# Quantification of vaccine waning as a challenge effect

Matias Janvin1,∗, Mats J. Stensrud2 1Oslo Centre for Biostatistics and
Epidemiology, University of Oslo, Norway  2Department of Mathematics, École
Polytechnique Fédérale de Lausanne, Switzerland

###### Abstract.

Knowing whether vaccine protection wanes over time is important for health
policy and drug development. However, quantifying waning effects is difficult.
A simple contrast of vaccine efficacy at two different times compares
different populations of individuals: those who were uninfected at the first
time versus those who remain uninfected until the second time. Thus, the
contrast of vaccine efficacy at early and late times can not be interpreted as
a causal effect. We propose to quantify vaccine waning using the challenge
effect, which is a contrast of outcomes under controlled exposures to the
infectious agent following vaccination. We identify sharp bounds on the
challenge effect under non-parametric assumptions that are broadly applicable
in vaccine trials using routinely collected data. We demonstrate that the
challenge effect can differ substantially from the conventional vaccine
efficacy due to depletion of susceptible individuals from the risk set over
time. Finally, we apply the methods to derive bounds on the waning of the
BNT162b2 COVID-19 vaccine using data from a placebo-controlled randomized
trial. Our estimates of the challenge effect suggest waning protection after 2
months beyond administration of the second vaccine dose.

Keywords. Causal inference, Challenge trials, Randomized trials, Sharp bounds

††footnotetext: ∗This work was done while the author was a PhD student at
École Polytechnique Fédérale de Lausanne

##  1\. Introduction

There are two prevailing approaches for quantifying vaccine waning. One
approach is to use immunological assays to measure antibody levels after
vaccination, and then use these measurements as a surrogate variable to infer
the degree of vaccine protection (Levin et al., 2021). However, measurement of
antibodies can fail to detect immunity, e.g. due to resident memory cells, and
therefore can be insufficient to fully characterize immunity from prior
vaccination or infection (Bergwerk et al., 2021; Khoury et al., 2021; Rubin et
al., 2022).

A second approach is to contrast interval-specific cumulative incidences (CI)
of infectious outcomes across vaccine and placebo recipients in randomized
controlled trials (RCTs) by computing the vaccine efficacy (VE), usually
defined as one minus the ratio of cumulative incidences during a given time
interval. Waning is quantified from direct observations of infection related
events, rather than immunological surrogate markers. In this context, it is
conventional to define vaccine waning as the decline over time of the VE
(Halloran et al., 1999, 1997, 2012; Follmann et al., 2020, 2021, 2022; Fintzi
and Follmann, 2021; Lin et al., 2021; Tsiatis and Davidian, 2022).

Estimands that quantify how the accrual of infectious outcomes changes over
time are important when deciding booster vaccination regimes, see e.g.
Goldberg et al. (2021). Similarly, empirical evidence of vaccine waning is
also important to decide when to schedule seasonal vaccines; for example, when
influenza vaccine protection wanes, these vaccines should be administered
close to the time of the influenza wave (Ray et al., 2019). Making such
decisions based on conventional VE estimands is problematic because the VE at
two different times compares different populations of individuals: those who
were uninfected at the first time versus those who remain uninfected until the
second time. Thus, the VE could decline over time only due to a depletion of
susceptible individuals (Lipsitch et al., 2019; Ray et al., 2020; Halloran et
al., 2012; Kanaan and Farrington, 2002; Hudgens et al., 2004).

As stated by Halloran et al. (1997), “[an] open challenge is that of
distinguishing among the possible causes of time-varying [VE] estimates.”
Smith et al. (1984) described two models of stochastic individual risk
illustrating distinct mechanisms by which VE can decline over time, later
known as the “leaky” versus “all-or-nothing” models (Halloran et al., 1992),
which were generalized to the “selection model” and “deterioration model”,
respectively (Kanaan and Farrington, 2002). These models parameterize
individual risk of infection by introducing an unmeasured variable encoding
the state of an individual’s vaccine response, but rely on strong parametric
assumptions that the investigators may be unwilling to adopt.

In this work, we propose to formally define waning in a causal (potential
outcomes) framework as a “challenge effect”. This effect is defined with
respect to interventions on both vaccination and exposure to the infectious
agent, which in principle can be realized in a future experiment. An
interventionist definition of vaccine waning is desirable because it is
closely aligned with health policy decisions (Robins et al., 2021; Richardson
and Robins, 2013) and establishes a language for articulating testable claims
about vaccine waning. Furthermore, the challenge effect can guide development
of new vaccines, say, to achieve a longer durability of protection.

The challenge effect can, in principle, be identified by executing a challenge
trial where the exposure to the infectious agent is controlled by the
trialists. However, conducting such challenge trials is often unethical and
infeasible (Hausman, 2021), in particular in vulnerable subgroups for which we
may be most interested in quantifying vaccine protection. Thus, one of our
main contributions is to describe assumptions that partially identify the
challenge effect under commonly arising data structures, such as conventional
randomized placebo controlled vaccine trials, where individuals are exposed to
the infectious agent through their community interactions. The identification
results do not require us to measure community exposure status, which is often
difficult to ascertain and therefore often not recorded in trial data.

###  1.1. Motivating example: COVID-19 vaccines

The safety and efficacy of the vaccine BNT162b2 against COVID-19 was tested in
a RCT that assigned 22,085 individuals to receive the vaccine and 22,080
individuals to receive placebo. The trial recorded infection times and adverse
reactions after vaccination. An overall vaccine efficacy of $0.913\
(95\%\text{ CI: }0.890-0.932)$ was reported, computed as one minus the
incidence rate ratio of laboratory confirmed COVID-19 infection at 6 months of
follow-up in individuals with no previous history of COVID-19. However, the
interval-specific vaccine efficacy was as high as $0.917\ (0.796,0.974)$ in
the time period starting 11 days after receipt of first dose up to receipt of
second dose, and later fell to $0.837\ (0.747,0.899)$ after 4 months past the
receipt of the second dose. One possible explanation for the difference in
estimates between these two time periods is that the vaccine protection
decreased (waned) over time. However, the difference might also be explained
by a depletion of individuals who were susceptible to infection during time
interval 1; more susceptible individuals were depleted in the placebo group
compared to the vaccine group, which could have reduced the hazard of
infection in the placebo group during interval 2 and thereby led to a smaller
VE at later times. This observation prompts a question that we address in this
work: does the protection of BNT162b2 wane over time, and if so, by how much?

##  2\. Observed data structure

Consider a study where individuals are randomly assigned to treatment arm
$A\in\\{0,1\\}$, such that $A=0$ denotes placebo and $A=1$ denotes vaccine.
Suppose that individuals are followed up over two time intervals
$k\in\\{1,2\\}$, where the endpoint of interval 1 coincides with the beginning
of interval 2. In Appendix E, we consider extensions to $K\geq 2$ time
intervals and losses to follow-up. Let $Y_{k}\in\\{0,1\\}$ indicate whether
the outcome of interest has occurred by the end of interval $k$, e.g. COVID-19
infection confirmed by nucleic acid amplification test in the COVID-19
example. Then, $\Delta Y_{k}=Y_{k}-Y_{k-1}$ is an indicator that the outcome
occurred during interval $k$, and we define $Y_{0}=0$. Finally, let $L$ denote
a vector of baseline covariates. We assume that the data are generated under
the Finest Fully Randomized Causally Interpretable Structured Tree Graph
(FFRCISTG) model (Richardson and Robins, 2013; Robins and Richardson, 2011;
Robins, 1986), which generalizes the perhaps more famous Non-Parametric
Structural Equation Model with Independent Errors (NPSEM-IE).111Based on the
FFRCISTG model, we let causal DAGs encode single world independencies between
the counterfactual variables. In particular, the FFRCISTG model includes the
NPSEM-IE as a strict submodel (Richardson and Robins, 2013; Robins, 1986;
Pearl, 2009). Because all estimands and identification assumptions in this
manuscript are single world, it would also be sufficient, but not necessary,
to assume that data are generated from an NPSEM-IE model (Pearl, 2009).
Similar to most vaccine trials (Tsiatis and Davidian, 2022; Halloran et al.,
1996), we will assume that there is no interference between individuals,
because they are drawn from a larger study population and therefore infectious
contacts between the trial participants are negligible. In Appendix A, we
clarify that it is possible to interpret the challenge effect in a trial with
no interference as being equivalent to a challenge effect in a (physical)
target population with interference. The observed variables are illustrated
using a causal directed acyclic graph (DAG) in Figure 1.

$A$$E_{1}$$E_{2}$$\Delta Y_{1}$$\Delta Y_{2}$$L$$U_{Y}$$U_{E}$

Figure 1. Causal DAG illustrating a data generating mechanism for the observed
variables

##  3\. Questions and estimands of interest

Let $\Delta Y_{1}^{a,e_{1}=1}$ be a counterfactual indicator of the outcome
$\Delta Y_{1}$, had individuals been given treatment $A=a$ at baseline and
subsequently, in time interval 1, been exposed to an infectious inoculum
through a controlled procedure ($e_{1}=1$). Furthermore, let $\Delta
Y_{2}^{a,e_{1}=0,e_{2}=1}=Y_{2}^{a,e_{1}=0,e_{2}=1}-Y_{1}^{a,e_{1}=0}$ be the
counterfactual outcome under an intervention that assigns treatment $A=a$,
then isolates the individual from the infectious agent during time interval 1
($e_{1}=0$) and finally exposes the individual to an infectious inoculum in
the same controlled manner at the beginning of time interval 2 ($e_{2}=1$).

We define the conditional challenge effect during time intervals 1 and 2,
respectively, by

$\displaystyle\text{VE}_{1}^{\mathrm{challenge}}(l)=1-\frac{E[\Delta
Y_{1}^{a=1,e_{1}=1}\mid L=l]}{E[\Delta Y_{1}^{a=0,e_{1}=1}\mid
L=l]}\leavevmode\nobreak\ ,$ (1)
$\displaystyle\text{VE}_{2}^{\mathrm{challenge}}(l)=1-\frac{E[\Delta
Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid L=l]}{E[\Delta Y_{2}^{a=0,e_{1}=0,e_{2}=1}\mid
L=l]}\leavevmode\nobreak\ .$

The challenge effect quantifies the mechanism by which the vaccine exerts
protective effects, outside of pathways that involve changes in exposure
pattern, by targeting hypothetical challenge trials where an infectious
challenge is administered after an isolation period (versus no isolation) in
vaccinated individuals. The practical relevance of the challenge effect is,
e.g., illustrated by the concrete proposal of Ray et al. (2020), who suggested
to study waning of influenza vaccines by enrolling participants to receive a
vaccine during a random week from August to November, and then contrasting the
incidence of influenza infection between recently and remotely vaccinated
individuals. Monge et al. (2023) and Hernán and Monge (2023) proposed a
related hypothetical challenge trial to describe selection bias in
quantification of immune imprinting of COVID-19 vaccines. However, while these
challenge trials are rarely conducted, to our knowledge, previous work has not
considered identification and estimation of such estimands from conventional
vaccine trials. In Sections 4-5, we clarify how to identify and estimate the
challenge effect using routinely collected data from conventional vaccine
trials.

We denote the conventional (observed) vaccine efficacy estimands by

$\displaystyle\textrm{VE}_{1}^{\mathrm{obs}}(l)=1-\frac{E[\Delta Y_{1}\mid
A=1,L=l]}{E[\Delta Y_{1}\mid A=0,L=l]}\leavevmode\nobreak\ ,$ (2)
$\displaystyle\textrm{VE}_{2}^{\mathrm{obs}}(l)=1-\frac{E[\Delta
Y_{2}\mid\Delta Y_{1}=0,A=1,L=l]}{E[\Delta Y_{2}\mid\Delta
Y_{1}=0,A=0,L=l]}\leavevmode\nobreak\ .$

To reduce clutter, we will write $\textrm{VE}_{k}^{\mathrm{challenge}}$ and
$\text{VE}_{k}^{\mathrm{obs}}$ for the challenge effect and observed vaccine
efficacy at time $k$, omitting the argument $l$. However, in general, both
quantities could vary with $l$. For a given controlled exposure to the
infectious agent ($e_{k}=1$), the challenge effect does not change with
infection prevalence. In contrast, $\text{VE}_{1}^{\mathrm{obs}}$ can depend
on the prevalence of infection in the communities of the trial participants
(Struchiner and Halloran, 2007).

We take the position that “waning” refers to a contrast of counterfactual
outcomes under different interventions, as formalized in the following
definition.

######  Definition 1 (Challenge waning).

$\displaystyle\text{VE}_{1}^{\mathrm{challenge}}>\text{VE}_{2}^{\mathrm{challenge}}\leavevmode\nobreak\
.$

We say that the vaccine effect wanes from interval 1 to interval 2 if the
challenge effect decreases from interval 1 to interval 2.

Importantly,
$\text{VE}_{1}^{\mathrm{challenge}}\neq\text{VE}_{2}^{\mathrm{challenge}}$
does not imply, nor is it implied by a change in a conventional vaccine
efficacy measure,
$\text{VE}_{1}^{\mathrm{obs}}\neq\text{VE}_{2}^{\mathrm{obs}}$. Thus, in the
COVID-19 example it is not sufficient to know that
$\text{VE}^{\mathrm{obs}}_{k}$ decreased over time in order to ascertain that
the vaccine protection has waned. We illustrate this point by simulating data
generating mechanisms with different values of $\text{VE}_{k}^{\mathrm{obs}}$
and $\text{VE}_{k}^{\mathrm{challenge}}$ in the Supplementary Material.

So far we have introduced a hypothetical exposure intervention without
characterizing in detail the properties of such an intervention. In the next
section, we describe a list of properties that the exposure intervention
should satisfy, give examples of real life challenge trials that plausibly
meet these conditions, and present examples where the conditions fail.

###  3.1. Exposure interventions

Returning to the COVID-19 example, we will now outline a hypothetical trial
for the joint intervention $(a,e_{1},e_{2})$. Suppose that assignment to
vaccine versus placebo is blinded, and that the intervention $e_{k}=0$ for
$k\in\\{1,2\\}$ denotes perfect isolation from the infectious agent, for
example by confining individuals under $e_{k}=0$ such that they are not in
contact with the wider community. Suppose further that $e_{k}=1$ denotes
intranasal inoculation by pipette at the beginning of time interval $k$ with a
dose of virus particles that is representative of a typical infectious
exposure in the observed data; the controlled procedure could, e.g., be
similar to the COVID-19 challenge experiment described by Killingley et al.
(2022). Furthermore, let $E_{k}=1$ be an (unmeasured) indicator that an
individual in the observed data is exposed to a load of virus particles that
exceeds a threshold believed to be necessary to develop COVID-19 infection. We
will use a hypothetical trial with this definition of $E_{k}$ to illustrate a
set of assumptions that characterize the exposure intervention.

######  Assumption 1 (Consistency).

We assume that interventions on treatment $A$ and exposures $E_{1},E_{2}$ are
well-defined such that the following consistency conditions hold for all
$a,e_{1},e_{2}\in\\{0,1\\}$:

  1. (i)

$\text{ if }A=a\text{ then }E_{1}=E_{1}^{a},\Delta Y_{1}=\Delta
Y_{1}^{a},E_{2}=E_{2}^{a},E_{2}^{e_{1}=0}=E_{2}^{a,e_{1}=0},\Delta
Y_{2}=\Delta Y_{2}^{a},$ $\Delta Y_{2}^{e_{1}=0}=\Delta
Y_{2}^{a,e_{1}=0}\leavevmode\nobreak\ ,$

  2. (ii)

$\text{ if }A=a,E_{1}=e_{1}\text{ then }\Delta Y_{1}=\Delta
Y_{1}^{a,e_{1}},E_{2}=E_{2}^{a,e_{1}},\Delta Y_{2}=\Delta
Y_{2}^{a,e_{1}}\leavevmode\nobreak\ ,$

  3. (iii)

$\text{ if }A=a,E_{2}^{a,e_{1}=0}=e_{2}\text{ then }\Delta
Y_{2}^{a,e_{1}=0}=\Delta Y_{2}^{a,e_{1}=0,e_{2}}\leavevmode\nobreak\ .$

Assumption 1 implicitly subsumes that the counterfactual outcomes of one
individual do not depend on the treatment of another individual (Pearl, 2010),
i.e. no interference. We discuss the assumption of no interference further in
Appendix A. Consistency assumptions are routinely invoked when doing causal
inference (Hernán and Robins, 2020) and requires that the target trial
exposure produces the same outcomes as the exposures that occurred in the
observed data. In other words, the intervention $e_{1}=1$ must be
representative of the observed exposures for individuals with $E_{1}=1$, and
similarly for time interval 2. However, Assumption 1 does not specify exactly
what this representative exposure is, i.e. what the dose of the viral inoculum
is in the target challenge trial.

