Effectiveness of Over-the-Counter Nicotine Replacement TherapyEffectiveness of Over-the-Counter Nicotine Replacement Therapy

To the Editor: Drs Pierce and Gilpin¹ conclude that nicotine replacement therapy (NRT) has not increased smoking cessation rates since it became available over-the-counter. We do not believe that the authors can draw such efficacy conclusions from this nonrandomized, noncontrolled study.

Pierce and Gilpin compared users of NRT vs nonusers, but these may be different populations. Smokers who cannot quit on their own may be more likely to use NRT and thus are likely to be more dependent than those who attempt to quit without it. Stratification for the number of cigarettes smoked cannot correct for this.

This study is also limited by retrospective self-reporting, which relies heavily on memory, and may be biased as smokers may be more likely to remember successful cessation attempts than short, unaided, and unsuccessful efforts. Furthermore, the authors did not obtain biochemical verification of abstinence. Finally, the authors suggest that NRT is not effective in smokers who smoke less than 15 cigarettes a day. However, they did not consider the growing antismoking climate in California during the 7-year period of their study, thereby confounding the conclusions about treatment effects in moderate and heavy smokers vs light smokers over time.

A recent meta-analysis² found that NRT doubles the successful completion rate relative to placebo. The authors' conclusions have the potential to damage public confidence in NRT and may deter smokers from using effective treatment. Authoritative agencies have recommended that smokers should use NRT when trying to quit smoking.^{3 - 4}

Disclosure: All of the authors work for Pharmacia, a manufacturer of nicotine replacement therapy products.

To the Editor: Although they may seem surprising, the results of Drs Pierce and Gilpin¹ are actually consistent with the few published controlled "minimal intervention" efficacy studies of the nicotine patch.^{2 - 3} For example, my colleagues and I³ found that an active patch achieved 10% abstinence while a placebo patch achieved 12% abstinence at 48-week follow-up, a nonsignificant difference. All patients had received a total of about 15 minutes of behavioral counseling in what could be fairly characterized as a "patch alone" condition. We were surprised by the results. As scientists, however, we must find room for data that challenge strongly held beliefs.

One of the difficulties in interpreting the efficacy of NRT independently of behavioral treatment is that NRT is designed to be combined with behavior therapy, and the majority of published studies include some form of behavioral intervention in addition to NRT.⁴ Simply wearing a patch, without any behavioral intervention, is unlikely to be effective.⁵ It could be argued that there is a public health benefit to any cessation attempt, with or without a patch, but it can be costly and disappointing for the vast majority of smokers who do not achieve their goal to quit smoking during a specific cessation attempt with the patch alone. I believe that patients require hopeful but realistic expectations regarding their efforts to quit. To do that, I think clinicians need to share the data of Pierce and Gilpin instead of trying to explain them away.

To the Editor: As a rural family physician with a large population of African American patients, who disproportionately experience greater smoking-attributable morbidity and mortality,¹ I am constantly searching for ways to reduce health disparities associated with smoking. I agree with Drs Pierce and Gilpin² that prescription benefit support of pharmaceutical cessation aids reduces the cost disincentives for their use. Many of my patients have such coverage. However, the most important factor in use of smoking cessation aids in African American and Hispanic patients in rural areas is access to information.

There is not even a daily newspaper in my county. Thus, patients' primary source of information (other than television) is print media with advertisements that specifically target increasing smoking in their ethnic groups. These magazines and monthly papers continue to have disproportionately large amounts of ads with images that glorify smoking. This leaves the physician with a profound responsibility to educate patients about the dangers of smoking.

I am the only African American family physician in my county and there is one Hispanic family physician. Many minority patients tell me that no health care provider has ever addressed the issue of smoking cessation with them, yet studies have shown that more than 80% of African American smokers desire to give up smoking.³ Many patients attribute this paucity of intervention to lack of interest, cultural insensitivity, and racism.

Placing smoking cessation aids on the shelf for easy access makes them more visible and provides opportunities for smokers to discuss them freely with their friends and local pharmacists. In my experience, this ultimately leads to increased use of smoking cessation aids. Not enough research has been done on smoking cessation patterns in minorities. Given that smoking is a significant cardiovascular disease risk factor in these communities,⁴ I believe these concerns warrant further investigation.

