### EPA Response to Peer Review Comments

**External Peer Review of EPA’s**  **Draft Document Approach to Assessing Non** 
**- cancer Health Effects from**  **Formaldehyde and Benefits from Reducing**  **Non**
**- cancer Health Effects as a Results of Im**  **plem enting Formaldehyde**  **Em ission Lim**  **its for Com**  **posite Wood Products**

**Peer Reviewers:** John R. Balmes, M.D. G lenn C. Blomquist, Ph.D. A. My rick Freeman III, Ph.D. Shelby Gerking, Ph.D. David Kriebel, Sc.D. Frederick J. Miller, Ph.D., Fellow ATS Rebecca T. Parkin, Ph.D. , MPH2 **I. GENERAL IMPRESSIONS NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  The document is clearl y and concisel y written. The background subsections of Section 2:

Non

- cancer Health Effects

– Derivation of Concentration

- Response Functions for sensory irritation (2.1.1), asthma (2.2.1), and female reproductive toxicity (2.3.1) are extremely brief, especiall y the latter two. While it is understandable that the EPA does not wish to be duplicative of the material in the draft IRIS document on formaldeh yde or the NAS review of the IRI S document, some readers of the “Approach” document will not have read the IR IS and NAS documents and thus will benefit from a bit more background context on formaldeh yde and asthma or formaldeh yde and female reproductive toxic ity. The aim of Section 2 is to present the development of the concentration

response functions, so details of the health effects themselves are deliberatel y brief. More detailed information can be found in the draft IR IS assessment. **David Kriebel, Sc.D.**  The overall impression is of a thoughtful and well

- written document. The authors have

provided a generall y cl ear and logical explanation of their reasoning throughout. There are a few exceptions, noted below, where additional explanation or documentation could improve the presentation. No response required.
**Frederick J. Miller, Ph.D., Fellow ATS**  The comments provided are related to the health assessment and concentration

- response

evaluation portion of the above cited document as this reviewer was not aske d to comment on the economic benefits assessment approach. For the most part, the sections on sensory irritation, asthma, and female reproductive toxicity are clearl y presented and the material is developed in a logical manner. Some exceptions are noted in this reviewer’s responses to the specific charge questions. The decision on the concentration

- response functions to take forward to the economic benefits anal ys es is best documented for sensory irritation. This reviewer provides a suggestion for how far b elow 100 ppb of formaldeh yd e the modeling results developed b y the Agency based on the Hanrahan et al. (1984) study can be used. The material included in support of using the McGwin et al. (2010) meta analy sis for asthma in children does not adequatel y des cribe the short comings of the meta anal ys is. The uncertainties and conflicting results of the studies make this reviewer reticent to endorse the concentration

- response function for the odds ratio based on the McGwin et al. (2010) meta anal ys is. The case t o use background adjusted exposure data for the female reproductive toxicity concentration

- response curve is adequately defended. However, the Agency does No response

required. (Specific issues addressed in comments below).3 not indicate if the linear risk or the exponential risk curve will be used. Overall, the information presented is accurate. To their credit, in a number of places, the EPA authors have incorporated criticisms included in the NAS report of the Agency ’s draft IR IS assessment document. By addressing the responses to the charge questions, the Agency will be in a good position to move forward with the cost benefit analy sis required by Executive Order 12866 related to the Formaldehyde Standards for Composite Wood Products Act. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  The draft is clearl y organized and, in large part, well

- written. Minor inaccuracies are noted

below. Most sections were clear, although some key issues were not mentioned or are not clear; these concerns are noted below. Except in a few instances as noted below, the conclusions are effectively supported by

the text provided. Uncertainties are important to discuss. EPA has captured man y of the important ones, but may need to add more to these sections based on this and other reviewer s’ comments. Being thorough in all uncertainty sections is crucial to the foundations of the benefit assessments. EPA has added further discussion of uncertainties addressing reviewer comments.

**II. RESPONSE TO CHARGE QUESTIONS CHARGE QUESTION 1:**  **The li terature base of residential epidemiology studies of the irritation effects with quantitative**  **concentration**
**- response data was limited, but data were available from which a concentration** 
**- response function could be estimated**  **for eye irritation. Please**  **comment on whether the concentration**
**- response function is appropriately derived from the studies used in the draft Approach**  **Document. NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  The concentration

- response function (CRF) for sensory irritation is derived from one small field study , Hanrahan et al. (1984). Because most individuals exposed to formaldehyde from the products of interest will be exposed at levels below 100 ppb, the EPA is appropriatel y concerned about the form of the CRF in this range. Unfort unately , the data for exposures below 100 ppb are not given in the original Hanrahan paper and the regression of prevalence of eye irritation and formaldehyde concentration in the paper covers the range of 100

- 800 ppb. Another issue regarding CRF derivati on from the Hanrahan paper is the relatively small sample size (n=61). The L iu et al. (1991) study , which involved a much larger population, is supportive of the concept that there is a CRF The regression covers the whole range of exposures (“< 0.10 ppm to 0.80 ppm”); however, in Hanrahan et al.’s Figure 1, onl y modeled4 for formaldeh yde and eye irritation at relativel y low levels of e xposure , but was not used in the actual derivation of such a CRF because of the way the authors aggregated their data into low, medium, and high levels of exposure. prevalences for exposures ≥ 100 ppb are portray ed. The Hanrahan et al. study is relativel y small; however, as noted by the reviewer, the L iu et al. study is supportive. **David Kriebel, Sc.D.**  I see no problems with the derivation of the concentration

- response function itself. In

Section 2.1.3, Ithink it would strengthen the argument to at least acknowledge the problem of acclimatization. There is evidence from a number of studies

– notabl y the studies of studies con ducting autopsies

– that there is a change over weeks in the short

- term irritant effects. One way

that this will impact the calculations is that cumulative exposure is probably not the appropriate exposure metric. The authors may have little choice to use the simplified approach they

have taken which assumes a constant exposure

- response relationship over time, but they could acknowledge that there is a source of uncertainty from the changes in potency of formaldehyde over time for various endpoints. Isuspe ct that the irritant effects diminish with time exposed, but the other two chosen endpoints probably do not. EPA has added some discussion of acclimatization.

**Frederick J. Miller, Ph.D., Fellow ATS**  The draft Approach Document adequatel y discussed the type of data available in the

literature from various studies and presented their strengths and weaknesses. The Agency wisely stayed away

from using the Liu et al. (1991) study as the primary

driver for the concentration

- response function for ey e irritation. T he categories from that study were formed on using a ppm

- hr per week metric. The eye irritation studies discussed in Section 2.1.2 for a 10 % additional risk for 560 ppb for 3 hours (i.e., 1,680 ppm

- hrs) compared to 240 ppb for 5 hours (i.e., 1,200 ppm

- hrs ) clearl y s how that Haber’s Law does not apply for the effects of formaldeh yde exposure on ey e irritation, which agrees with Miller et al. (Haber’s rule: a special case in a family of curves relating concentration and duration of exposure to a fixed level of response for a given endpoint. Toxicology 149:21

– 34, 2000). Thus, the Agency

would have been hard pressed to defend a translation of the ppm

- hrs metric of Liu et al. (1991) as the basis for developing a concentration

- response function for eye irritation

. No response required.5 Rather, the Hanrahan et al. (1984) study that reported ey e irritation was associated with in

home formaldeh yd e exposures ( p < 0.05) (both as “burning ey es” and “ey e irritation”) was used as the data for developing a concentration

- response relationship f or eye irritation. Moreover, the logistic regression model developed by Hanrahan et al. (1984) gave insight as to the needed nature of the curve if one were to extrapolate below the range of exposures reported b y those authors (i.e., from 100 to 800 ppb). In the opinion of this reviewer, the concentration

- response function was appropriately derived by

the Agency

. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  First, I will comment on each study and then on the derivation process.

**Liu et al (1991):** This paper adequatel y describes how homes were randomly selected, but omits some key

information related to monitoring results for the homes included. The study was conducted throughout California (p. 93); a very large state with a wide range of climatic conditions. “Summer” and “winter” sampling periods were used, but these seasons are quite different in different parts of the state. It is well

- known that temperature and relative humidity

affect formaldehyde (HCHO) levels, but there is no mention of ho w these factors varied in the study homes or how they

may have affected measured HCHO levels. Further, the Qualit y Assurance/Quality Control methods are not described, and the number of laboratories used to analyze the passive area monitoring samples is n ot stated. These omissions leave this reviewer without key information to assess the accuracy or validity

of the HCHO levels reported. Residents received instructions on how to uncap, place and mail back the samplers. The use of the kitchen and master bedroom as monitoring sites may be most relevant for the homeowner and less relevant for other occupants. Although averaging the monitored levels for each home may

have lost some useful variation, it is not likely that in fairly

small homes (such as mobi le homes) that this loss

– except for peak exposures

– would be particularl y important. The study appropriately

controls the impact of smoking indoors, and does not discuss gas cooking stoves or appliances, opening of windows and doors, or other factors that have been reported b y other authors as having non

- significant impacts on HCHO levels.6 More importantly , if I am reading the article correctly (p. 92), some indoor samples in this cross - sectional study

were taken after s ymptoms were recorded. This conflicts with determining the appropriate temporal sequence of cause preceding effect. I believe m y reading is different from what EPA states on p. 10 of their draft, which indicates that exposures were recorded in a period preceding the documentation o f s ymptoms. **Hanrahan et al (1984):** This cross

- sectional study , conducted in Wisconsin during July 1979, sampled a smaller number of mobile homes (65) than did L iu et al.; it also had a lower percentage of participants among those contacted (31% vs. 44%). In this study , personal samplers were used and 33 outdoor samples were taken (at least 1 in each mobile home park). The authors noted that prior to and during sampling periods home windows were closed, gas appliances were turned off and smoking was proh ibited. The Quality

Control and specific laboratory methods were noted (unlike in Liu et al). The indoor samples for each home were averaged, as in L iu et al, with similar but less specific sampling locations noted. It is not clear whether the residents or the researchers collected the air samples in this study

. Smoking was appropriately considered, and indoor and outdoor temperature and humidity , and appliance and construction characteristics were noted. Some but not all of these factors’ influenc es on HCHO levels were presented in the article. **Derivation:** The seasonal and cumulative averages and ranges of indoor levels, the concentration

- response data are correctl y extracted from the **Liu et al.** article. The method to estimate the average number of hours indoors seems appropriate; however, this reviewer wonders whether EPA attempted to determine whether the authors still have the raw data that could be used for a more accurate assessment of hours spent indoors. EPA had to make man y more adjustme nts when using the **Hanrahan et al.** article. First, EPA estimated the lower bound for the indoor levels based on the standard deviation for the outdoor levels; this is a reasonable approach given the missing data for the indoor levels. Second, the Agency assumed that the distribution of indoor levels is log

- normal in order to estimate the number of samples with HCHO levels below 100 and 50 ppb. However, if this assumption or the estimated standard deviation is not correct, the numbers of samples could EPA has corrected this.

