Risk for Reinfection After SARS-CoV-2: A Living, Rapid Review for American College of Physicians Practice Points on the Role of the Antibody Response in Conferring Immunity Following SARS-CoV-2 InfectionFREE

This update focuses on 2 of the key questions addressed in our living review (as modified to reflect the inclusion decision described in the previous paragraph). This review used rapid methods, primarily in the screening stages of the review. Details of the plan for updating each question and a summary of our methods are described in our protocol (3). A final update of all key questions in this review will be produced in early 2022. The PROSPERO record for our original review is CRD42020207098.

For this update, our search strategies focused on identifying longitudinal controlled studies of risk for reinfection published before 22 September 2021. We searched Ovid MEDLINE ALL, the World Health Organization global literature database, ClinicalTrials.gov, COVID19reviews.org, and reference lists of reviews (Supplement Item 1).

We included longitudinal studies that compared the risk for reinfection for individuals who had a documented infection with SARS-CoV-2 (the “positive” cohort) with the risk for new infection in those with no prior infection (the “negative” cohort) (4). Studies in the general population, health care workers, college students, and long-term care facilities were eligible, as were registry-based studies of patients with a specific condition. Studies without an uninfected comparison cohort were ineligible.

We used the Joanna Briggs Institute cohort study checklist (5) to screen for methodological limitations that would almost certainly invalidate the study findings (Supplement Table 1). Using this tool, we excluded 2 studies (6, 7) that used invalid criteria to allocate participants to the positive and negative cohorts or did not follow participants for an adequate length of time for potential reinfection.

We extracted the following information by study: study design, population, data sources, study inclusion and exclusion criteria, age, race, gender, comorbid conditions, immunoassay type and brand (when applicable), definition of reinfection, follow-up test type and frequency of follow-up testing, primary infection symptom status, waiting period (if applicable), counts for all infection events and nonevents, and main findings.

For included studies, we identified potential biases in the following 4 areas: sampling, cohort assignment, case definition, and ascertainment of cases during follow-up. We abstracted information relevant to these methodological features from each study, recording variations in methods that could affect the observed effect. Considerations include the following.

Sampling. We assessed whether selection bias could arise from the data sources used to identify eligible persons. Selection bias could spuriously influence effect size if some groups were less likely to be recruited, if the cohorts were differentially enriched with persons who had unusual risk profiles, or if cohort inception was poorly delineated.

Cohort assignment. Within a given sample, the “positive” (infected) and “negative” (not infected) cohorts form the denominators for follow-up and analyses. To assess misclassification, we considered which tests were used (serologic, virologic, and clinical assessment), when they were done in relation to illness onset, and whether they were applied to all participants.

Outcome ascertainment. We assessed the methods used to ascertain new infections during follow-up, such as scheduled surveillance with PCR tests, clinical surveillance, or identification of cases in clinical care. In assessing ascertainment, we also considered whether surveillance for symptoms or access to medical evaluation differed among cohorts and (if applicable) adherence to scheduled testing. Bias could also occur if the follow-up period was too short.

Classification of potential cases of reinfection during the follow-up period. In most studies, reinfection was diagnosed when an individual had a positive result on a PCR test after a “waiting period” intended to give time for the initial episode to resolve clinically and virologically. Bias can occur if a positive PCR result due to persistent viral shedding is counted as a reinfection or if adjudication of reinfections is not equally rigorous in the positive and negative cohorts.

In each of these 4 categories, we identified methodological variations that are likely to be associated with higher or lower quality (risk of bias). In some cases, we did sensitivity analyses to assess how the overall protection estimate would change because of study-level factors. Such factors include study duration, the waiting period between cohort inception and the first reinfection assessment (8), median participant age, underlying prevalence (proxied by the proportion of new infections in the negative cohort), whether criteria for diagnosis of the initial infection would select only symptomatic infections, and whether serology, PCR, or both were used for cohort allocation.

In our original review and in each update, we report on studies identified by surveillance, particularly those that are not yet fully reported but may eventually be eligible for inclusion and those that are ineligible but can provide perspective on our results, such as uncontrolled studies of risk factors for reinfection in special populations or in the setting of emerging variants of concern. For this update, we summarize surveillance through 30 November 2021.