To the Editor: Drs Pierce and Gilpin¹ state: "Since becoming available over the counter, NRT appears no longer effective in increasing long-term successful cessation in California smokers." This is a strong assertion that has the potential to significantly damage public confidence in NRT. In fact, this conclusion is much stronger than can be justified by the study results. The findings are derived from self-reported data on past cessation attempts from cross-sectional surveys in a single state. We believe that it is premature to draw inferences from this research.

One major limitation is the reliance on a comparison between nonrandomized groups: those who chose to use NRT vs those who did not. The analysis corrected for demographics and recall of cigarette consumption a year earlier but may not have accounted for all potential confounding factors. People deciding to use NRT in a cessation attempt are likely to be different in important but unmeasured ways compared with those who attempt to quit without pharmacotherapy. For example, they may be more addicted to nicotine, even controlling for cigarette consumption, and they might have different histories of psychiatric comorbidities. The authors also excluded cessation attempts lasting less than 1 day. This could have a profound impact on estimation of relative long-term success because relapse often begins early in the cessation attempt (within 24 hours² ), and a good proportion of NRT effects may occur in this early postcessation period.³

The authors' main conclusion is that the long-term success of cessation attempts in those using NRT compared with nonusers has decreased since NRT became available over the counter in 1996. However, the conclusion is based only on the absence of a difference in long-term abstinence rates between NRT users and nonusers in 1999; the authors do not directly compare the difference between cessation rates of NRT users and nonusers in 1999 vs earlier years. Their hypothesis must be tested by assessing whether there was a significant change in the NRT effect across the 3 survey years. The authors should also assess whether the cessation rate among NRT users changed during this time.

We were disappointed that Pierce and Gilpin did not address limitations in their data. They only addressed limitations in the work of others. The need to address their own study's limitations is particularly important because the authors' conclusions challenged a large body of research⁴ and authoritative evidence-based clinical practice guidelines.⁵

Disclosure: All authors contribute to treatobacco.net, a database on the treatment of tobacco dependence run by the Society for Research on Nicotine and Tobacco and the World Health Organization.

Financial Disclosure: Dr Fiore has served as a consultant to, given lectures sponsored by, or has conducted research sponsored by Ciba-Geigy, GlaxoSmithKline, Lederle Laboratories, McNeil, Elan Pharmaceutical, Pharmacia, and Pfizer. Dr Hatsukami is on the Tobacco Dependence Scientific Advisory Board for Pharmacia Upjohn and has received products from Pharmacia Upjohn and GlaxoSmithKline for National Institutes of Health–funded studies. Dr West has undertaken research and paid consultancy for and received travel expenses and hospitality from manufacturers of nicotine replacement products.

In Reply: Dr Franzon and colleagues note that meta-analyses of randomized trials estimate the efficacy of NRT as doubling the rate of long-term successful cessation.^{1 - 2} Our data and that of others,³ however, suggest that its long-term effectiveness in the general population is less promising. There are many possible reasons for this discrepancy. The majority of the studies reviewed in the US Public Health Service guidelines¹ use point prevalence as the primary outcome measure; we used continuous abstinence. The guidelines suggest that continuous abstinence underestimates success¹ because it does not count as successful those smokers who relapsed and were then abstinent again by follow-up, regardless of NRT use for the latest attempt. Previously, we reported that only 50% of smokers who quit between 3 and 6 months were still abstinent 18 months later.⁴ Thus, we believe that point prevalence inflates the estimate of success and is not the best measure of either efficacy or effectiveness.

Dr Antonuccio notes other reasons for mismatch between the clinical trial and real world setting. Nearly all NRT trials included a counseling component, which by itself can increase successful cessation.⁵ Also, moderate to heavy smokers in the general population may not be properly informed about correct use of NRT products. The general lack of NRT efficacy in clinical trials of light smokers has been noted previously,² and many trials only enrolled smokers if they quit for a day. Also, as Dr Cadore notes, there is a considerable cost disincentive for NRT use in the real world. This is not the first instance where clinical trial efficacy did not translate into a comparable level of effectiveness in the general population.⁶

In response to Ms Stead and colleagues, details of our survey methodology are published and referenced, including concerns with recall of short-duration cessation attempts,⁷ without which long-term success rates are increased. Furthermore, with similar methodology (eg, ignoring <24-hour cessation attempts) for all 3 surveys, results across time should not be differentially biased. Despite changes in smoking behavior resulting from the California Tobacco Control Program, it is important to note that the relapse curves for smokers not using NRT were superimposable for all 3 survey years. Abstinence rates at 85 days (to avoid reporting number preference) for NRT users were 38% in 1992, 33% in 1996, 29% in 1999, and about 25% in nonusers over all 3 years. Although this difference between users and nonusers was statistically significant in 1996, it was not in 1999.