While routinely invoked, consistency can be violated if multiple versions of
exposure, which have different effects on future outcomes, are present in the
data (Hernán, 2016). For the motivating exposure intervention, this could
happen if there exist subgroups that are exposed to substantially different
viral loads compared to the rest of the population, and if the risk of
acquiring infection is highly sensitive to such differences in viral load. The
same ambiguity would occur if there are substantial variations in the number
of exposures per individual within each time interval.

Appendix D discusses how Assumption 1 can be weakened under multiple treatment
versions, building on VanderWeele (2022); VanderWeele and Hernán (2013). In
particular, we show that an analogous identification argument holds when the
number of viral particles in the controlled inoculum is a random variable
sampled from a suitable distribution, or when the viral inoculum has a
constant representative size that exists in a non-trivial class of settings.
It is possible to test the strict null hypothesis that the vaccine does not
wane under any (observed) size of viral inoculum by assuming that the
distribution of viral inocula amongst exposed individuals remains the same
between intervals $k=1$ and $k=2$. This is closely related to the “Similar
Study Environment” assumption adopted by Fintzi and Follmann (2021), who give
several examples of changes in study environment that could lead to changing
$\text{VE}^{\mathrm{obs}}$ over time; for example, changes in viral strands
over time, or a change in mask wearing behavior that could lead to different
viral load exposures at different times.

Violations of Assumption 1 can be mitigated by adopting a blinded crossover
trial design (Follmann et al., 2021), where individuals are randomized to
vaccine or placebo at baseline and subsequently receive the opposite treatment
after a fixed interval of time. In such trials, one can minimize differences
in background infection prevalence or viral load per exposure between recent
versus early recipients of the active vaccine by contrasting the cumulative
incidence of outcomes during the same interval of calendar time (Lipsitch et
al., 2019; Ray et al., 2020).

To establish a relation between exposures and outcomes, we introduce the
following assumption.

######  Assumption 2 (Exposure necessity).

For all $a\in\\{0,1\\}$ and $k\in\\{1,2\\}$,

$\displaystyle E^{a}_{k}=0\implies\Delta Y_{k}^{a}=0\text{ and
}E_{2}^{a,e_{1}=0}=0\implies\Delta Y_{2}^{a,e_{1}=0}=0\leavevmode\nobreak\ .$

The exposure necessity assumption (Stensrud and Smith, 2023) states that any
individual who develops the infection, must have been exposed. Standard
infectious disease models typically express the infection rate as a product of
a contact rate and a per exposure transmission probability, see e.g. (2.14) in
Halloran et al. (2012) or (2) in Tsiatis and Davidian (2022). Such models not
only imply that exposure is necessary for infection, but also impose strong
parametric assumptions on the infection transmission mechanism, and it is not
clear how these parametric assumptions can be empirically falsified. In
contrast, exposure necessity can be falsified by observing whether any
individuals develop the outcome without being exposed. In the COVID-19
example, exposure necessity is plausible because COVID-19 is primarily
believed to spread through respiratory transmission (Meyerowitz et al., 2021),
where viral particles come in to contact with the respiratory mucosa.

Similarly to other works on vaccine effects, we require the exposure to be
unaffected by the treatment assignment (Halloran et al., 1999).

######  Assumption 3 (No treatment effect on exposure in the unexposed).

$\displaystyle E_{1}^{a=0}=E_{1}^{a=1}\text{ and
}E_{2}^{a=0,e_{1}=0}=E_{2}^{a=1,e_{1}=0}\text{ w.p.\leavevmode\nobreak\
1}\leavevmode\nobreak\ .$

In blinded placebo controlled RCTs, such as the COVID-19 example introduced in
Section 1.1, patients do not know whether they have been assigned to vaccine
or placebo shortly after treatment assignment. Therefore, their community
interactions are unlikely to be affected by the treatment assignment, and we
find it plausible that $E_{1}^{a=0}=E_{1}^{a=1}$ (Halloran and Struchiner,
1995; Stensrud and Smith, 2023). However, an individual who develops the
outcome during time interval 1 may change their subsequent behavior during
time interval 2. If more individuals develop the outcome under placebo
compared to the active vaccine, then treatment could affect exposures during
time interval 2 via infection status in time interval 1, through a path
$A\rightarrow\Delta Y_{1}\rightarrow E_{2}$ (Figure 1). This reflects a
retention of highly exposed vaccine recipients in the risk set (Hudgens et
al., 2004). Under an intervention that eliminates exposure during time
interval 1, there are no such selection effects during time interval 2. Thus,
Assumption 3 is plausible in our motivating target trial.

Assumptions about balanced exposure between treatment arms are standard in
vaccine research in order to interpret VE estimates as protective effects of
treatment not via changes in behavior (Hudgens et al., 2004). For example,
Tsiatis and Davidian (2022) used a related assumption, stating that the
counterfactual contact rate $c_{a}^{b}(t)$ under a blinded assignment to
treatment $a$ is equal for $a=0$ and $a=1$ at all times and for all
individuals.

To identify outcomes from under an intervention that isolates individuals
during interval 1 from the observed data, we introduce the following
assumption.

######  Assumption 4 (Exposure effect restriction).

For all $a\in\\{0,1\\}$,

(3) $\displaystyle E[\Delta Y_{2}\mid A=a,L]\leq E[\Delta Y_{2}^{e_{1}=0}\mid
A=a,L]\leq E[\Delta Y_{1}+\Delta Y_{2}\mid A=a,L]\text{ w.p.
1}\leavevmode\nobreak\ .$

To give intuition for Assumption 4, consider the following example where the
expected counterfactual outcome under isolation reaches the upper and lower
limits (Figure 2). Suppose that 3 out of 40 individuals in stratum $A=a,L=l$
developed the infectious outcome during interval 1. Subsequently, 5
individuals experienced the outcome during time interval 2. In the worst case
scenario, all 3 individuals who developed the outcome in interval 1 would also
have the outcome during interval 2 if they were isolated during interval 1,
and in the best case scenario none of the 3 individuals would have the outcome
after isolation. If the outcomes in the remaining 37 individuals were
identical under isolation versus no isolation, a total of 5/40 (best case) to
8/40 (worst case) individuals would experience the outcome during interval 2
after isolation. In the example, suppose further that all proportions
represent expectations.

Figure 2. Illustration of a scenario where the bounds in Assumption 4 are
reached. Each panel is evaluated in a stratum $A=a,L=l$. Under isolation
during time interval 1, there would be 3 more individuals at risk during time
interval 2 compared to the observed data with no isolation. In the best case
scenario, none of the 3 individuals would develop the outcome during interval
2 after isolation. In the worst case scenario, all 3 individuals would develop
the outcome during interval 2 after isolation.

Assumption 4 can be violated if there exist causal paths from $E_{1}$ to
$\Delta Y_{2}$ that are not intersected by $\Delta Y_{1}$, e.g. the path
$E_{1}\rightarrow\Delta Y_{2}$ in Figure 3 (A). In Appendix C, we show that
Assumption 4 is implied by an exclusion restriction assumption under an
intervention that prevents the outcome from occurring during time interval 1.
For example, Assumption 4 can fail if isolation during time interval 1
precludes exposure to the infectious pathogen in cases where recurrent
exposures contribute to sustained natural immunity without causing the
outcome. In other words, Assumption 4 can fail if a substantial proportion of
infections are not detected, e.g. when infections are asymptomatic. In such
cases, individuals may become more susceptible to infectious exposures during
time interval 2 if they are isolated during time interval 1. For example,
natural immunity against severe malaria wanes over time in individuals who
migrate from malaria endemic countries to non-endemic countries (Mischlinger
et al., 2020). Likewise, increases in RSV infections after COVID-19 lockdown
may have been caused by prolonged periods without viral exposure, reducing
naturally acquired immunity (Bardsley et al., 2023). It is possible to falsify
Assumption 4 by observing whether any placebo recipients develop antibodies
(or other vaccine-specific immune markers) during interval 1 without
experiencing the event $\Delta Y_{1}$.

Assumption 4 can also fail for other outcomes than infection. For instance,
suppose that $\Delta Y_{k}$ denotes death during interval $k$. Then, an
infection in time interval 1 can affect survival in time interval 2 through
pathways that are not intersected by survival status during time interval 1,
for example by causing serious illness and prolonged hospitalization. This
would correspond to a path $E_{1}\rightarrow\Delta Y_{2}$ in Figure 3 (A).

In the COVID-19 example, an exposure that does not result in COVID-19
infection during time interval 1 is unlikely to change an individual’s contact
behavior during time interval 2, corresponding to the path $E_{1}\rightarrow
E_{2}\rightarrow\Delta Y_{2}$ in Figure 3 (A).

In the following example, we consider another exposure intervention.

######  Example (Alternative exposure intervention).

Let $E_{k}=1$ denote individuals who are free to interact in an environment
where they can be exposed to the infectious agent. Conversely, define
$E_{k}=0$ to mean that individuals are isolated, i.e. confined to an
environment where they cannot be exposed to the infectious agent. Likewise,
let $e_{k}=0$ and $e_{k}=1$ denote controlled procedures whereby individuals
are isolated versus introduced into such an environment. For example, in the
trial design discussed by Ray et al. (2020), individuals are vaccinated for
influenza before the seasonal outbreak, and are therefore initially isolated
until the seasonal outbreak begins, disregarding infections out of season.
Alternatively, in a trial contrasting early versus late vaccination of
individuals before travelling to areas where the infectious agent is
widespread, individuals are isolated before travel, and then exposed on
arrival. Under this definition of infectious exposure, being part of a
population of infective individuals is viewed as an infectious challenge in
itself. Thus, in the observed data described in Section 2, $E_{k}=1$ w.p. 1.
Then, Assumptions 2-3 and Assumption 5 hold by design, although Assumption 4
can still fail. Furthermore, to interpret the challenge effect as a measure of
vaccine protection, we still require the study environment, e.g. viral load
per exposure, to be constant across intervals 1 and 2.

##  4\. Identification

###  4.1. Identification assumptions

The following additional assumption, which concerns common causes of exposure
and the outcome, is useful for identification of the challenge effect.

######  Assumption 5 (Exposure exchangeability).

For all $a,e_{1},e_{2}\in\\{0,1\\}$,

$\displaystyle\Delta Y_{1}^{a,e_{1}},\Delta
Y_{2}^{a,e_{1}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}E_{1}^{a}\mid A=a,L\text{ and }\Delta
Y_{2}^{a,e_{1},e_{2}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}E_{2}^{a,e_{1}}\mid A=a,L\leavevmode\nobreak\
.$

Exposure exchangeability states that exposure and the outcome are unconfounded
conditional on baseline covariates. Tsiatis and Davidian (2022) used an
assumption closely related to Assumption 5; they assumed that
$\\{\pi_{1}(t,\tau),\pi_{0}(t,\tau)\\}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}\\{S,c^{b}\\}\mid X$, where $\pi_{a}(t,\tau)$
is the counterfactual individual-specific transmission probability per contact
under treatment $A=a$, $S$ denotes a vaccination site, $X$ is a set of
baseline covariates and $c^{b}$ is a contact rate.

The causal graphs in Figure 3 (A) and (B) illustrate two different data
generating mechanisms violating Assumptions 3-5 by paths $A\rightarrow E_{k}$,
$E_{1}\rightarrow\Delta Y_{2}$, $E_{1}\rightarrow E_{2}$ and
$E_{2}^{a,e_{1}}\leftarrow U_{EY}\rightarrow\Delta Y_{2}^{a,e_{1},e_{2}}$. In
contrast, the causal graph in Figure 1 satisfies Assumptions 3-5.

$A$$E_{1}$$E_{2}$$\Delta Y_{1}$$\Delta Y_{2}$$L$

(a)

$A$ $a$ $E_{1}^{a}$ $e_{1}$ $E_{2}^{a,e_{1}}$ $e_{2}$ $\Delta
Y_{1}^{a,e_{1}}$$\Delta Y_{2}^{a,e_{1},e_{2}}$$L$$U_{EY}$$U_{Y}$$U_{E}$

(b)

Figure 3. (A) The red paths $E_{1}\rightarrow\Delta Y_{2}$ and
$E_{1}\rightarrow E_{2}$ can violate exposure effect restriction (Assumption
4), and the red paths $A\rightarrow E_{k}$ can violate no effect of treatment
in the unexposed (Assumption 3). (B) Backdoor paths between exposure $E_{k}$
and outcome $\Delta Y_{k}$ that are not blocked by baseline covariates $L$,
such as the red path $E_{2}^{a,e_{1}}\leftarrow U_{UE}\rightarrow\Delta
Y_{2}^{a,e_{1},e_{2}}$, can violate exposure exchangeability (Assumption 5).
However, common causes of $\Delta Y_{k}$ and $E_{k}$, such as the blue paths
$\Delta Y_{1}^{a,e_{1}}\leftarrow U_{Y}\rightarrow\Delta
Y_{2}^{a,e_{1},e_{2}}$ and $E_{1}^{a}\leftarrow U_{E}\rightarrow
E_{2}^{a,e_{1}}$, do not violate exposure exchangeability. In the absence of
$U_{E},U_{Y}$ (blue paths),
$\text{VE}_{k}^{\mathrm{challenge}}=\text{VE}_{k}^{\mathrm{obs}}$ during both
intervals $k\in\\{1,2\\}$, otherwise $\text{VE}_{2}^{\mathrm{challenge}}$ can
differ from $\text{VE}_{2}^{\mathrm{obs}}$ due to depletion of susceptible
individuals during time interval 1.

###  4.2. Identification results

In the following theorem, we give bounds on the challenge effect under the
assumptions introduced so far.

######  Theorem 1.

Suppose that Assumptions 1-5 hold in a conventional vaccine trial (formalized
in Appendix B). Then, the challenge effect during time interval 1 is point
identified,

(4)
$\displaystyle\text{VE}_{1}^{\mathrm{challenge}}(l)=\text{VE}_{1}^{\mathrm{obs}}(l)=1-\frac{E[Y_{1}\mid
A=1,L=l]}{E[Y_{1}\mid A=0,L=l]}\leavevmode\nobreak\ ,$

whenever $E[\Delta Y_{1}\mid A=a,L=l]>0$ for all $a\in\\{0,1\\}$, and the
challenge effect during interval 2 is partially identified by sharp bounds
$\mathcal{L}_{2}(l)\leq\text{VE}_{2}^{\mathrm{challenge}}(l)\leq\mathcal{U}_{2}(l)$,
where

(5) $\displaystyle\mathcal{L}_{2}(l)$ $\displaystyle=1-\frac{E[Y_{2}\mid
A=1,L=l]}{E[Y_{2}-Y_{1}\mid A=0,L=l]}\leavevmode\nobreak\ ,$ (6)
$\displaystyle\mathcal{U}_{2}(l)$ $\displaystyle=1-\frac{E[Y_{2}-Y_{1}\mid
A=1,L=l]}{E[Y_{2}\mid A=0,L=l]}\leavevmode\nobreak\ ,$

whenever $E[Y_{2}-Y_{1}\mid A=a,L=l]>0$.

A proof of Theorem 1 is given in Appendix B. Additionally, in the
Supplementary Material, we give R code illustrating a counterfactual data
generating mechanism that attains the bounds $\mathcal{L}_{2}(l)$ and
$\mathcal{U}_{2}(l)$.

