Twin $j$, or a measured or unmeasured factor shared by both twins. While we can explicitly adjust for measured confounders, unobserved confounders would typically preclude identification of the causal effect. However, using the co-twin control method, all shared factors—whether measured or unmeasured—are naturally accounted for by the fact that the two twins are matched on these factors. Therefore, Sjölander et al.[21] showed, in cases where there is no unmeasured confounding due to individual factors, a causal effect is identified by adjusting for the measured individual covariates $X_{1}$ and $X_{2}$.

Let $U_{sh}$ denote the set of all confounders, including both measured and unmeasured factors, which are shared between the two twins. Consider the causal diagram in Figure 1(a), where a directed arrow means that the first variable has a possible causal impact on the second, while a bidirected arc between two variables indicates that there may be unobserved variables that are common causes of the two variables. Assume that the relationship among the variables is given by this diagram. In particular, assume that there is no interference between the two twins, as signaled by the absence of directed arrows $A_{1}\to Y_{2}$ and $A_{2}\to Y_{1}$, and assume that there are no non-shared unmeasured variables that directly impact both $A_{j}$ and $Y_{j}$.

Consider the subgroup of twins who are discordant with their co-twins for the exposure, but who have the same level $x$ of individual covariates as their co-twins. Write $E\big{[}Y^{1}-Y^{0}|A_{1}\neq A_{2},X_{1}=X_{2}=x\big{]}$ to denote the average causal effect on this subgroup. For an exposed twin in this subgroup, their potential outcome $Y^{1}$ is observed; and while their potential outcome $Y^{0}$ is not observed, their unexposed co-twin’s potential outcome $Y^{0}$ is observed. [21] show that, because of symmetry between the group of twins designated Twin 1 and the group designated Twin 2, we may use the unexposed co-twins’ outcomes as proxies for the exposed twins’ $Y^{0}$ potential outcomes, and that the causal parameter $E\big{[}Y^{1}-Y^{0}|A_{1}\neq A_{2},X_{1}=X_{2}=x\big{]}$ is equal to $E\big{[}Y_{j}|A_{j}=1,A_{3-j}=0,X_{1}=X_{2}=x\big{]}-E\big{[}Y_{j}|A_{j}=0,A_{3-j}=1,X_{1}=X_{2}=x\big{]}$, the mean difference in the observed outcome for the exposed twin and the observed outcome for the unexposed twin, within this subgroup. The latter difference can now be estimated, for example by fitting a between-within regression model as described in Sjölander et al. Thus when all individual confounders are fully observed, Sjölander et al. have shown that the within-pair coefficient in the between-within regression model has a causal interpretation, which is the causal effect for the subgroup of twins who are discordant with their co-twin for the exposure but have the same level of individual covariates as their co-twin.

Here we modify the scenario described in Section 2.3 to allow for interference between the two twins in each pair. Suppose now that the relationship among the variables is as in Figure 1(b). In particular, there may be shared factors (both measured and unmeasured) which impact both the exposures and the outcomes, but we assume that there are no unmeasured non-shared factors that directly cause both $A_{j}$ and $Y_{j}$, or that directly cause both $A_{3-j}$ and $Y_{j}$. As before, the matching between the twins on shared factors allows for identification of one subgroup causal effect: importantly, this is the effect which is estimated using the co-twin control method if there is interference present. However, we argue that this is not an effect of prime importance, and that a different approach is needed in order to identify more useful effects such as average main effects and average spillover effects.