No, EPA used solely what was presented in the paper.

EPA has added additional discussion about the distributional assumption.7 be quite different. It is not clear in Figure 2 whether the data shown are for EPA’s or the authors’ use of “ey e irritation;” e.g., does “eye irritation” here mean the “burning eyes” AND “ey e irritation” results in the article? I f combined data were used, did EPA assume that all of these sy mptoms were distinct and not co

- occurring events? Are we looking at data for the number of s ymptoms reported or the number of people with ey e sy mptoms (meaning “burning ey es” and “ey e irritation”) at each level of expos ure? This question should also be asked of the data shown in the draft Table 1. Without knowing whether EPA combined data in Figure 2 and Table 1, it is difficult to comment further on this part of the draft. The conversion of data in the article to pre valence odds seems appropriate. The display of estimates below 150 ppb in Figure 4b are derived from Equation 2

- 2 and are likely correct. This reviewer did not verify the mathematics. The EPA authors have noted many key uncertainties in the two studies and how these affect their estimates of the relational function. However, the validity of the HCHO monitored levels remains a question, due to missing information in the articles; exposure misclassification is possible in both studies but is not discusse d in the draft. EPA has clarified that the results in Fig. 2 are for “burning ey es” only but that EPA is using this endpoint to represent eye irritation more broadly

.

EPA has added more discussion about the uncertainties associated with exposure sampling in these studies. **CHARGE QUESTION 2: Please comment**  **on the validity of extrapolating the concentration**
**- response function and using the**  **function to estimate effects at concentrations below 100 ppb. NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  Given the limitations of the data available from the Hanrahan paper, the method of

derivation of the CRF including the portion of the curve below 100 ppb is appropriate, but the extrapolation is pushing the envelope of what reasonabl y can be extracted from the data. The assumption that the reported standard deviation of the outdoor formaldehyde measurement s represents the lower bound on the standard deviation of the indoor concentration s appears reasonable, but nonetheless the distribution of exposure data below 100 ppb in the Hanrahan study was assumed rather than based on the actual data. The EPA used the graphical display of the regression data over the range of 100

- 800 ppb in the Hanrahan paper to derive a CRF and then to infer the shape of the CRF bel ow 100 ppb

. EPA has added some discussion of the short

- term sampling used b y Hanrahan et al. to the uncertainties section (Section 2.1.4). EPA notes that the L iu et al.8 Given that the Hanrahan study onl y included 61 subjects and that the formaldeh yde measurements in the mobile homes were onl y for 30

- 60 minutes, the validity of the extrapolated CRF can be questioned even if an appropriate method was used. study , which used 7

- day sampling is supportive of the Hanrahan et al. results **David Kriebel, Sc.D.**  I am comfortable with this extrapolation. However , I think that it would be appropriate to

acknowledge that errors in exposure estimation in the studies on which the function is based have not been included in the uncertainty calculations. This is a general concern

– for all 3 endpoints, there were certainly errors in the exposure estimation, and the impact of these on the uncertaint y in the exposure

- response function has not been considered. It might be noted that the extrapolation downwards assumes a logis tic shape, which is reasonable but not subject to validation. It might be noted that the excellent R2 for Figure 3b is a bit misleading since it is fitting a curve to categorical data, while the actual individual exposure data were of course continuous

– the fit of this curve to the original data would not have been nearl y as good. And again, see my comment just above about failure to point out that the exposure data had error , which was not taken into consideration in the model error calculations. EPA has added discussion of exposure measurement error. EPA has clarified that the point of the R2 value was to compare EPA’s attempt to recreate Hanrahan et al.’s model to the discrete model predictions (not categorical data) presented b y Hanrahan et al. **Freder ick J. Miller,**  **Ph.D., Fellow ATS** The Agency appropriately

focused on the data from the Hanrahan et al. (1984) study to develop the concentration

- response curve for eye irritation. Importantly , the Agency used a power law curve to fit the prevalence odds data. This ensures that the fitted curve will asy mptoticall y approach zero for a zero formaldehyde exposure level and makes it reasonable to use Equation 2.2 below 100 ppb. Given (1) the limit of detection (L OD) was 10 ppb at the time the Hanrahan et al. (19 84) study was conducted, (2) the Agency ’s assumption about the outdoor standard deviation of measurements being 30 ppb around a log

- normal distribution of measurements, and (3) the known overall shape of the concentration

- response curve below 100 ppb, this reviewer believes it would be reasonable for the Agency

to use the fitted equation down to a level of about 40 ppb, which would correspond to the LOD plus one standard deviation. Given the general support from the other reviewers, the absence of alternati ve response estimates for residential exposures below 40 ppb, and the difficulties in rationalizing a cut

off based on an9 unreported LOD and an estimate for the SD that was presented for illustrative purposes only , EPA has decided against using 40 ppb as a cut

- off for the model below 100 ppb. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  The validity of the extrapolation in the Hanrahan et al. paper depends in part on what data were used for the outcome measure. If “burning eye” AND “ey e irritation” data were combined, m ore information is needed in the draft to describe what assumptions were made in the combining process. (See comments above.) The validity

of the estimates below 100 ppb based on the Hanrahan et al. data is strengthened b y their alignment with the results in the L iu et al. study

. However, clearer discussion of the Agency ’s choice of and uncertainties in the points of departure would improve this portion of the draft. EPA has clarified that only “burning eyes” was modeled.

EPA has added discuss ion about uncertainties in the data and in the derivation of the exposure - response relationship. For the purposes of this document, the exposure - response relationships are used to estimate risks at exposure levels of interest. This methodology10 does not i nvolve points of departure. **CHARGE QUESTION 3: The studies considered for the concentration** 
**- response function are residential studies because residential**  **exposures are the focus of the rule and the residential studies avoid some of the limitations of other types of studies (e.g., controlled**  **exposure chamber studies used high, acute exposures, and occupational studies reflect high exposure levels and potential dose**
**- rate**  **effects from peak exposures). Are there other studies (e.g., chamber or non**
**- residen**  **tial studies) that should be used as supporting evidence for the currently derived concentration** 
**- response function for eye irritation? If so, please provide information about the**  **studies and discuss how they should be used to support the concentration**
**- res**  **ponse function. NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  I do not know of other studies that would be better to use for derivation of a CRF for

formaldeh yde exposure and sensory irritation given the EPA’s interest in chronic, low

level, non

- peak exposures. No response required. **David Kriebel, Sc.D.**  I think you should use the other studies

– particularly the chamber studies and the autops y studies

– to show the consistency of the findings across many settings. I am comfortable with the argument that the function should be derived from the residential studies. But I think that the logic of extrapolating downwards is supported by some of the other studies. Kriebel et al

. Arch Env Hlth 2001; 56:11

- 18 contains fairly detailed exposure data linked to eye irritation scores. While much of the data are above the range you are concerned with, there is evidence here that the relationship observed was valid across the full range of exposures. EPA has added some discussion of non - residential studies and has cited the Kriebel et al. (2001) stud y.

**Frederick J. Mill er,**  **Ph.D., Fellow ATS** Be yond the studies considered b y EPA, this reviewer knows of no chamber or

epidemiology

studies that would be useful in developing the concentration

- response function for eye irritation. Given the definition of an inhalation RfC and the focus on extended periods of exposure, the residential studies were conducted in a manner that best fits the criteria for developing a RfC and using it in the benefits analyses that the Agency is being required to conduct. No response required.

**Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  I am not aware of an y other studies that should be considered for this function. No response required. **CHARGE QUESTION 4: Are there other sensory irritation endpoints besides eye irritation for which a concentration** 
**- response**  **functi on can and should be developed for assessing effects at concentrations below 100 ppb? If so, please provide references of**  **appropriate studies and a description of how the studies could be used to develop a concentration**
**- response function.**  **NAME COMMENT**  **RESPONSE John R. Balmes,**  I do not know whether a CRF can be developed for other sensory irritation endpoints. No response11

**M.D.** required. **David Kriebel, Sc.D.**  Both nose and throat irritation can be linked to increased risk of lower respiratory tract infection including bronchitis. So you could argue that these would have greater economic impacts. Without data linking the effects or linking formaldeh yde exposure directly to RTI s, EPA cannot develop exposure - response functions for those effects. In addition, there are other effects for which EPA has hazard data but for which exposure

response functions could not be derived and, hence, for which no benefits could be calculated. **Frederick J. Miller, Ph.D., Fellow ATS**  Sensory irritation may

be indirectly

reflected in pulmonary

function responses measured after exposure to formaldehyde. However, these studies were not conducted at levels that would be relevant to what the Agency is being charged with investigating. There are studies linking formaldeh yde exposure directly to decreased pulmonary function (e.g., Krzy zanowski et al., 1985); however this effect could not be linked to specific economic12 costs and, hence, was not included in the Approach document. EPA has added text to this effect in the introduction. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  I agree with EPA and NAS that ey e irritation is the most sensitive sensory irritation

endpoint and therefore is the most appropri ate endpoint to use. No response required. **CHARGE QUESTION 5 :**  **Several studies of the association between formaldehyde and asthma have been published and these were quantitatively summarized in a meta** 
**- analysis by McGwin et al. (2010).**  **Please comment on whether the McGwin et al. (2010) meta**
**- analysis is an appropriate summary of the association between**  **formaldehyde inhalation exposures and childhood asthma. NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  The McGwin et al. (2010) meta

- anal ys is of the association between formaldehyde exposure

and risk of asthma in childhood appears to have been well conducted, using state

- of

- the

- art methods, including both fixed and random effects models and various sensitivity anal ys es. Because the meta

- anal ys is was based on a sy stematic review of the literature that appears to have been comprehensive, the results can be considered an appropriate summary of what is known about the association from epidemiological studies. No response required.

**David Kriebel, Sc.D.**  I agree that it is appropriate. No response required. **Frederick J. Miller, Ph.D., Fellow ATS**  There are man y problems with the studies used in the meta anal ys is conducted by M cGwin et al. (2010). Relative to the description of the metal anal ys is, the Agency d id a reasonable job of pointing out many o f the strengths and weakness that McGwin and colleagues noted in their paper, but this description could be improved.