The upper bound $\mathcal{U}_{2}(l)$ is reached when $i$) all the individuals
that were infected during time interval 1 in the placebo arm would have become
infected if they were isolated during interval 1 and challenged with the
exposure during interval 2, $ii$) none of the individuals that were infected
during time interval 1 in the vaccine arm would have become infected if they
were isolated during interval 1 and challenged with the exposure during
interval 2 and $iii$) every individual that was uninfected during interval 1
would have an unchanged outcome during interval 2 if they were isolated during
interval 1. We can use a similar argument to find a scenario where the lower
bound $\mathcal{L}_{2}(l)$ is reached.

It is straightforward to show that
$\mathcal{L}_{2}(l)\leq\text{VE}_{2}^{\mathrm{obs}}(l)\leq\mathcal{U}_{2}(l)$
by re-expressing the bounds in Theorem 1 in terms of discrete hazards
functions. If few events occur during time interval 1, it follows from Theorem
1 that the resulting bounds both approach $\text{VE}_{2}^{\mathrm{obs}}$. A
heuristic observation along these lines was made by Follmann et al. (2021);
Fintzi and Follmann (2021). Furthermore, Theorem 1 clarifies plausible and
testable assumptions for partial identification of (challenge) vaccine waning
and provides sharp bounds under the identifying assumptions.

Because $e_{k}=1$ denotes inoculation by a representative dose of the
infectious agent (Assumption 1), a comparison across studies of challenge
effects identified by Theorem 1 typically compares infectious inocula of
different sizes that e.g. depend on the prevalence of infection in the
respective background populations.

The marginal challenge effect, involving quantities $1-E[\Delta
Y_{1}^{a=1,e_{1}=1}]/E[\Delta Y_{1}^{a=0,e_{1}=1}]$ and $1-E[\Delta
Y_{2}^{a=1,e_{1}=0,e_{2}=1}]/E[\Delta Y_{2}^{a=0,e_{1}=0,e_{2}=1}]$, can be
expressed as a weighted average over the conditional challenge effect in (1)
with weights that are unidentified when exposure status $E$ is unmeasured
(Stensrud and Smith, 2023; Huitfeldt et al., 2019). However, under the
additional assumption that infectious exposure deterministically causes the
outcome in placebo recipients, the marginal challenge effect is also point
identified (Stensrud and Smith, 2023).

######  Proposition 1.

Suppose that Assumptions 1-5 hold in a conventional vaccine trial (formalized
in Appendix B). Assume further that for all $a\in\\{0,1\\}$,

(7) $\displaystyle\Delta Y_{2}^{a}$ $\displaystyle\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}E_{1}^{a}\mid\Delta
Y_{1}^{a},E_{2}^{a},A=a,L\leavevmode\nobreak\ ,$ (8) $\displaystyle E_{2}^{a}$
$\displaystyle\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}E_{1}^{a}\mid\Delta
Y_{1}^{a},A=a,L\leavevmode\nobreak\ ,$

and that $P(E_{1}=0\mid A=a,L)>0$ and $E[\Delta Y_{2}\mid A=a,L]>0$ w.p. 1.
Then,

(9) $\displaystyle E[\Delta Y_{2}^{e_{1}=0}\mid A=a,L]=E[\Delta
Y_{2}\mid\Delta Y_{1}=0,A=a,L]\text{ w.p. 1 }\leavevmode\nobreak\ ,$

which implies that
$\text{VE}_{2}^{\mathrm{challenge}}(l)=\text{VE}_{2}^{\mathrm{obs}}(l)$ for
all $l$.

Equality (9) implies Assumption 4, and thus (7)-(8) imply Assumption 4.
Furthermore, (9) is an equality involving only single world quantities
(Richardson and Robins, 2013), and can therefore in principle be falsified in
a future challenge trial with an immediate challenge versus isolation followed
by a delayed challenge. Challenge trials will clearly be unethical to conduct
in many settings, especially if recipients of the control treatment $A=0$ are
vulnerable to severe infectious outcomes, but there are also many examples of
such trials being conducted, see e.g. Roestenberg et al. (2012); Killingley et
al. (2022).

Expressions (7)-(8) are strong homogeneity assumptions, which can be violated
by the presence of $U_{Y}$, $U_{E}$ or paths $E_{1}\rightarrow E_{2}$,
$E_{1}\rightarrow\Delta Y_{2}$ in Figure 3, and are not necessary for the
bounds in Theorem 1 to be informative about vaccine waning. Proposition 1
formalizes sufficient conditions under which
$\text{VE}_{2}^{\mathrm{challenge}}(l)$ is identified by
$\text{VE}_{2}^{\mathrm{obs}}(l)$. A special case arises when Assumptions 1-5
and (7)-(8) hold without baseline covariates; then,
$\text{VE}_{k}^{\mathrm{challenge}}=\text{VE}_{k}^{\mathrm{obs}}$ marginally
for all $k$, and conventional vaccine efficacy estimates are equal to the
marginal challenge effect. This is an even stronger homogeneity condition,
which also requires the absence of all backdoor paths $E_{k}\leftarrow
L\rightarrow\Delta Y_{k}$ in Figure 3 (A). Investigators who want to quantify
vaccine waning should decide on a case-by-case basis whether to report
estimates of
$\mathcal{L}_{2}(l),\mathcal{U}_{2}(l),\text{VE}_{2}^{\mathrm{obs}}(l)$ or
marginal estimands, and justify their assumptions accordingly using subject
matter knowledge. We do not rely on these homogeneity conditions in our
analysis of the BNT162b2 COVID-19 vaccine trial in Section 6.

Next, suppose that the effect of placebo does not wane in the sense that the
risk of the outcomes under a challenge immediately after placebo
administration is equal to the risk of outcomes under isolation during
interval 1, and subsequent challenge during interval 2.

######  Assumption 6 (No waning of placebo).

(10) $\displaystyle E[\Delta Y_{1}^{a=0,e_{1}=1}\mid L]=E[\Delta
Y_{2}^{a=0,e_{1}=0,e_{2}=1}\mid L]\text{ w.p.\leavevmode\nobreak\
1}\leavevmode\nobreak\ .$

Assumption 6 states that a controlled exposure leads to the same outcomes in
conditional expectation, whether or not the exposure is preceded by an
isolation period. The assumption could be violated if isolation during
interval 1 leads to a loss of natural immunity against the infectious agent,
but this violation is unlikely in Thomas et al. (2021) since around $95\%$ of
participants had no prior history of COVID-19 infections, and we do not expect
short term isolation to affect natural immunity in immunologically naive
individuals.

###  4.3. An alternative target trial

Under no waning of placebo, it follows straightforwardly from Theorem 1 that
we can bound the ratio $\psi=E[\Delta Y_{1}^{a=1,e_{1}=1}\mid L=l]/E[\Delta
Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid L=l]$ by

(11)
$\displaystyle\mathcal{L}_{\psi}(l)\leq\psi\leq\mathcal{U}_{\psi}(l)\leavevmode\nobreak\
,$

where

(12) $\displaystyle\mathcal{L}_{\psi}(l)$
$\displaystyle=\frac{1-\text{VE}_{1}^{\mathrm{obs}}(l)}{1-\mathcal{L}_{2}(l)}\leavevmode\nobreak\
,$ (13) $\displaystyle\mathcal{U}_{\psi}(l)$
$\displaystyle=\frac{1-\text{VE}_{1}^{\mathrm{obs}}(l)}{1-\mathcal{U}_{2}(l)}\leavevmode\nobreak\
.$

The estimand $\psi$ can also be expressed as
$\psi=(1-\text{VE}_{1}^{\mathrm{challenge}}(l))/(1-\text{VE}_{2}^{\mathrm{challenge}}(l))$,
and corresponds to the following target trial (Hernán et al., 2022): Let a
group of individuals be randomized to one of two treatment groups on a
calendar date $X$. On the same date, all individuals in both groups are
vaccinated. In one treatment group, all individuals are isolated against
infectious exposures until calendar date $Y$, and then they are inoculated
through a controlled procedure. In the second treatment group, all individuals
are vaccinated and directly inoculated with the infectious agent through the
same controlled procedure. The outcome of interest is the cumulative incidence
of infection during a pre-specified duration of time after calendar date $Y$,
for example 2 months. If there are more outcome events under a challenge that
precedes an isolation period after vaccination ($\Delta
Y_{2}^{a=1,e_{1}=0,e_{2}=1}$) compared to an immediate challenge after
vaccination ($\Delta Y_{1}^{a=1,e_{1}=1}$), that is, $\psi<1$, then the
vaccine has waned. The target trial is similar to the estimand identified by
the clinical experiment proposed by Ray et al. (2020), which is a contrast of
observed incidence of influenza infection in recently vaccinated individuals
versus individuals vaccinated further in the past.

Finally, under the homogeneity conditions in Proposition 1, $\psi$ is
identified by the naive contrast of cumulative incidences
$\psi^{\mathrm{obs}}=(1-\text{VE}_{1}^{\mathrm{obs}})/(1-\text{VE}_{2}^{\mathrm{obs}})$.

##  5\. Estimation

Suppose we have access to data for individuals $i\in\\{1,\dots,n\\}$
consisting of treatment and covariates $A_{i},L_{i}$ and event times $T_{i}$
subject to losses to follow-up (censoring), indicated by $C_{i}\in\\{0,1\\}$.
We assume that individuals are sampled into the study through a procedure such
that the random vectors $(A_{i},L_{i},T_{i},C_{i})$ are i.i.d. (Cox, 1958).
Then, for each treatment group $a\in\\{0,1\\}$, we estimate the conditional
cumulative incidence functions, $E[Y_{k}\mid A=a,L=l]$, at the end of interval
$k$ (time $t_{k}$) by
$\widehat{\mu}_{k,a,l}=1-\exp(-\widehat{\Lambda}_{0,a}(t_{k}))^{r(l;\widehat{\beta}_{a})}$
using the Breslow estimator $\widehat{\Lambda}_{0,a}(t)$ and estimated
coefficients $\widehat{\beta}_{a}$ that maximizes the partial likelihood with
respect to the proportional hazards model $\lambda(t\mid
A=a,L=l)=\lambda_{0,a}(t)r(l;\beta_{a})$ for $t\in[0,t_{K}]$ (Cox, 1972).
Here, $\lambda_{0,a}(t)$ denotes the baseline hazard of the infectious outcome
at time $t$ in treatment group $A=a$. The estimator $\widehat{\mu}_{k,a,l}$ is
a standard cumulative incidence estimator (Therneau and Grambsch, 2000), and
can easily be implemented using standard statistical software. We give an
example in R using the survival package (Therneau, 2023) in the Supplementary
Material. In our data example, we assumed that the parametric part of the
hazard model is given by $r(l;\beta_{a})=\exp(\beta_{a}l)$. We chose to handle
tied event times in the Cox model fit using the Efron approximation (Therneau
and Grambsch, 2000). It is also possible to estimate the cumulative incidence
function through other frequently used regression models, such as logistic
regression, as we discuss in Appendix F, or additive hazards models (Aalen et
al., 2008).

Finally, expressions (2), (4)-(6) and (12)-(13) motivate the plugin-estimators

$\displaystyle\widehat{\text{VE}}_{1}^{\mathrm{obs}}(l)$
$\displaystyle=1-\frac{\widehat{\mu}_{k=1,a=1,l}}{\widehat{\mu}_{k=1,a=0,l}}\leavevmode\nobreak\
,$ $\displaystyle\widehat{\text{VE}}_{2}^{\mathrm{obs}}(l)$
$\displaystyle=1-\frac{\widehat{\mu}_{k=2,a=1,l}-\widehat{\mu}_{k=1,a=1,l}}{\widehat{\mu}_{k=2,a=0,l}-\widehat{\mu}_{k=1,a=0,l}}\cdot\frac{1-\widehat{\mu}_{k=1,a=0,l}}{1-\widehat{\mu}_{k=1,a=1,l}}\leavevmode\nobreak\
,$ $\displaystyle\widehat{\mathcal{L}}_{2}(l)$
$\displaystyle=1-\frac{\widehat{\mu}_{k=2,a=1,l}}{\widehat{\mu}_{k=2,a=0,l}-\widehat{\mu}_{k=1,a=0,l}}\leavevmode\nobreak\
,$ $\displaystyle\widehat{\mathcal{U}}_{2}(l)$
$\displaystyle=1-\frac{\widehat{\mu}_{k=2,a=1,l}-\widehat{\mu}_{k=1,a=1,l}}{\widehat{\mu}_{k=2,a=0,l}}\leavevmode\nobreak\
,$ $\displaystyle\widehat{\mathcal{L}}_{\psi}(l)$
$\displaystyle=(1-\widehat{\text{VE}}_{1}^{\mathrm{obs}}(l))/(1-\widehat{\mathcal{L}}_{2}(l))\leavevmode\nobreak\
,$ $\displaystyle\widehat{\mathcal{U}}_{\psi}(l)$
$\displaystyle=(1-\widehat{\text{VE}}_{1}^{\mathrm{obs}}(l))/(1-\widehat{\mathcal{U}}_{2}(l))\leavevmode\nobreak\
.$

Pointwise confidence intervals can, e.g., be estimated with individual-level
data using non-parametric bootstrap, which we illustrate in Appendix H using a
publicly available synthetic dataset resembling the RTS,S/AS01 malaria vaccine
trial (RTS,S Clinical Trials Partnership, 2012), described by Benkeser et al.
(2019).

Suppose a decision-maker is interested in the lower bound
$\mathcal{L}_{k}(l)$, because they are concerned about the worst-case scenario
corresponding to the greatest extent of waning. Then, we propose to use a
lower one-sided $95\%$ confidence interval for $\widehat{\mathcal{L}}_{k}(l)$,
as $\mathcal{L}_{k}(l)$ will exceed this confidence limit in 95% of cases
under correctly specified assumptions. Conversely, for a decision-maker who is
interested in testing whether any waning is present, we propose to use a one-
sided upper $95\%$ confidence interval for $\widehat{\mathcal{U}}_{k}(l)$.
Finally, decision-makers who seek to weigh the lower and upper bounds evenly
may prefer to use a joint confidence for the lower and upper bound (Horowitz
and Manski, 2000).

In Appendix G, we describe estimators of the bounds $\mathcal{L}_{k}$ and
$\mathcal{U}_{k}$ using summary data for the number of recorded events and
person time at risk. Furthermore, in Appendix I, we describe estimators of
$\text{VE}_{k}^{\mathrm{obs}}$ and of bounds of
$\text{VE}_{k}^{\mathrm{challenge}}$ that use logistic regression to estimate
the cumulative incidences, and illustrate the approach with a simulated
example.

##  6\. Example: BNT162b2 against COVID-19

We analyzed data from a blinded, placebo controlled vaccine trial described by
Thomas et al. (2021), where individuals were randomized to two doses of the
mRNA vaccine BNT162b2 against COVID-19 ($A=1$) or placebo ($A=0$), 21 days
apart. Participants were 12 years or older, and were enrolled during a period
of time from July 27, 2020 to October 29, 2020 (older than 16) and from
October 15, 2020 to January 12, 2021 (aged 12-15), in 152 sites in the United
States (130 sites), Argentina (1 site), Brazil (2 sites), South Africa (4
sites), Germany (6 sites) and Turkey (9 sites). By January 12, 2021, there had
been 21.94 million cases of COVID-19 in the United States (Mathieu et al.,
2020), amounting to roughly 7% of the US population (United States Census
Bureau, 2024). The study included systematic measures to test participants for
infection with COVID-19, with 5 follow-up visits within the first 12 months,
and an additional sixth follow-up visit after 24 months (Thomas et al., 2021,
Protocol). Here, participants were questioned about respiratory symptoms.
Additionally, they were instructed to report any respiratory symptoms via a
telehealth visit after symptom onset.

Vaccine efficacy estimates ($\text{VE}^{\mathrm{obs}}$) were reported to
decrease with time since vaccination (Thomas et al., 2021). In principle, the
decrease of $\text{VE}^{\mathrm{obs}}$ over time could be due to declining
protection of the vaccine, or alternatively also due to a higher depletion of
susceptible individuals in the placebo group compared to the vaccine group
during time interval 1. To distinguish between these two explanations, we
conducted inference on (1) using publicly available summary data from Thomas
et al. (2021), reported in Table 1. A detailed description of the estimators
is given in Appendix G.

