Potential test-negative design study bias in outbreak settings: application to Ebola vaccination in Democratic Republic of Congo

Abstract Background Infectious disease outbreaks present unique challenges to study designs for vaccine evaluation. Test-negative design (TND) studies have previously been used to estimate vaccine effectiveness and have been proposed for Ebola virus disease (EVD) vaccines. However, there are key differences in how cases and controls are recruited during outbreaks and pandemics of novel pathogens, whcih have implications for the reliability of effectiveness estimates using this design. Methods We use a modelling approach to quantify TND bias for a prophylactic vaccine under varying study and epidemiological scenarios. Our model accounts for heterogeneity in vaccine distribution and for two potential routes to testing and recruitment into the study: self-reporting and contact-tracing. We derive conventional and hybrid TND estimators for this model and suggest ways to translate public health response data into the parameters of the model. Results Using a conventional TND study, our model finds biases in vaccine effectiveness estimates. Bias arises due to differential recruitment from self-reporting and contact-tracing, and due to clustering of vaccination. We estimate the degree of bias when recruitment route is not available, and propose a study design to eliminate the bias if recruitment route is recorded. Conclusions Hybrid TND studies can resolve the design bias with conventional TND studies applied to outbreak and pandemic response testing data, if those efforts collect individuals’ routes to testing. Without route to testing, other epidemiological data will be required to estimate the magnitude of potential bias in a conventional TND study. Since these studies may need to be conducted retrospectively, public health responses should obtain these data, and generic protocols for outbreak and pandemic response studies should emphasize the need to record routes to testing.


S2.1 Model Diagram
: Model Diagram. This diagram illustrates the conceptual model of the population and recruitment process, showing: how the intervention might be distributed in the population (panel (a)), with the corresponding intervention term definitions for targeted fraction, p in , and intervention coverage, L (panel (b)); and how the primary process proceeds by finding an expected number of test-negatives, B, until finding a test-positive case, which initiates the secondary process leading to an expected number of additional tests, λ, of which R ′′ are expected to be test-positive in the absence of the study intervention (panel (c)), with the corresponding to summary categories of different routes to recruitment into the study (panel (d)).

S2.2 Population Heterogeneity
events (i.e., those that lead to primary or secondary recruitment) that occur, just that observation rates do 110 not differ by targeted status.

112
These real-world infection and testing processes are stochastic, and we consider the asymptotic expected 113 (i.e., average) outcomes of these processes. We define the following set of parameters corresponding to 114 expected counts of recruitment-related events per primary test-positive, and the probability of preventing 115 infection. 116 B + 1: the expected number of tests from the primary process required to find a single test-positive case; i.e., 117 on average, for B + 1 individuals tested via primary route, B are test-negative and 1 is test-positive. 118 λ: the expected number of tests from the secondary process, for each case identified by the primary process.

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R ′′ : the expected number of test-positives in the contacts of identified cases when there is no intervention. 120 E: the intervention efficacy; i.e., the probability that an individual who has received the intervention will 121 avoid infection when exposed (relative to an individual without the intervention) either via the primary = 1 − # intervention, test-positive # non-intervention, test-positive × # non-intervention, test-negative # intervention, test-negative In terms of the types of individuals defined at the end of Section S2.3, this equation becomes: which can be thought of as two odds of having received the intervention, each conditional on the two possible test outcomes. We will refer to these as the test-positive odds and the test-negative odds.

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To determine the potential bias ofÊ for a TND study in an outbreak setting, we need to translate Eq. S1 from 140 being in terms of total individual counts, into the expected totals, given the study target intervention and 141 outbreak conditions. We will examine each of the two odds terms in turn, then combine the results.