There are various inconsistencies in the studies selected for the meta analy sis that would make this reviewer reticent to put much trust in the findings for applicability t o the U.S. population. First, onl y one study w as conducted in the U. S. and that study d id not fi nd a statistically

significant odds ratio (OR) with exposures being in the range of 30 to 80 μg/m 3 EPA notes that other reviewers stated that the meta

- anal ys is was appropriatel y conducted. The meta

- anal ys is was based on available studies of which most were13 of formaldehyde. Moreover, the sample size of the U.S. study w as greater than that of 5 of the other studies contained in Table 1 of McGwin et al. (2010).
A Swedish study

w ith exposures no greater than 10 μg/m 3 had an OR more than twice that of an y other stud y even though several of those studies involved formaldehyde exposures in the 5 to 70 μg/m 3 range, including another Swedish study

. The Zh ao et al. (2008 ) study results are inconceivable to this reviewer for inclusion in a reliable meta analy sis. With school exposures (1 to 5 μg/m 3 ) and outdoor exposures (5 to 7 μg/m 3 ), mean OR estimates were found to represent decreased risk, yet the upper bound of the 95 % confidence interval was 17 for the school OR and more than 2.3 million for the outdoor OR for the same set of 1,993 children having a mean age of 12.8 years.

McGowan et al. (2010) state that to evaluate whether the results they f ound were undul y influenced by

any i ndividual study

and to determine if there was any p ublication bias, an influence plot and a funnel plot, respectivel y were used. However, they did not present these plots in their paper. The computed values of the Q and I2 statistics we re stated to support the presence of moderate between

- study heterogeneit y. The EPA document cites values for these statistics but does not explain how they are calculated, but should do so. Q (better known as Cochran’s Q) is a classical measure of heteroge neity and is calculated as the weighted sum of squared differences between individual study e ffects and the pooled effect across studies, with the weights being those used in the pooling method. Q is distributed as a chi

- square statistic with k (number of studies) minus 1 degrees of freedom (d.f.). The I 2 statistic describes the percentage of variation across studies that is due to heterogeneity

rather than chance and is computed as 100* (Q

– d.f.)/Q. On page 18 of the EPA document, the overall OR for a fixed effects model is given as 1.026 but on page 20 the same result is stated as an OR of 1.03. The Agency n eeds to be consistent. If the data are only sufficient to give an OR with 2 digits after the d ecimal point, conducted outside the U.S.
In clusion criteria were not conditional upon the findings. EPA has clarified that the confidence intervals for the Zhao et al. study are so large that the study has virtually no weight in the meta

anal ys is; thus, its inclusion is inconsequential. EPA has added descriptions of the Q and I 2 statistics.

EPA has addressed this discrepancy

in14 say s o and change the value on page 18 and vice versa. For the reader to better judge the reasonableness of the meta anal ys is results, the EPA document should include Table 1 of the McGwin et al. (2010) paper in addition to Figure 1 from that paper. reporting of decimal places. EPA has added McGwin et al.’s Table 1. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  The authors clearl y built on well

- accepted guidelines for s ys tematic meta

- analy sis (Stroup

et al., 2000). The study s e lection/exclusion criteria and process used b y M cGwin et al. is well

- documented in their article. The variables extracted and utilized are stated. The determination to use a consistent metric (odds ratio per 10 μg/m 3 with the related 95% confidence inter

val) across the 7 studies for which actual HCHO measurements were available is appropriate. The methods used to pool the odds ratios and test for heterogeneity

are standard anal yt ic approaches. Their evaluation of the potentially undue influence of an y o ne study , using influence and funnel plots, adds strength to their anal ys is. The results are shown with and without Rumchev et al., allowing the reader to judge whether this paper should have been included or not. The data in Table 2 indicate that the ma gnitude of the HCHO effect on asthma prevalence is significant whether this study is included or not. The presentation of the Q and I 2 statistics guides the reader to the key results for interpreting the data in this table. In summary , this reviewer find s that the McGwin et al. meta

- analy sis is an appropriate summary and sy nthesis of the eligible studies reporting a quantitative relationship between HCHO and prevalence of childhood asthma. No response required.

**CHARGE QUESTION 6: Please comment on whethe** **r EPA chose the appropriate function from the McGwin et al. paper to use in the benefits assessment.**  **NAME COMMENT**  **RESPONSE John R. Balmes,**  **M.D.** Exponentiating the linear slope of the fixed effects model from the McGwin et al

. paper is

appropriate, especially

given that the random effects model gave essentiall y the same pooled odds ratio. No response required. **David Kriebel, Sc.D.**  I am comfortable with the choice to exclude Rumchev, and agree with the derivation of the

function as described. No response required. **Frederick J. Miller, Ph.D., Fellow ATS**  The EPA document does not specifically s tate which model result (i.e. fixed effects or random effects) was selected. Rather they s tate that the mean OR was 1.24 per 10 ug formaldeh yde per m 3 for both models. One only d etermines that the Agency c hose to use the random effects model if one calculates the transformed 95 % confidence interval for an OR for an increase of 1 ppb and sees that what is stated on page 18 corresponds to the confidence interval for the random effects model. EPA has clarified that it selected the rando m - effects model and has provided a rationale for this15 The lack of significant between

- study h eterogeneity

i n the meta anal ys is of McGwin et al. (2010) supports using a fixed effects model; however, the extent of the uncertainties among the studies an d the fact that the random effects confidence interval will alway s be larger than the fixed effects confidence interval supports the conservative selection by the Agency to use the random effects model results.
In view of the additional problems this revi ewer discussed earlier concerning the choice of studies for inclusion in the meta anal ys is, this reviewer would be reticent to have the benefits assessment use only o ne function (i.e., the OR of 1.03 per one ppb increase in formaldeh yde exposure with a 95 % confidence interval from 1.008 to 1.047). The single U.S. study

s hould also be evaluated wherein the OR is 1.0083 per 1 ppb increase in formaldeh yde exposure with a 95 % confidence interval of 0.97 to 1.045. selection.

The single U.S. study did not adjust for other factors while the remainder of studies did, and EPA considered the identified meta

- anal yt ic result to be more robust that that of a single stud y. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  The Agency has chosen the appropriate function from the McGwin et al. paper. With the exception of the discussion of the rationale for excluding Rumchev et al., however, more insightful comments about the strengths of the meta

- anal ys is would lend greater support to the Agency ’s use of and reliance on the fixed

- effects model’s OR=1.24. Deepening the discussion would improve the support for the Agency ’s conclusions and recommendation. For example, McGwin et al. stated that an I2 value of <50% would point to relying on the fixed

- effect results (p. 314). Although the Agency uses the fixed

- effect modeling results, correctly stating that the Q and I2 data indicate low heterogeneity , the draft does not include the key cut

- point (I 2 <50%) for the use of fixed

- vs. random

- effect modeling results. In this rev iewer’s opinion, pointing the reader explicitly to this cut

- point and the relevant data in McGwin et al.’s Table 2 would sharpen the Agency’s rationale for choosing the fixed

- effect results The discussion of uncertainties in this section includes the key issues (such as the changes in definition and determination of “asthma” over time) and is appropriatel y written. EPA has clarified that it selected the random

- effects model and has provided a rationale for this selection16

**C HARGE QUESTION 7**  **: The literature base describing reproductive effects of formaldehyde exposure in humans is limited;**  **however, there are supportive findings from the animal toxicological literature. The epidemiologic literature suggests an as sociation**  **between formaldehyde a nd increased risk of spontaneous abortion and a related delay in time to pregnancy (i.e., reduced fertility).**  **The only study with quantitative concentration**
**- response data was Taskinen et al. (1999).**  **The a priori**  **hypothesis in Taskinen et al. (1999) was t hat formaldehyde would be associated with decreased fertility. The primary**  **analyses showed that there was a statistically significant reduction of fertility among the women in the highest exposure gro up that**  **appeared to be concentration dependent. Post**
**- h**  **oc subgroup analyses showed that stratification of the 39 women in the highest exposure group by reported glove use yielded effect estimates whose confidence intervals overlapped. The FDR for the 17 wome** **n who were classified as not wearing gloves was 0.51**  **[95% CI: 0.28 −0.92]. The FDR for women who were classified as always or**  **sometimes wearing gloves was 0.79 [95% CI: 0.47 −1.23].**  **In light of the results regarding glove use, in what way(s) can the Taskinen et al. results be used to support calculating a**  **concentration response for formaldehyde inhalation risk to time to pregnancy? NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  The results of the stratified anal ys is regarding glove use are suggestive of the possibility

that the dermal route may contribute to total exposure, but are not adequate to consider modification of a CRF for decreased fertility based on inhalational exposures, especially given the small size of the two strata and the wide confidence intervals of the FDR p oint estimates. No response required.

**David Kriebel, Sc.D.**  Yes, but you could strengthen your argument. First, there is a trend in both FDR and

spontaneous abortion across levels of formaldeh yde, so you should not only focus on the effect modification b y glove use in the high exposure group. While the high exposur e is the only group for which the authors provided the results stratified by glove use, the fact that there is a trend across air concentrations suggests that glove use

– not constant across exposure levels

– could not be a very important source of protect ion or you would not see the trend. Second, you have not correctl y dealt with the question of whether or not there is effect modification b y glove use. The overlap of confidence intervals is not the correct way to do this. Construct the null hy pothesis that glove users and non

- users have the same FDR and then calculate a p

- value testing this null. You can do it with the data provided

– back calculate the standard errors from the confidence intervals, or ask the authors for the standard errors. I am pretty s ure that this p

- value will be large, and then yo u will be in a strong position to say

that the appropriate conclusion is to act as if glove use has not modified the FDR. A p

- value calculation has been added.17

**Frederick J. Miller, Ph.D., Fellow ATS**  The res ults after stratifying for glove use are indirectly supportive for an inhalation effect of formaldeh yde on the fecundity density ratio (FDR). Those women who did not wear gloves had a statistically

significantly

decreased FDR of 0.51 (i.e., 95 % confidence interval did not include 1). Women classified as alway s or sometimes wearing gloves had a FDR closer to 1 and their confidence interval included 1. Thus, the inclusion of women wearing gloves would tend to move the overall FDR closer to 1, where FDR value s lower than 1 can be interpreted as an adverse effect in that the time to achieve conception is delayed. This was indeed the case since a FDR of 0.64 was found for all women in the highest exposure group. This provides evidence in support of the hypothesi s that effects on FDR were most likely due to inhalation exposure rather than to dermal exposure to formaldehyde. No response required.

**Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  The article (p. 208) is not clear as to whether the post

- hoc anal ys is was adjusted for th e

variables noted in the footnote of Table VI; if not, the post

- hoc results would not be directl y comparable to the data presented there. That said, the reported post

- hoc high exposure group glove/not odds ratios and confidence intervals expand and are co nsistent with the trend shown in Table VI. However, all of the confidence intervals overlap each other, yi elding a set of non

- significant odds ratios. If the adjusted post

- hoc odds ratios are available, it would be interesting to see the results of a tes t for trends comparing high exposure - gloves not used, high exposure

- gloves used, medium exposure, and low exposure. The trend probably

is not significant, but testing its significance may offer more information for interpreting the concentration

- response relationship. EPA has included a test for heterogeneity across the strata of reported glove use in the highest exposure group, which yielded the result that the ORs for the glove

- use subgroups are not significantl y different **C HARGE QUESTION 8**  **: Please comment on whether the concentration** 
**- response function is appropriately derived from the**  **Taskinen et al. (1999) study. NAME**  **COMMENT RESPONSE**  **John R. Balmes, M.D.**  The CRF for formaldeh yde exposure and decreased fertility appears to be appropriatel y derived from the Taskinen et al. (1999) study. The adjustment for probable exposure to formaldeh yde outside of the workplace is appropriate given the interest of the EPA in potentially controlling indoor exposures due to off

- gassing from certain products. The use of reasonably

contemporaneous background exposure data from Finland (Jurvelin et al., 2001) for this adjustment is also appropriate. No response required.

**David Kriebel, Sc.D.**  Can’t you ask Taskinen to confirm your (and my) assumption that age was the conditioning

time variable in their FDR calculations? EPA did not receive a response18 The process of adjusting for background exposure is OK, but Idon’t think it strengthens the presentation. First, I doubt very much that the relevant background formaldehyde exposure for the women in this plant could have been so much higher than the levels inside the plant. My guess is that the mean (one mean for an entire country over a long period of time? How useful is that?) had a wide range around it. Second, any of m y graduate students could have told you that adding a constant to all the x values in a regression model will not change the slope. from the author. As noted, the standard practice is to condition on age. EPA has clarified the discussion of the adjustment for “non

- work

- station” exposure, which apparentl y was mis

- understood by this reviewer. **Frederick J. Miller, Ph.D., Fellow ATS**  A concentration

- response function can be derived from the Taskinen et al. (1999) study ,

and the selected function must be one for which there was an adjustment for background exposure levels; however, the EPA document does not actually s tate whether they

w ill use the linear function of risk or the exponential function of risk equations that are discussed in the document (i.e. will the Agency use Eq. 2

- 5 or 2

- 6?). The two curves presented in Figures 6 and 7 of the Agency d ocument are not explained either in the figure legend or in the text. While they o bviously

r elate to the regression of risk on formaldeh yd e concentration, their difference is not explained. The Agency c learl y picked up on most of the criticisms provided by the NAS review of the draft IRI S d ocument related to the Taskinen et al. (1999) study

. However, the Agency ’s section on the discussion of uncertainties does not comment at all on the clear possibility of confounding due to xylene exposures in the Finnish worker study

. Also, there is no dis cussion of the possible magnitude or direction of any e xposure misclassification bias in the Taskinen et al. (1999) study

. If the Agency i s going to use the Taskinen et al. (1999) study i n their economic anal ys is, more attention to a description and discus sion of the study ’s strengths and weaknesses is needed. EPA has clarified that the linear function is preferred.

EPA has clarified the text, and now only one figure is presented. EPA has expanded the uncertainties discussion regarding the Taskinen et a l. study to address these and other issues. **Rebecca T.**  **Pa rkin,**  Exposure measurements were available onl y for the middle of the study period, but the19

**Ph.D. , MPH**  authors were able to verify “most” women’s self

- reported exposure levels based on data from the ir workplaces. The article does not state whether this verification was completed to the same extent across the entire study period. This reviewer also wonders whether for some women (outside of the undefined “most”) the authors assumed that self

- reporte d HCHO exposure levels were accurate and did not change during the study period. The Agency draft notes general exposure measurement concerns and agrees with Taskinen et al. regarding their modest response rate to the mailed questionnaire. Although Taskinen et al. note that reporting biases may be present in their study , they did not report an y evaluation of their data to address that concern. For example, the response rates for women with pregnancies in the 1985

- 90 vs. 1991

- 95 periods were quite di fferent. Although the authors note that “ onl y a few women could not report the length of time to pregnancy ,” they

do not indicate whether more women in the earlier vs. later period were non - reporters. Also, there is no mention to what extent the authors believe the recall of the number of months

- to

- pregnancy was accuratel y recalled b y either group of women. Neither Taskinen et al. nor EPA adequately discuss whether self

- reported time

- to

pregnancy

(or spontaneous abortion) data are reliable for use as an outcome measure. If outcome misclassification is an issue as well as exposure misclassification, the odds ratios could be further compromised toward the null. Discussion of the reliability of self

- reported outcome data should be considered for the next draft. The Agency ’s adjustment for non

- occupational HCHO exposures, based on contemporaneous data, shifts the relationship to the right (from Figure 6 to Figure 7) but does not consider the variation in exposure levels found by Jurvelin et al. The draft a ssumes that all of the women in the study had the same non

- occupational HCHO exposures. Considering the range, not just the mean, of Jurvelin et al.’s measurements would be more informative and would allow for the identification of upper and lower bounds on the concentration

- response relationship. EPA has added some discussion about errors in outcome reporting.

For the purposes of this document, EPA was primaril y concerned with “best estimates” for the exposure

response relationships **III. SPECIFIC OBSERVATIONS ON THE DOCUMENT**  **NAME COMMENT**  **RESPONSE John R. Balmes,**  **M.D. Page 10, 1**  **st full paragraph; page 14, figure 4a legend; page 15, 2**  **nd full paragraph.**  The

use of “inhalation” exposure in the context of eye irritation seems inappropriate. I would eliminate the use of “inhalation” in all three sentences. EPA has eliminated the use of the word20 **Page 16, paragraph. 2.2.1.** Asthma is defined b y the Global Initiative for Asthma (GINA) as a disease characterized by inflammation of the airway s, not lungs. I would e liminate “and lungs” in the first sentence of this paragraph. To avoid confusion, I would not use “sensitization” when discussing non

- allergic, neurogenic mechanisms of irritant chemical

induced asthma in the third sentence. **Page 20, paragraph 2.3.1.** “Increased relative risk estimates (RRs) were in the range of 1.7 to more than 3.0.” To avoid confusion, I would cite the specific papers that reported these increased relative risks. **Page 22, last sentence of text.** The text here refers to “estimated conce ntration

- response functions” but does not explain why there is more than one CRF in Figure 6. It is not until page 24 that one learns that “Regression equations for linear and exponential fits are also provided.” If the two lines in Figures 6 and 7 are f or both ty pes of fits then this should be clearl y indicated.
**Page 26, last full sentence.** The use of a contraction here (“didn’t”) is unprofessional. “inhalation” in the context of exposures resulting in eye irritation. EPA has made these revisions to the first paragraph on asthma.

These studies are cited.

EPA has added a sentence identifying the use of both models before the figure appears. EPA has changed “didn’t” to “did not”. **David Kriebel, Sc.D.**  **Page 20, s**  **ection 2.3.1, 6 th**  **and 7 th**  **lines.** The statement “Increased relative risk estimates

(RRs) were in the range of 1.7 to more than 3.0” is not helpful

– without explaining whose risk is being compared to whose, the absolute value of an RR is not useful.
**Sec tion 2.0 Background on the Identification of Non** 
**- Cancer Health Effects, last**  **sentence.** It would be helpful to summarize at least briefly the logic behind focusing on these 3 endpoints. If I have understood the NAS comments correctl y, that Committee also ra ised questions about these choices, and in particular on the decision not to use pulmonary function evidence. Given this concern from the NAS, Ithink a bit more explanation of the EPA has clarified this.
EPA has expanded its discussion of endpoint selection and specifically stated wh y21 perceived inadequacies in the data for the other endpoints would strengthen this document. pulmonary function data were not used. **Frederick J. Miller, Ph.D., Fellow ATS**  None. No response required. **Rebecca T.**  **Pa rkin,**  **Ph.D. , MPH**  Eye Irritation

**Page 10, last paragraph, line 4 and Figure 2, line 2.** The EPA draft states that these samples were taken from 30

- 60 minutes, but the authors only mention pumps running “for approximately

one hour” (p. 1026). Does EPA have info rmation in addition to what is in the article or is the 30

- minutes an error? **Pages 11**
**- 12.**  Figure 2 in the draft has a more detailed caption, but otherwise seems to be exactly the same as the one in the Hanrahan et al. paper (which is data for “burning eyes”); is it the same as in the paper? If so, shouldn’t it clearl y indicate that it is “burning eye” data?
**Page 12.** Table 1 may

need a clearer caption indicating whether the data shown are for “burning ey es” AND “eye irritation” or “eye irritation” alone. Wherever combined data are used, EPA should clarify this usage and possibly create a new name for combined eye sy mptom data. Further, the title of Table 1 would be more accurate if it included “...extracted and calculated from...” Asthma **Page 16, last paragraph, last 2 lines and top of page 1.**  The descriptive language in the Agency draft about using the McGwin et al.’s I2 statistic would be stronger if made more specific; e.g., noting that McGwin et al. used a cut

- point of <50% for choosing fixed

- vs. random

- effects data (page 314, top of middle column). It appears that EPA agreed with this cut

- point.
**Page 18, first complete paragraph, line 6.** The Agency states that the I2 statistic is 11.2 EPA has corrected this.