The outcomes of interest were the effects of previous infection on the risk for symptomatic reinfection, risk for any reinfection, severity of reinfection, and duration of protection. These outcome metrics, termed “protection,” are analogous to the end points used in studies of vaccine efficacy (9). Here, however, incident infections detected during the follow-up period in the positive cohort are reinfections, and those in the negative cohort are primary infections. The category “any reinfection” includes asymptomatic persons in whom virus has been detected.

Although many studies reported hazard ratios or relative rates of infection per person-time (often adjusted for various factors), our meta-analysis used absolute counts of events in both groups to obtain a relative risk estimate. We subsequently found a high degree of concordance between our calculated risk estimates and the rates reported in studies.

The primary analyses focused on the magnitude of protection against reinfection, quantified as the proportion or percentage of prevented infections. Each included study provided counts of reinfected individuals from the positive cohort and newly infected individuals from the negative cohort, which together yield an estimate of protection from reinfection—the difference in the proportion of incident infections between the negative and positive cohorts relative to the proportion observed in the negative cohort. We pooled these estimates via meta-analysis, both unstratified and stratified by population composition (general population, health care workers only, young adults only, or elderly persons only), to obtain combined effect estimates and corresponding 95% CIs. We used a continuity correction of 0.5 for 2 studies that reported 0 reinfections; this approach imparts a small but acceptable null bias to the meta-analysis, leading to conservative inference. We generated uncorrected estimates for comparison. The empirical Bayes random-effects meta-analysis model was chosen for its robustness properties and low bias in small-sample settings (10, 11). Study heterogeneity within strata was assessed using the I ² statistic (12). We assessed heterogeneity across strata using the Cochran Q _b statistic (13). Analysis was done using Stata, version 16.1 (StataCorp). (Supplement Item 2 provides further details.)

For some factors, including demographic variables, symptom status, health behaviors, vaccination, and variants, we could not examine their quantitative impact on effect sizes within a meta-analytic framework because of inconsistent reporting among studies. We abstracted information from study-specific sensitivity analyses and regression analyses when available, and we summarize these findings qualitatively.

Study-level factors that might influence estimates of protection include study duration, waiting interval between reinfection assessments, median participant age, underlying prevalence (proxied by the proportion of new infections in the negative cohort), and rigor in assessing positivity of infection (for example, whether asymptomatic infections were identified by surveillance and whether validation testing was done). We assessed these visually for relationships with effect sizes using scatter plots and nonparametric mean-smoothing of trends. We used meta-regression techniques to estimate R² values to examine each potential factor that may explain between-study heterogeneity. We also produced a L’Abbé and funnel plot as visual assessments of bias and sensitivity to study characteristics. The Harbord test was used to evaluate the evidence for asymmetry in the funnel plot (14).

We graded the strength of evidence to describe our confidence in effect estimates as high, moderate, low, or insufficient. The assessment is based on our analysis of the study limitations, directness, consistency, precision, dose-response, plausible confounding, and strength of association (15).

This work is based on a living rapid review done for the Agency for Healthcare Research and Quality. The funding source assigned the topic and contributed to the development of the review aims and scope but was not involved in data collection, analysis, manuscript preparation, or submission.

All of the studies were initiated in 2020 in the United States (16, 24–26), Europe (4, 27–37), or the Middle East (17, 38) and were completed before the emergence of the highly transmissible Delta and Omicron variants and before vaccine rollouts began. Nine studies used antibody test results to assign patients to the “positive” and “negative” cohorts (16, 25, 27, 29, 30, 32, 36–38), 3 used a combination of antibody test results and PCR (4, 28, 35), and 6 used PCR alone (Supplement Table 2) (17, 24–26, 31, 33). Study quality (risk of bias) ranged from moderate to high (Supplement Table 3).

All included studies found that reinfection was an uncommon event (range, 0% to 2.2%). The highest reinfection proportion was in a college student population, where the risk for infection in the control group was also very high (12.1%) (24). In settings with high proportions of control group infection (≥10%), reinfection risks were also relatively high (approximately 1% to 2%). When control group incidence of infection was below 5%, reinfection incidence was relatively low (about 0.7% at most).