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Starting with the test-positive odds term, we first factorise (by C ′ + , or N ′ + ), such that most terms are expressed 144 as proportions: multiple sources. Thus, amongst targeted individuals (i.e. those in C), R ′′ will be reduced on average by the 152 probability that exposed individuals are intervention recipients and protected. This probability is equal to 153 coverage, L, multiplied by the true efficacy, E. Therefore, Using these substitutions and introducing some identity multipliers, 1 = C ′′ + C ′′ + , we can rewrite Eq. S2 as: Next, we show how the proportions between the counts of the targeted individuals can be substituted to probability that an exposure results in an infection is lower. Given an exposure event: these four ratios are: which means we can further substitute in Eq. S3: Like for determining the fraction of infections in targeted individuals that did or did not receive the inter-165 vention (Eq. S3.1), we can also use Bayes Theorem to find the relative fractions of infections that occurred 166 in individuals that were or were not targeted, and therefore, In conventional TND studies there is no secondary recruitment. If secondary recruitment were eliminated 170 under outbreak circumstances, that would imply that λ → 0, which also means that R ′′ → 0. During outbreaks, the secondary process would still occur as part of the response (i.e. there would both testing and 172 case-finding), but the people identified would not be recruited. Under that limit: which suggests a useful re-arrangement of the final form of the test-positive odds, so it has a clear separation of the terms which appear in the unbiased estimator (i.e. primary recruiting only) and the remaining 175 factors: In Eq. S10, we now have only terms that describe the intervention (targeted and coverage probabilities, p in 177 and L, and efficacy E) and epidemiology (R ′′ ).

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We assume that the testing criteria for the secondary process is not affected by the presence of the inter-180 vention. For example, a contact-tracing-related criteria might be principally about high-risk interactions 181 rather than particular symptoms, or the symptom threshold might be sufficiently relaxed that almost all 182 contacts meet it. Similarly, a purely geographical criteria would be unaffected by presence or absence of the 183 intervention. Thus, in our model all the prevented secondary infections (via true intervention efficacy E) 184 are still recruited by the secondary process as test-negatives. This is a bounding assumption; see the end of 185 this section for relaxing this assumption.

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Turning to the test-negative odds, we first replace the primary test-negatives by the contribution from B, 187 the average number of test-negatives per test-positive via the primary route. Given that definition, the total 188 number of primary test-negatives is T ′ − = BT ′ + . Because the intervention has no effect on the causes that lead 189 to testing negative via the primary route, the representation of individuals follows their proportions in the 190 population: As with the test-positives odds, we can factorise and introduce identity multiples to re-arrange into terms 192 that we can then use Bayes Theorem to replace with model parameters: We can use the targeted and non-targeted fractions of primary test-positives,

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Amongst non-targeted individuals, on average λ − R ′′ of recruits from the secondary route will be test- 196 negative. This means that 197 This definition also implies that the exposed proportion is p t = R ′′ λ because R ′′ individuals are infected per λ 198 secondary individuals. The complementary non-exposed proportion is therefore 1 − p t = λ−R ′′ λ . This value is 199 like a transmission probability, though that interpretation should be used with caution: the denominator is 200 determined by the secondary observation process, and thus the proportion may not clearly translate to the 201 biological process probability.

202
Also by definition, amongst targeted individuals, only 1 − LE of the exposed individuals are infected, therefore: We again use Bayes Theorem to translate these ratios into model parameter expressions.
Substituting these into the for the appropriate ratios, we obtain: As in Section S3.1, for the conventional TND assumptions, λ → 0 and R ′′ → 0. Again, it is not that 205 the secondary process ceases, but just that recruitment via that route is disallowed. Enforcing those con-206 straints: As with test-positives odds, we can refactor in terms of the conventional TND limit: In Eq. S16, we now have only terms that describe the intervention (p in , L, and E) and epidemiology 209 (R ′′ , λ, and B). Note that this term includes more of the model parameters than the test-positive odds 210 (Eq. S10).

212
Recruits 213 Earlier, we assumed that the secondary recruitment process was unperturbed by the study intervention. For 214 a secondary process that is, for example, purely geographical because it concerns a pathogen that is highly 215 asymptomatic (e.g., neighbor-household testing for dengue), this assumption is consistent. Where it becomes 216 less clearly acceptable as a simplification, is if there remains some disease-or symptom-based component to 217 secondary recruitment.

218
In the main text, we focus on a vaccine study for EVD, where the primary process was self-reporting 219 with multiple EVD-like symptoms leading to testing. The secondary process is nominally contact-tracing 220 combined with a fever. We assumed that subjective fever would almost always be present for the contacts 221 that avoided EVD infection because of the vaccine. In reality there would be some attack rate less than 222 100%.