EPA has re

- titled the figure to indicate that the data are for “burning ey es”.
Ta ble 1 presents data EPA extracted from Fig 2, which has been re

- titled to indicate that the data are for “burning ey es”. EPA selected the random

- effects model and has provided a rationale for this choice. This has been22 when the Rumchev et al. paper is excluded, but Tabl e 2 in McGwin et al. shows 11.3. Female Reproductive Toxicity **Page 22.** The title on Table 2 should state which “response” (TTP) is presented. corrected.
The response has been added to the title.23 **V I**  **. PEER REVIEWER COMMENT TABLE**  **ON THE BENEFITS ASSESSMENT APPROACH** 24 **I. GENERAL IMPRESSIONS NAME**  **COMMENT RESPONSE**  **G lenn C.**  **Blomquist, Ph.D.** Overall, the draft Approach Document is well

- written. Refreshingl y, Standard English

language is used extensively and technical terms introduced when necessary . Examples to explain terms such as odds ratio s should make the document understandable to educated lay readers with varied backgrounds. The key concentration

- response functions are clearl y presented in the form of equations and graphs or tables. This draft is readable. Information presented appear s to be accurate and representative of studies that are the source of the information. Brief descriptions of key studies are given in addition to the findings relevant to the topic of this draft Approach Document. The extensive list of references allows the reader to learn more about the studies from which crucial estimates are taken. Conclusions regarding concentration

- response functions and valuation (monetization) as reflected in their use in the examples follow from the information and models present ed in a logical and reasonable way . M y assessment of presentation applies to the entire document. My assessment of accuracy

and soundness applies mostly to Section 3 Benefits Assessment Approach because of m y background in environmental and health econom ics. No response required

**A. Myrick Freeman III, Ph.D.**  The general model for aggregating over time and across individuals that is outlined in

Section 3.1 is correct. For other “impressions,” see m y responses to specific charge questions below. No response required **Shelby Gerking, Ph.D.**  The report is, for the most part, complete and clearly written. I had no problem following the narrative, however, an executive summary , a conclusion and a map of the climate zones would have been helpful. Also, in Section 3, there are at least seven issues that warrant additional thought. First, the choice of the 3% discount rate, while not unreasonable, appears from out of nowhere. Some attention needs to be given to this choice as well as to the assumpt ion of exponential discounting. Other t yp es of discounting considered by behavioral economists may also be appropriate. Second, the contingent valuation estimates of WTP for ey e irritation are rather dated

— those obtained by

Tolley et al. are 25 ye ars old. EPA still uses these estimates, but there have been a number of advances over the ye ars in the application of stated pr eference methods aimed at reducing h ypothetical bias which causes stated preference estimates to be A map of climate zones was added.

A footnote was added justifying the 3% exponential discount rate.
An explicit point about the age of the Tolley

values and hy pothetical25 too high.
Third, the Dickie et al. estimates in Table J

- 10 may not be directl y comparable to those of Tolley et. al. and Loehman et. al. in that they ar e based on the averting behavior method (which looks at actual purchases of goods), rather than on contingent valuation. In any case, the narrative might usefully reflect the fact that sound willingness to pay estimates are elusive and that different methods of estimating WTP often give (very) different results. Fourth, both asthma and eye irritation estimates rely on transferring adult WTP estimates to children. This procedure, which may be the onl y available option, may well lead to substantial inac curacies. Parents, for example, may be WTP more to reduce health sy mptoms for their children than they are WTP to reduce those same s ymptoms for themselves. In an y case, the issue of WTP for adults vs. WTP for kids (with citations to recent literature) s hould be a discussion point in the report. Fifth, the WTP estimates presented implicitly assume that switching to different building materials, or treating wood products to cut down formaldehyde off

- gassing will not occur for the 30 ye ar horizon analyze d. Is this assumption reasonable?

In this same vein, could health effects from formaldehyde off

- gassing be lessened b y providing particularl y residents of new homes with information that would lead them to install better ventilation sy stems? I f so , the marginal cost of better ventilation (if such a strategy is appropriate) might then form the basis of a simple WTP estimate along the lines of the headache example given on p. 31. Sixth, the population by

housing t ype and climate zone apparentl y ar e assumed not to change over the next 30 years, even though there have been major changes in population by housing t ype and climate zone over the past 30 ye ars. This assumption seems hard to bias in CV studies has been added. EPA, but the Dickie et al. results in J

- 10 are not actuall y use d.
Recognition that parents may

be willing to pay more for children has been added.
Actually , benefits occur immediatel y. The 30 time horizon is only

to capture the benefits of the rule into the future. This is possible, but unnecessary given that we have stated preference WTP values. Whi le a static population and housing t ype is26 defend, although as noted on p. 42 it would be a difficult task to predict these movements.

Seventh, it would be helpful to develop the main features of the cohort x housing type x climate zone model in introductory Section 3.1. It would be helpful in this section to explain about the assumptions underlyin g this approach (some of these are identified above). This reorganization will clarify the narrative at a number of points and avoid misunderstandings created when readers simpl y encounter model assumptions in the explanation of results. hard to defend, at this time EPA is not able to predict changes in demographics at the required level of detail to assume something different. The document now includes this reorganization.

**II. RESPONSE TO CHARGE QUESTIONS CHARGE QUESTION 1:**  **The concentration**
**- response function for the prevalence of eye irritation is based on Hanrahan et al.**  **(1984). While Hanrahan does not identify the relevant time period for this relationship, Liu et al. (1991) produced qualitati vely**  **similar results for a two**
**- week time period. We assumed that the concentration** 
**- response relationship for eye irritation is for a two** 
**** **week period and multiplied the concentration**
**- response function times 26 to obtain the number of cases of eye irritation experienced**  **in one year. Th**  **e concentration**
**- response curve used is non** 
**- linear, which means that the annual approach may not produce an exact measure of**  **the benefits, but it is believed that the bias is probably relatively small given the small change in exposure. Please comment on w** **hether the concentration**
**- response function is used appropriately in the benefits assessment approach.**  **NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  The change in exposure expected from the policy appears to be small relative to ty pical exposure. It follows that the linear approximation implied by multiplication by

26 to obtain annual changes in number of cases of ey e irritation should produce onl y a small bias. It seems as reasonable as other approaches. No response required **A. Myrick Freeman** It was used appropriatel y. No response27

**III, Ph.D.**  required **Shelby Gerking, Ph.D.**  The non

- linear concentration response function is appropriatel y used in the benefits

assessment approach. However, the approach used here appears to take no account of other so urces of formaldeh yd e exposure , such as workplace exposures. In any case, the policy

related reductions in formaldehyde exposure should be treated as reductions in total exposure, not simply

reductions in home exposure. This refinement may alter the bene fits calculation given the use of a non

- linear concentration response function. EPA does account for other sources of exposure. The text has been amended to reflect this. **CHARGE QUESTION 2: The concentration** 
**- response curve is for an acute effect occurring**  **at a time less than the one**
**- year time**  **step of the exposure model. The willingness to pay to avoid cases of eye irritation is calculated for each year of analysis b y**  **multiplying the number of cases in a year by the marginal willingness to pay value to avoi d one case. This may produce biased**  **results, but the direction of that bias is unknown. On one hand, s**  **ome studies have suggested that the willingness to pay per symptom** 
**- day declines as the number of symptom** 
**- days**  **avoided increases. In other words, the valu e to reduce two symptom** 
**- days of some effect is less than two times the value for one**  **symptom -**  **day. Therefore, this approach may overstate the total value. On the other hand, this analysis only applies values to one symptom, eye irritation, largely because**  **this is the only symptom for which an effective concentration** 
**- response curve was derived. However, there is evidence that there are other forms of minor eye, nose, and**  **throat irritation associated with formaldehyde exposure. Since eye irritation is the la rgest of the median values from the Tolley et al.**  **(1986) study, the values used here likely represent a lower bound on the true effect of multiple symptoms. A reasonable upper bound**  **of the total effect for one symptom**
**- day would be sum of the willingness to**  **pay for one symptom**
**- day of each effect individually.**  **Please comment on whether the annualized approach as opposed to the lifetime approach is appropriate in this context. NAME**  **COMMENT RESPONSE**  **G lenn C.**  **Blomquist, Ph.D.** I admit to being confused by the statement that eye irritation has the largest of the median values in the Tolley

et al. (1986) study . (For full disclosure, I am one of et al.) Much of that study was published in Tolley , Kenkel, and Fabian Valuing Health for Policy (1994) particularl y in Chapter 4 by Kenkel, Berger, and me. In Table 4.3A on page 88, the median values for willingness to pay to avoid an additional sy mptom day

are $11 for coughing, $12.50 for ey e irritation, $13 for throat irritation, and $ 14 for sinus congestion. All three are similar, but eye irritation is not the largest. It will not make much difference, however, if either of the other two is used instead of $12.50 for ey e irritation. The statement that eye irritation is the largest median value is incorrect. EPA has corrected this in the text.28 Comparing results reported in Table 4.3A and Table 4.3B suggests that willingness to pay per s ymptom

- day

declines as the number of s ymptom day s avoided increases. For example, the median value for avoiding 30 s ymptom

- day s of ey e irritation is $100 which is less than 30 times $12.50 (or $375). This sugge sts that multiplying the $12.50 times the number of day s of ey e irritation avoided will bias the annual estimate for avoiding ey e irritation upwards if there are multiple day s for individuals. Declining marginal willingness to pay for avoided illnesses is also found in the recent study , Bosworth, Ryan, Trudy Ann Cameron, and J.R. DeShazo. “Demand for Environmental Policies to Improve Health: Evaluating Community

- Level Policy Scenarios” Journal of Environmental Economics and Management 57 (2009): 293

- 308. Table 4 also shows willingness to pay values for avoiding combinations of sy mptoms in a day . The willingness to pay values for avoiding combinations of sy mptoms in a day

are less than the sums of the willingness to pay values for avo iding the s ymptoms separatel y. The declining marginal value of adding another light s ymptom suggest that a reasonable upper bound of the annual value of the total effect for one s ymptom

- day would be the sum of the willingness to pay

for one s ymptom

- day

of each effect individually

. On page 34, the paragraph that begins with Tolley et al. (1986) is mostly correct. (I am a coauthor on that Tolley

report and the Berger et al. (1987) article.) It is correct, as stated, that the mean willingness to pay to rel ieve one s ymptom

- day of a light s ymptom was $25

- $50. It is mostly

correct, as stated, that Berger et al. report higher willingness to pay values for these same s ymptoms. The difference is due to different samples. The Tolley et al. values are based on a sample of 176 respondents, some of whom had experienced the sy mptoms and some of whom had not. The Berger et al. values are based on a subsample of 119 who actually

had experienced a s ymptom. The mean values for the subsample that had experienced the sy

mptoms are greater than for the full sample for five of the seven light sy mptoms, nearl y the same for one, and less for the remaining one. The mean value for eye irritation was $48.48 for the 16 who reported ey e irritation whereas the mean value was $27 .73 for all 176 who responded. The values reported are in 1984 dollars in both the Tolley et al. report and the Berger et al. article. The median value for eye irritation of $12.50 that Weitzel (1990) found is also reported in Tolley , Kenkel, and Fabian Valuing Health for Policy (1994) in Table 4.3 on page 88. It is correct that it too is in 1984 dollars. EPA has recognized in the uncertainties section and added the refer ence.