As in Section 2.3, consider the subgroup of twins who are discordant with their co-twins for the exposure, but who have the same level $x$ of individual covariates as their co-twins. For an exposed twin in this subgroup, their potential outcome $Y^{1,0}$ is observed, and for an unexposed twin in this subgroup, their potential outcome $Y^{0,1}$ is observed. In Appendix A, we prove that, under the assumptions listed there, the mean of the contrast $Y^{1,0}-Y^{0,1}$ on this subgroup, $E\big{[}Y^{1,0}-Y^{0,1}|A_{1}\neq A_{2},X_{1}=X_{2}=x\big{]}$, is equal to $E\big{[}Y_{j}|A_{j}=1,A_{3-j}=0,X_{1}=X_{2}=x\big{]}-E\big{[}Y_{j}|A_{j}=0,A_{3-j}=1,X_{1}=X_{2}=x\big{]}$. Note that the latter difference is the same quantity that appears in Section 2.3, and which is estimated using a between-within regression model, but that the causal interpretation of this parameter is different in cases where there is interference between twins. The different interpretations for the two settings are highlighted in Table 1. The effect $E\big{[}Y^{1,0}-Y^{0,1}|A_{1}\neq A_{2},X_{1}=X_{2}=x\big{]}$ identified here is the average difference in twins’ outcomes that we would see if we could intervene to change the twins from unexposed to exposed, while conversely intervening to change their co-twins from exposed to unexposed, in the subgroup described above. It is difficult to see why one would want to target this particular combination of interventions. The contrast $Y^{1,0}-Y^{0,1}$ is the difference of the spillover effect $Y^{0,0}-Y^{0,1}$ and the main effect $Y^{0,0}-Y^{1,0}$; however we cannot tease apart these two effects, and the value of $Y^{1,0}-Y^{0,1}$ itself is not readily interpretable. For example, a zero value of $Y^{1,0}-Y^{0,1}$ could reflect the fact that $Y^{1,0}=Y^{0,0}=Y^{0,1}$, or it could reflect a qualitatively different scenario where $Y^{0,0}-Y^{0,1}$ and $Y^{0,0}-Y^{1,0}$ are each nonzero but cancel each other out. That is, a null value of $Y^{1,0}-Y^{0,1}$ is equally compatible with the exposure having no causal effect, or with the presence of very strong interference.

The co-twin control method is a unique tool which allows for estimation of a causal effect even with shared unmeasured confounders, based on the use of discordant pairs. However, we cannot identify contrasts involving $Y^{1,1}$ or $Y^{0,0}$ from discordant pairs when interference is present, since these potential outcomes need not equal the observed outcome of either twin in a discordant pair. Therefore, the presence of shared unmeasured confounders poses a greater barrier than it does in settings with no interference, since the co-twin control method does not provide a means of estimating important causal effects for the interference setting. In order to identify average main effects and average spillover effects, throughout the rest of the paper we work under the assumption that there is no unmeasured confounding due to either individual or shared factors.

Throughout the rest of the paper we make the following assumption of no unmeasured confounding: there are no unmeasured factors, whether shared or non-shared, which directly cause both $A_{j}$ and $Y_{j}$, or that directly cause both $A_{3-j}$ and $Y_{j}$. Specifically, we assume that any unmeasured factors $U$ which impact both an outcome and an exposure do so only through the measured baseline covariates $C$, $X_{1}$, and $X_{2}$. Under this assumption, adjusting for the measured baseline covariates $C,X_{1},X_{2}$ controls for all confounding of the effects of $A_{j}$ and $A_{3-j}$ on $Y_{j}$. This is an untestable assumption which is not automatically satisfied by design in an observational study; how reasonable the assumption is in a given study will depend on factors specific to that study, including how rich a set of baseline covariates is measured.

Consider the four groups of twin pairs with the four exposure patterns $(A_{1}=1,A_{2}=1)$, $(A_{1}=1,A_{2}=0)$, $(A_{1}=0,A_{2}=1)$, and $(A_{1}=0,A_{2}=0)$, and consider a specific potential outcome $Y_{j}^{a,b}$. In general the potential outcomes $Y_{j}^{a,b}$ could be systematically higher among one of these four groups than another. For example they could be higher among the $(A_{1}=1,A_{2}=1)$ group than among the $(A_{1}=0,A_{2}=0)$ group if having some predictor $V$ causes both exposures and potential outcomes to be higher. However, our assumption of no unmeasured confounding implies that adjusting for the measured baseline covariates breaks any such association between $Y_{j}^{a,b}$ and the exposures, and that within levels of the measured baseline covariates $C,X_{1},X_{2}$, the four groups are exchangeable in terms of potential outcomes $Y_{j}^{a,b}$. This assumption of no unmeasured confounding, or exchangeability, is given by:

