ANALYSIS: Wolff Did Not Rule Out Viral Interference and Has Several Notable Problems

The paper asked the right question, changed the denominator, removed the temporal biology, and then treated a statistically nonsignificant pooled estimate as proof that the problem did not exist.

Greg Wolff’s 2020 paper, Influenza Vaccination and Respiratory Virus Interference Among Department of Defense Personnel During the 2017-2018 Influenza Season, began with a legitimate scientific concern.

The test-negative design used in influenza vaccine-effectiveness studies assumes that influenza vaccination does not alter the probability of acquiring another respiratory infection. If vaccination changes susceptibility to non-influenza respiratory viruses, then people infected with those viruses no longer form a neutral control group. Vaccine-effectiveness estimates can shift simply because the composition of the control group changed.

Wolff recognized that vulnerability.

He did not resolve it.

The paper concluded that influenza vaccination was “not associated with virus interference” in the study population. That conclusion exceeds what the study measured. Wolff did not compare respiratory-virus incidence in vaccinated and unvaccinated populations. He compared laboratory-result categories among people already selected for respiratory illness, specimen collection, and testing. He removed participants with repeated specimens, removed influenza-non-influenza coinfections, excluded illnesses occurring before an eventual vaccination, classified illnesses occurring within fourteen days after vaccination as unvaccinated, pooled biologically distinct viruses, and selected confounders according to statistical significance.

The published tables then fail basic internal reconciliation.

Wolff’s data do not prove that influenza vaccination causes viral interference. They also do not rule it out. The correct conclusion is that this study cannot answer the question it claimed to answer. [1]

A Study of Tested Patients Is Not a Study of Infection Risk

Wolff began with 11,943 respiratory specimens. He excluded 2,474 specimens - 20.7% of the original set - and retained 9,469 unique participants. Every retained participant had already entered the healthcare and surveillance system and submitted a respiratory specimen.

That selected population does not provide the denominator required to estimate the risk of acquiring a respiratory infection.

The study contains no vaccinated population under observation, no unvaccinated population under observation, no person-time, and no count of respiratory illnesses occurring outside the specimen-submission system. It cannot tell us how often vaccinated people acquired non-influenza infections relative to unvaccinated people. It can tell us only how vaccination status was distributed among different test-result categories within a selected group of patients.

The primary analysis asks:

Among people who became ill, sought care, were sampled, survived the exclusion criteria, and received a classifiable laboratory result, were vaccinated participants more likely to fall into the non-influenza-positive category than into the pan-negative category?

That is not the same question as:

Did influenza vaccination alter the incidence of non-influenza respiratory infection?

Vaccination status, infecting pathogen, symptom severity, healthcare-seeking behavior, specimen timing, clinician sampling decisions, and assay detection can each affect whether a person enters the study. Conditioning on that pathway can create, suppress, or reverse associations. Test-negative designs can reduce certain forms of healthcare-seeking bias only when their restrictive assumptions hold. They do not magically make symptomatic tested patients representative of the source population. Methodological work on the test-negative design has repeatedly identified susceptibility to selection bias, residual confounding, outcome-dependent care-seeking, and violations of the assumption that vaccination leaves test-negative illnesses unaffected. [2]

Wolff nevertheless used the language of “risk,” “protection,” and “virus interference” as though the odds of occupying one laboratory category among tested patients represented the incidence of disease.

It does not.

The Denominator Changes the Verdict

The paper’s most revealing problem appears when the same data are analyzed using different comparison groups.

In Table 3, Wolff compared participants with a non-influenza respiratory virus against pan-negative participants. The crude odds ratio was calculated from these cells:

(2050 / 2441) / (830 / 799) = 0.81

That comparison suggested lower crude odds of a non-influenza virus among vaccinated participants.