We let $k=1$ denote the time interval from 11 days after dose 1 until 2 months
after dose 2, and $k=2$ to denote the time interval from 2 months after dose 2
until 4 months after dose 2 (Figure 4). Individuals received the second dose
of the vaccine 10 days into interval $k=1$. The estimate
$\widehat{\mathrm{VE}}^{\mathrm{challenge}}_{1}$ can be interpreted as a
conservative estimate of the challenge effect if individuals had been isolated
from dose 1 until shortly after dose 2 and then inoculated ($e_{1}=1$), under
the assumption that vaccine protection was at its greatest shortly after dose
2. We give a detailed argument for this claim in Appendix J, and present a
sensitivity analysis which does not use this assumption in Table 8 (Appendix
J).

Figure 4. Illustration of time intervals $k=1$ and $k=2$

For a given interval 1, investigators face a trade-off when choosing an
appropriate length of interval 2: a longer interval 2 gives narrower bounds
(5)-(6), in addition to narrower confidence interval as more events are
accrued. Thereby, a longer interval 2 can give a more sensitive test of
vaccine waning. However, Assumption 1 is more likely to be violated if
interval 2 greatly exceeds interval 1 in length, as viral loads per exposure
may change over time, and the risk of multiple exposures per interval
increases with a longer interval 2. This could lead the contrast of estimates
$\widehat{\text{VE}}_{1}^{\mathrm{challenge}}$ vs.
$\widehat{\text{VE}}_{2}^{\mathrm{challenge}}$ to compare different versions
of infectious challenges if the lengths of intervals 1 and 2 differ greatly.

Table 1. Estimates and 95% confidence intervals for (2), (5)-(6) and (12)-(13). Interval 1 ranged from 11 days after dose 1 until 2 months after dose 2 (71 days in total) and interval 2 ranged from 2 months after dose 2 until 4 months after dose 2 (61 days in total). Confidence intervals for the bounds $\mathcal{L}_{\bullet},\mathcal{U}_{\bullet}$ were one-sided, whereas two-sided confidence intervals were used for VE estimates. The point estimates of $\widehat{\text{VE}}_{1}^{\mathrm{obs}},\widehat{\mathcal{U}}_{2}$ and $\widehat{\mathcal{U}}_{\psi}$ are consistent with waning vaccine protection, but the confidence intervals include the null value of no waning.  Estimand |  Estimate (95% CI)
---|---
$\widehat{\text{VE}}_{1}^{\text{obs}},\widehat{\text{VE}}_{1}^{\text{challenge}}$ |  $0.95(0.93,0.97)$
$\widehat{\text{VE}}_{2}^{\text{obs}}$ |  $0.90(0.87,0.93)$
$\widehat{\mathcal{L}}_{2}$ |  $0.87(0.84,-)$
$\widehat{\mathcal{U}}_{2}$ |  $0.94(-,0.95)$
$\widehat{\mathcal{L}}_{\psi}$ |  $0.36(0.26,-)$
$\widehat{\mathcal{U}}_{\psi}$ |  $0.81(-,1.27)$

The upper confidence limit of $\widehat{\mathcal{U}}_{2}$ was close to
$\widehat{\text{VE}}_{1}^{\mathrm{challenge}}$ (Table 1), although the upper
confidence limit of $\widehat{\mathcal{U}}_{\psi}$ exceeded 1. In Table 7
(Appendix J), where interval 2 was extended until day 190, the upper
confidence limit of $\widehat{\mathcal{U}}_{2}$ was close to the lower
confidence limit of $\widehat{\text{VE}}_{1}^{\mathrm{challenge}}$.
Additionally, the upper confidence limit of $\widehat{\mathcal{U}}_{\psi}$ was
smaller than 1. In Table 8, we considered an additional choice of intervals to
illustrate possible depletion of susceptible individuals between dose 1 and
dose 2 of the vaccine, which gave wide bounds that included the null (no
waning). Overall, our analyses are suggest waning vaccine protection from
interval 1 to interval 2.

Our primary analysis did not condition on any baseline covariates $L$, as
individual patient data were not available. To illustrate the use of
estimators described in Section 5 with individual-level data, we have included
an additional analysis motivated by a malaria vaccine trial in Appendix H. As
a sensitivity analysis, we conducted subgroup analyses of Thomas et al. (2021)
in Appendix J which show that the cumulative incidence of the outcome by the
end of follow-up was nearly constant across the following baseline covariates
($L$): age over 65, Charlson Comorbidity Index category $\geq 1$ and obesity,
for both vaccine and placebo treatment. Therefore, we expect that estimates
$\widehat{\mathrm{VE}}_{1}^{\mathrm{obs}}(l),\widehat{\mathcal{L}}_{2}(l),\widehat{\mathcal{U}}_{2}(l)$
conditional on the baseline covariates $l$ would have been close to the
marginal estimates reported in Table 1 for all baseline covariates $l$.
Although we cannot guarantee the absence of residual confounding given $L$
($U_{EY}$ in Figure 3 (B)), it is plausible that the above choice of baseline
covariates $L$ is sufficient to block open backdoor paths between exposure and
infection status.

Our main analysis suggests that depletion of susceptible individuals could not
alone account for the decline in vaccine efficacy over time. Large real-world
effectiveness studies that established waning of the BNT162b2 vaccine, such as
Goldberg et al. (2021); Levin et al. (2021), were published in 2021. However,
it would have been possible to estimate challenge effects (4)-(6) using
preliminary trial data from the BNT162b2 vaccine trial, published already in
December 2020 (Polack et al., 2020). This could have provided earlier evidence
of vaccine waning. Such analyses could guide future vaccination policies
during the window of time before booster trials are available.

In the Supplementary Material, we include R code to simulate a data generating
mechanism that reaches the bounds in Theorem 1 for the observed data
distribution. This illustrates that the bounds are sharp, i.e. that the true
value of $\text{VE}_{2}^{\mathrm{challenge}}$ in the vaccine trial could lie
on the bounds $\widehat{\mathcal{L}}_{2},\widehat{\mathcal{U}}_{2}$ under
Assumptions 1-5.

##  7\. Discussion

The challenge effect quantifies the vaccine waning that would be observed in a
hypothetical challenge trial. Often, investigators only have access to data
from a conventional randomized vaccine trial where participants are freely
exposed to the infectious agent in the community. We have shown that sharp
bounds on the challenge effect can be derived under plausible assumptions, and
we illustrate that these bounds can confirm clinically significant waning.

Our results are broadly applicable to vaccine trials using routinely collected
data and can be extended to account for treatment outcome confounding in
observational vaccine studies. Furthermore, the bounds on the challenge effect
can be estimated using standard statistical methods that are implemented in
commonly used software packages. As illustrated in Section 6, the estimators
for summary data can also be applied to re-analyze historical data from
vaccine studies when individual-level data are not available, for example due
to privacy concerns.

The challenge effect makes it possible to distinguish between settings where
the observed vaccine efficacy diminishes solely due to depletion of
susceptible individuals and settings where the vaccine protection wanes over
time, and thereby addresses, and formalizes, an open problem in the analysis
of vaccine trials (Halloran et al., 1997). The proposed methods can offer new
empirical evidence of interest in health policy questions, for example about
timing of vaccinations or booster doses.

##  8\. Acknowledgements

This work was supported by the Swiss National Science Foundation Starting
Grant called “Causal inference for infectious disease control”.

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##  Appendix A Identification under interference

As in Tsiatis and Davidian (2022), Halloran et al. (1996), and (implicitly) in
most vaccine randomized trials, we have assumed that interference between the
participants in the observed trial data is negligible, such that one
participant’s outcome does not depend on another participant’s treatment
assignment (no interference among the participants). However, while it is
often plausible that interference between the trial participants is
negligible, there will often be interference in a setting where a vaccine
program is rolled-out in a human population. Thus, when applying conventional
estimators under i.i.d. assumptions to the trial data, we draw valid
superpopulation inference in a (fictive) population with potentially limited
practical relevance. Yet, we will argue that the interference is not an issue
when studying the challenge effect, unlike the usual vaccine efficacy estimand
($\text{VE}^{\mathrm{obs}}$). This is because the challenge effect is
insensitive to the interference that arises in most infectious disease
settings.

To be explicit, consider a classical randomized vaccine trial, i.e., a trial
without any controlled infectious challenges. Then, the vaccine efficacy
($\text{VE}^{\mathrm{obs}}$) in the (fictive) superpopulation with no
interference will not correspond to $\text{VE}^{\mathrm{obs}}$ in a realistic
target population, because there will be interference (e.g. heard immunity)
between individuals in the realistic target population.

Consider now a challenge trial corresponding to (1). Then, the challenge
effect in the (fictive) superpopulation with no interference would be
identical to the challenge effect in the (more realistic) target population
with interference, because the interference is trivial under an intervention
on exposure; indeed, there is no longer any interference when the exposure to
the infectious agent is controlled (fixed) for all individuals. In this sense,
considering effects under interventions on exposure will often be more
practically relevant.

##  Appendix B Identification with two time intervals

######  Assumption 7 (Treatment exchangeability).

For all $a,e_{1},e_{2}\in\\{0,1\\}$,

$\displaystyle E_{1}^{a},\Delta Y_{1}^{a},\Delta
Y_{1}^{a,e_{1}},E_{2}^{a,e_{1}},\Delta Y_{2}^{a},\Delta
Y_{2}^{a,e_{1},e_{2}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}A\mid L\leavevmode\nobreak\ .$

######  Assumption 8 (Positivity).

$\displaystyle P(A=a\mid L)$ $\displaystyle>0\text{ for all
}a\in\\{0,1\\}\leavevmode\nobreak\ \text{ w.p. 1}\leavevmode\nobreak\ .$

Assumptions 7 and 8 hold by design when $A$ is assigned by randomization, for
example in an RCT.

###  B.1. Proof of Theorem 1

For the first time interval,

(14) $\displaystyle P(\Delta Y_{1}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{1}^{a}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity 2 intervals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{1}^{a}=1,E_{1}^{a}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass:consistency 2
intervals} }}}{{=}}$ $\displaystyle P(\Delta
Y_{1}^{a,e_{1}=1}=1,E_{1}^{a}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
exchageability 2 intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{1}^{a,e_{1}=1}=1\mid A=a,L)P(E_{1}^{a}=1\mid A=a,L)$ (15)
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass: treatment
exchageability 2 intevals},\ref{ass: exposure positivity 2 intervals}}}}{{=}}$
$\displaystyle P(\Delta Y_{1}^{a,e_{1}=1}=1\mid L)P(E_{1}^{a}=1\mid
L)\leavevmode\nobreak\ .$

Taking the ratio of (15) for $a=1$ vs. $a=0$, and using Assumption 3 to cancel
the ratio of exposure probabilities gives

$\displaystyle\frac{E[\Delta Y_{1}^{a=1,e_{1}=1}\mid L]}{E[\Delta
Y_{1}^{a=0,e_{1}=1}\mid L]}=\frac{E[\Delta Y_{1}\mid A=1,L]}{E[\Delta
Y_{1}\mid A=0,L]}\leavevmode\nobreak\ ,$

and therefore
$\text{VE}_{1}^{\mathrm{challenge}}=\text{VE}_{1}^{\mathrm{obs}}$.

For the second time interval,

$\displaystyle P(\Delta Y_{2}^{e_{1}=0}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity 2 intervals}}}}{{=}}$ $\displaystyle P(E_{2}^{a,e_{1}=0}=1,\Delta
Y_{2}^{a,e_{1}=0}=1\mid A=a,L)$ (16)
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(E_{2}^{a,e_{1}=0}=1,\Delta
Y_{2}^{a,e_{1}=0,e_{2}=1}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass: exposure
exchageability 2 intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{2}^{a,e_{1}=0,e_{2}=1}=1\mid A=a,L)P(E_{2}^{a,e_{1}=0}=1\mid A=a,L)$ (17)
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass: treatment
exchageability 2 intevals},\ref{ass: exposure positivity 2 intervals}}}}{{=}}$
$\displaystyle P(\Delta Y_{2}^{a,e_{1}=0,e_{2}=1}=1\mid
L)P(E_{2}^{a,e_{1}=0}=1\mid L)\leavevmode\nobreak\ .$

Taking the ratio of (17) for $a=0$ vs. $a=1$ and using Assumption 4 gives

$\displaystyle\frac{E[\Delta Y_{1}\mid A=1,L]}{E[\Delta Y_{1}+\Delta Y_{2}\mid
A=0,L]}$ $\displaystyle\quad\leq\frac{E[\Delta Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid
L]}{E[\Delta Y_{2}^{a=0,e_{1}=0,e_{2}=1}\mid
L]}\cdot\frac{P(E_{2}^{a=1,e_{1}=0}=1\mid L)}{P(E_{2}^{a=0,e_{1}=0}=1\mid L)}$
$\displaystyle\qquad\leq\frac{E[\Delta Y_{1}+\Delta Y_{2}\mid A=1,L]}{E[\Delta
Y_{2}\mid A=0,L]}\leavevmode\nobreak\ .$

Finally, using Assumption 3 to cancel the ratio of exposure probabilities, we
obtain

$\displaystyle\frac{E[\Delta Y_{2}\mid A=1,L]}{E[\Delta Y_{1}+\Delta Y_{2}\mid
A=0,L]}\leq\frac{E[\Delta Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid L]}{E[\Delta
Y_{2}^{a=0,e_{1}=0,e_{2}=1}\mid L]}\leq\frac{E[\Delta Y_{1}+\Delta Y_{2}\mid
A=1,L]}{E[\Delta Y_{2}\mid A=0,L]}\leavevmode\nobreak\ .$

To establish sharpness of the bounds (5) and (6), it is sufficient to show
that there exists a counterfactual data generating mechanism that attains the
bounds. An example that attains the lower bound $\mathcal{L}_{2}$ is given
below. We define $p_{k,a,l}=E[\Delta Y_{k}\mid A=a,L=l]$ for all $k,a,l$ and
denote the observed laws of $A,L$ by $P_{A},P_{L}$ respectively.

######  Data generating mechanism 1.

  1. (I)

$L\sim P_{L}$

  2. (II)

$A\sim P_{A}$

  3. (III)

$U_{Y}\sim\mathrm{Unif}[0,1]$

  4. (IV)

$E_{1}^{a}=E_{2}^{a,e_{1}}=1$ for all $a,e_{1}$

  5. (V)

    1. (a)

$\Delta Y_{1}^{a,e_{1}=1}=I(U_{Y}\leq p_{k=1,a,L})$ for all $a$

    2. (b)

$\Delta Y_{1}^{a,e_{1}=0}=0$ for all $a$

  6. (VI)

    1. (a)

$\Delta Y_{2}^{a=1,e_{1}=0,e_{2}=1}=I(U_{Y}\leq p_{k=1,a=1,L}+p_{k=2,a=1,L})$

    2. (b)

$\Delta Y_{2}^{a=0,e_{1}=0,e_{2}=1}=I(p_{k=1,a=0,L}<U_{Y}\leq
p_{k=1,a=0,L}+p_{k=2,a=0,L})$

    3. (c)

$\Delta Y_{2}^{a,e_{1}=1,e_{2}=1}=\Delta Y_{2}^{a,e_{1}=0,e_{2}=1}I(\Delta
Y_{1}^{a,e_{1}=1}=0)$ for all $a$

    4. (d)

$\Delta Y_{2}^{a,e_{1},e_{2}=0}=0$ for all $a,e_{1}$

All other counterfactuals are understood to be recursively related to (I)-(VI)
through Definition 43 of Richardson and Robins (2013), under interventions
restricted to $A,E_{1}$ and $E_{2}$.