We additionally make the positivity assumption that, within each level of the baseline covariates, there is a nonzero probability of having each of the 4 exposure patterns, and the consistency assumption that a twin’s observed outcome $Y_{j}$ is equal to the twin’s potential outcome corresponding to the exposures actually received by the the twin and their co-twin:

The assumptions of exchangeability, positivity, and consistency are sufficient for identification of the parameters $E\big{[}Y_{j}^{a,b}\big{]}$. That is, under these three assumptions, we can express the causal parameter $E\big{[}Y_{j}^{a,b}\big{]}$ as a function of the observed data, as we show for completeness below. Exchangeability and positivity allow us to take the mean over just the group with the exposure pattern $(A_{j}=a,A_{3-j}=b)$ rather than over all twins labeled as Twin $j$ in the population, within each level of the baseline covariates; and consistency implies that, among the twins in this group, the potential outcome $Y_{j}^{a,b}$ is equal to the observed outcome $Y_{j}$.

We will consider two models for the data for each twin pair. The larger of these, Model 1, makes only the assumptions used for identification above, and corresponds to the diagram in Figure 2(a). Here $U$ represents any unmeasured factors (shared or not). The absence of arrows pointing directly from $U$ to the exposures and the outcomes corresponds to the no unmeasured confounding assumption. Model 2 is a smaller model in which we make three extra assumptions in addition to the identification assumptions, and corresponds to the diagram in Figure 2(b). These three extra assumptions, A4-A6, are that Twin $j$’s individual covariates do not have a causal impact on their co-twin’s exposure (as seen by the lack of a directed arrow $X_{j}\to A_{3-j}$), or on their co-twin’s outcome (as seen by the lack of a directed arrow $X_{j}\to Y_{3-j}$); and that Twin 1’s exposure and Twin 2’s exposure are conditionally independent given the measured shared and individual baseline covariates (as seen by the lack of a bidirected arc $A_{1}\leftrightarrow A_{2}$).

The assumption that Twin $j$’s individual-level covariates do not impact their co-twin’s exposure or outcome is one that is commonly used in the twin literature [21], and the distinction drawn in Model 2 between the individual and the shared covariates is a feature that distinguishes Model 2 from models considered elsewhere in the interference literature. While Model 1, being less restrictive, gives valid inference in a wider range of settings than Model 2, the advantage of Model 2 is that it allows for improved (asymptotic) efficiency: in settings which meet the assumptions posited for Model 2, we may leverage these additional assumptions to make a more efficient use of the data in estimating our causal parameters of interest, allowing for narrower confidence intervals in large samples. We demonstrate this improved efficiency in a simulation study in Section 6.

Here we derive the efficient estimator of the parameter $\beta^{a,b}=E\big{[}Y^{a,b}\big{]}$ for each of the two models described in Section 3.2. That is, we derive the estimator $\widehat{\beta}_{1}^{a,b}$ with the smallest asymptotic variance, out of all estimators for $\beta^{a,b}$ which are regular and asymptotically linear (RAL) under every distribution in Model 1, and similarly for Model 2. Since Model 2 is a smaller model contained in Model 1, any RAL estimator for Model 1 may be used in Model 2, while the converse need not hold; and we will see that, in fact, there are RAL estimators for Model 2 that are more efficient than any Model 1 estimator.

RAL estimators are asymptotically normal with asymptotic variance determined by their influence function. In order to obtain the RAL estimator with the smallest possible asymptotic variance, we first derive the efficient influence function $\varphi_{k}(O;\beta^{a,b})$ for the parameter $\beta^{a,b}$ in each Model $k$. The efficient estimator $\widehat{\beta}_{k}^{a,b}$ based on data $O_{1},\ldots,O_{n}$ from $n$ independent twin pairs is then found as the solution to the estimating equation $\sum_{i=1}^{n}\varphi_{k}(O_{i};\beta^{a,b})=0$. See Tsiatis [25] for more on efficient influence functions.