In Table 5, Wolff reported an odds ratio of 1.15 for “Non-Influenza Virus.” That estimate came from comparing non-influenza-positive participants against everyone who was not classified as non-influenza-positive, including influenza cases:

(2050 / (6541 - 2050)) / (830 / (2928 - 830)) = 1.15

The same dataset therefore produced a crude odds ratio of 0.81 when pan-negative patients served as controls and 1.15 when influenza cases and pan-negative patients were combined into the implicit control group.

One analysis pointed below one. The other pointed above one.

The biology did not change.

The denominator changed.

That problem becomes decisive in Table 5’s pathogen-specific results. The reported coronavirus odds ratio of 1.36 and human metapneumovirus odds ratio of 1.51 did not compare those infections against a stable pan-negative control group. Each pathogen was compared against all other outcomes combined. That comparator included influenza - an outcome explicitly expected to be less common among vaccinated people.

Once vaccination changes the size of the influenza category, it changes the composition of the “not coronavirus” and “not metapneumovirus” categories. A positive pathogen-specific odds ratio can therefore emerge without any increase in the population incidence of that pathogen.

A simple reconstruction using Wolff’s own counts demonstrates the instability. If coronavirus-positive participants are compared only with pan-negative participants, the crude odds ratio becomes:

(507 / 2441) / (170 / 799) = 0.98

For human metapneumovirus, the corresponding crude comparison becomes:

(335 / 2441) / (101 / 799) = 1.09

These recalculations do not produce valid causal estimates; they remain unadjusted and subject to the study’s other biases. They demonstrate something more basic: the headline pathogen-specific findings depend heavily on which patients Wolff placed in the denominator.

Table 5’s “significant” coronavirus and metapneumovirus results cannot establish vaccine-associated interference. The pooled null cannot disprove it. Both depend on compositional comparisons inside a selected tested population.

The paper generated competing narratives from the same observations and did not confront the reason.

Influenza Cases Cannot Serve as Invisible Controls

Table 5’s one-versus-everything-else construction causes another distortion.

Vaccinated participants had fewer influenza-positive results than unvaccinated participants: 31.3% versus 44.4%. Influenza cases therefore occupied a much larger share of the unvaccinated “not coronavirus,” “not metapneumovirus,” and “not non-influenza virus” denominators.

That imbalance can make non-influenza categories appear proportionally more common among vaccinated participants even when their absolute incidence has not increased.

This is a closed compositional system. Every participant must occupy one of three broad categories: influenza, non-influenza virus, or no detected pathogen. Reducing the proportion in one category necessarily increases the relative share available to the others.

That arithmetic does not tell us whether vaccination caused more coronavirus infections, more metapneumovirus infections, fewer influenza infections, altered symptom severity, altered testing, or merely changed which diagnostic category a tested patient entered.

A valid pathogen-specific analysis required a consistent control definition, preferably pan-negative controls or an explicitly specified multinomial model, followed by adequate adjustment for age, calendar week, site, beneficiary category, prior vaccination, healthcare use, and other prespecified confounders. Wolff instead used crude one-versus-rest odds ratios and interpreted their direction biologically.

The paper’s central estimates are not merely imprecise. They answer different questions.

The Study Removed the Temporal Biology

Virus interference is a temporal phenomenon.

The hypothesis concerns whether one exposure - natural infection or vaccination - changes susceptibility to a subsequent infection over a defined interval. A proper test therefore requires exposure dates, infection sequences, time at risk, recurrent events, and biologically justified windows.

Wolff removed individuals who submitted multiple specimens during the season because they “could have had multiple different viruses.”

That is precisely why those individuals mattered.

A participant with influenza followed by another respiratory infection, or one non-influenza infection followed by another, carries information about sequence, interval, recurrence, and possible transient immunity. Instead of modeling those repeated events, the study excluded the people most capable of informing the proposed mechanism.

The paper also excluded influenza-non-influenza coinfections because they could not be assigned uniquely to one category. That decision simplified the bins while deleting another biologically informative outcome.