The data generating mechanism generalizes the example in Figure 2. It is
straightforward to verify that Data generating mechanism 1 satisfies
Assumptions 1-5 and 7-8. Furthermore, the lower bound $\mathcal{L}_{2}$ is
attained since

$\displaystyle E[\Delta Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid L]$ $\displaystyle=$
$\displaystyle E[I(U_{Y}\leq p_{k=1,a=1,L}+p_{k=2,a=1,L})\mid L]$
$\displaystyle=$ $\displaystyle p_{k=1,a=1,L}+p_{k=2,a=1,L}$ $\displaystyle=$
$\displaystyle E[\Delta Y_{1}+\Delta Y_{2}\mid A=1,L]\leavevmode\nobreak\ ,$

and

$\displaystyle E[\Delta Y_{1}^{a=0,e_{1}=0,e_{2}=1}\mid L]$ $\displaystyle=$
$\displaystyle E[I(p_{k=1,a=0,L}<U_{Y}\leq p_{k=1,a=0,L}+p_{k=2,a=0,L})\mid
L]$ $\displaystyle=$ $\displaystyle p_{k=2,a=0,L}$ $\displaystyle=$
$\displaystyle E[\Delta Y_{2}\mid A=0,L]\leavevmode\nobreak\ .$

Additionally, Data generating mechanism 1 is consistent with the observed
cumulative incidences $E[\Delta Y_{k}\mid A=a,L]$ for all $a,k$, since

$\displaystyle E[\Delta Y_{1}\mid A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass:consistency 2
intervals},\ref{ass: treatment exchageability 2 intevals},\ref{ass: exposure
positivity 2 intervals}}}}{{=}}$ $\displaystyle E[\Delta Y_{1}^{a}\mid L]$
$\displaystyle=$ $\displaystyle E[\Delta Y_{1}^{a,e_{1}=1}\mid L]\text{ since
}E_{1}^{a}=1\text{ w.p. 1}$ $\displaystyle=$ $\displaystyle E[I(U_{Y}\leq
p_{k=1,a,L})\mid L]$ $\displaystyle=$ $\displaystyle
p_{k=1,a,L}\leavevmode\nobreak\ ,$

and

$\displaystyle E[\Delta Y_{2}\mid A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass:consistency 2
intervals},\ref{ass: treatment exchageability 2 intevals},\ref{ass: exposure
positivity 2 intervals}}}}{{=}}$ $\displaystyle E[\Delta Y_{2}^{a}\mid L]$
$\displaystyle=$ $\displaystyle E[\Delta Y_{2}^{a,e_{1}=1,e_{2}=1}\mid
L]\text{ since }E_{1}^{a}=E_{2}^{a}=1\text{ w.p. 1}$ $\displaystyle=$
$\displaystyle E[I(p_{k=1,a,L}<U_{Y}\leq p_{k=1,a,L}+p_{k=2,a,L})\mid L]$
$\displaystyle=$ $\displaystyle p_{k=2,a,L}\leavevmode\nobreak\ .$

Finally, the upper bound $\mathcal{U}_{2}$ can be reached by permuting
treatment groups $a=0\leftrightarrow a=1$ in (VI) (a) and (b) of Data
generating mechanism 1. An implementation of Data generating mechanism 1 in R
for a simplified setting with $A\sim\mathrm{Ber}(1/2)$ and without $L$ is
given in the Supplementary Material.

###  B.2. Proof of Proposition 1

We have that

$\displaystyle P(\Delta Y_{2}=1\mid\Delta Y_{1}=0,A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a}=1\mid\Delta
Y_{1}^{a}=0,A=a,L)$ $\displaystyle\stackrel{{\scriptstyle\text{Assumption
\ref{ass: exposure necessity 2 intervals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{2}^{a}=1,E_{2}^{a}=1\mid\Delta Y_{1}^{a}=0,A=a,L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{2}^{a}=1\mid E_{2}^{a}=1,\Delta
Y_{1}^{a}=0,A=a,L)P(E_{2}^{a}=1\mid\Delta Y_{1}^{a}=0,A=a,L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{2}^{a}=1\mid E_{1}^{a}=0,E_{2}^{a}=1,\Delta
Y_{1}^{a}=0,A=a,L)$ $\displaystyle\quad\times P(E_{2}^{a}=1\mid
E_{1}^{a}=0,\Delta Y_{1}^{a}=0,A=a,L)W_{Y,a}W_{E,a}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity 2 intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a}=1\mid
E_{1}^{a}=0,E_{2}^{a}=1,A=a,L)P(E_{2}^{a}=1\mid
E_{1}^{a}=0,A=a,L)W_{Y,a}W_{E,a}$ $\displaystyle=$ $\displaystyle P(\Delta
Y_{2}^{a}=1,E_{2}^{a}=1\mid E_{1}^{a}=0,A=a,L)W_{Y,a}W_{E,a}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity 2 intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a}=1\mid
E_{1}^{a}=0,A=a,L)W_{Y,a}W_{E,a}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid
E_{1}^{a}=0,A=a,L)W_{Y,a}W_{E,a}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
exchageability 2 intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{2}^{a,e_{1}=0}=1\mid A=a,L)W_{Y,a}W_{E,a}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass:consistency 2
intervals}}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{e_{1}=0}=1\mid
A=a,L)W_{Y,a}W_{E,a}\leavevmode\nobreak\ ,$

where we have defined the weights

$\displaystyle W_{Y,a}$ $\displaystyle=\frac{P(\Delta Y_{2}^{a}=1\mid
E_{2}^{a}=1,\Delta Y_{1}^{a}=0,A=a,L)}{P(\Delta Y_{2}^{a}=1\mid
E_{2}^{a}=1,\Delta Y_{1}^{a}=0,E_{1}^{a}=0,A=a,L)}\leavevmode\nobreak\ ,$
$\displaystyle W_{E,a}$ $\displaystyle=\frac{P(E_{2}^{a}=1\mid\Delta
Y_{1}^{a}=0,A=a,L)}{P(E_{2}^{a}=1\mid E_{1}^{a}=0,\Delta
Y_{1}^{a}=0,A=a,L)}\leavevmode\nobreak\ .$

When (7)-(8) hold, then $W_{Y,a}=W_{E,a}=1$, which implies (9). Taking the
ratio of (17) for $a=1$ vs. $a=0$, and using (9),

$\displaystyle\frac{E[\Delta Y_{2}^{a=1,e_{1}=0,e_{2}=1}\mid L]}{E[\Delta
Y_{2}^{a=0,e_{1}=0,e_{2}=1}\mid L]}=\frac{P(\Delta Y_{2}=1\mid\Delta
Y_{1}=0,A=1,L)}{P(\Delta Y_{2}=1\mid\Delta
Y_{1}=0,A=0,L)}\cdot\frac{P(E_{2}^{a=0,e_{1}=0}=1\mid
L)}{P(E_{2}^{a=1,e_{1}=0}=1\mid L)}$ $\displaystyle=$
$\displaystyle\frac{P(\Delta Y_{2}=1\mid\Delta Y_{1}=0,A=1,L)}{P(\Delta
Y_{2}=1\mid\Delta Y_{1}=0,A=0,L)}\leavevmode\nobreak\ ,$

where we have used Assumption 3 to cancel the ratio of exposure probabilities
in the final line.

##  Appendix C Motivation for Assumption 4

Suppose that it is possible to intervene on $\Delta Y_{1}$, for example
through a form of post exposure treatment that prevents the infection from
developing. Thus, we assume that Definition 43 in Richardson and Robins (2013)
holds for interventions on $A,E_{1},E_{2}$ and $\Delta Y_{1}$. An example of
such an intervention is antiretroviral post-exposure prophylaxis (PEP) for HIV
(DeHaan et al., 2022). Next, assume the population level exclusion restriction

(18) $\displaystyle P(\Delta Y_{2}^{a,e_{1}=1,\Delta y_{1}=0}=1\mid
L)=P(\Delta Y_{2}^{a,e_{1}=0,\Delta y_{1}=0}=1\mid L)\text{ w.p.
1}\leavevmode\nobreak\ ,$

which can be violated by arrows $E_{1}\rightarrow E_{2}$ or
$E_{1}\rightarrow\Delta Y_{2}$ in Figure 3 (A). Then,

$\displaystyle P(\Delta Y_{2}^{a}=1\mid L)$ $\displaystyle=$ $\displaystyle
P(\Delta Y_{1}^{a}=0,\Delta Y_{2}^{a}=1\mid L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{1}^{a}=0,\Delta Y_{2}^{a,\Delta Y_{1}^{a}}=1\mid
L)$ $\displaystyle=$ $\displaystyle P(\Delta Y_{1}^{a}=0,\Delta
Y_{2}^{a,\Delta y_{1}=0}=1\mid L)$ $\displaystyle=$ $\displaystyle P(\Delta
Y_{2}^{a,\Delta y_{1}=0}=1\mid L)$ $\displaystyle\quad-P(\Delta
Y_{1}^{a}=1,\Delta Y_{2}^{a,\Delta y_{1}=0}=1\mid L)\leavevmode\nobreak\ .$

We have used the recursive definition of counterfactuals (Definition 43 in
Richardson and Robins (2013)) in the third line. Using the fact that

$\displaystyle 0\leq P(\Delta Y_{1}^{a}=1,\Delta Y_{2}^{a,\Delta
y_{1}=0}=1\mid L)\leq P(\Delta Y_{1}^{a}=1\mid L)\leavevmode\nobreak\ ,$

it follows that

$\displaystyle P(\Delta Y_{2}^{a}=1\mid L)\leq P(\Delta Y_{2}^{a,\Delta
y_{1}=0}=1\mid L)\leq P(\Delta Y_{1}^{a}=1\mid L)+P(\Delta Y_{2}^{a}=1\mid
L)\leavevmode\nobreak\ .$

Finally, we obtain (3) from the fact that and $P(\Delta Y_{k}^{a}=1\mid
L)=P(\Delta Y_{k}=1\mid A=a,L)$ for $k\in\\{1,2\\}$ by Assumptions 7-8, and

$\displaystyle P(\Delta Y_{2}^{a,\Delta y_{1}=0}=1\mid L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{2}^{a,E_{1}^{a},\Delta y_{1}=0}=1\mid L)$
$\displaystyle\stackrel{{\scriptstyle\eqref{eq: exclusion Y
intervention}}}{{=}}$ $\displaystyle P(\Delta Y_{2}^{a,e_{1}=0,\Delta
y_{1}=0}=1\mid L)$ $\displaystyle=$ $\displaystyle P(\Delta
Y_{2}^{a,e_{1}=0,\Delta Y_{1}^{a,e_{1}=0}}=1\mid L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid L)\leavevmode\nobreak\ .$

The penultimate line used the fact that $P(\Delta Y_{1}^{a,e_{1}=0}=0\mid
L)=1$, which holds because

$\displaystyle P(\Delta Y_{1}^{a,e_{1}=0}=0\mid L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass:consistency 2
intervals},\ref{ass: treatment exchageability 2 intevals},\ref{ass: exposure
positivity 2 intervals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{1}^{a,e_{1}=0}=0\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
exchageability 2 intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{1}^{a,e_{1}=0}=0\mid E_{1}^{a}=0,A=a,L)$ $\displaystyle=$ $\displaystyle
P(\Delta Y_{1}^{a,E_{1}^{a}}=0\mid E_{1}^{a}=0,A=a,L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{1}^{a}=0\mid E_{1}^{a}=0,A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity 2 intervals}}}}{{=}}$ $\displaystyle 1\leavevmode\nobreak\ .$

###  C.1. Alternative motivation using cross world assumptions

Instead of (18), suppose the following cross-world equality holds:

(19) $\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid\Delta Y_{1}^{a}=0,L)$
$\displaystyle=P(\Delta Y_{2}^{a}=1\mid\Delta Y_{1}^{a}=0,L)\text{ w.p.
1}\leavevmode\nobreak\ .$

The equality (19) is motivated by the following: the infectious outcome during
time interval 2 would be the same in those who were naturally uninfected,
regardless of whether or not they would have been isolated during time
interval 1. However, this justification may be deceptively simple: the
equality (19) is difficult to justify in principle because it involves a
cross-world quantity on the left hand side, which is difficult to interpret.
Therefore, although (19) may provide intuition for (3), we do not endorse the
assumption as a sufficient justification for (3).

Expression (19) implies the single world inequality (3). To see this, we have
from the laws of probability that

$\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid L)$ $\displaystyle=$
$\displaystyle P(\Delta Y_{2}^{a,e_{1}=0}=1\mid\Delta Y_{1}^{a}=0,L)P(\Delta
Y_{1}^{a}=0\mid L)$ $\displaystyle\quad+P(\Delta Y_{2}^{a,e_{1}=0}=1\mid\Delta
Y_{1}^{a}=1,L)P(\Delta Y_{1}^{a}=1\mid L)\leavevmode\nobreak\ .$

The inequality (3) follows from substituting (19) on the right hand side, and
using the inequality $0\leq P(\Delta Y_{2}^{a,e_{1}=0}=1\mid\Delta
Y_{1}^{a}=1,L)\leq 1$.

##  Appendix D Identification with multiple versions of exposure

###  D.1. Identification assumptions

In this section, we establish conditions that allow identification and
hypothesis testing of vaccine waning in the presence of multiple versions of
treatment. Suppose that multiple versions of the observed exposure $E_{k}=1$
are present in the observed data. For example, among individuals with
$E_{k}=1$, there may be subgroups that are exposed 1) more than once during
interval $k$, 2) to larger (or smaller) infectious inocula per infectious
exposure or 3) at different anatomical barriers, for example gastrointestinal
versus respiratory mucosa. In contrast, the counterfactuals $\Delta
Y_{1}^{a,e_{1}=1}$ and $\Delta Y_{2}^{a,e_{1}=0,e_{2}=1}$ refer to potential
outcomes under a well-defined, controlled exposure $e_{k}=1$, e.g. by
intranasal inoculation with a particular quantity of infectious inoculum, in
keeping with Section 3.1. We denote the exposure version (quantity of the
controlled infectious inoculum) by $q$. In this case, Assumption 1 may fail
for $e_{1}=1$ or $e_{2}=1$, as there may be some individuals who would have
developed the outcome under the observed exposure ($E_{k}=1$), but not under
the counterfactual controlled exposure ($e_{k}=1$) or vice versa. However,
throughout this section we will continue to assume that there is only one
version of not being exposed, such that Assumption 1 holds whenever $e_{1}=0$
and $e_{2}=0$.

To accommodate multiple versions of the observed exposure $E_{k}=1$, we will
consider a modified version $G$ of the vaccine trial described in Section 2,
motivated by VanderWeele and Hernán (2013) and VanderWeele (2022). In the
modified trial $G$ (Figure 5), individuals are first randomized to vaccine
versus placebo, $A\in\\{0,1\\}$, and then to a version of infectious exposure
$Q_{1},Q_{2}\in\mathcal{Q}$ during intervals 1 and 2 respectively. The support
$\mathcal{Q}$ contains a collection of well-defined controlled procedures to
expose individuals to infectious inocula in different ways; for example by
intranasal inoculation with a pipette containing a random quantity $Q_{k}$ of
infectious inoculum, drawn from a pre-specified distribution. As before, we
assume that there is only one version of $Q_{k}$ where individuals are not
exposed to the infectious agent, and denote this by $Q_{k}=0$. In particular,
we let the intervention that assigns $q_{k}=0$ in $G$ be identical to the
intervention that assigns $e_{k}=0$ in the original trial for $k\in\\{1,2\\}$.
In the modified trial $G$, we define the exposure status $E_{k}$ to be a
coarse-grained version of $Q_{k}$: for $k\in\\{1,2\\}$, let

(20) $\displaystyle E_{k}=I(Q_{k}\neq 0)\text{ and
}E_{2}^{q_{1}=0}=I(Q_{2}^{q_{1}=0}\neq 0)\leavevmode\nobreak\ .$

To establish a relation between the modified trial $G$ and the original
vaccine trial, we introduce the following assumption.