Both Franzon et al and Stead et al feel that our conclusions are much stronger than the data justify. They worry that these findings will damage public confidence in NRT. We would hope that our results point to the need for research into how NRT can be made more effective in the general population. We agree with Silagy et al² that "Falsely raising the expectations of smokers who purchase these products ‘over-the-counter' without at least providing minimal support and an adequate explanation of the limitations of using NRT may be counterproductive in the long term."

To the Editor: In their meta-analysis, Dr Safdar and colleagues¹ concluded that antibiotic exposure during Escherichia coli O157:H7 colitis was not associated with an increased risk of hemolytic uremic syndrome (HUS). Because the included studies were very heterogeneous, however, conclusions based on a single risk estimate may be misleading.

In Figure 1 of the article, 2 of 9 studies reported significantly increased odds ratios (ORs); 6 studies showed no association; and 1 study, which treated patients with fosfomycin, showed a decreased risk of HUS. Safdar et al treated the 2 studies with increased ORs as statistical outliers and averaged these effects against the much larger studies.

Part of this heterogeneity may be related to underlying biological mechanisms. Different strains of E coli O157:H7 respond differently in their production of Shiga-toxin with exposure to subinhibitory concentrations of antibiotics; some strains increase Shiga-toxin production while others do not.² This is believed to result from differential expression of bacteriophage-encoded Shiga-toxin genes.³ Given that E coli O157:H7, recovered from separate outbreaks, are usually single-strain clones whose response to antibiotics may not be generalizable to outbreaks due to other strains,⁴ the result could be a multimodal distribution of responses to antibiotics between outbreaks. Therefore, the size of each outbreak is less important than is the genetic characteristics of the strain involved. However, taking the average effect of all outbreaks effectively obscures what might well be an accurate description of the behavior of different clones of E coli O157:H7.

Although the random-effects model would have been preferable to the fixed-effects model used in this meta-analysis, this alone would not have resolved the fundamental problem that arises when attempting to summarize a pool of studies with a bimodal distribution of risk factors. This limitation of meta-analysis has been described previously⁵ and could conceivably be corrected using meta-regression or a stratified analysis.

A more meaningful measure of the risk from this pathogen could be obtained by determining the proportion of all isolates of enterohemorrhagic E coli that increase their Shiga-toxin secretion when exposed to antibiotics. However, because clinicians cannot know the characteristics of a given strain of E coli O157:H7 in advance, we believe that withholding antibiotics for patients suspected to be infected with this pathogen remains the preferred strategy.

To the Editor: We are concerned that Dr Safdar and colleagues¹ did not account for important limitations of 2 of the studies in their meta-analysis. First, of the 300 culture-positive patients in the study by Ikeda et al,² 100% of patients who had HUS were given antibiotics (including, but not limited to, fosfomycin). Among those who did not develop HUS, 99% of patients received antibiotics. This analysis lacks a significant control group of culture-positive patients who did not receive antibiotics; Safdar et al stated this would be a criterion for exclusion. Furthermore, the OR that Safdar et al report is only for fosfomycin administered on day 2 of illness and not on other days. This is after excluding culture-positive treated patients with incomplete and complete HUS, and those treated with antibiotics other than fosfomycin. Thus, the OR showing a significant negative association may be a spurious finding.

Second, the "inflated OR" between antimicrobial use and HUS in the study of Pavia et al³ appears to have been derived from an error in the OR calculation and not from a lack of control for the severity of illness. Of the 14 patients described, 7 received antibiotics and 7 did not. Of the 7 who developed HUS, 5 received antibiotics. Of the 7 who did not receive antibiotics, 2 developed HUS. Therefore, we calculate the OR as 6.25 (95% confidence interval [CI], 0.69-56.8) (STATA version 6.0, Stata Corp, College Station, Tex) and not 80.6 (95% CI, 3.38-1922), as calculated by Safdar et al.

Neither the individual studies cited by Safdar et al nor their meta-analysis demonstrate a substantial benefit of antimicrobial therapy in the presence of culture-proven E coli O157:H7 gastroenteritis. Given presently available data, there is no compelling or ethical reason to perform a randomized controlled trial (RCT), as Safdar et al suggest. If there is no prospect that antibiotic treatment of E coli O157:H7 will produce any benefit, then there is no need for an RCT to determine whether it will cause any harm.