The result was not a study of interference over time. It was a study of mutually exclusive labels attached to one retained specimen per person.

A cross-sectional laboratory category cannot establish whether vaccination changed later susceptibility, whether a prior infection temporarily altered risk, whether two pathogens competed, or whether vaccination changed symptom expression or care-seeking.

Wolff invoked a dynamic biological mechanism and then stripped time and sequence from the analysis.

Future Vaccination Was Used to Remove Earlier Illness

The exposure rules introduced a second temporal defect.

Wolff excluded subjects who became ill before receiving an influenza vaccination. Those participants were unvaccinated when their illnesses occurred. Their subsequent vaccination did not retroactively change their exposure status at the time of illness.

A time-valid analysis would count their pre-vaccination observation period as unvaccinated person-time. Wolff instead used a future event - later vaccination - to remove an earlier illness.

That exclusion preferentially eliminates illnesses occurring in people who would later become vaccine recipients. It can make the vaccinated trajectory look healthier by deleting events that occurred before vaccination while retaining illnesses among people who never became vaccinated.

The paper also classified people vaccinated fewer than fourteen days before specimen submission as unvaccinated. That convention often appears in influenza vaccine-effectiveness studies because adaptive protection may require time to develop. It does not automatically belong in a study of off-target respiratory effects.

If a nonspecific effect occurs during the first thirteen days after vaccination, Wolff’s rule assigns those illnesses to the unvaccinated group. The study did not justify why a fourteen-day latency appropriate to influenza-specific effectiveness should define the exposure window for every proposed mechanism of viral interference.

The combined rules create a peculiar exposure structure:

Illness before an eventual vaccination was excluded.

Illness shortly after vaccination was classified as unvaccinated.

Only illness at least fourteen days after vaccination counted as vaccinated.

That structure may be convenient for conventional vaccine-effectiveness analysis. It is not a neutral test of all plausible post-vaccination effects.

The Two Exposure Groups Were Different Populations

The vaccinated and unvaccinated participants differed profoundly before any statistical model was applied.

Children constituted 50.2% of the unvaccinated group but only 24.4% of the vaccinated group. Active-duty members constituted 55.3% of the vaccinated group, according to the reported percentage, but only 8.4% of the unvaccinated group. Children constituted 42.9% of non-influenza-virus-positive participants but only 21.1% of pan-negative participants.

These are not minor imbalances.

Age strongly determines exposure patterns, pathogen prevalence, symptom profiles, specimen submission, and probability of detecting RSV, metapneumovirus, rhinovirus, coronavirus, and other respiratory agents. Beneficiary category also separates active-duty adults, children, spouses, retirees, and other dependents with different living conditions, occupations, access patterns, and vaccination rules. [1]

Wolff adjusted the primary pooled interference analysis only for three broad age groups: 0-17, 18-35, and 36 years or older.

An infant, a six-year-old, and a seventeen-year-old were treated as members of one adjustment stratum. That cannot adequately control the age structure of pediatric respiratory infections.

The paper considered beneficiary category but discarded it because it did not remain statistically significant in the final model. That decision is methodologically unsound. Confounding does not cease because a covariate’s coefficient fails to cross a p-value threshold.

A variable belongs in a causal adjustment set because it lies on a plausible confounding pathway - not because software declares it independently “significant.”

P-Values Chose the Confounders

The paper describes a model-building procedure in which variables were screened at p < 0.20, entered into a fuller model, and retained only if they remained statistically significant.

That is not principled confounder control.

Significance-driven selection can remove important confounders, retain variables that do not belong in the causal model, destabilize coefficients, distort standard errors, and make results sensitive to the particular sample. It is especially damaging here because vaccination status, beneficiary category, age, sex, and calendar period were visibly imbalanced.

The primary model omitted beneficiary category, sex, site, military installation, healthcare-utilization behavior, comorbidity, pregnancy, immune status, occupation, deployment, prior-season vaccination, repeated annual vaccination, vaccine formulation, exact vaccination date, and interval between symptom onset and specimen collection.