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If we define the proportion of people meeting a symptom-based component of the secondary process as α 224 and ignore the zero-bias term (Eq. S15) as a coefficient, then Eq. S16 becomes: That is, of all the potential secondary recruits that could be added to test-negatives due to prevention of 226 infection, only some exhibit the additional criteria. Note that there is no impact of relaxing this assumption 227 on the test-positive odds.

228
If α → 1, i.e. everyone meets this extra criteria, we get Eq. S16. As α → 0, the denominator decreases, 229 increasing the test-negative odds overall, and in turn reducing the estimated effectiveness. When α = 0: In the case of p in = 1, this reduces to unity. More generally, This means that without any contribution from α, test-negative odds biases increasingly towards under-232 estimation as targeted fraction decreases. As α → 1, this effect is counteracted, but can in turn lead to 233 overestimation of effectiveness.

235
Combining the test-positives odds and test-negatives odds: This suggests a different factorization: We can define secondary test-positive fraction, p t = R ′′ λ , the negative proportion of primary alerts, f − = B B+1 , 238 and relative rate of secondary recruitment to primary recruitment, ρ = λ B+1 . Noting that This yields: We use this framing for all the main text results. This formulation highlights the important relative values 241 within the model, while still maintaining terms that can be reasoned about and potentially measured. In As the intervention tends toward either doing nothing (E → 0) or perfect protection (E → 1), the estimator 247 bias tends to vanish.
The final factorization in Eq. S25 shows that, in the limit of perfect alignment of targeting and recruitment, 250 the intervention coverage, L, is removed, and the bias depends only on the true efficacy, E, and a combination 251 of epidemiological parameters: R ′′ B+λ . This relationship can be inverted; which allows us to determine the 252 true efficacy in terms of the estimator value and other parameters: this factor only has B + λ, we do not need to distinguish primary versus secondary test-negatives. If a 262 test-negative from λ was mistakenly assigned to B (or vice versa), that would not change this factor.

263
Thus, if a study were able to achieve p in ≈ 1, it only need to be able to distinguish between primary and 264 secondary test-positives to correctly bound the estimator.

S4.3 Secondary Case Recruitment, p t , limits
If we consider secondary case limits, that is what proportion of secondary recruiting is test-positive, then we 267 obtain: One way to interpret p t → 1 is that transmission probability (conditional on high risk contact) is going up.

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Another way to think about it is λ coming down to meet R ′′ ; i.e., the decision about whether to test a 270 contact or not becoming more accurately linked to whether they were infected. As primary recruiting increasingly outweighs secondary recruiting (including both increasing primary re-273 cruitment and disallowing secondary recruitment), ρ → 0. In this limit: Thus, for sufficiently high rate of primary recruitment leading to test-negatives, the bias goes to 0.

276
Given that the bias in conventional design arises from aggregating the primary and secondary recruitment 277 routes, we might expect that treating the recruitment routes as separate could limit this bias. If we consider 278 the secondary recruitment population as a cohort study, then the conventional cohort design estimator 279 is: 280 estimated effectiveness = 1 − attack rate in individuals receiving study intervention attack rate in remaining individualŝ We make a simpler argument in the main text, but we can also use previously identified relationships to show this is unbiased. Recall Eq. S4 and additional definitions: Using a similar approach as that for the TND estimator, and re-using those ratios: Eq. S31 implies that if it were possible to observe secondary cases (out of secondary contacts) as a cohort, 284 there would be no bias in such a study, regardless of heterogeneity in vaccine uptake. Another advantage of 285 this study design is that there's no uncertainty about testing criteria (high risk contacts, regardless of symp-286 toms), unlike the test-negative design (where symptoms may play a role in secondary recruitment).