To The Editor: We are concerned that the study of Ikeda et al¹ disproportionately influenced the results of the meta-analysis by Dr Safdar and colleagues.² Specifically, Ikeda et al concluded that use of fosfomycin in the first 2 days of illness, but not later, was associated with decreased risk of HUS. Designating the first day of illness as that on which any sign or symptom first occurred (including fever and abdominal pain and not only diarrhea) is problematic and not clinically useful because of the subjectivity and poor specificity of these assessments. Even if this definition could measure accurately the interval between illness onset and treatment, the benefit accruing to patients starting fosfomycin on day 2 (the only group chosen for analysis by Safdar et al) is no more than subgroup analysis. Moreover, benefit when administered during the second day of symptoms, but not when administered on other days, is microbiologically implausible. Ikeda et al adjusted only for parental report of fever but not for white blood cell count, a repeatedly demonstrated risk factor for HUS. Also, because few patients received no antibiotics, nontreatment with antimicrobials was not assessed.

Safdar et al excluded a prospective study³ that " . . . did not use physiological measures to control for severity of illness, which may have contributed to an increased magnitude of the association found . . . " without specifying what physiological measures were incorporated into studies that were retained. Nonbloody traveler diarrhea, which is appropriately treated by antibiotics, and E coli O157:H7 diarrhea, which is usually bloody, are termed indistinguishable by Safdar et al. The authors cite 2 studies supporting a "protective effect" of fosfomycin, but elsewhere Safdar et al disqualify 1 study⁴ from analysis because it did not " . . . define clear diagnostic criteria for HUS"; the second study was conducted in protein-calorie malnourished mice.⁵

Safdar et al address interstrain differences when evaluating E coli O157:H7 treatments. However, performing a nationwide RCT as they propose, " . . . to conclusively determine whether antibiotic treatment of E coli O157:H7 enteritis increases the risk of HUS," would be unethical, unless and until credible data demonstrate the potential benefit of this treatment. In view of existing data that antibiotics are either neutral or harmful, the authors' implied message that antibiotic treatment of E coli O157:H7 infections might be beneficial is unwarranted.

In Reply: We agree with the concerns of Dr Gill and colleagues regarding the differential expression of Shiga-toxin genes. We also agree that the genetic characteristics of the infecting strain of E coli 0157:H7 are important to consider when assessing the effects of antimicrobial use on the risk of development of HUS. Their concerns would be obviated by the large multicenter RCT we advocate, with multiple strains of infecting E coli 0157:H7 represented in the study population.

Dr Wong and colleagues and Dr Tarr and colleagues express concerns regarding our inclusion of the study by Ikeda et al.¹ Although some data in this study were gathered in 1997, data collection was started at the time the outbreak occurred. Excluding this study does not materially change the results of the meta-analysis of all studies (OR, 1.4; 95% CI, 0.9-2.2).

In response to Wong et al, we point out that 6 of the 8 patients with HUS in the study of Pavia et al² had been given a sulfonamide compared with none of 15 persons (residents of institutions for cognitively impaired persons and members of the staff) with E coli 0157:H7 infection who did not develop HUS. Recalculating the OR with these data produces a result of 80.6 (95% CI, 3.38-1922), our original result.

Finally, we disagree with the contention that a large, prospective RCT to assess the effect of antimicrobial therapy for E coli 0157:H7 enteritis on the risk of developing HUS is unnecessary and even unethical. We reassert our belief that the conclusion that antimicrobial therapy in patients with HUS is deleterious is not proven by the sum total of studies to date. We further point out that the study by Bell et al,³ included in our meta-analysis, did not find antimicrobial use to be a risk factor for HUS. We also emphasize that we did not and do not advocate antimicrobial therapy for E coli 0157:H7 enteritis but have simply tried to show that the issue has not been resolved.

Numerous examples can be found in the medical literature in which prospective RCTs have found vastly disparate results compared with the observational epidemiologic studies preceding them that had been accepted as the final answer.^{4 - 6} We think it can be argued equally well that it might be unethical not to do such a trial. The discordant results of the studies included in our meta-analysis indicate that without a large, prospective RCT free of the unaccounted confounding present in observational studies, the role of antibiotic therapy in complicating E coli 0157:H7 infection will remain uncertain.