Calendar time was reduced to winter, spring, summer, and fall. Respiratory viruses do not circulate in three-month blocks. Influenza, RSV, metapneumovirus, rhinovirus, parainfluenza, and seasonal coronaviruses rise and fall on different weekly trajectories. Vaccine uptake also changes over the season. A quarterly category cannot control that temporal structure.

A more careful virus-interference analysis published by Feng and colleagues matched or adjusted analyses by calendar week and stratified by age and season phase. Wolff cited that literature but used a much coarser structure. [3]

The paper also states that it used “conditional logistic regression,” yet it identifies no matching sets or conditioning strata. The reader cannot reconstruct what was conditioned upon.

The model is therefore undercontrolled, involved “data peeking” to identify de novo confounders, and underreported.

The Active-Duty Comparison Violates Exchangeability

Influenza vaccination was mandatory for active-duty personnel.

That fact did not strengthen the comparison. It damaged it.

When nearly everyone in a defined group receives the exposure, the few people who remain unvaccinated become highly selected. They may include people with medical exemptions, contraindications, incomplete records, recent accession, delayed compliance, or other circumstances connected to health status or healthcare use.

The active-duty vaccinated and unvaccinated groups therefore cannot be assumed exchangeable.

Wolff acknowledged that mandatory vaccination had made previous active-duty vaccine-effectiveness analyses difficult to interpret. He then argued that the active-duty subgroup did not show statistically significant interference and therefore did not appear to be skewing the full result.

That inference fails twice.

First, non-significance in a small, selected unvaccinated subgroup does not establish comparability.

Second, the active-duty sensitivity-analysis table does not contain the control group it claims to contain.

The Tables Do Not Add Up

The defects in Tables 2 and 3 require correction before this paper can be treated as reliable evidence.

Table 2 reports 2,516 vaccinated active-duty participants, described as 55.3% of 6,541 vaccinated participants.

That is arithmetically impossible.

The six vaccinated beneficiary-category counts printed in Table 2 sum to only 5,441, leaving 1,100 participants unaccounted for. Replacing 2,516 with 3,616 makes the category counts sum to 6,541 and makes the reported percentage correct:

3616 / 6541 = 55.3%

Table 3 independently confirms that correction. Its vaccinated active-duty cells total:

1046 + 2570 = 3616

The active-duty subgroup therefore contained 3,616 vaccinated and 247 unvaccinated participants, for a total of 3,863.

The more serious problem appears in Table 3’s purported “Pan-Negative Respiratory Virus” column.

The active-duty non-influenza-virus cells total:

1046 + 73 = 1119

That matches Table 1’s count of 1,119 active-duty participants with a non-influenza respiratory virus.

The purported active-duty pan-negative cells total:

2570 + 174 = 2744

But Table 1 reports only 1,625 pan-negative active-duty participants.

The excess is:

2744 - 1625 = 1119

That number exactly equals the inferred count of active-duty influenza cases:

3863 - 1119 - 1625 = 1119

Under the paper’s own totals, the Table 3 “pan-negative” column appears to contain both true pan-negative participants and influenza-positive participants.

Either influenza cases were included in a column labeled pan-negative, or one or more of the published tables is wrong.

Neither possibility permits the active-duty sensitivity analysis to stand as reported.

The AFCITA-record subgroup shows the same warning. Its four Table 3 cells sum to 4,549 - the exact number the paper identifies as the entire AFCITA-record population. If the analysis genuinely compared non-influenza-virus-positive participants only with pan-negative participants, influenza-positive AFCITA participants should not have been included, and the cells should not sum to the entire subgroup.

The printed table strongly suggests that the sensitivity analyses compared non-influenza-positive participants with all other outcomes, not with pan-negative controls.

That would make the sensitivity analyses different from the primary analysis while presenting them as replications of it.