288
We can now consider combining the TND estimator and the cohort estimator: In this combination, the limiting condition for the TND of no secondary testing applies (all those individuals 290 go into the cohort term) and thus the TND estimator is unbiased (per Eq. S28). We have just shown that 291 the cohort study using only secondary recruitment is also unbiased (under our other assumptions). Thus, 292 any weighted average of the terms, like Eq. S32, is also unbiased. Therefore, selection of these weights can 293 optimize for other study features, such as power.  These plots show some trends under specific conditions. In general, increasing targeted fraction decreases 302 bias range, though not absolutely (e.g., ρ = 1 9, p t = 1 4, f − = 0.75). Increasing coverage can shift bias 303 towards underestimation or overestimation, depending p t . 304 Figure S2: General Bias Sensitivity, 1 of 9: These series of plots show general sensitivity of the TND estimator to all of the model parameters. For each plot, the rightmost column corresponds to very high (99%) targeted fraction, which indicates the minimal bias surface when the study manages to maximize targeted fraction. Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.5. Figure S3: General Bias Sensitivity. 2 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.75. Figure S4: General Bias Sensitivity. 3 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.9. Figure S5: General Bias Sensitivity. 4 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.5. Figure S6: General Bias Sensitivity. 5 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.75. Figure S7: General Bias Sensitivity. 6 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recruits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.9. Figure S8: General Bias Sensitivity. 7 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recruits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.5. Figure S9: General Bias Sensitivity. 8 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.75. Figure S10: General Bias Sensitivity.: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recruits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.9.

305
An alternative approach to controlling the bias is to restrict to primary recruitment only. If we assume 306 that the study excludes secondary recruitment perfectly for test-positives (e.g. because they are extensively 307 monitored) but incompletely excludes secondary recruitment for test-negatives (e.g. because data for them 308 is incomplete) then the full estimator equation: will lose the test-positive bias contribution, because it goes to 1 (note that for any non-zero p t , this term is 310 less than 1): So the overall bias becomes: where β ∈ (0, 1) is the exclusion failure probability; β = 0 is perfect exclusion of secondary test-negatives (in 313 which case the test-negative term also reduces to 1) while β = 1 implies that no secondary test-negatives are 314 excluded. Note that this factor is simply reducing ρ in the test-negative odds term. Thus, we can drop β 315 and instead reduce the range we consider for ρ. The error expression for this scenario is: For an unbiased estimate, the first term in the square brackets would need to be 1, which would imply: There is no further reduction to the final line of Eq. S36, thus this term is only equal to 1 for specific 318 combinations of {L, E, p in , p t }. Nor is there a strict direction of inequality. For example, at L ≈ 0, the left 319 hand side is less than or equal to the right, while at L ≈ 1 the inequality can be either direction depending on 320 the value of p t . The directions of this inequality determine whether the residual term in Eq. S36 is greater 321 than 1 (i.e., the left hand side is greater than the right) or less than 1 (vice versa).

322
Defining this residual term as Y for the moment, and term corresponding to the test-positives as X (which 323 recall is X ≤ 1), we can consider the magnitude of the error excluding only the secondary test-positives versus 324 keeping all the secondary recruiting by: For Y ≤ 1, we know XY ≤ Y ≤ 1 and thus XY − 1 ≤ Y − 1 ≤ 0. This implies reduced (or at least the same) 326 error magnitude whenever Y ≤ 1 holds, i.e. the left hand side of Eq. S36 is less than or equal to the right.

327
Decreasing E always increases the right hand side without effecting the left, making the constraint harder 328 to satisfy and the least true efficacy we considered was E = 0. Increasing p t always decreases the left hand 329 side while increasing the right, so the smallest p t is also the most restrictive condition to meet this criterion.

330
In the main text, the smallest value we considered was p t ≈ 0.07. Under these circumstances: This only true for low L and high p in combinations, outside what we considered in the main text.

332
For Y > 1, some reduction in XY due the X ≤ 1 term reduces bias magnitude, namely if but too much will overshoot and lead to increased bias magnitude (though in the other direction). Of course, X and Y share terms, so Because p in remains in the equation, in multiple places, the targeted fraction plays an important role in bias.