The efficient influence function for $\beta^{a,b}=E\big{[}Y^{a,b}\big{]}$ in Model 1 is:

Proofs are given in Appendix B. In order to use $\varphi_{1}\big{(}O;\beta^{a,b}\big{)}$ to obtain an estimator for $\beta^{a,b}$, we need a model for the joint propensity score $P(A_{j}=a,A_{3-j}=b|C,X_{j},X_{3-j})$ and a model for the outcome regression $E\big{[}Y_{j}|A_{j},A_{3-j},C,X_{j},X_{3-j}\big{]}$. The resulting estimator of $\beta^{a,b}$ will be efficient provided that both of these models are correctly specified, and provided that the estimated values converge to the truth at fast enough rates. (See Section 4.2 for more discussion of rates.) Suppose this is the case. Let $\hat{\pi}_{a,b}(C_{i},X_{ij},X_{i,3-j})$ be the predicted propensity score for a twin pair with covariates $C_{i},X_{ij},X_{i,3-j}$, and let $\hat{\mu}_{j,a,b}(C,X_{ij},X_{i,3-j})$ be the predicted outcome regression for Twin $j$ in a twin pair with covariates $C_{i},X_{ij},X_{i,3-j}$ if the twins’ exposures were set to $A_{j}=a,A_{3-j}=b$. Then the efficient estimator for $\beta^{a,b}$ in Model 1, based on data $O_{1},\ldots,O_{n}$, is given by:

The estimator $\widehat{\beta}_{1}^{a,b}$ is the augmented inverse probability weighted estimator for a bivariate exposure. It is a doubly robust estimator [20]: as long as at least one of the propensity score model or the outcome regression model is correctly specified, $\widehat{\beta}_{1}^{a,b}$ remains a consistent estimator for $\beta^{a,b}$, even if the other model is misspecified. Liu et al. [14] have presented three doubly robust estimators of average main effects and average spillover effects in groups of size $n$, working in the analog of Model 1. Our estimator $\widehat{\beta}_{1}^{a,b}$ corresponds to one of their estimators specialized to groups of size 2. Our contribution as regards Model 1 is to prove that this estimator is semiparametric efficient in Model 1, thus providing a partial answer to a question posed in Liu et al. [14]. To the best of our knowledge, Model 2 is distinct from other models that have been considered in the interference literature.

If the true distribution lies inside the smaller Model 2, a more efficient estimator than $\widehat{\beta}_{1}^{a,b}$ is possible. The efficient influence function for $\beta^{a,b}$ in Model 2 is:

In order to use $\varphi_{2}(O;\beta^{a,b})$ to obtain an estimator of $\beta^{a,b}$, we need a model for the outcome regression $E\big{[}Y_{j}|A_{j},A_{3-j},C,X_{j}\big{]}$, a model for the propensity score $P(A_{j}=1|C,X_{j})$ which relates Twin $j$’s exposure to their own covariates, and a model for the propensity score $P(A_{j}=1|C,X_{3-j})$ which relates Twin $j$’s exposure to their co-twin’s covariates. The resulting estimator of $\beta^{a,b}$ will be efficient provided that all three of these models are correctly specified, and provided that the estimated values converge to the truth at fast enough rates. Suppose this is the case. Let $\hat{\pi}_{j,a}(C_{i},X_{ij})$ be the predicted value of the propensity score $P(A_{j}=a|C,X_{j})$ for a twin pair with covariates $C_{i},X_{ij}$. Let $\hat{\theta}_{j,a}(C_{i},X_{i,3-j})$ be the predicted value of the propensity score $P(A_{j}=a|C,X_{3-j})$ for a twin pair with covariates $C_{i},X_{i,3-j}$. Let $\hat{\mu}_{j,a,b}(C,X_{ij})$ be the predicted outcome regression for Twin $j$ in a twin pair with covariates $C_{i},X_{ij}$ if the twins’ exposures were set to $A_{j}=a,A_{3-j}=b$. Then the efficient estimator for $\beta^{a,b}$ in Model 2, based on data $O_{1},\ldots,O_{n}$, is given by:

The estimator $\widehat{\beta}_{2}^{a,b}$ is also doubly robust: it is consistent if (i) both propensity score models are correct, even if the outcome regression model is incorrect, or (ii) the outcome regression model is correct, even if one or both propensity score models are incorrect. We show the double robustness of both estimators in Appendix C, and we also illustrate this property in the simulation study in Section 6.

