8065	Assessment Initial Draft	Final Draft comments
Abstract	No abstract.	While the abstract is well written and informative about the topic, it says nothing about the proposed research, which is the goal of the proposal on which the abstract should focus.
Research Question	The area of interest in clear, but the actual research question is not.  Indeed, it is difficult to understand the stated principal hypothesis.  Neither of the implied predictions seem reasonable on the surface.  The first is that the rate of foreclosure will have a positive relationship with a group of "independent" variables that include the number of flood insurance policies, the number of claims, etc.  Since the "independent" variables vary by the population size of the county (or floodplain) but the rate of foreclosure does not, we would commonly expect no relationship.  With respect to the quality of levees, the other "dependent" variable, we would probably expect no relationship with some "independent" variables and a negative relationship with others (such as number of floods and claims).  In short, the hypotheses might be plausible, but without further explanation they do not appear sensible.  The principal hypotheses need to be spelled out much more clearly.  Readers should be able to understand what motivates and justifies a hypothesis even if they aren’t familiar with the NFIP program or flood insurance more generally.	While perhaps interesting, the research questions as stated are too broad, vague, and ambiguous for a research proposal.  Take, for example, the first bullet point.  Asking what a storm "revealed" about inequality is too vague to be meaningful as a research question.  The second sentence, "Is it possible to determine what impact Sandy and Biggert-Waters had on these populations individually?" is worded so ambiguously that we do not know if it means to ask if we can identify the affects on individuals or can we separate the effects of the storm from the effects of the legislation.  Or, looking at the third bullet point, we know the answer to the first question without research: obviously, if the ongoing costs go up, meeting these costs becomes more difficult.  Overall, the apparent research question buried here is: to what degree did the legislation increase the costs of residents after Sandy and, possibly, how might this have increased foreclosure rates.
Literature Review	The information in the introduction, background, and literature review sections is all a bit jumbled and doesn’t flow logically.   This makes great demands on the reader to impose a logic (and under such conditions, readers commonly impose their own logic, not the one the author hoped for). A good literature review must be careful to represent the reviewed works accurately.  Some weaknesses appear here.  For example, the point of the Fell & Kousky 2015 article would appear to be that if people see flood protection as effective, being in a flood plain does not reduce the value of commercial properties; but absent such protection it does.  The summary in the literature review does not convey this.  Similarly, the review discussion of Zhang (2016) suggests it is responding to the Fell & Kousky (2015) research design, but Zhang never refers to these authors.  This is not surprising, as Zhang is aiming at a quite different research question, the relative impact of flood risk on the prices of different parts of the residential housing market.  The review also seems to misinterpret the aim of the quantile regression, in Zhang.  It is still a hedonic model, with the goal not being so much to improve controls for unobservables (indeed, the Coarsened Exact Matching of Fell & Kousky might be considered better by some; in Zhang, this is addressed, if by anything, by the use of the difference in differences technique), but to distinguish effects at different parts of the distribution.  The main point here is that a literature review must be accurate. The moment that reviewers perceive the author of a proposal does not accurately portray some aspect of the existing literature, is a moment when the proposal loses credibility.	The literature review is narrow, without clear objectives, and seemingly unreliable.  The formal literature review discusses a range of points attributed to a few articles that concern the NFIP, Biggert-Waters, or flood risk insurance.  These are on the right subject, but as a whole do not get far.  There are no references to the extensive literatures on risk assessment and insurance policy, or on the determinants of government policy decisions, or on the unequal impact of legislation with economic effects.  The earlier section titled "Background" reviews the history of the relevant policies, which is certainly interesting, but as the research does not concern policy decisions this background offers little theoretical or empirical background to the project.  Again, the issue of representing the literature accurately is critical.  In the first paragraph of the literature review, the final sentence reads:"These consequences, according to Elliott (2017), are felt disproportionately as socioeconomically-vulnerable communities throughout the country experience a lack of physical protection, increased flood risk, and depleted financial security after disaster (Curran, 2016; Johnson, 2015)."  However, Elliott's article has no relevant research results (it is on the debates over the policies) and the author's most direct statement appears to be "In truth, property owners of highly varied resources were affected by Biggert-Waters. Luxury condominium developments and vacation homeowners have benefited from subsidized flood insurance, along with working-class communities."  This article presents descriptions of they claims by the rival actors, not research on the actual circumstances.  If a proposal attributes what is apparently a factual finding to a source, that source should be a report of the research that demonstrates the fact. Moreover, this version of the proposal repeats the problematic interpretations of the Fell & Kousky 2015 article and the Zhang 2016 article described in the comments on the initial draft.