######  Assumption 9 (Equivalence of the modified trial $G$).

The modified trial $G$ is conducted in an identical population to the trial in
Section 2, with a choice of $\mathcal{Q}$ and randomization rule for
$A,Q_{1},Q_{2}$ such that

(21) $\displaystyle P_{G}(A,L,E_{1},\Delta Y_{1},E_{2},\Delta
Y_{2})=P(A,L,E_{1},\Delta Y_{1},E_{2},\Delta Y_{2})\leavevmode\nobreak\ ,$
(22) $\displaystyle P_{G}(A,L,E_{1},\Delta
Y_{1}^{q_{1}=0},E_{2}^{q_{1}=0},\Delta Y_{2}^{q_{1}=0})=P(A,L,E_{1},\Delta
Y_{1}^{e_{1}=0},E_{2}^{e_{1}=0},\Delta Y_{2}^{e_{1}=0})\leavevmode\nobreak\ ,$

where right hand side is the distribution of the trial in Section 2.

Importantly, the original trial in Section 2 and the modified trial $G$ are
not necessarily identical, but they are equivalent in the sense of Assumption
9. The equivalence assumption can fail if the controlled infectious exposure
versions in $\mathcal{Q}$ are not representative of the infectious exposures
in the original trial, meaning that there does not exist any randomization
rules for $A,Q_{1},Q_{2}$ for controlled exposures $\mathcal{Q}$ in the trial
$G$ such that $P_{G}$ satisfies (21)-(22).

$A$$Q_{1}$$Q_{2}$$\Delta Y_{1}$$\Delta Y_{2}$$L$$U_{Y}$$U_{E}$ Figure 5.
Modified trial $G$ with exposure versions $Q_{1}$ and $Q_{2}$

$A$ $a$ $Q_{1}^{a}$ $q$ $Q_{2}^{a,q_{1}=q}$$\Delta Y_{1}^{a,q_{1}=q}$$\Delta
Y_{2}^{a,q_{1}=q}$$L$$U_{Y}$$U_{E}$

(a)

$A$ $a$ $Q_{1}^{a}$ $q_{1}=0$ $Q_{2}^{a,q_{1}=0}$ $q$ $\Delta
Y_{1}^{a,q_{1}=0}$$\Delta Y_{2}^{a,q_{1}=0,q_{2}=q}$$L$$U_{Y}$$U_{E}$

(b)

Figure 6. Interventions on exposure to the infectious agent in the modified
trial $G$ during interval 1 (A) and interval 2 (B)

In this section, our aim is to identify

$\displaystyle\text{VE}_{1}^{\mathrm{challenge}}(l,q)$
$\displaystyle=1-\frac{E_{G}[\Delta Y_{1}^{a=1,q_{1}=q}\mid L=l]}{E_{G}[\Delta
Y_{1}^{a=0,q_{1}=q}\mid L=l]}\leavevmode\nobreak\ ,$
$\displaystyle\text{VE}_{2}^{\mathrm{challenge}}(l,q)$
$\displaystyle=1-\frac{E_{G}[\Delta Y_{2}^{a=1,q_{1}=0,q_{2}=q}\mid
L=l]}{E_{G}[\Delta Y_{2}^{a=0,q_{1}=0,q_{2}=q}\mid L=l]}\leavevmode\nobreak\
,$

the challenge effect under infectious exposure $q$ in trial $G$ (Figure 6), in
terms of the observed distribution $P(A,L,\Delta Y_{1},\Delta Y_{2})$ in the
original trial. To this end, we introduce the following assumptions.

######  Assumption 10 (Consistency (multiple exposure versions)).

We assume that interventions on treatment $A$ and exposures $Q_{1},Q_{2}$ are
well-defined such that the following consistency conditions hold in trial $G$
for all $a\in\\{0,1\\}$ and $q_{1},q_{2}\in\mathcal{Q}$:

  1. (i)

$\text{ if }A=a\text{ then
}Q_{1}=Q_{1}^{a},Q_{2}^{q_{1}=0}=Q_{2}^{a,q_{1}=0},\Delta
Y_{2}^{q_{1}=0}=\Delta Y_{2}^{a,q_{1}=0}$ ,

  2. (ii)

$\text{ if }A=a,Q_{1}=q_{1}\text{ then }\Delta Y_{1}=\Delta Y_{1}^{a,q_{1}}$ ,

  3. (iii)

$\text{ if }A=a,Q_{2}^{a,q_{1}=0}=q_{2}\text{ then }\Delta
Y_{2}^{a,q_{1}=0}=\Delta Y_{2}^{a,q_{1}=0,q_{2}}$ .

######  Assumption 11 (Treatment exchangeability (multiple exposure
versions)).

For all $q_{1},q_{2}\in\mathcal{Q}$,

$\displaystyle\Delta Y_{1}^{a,q_{1}},\Delta
Y_{2}^{a,q_{1},q_{2}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}A\mid L\leavevmode\nobreak\ .$

######  Assumption 12 (Exposure exchangeability (multiple exposure versions)).

For all $a\in\\{0,1\\}$ and $q_{1},q_{2}\in\mathcal{Q}$,

$\displaystyle\Delta Y_{1}^{a,q_{1}},\Delta
Y_{2}^{a,q_{1}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}Q_{1}^{a}\mid A=a,L\leavevmode\nobreak\
,\text{ and }\Delta Y_{2}^{a,q_{1},q_{2}}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}Q_{2}^{a,q_{1}}\mid A=a,L\leavevmode\nobreak\
.$

######  Assumption 13 (No waning of placebo (multiple exposure versions)).

For all $q\in\mathcal{Q}$,

$\displaystyle E_{G}[\Delta Y_{1}^{a=0,q_{1}=q}\mid L]=E_{G}[\Delta
Y_{2}^{a=0,q_{1}=0,q_{2}=q}\mid L]\text{ w.p.\leavevmode\nobreak\
1}\leavevmode\nobreak\ .$

######  Assumption 14 (Stationarity of exposure versions among the exposed).

For all $a\in\\{0,1\\}$ and $q\in\mathcal{Q}$,

$\displaystyle P_{G}(Q_{1}\leq q\mid E_{1}=1,A=a,L)=P_{G}(Q_{2}^{q_{1}=0}\leq
q\mid E_{2}^{q_{1}=0}=1,A=a,L)\text{ w.p.\leavevmode\nobreak\
1}\leavevmode\nobreak\ .$

Assumption 14 is closely related to the “Similar Study Environment” assumption
by Fintzi and Follmann (2021):

> “The proportional hazards model allows for the attack rate to change with
> time. But if the pathogen mutates to a form that is resistant to vaccine
> effects, efficacy may appear to wane. Another possibility is if human
> behavior changes in such a way that the vaccine is less effective. For
> example, if there is less mask wearing in the community over the study, the
> viral inoculum at infection may increase over the study and overwhelm the
> immune response for later cases. Vaccines may work less well against larger
> inoculums and thus VE might appear to wane. For viral mutation, analyses
> could be run separately for different major strains provided they occur both
> prior and post crossover.”

An assumption such as Assumption 14 or the Similar Study Environment
assumption seems to be a bare minimum needed to identify waning using
cumulative incidences of the infectious event; without such an assumption one
cannot discern whether changes in cumulative incidences over time are due to
changes in the exposure versions or changes in the challenge effect, as also
alluded to in the quote from Fintzi and Follmann (2021). In particular, this
consideration also applies to conventional approaches to vaccine waning, i.e.
the direct comparison of $\text{VE}_{1}^{\mathrm{obs}}$ vs.
$\text{VE}_{2}^{\mathrm{obs}}$ as considered by e.g. Fintzi and Follmann
(2021). Assumption 14 does not require that the same number of individuals are
exposed during intervals 1 and 2. In other words, the assumption is not
necessarily violated if $P(E_{1}=1\mid L)<P(E_{2}=1\mid L)$, e.g. if the
prevalence of infection increases in the larger population that embeds the
trial participants. For instance, in an all-or-nothing model of vaccine
protection (Halloran et al., 2012), immune individuals will never contract
infection, regardless of the number of exposures during a given time interval,
and those who are not immune will always contract infection if exposed.
However, in a leaky model of vaccine protection, individuals with multiple
exposures during interval $k$ will have a greater risk of the outcome than an
individual with a single exposure. If $P(E_{1}=1\mid L)\ll P(E_{2}=1\mid L)$
w.p. 1, e.g. due to a large difference in the lengths of intervals $k=1$ vs.
$k=2$, or due to a large change in the infection prevalence, then multiple
exposures are more likely during interval 2 compared to 1, which could violate
Assumption 14.

If one compares the incidence of recent versus early vacinees during the same
interval of calendar time, as suggested by Lipsitch et al. (2019), then
Assumption 14 is particularly plausible in the blinded crossover trial
discussed by Follmann et al. (2021), where individuals are randomly assigned
to vaccine versus control at baseline, and then cross over to the other
treatment arm after a pre-specified interval of time.

To state the next assumption, we the define the dose-response relations
$\varphi_{k}(q)$ and an auxiliary function $h$.

$\displaystyle\varphi_{1}(q)$ $\displaystyle=E[\Delta Y_{1}^{a=1,q_{1}=q}\mid
L=l]\leavevmode\nobreak\ ,$ $\displaystyle\varphi_{2}(q)$
$\displaystyle=E[\Delta Y_{2}^{a=1,q_{1}=0,q_{2}=q}\mid
L=l]\leavevmode\nobreak\ ,$ $\displaystyle h(q)$
$\displaystyle=\frac{\varphi_{1}(q)}{E_{G}[\varphi_{1}(Q_{1})\mid
E_{1}=1,A=1,L=l]}-\frac{\varphi_{2}(q)}{E_{G}[\varphi_{2}(Q_{1})\mid
E_{1}=1,A=1,L=l]}\leavevmode\nobreak\ .$

######  Assumption 15 (Existence of a representative exposure (weak)).

There exists a representative exposure $q_{l}^{\ast}\in\mathcal{Q}$ such that

$\displaystyle h(q_{l}^{\ast})=0\leavevmode\nobreak\ .$

Since $E_{G}[h(Q_{1})\mid E_{1}=1,A=1,L=l]=0$, Assumption 15 is implied by the
mean value theorem for a non-trivial class of dose-response relations
$\varphi_{k}(q)$ and distributions of $Q_{k}$.

######  Assumption 16 (Existence of a representative exposure (strong)).

There exists a representative exposure $q_{l}^{\ast\ast}\in\mathcal{Q}$ such
that

(23) $\displaystyle E_{G}[\Delta Y_{1}^{a,q_{1}=q_{l}^{\ast\ast}}\mid L=l]$
$\displaystyle=E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}}\mid L=l]\mid
E_{1}=1,A=a,L=l]\leavevmode\nobreak\ ,$ (24) $\displaystyle E_{G}[\Delta
Y_{2}^{a,q_{1}=0,q_{2}=q_{l}^{\ast\ast}}\mid L=l]$
$\displaystyle=E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{q_{1}=0}}\mid
L=l]\mid E_{2}^{q_{1}=0}=1,A=a,L=l]\leavevmode\nobreak\ ,$

for all $a\in\\{0,1\\}$.

Assumption 16 can be regarded as a consistency assumption in conditional
expectation, and states that an infectious inoculum of version
$q_{l}^{\ast\ast}$ leads to the same outcome in conditional expectation as an
average over a random version $Q_{1}$ among individuals with $E_{1}=1$, and
likewise for a random version $Q_{2}^{q_{1}=0}$ among individuals with
$E_{2}^{q_{1}=0}=1$. In other words, individuals with $Q_{1}>q_{l}^{\ast\ast}$
are perfectly balanced by individuals with $Q_{1}<q_{l}^{\ast\ast}$, for both
treatment groups $A\in\\{0,1\\}$, and correspondingly for the second time
interval. One scenario where this happens is if the conditional distribution
of $Q_{1},Q_{2}^{q_{1}=0}$ is narrow and centers around the particular version
$q_{l}^{\ast\ast}$. Then, only one version of the treatment occurs
effectively. This is equivalent to the statement that the dose-response
relations $E_{G}[\Delta Y_{1}^{a,q}\mid L=l]$ and $E_{G}[\Delta
Y_{2}^{a,q_{1}=0,q_{2}=q}\mid L=l]$, viewed as functions of $q$, do not vary
in $q$ over the range of treatment versions with non-negligible probability,
i.e. that all the observed exposure versions lead to the same outcomes in
conditional expectation. This occurs in an all-or-nothing model of vaccine
protection, but not necessarily in a leaky model (Halloran et al., 2012).

###  D.2. Identification results

######  Proposition 2.

Under Assumptions 1 (i) and (ii) for $e_{1}=0$ and Assumptions 8-12,

(25) $\displaystyle E[\Delta Y_{1}^{a}\mid
E_{1}^{a}=1,A=a,L=l]=E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}}\mid L=l]\mid
E_{1}=1,A=a,L=l]\leavevmode\nobreak\ ,$ $\displaystyle E[\Delta
Y_{2}^{a,e_{1}=0}\mid E_{2}^{a,e_{1}=0}=1,A=a,L=l]$ (26)
$\displaystyle\quad=E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{q_{1}=0}}\mid
L=l]\mid E_{2}^{q_{1}=0}=1,A=a,L=l]\leavevmode\nobreak\ .$

Under the additional Assumptions 2-4 and Assumption 7,

(27) $\displaystyle 1-\frac{E_{G}[E_{G}[\Delta Y_{1}^{a=1,Q_{1}}\mid L=l]\mid
E_{1}=1,A=1,L=l]}{E_{G}[E_{G}[\Delta Y_{1}^{a=0,Q_{1}}\mid L=l]\mid
E_{1}=1,A=0,L=l]}$
$\displaystyle=\text{VE}_{1}^{\mathrm{obs}}(l)\leavevmode\nobreak\ ,$ (28)
$\displaystyle 1-\frac{E_{G}[E_{G}[\Delta
Y_{2}^{a=1,q_{1}=0,Q_{2}^{q_{1}=0}}\mid L=l]\mid
E_{2}^{q_{1}=0}=1,A=1,L=l]}{E_{G}[E_{G}[\Delta
Y_{2}^{a=0,q_{1}=0,Q_{2}^{q_{1}=0}}\mid L=l]\mid E_{2}^{q_{1}=0}=1,A=0,L=l]}$
$\displaystyle\in[\mathcal{L}_{2}(l),\mathcal{U}_{2}(l)]\leavevmode\nobreak\
.$

###### Proof.

Expression (25) follows from

$\displaystyle E[\Delta Y_{1}^{a}\mid E_{1}^{a}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency 2 intervals}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle E[\Delta Y_{1}\mid E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:equivalence_modified_trial}}}}{{=}}$ $\displaystyle E_{G}[\Delta
Y_{1}\mid E_{1}=1,A=a,L]$ $\displaystyle=$ $\displaystyle E_{G}[E_{G}[\Delta
Y_{1}\mid Q_{1},E_{1}=1,A=a,L]\mid E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\eqref{eq: Ek definition}}}{{=}}$
$\displaystyle E_{G}[E_{G}[\Delta Y_{1}\mid Q_{1},A=a,L]\mid E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency_multiple_versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}^{a}}\mid Q_{1}^{a},A=a,L]\mid
E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: exposure exchageability multiple versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}^{a}}\mid A=a,L]\mid E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: treatment exch multiple versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}^{a}}\mid L]\mid E_{1}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency_multiple_versions}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle E_{G}[E_{G}[\Delta Y_{1}^{a,Q_{1}}\mid L]\mid
E_{1}=1,A=a,L]\leavevmode\nobreak\ .$

The penultimate equality used the positivity condition $P_{G}(A=a\mid L)>0$
for all $a\in\\{0,1\\}$ w.p. 1, which follows from Assumption 8 and definition
of the trial $G$ (Assumption 9). Likewise, (26) follows from

$\displaystyle E[\Delta Y_{2}^{a,e_{1}=0}\mid E_{2}^{a,e_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency 2 intervals}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle E[\Delta Y_{2}^{e_{1}=0}\mid E_{2}^{e_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:equivalence_modified_trial}}}}{{=}}$ $\displaystyle E_{G}[\Delta
Y_{2}^{q_{1}=0}\mid E_{2}^{q_{1}=0}=1,A=a,L]$ $\displaystyle=$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{2}^{q_{1}=0}\mid
Q_{2}^{q_{1}=0},E_{2}^{q_{1}=0}=1,A=a,L]\mid E_{2}^{q_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\eqref{eq: Ek definition}}}{{=}}$
$\displaystyle E_{G}[E_{G}[\Delta Y_{2}^{q_{1}=0}\mid
Q_{2}^{q_{1}=0},A=a,L]\mid E_{2}^{q_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency_multiple_versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{a,q_{1}=0}}\mid
Q_{2}^{a,q_{1}=0},A=a,L]\mid E_{2}^{q_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: exposure exchageability multiple versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{a,q_{1}=0}}\mid A=a,L]\mid
E_{2}^{q_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: treatment exch multiple versions}}}}{{=}}$ $\displaystyle
E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{a,q_{1}=0}}\mid L]\mid
E_{2}^{q_{1}=0}=1,A=a,L]$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency_multiple_versions}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle E_{G}[E_{G}[\Delta Y_{2}^{a,q_{1}=0,Q_{2}^{q_{1}=0}}\mid L]\mid
E_{2}^{q_{1}=0}=1,A=a,L]\leavevmode\nobreak\ .$

In the first and second lines, we have used that quantities under intervention
$e_{1}=0$ are well-defined, which follows from Assumption 1 (ii) for
$e_{1}=0$.