In our meta-analysis, prior infection reduced the risk for symptomatic infection by 87% (95% CI, 84% to 90%) compared with no prior infection (Figure 1). The estimate was similar in studies that used serology alone to identify infected persons (risk reduction among 8 studies, 89% [CI, 87% to 91%]). The protection for health care workers and general populations was similar (87% and 88%, respectively). The risk differences were −0.043 (CI, −0.071 to −0.015) (4.3 infections per 100 individuals) in the general population studies, −0.043 (CI, −0.069 to −0.016) in health care workers, −0.099 (CI, −0.107 to −0.090) in college students, and −0.266 (CI, −0.449 to −0.083) in care facilities. Repeating the analysis without the use of continuity correction of 0 counts resulted in numerical differences to the meta-analyzed protection estimates of 0.01 or less.

Between-study differences in effect size relative to total variance were substantial (I ² = ∼85%), but this value should be interpreted in the context of high precision resulting from large sample sizes and low overall counts of reinfection. The effect sizes all fall within a narrow and high range, varying between 80% and about 100% protection, and are always indicative of very high protection. The L’Abbé plot shows no indication of systematic deviation from the meta-effect, no outlying studies, and no study suggesting a qualitatively different effect size (Figure 2). The Harbord test did not indicate that small-study effects or publication bias was present (P = 0.22).

Twelve studies reported the proportion of asymptomatic reinfections (4, 16, 24, 26, 27, 29, 31, 32, 35–38). Across studies, prior infection clearly protected against asymptomatic reinfection, but whether this protection is as strong as that against symptomatic reinfection is unclear. Follow-up methods were not always adequate to accurately detect symptoms that were present at the time of, or in the weeks after, a positive result on a PCR test. In the SIREN (SARS-CoV-2 Immunity and Reinfection Evaluation) study, which used the best methods, antibody-positive health care workers in England had lower risk for both symptomatic and asymptomatic infections than antibody-negative workers, but the degree of protection was different (93% lower risk for symptomatic reinfection vs. 52% lower risk for asymptomatic reinfection) (4). In contrast, in a retrospective cohort study based in the United States (26), protection was 84.5% for symptomatic infections versus 81.8% when asymptomatic infections were included (26).

Because prior infection prevented at least 80% of symptomatic reinfections, severe reinfection is a rare event (27, 31, 32, 36). In the largest series, 18 of 31 patients who had symptomatic reinfection were hospitalized within 30 days of diagnosis, but only 5 had COVID-19 symptoms at the time of hospitalization, and none required intensive care (26). In the other relatively large series, a study from Austria, 5 cases were described as moderate and 27 as mild (33).

Eight studies (26, 29, 33–38) that included more than 9 million participants in total (80 206 exposed and 9 696 466 control) examined whether the risk for reinfection varies over time (Supplement Table 4). All 8 found no evidence of waning protection during 6 to 13 months of follow-up. Further, 2 of the studies noted that the protection against reinfection may have increased over time (26, 38). There was no relationship between the length of the waiting interval and the reported duration of protection.

We analyzed 6 additional factors that might affect reinfection risk, but they varied among studies because best practices for studying SARS-CoV-2 reinfection are not established (Supplement Table 5). Study duration, waiting interval, median age of participants, underlying prevalence, inclusion of asymptomatic people in the positive cohort, and type of test used to allocate people to the 2 cohorts did not seem to have a strong relationship with the estimated effect size (Figure 3). R² values for effect size were low for other potential sources of variation in those estimates: cohort allocation criterion (13.2%; Q _B = 2.85; P = 0.241), median age of participants (6.7%), infection proportion in negative group (<0.1%), waiting period (<0.1%), total follow-up (<0.1%), and symptom status at baseline (<0.1%) (Figure 3). Protection against reinfection was slightly lower in 2 studies that used the most reliable methods to characterize reinfections (0.81 and 0.80 vs. 0.86 overall), but other factors could account for this difference (4, 34).

Some studies reported their own sensitivity analyses or mathematical modeling of the effect of these methodological factors (4, 16, 27, 29, 34, 36). Overall, protection against reinfection was not correlated with the asymptomatic testing rate, cohort assignment criteria, or method for assessment of infection during the follow-up period (4, 29, 36).

We saw no gender differences in protection against reinfection.

Studies offered no useful information about the effect of race and ethnicity on protection from reinfection. Although some studies adjusted for immunosuppression or other comorbid conditions, none of our included studies reported on the incidence of reinfections in immunocompromised persons or other comorbidity subgroups. A study that was ineligible for inclusion in our meta-analysis investigated characteristics of 23 suspected reinfections in electronic health records and found that 83% of presumed reinfections were in those with immunocompromised conditions (19).