Data & Analysis	The section on data strikes an ambitious tone, but manages to be too obscure to assess effectively.  It implies that a lot of good data will just fold together and make for a good analysis.  This would be a good outcome, but things are rarely so easy. Lets look at some specifics.  The data section fails to ever say that the NYU data being discussed is the RealityTrac data.  It refers to Gallagher (2014) as the source of further data, but neglects to include the reference in the bibliography ("Learning About an Infrequent Event: Evidence from Flood Insurance Take-Up ...").  The assertion that three data sets will be merged provides no hint at what level or by what unit they will be merged and ignores that the Gallagher data and the RealityTrac data are for different periods that only overlap for two years.  The proposal states that the unit of analysis will be the county, but does not discuss how the source data sets will be converted to county level.  Nor does it consider the analytic implications of using summary data (presumably means, rates, and the like).  For example, the listed predictor variables that are raw counts ("number of ...") would not under any standard analyses be applied against the proposed outcome variable "Home Foreclosure Rate").  And it is difficult to guess how the quality of levees became a dependent variable given the rest of the proposal (and ignoring that the boundaries of levees may not correspond to other distinctions), in which they only seem to make sense as an independent variable.	The data on areas affected by hurricane Sandy appears fine in the abstract, but the plan for data analysis is hard to follow and seems problematic.  The proposal suggests that the county will be the unit of analysis and discusses this at some length.  It also claims that the research will use "hierarchal or multilevel mixed models".  To do this would imply another unit of analysis which the discussion in the proposal does not appear to recognize. Also problematic is the indifference in the proposal to what it means to select the county as the unit of analysis.  First, with only 34 counties, or data points, the capacity to disentangle multivariate relationships as planned is severely limited.  Second, this plan does not leave much room for doing any kind of statistical analysis.  The 34 counties are defined as the universe of counties subject to the effects of Sandy, not a sample.  These counties are also not a random or representative sample of all counties in the U.S. vulnerable to flooding.  The purpose of inferential statistical procedures, of course, is to ascertain if relationships observed in a sample can be reasonably inferred to exist in the population from which the sample is drawn.  So, if the data are not a sample, the inferential statistical procedures do not apply.  Note that this issue would also appear to exist if the analysis were changed to households within these counties if the data covered all dwellings and foreclosures, as it appears to do - that is if the data includes the full population.  This is not a bad thing from the perspective of identifying the relationships between characteristics; it means that one accurately measures rather than estimates the parameters in the population.  Essentially, however, the project appears to be moving in the direction of a case study.  One may generalize from a case study under the right circumstances, although given the historical specificity for this case - in terms of the hurricane and in terms of the legal and economic conditions - it is not obvious what room there might be.
Causal Interpretations	The current draft contains little in terms of causal discussion, and what it does, in terms of the guiding hypotheses, is difficult to understand.  It could help considerably if the proposal included a basic model linking the independent variables to dependent variables, and discussed the causal mechanisms assumed to produce the pattern of causal linkages.  This would potentially help to clarify the development of other parts of the proposal and it would help readers make sense of the research design.	The proposal suffers significantly from several principal issues related to causal analysis.  (1) It should take into account the wider literature on foreclosure rates, in particular so that the research design takes into account now neglected critical variables representing known causes.  (2) The proposal does should address the issue of historical specificity with regard to the Sandy case.  (3) The proposal should strive to overcome the conflation between empirical questions and normative judgments.  Let us look at each of these. This research agenda with its concern with foreclosures is unlikely to achieve an adequate design without considering the extensive literature of the causes of foreclosures.  The classic interpretations in the U.S., which it appears most accounts consider still applicable in the face of the Great Recession foreclosure crisis, are reduced economic circumstances of the  mortgage payers and reduced value of the homes.  In part, reduced home value contributes to a possible calculation that the remaining mortgage significantly exceeds the current house value, so that defaulting (letting the banks take back the home) may become a rational effort to save.  Probably even more, as homes are a primary asset used for refinancing to provide funds when income fails, reduced home values leave many disadvantaged people without assets to protect their investment (e.g., through a home equity loan) during economically difficult times.  Some research on the high rates of foreclosures during the Great Recession suggest that these causes were still more important than rising interest rates from variable rate, subprime mortgages.  Note the obvious application of these interpretations to the  current project.  To the degree that the in aftermath of Sandy people faced income issues (either as a result of storm effects or an incidental historical coincidence) or declining value of their homes (again, either due to the storm, or incidental historical conditions, or the implications of changes in insurance requirements), these circumstances could be expected to increase foreclosure rates.  Also, note that there is potentially a fairly straightforward comparison that can be made between rising insurance rates and rising interest rates.  Essentially, they have the same effect by increasing the carrying cost of the home.  So, research on the effects of a forced rise in insurance costs is fundamentally the same as research on the effects of rising interest rates with respect to foreclosures.  Given that, one would expect that changes in income and in property values would be crucial parts of the explanation.  Yet they are not. As I understand the presentation, the planned research in this proposal is also very historically specific, because it focuses on the experience of the legislation in an area where the legislation essentially applied only after they suffered a flood.  To the degree that the legislative goal was to influence behavior prior to floods, the outcome of this case has limited room for generalization (which seems to be its overarching goal).  That is to say, this is a very interesting case by itself, but it is not obvious how this case will lead to any generalizable results.  The proposal should either acknowledge this or present an argument showing that generalization is possible. It seems that each version of this proposal may suffer because they repeatedly blur the difference between empirical questions and normative judgments in its questions about disproportionate effects of flood risk policies.  By analogy, a sales tax on basic consumer goods may be seen as egalitarian by those who focus on all people paying the same tax rate on purchases and as regressively unequal by those who focus on poorer people paying a higher proportion of income in sales taxes (because a higher proportion of their income goes for standard consumable goods).  Everyone agrees on the numbers, they disagree on interpretation.  The discussions of disproportionate burdens for the victims of floods or those with dwellings in flood zones does not seem to maintain a clear distinction between these issues - the empirical and the normative judgment - which makes decisions over research strategy cloudy.