Efficient influence functions of average main effects and average spillover effects are obtained as differences of efficient influence functions of the $\beta^{a,b}$ parameters. For example, the efficient influence function of the spillover effect $\beta_{sp}=\beta^{0,0}-\beta^{0,1}$ in Model $k$ is $\varphi_{k}(O;\beta^{0,0})-\varphi_{k}(O;\beta^{0,1})$. Similarly the efficient estimator of $\beta_{sp}$ in Model $k$ is $\widehat{\beta}^{0,0}_{k}-\widehat{\beta}^{0,1}_{k}$.

Here we consider confidence intervals for a parameter $\beta^{a,b}=E\big{[}Y^{a,b}\big{]}$ or a linear combination of such parameters, such as an average spillover effect or average main effect, based on the efficient estimators presented above.

Denote the parameter of interest by $\beta$. Let $\psi_{k}(O;\beta,\nu)$ denote the efficient influence function of $\beta$ in Model $k$, where $\nu$ represents the parameters of the propensity score models and outcome regression model, which must be estimated in order to obtain the efficient estimator for $\beta$. Under the assumption that the parameters $\nu$ are estimated consistently at fast enough rates, the resulting estimator for $\beta$ will be asymptotically normal at root-$n$ rates. Therefore, we may use a Wald-type confidence interval for $\beta$. Estimating $\nu$ at rates faster than $n^{-1/4}$—that is, using an estimator $\widehat{\nu}$ such that $n^{1/4+\epsilon}\big{(}\widehat{\nu}-\nu\big{)}$ is bounded in probability for some $\epsilon>0$—is sufficient. However, this can be relaxed somewhat since our estimator for $\beta$ is doubly robust, and the bias of a doubly robust estimator is the product of the bias in the propensity score estimation times the bias in the outcome regression estimation. Therefore it suffices that we estimate the propensity scores and outcome regression at rates whose product is less than $n^{-1/2}$. Suppose this is the case, and let $\widehat{\beta}_{k,eff}$ be the solution of the estimating equation $\sum_{i=1}^{n}\psi_{k}\big{(}O_{i};\beta,\widehat{\nu}\big{)}=0$. Because of the assumption on the rate of convergence for $\widehat{\nu}$, the influence function of $\widehat{\beta}_{k,eff}$ is the efficient influence function $\psi_{k}\big{(}O;\beta,\nu\big{)}$ (with the true value of the nuisance parameters $\nu$). Therefore $\widehat{\beta}_{k,eff}$ is the efficient estimator of $\beta$, and the asymptotic variance of $\widehat{\beta}_{k,eff}$ is the variance of $\psi_{k}\big{(}O;\beta,\nu\big{)}$.

Thus in large samples, the variance of $\widehat{\beta}_{k,eff}$ is approximately $\frac{1}{n}Var\big{(}\psi_{k}(O;\beta,\nu)\big{)}=\frac{1}{n}E\big{[}\psi_{k}(O;\beta,\nu)^{2}\big{]}$. A consistent estimator of $Var\big{(}\psi_{k}(O;\beta,\nu)\big{)}$ is $\frac{1}{n}\sum_{i=1}^{n}\psi_{k}\big{(}O_{i};\widehat{\beta}_{eff},\hat{\nu}\big{)}^{2}$. Therefore, a large-sample $95\%$ Wald-type confidence interval for $\beta$ is given by:

Alternatively, we may use a bootstrap-based confidence interval, which may have better coverage than the Wald-type confidence interval at moderate sample sizes.