We proceed similarly to Section B.1.

$\displaystyle\frac{E[\Delta Y_{1}^{a=1}\mid E_{1}^{a=1}=1,A=1,L]}{E[\Delta
Y_{1}^{a=0}\mid E_{1}^{a=0}=1,A=0,L]}$ $\displaystyle=$
$\displaystyle\frac{E[I(E_{1}^{a=1}=1)\Delta Y_{1}^{a=1}\mid
A=1,L]}{E[I(E_{1}^{a=0}=1)\Delta Y_{1}^{a=0}\mid
A=0,L]}\times\frac{P(E_{1}^{a=0}=1\mid A=0,L)}{P(E_{1}^{a=1}=1\mid A=1,L)}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions\leavevmode\nobreak\
\ref{ass: treatment exchageability 2 intevals}, \ref{ass: exposure positivity
2 intervals}}}}{{=}}$ $\displaystyle\frac{E[I(E_{1}^{a=1}=1)\Delta
Y_{1}^{a=1}\mid A=1,L]}{E[I(E_{1}^{a=0}=1)\Delta Y_{1}^{a=0}\mid
A=0,L]}\times\frac{P(E_{1}^{a=0}=1\mid L)}{P(E_{1}^{a=1}=1\mid L)}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:no effect on exposure 2 intervals}}}}{{=}}$
$\displaystyle\frac{E[I(E_{1}^{a=1}=1)\Delta Y_{1}^{a=1}\mid
A=1,L]}{E[I(E_{1}^{a=0}=1)\Delta Y_{1}^{a=0}\mid A=0,L]}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: exposure necessity 2 intervals}}}}{{=}}$
$\displaystyle\frac{E[\Delta Y_{1}^{a=1}\mid A=1,L]}{E[\Delta Y_{1}^{a=0}\mid
A=0,L]}$ (29)
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions\leavevmode\nobreak\
\ref{ass:consistency 2 intervals}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle\frac{E[\Delta Y_{1}\mid A=1,L]}{E[\Delta Y_{1}\mid
A=0,L]}\leavevmode\nobreak\ ,$

and

$\displaystyle\frac{E[\Delta Y_{2}^{a=1,e_{1}=0}\mid
E_{2}^{a=1,e_{1}=0}=1,A=1,L]}{E[\Delta Y_{2}^{a=0,e_{1}=0}\mid
E_{2}^{a=0,e_{1}=0}=1,A=0,L]}$ $\displaystyle=$
$\displaystyle\frac{E[I(E_{2}^{a=1,e_{1}=0}=1)\Delta Y_{2}^{a=1,e_{1}=0}\mid
A=1,L]}{E[I(E_{2}^{a=0,e_{1}=0}=1)\Delta Y_{2}^{a=0,e_{1}=0}\mid
A=0,L]}\times\frac{P(E_{2}^{a=0,e_{1}=0}=1\mid
A=0,L)}{P(E_{2}^{a=1,e_{1}=0}=1\mid A=1,L)}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions\leavevmode\nobreak\
\ref{ass: treatment exchageability 2 intevals}, \ref{ass: exposure positivity
2 intervals}}}}{{=}}$ $\displaystyle\frac{E[I(E_{2}^{a=1,e_{1}=0}=1)\Delta
Y_{2}^{a=1,e_{1}=0}\mid A=1,L]}{E[I(E_{2}^{a=0,e_{1}=0}=1)\Delta
Y_{2}^{a=0,e_{1}=0}\mid A=0,L]}\times\frac{P(E_{2}^{a=0,e_{1}=0}=1\mid
L)}{P(E_{2}^{a=1,e_{1}=0}=1\mid L)}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:no effect on exposure 2 intervals}}}}{{=}}$
$\displaystyle\frac{E[I(E_{2}^{a=1,e_{1}=0}=1)\Delta Y_{2}^{a=1,e_{1}=0}\mid
A=1,L]}{E[I(E_{2}^{a=0,e_{1}=0}=1)\Delta Y_{2}^{a=0,e_{1}=0}\mid A=0,L]}$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: exposure necessity 2 intervals}}}}{{=}}$
$\displaystyle\frac{E[\Delta Y_{2}^{a=1,e_{1}=0}\mid A=1,L]}{E[\Delta
Y_{2}^{a=0,e_{1}=0}\mid A=0,L]}$ (30)
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass:consistency 2 intervals}\leavevmode\nobreak\ (i)}}}{{=}}$
$\displaystyle\frac{E[\Delta Y_{2}^{e_{1}=0}\mid A=1,L]}{E[\Delta
Y_{2}^{e_{1}=0}\mid A=0,L]}$ (31)
$\displaystyle\stackrel{{\scriptstyle\text{Assumption\leavevmode\nobreak\
\ref{ass: exclusion 2 intervals}}}}{{\in}}$ $\displaystyle\left[\frac{E[\Delta
Y_{2}\mid A=1,L]}{E[\Delta Y_{1}+\Delta Y_{2}\mid A=0,L]},\frac{E[\Delta
Y_{1}+\Delta Y_{2}\mid A=1,L]}{E[\Delta Y_{2}\mid
A=0,L]}\right]\leavevmode\nobreak\ .$

Combining (25) and (29) gives (27). Likewise, (26) and (31) imply (28). ∎

Expressions (25)-(26) state that the conditional exposure risk among the
exposed is equal to a marginalization of the dose-response relations
$\varphi_{1}(Q_{1})$ and $\varphi(Q_{2}^{q_{1}=0})$ over random exposure
versions $Q_{1}$ and $Q_{2}^{q_{1}=0}$. Thus, (27)-(28) allows us to interpret
(4) and (5)-(6) as identification formulas for a randomized exposure
intervention, where an investigator draws a version $Q_{1}$ and
$Q_{2}^{q_{1}=0}$ at random according to the conditional distribution
functions $F_{Q_{1}\mid E_{1}=1,A=a,L=l}$ and $F_{Q_{2}^{q_{1}=0}\mid
E_{2}^{q_{1}=0}=1,A=a,L=l}$. However, a contrast of (27) vs. (28) could be
non-null due to changes in exposure versions over time, unless Assumptions 14
holds.

Let $\mathrm{H}_{0}$ be the strict null hypothesis that the vaccine does not
wane for any exposure version $q\in\mathcal{Q}$,

$\displaystyle\mathrm{H}_{0}:\leavevmode\nobreak\ E[\Delta
Y_{1}^{a=1,q_{1}=q}\mid L]=E[\Delta Y_{2}^{a=1,q_{1}=0,q_{2}=q}\mid L]\text{
w.p.\leavevmode\nobreak\ 1 for all }q\in\mathcal{Q}\leavevmode\nobreak\ .$

######  Proposition 3.

Under Assumptions 1 (i) and (ii) for $e_{1}=0$, Assumptions 2-4 and
Assumptions 7-14,

(32) $\displaystyle\mathrm{H}_{0}\implies\mathcal{L}_{\psi}(l)\leq
1\leq\mathcal{U}_{\psi}(l)\leavevmode\nobreak\ .$

###### Proof.

Evaluating the ratio of (25) and (26) for $a=0$, and using Assumptions 13 and
14, gives

(33) $\displaystyle\frac{E[\Delta Y_{1}^{a=0}\mid
E_{1}^{a=0}=1,A=0,L]}{E[\Delta Y_{2}^{a=0,e_{1}=0}\mid
E_{2}^{a=0,e_{1}=0}=1,A=0,L]}=1\leavevmode\nobreak\ .$

Similarly, by evaluating the ratio of (25) and (26) for $a=1$ under
$\mathrm{H}_{0}$ and Assumption 14, we find that

(34) $\displaystyle\frac{E[\Delta Y_{1}^{a=1}\mid
E_{1}^{a=1}=1,A=1,L]}{E[\Delta Y_{2}^{a=1,e_{1}=0}\mid
E_{2}^{a=1,e_{1}=0}=1,A=1,L]}=1\leavevmode\nobreak\ .$

Taking the ratio of (33) and (34) gives

(35) $\displaystyle 1=$ $\displaystyle\frac{\frac{E[\Delta
Y_{2}^{a=1,e_{1}=0}\mid E_{2}^{a=1,e_{1}=0}=1,A=1,L]}{E[\Delta
Y_{2}^{a=0,e_{1}=0}\mid E_{2}^{a=0,e_{1}=0}=1,A=0,L]}}{\frac{E[\Delta
Y_{1}^{a=1}\mid E_{1}^{a=1}=1,A=1,L]}{E[\Delta Y_{1}^{a=0}\mid
E_{1}^{a=0}=1,A=0,L]}}\leavevmode\nobreak\ .$

Using (29) and (31) in (35) gives the final result. ∎

By testing whether the observed data violates (32), one can test the null
hypothesis $\mathrm{H}_{0}$. Proposition 3 clarifies that it is possible to
test for the presence of vaccine waning even under arbitrary distributions of
versions of treatment, as long as the distribution is stationary over time. A
violation of $\mathrm{H}_{0}$ implies that there exists at least one
infectious inoculum $q$ for which the vaccine wanes, but it does not establish
for which inocula $q$ the vaccine wanes. However, it would be surprising if
$\text{VE}_{1}^{\mathrm{challenge}}(l,q)>\text{VE}_{2}^{\mathrm{challenge}}(l,q)$
for some $q$ while
$\text{VE}_{1}^{\mathrm{challenge}}(l,q)<\text{VE}_{2}^{\mathrm{challenge}}(l,q)$
for other versions $q$, and therefore a violation of $\mathrm{H}_{0}$ gives
meaningful insight into vaccine waning, even though it does not tell us by how
much the vaccine wanes for each exposure version $q$. Furthermore, the power
to reject $\mathrm{H}_{0}$ is driven by exposure versions that appear
frequently, or wane substantially, in the observed data, and therefore a
rejection of $\mathrm{H}_{0}$ gives insight on waning of such exposure
versions.

In the following propositions, we clarify conditions which allow us to
interpret previous identification results for
$\text{VE}_{1}^{\mathrm{challenge}}$ and $\text{VE}_{2}^{\mathrm{challenge}}$
in terms of controlled exposures to non-random, representative infectious
inocula.

Let $\psi(l,q)=E_{G}[\Delta Y_{1}^{a=1,q_{1}=q}\mid L=l]/E_{G}[\Delta
Y_{2}^{a=1,q_{1}=0,q_{2}=q}\mid L=l]$.

######  Proposition 4.

Under Assumptions 1 (i) and (ii) for $e_{1}=0$, Assumptions 2-4 and
Assumptions 7-15,
$\mathcal{L}_{\psi}(l)\leq\psi(l,q^{\ast})\leq\mathcal{U}_{\psi}(l)$.

###### Proof.

Multiplying both sides of (29) by $E_{G}[\Delta Y_{1}^{a=1,q_{1}=q}\mid
L]/E_{G}[\Delta Y_{1}^{a=0,q_{1}=q}\mid L]$ and both sides of (30) by
$E_{G}[\Delta Y_{2}^{a=1,q_{1}=0,q_{2}=q}\mid L]/E_{G}[\Delta
Y_{2}^{a=0,q_{1}=0,q_{2}=q}\mid L]$ gives

(36) $\displaystyle\scriptstyle\frac{P_{G}(\Delta Y_{1}^{a=1,q_{1}=q}=1\mid
L)}{P_{G}(\Delta Y_{1}^{a=0,q_{1}=q}=1\mid L)}$
$\displaystyle=\scriptstyle\frac{P(\Delta Y_{1}=1\mid A=1,L)}{P(\Delta
Y_{1}=1\mid A=0,L)}\times\frac{\frac{P_{G}(\Delta Y_{1}^{a=1,q_{1}=q}=1\mid
L)}{P(\Delta Y_{1}^{a=1}=1\mid E_{1}^{a=1}=1,A=1,L)}}{\frac{P_{G}(\Delta
Y_{1}^{a=0,q_{1}=q}=1\mid L)}{P(\Delta Y_{1}^{a=0}=1\mid
E_{1}^{a=0}=1,A=0,L)}}\leavevmode\nobreak\ ,$ (37)
$\displaystyle\scriptstyle\frac{P_{G}(\Delta Y_{2}^{a=1,q_{1}=0,q_{2}=q}=1\mid
L)}{P_{G}(\Delta Y_{2}^{a=0,q_{1}=0,q_{2}=q}=1\mid L)}$
$\displaystyle=\scriptstyle\frac{P(\Delta Y_{2}^{e_{1}=0}=1\mid
A=1,L)}{P(\Delta Y_{2}^{e_{1}=0}=1\mid A=0,L)}\times\frac{\frac{P_{G}(\Delta
Y_{2}^{a=1,q_{1}=0,q_{2}=q}=1\mid L)}{P(\Delta Y_{2}^{a=1,e_{1}=0}=1\mid
E_{2}^{a=1,e_{1}=0}=1,A=1,L)}}{\frac{P_{G}(\Delta
Y_{2}^{a=0,q_{1}=0,q_{2}=q}=1\mid L)}{P(\Delta Y_{2}^{a=0,e_{1}=0}=1\mid
E_{2}^{a=0,e_{1}=0}=1,A=0,L)}}\leavevmode\nobreak\ .$

Assumptions 14 and 15 together imply that

(38) $\displaystyle\scriptstyle\frac{P_{G}(\Delta
Y_{1}^{a=1,q_{1}=q_{l}^{\ast}}=1\mid L)}{E_{G}[E_{G}[\Delta
Y_{1}^{a=1,Q_{1}}\mid L]\mid E_{1}=1,A=1,L]}=\scriptstyle\frac{P_{G}(\Delta
Y_{2}^{a=1,q_{1}=0,q_{2}=q_{l}^{\ast}}=1\mid L)}{E_{G}[E_{G}[\Delta
Y_{2}^{a=1,q_{1}=0,Q_{2}^{q_{1}=0}}\mid L]\mid
E_{2}^{q_{1}=0}=1,A=1,L]}\leavevmode\nobreak\ .$

Next, Assumptions 13 and 14 imply that

(39) $\displaystyle\scriptstyle\frac{P_{G}(\Delta
Y_{1}^{a=0,q_{1}=q_{l}^{\ast}}=1\mid L)}{E_{G}[E_{G}[\Delta
Y_{1}^{a=0,Q_{1}}\mid L]\mid E_{1}=1,A=0,L]}=\scriptstyle\frac{P_{G}(\Delta
Y_{2}^{a=0,q_{1}=0,q_{2}=q_{l}^{\ast}}=1\mid L)}{E_{G}[E_{G}[\Delta
Y_{2}^{a=0,q_{1}=0,Q_{2}^{q_{1}=0}}\mid L]\mid
E_{2}^{q_{1}=0}=1,A=0,L]}\leavevmode\nobreak\ .$

