Ultraviolet-C Radiation and Hospital Acquired Infections

James Lyons-Weiler, PhD

Hodges and colleagues began with an observational finding that should immediately have focused attention on the structure of their statistical adjustment. Among subsequent occupants of rooms receiving standard chlorine-based terminal cleaning, they identified 382 pathogen transfers among 24,277 eligible observations, a rate of 1.6%. Among occupants of rooms receiving chlorine-based cleaning plus ultraviolet-C disinfection, they identified 118 transfers among 4,982 observations, a rate of 2.4%. The unadjusted difference was statistically significant at P<.001.

Those counts correspond to a crude odds ratio of approximately 1.52. Nothing about that number establishes that UV-C increased transmission, because UV-C was not randomly assigned and the treated and untreated rooms differed in several respects. We have seen other studies in which over-adjustment leads to implausible results in the other direction.

The study was observational, and the authors explicitly describe UV-C deployment as discretionary. Confounding is therefore not merely possible; it is one of the principal problems the analysis had to solve. How they did, however, leaves a lot to be desired.

The difficulty is that the adjusted result moved a long way. After the authors controlled for facility, source-patient time in the room, time between the source patient’s discharge and the next patient’s admission, and the exposed patient’s time in the room, the UV-C estimate became OR 1.06, with a 95% confidence interval of 0.84 to 1.32 and P=.64. The crude association of roughly 1.52 had effectively disappeared.

That transformation is the central methodological issue in the paper. The relevant question is not whether adjustment is generally desirable. The question is whether the variables chosen for adjustment are appropriate for estimating the effect the authors claim to have estimated.

The authors’ final logistic regression included four principal adjustment terms in addition to UV-C exposure: facility, source-patient duration in the room, the interval between patients, and exposed-patient duration in the room. The time variables were log transformed. In Table 4, source-patient time had an OR of 1.13, time between patients had an OR of 0.99, exposed-patient time had an OR of 3.98, and UV-C use had an OR of 1.06.

There is no obvious classic overfitting problem. The dataset contained hundreds of transfer events, and the number of reported predictors was modest. The more important concern is causal specification.

Facility is an understandable adjustment variable because hospitals differed in implementation, surveillance, cleaning practices, and patient mix. Source-patient time in the room is also reasonably interpretable as a pretreatment variable because a longer stay could increase environmental contamination and might influence the decision to use enhanced terminal disinfection.

The other two variables are much harder to defend without a clearly stated causal model.

“"Exposed-patient length of stay” occurs after the cleaning decision and after the patient enters the room. It is therefore not an ordinary baseline confounder. It is also the strongest predictor in the reported model, with an odds ratio of 3.98.

That association is unsurprising because a patient who remains in the room longer has more time in which to acquire an organism, more time for colonization or infection to become clinically apparent, and more opportunity to be cultured. The study’s own case definition reinforces this dependence on time. A positive culture could count as an incident transfer if it occurred after admission through one day after discharge.

Exposed-patient length of stay is therefore closely related to both time at risk and opportunity for ascertainment. It may also be affected by illness severity, complications, and potentially by the acquisition of the very infection being studied. Once a variable can be influenced by causes of infection and by infection itself, ordinary regression adjustment becomes hazardous because conditioning on that variable may create or distort associations rather than remove confounding.

The causal structure can be stated simply. Illness severity can prolong hospitalization and independently increase the risk of hospital-acquired infection. Acquisition of an MDRO can also prolong hospitalization. Eventual length of stay can therefore become a common consequence of multiple causal processes. Conditioning on that common consequence creates a plausible route to collider bias.

This does not establish that collider bias caused the adjusted UV-C estimate to move toward 1.06. The paper does not provide enough information to determine that. It does establish that eventual exposed-patient length of stay required a much more careful causal justification than the paper provides, particularly because it is such a strong predictor of the outcome.

The natural alternative would have been to preserve the temporal structure of the data. Patient time in the room could be handled as time at risk in a survival or multistate analysis, with discharge and possibly death treated appropriately rather than reducing the process to a binary logistic outcome and then adjusting for the patient’s eventual duration of exposure.

The interval between the source patient’s departure and the subsequent patient’s admission raises a different problem.

Rooms without UV-C had a median interval of five minutes between patients. Rooms receiving UV-C had a median interval of ten minutes. The authors also report a median UV-C treatment duration of 17 minutes.

If implementation of UV-C changes the room-turnover process, and the additional interval before another patient enters changes pathogen survival or exposure, then turnaround time may be part of the causal effect of implementing UV-C. In that case, adjusting for turnaround time removes part of the very effect being studied.

That distinction depends on the scientific question. If the intended estimand is the total effect of adding UV-C to routine hospital practice, then operational consequences of performing UV-C generally belong to that total effect. If the intended estimand is instead the direct effect of ultraviolet exposure while somehow holding turnaround time constant, adjustment for turnaround time may be defensible, but the paper does not frame its conclusion that way.

The authors conclude that UV-C “does not provide incremental value” beyond standard cleaning. That is a practical implementation claim. A model that conditions on something caused by implementation may estimate a narrower quantity than the conclusion implies.

There is also an unresolved measurement issue in Table 2. The median reported interval between patients in UV-C rooms is ten minutes, while median UV-C treatment duration is 17 minutes. There may be a perfectly reasonable explanation involving how the timestamps were defined or which observations contributed to each variable, but the paper does not make that reconciliation obvious. Because turnaround time was used as an adjustment variable, the definitions deserve clarification rather than assumption.