Smaller inconsistencies appear elsewhere. The results text gives the “no pathogen detected” odds ratio as 1.51, while Table 5 reports 1.59. The AFCITA adjusted p-value appears as 0.24 in the prose and 0.25 in Table 3.

A one-digit typographical error does not destroy a study. A mislabeled comparator group does.

The authors and journal should publish a corrigendum identifying the correct Table 2 count, defining the actual Table 3 controls, and reproducing the analysis from released code and corrected contingency tables.

“No Pathogen Detected” Does Not Mean Healthy

Every pan-negative participant was symptomatic or clinically concerning enough to have a respiratory specimen submitted.

“No pathogen detected” means that the assays used did not detect one of their targets. It does not mean that the patient had no illness, experienced a better outcome, or received protection from influenza vaccination.

Wolff reported that vaccinated participants had higher odds of falling into the pan-negative category: Table 5 gives an odds ratio of 1.59. The discussion and conclusion treated this finding as favorable evidence.

It is not inherently favorable.

A pan-negative result can reflect an organism outside the panel, a noninfectious respiratory syndrome, specimen timing, specimen quality, viral load below the detection threshold, or another cause not resolved by the available assays. The paper did not determine which.

The higher pan-negative proportion could also arise mechanically because vaccinated participants occupied the influenza category less often.

The study transformed an unresolved illness category into rhetorical support for the vaccine.

A Nonsignificant P-Value Is Not a Safety Boundary

The principal adjusted estimate was 0.97, with a 95% confidence interval of 0.86 to 1.09 and p = 0.60.

That result indicates that the selected data did not reject a sharp null in the specified pooled model. It does not establish equivalence, prove absence of interference, or validate the test-negative design.

Wolff specified no equivalence margin and performed no equivalence test.

The verified-record analysis produced an adjusted point estimate of 1.23, with a 95% confidence interval of 0.86 to 1.76. The active-duty analysis produced an adjusted estimate of 1.20, with a confidence interval of 0.89 to 1.61.

Even setting aside the Table 3 control-group problem, those intervals remain compatible with substantial increases in the measured odds. The analyses were simply too imprecise to distinguish those possibilities.

The paper repeatedly moves from “not statistically significant” to “does not appear to be skewing study results.” That move is invalid.

A p-value above 0.05 does not certify the null. It reports that the study, model, and available sample did not produce enough evidence to reject it.

Pooling Viruses Can Manufacture a Null

Wolff combined adenovirus, coronavirus, human bocavirus, metapneumovirus, parainfluenza, RSV, rhinovirus/enterovirus, and non-influenza coinfections into one pooled endpoint.

Those pathogens differ in age distribution, seasonality, transmission setting, symptom profile, duration of detection, and relationship to healthcare seeking.

The reported estimates also pointed in opposite directions.

Coronavirus and human metapneumovirus appeared elevated under Table 5’s crude one-versus-rest analysis. Parainfluenza, RSV, and non-influenza coinfections appeared reduced. Rhinovirus/enterovirus appeared near one.

Combining positive and negative associations can yield an aggregate odds ratio near one through cancellation. A pooled null does not prove that every component is null.

The pathogen-specific analysis did not solve the problem because its odds ratios were crude, its comparator changed with every outcome, and the paper conducted numerous tests without a prespecified hierarchy or multiplicity control.

Wolff described lower odds of parainfluenza and RSV as “protection” associated with influenza vaccination.

That interpretation should have triggered skepticism, not confidence.

An influenza vaccine does not target RSV or parainfluenza. Apparent protection against unrelated viruses in an observational analysis can signal residual confounding, selection bias, comparator distortion, or differential detection. Such findings function as negative-control alarms. They do not “rebut” viral interference.

The paper interpreted positive off-target associations as possible interference and negative off-target associations as protection. It failed to apply the same causal standard in both directions.