EPA has included this statement in the uncertainties section

Thank you for this clarification. EPA has revised the text accordingl y and added the reference. Since the Tolley , Kenkel, and Fabian is the primary reference to the median values, the reference to Witzel has been removed.29 On page 36, if the BLS Inflation Calculator is used to inflate the median value of $12.50 for eye irritation from 1984 dollars to 1999 dollars, the value is $20.03 as shown in Table J

- 10. If the same is done for 1984 to 2006, the value is $24.25, which rounds to $24, as reported below Table J

- 10. Two recent studies find that different lifetime risk profiles are valued differently; see Nielsen, J ytte Seested, Susan Chilton, Michael Jones

- Lee, and Hugh Metcalf. “How Would You L ike Your Gain in Life Expectancy to Be Provided? An Experimental Approach” Journal of Risk and Uncertainty 41 (December 2010): 195

- 218 and Cam eron, T.A., J.R. DeShazo, and P. Stiffler. “Demand for Health Risk Reductions: A Cross

- national Comparison between the U.S. and Canada” Journal of Risk and Uncertainty 41 (December 2010): 245

- 273. Given the limited information on the sy mptoms of interest it is not clear how incorporate these finding into the Approach Document

. No response required

These are interesting articles but EPA agrees that it is unclear how we would incorporate them.
**A. Myrick Freeman III, Ph.D.**  I don’t understand the question. What do you mean by the “lifetime approach”? If you mean the results shown in Table 3 on p. 42, then either approach is appropriate. They are just different way s of summarizing the data. Reference to the “lifetime approach” was designed to be contrasted with adding up benefit ye ar - by

- ye ar, described as the “annual approach” in the text. However, EPA agrees with the reviewer’s comment that they are just different way s of summarizing the data. **Shelby Gerking,** A search of the review document turned up no references to “life time approach”, so the Reference t o the30

**Ph.D.** issue to be addressed here is not entirely clear.

Nonetheless, it is likely

that WTP per sy

mptom day

of ey e irritation falls as the number of sy mptom day s increase. This outcome would be a general implication of utility maximization under a fixed budget. As additional resources are spent to relieve eye irritation, the opportunity cost of foregone consumption will increase. If eye irritation is coupled wi th other s ymptomatic discomforts, then we may have a different problem. On the one hand, suppose that there exists a good that will reduce ey e irritation together with all of the other s ymptoms. Then, the marginal cost (inclusive of both time and money) of using the good to reduce these sy mptoms will be the WTP for all combined. On the other hand, if more than one good needs to be purchased to reduce all of the s ymptoms, then the WTP would be the marginal cost of the combination of goods that will do the job. In an y case, it is problematic to simply add up CVM estimates of WTP for individual sy mptoms as this is likely

to yield a total WTP value that really is upward biased. Note that the CVM estimates themselves are probably upward biased. “lifetime approach” was designed to be contrasted with adding up benefit ye ar - by

- ye ar, described as the “annual approach” in the text. The text regarding diminishing marginal WTP and adding estimates has been revised in the uncertainties section.

**CHARGE QUESTION 3: The concentration** 
**- response function for the prevalence of eye irritation is for a single two** 
**- week period.**  **The annualized approach used an adjusted concentration**
**- response relationship that consisted in multiplying the concentration** 
**** **respo nse function obtained from Hanrahan et al. (1984) by 26 two** 
**- week periods.**  **Please comment on whether the adjustment of the concentration**
**- response function is appropriate in the annualized approach.**  **NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  It seems as reasonable as other possible approaches. No response required **A. Myrick Freeman III, Ph.D.**  Yes, it is appropriate. No response required31

**Shelby Gerking, Ph.D.**  An issue here is that there appear to be different way s to interpret the Total WTP

expression on p. 39. Should we assume that the same people experience eye irritation repeatedly

for each 26 two

- week periods in the ye ar? If this (Groundhog Day) assumptio n is correct, then the WTP value applied may well be on the high side. On the other hand, if we assume that a different set of people experience these sy mptoms in each of the two week periods, then the calculations presented may be more defensible. EPA has included this comment in the uncertainties section.
**CHARGE QUESTION 4: The concentration** 
**- response relationship for asthma incidence is given as an odds ratio for children**  **exposed to formaldehyde. An odds ratio is a way of comparing the difference in the probability of an event, in this case asthma**  **diagnosis, occurring in groups exposed at different levels. The odds ratio is used to determine the willingness to pay for an y change**  **in emissions exposure over a 16 year period. We assume that the probabili ty of being diagnosed with asthma is uniformly distributed**  **across these 16 years. The use of an odds ratio implies that the concentration** 
**- response relationship is non** 
**- linear. However, given that the change in**  **exposure is relatively small, the results fro m**  **using this implied non**
**- linear function are anticipated to be similar to the results if we**  **were to use a linear function. Please comment on whether the concentration** 
**- response function is used appropriately in the benefits assessment approach.**  **NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  It seems as reasonable as other possible approaches. No response required **A. Myrick Freeman III, Ph.D.**  It was used appropriatel y. No response required **Shelby Gerking, Ph.D.**  I agree that the bias from using the implied non

- linear function is likely to be small, but please see #1 in the eye irritation section for a possible qualification. EPA assumes that the reviewer is referring to the concern about accounting for other sources of exposure. EPA does account for these sources. The text has been32 amended to reflect this. **CHARGE QUESTION 5 :**  **The valuation of asthma effects from formaldehyde exposure is based on valuing the incidence of asthma rather than the more standard valuation based on the exacerbation of asth**  **ma symptoms. The reason for this is that a statistical relationship between formaldehyde exposure and asthma exacerbation has not been sufficiently well established, but there is a**  **statistical relationship between formaldehyde exposure and asthma occurrenc e or incidence. However, the only time that EPA has**  **valued asthma exacerbation is for the first prospective study of the benefits and costs of the Clean Air Act (EPA 1999). This is**  **probably due to a lack of an appropriate concentration**
**- response relationshi**  **p. The EPA’s Office of Air does include recommended values for the monetization of chronic asthma in its BenMAP documentation (EPA 2011b), which is based on an average of the**  **results from Blumenschein and Johannesson (1998) and O’Conor and Blomquist (1997)**
**. For this analysis, EPA treats prevalence as a measure of cumulative incidence by assuming that the disease duration is the re**  **st of the child’s life. However, the EPA (2000a) has previously assumed that a portion of asthmatic children will become asympto**  **matic as they move into adulthood.**  **Please comment on whether the annualized approach as opposed to the lifetime approach is appropriate in this context.**
**NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  The approach used seems reasonable except for ignoring that some of the asthmatic

children are likely

to become asy

mptomatic as adults. I f the incidence and prevalence data can support outgrowing asthma, then it should be incorporated in the estimates of valuing the incidence of asthma. Otherwise, the estimates will be biased upward.

I agree with the choice of the best estimate from O’Conor and Blomquist (1997) for the implied annual value of asthma control (page 47). It is $1,474 and is based on the risk

- risk tradeoff and the assumed value of st atistical life of roughl y $6 million. The $1,474 is close to the nonparametric estimates of $1,500 for the 5 unit change and $1,440 for the 10 unit change. It is also close to the parametric estimates assuming a value of statistical life of $6 million of $1,468 for Model 3 and $1,504 for Model 4. They are the more complete specifications of the drug choice logistic regression. Since survey s were done in 1995, the values are in 1995 dollars. The monet ization section has been revised to include the children who become asy mptomatic. The values have been updated to 2010 dollars.33 The implied annual value of asthma control of $1,474 in 1995 d ollars is also close to the best estimates from our more recent work; see Glenn C. Blomquist, Mark Dickie, and Richard M. O’Conor. “Willingness to Pay for Reducing Fatality

Risks and Asthma Sy mptoms: Values for Children and Adults of All Ages” Resource an d Energy Economics 33 (May 2011): 410

- 425. In this recent work, we are able to estimate the willingness to pay without assuming a value of statistical life. As Table 5 shows, for the ordered logistic regression for willingness to pay for the more effectiv e drug we have a larger sample for the preferred specification (263 in 2011 > 75 in 1997) and the ratio of the coefficient for efficacy in controlling asthma to its standard error is much larger (3.14 in 2011 > 0.70 in 1997). This facilitates estimation d irectly from the willingness to pay logit rather than indirectly from the risk

- risk logit and an assumed value of statistical life. We were also able to test for selection bias related to the choice of drug at the first stage of the hy brid contingent valu ation. (We found we could not reject the null of no correlation between errors and so based estimates of willingness to pay on the logit regression without selection.) Lastl y, we made estimates based on using onl y “definitely yes ” as a “yes” instead of b oth “definitely yes” and “probabl y yes ” as a “yes” as in O’Conor and Blomquist (1997). In Table 6 we report values that turn out to be comparable to the best estimate from our earlier work. For the average age adult (45 ye ars) our estimate for the annual value of asthma control is $1,960 in 2007 dollars (or $1,441 in 1995 dollars). From Table 6 which reports annual values of asthma control by age we cautiously summarize saying that the pattern of results hints that values are higher for children and yo ung adults. For the average age child (11 years) our estimate for annual value of asthma control is $2,842 in 2007 dollars (or $2,089 in 1995 dollars.) This pattern is relevant for estimating the asthma related benefits because the ages considered are 0

– 16 and point estimates for values for children are greater than the value for the average age adult. The pattern suggests that estimates based on the average value for adults are probably underestimates, at least with respect to this factor. Reference to this work has been added.

The monetization section has been revised to more accuratel y reflect the higher value for children.
**A. Myrick Freeman III, Ph.D.**  Again, I don’t understand the question. What do you mean by the “lifetime approach”? The term is not used in the document. No response required

. **Shelby Gerking, Ph.D.**  A search of the review document turned up no references to “lifetime approach” so the

issue to be addressed here is not entirely clear. Reference to the “lifetime34 Nonetheless, the report makes clear that valuation of asthma effects is based on valuing the incidence of asthma, rather than s ymptom exacerbation. This approach is crude for two reasons. First, there is substantial heterogeneity in cases of asthma. Fo r some people, asthma is little more than an anno yan ce, while for others this illness is debilitating. Willingness to pay

to avoid asthma would be expected to vary according to how serious a case is contemplated.