The observational design creates a more basic question: why was UV-C used for some rooms and not others?

The authors state that UV-C deployment was discretionary and that deployment strategies differed across hospitals. Once treatment is discretionary, the probability of receiving UV-C may be related to factors that also affect transmission risk. Those factors could include pathogen type, unit, perceived contamination, outbreak conditions, isolation status, staffing, bed pressure, patient acuity, environmental-services workload, availability of the device, or local infection-control policy.

The paper does not establish that all of those factors actually influenced treatment assignment, and they should not be assumed to have done so. The problem is that the study offers relatively little information about the treatment-assignment process and relatively sparse adjustment for patient-level clinical determinants of acquisition.

The primary regression shown in Table 4 does not include variables such as patient severity, comorbidity, antibiotic exposure, immune status, invasive devices, or specific hospital unit. Those omissions matter because they are more naturally conceived as potential confounders than eventual exposed-patient length of stay.

The paper also acknowledges that active surveillance for MRSA and VRE varied among facilities and that some participating hospitals discontinued routine contact precautions for MRSA, VRE, and selected non-CRE gram-negative organisms in 2018. The authors correctly note that differences in surveillance and contact-precaution practices could affect case ascertainment and transmission, while suggesting that adjustment for facility may account for those differences.

Facility adjustment may account for stable differences between hospitals. It cannot necessarily absorb a change in policy, surveillance, or practice occurring within a hospital over calendar time. That matters here because the hospitals introduced UV-C at different times during the 2016–2018 study period.

A facility indicator and a calendar-time adjustment are not interchangeable. If surveillance practices, contact precautions, pathogen prevalence, or patterns of UV-C deployment changed within hospitals over time, residual confounding remains plausible.

This produces a curious imbalance in the modeling strategy. Variables that clearly occur before treatment and might help explain discretionary UV-C assignment appear incompletely represented, while two variables occurring after the UV-C decision were included in the final adjustment.

That is precisely the situation in which a causal diagram and a prespecified statement of the estimand would have helped.

The outcome itself also limits the strength of the conclusion.

The investigators did not conduct active surveillance of every source and exposed patient, and they did not genetically type isolates to confirm that organisms detected in subsequent occupants were related to organisms carried by the prior occupants. They acknowledge both limitations.

The outcome was therefore putative prior-occupant transmission based on organism identity, resistance pattern, and temporal relationship.

That is a reasonable epidemiologic proxy. It is not proof of the transmission pathway.

Some detected events could have arisen from healthcare workers, other patients, other environmental reservoirs, or previously undetected colonization. Such events would not necessarily be preventable by terminal UV-C treatment of the room. If those events were included in the outcome, they could dilute a genuine effect of UV-C on transmission specifically mediated by environmental contamination from the previous occupant.

Again, this does not demonstrate that UV-C is effective. It limits the inference available from a failure to detect effectiveness.

The broader literature is similarly more nuanced than either a universal claim of benefit or a universal claim of futility. The BETR Disinfection randomized trial reported reductions under some UV-C strategies and not others, including differences depending on the background disinfectant regimen and organism. Hodges et al. themselves acknowledge that the BETR findings were mixed and that no significant additional benefit was observed in the bleach-based comparison most analogous to their chlorine-based setting.

That is exactly why this observational study should be interpreted on its own terms rather than used to settle the broader question.

Take this course with us and you, too, will be able to expertly critique studies.

The paper would become considerably easier to interpret if the authors showed how the UV-C estimate changed as covariates entered the model.

Begin with the crude association.

Then add facility.

Then add source-patient duration and other clearly pretreatment variables.

Then show the estimate with and without turnaround time.

Finally, show what happens when exposed-patient length of stay is introduced.

If the estimate moves from approximately 1.52 toward 1.06 primarily after facility adjustment, that would strongly suggest that the crude association was driven by differences among hospitals.

If the major shift occurs after exposed-patient duration enters the model, the interpretation would be quite different because that variable occurs after exposure and is strongly tied to the outcome process.

If turnaround time materially changes the estimate, then the authors need to state whether they are estimating the total effect of implementing UV-C or a direct effect after removing part of the operational pathway through which implementation may work.

Without those intermediate models, readers see the beginning and the end of the statistical transformation but not what produced it.

The study therefore supports a narrower conclusion than the one stated in the discussion. In this retrospective, nonrandomized dataset, the authors’ selected adjusted logistic regression did not detect a statistically significant protective association between adjunctive UV-C and their definition of putative prior-room-occupant pathogen transfer. That result is real and should be reported.

It does not establish that adjunctive UV-C provides no incremental value.

The observed transfer rate was 2.4% in UV-C rooms and 1.6% in rooms without UV-C, corresponding to a crude odds ratio of about 1.52. The final adjusted estimate was 1.06. The model producing that estimate included eventual exposed-patient time in the room, the strongest predictor reported in the model at OR 3.98, as well as an interpatient interval that may partly lie downstream of UV-C implementation.

Those choices may prove defensible. They may even produce the same null estimate under a more explicitly causal analysis.

But this paper does not show us that. It leaves the question open due to deficient design of analysis.

Hodges JC, Bilderback AL, Bridge CM, et al. (2022). Assessment of the effectiveness of ultraviolet-C disinfection on transmission of hospital-acquired pathogens from prior room occupants. Antimicrobial Stewardship & Healthcare Epidemiology 2:e110.