Research Contribution	Aside from some vague comments at the end of the literature review, this is not addressed.	Aside from fairly vague claims about providing broad new insights to diverse audiences in the "Expected Audience" section, the proposal still does not show how the research will advance knowledge over past work.  A lot of research has addressed foreclosure rates.  Quite a bit of research has considered the consequences of disasters.  People have even written a fair amount about the effects of Sandy.  What are we going to learn from this research that is new?
Citations & Bibliography	The overall reference apparatus is fine, but incomplete.  At least one major citation in the literature review (Fell and Kousky, 2015) is absent from the bibliography, as is the data source, Gallagher (2014).  Citations and bibliographies should be complete with no errors.	The reference structure is okay.
Quality of Writing & Organization	The prose is fine, but the logical progression is sometimes awkward and sometimes confusing.  The main points are often lost as readers wade through long, complex sentences.  Focus on brevity, clarity, and non-technical language.  Every section might be improved by asking "what is this supposed to convey?", then trying to outline what is there to see how well it responds to that question's answer.	The writing is okay.
Priorities for Revising / Responsiveness to Feedback	What stand out most here are probably the ambiguity surrounding the research question, the implicit causal models driving the research design, and how the proposed data will be transformed into a unified dataset that responds to the research question.	The final proposal has changed the project considerably.  Some of these changes appear beneficial, others appear questionable.  Revisions to the literature review did remove some problematic material and add some useful.  It also retained some that was explicitly pointed out as problematic without changes or defense and added more material that does not seem to accurately represent the original arguments.  The refocus of the research to the Sandy outcomes seems a good strategy for making the project more manageable.  However, the confusion over the unit of analysis and what statistical strategies are possible is problematic.  The limitations of the causal analysis have not improved.
Miscellaneous Notes	The proposal suggests a great deal of background research and the background/literature review is very detailed. However, the actual research plan needs to be more concrete and detailed to show if it is viable.	After several rounds, this proposal still seems troubled.  This may in part reflect the limitations of the literature that has been consulted.  Consider a couple relevant background points.  First, if a highly increased insurance rate is imposed along with a mandatory insurance requirement on residents of flood zones, it amounts to the equivalent of a regressive tax assuming that the insurance rates are proportionate to value.  Regressive taxes are easily modeled and well understood.  That they are a greater burden on the economically disadvantaged is essentially an accepted fact which does not require additional evidence in particular cases.  So, to show that the imposed insurance rates will be experienced as an unequal burden really depends on documenting the rates, and does not require evidence of experienced distress (although the latter might have political value, it adds little analytically).  Second, From the economic perspective that motivated Biggert-Waters, finding increased foreclosure rates is not inherently problematic, but rather evidence that they were right to infer that people had been building and buying housing for which they could not afford the associated risks.  While there may be a lot of room for political arguments over who should pay for risks, higher foreclosure rates in the wake of significantly higher insurance rates would seem to be a straightforward prediction from all sides.  They would disagree on the justice of the outcome, and potentially on the long-term causes (e.g. if people were induced to buy such housing by state policy), but not on the short-term effects.  Third, as discussed above, the causal theories about foreclosure rates raise serious questions about the plausibility of foreclosure rates functioning as the critical symptoms of misapplied social policy. Unfortunately, after looking at some of the literature cited in the proposal, it seems that much of the closely related work is a bit simplistic, possibly because so much is driven by policy motives.
Proposal		After all the transitions in the various versions of this proposal, it remains rather problematic.
Class Overall		Sustained effort through the class.