Second, willingness to pay to redu ce additional cases of asthma will not include the willingness to pay

to reduce exacerbated s ymptoms of those who already have asthma.

Two other issues: (1) While estimates of increased incidence of asthma pertain to children (see p. 19), estimat es of WTP to reduce asthma incidence are based on two studies of adults. Parents may

well be willing to pay

more to reduce asthma incidence among their approach” was designed to be contrasted with adding up benefit ye ar - by

- ye ar, described as the “annual approach” in the text. This is a reasonable concern but neither th e concentration

response function nor the valuation distinguish the level of severity

of asthma. Therefore, this adjustment cannot be made. At present, a defensible concentration

response function cannot be derived for this endpoint, so it is not valued i n this analy sis. The monetization section has been revised to more35 children than they

are WTP to protect themselves from the same illness.

(2) It might be useful to perform a sensitivity analy sis on the estimates provided to determine how much difference it would make to assume that a percentage of childhood asthmatics become asy

mptomatic when they

become adults, rather than assume that childhood asthmatics carry their illness forward to adulthood. accuratel y reflect the higher value for children. The monetization section has been revised to include the children who become asy mptomatic. **CHARGE QUESTION 6: The concentration** 
**- response**  **relationship is based on an odds ratio for a period of time longer than the one year. The exposure model produces results for one** 
**- year of exposure to formaldehyde for each age, housing type, and climate cohort.**  **As a consequence, an adjustment to the simpl e model needed to be made to model the effect on individuals who are currently alive**  **when the regulation takes effect. As an upper bound estimate, we assume that the odds ratio can be applied to the one year reduction in the same fashion as it**  **was applied**  **for the 16 year time period. The problem with this approach is that it effectively treats the exposure as an acute effect. If the**  **odds ratio indicates a particular percentage reduction in asthma cases from a reduction in formaldehyde exposure over 16 year s, the**  **upper bound approach would suggest the same percentage reduction in asthma case in one single year if we were to witness the same**  **reduction in formaldehyde exposure in one year. The lower bound approach assumes that a particular exposure reduction f or one**  **year produces the same effect as if that exposure reduction were spread out over the entire 16**
**- year time period.**  **Please comment on the upper and lower bound methodology used. NAME**  **COMMENT RESPONSE**  **G lenn C.**  **Blomquist, Ph.D.** It seems as reasonable as other possible approaches. No response required

. **A. Myrick Freeman III, Ph.D.**  The approach seems reasonable. The bounds are relatively narrow, as shown in Table 7.

How will the results be presented in the final report, as upper and lower bounds or averaged to give a “best” estimate? Reference to the “lifetime approach” was designed to be contrasted with adding up benefit ye ar - by

- ye ar,36 described as the “annual approach” in the text. **Shelby Gerking, Ph.D.**  The upper bound estimates are obtained b y assuming that asthma onset is an acute effect of

formaldeh yde exposure particularl y among older teenagers. I am uncertain as to whether this assumption is at variance with scientific information regarding the deve lopment of this disease and would defer to another panel member with greater expertise on this point. If asthma onset from formaldehyde exposure cannot be considered an acute effect, then the upper bound estimates would be less credible. Nonetheless, the upper bound estimates and the lower bound estimates do not differ greatly . Table 7 reports that for the three housing profiles total discounted upper bound WTP is $4,939,166 and the corresponding lower bound figure is $4,340,740. So, the upper bound est imate is about 14% larger than the lower bound estimate. An alternative to the lower bound estimate might be to assume that currently living children are unaffected b y reduced formaldeh yde exposure. Instead, we might assume that the reduced exposure ap plies only as “new” children as they enter the model. These “new” children are then assigned cases of asthma with the incidence rates described on p. 48 of the review document. EPA does not have a definitive model of the development of asthma, so this u pper bound is, at minimum, possible.

This would, indeed, produce an even lower bound, but it would require assuming that there are no benefits to formaldeh yde reduction unless one experiences 12 full years of that reduction. Given that this would be a very extreme assumption, this new lower bound has not been estimated.37

**C HARGE QUESTION 7**  **: The prevalence data suggest that 7.2% of children age 0** 
**- 4 have been told that they have asthma. 16.4% of**  **children aged 5**
**- 14 have been told that they have asthma. We**  **assume that the probability of being diagnosed is uniformly distributed across the 0 to 16 age bracket, so that the incidence rate would be 1.44% for the first five years and 1.49% for the next ele** **ven years. Allocating cases uniformly across the age bracke** **ts provides us with a way to calculate the annual benefits of any exposure reduction that occurs for the entire time period, but may not be appropriate if the diagnosis of asthma for very young children (e.g.,**  **age 0**
**- 2)**  **differs from older children. Is the**  **assumption about applying the concentration**
**- response function to children aged 0 to 16 appropriate, given the asthma onset**  **studies’ focus on school**

**- aged children and adolescents, and given the potential uncertainty of the Rumchev study involving younger**  **ch ildren?**  **NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  It seems as reasonable as other possible approaches.

A question about this and the other concentration

- response functions and exposure is whether or not they

take into account averting behavior. Smell leads to open windows and more time outside of house and less exposure. No response required

. The concentration response functions were developed using in

- home samples which, implicitly , included the averting behavior of the home participants. However, averting behavior changes (e.g., reduced smells leading to fewer open windows) were not included in the economic analy sis. **A. Myrick Freeman** I can’t answer this. It lies outside my area of expertise. No response38

**III, Ph.D.** required

. **Shelby Gerking,**  **Ph.D.** I defer to another panel member here as I have no expertise in this area. No response required

. **C HARGE QUESTION 8**  **: The linear concentration** 
**- response function accounting for background exposures based on Taskinen**  **et al. (1999) is used for the annual approach.**  **Please comment on whether the concentration**
**- response function is used appropriately in th**  **e benefits assessment approach. NAME**  **COMMENT RESPONSE**  **G lenn C.**  **Blomquist, Ph.D.** It seems as reasonable as other possible approaches. No response required

. **A. Myrick Freeman III, Ph.D.**  It was used appropriatel y. No response required

. **Shelby Gerking, Ph.D.**  The concentration

- response function appears to have been applied correctly in the benefits assessment approach. Note that the concentration

- response function is linear, so accounting for other sources of formaldeh yde exposures would be less important. However, two other issues might be addressed. First, equations (18) and (19) in the text may require some clarification. My question relates to the term

, , , , [( exp ) ( exp )] hcb aseline h c policy a b osure osure        . Does a =


###  ? Does b =  ? I f so, the notation should be changed. If not, the equation needs addi tional explanation.

Second, in these equations, population refers to women who have difficulty conceiving. The population of women who are activel y attempting to become pregnant would instead be more appropriate. P age 59 indicates that for the propo sed rule this latter definition would be incorporated. I agree that this change would be appropriate. No response required

. EPA does account for other sources of exposure.
You are correct that a = 

###  and b =  . The notation has been changed. The model has been revised to use women who are seeking pregnancy as the appropriate population. **C HARGE QUESTION 9**  **: Monetization of delayed fertility has been discussed in the literature but has never been included in**  **primary analyses of EPA rules becaus e it was believed that the scientific knowledge on reproductive and developmental health effects**  **was not strong enough to quantify risk in the primary benefits analysis.**39

**While there appears to be good data on the cost of treatment, there are few studies on the willingness to pay to reduce delay ed**  **conception. Most economic valuation studies regarding fertility focus on an individual’s or a couple’s willingness to pay for in**  **fertility treatment, particularly in** 
**- vitro fertilization (IVF). Conceptually, the willingness to pay approach is preferable and could be deduced**  **from the valuation studies. However, given that there has been less research on these willingness to pay value s than other values and**  **the fact that the values have not been used in previous economic analyses, we used the more straight**
**- forward cost of illness approach**  **for this analysis. As an upper bound, we assume that any woman who has difficulty conceiving (i.e**  **., time to pregnancy exceeds 12 months) will obtain some type of fertility service. This may be a reasonable upper bound, but there are certainly women who have trouble becoming**  **pregnant and do not seek fertility treatment. The willingness to pay for fer** **tility treatment is treated as an expected value. The average cost of various cycle**
**- based fertility**  **treatments is multiplied times the probability of obtaining that treatment at various ages. There is probably a small opposit e effect**  **associated with an inc rease in pregnancy from reduced formaldehyde exposure by women who do not want to become pregnant, but**  **we do not consider this effect Please comment on whether the annualized approach as opposed to the lifetime approach is appropr** **iate in this context. NA**  **ME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  It seems as reasonable as other possible approaches.

On page 58, the choice is made to use the cost

- of

- illness estimates from Katz et al. (2011) for valuing difficult y in conceiving due to formaldehyde exposure. A strength of these estimates is that apparently most fertility

treatment costs are paid for out

- of

- pocket b y consumer/patients rather than by third parties through private or public insurance. As such, consumers reveal that the treatments are worth at least as much as they paid. Their maximum willingness to pay would be expected to be greater than these costs because of consumer surplus. (This does not take into account any utility or disutility

of treatments.) If data were available and demand for fertility treatment could be estimated, then a better estimate of maximum willingness to pay could be made. This suggests using cost

- of

- illness will produce an underestimate. However, if the values are applied to all women who are exposed to formaldehyde, benefits will tend to be overestimated. The reason is that not all the women whose fertility is affected will pay the market prices for the treatments. In other No response required

. An explicit discussion of this point has been added to the uncertaint y section.40 words, the price is known for the various packages of treatments, but the number of women who are willing to pay

the price is not. The maximum willingness to pay for treatment for the women whose fertility is affected but choose to forgo treatment and the number of them are unknowns. Their values are likel y to be positive, but they are less than the costs. Katz et al. report treatment costs per successful outcome of more than $70,000. The y also report that 72% of the women had college education. A hunch is that those women have above average household incomes and spend most of their time in single famil y detached homes where exposure reduction is smallest. L ess educated women with lower household incomes are probabl y less likely to pay for treatments at the going prices. Assuming that women who have below average incomes and live in mobile homes will pay the market prices for the same distribution of fertility treatments is likely

to bia s the estimate of benefits of reducing exposure to formaldeh yd e upward. **A. Myrick Freeman III, Ph.D.**  Again, I don’t understand the question. What do yo u mean by the “lifetime approach”? The term is not used in the document.