Taking the ratio of (38) and (39), and using (25)-(26) gives

(40) $\displaystyle\frac{\frac{P_{G}(\Delta
Y_{1}^{a=1,q_{1}=q_{l}^{\ast}}=1\mid L)}{P(\Delta Y_{1}^{a=1}=1\mid
E_{1}^{a=1}=1,A=1,L)}}{\frac{P_{G}(\Delta Y_{1}^{a=0,q_{1}=q_{l}^{\ast}}=1\mid
L)}{P(\Delta Y_{1}^{a=0}=1\mid E_{1}^{a=0}=1,A=0,L)}}=\frac{\frac{P_{G}(\Delta
Y_{2}^{a=1,q_{1}=0,q_{2}=q_{l}^{\ast}}=1\mid L)}{P(\Delta
Y_{2}^{a=1,e_{1}=0}=1\mid E_{2}^{a=1,e_{1}=0}=1,A=1,L)}}{\frac{P_{G}(\Delta
Y_{2}^{a=0,q_{1}=0,q_{2}=q_{l}^{\ast}}=1\mid L)}{P(\Delta
Y_{2}^{a=0,e_{1}=0}=1\mid E_{2}^{a=0,e_{1}=0}=1,A=0,L)}}\leavevmode\nobreak\
.$

Finally, taking the ratio of (36) and (37), and using Assumption 4 to bound
$P(\Delta Y_{2}^{e_{1}=0}=1\mid A=1,L)/P(\Delta Y_{2}^{e_{1}=0}=1\mid A=0,L)$
and (40) to cancel the remaining unidentified fractions for $q=q_{l}^{\ast}$
gives the final result. ∎

######  Proposition 5.

Assumptions 1 (i) and (ii) for $e_{1}=0$, Assumptions 2-4 and Assumptions 7-12
combined with Assumption 16, imply that

(41)
$\displaystyle\text{VE}_{1}^{\mathrm{challenge}}(l,q_{l}^{\ast\ast})=\frac{E[\Delta
Y_{1}\mid A=1,L=l]}{E[\Delta Y_{1}\mid A=0,L=l]}\leavevmode\nobreak\ ,$ (42)
$\displaystyle\mathcal{L}_{2}(l)\leq$
$\displaystyle\text{VE}_{2}^{\mathrm{challenge}}(l,q_{l}^{\ast\ast})\leq\mathcal{U}_{2}(l)\leavevmode\nobreak\
.$

###### Proof.

By (25)-(26), Assumption 16 implies that

(43) $\displaystyle P_{G}(\Delta Y_{1}^{a,q_{1}=q_{l}^{\ast\ast}}=1\mid L)$
$\displaystyle=P(\Delta Y_{1}^{a}=1\mid E_{1}^{a}=1,A=a,L)\leavevmode\nobreak\
,$ (44) $\displaystyle P_{G}(\Delta
Y_{2}^{a,q_{1}=0,q_{2}=q_{l}^{\ast\ast}}=1\mid L)$ $\displaystyle=P(\Delta
Y_{2}^{a,e_{1}=0}=1\mid E_{2}^{a,e_{1}=0}=1,A=a,L)$

for all $a\in\\{0,1\\}$. We obtain (41) from using (43) in (36) and likewise
we obtain (42) from using (44) and Assumption 4 in (37).

∎

Similarly to Proposition 3, the identification results in Propositions 4-5 do
not tell us exactly for which exposure versions
$q_{l}^{\ast},q_{l}^{\ast\ast}$ we (potentially) identify vaccine waning.

##  Appendix E Extension to multiple time intervals and loss to follow-up

We assume that interventions on $A,E_{k},C_{k}$ for $k\in\\{1,\dots,K\\}$ are
well-defined (Definition 43 in Richardson and Robins (2013)). We use an
underbar to denote future variables, e.g.
$\underline{Y}_{k}=(Y_{k},\dots,Y_{K})$, and an overbar to denote the history
of a random variable through time $k$, e.g.
$\overline{E}_{k}=(E_{1},\dots,E_{k})$. Under an additional intervention to
prevent losses to follow-up, the challenge effect at time $k$ is defined as

$\displaystyle\text{VE}_{k}^{\mathrm{challenge}}(l)=1-\frac{E[\Delta
Y_{k}^{a=1,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}\mid L=l]}{E[\Delta
Y_{k}^{a=0,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}\mid
L=l]}\leavevmode\nobreak\ .$

Suppose that the following assumptions hold for all $a,k,\overline{e}_{k},l$.

######  Assumption 17 (Exposure necessity ($K$ intervals)).

$\displaystyle E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=0\implies\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=0\leavevmode\nobreak\ .$

######  Assumption 18 (No treatment effect on exposure in the unexposed ($K$
intervals)).

$\displaystyle
E_{k}^{a=0,\overline{e}_{k-1}=0,\overline{c}=0}=E_{k}^{a=1,\overline{e}_{k-1}=0,\overline{c}=0}\leavevmode\nobreak\
.$

######  Assumption 19 (Exposure effect restriction ($K$ intervals)).

$\displaystyle E[\Delta Y_{k}^{\overline{c}=0}\mid A=a,L]\leq E[\Delta
Y_{k}^{\overline{e}_{k-1}=0,\overline{c}=0}\mid A=a,L]\leq
E[Y^{\overline{c}=0}_{k}\mid A=a,L]\text{ w.p. 1}\leavevmode\nobreak\ .$

######  Assumption 20 (Exposure exchangeability ($K$ intervals)).

$\displaystyle\Delta
Y_{k}^{a,\overline{e}_{k-1},e_{k},\overline{c}=0}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}E_{k}^{\overline{e}_{k-1},\overline{c}=0}\mid
A=a,L\leavevmode\nobreak\ .$

######  Assumption 21 (Treatment exchangeability ($K$ intervals)).

$\displaystyle E_{k}^{a,\overline{e}_{k-1},\overline{c}=0},\Delta
Y_{k}^{a,\overline{e}_{k-1},e_{k},\overline{c}=0}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}A\mid L\leavevmode\nobreak\ .$

######  Assumption 22 (Exchangeability for loss to follow-up ($K$ intervals)).

(45)
$\displaystyle\underline{Y}_{k+1}^{a,\overline{c}=0}\mathchoice{\mathrel{\hbox
to0.0pt{$\displaystyle\perp$\hss}\mkern
2.0mu{\displaystyle\perp}}}{\mathrel{\hbox
to0.0pt{$\textstyle\perp$\hss}\mkern 2.0mu{\textstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptstyle\perp$\hss}\mkern
2.0mu{\scriptstyle\perp}}}{\mathrel{\hbox
to0.0pt{$\scriptscriptstyle\perp$\hss}\mkern
2.0mu{\scriptscriptstyle\perp}}}C_{k+1}^{a,\overline{c}=0}\mid
C_{k}^{a,\overline{c}=0},Y_{k}^{a,\overline{c}=0},A=a,L\leavevmode\nobreak\ .$

######  Assumption 23 (Positivity for loss to follow-up ($K$ intervals)).

$\displaystyle f_{Y_{k},C_{k},A,L}(0,0,a,l)>0$ (46)
$\displaystyle\quad\implies P(C_{k+1}=0\mid Y_{k}=0,C_{k}=0,A=a,L=l)>0\text{
for all }l\leavevmode\nobreak\ .$

Let $\Lambda_{k,a,l}=P(Y_{k}=1\mid Y_{k-1}=0,C_{k}=0,A=a,L=l)$ be a discrete
time hazard of the outcome.

######  Assumption 24 (Rare events ($K$ intervals)).

(47) $\displaystyle\sum_{k=1}^{K}\Lambda_{k,a,l}\ll 1\text{ for all
}a,l\leavevmode\nobreak\ .$

######  Theorem 2 (Bounds for $K$ intervals).

Under Assumption 8 and Assumptions 17-21,

$\displaystyle\mathcal{L}_{k}(l)\leq\text{VE}_{k}^{\mathrm{challenge}}(l)\leq\mathcal{U}_{k}(l)\leavevmode\nobreak\
,$

where

$\displaystyle\mathcal{L}_{k}(l)$
$\displaystyle=1-\frac{E[Y^{\overline{c}=0}_{k}\mid A=1,L=l]}{E[\Delta
Y^{\overline{c}=0}_{k}\mid A=0,L=l]}\leavevmode\nobreak\ ,$
$\displaystyle\mathcal{U}_{k}(l)$ $\displaystyle=1-\frac{E[\Delta
Y^{\overline{c}=0}_{k}\mid A=1,L=l]}{E[Y^{\overline{c}=0}_{k}\mid
A=0,L=l]}\leavevmode\nobreak\ ,$

whenever $E[\Delta Y^{\overline{c}=0}_{k}\mid A=a,L=l]>0$ for all
$a\in\\{0,1\\}$.

###### Proof.

$\displaystyle P(\Delta Y_{k}^{\overline{e}_{k-1}=0,\overline{c}=0}=1\mid
A=a,L)$ $\displaystyle=$ $\displaystyle P(\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
necessity K intervals}}}}{{=}}$ $\displaystyle
P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1,\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1\mid A=a,L)$ $\displaystyle=$
$\displaystyle P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1,\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0},\overline{c}=0}=1\mid
A=a,L)$ $\displaystyle=$ $\displaystyle
P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1,\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumption \ref{ass: exposure
exchageability K intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}=1\mid
A=a,L)P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1\mid A=a,L)$
$\displaystyle\stackrel{{\scriptstyle\text{Assumptions \ref{ass: exposure
positivity 2 intervals}, \ref{ass: treatment exchageability K
intevals}}}}{{=}}$ $\displaystyle P(\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}=1\mid
L)P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1\mid L)\leavevmode\nobreak\
.$

Therefore, by Assumption 19

$\displaystyle E[\Delta Y^{\overline{c}=0}_{k}\mid A=a,L]$
$\displaystyle\quad\leq E[\Delta
Y_{k}^{a,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}\mid
L]P(E_{k}^{a,\overline{e}_{k-1}=0,\overline{c}=0}=1\mid L)$
$\displaystyle\qquad\leq E[Y^{\overline{c}=0}_{k}\mid
A=a,L]\leavevmode\nobreak\ .$

Taking the ratio for $a=1$ vs. $a=0$, and using Assumption 18 to cancel the
resulting quotient of exposure probabilities gives

(48) $\displaystyle\frac{E[\Delta Y^{\overline{c}=0}_{k}\mid
A=1,L]}{E[Y^{\overline{c}=0}_{k}\mid A=0,L]}\leq\frac{E[\Delta
Y_{k}^{a=1,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}\mid L]}{E[\Delta
Y_{k}^{a=0,\overline{e}_{k-1}=0,e_{k}=1,\overline{c}=0}\mid
L]}\leq\frac{E[Y^{\overline{c}=0}_{k}\mid A=1,L]}{E[\Delta
Y^{\overline{c}=0}_{k}\mid A=0,L]}\leavevmode\nobreak\ .$

∎

Under Assumptions 22 and 23, we can identify the lower and upper limits of
Theorem 2 using the fact that

(49) $\displaystyle E[Y_{k}^{\overline{c}=0}\mid
A=a,L]=\sum_{r=1}^{k}\prod_{v=1}^{r-1}(1-\Lambda_{v,a,l})\cdot\Lambda_{r,a,L}\leavevmode\nobreak\
,$

see e.g. Appendix C in Janvin et al. (2023). Under Assumption 24, the product
in (49) simplifies and we obtain the approximate bounds

(50)
$\displaystyle\mathcal{L}_{k}(l)=1-\frac{\sum_{k^{\prime}=1}^{k}\Lambda_{k^{\prime},a=1,l}}{\Lambda_{k,a=0,l}}\quad\text{
and
}\quad\mathcal{U}_{k}(l)=1-\frac{\Lambda_{k,a=1,l}}{\sum_{k^{\prime}=1}^{k}\Lambda_{k^{\prime},a=0,l}}\leavevmode\nobreak\
.$

##  Appendix F Logistic regression with individual-level data

Suppose we have access to individual baseline variables $L_{i}$, treatment
$A_{i}$, loss to follow-up (censoring) indicator $C_{i,k}$ and outcome $\Delta
Y_{i,k}$ from $k\in\\{1,\dots,K\\}$ time intervals for individuals
$i\in\\{1,\dots,n\\}$. As we assume individuals in the sample are i.i.d., we
suppress the subscript $i$.

Let $f_{k}(a,l;\beta_{k})=E[Y_{k}\mid Y_{k-1}=0,C_{k}=0,A=a,L=l;\beta_{k}]$ be
a parametric model for $\Lambda_{k,a,l}$ for each time interval
$k\in\\{1,\dots,K\\}$, e.g. a logistic regression model. Suppose that the
number of time intervals $K$ is fixed, and that the parameter
$\beta_{k}=(\beta_{1,k},\dots,\beta_{d,k})^{T}$ has a fixed dimension $d$.
Denote the maximum likelihood estimator of $\beta_{k}$ by
$\widehat{\beta}_{k}$ and let
$\widehat{\Lambda}_{k,a,l;\widehat{\beta}_{k}}=f_{k}(a,l;\widehat{\beta}_{k})$
be a prediction of $\Lambda_{k,a,l}$ using the estimated coefficients
$\widehat{\beta}_{k}$. We then estimate the bounds $\mathcal{L}_{k}(l)$ and
$\mathcal{U}_{k}(l)$ using plugin estimators

(51)
$\displaystyle\widehat{\mathcal{L}}_{k}(l)=1-\frac{\sum_{k^{\prime}=1}^{k}\widehat{\Lambda}_{k^{\prime},a=1,l;\widehat{\beta}_{k}}}{\widehat{\Lambda}_{k,a=0,l;\widehat{\beta}_{k}}}\text{
and
}\widehat{\mathcal{U}}_{k}(l)=1-\frac{\widehat{\Lambda}_{k,a=1,l;\widehat{\beta}_{k}}}{\sum_{k^{\prime}=1}^{k}\widehat{\Lambda}_{k^{\prime},a=0,l;\widehat{\beta}_{k}}}\leavevmode\nobreak\
.$

##  Appendix G Summary data

###  G.1. Identification

We define each of intervals $k=1$ and $k=2$ by combining several subintervals,
summarized in Table 2, using publicly available summary data from Figure 2 in
Thomas et al. (2021). Let, $j=1,\dots,j_{k}$ denotes subinterval $j$ of
interval $k$, and let $s$ index a short time interval of duration $\Delta s=1$
day, such that $s_{k,j}^{-},s_{k,j}^{+}$ denote the first and last days of
subinterval $(k,j)$ respectively. Let $\tau_{k,j}$ denote the duration (in
days) of subinterval $(k,j)$. Next, let $T_{k,j,a}$ and $N_{k,j,a}$ denote
respectively the total person time at risk (in days) and the number of
recorded cases of infection during subinterval $(k,j)$ of treatment group
$A=a$. All quantities introduced in this paragraph are evaluated in a subset
$L=l$ of baseline covariates, even though they are not indexed by $l$ to
reduce clutter.

Assume that interventions on loss to follow-up $C_{s}$ are well-defined at all
times $s$ (Definition 43 in Richardson and Robins (2013)). We denote the
discrete-time hazard of $Y_{s}$ by $\lambda_{s,a,l}=P(Y_{s}=1\mid
C_{s}=0,Y_{s-1}=0,A=a,L=l)/\Delta s$, and assume the following.

######  Assumption 25 (Constant subinterval hazard).

Within each subinterval $(k,j)$ of every stratum stratum $\\{A=a,L=l\\}$, the
hazard $\lambda_{s,a,l}$ is a constant function of time $s$, denoted by
$\lambda_{s,a,l}=\lambda_{k,j,a}$ for all
$s\in\\{s_{k,j}^{-},\dots,s_{k,j}^{+}\\}$.

Importantly, we do not assume a constant value of the hazard for different
subintervals $(k,j)$. Assumption 25 is plausible for short time intervals,
such as subintervals $(k,j)$ in Table 2. Furthermore, (25) can be falsified by
inspecting whether the cumulative incidence curves, such as Figure 2 of Thomas
et al. (2021), deviate from the piecewise exponential form implied by
Assumption 25.