336
If targeted fraction is high, and for the case of p in → 1, then we can then recover:  Figure S11: Bias Sensitivity Without Secondary Test-Positives, 1 of 9: These series of plots show sensitivity of the TND estimator which excludes secondary test-positives to all of the model parameters.
For each plot, the rightmost column corresponds to very high (99%) targeted fraction, which indicates the minimal bias surface when the study manages to maximize targeted fraction. Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.5. Figure S12: Bias Sensitivity Without Secondary Test-Positives. 2 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.75. Figure S13: Bias Sensitivity Without Secondary Test-Positives. 3 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 9 and f − = 0.9. Figure S14: Bias Sensitivity Without Secondary Test-Positives. 4 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.5. Figure S15: Bias Sensitivity Without Secondary Test-Positives. 5 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.75. Figure S16: Bias Sensitivity Without Secondary Test-Positives. 6 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 3 and f − = 0.9. Figure S17: Bias Sensitivity Without Secondary Test-Positives. 7 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.5. Figure S18: Bias Sensitivity Without Secondary Test-Positives. 8 of 9: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.75. Figure S19: Bias Sensitivity Without Secondary Test-Positives.: Recall, ρ = λ B+1 is the expected ratio of secondary to primary recuits; p t = R ′′ λ is the expected fraction of secondary recruits that test positive when no intervention is present; and f − = B B+1 is the expect fraction of primary recruits that are test-negative. In this panel, ρ = 1 and f − = 0.9.
In the model, we make no assumptions of how non-intervention occurs in the targeted population, just that 361 it occurs randomly within that group. Thus the ineligible count represents the minimum non-intervention 362 amongst the targeted population (the upper limit of L); there may be other sources (e.g., targeted individuals 363 are unavailable on the day offered). Potentially, when distributing the intervention, targeted individuals could 364 be asked about members of their household, neighbors, etc. that wanted to get the intervention, but were 365 unable to do so, but this number would also have many uncertainties (e.g. duplicate reporting, reporting 366 individuals that do receive the intervention at a different time or place).

367
If the study intervention has multiple steps (e.g. a two-dose vaccine, repeat application of vector-control 368 insecticides), then the decrease in coverage between steps could be informative about the targeted fraction, 369 p in . If we assume not receiving the intervention is due to a mix of short-term (e.g. ill that day) and long-term 370 (e.g. too young to be eligible) effects, then we can potentially further constrain L and p in . In the following 371 we assume that: i) long-term ineligibles only present themselves at the first step (though they may also 372 not), ii) short-term ineligibles present at the same rate in the subsequent steps, and iii) individuals that 373 did not present at earlier steps will also not present later. If we apply these assumptions to a two-step 374 intervention, and we call unobserved long-term ineligibles I 0 , the long-term ineligibles that appear initially 375 are I 1 , and the intervention recipients (V ) and short-term ineligibles that present (U * ) or not (U ) at each 376 stage (V 1 , V 2 , U * 1 , U * 2 , U 1 , U 2 ), then the following relations hold.

377
We have six observed pieces of information: the total population (T ), the number given the intervention 378 versus short term ineligible at both steps (V 1 , V 2 , U * 1 , U * 2 ), and the number of long-term ineligibles at the 379 first step (I 1 ). 380 We know that at the second intervention step, we have only people that got vaccinated in the previous step, 381 no new long term ineligibles, and the breakdown of short term ineligibles versus those that receive the second 382 step. So: Finally, the pieces must add up to the total population, and therefore: 388 C = V 1 + U * 1 + I 1 + U 1 + I 0 So using these assumptions, we can estimate the coverage and the targeted fraction: Both of these equations consist only of the measured values. Since the model is an approximation, there 390 may be other effects, but these relations can provide a useful guide to the value of the study parameters that 391 contribute to bias.

393
In the main text, we described applying this model to evaluating a novel vaccine during an Ebola outbreak, 394 but noted in the discussion that the approach could be generically applicable. The previous sections outline 395 the model in generic terms. Here we provide an example translation of that generalisation to another case: 396 a vector control intervention for dengue.

397
In this scenario, we consider an intervention like indoor residual spraying, applied to urban households on 398 a block basis (i.e. set of contiguous households, determined by street intersections) ahead of the dengue 399 season. Some blocks would get no coverage (i.e. be amongst the non-targeted population), while others 400 would receive coverage at some level (with non-coverage corresponding to e.g. availability to let treatment 401 teams into house on that day or presence of children under some age).

402
Later, during the dengue season, people in the study population would seek healthcare with symptoms that 403 would lead to testing for dengue, corresponding to the primary process. However, because dengue is fre-404 quently asymptomatic, the secondary process would be to test individuals in the primary cases household and 405 adjacent households. Instead of a contacts-based secondary route, there is geospatial secondary route.

406
Whether a TND study would be ideal for this scenario is certainly a topic for debate. However, it is possible 407 to frame this scenario and other potential pathogen spread and surveillance processes in the same terms we 408 have introduced in this analysis.