Similar Vaccine-Effectiveness Estimates Do Not Validate the Design

Wolff compared influenza cases with three control groups: all influenza-negative participants, non-influenza-virus-positive controls, and pan-negative controls. The adjusted odds ratios ranged from 0.46 to 0.51.

The paper called the five-percentage-point spread “minute” and concluded that the similarity did not support virus interference.

That analysis does not validate the design.

The three comparisons reused the same influenza cases and used overlapping control groups. Their estimates were correlated. The paper reported overlapping confidence intervals but no formal contrast, equivalence test, or prespecified threshold for a meaningful difference.

More importantly, all three control groups came through the same symptomatic-testing and specimen-selection system. Shared selection bias can produce similar estimates across several control definitions.

Three similarly biased comparisons do not become unbiased through agreement.

The test-negative design itself requires the assumption under investigation: that vaccination does not affect susceptibility to the conditions producing test-negative controls. Jackson and Nelson described that assumption explicitly, and later methodological analyses showed that the test-negative odds ratio can remain biased when vaccination decisions correlate with susceptibility or exposure, when healthcare seeking differs, or when the vaccine’s biological action does not fit restrictive model assumptions. [4,5]

Wolff did not validate the assumption. He recycled it through three related denominators.

The Study Never Measured the Proposed Mechanism

The biological account presented in the paper suggests that natural influenza infection may produce temporary nonspecific immunity against another respiratory virus, while vaccinated people who avoid influenza might not receive that temporary effect.

Testing that proposition requires more than knowing vaccination status and the result of one retained specimen.

A valid mechanistic analysis would need to know whether a participant experienced influenza, when it occurred, what infection followed, the interval between infections, whether the first infection altered symptoms or testing for the second, and how vaccination modified those pathways.

Wolff measured none of that.

The study collected no sequential infection model, no serial immune measurements, no interferon response, no infection-order analysis, no recurrent-event analysis, and no time-dependent susceptibility estimate.

It therefore cannot distinguish vaccine-mediated interference from natural-infection-mediated interference, pathogen competition, altered symptom severity, altered care seeking, compositional effects, or residual confounding.

It attached the term “virus interference” to a cross-sectional odds ratio without measuring interference.

What Wolff Can Legitimately Say

The defensible conclusion is narrow:

Among selected symptomatic Department of Defense beneficiaries who submitted a respiratory specimen during the 2017-2018 season and survived the study’s exclusion rules, an age-adjusted comparison of pooled non-influenza-virus-positive results with pan-negative results produced an odds ratio of 0.97. Pathogen-specific crude associations varied according to the organism and comparator. Verified-record and active-duty subgroup analyses were imprecise and, as published, contain unreconciled control-group counts.

That is the result.

The paper cannot establish that influenza vaccination does not increase the incidence of another respiratory infection.

It cannot establish that the test-negative design remains unbiased when vaccination changes the respiratory-disease ecology.

It cannot establish protection against RSV or parainfluenza.

It cannot use its coronavirus result to make claims about SARS-CoV-2; the specimens came from the 2017-2018 season, before SARS-CoV-2 existed in the study population.

It cannot claim to have excluded clinically important interference during the first fourteen days after vaccination because those illnesses were assigned to the unvaccinated category.

It cannot claim to have studied recurrent or sequential infections because it excluded people with multiple specimens.

Most importantly, it cannot support the categorical abstract conclusion that receipt of influenza vaccination “was not associated with virus interference.”

What a Valid Study Would Require

A credible investigation would begin with a defined source population and measure person-time under a time-varying exposure model. Illnesses occurring before vaccination would count as unvaccinated outcomes. Outcomes after vaccination would be analyzed in prespecified windows rather than automatically discarded or reassigned for fourteen days.

The study would retain repeated infections and coinfections. Recurrent-event and multistate models would preserve the sequence between influenza, non-influenza respiratory infection, recovery, and subsequent infection.