Perhaps the charge question should be " **Please comment on the annual approach to calculating a total WTP per year as described in Section 3.4.2**  ." My answer to that questi on is that if a valid individual WTP per y ear can be obtained, equation (18) is the appropriate way

to calculate aggregate WTP per year. But for reasons I point out in the Specific Observations section below (see m y comments to question #3), Ihave seriou s doubts about the ability

to obtain a valid individual WTP per year. Reference to the “lifetime approach” was designed to be contrasted with adding up benefit ye ar - by

- ye ar, described as the “annual approach” in the text. EPA believes that there is suffic ient data to monetize this endpoint, so we have included this estimate. However, the concerns that the reviewer raises are very important.41 The uncertainty section for this endpoint has been expanded and these point have been explicitly included in the text

. **Shelby Gerking, Ph.D.**  Cost

- of

- illness estimates are conceptuall y inappropriate in this context for two reasons. First, cost

- of

- illness is not a conceptually sound approach for estimating willingness to pay

. This point is noted in the document on p. 58. In consequence, I woul d suggest that cost

- of

illness estimates might be used onl y as a last resort. The WTP estimates obtained by Smith and van Houtven may

well be a more defensible choice. Careful thought should be given to whether this alteration would be an improvement. S econd, the COI estimates utilized (see equation (20) and Table 10) do not reall y pertain to the delay in conception addressed in the Taskinen study . Women (or couples) may be willing to pay to reduced time to conceive, but may

at the same time be reluctant to seek fertility treatment. At a minimum, this potential misalignment should be addressed. This point was explicitly recognized in the uncertainties section.

**C HARGE QUESTION 10**  **: The time period associated with the exposure** 
**- response function is longer than the time step of the**  **exposure model. The Taskinen (1999) study examined the fecundity of women age 20**
**- 40. This causes a problem if we have an**  **individual who does not experience t he exposure reduction for the full time period. We can form an upper and lower bound of this**  **willingness to pay as we did for asthma prevalence. The upper bound is based on the assumption that the linear concentration**
  ** response function holds for an acute e** **xposure of one year. The lower bound assumes that an exposure reduction for one year represents 1/20** **th of an exposure reduction for the entire 20** 
**- year time period.**  **Please comment on the upper and lower bound methodology used. NAME**  **COMMENT RESPONSE**  **G lenn C.**  **Blomquist, Ph.D.** It seems as reasonable as other possible approaches. No response required

. **A. Myrick Freeman III, Ph.D.**  The approach seems reasonable. How will the results be presented in the final report, as

upper and lower bounds or averaged to give a “best” estimate? No response required

. **Shelby Gerking, Ph.D.**  The Taskinen study a ppears to treat formaldeh yde exposure as a long term exposure. In consequence, I am uncertain that the upper bound estimates are defensible (see the related EPA does not have a definitive model42 point #6 in asthma above). N onetheless, the upper and lower bound WTP estimates differ only by a bout $57,000 (see Table 12). T his outcome could change of course if the anal ys is is redone along lines suggested above.

Also, as with asthma, I would suggest the possibility t o treat “new” women entering the model as those affected by the contemplated reduction in formaldehyde exposure. of the development of asthma, so this upper bound is, at minimum, possible. This would, indeed, produce an even lower bound, but it would require assuming that there are no fertility benefits from formaldeh yd e reduction unless a woman experiences 20 full ye ars of that reduction. Given that this would be a very extreme assumption, this new lower bound has not been estimated. **C HARGE QUESTION 11**  **: The ages used in this analysis reflect the ages reported in the Taskinen (1999) study, ages 20** 
**- 40.**  **However, women older than age 40 obtain fertility treatment. The value of reduced infertili ty effects from reduced formaldehyde**  **exposure is not reflected in this analysis in order to remain consistent with Taskinen (1999). Please comment on whether the concentration** 
**- response function was applied to appropriate age groups given the age groups in**  **the studies.**  **NAME COMMENT**  **RESPONSE G** **lenn C.** It seems as reasonable as other possible approaches. No response43

**Blomquist, Ph.D.** required

. **A. Myrick Freeman III, Ph.D.**  Given my reservations about using the cost

- of

- fertility treatment to monetize this effect (see my comments to question #3 in the Specific Observations section below) , I have no problem in limiting the quantification of this effect to the age group covered in the Taskinen study

. No response required

. **Shelby Gerking, Ph.D.**  The Taskinen study does not appear to provide a direct basis for adding women aged 40 and older to the analy sis. However, relativel y few of these women may seek to become pregnant in a given ye ar. If the analy sis focused on women who seek to become pregnant, exclusi on of women over 40 y ears of age may not be a grave oversight. I would defer to a panel member more knowledgeable about fertility issues to make a judgment on this issue. Reference to the “lifetime approach” was designed to be contrasted with adding up be nefit ye ar - by

- ye ar, described as the “annual approach” in the text. **III. SPECIFIC OBSERVATIONS ON THE DOCUMENT**  **NAME COMMENT**  **RESPONSE G** **lenn C. Blomquist, Ph.D.**  **Page 53, bottom.** $4.9 instead of $4,9.

**Page 56, 3 rd**  **paragraph.** M onetization is misspelled. **Page 58.** V an Houtven and Smith (1999) instead of 1997 and $12,500 instead of $12,50. **Page 59.** Is the probability of obtaining cycle

- based fertility treatment shown in Table 8, the best projection for future treatment? The utilization percentages give n on page 916 in Katz et al. seem different.

**Page 68.** O’Conor instead of O’Connor. These edits have been included.

A more accurate method for estimating the probability

of obtaining cycle

based fertility treatment has been added. This edit has been44 included.

**A. Myrick Freeman III, Ph.D.**  There are a number of t ypographical and editorial errors. This is not a complete list:

**Table of Contents.** P age numbers are wrong. **Page 17.** F igure 2 should be labeled figure 5. **Section 3.** Why

do the table and figure numbers start over inste ad of continuing throughout the report? And some of the table numbers seem to be wrong (e.g., J

- 10 on page 36). **Page 6.** T he report gives the aim of developing concentration

- response relationships as being “ ... to inform the economic benefits assessment of potential cost savings ...” This is not about “cost savings;” it is about welfare gains.
In some places, coefficients in the concentration

- response relationships are Greek letters. In other places they

are not. **Section 2.1.1, 3 rd**  **sentence in the first paragraph.** N eeds editing. **Page 53.** Where it say s “($93,0 95 + $58,662 + $90,852= $242,602),” it should be = $242,609. **Page 58.** It say s “willingness to pay of between $3,750 and $12,50 for fertility treatment.” **Page 59.** T he probability of using IVF should be 2.5%, not .25%. **Page 61, last paragraph.** T here are two references to Table 10 , which should be Table 12. **Page 63.** T he sentence, “This is probably the largest category

of value associated fertility issue from a reduction in formaldeh yde exposure,” needs editing. **I have added the following three charge questions based on my expertise in non**
  ** ma** **rket valuation:** These edits have been included.45 **(1) Please comment on the validity of the monetization of sensory irritation.**  The approach to the monetization of this effect is the same as that used in the First Prospective Section 812 Report. In my

judgement, this is a valid approach and makes the bes t use of the available empirical evidence. However, it should be noted that the effect actually valued in the First Prospective Section 812 Report as “Upper Respiratory S ymptoms” defined as “two or more of the following sy mptoms: runny

or stuffy nose; coughing; and eye irritation.” Since this document states that formaldeh yde can cause a variety of types of sensory irritation in the upper respiratory sy stem (p. 7), this is appropriate. But it should be made clear that more than simply eye irritation i s involved.

**(2) Please comment on the validity of the monetization of chronic asthma.** The approach to the monetization of this effect is the same as that used in the First Prospective Section 812 Report. In my

judgement, this is a valid approach and makes the best use of the available empirical evidence. **(3) Please comment on the validit y of the monetization of reduced fertility.**  I have serious No response required

.

Appendix H (pg. H

- 24) defines it as “o ne or more of the following: runny or stuffy nose, wet cough, burning, aching, or red eyes .” This means that it is the same value used in the retrospective study

. Nevertheless, EPA understands the reviewer’s concern and has included the definition in the discussion of the retrospective study

. No response required

.

These are46 reservations about the approach taken here to monetize this effect. First, “reduced fertility” is not a well

- defined effect. There is ambiguit y as to both the degree of reduction and its duration . This makes determining the proper valuation difficult.
I agree that conceptuall y , the willingness to pay (WTP) approach is preferable to a cost

- of

illness or cost

- of

- treatment approach. However, as Iread the available WTP studies, they apply to the more serious infertility rather than to the “subfertility” (p. 21) associated with exposure to formaldeh yd e. Thus, the available WTP studies are not suitable for benefits transfer. The report takes a cost of treatment approach to valuation. But it is n ot at all clear to me that the “cycle

- based treatments” described here are either appropriate treatments or likely to be effective in the face of continued formaldeh yde exposures. For these reasons, I recommend that this effect be described and quantified to the extent that evidence supports quantification, but that it be acknowledged that there is not an adequate basis for monetization of this effect. important considerations and they have been explicitly included in the text.

It is EPA’s position, however, that there is sufficient data to monetize this endpoint. **Shelby Gerking, Ph.D.**  The document appears to have been put together hastily as there are numerous ty pos and other glitches. Below is a list of ty pos that I flagged

— I am certain there are more. **Page 31, first line below eq**  **uatio n (1).**  ...risk reduction at age a. **Page 35, next to last line of third full paragraph.** D ata should be day s **Page 36.** N ot sure wh y the Table is called “Table J

- 10”. Other tables are not numbered this way . Also , in this table Dickie et al. needs a date **Page 44 , first line under monetization. Analysis should be analyses.**  **Page 45, Table IV.** 2

- 17 not numbered consistently with other tables, also in two places These edits have been included.47 decimal points are mistakenly used for commas **Page 53, last full line.** S hould be $4.9 million **Page 56, eighth line up from bottom.**  Undergoes should be undergo **Page 57, fourth full paragraph, first line.** Ryan (1996) conducted a contingent ... **Page 58, first full paragraph, line 4.** Respondents were asked to consider taking... **Page 59, line 8 under equat ion (19) (and elsewhere).**  The word data is plural, not singular **Page 59, line 12 under equation (19).**  D ifficulty is misspelled **Page 59, second line up from bottom.** R eduction is misspelled **Page 60, part of Table 9 appears to be missing.** Also, the heading is missing a number for ppb. **Page 60, Table 10.** T he probability values are missing