Results for age are conflicting. In the meta-analysis, there was no compelling evidence that cohort composition (that is, whether mostly young or mostly old) influenced the degree of protection afforded by prior infection (Q _b(3) = 5.63; P = 0.131). Across studies, estimates for young (median age, ∼20 years) and older (median age, ∼85 years) adults were also qualitatively similar (82% for young vs. 92% for old), although for both estimates there were few studies and sample sizes for the available studies were not large. A large, population-based study from Denmark found no difference by sex in estimates of protection against repeated infection but a striking difference in protection against repeated infection in the elderly (34). Among persons aged 0 to 64 years, estimated protection was 80% to 82%, whereas in those older than 65 years, it was 47.1% (CI, 24.7% to 62.8%). Among those older than 65 years who had a previous infection, the infection rate was 8.01 per 100 000 person-days of follow-up, compared with 4.25 to 5.92 per 100 000 person-days in the younger age groups. However, in the negative control cohort, the infection rate in the elderly was much lower than in the younger groups (16.92 vs. 27.42 to 38.13 per 100 000 person-days). The low infection rate in the elderly control participants relative to other control participants could be related to public health approaches to opening up after lockdown (perhaps selective isolation of more vulnerable groups), but this explanation does not account for the relatively high rate of reinfection in the positive cohort. Another study in Switzerland found a higher risk for reinfection among those older than 60 years compared with younger persons (>60 years old: hazard ratio, 0.44 [CI, 0.14 to 1.4]; <60 years old: hazard ratio, 0.05 [CI, 0.01 to 0.20]) (36). A study in Israel compared protection among age groups and found a slight decrease in protection for those older than 80 years (overall protection: 94.8% [CI, 94.4% to 95.1%]; over-80 protection: 91.4% [CI, 85.5% to 94.9%]) (17).

These findings on age conflict with results from studies of presumably frail elderly patients in long-term care facilities, where rates of infection in the control groups were far higher and rates of reinfection in the positive groups were as low as, or lower than, those in other populations (Figure 1) (29, 30).

Assessments of the relationship between the severity of the initial infection and protection against reinfection were limited. In most studies, initial infections were not detected until antibodies had formed and information about symptoms was either unrecorded or subject to recall bias. Hospitalization during the initial infection could also be a proxy for severity, but in most studies the number of hospitalized patients was too small for analysis. Comparing studies that used sampling methods that detected people with no or mild symptoms (27, 31, 35–37) with those that recruited only symptomatic people (25, 26, 28, 33) did not show a clear relationship between recruitment method and protection against reinfection. A recently published cohort study found that mild COVID-19 was associated with protection against reinfection and generally supports our conclusions, although no reinfections were observed and the sample was relatively small (23).

The B.1.1.7 (Alpha) variant was studied in 4 of the studies meta-analyzed. Although evidence is sparse, there is no indication of increased risk for reinfection for this variant (4). Of 2 additional studies that reported on the Alpha variant, neither indicated an effect of the variant on reinfection (17, 29). In an ecologic study among 36 920 U.K. users of the COVID-19 Symptom Study app, the rate of “possible reinfection” was 0.7 and did not change after the Alpha variant became prevalent (18).

Data on reinfection risk in the setting of the B.1.617.2 (Delta) variant are sparse and are still developing, but a preprint from Israel, surveillance data from Kentucky, and an outbreak investigation in Texas recently indicated that immunity acquired by infection provided substantial protection after the Delta variant became predominant (20–22, 39). Preliminary data on Omicron raise the possibility that protection against symptomatic (but not serious) reinfection may be lower than that observed in the studies we reviewed (39).

Vaccination during follow-up could bias estimates of protection, particularly if vaccination rates differ between the positive and negative cohorts. In 5 of the studies included in our meta-analysis, the follow-up period traversed the first vaccine rollout. However, most were nearly completed at the time of the vaccine rollout, and none had sufficient data to assess how vaccination influenced the estimate of protection (4, 17, 29, 35). For example, in the SIREN study, which had the largest subgroup of vaccinated participants (n = 13 401), only 0.4% of the study's person-time of follow-up included participants who would be considered to have protection as the result of vaccination.