It would use verified vaccination dates, formulations, prior-season vaccination, multi-year vaccination histories, and exact intervals between vaccination, symptom onset, and specimen collection.

Enrollment criteria, specimen timing, assay platforms, and testing indications would be standardized across sites. Analyses would control calendar time at the week level, not by season of the year. Age would be modeled finely, especially in children. Beneficiary category, site, healthcare utilization, comorbidity, immune status, pregnancy, occupation, and prior respiratory history would enter a prespecified causal model rather than compete for admission through p-values.

Pathogen-specific hypotheses would be prespecified. A consistent comparator or multinomial framework would prevent the control denominator from changing invisibly across outcomes. Multiplicity would be addressed. Absolute incidence, severity, hospitalization, recurrent illness, and all-cause respiratory burden would accompany pathogen-specific detection.

The authors would publish the protocol, analytic code, exclusion accounting, and corrected contingency tables.

That study could test viral interference.

Wolff’s did not.

The Correct Conclusion Is Uncertainty

Wolff deserves credit for identifying a real vulnerability in influenza vaccine-effectiveness research. The test-negative design depends on the proposition that vaccination does not alter the risk of the illnesses used to construct its control group.

But recognizing an assumption does not validate it.

The study selected on illness and testing. It lacked a population denominator. It altered exposure status using future vaccination. It made the first fourteen post-vaccination days invisible to the vaccinated analysis. It discarded recurrent infections. It discarded influenza coinfections. It pooled biologically different viruses. It chose confounders by p-value. It used crude pathogen-specific comparisons with unstable denominators. It interpreted symptomatic pan-negative patients as a favorable category. It treated nonsignificance as evidence of no effect. Its tables do not reconcile.

Wolff did not demonstrate that influenza vaccination causes viral interference.

He did not demonstrate that it does not.

The paper demonstrated how easily a selected denominator, a pooled endpoint, and a p-value can be mistaken for an answer.

Before this study is cited again as proof against viral interference, Vaccine should require corrected tables, a clear definition of every comparator, release of the analytic code, and a complete reanalysis.

The scientific answer remains what the paper worked too hard to avoid:

We do not know.

Sources

1. Wolff GG. Influenza vaccination and respiratory virus interference among Department of Defense personnel during the 2017-2018 influenza season. Vaccine. 2020;38(2):350-354. DOI: 10.1016/j.vaccine.2019.10.005. PMID: 31607599. PMCID: PMC7126676. Publisher / DOI

2. Sullivan SG, Tchetgen Tchetgen EJ, Cowling BJ. Theoretical basis of the test-negative study design for assessment of influenza vaccine effectiveness. American Journal of Epidemiology. 2016;184(5):345-353. DOI: 10.1093/aje/kww064. PMID: 27587721. PMCID: PMC5013887. Publisher / DOI

3. Feng S, Fowlkes AL, Steffens A, Finelli L, Cowling BJ. Assessment of virus interference in a test-negative study of influenza vaccine effectiveness. Epidemiology. 2017;28(4):514-524. DOI: 10.1097/EDE.0000000000000670. PMID: 28362642. PMCID: PMC5535302. Publisher / DOI

4. Jackson ML, Nelson JC. The test-negative design for estimating influenza vaccine effectiveness. Vaccine. 2013;31(17):2165-2168. DOI: 10.1016/j.vaccine.2013.02.053. PMID: 23499601. Publisher / DOI

5. Lewnard JA, Tedijanto C, Cowling BJ, Lipsitch M. Measurement of vaccine direct effects under the test-negative design. American Journal of Epidemiology. 2018;187(12):2686-2697. DOI: 10.1093/aje/kwy163. PMID: 30099505. PMCID: PMC6269249. Publisher / DOI

Editorial note: All numerical reconstructions in this critique use the counts printed in Wolff’s Tables 1-5. The paper’s Table 2 active-duty count and Table 3 subgroup labels require formal correction or clarification by the author and journal.