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Economics Of The Movie Business Essay

In this section I provide a review of the movie business with an emphasis on how blind bidding evolved from the Golden Age of Hollywood in the 1930‘s and 1940‘s until its demise in the beginning of 1986. For many decades blind bidding was not a concern for theater owners, because it was not the dominant method by which films were licensed. During the Golden Age, block booking was the way a majority of films were licensed. With this method, high and low quality films were sold together in a bundle to theater owners, without an opportunity to trade screen them.

The landmark United States vs. Paramount et al. decision by the Supreme Court in 1948 altered the motion picture distribution system. The five major movie companies that produced, distributed, and operated theaters as well as the three studios which did not own theaters were all found in violation of the Sherman Act for attempting to monopolize the industry. One of the major consequences of this decision was the elimination of block booking. After the Paramount decision, films were licensed by product splitting, open bidding, or blind bidding.

Product splitting was when theater owners decided among themselves which one had the first opportunity to negotiate for a film with a movie studio in a given market. Open bidding referred to a situation in which theater owners had the opportunity to trade screen films before bidding. Blind bidding was used infrequently until the 1960‘s, which prompted a two-year agreement from January 1, 1969 to January 1, 1971 between the movie companies and the Department of Justice. This agreement limited 1 9 the number of films which could be blind bid to three per studio per year.

The two-year agreement was renewed twice, which limited the practice through January 1, 1975. However, the Department of Justice revoked all restrictions limiting blind bidding after this date and the practice accelerated rapidly. Movie companies perceived blind bidding as a necessary way to finance blockbuster films, and it persisted for an eleven year period from 1975-1985. Chapter 2 LITERATURE REVIEW In this chapter, I will review the economic literature on blind bidding, exit, and natural experiments. The selected papers motivate my empirical model of the effects of blind bidding. Section 2. 1 discusses the blind bidding literature.

Section 2. 2 surveys natural experiments testing the impact of a policy change. 2. 1 Blind Bidding In this section, I discuss two studies which arrive at different conclusions about the impact of the anti-blind bidding laws. Although neither study addresses explicitly the issues of exit, admission prices, and delays, the empirical findings are relevent. Blumenthal (1998) finds that average bids are lower for blind bid theater owners and as a result their returns are higher. However, since the returns of blind bid theater owners are more volatile, she concludes risk averse theater owners are worse

off under blind bidding, legitimizing their efforts to pass anti-blind bidding laws. Forsythe, Isaac, and Palfrey (1989) model the behavior of n buyers and one seller in a sealed-bid, first-price auction. They conclude that the anti-blind bidding laws were unnecessary as buyers would learn that a seller withholds information when it is unfavorable. A seller would abandon blind bidding once all buyers learn that withholding information was in the seller‘s best interest and not theirs. I find that practices in the motion picture industry were not consistent with this prediction,

because the movie companies trade screened unfavorable films and blind bid highly anticipated films. Blumenthal (1988) justifies theater owners‘ rationale to seek relief from blind bidding by showing that they experience lower utility in blind-bid environments than preview ones. The author uses generalized least squares to test three hypotheses about film bids or film returns for blind-bid and trade screen theaters using the rental terms of 18 films from a national theater chain in 1982. First, she hypothesizes that theater owners in blind-bid states submit lower bids, because in accordance with

economic theory, bidders reduce their bids on average in an auction where there is uncertainty about the value of a product. Second, blind-bid theater owners place a greater emphasis on the limited information contained in a bid letter. Therefore, bid letter information will explain a larger percentage of the variance for bids in blind-bid theaters than trade screen ones. Third, mean returns are higher for blind-bid theaters, but they experience greater volatility than trade screen theaters. Depending on the hypothesis in question, the dependent variable is either film bids or film returns.

1 She includes film budget and saturation as predictor variables, since higher budgeted films and wider released films would be an indication of larger expected returns by the movie companies. Other independent variables include theater operating expenses, an indicator variable signifying theaters in blind bid states, and the number of movie theaters located within the metropolitan area. The Film returns are the box office revenue less the price paid for the film. blind bidding dummy variable was interacted with film budget and saturation to test the second hypothesis. The author finds theater owners submit lower average bids in blind

bidding states than in trade screen ones. With regards to the second hypothesis, blindbid theater owners place a greater emphasis on bid letter information: for every million dollar increase in film cost, blind bid theater owners bid an additional $8,900 while trade screen ones bid an additional $5,100. Regarding the final hypothesis, Blumenthal models utility as a function of the mean and variance of film returns which measures the degree of risk aversion among theater owners. In terms of utility, risk averse theater owners are worse off, because higher revenues are accompanied by greater volatility.

Theater owners are unable to reduce their bids enough to offset the extra volatility because of competitive forces. Using a laboratory experiment in several markets, Forsythe, Isaac, and Palfrey (1989) consider the anti-blind bidding laws unnecessary. They find an equilibrium where buyers learn to assume the worst about a seller‘s decision to blind bid items causing most items to no longer be blind bid. The game has a single seller versus n buyers, and the former must decide whether to reveal information about the item to all buyers. A seller reveals his information to buyers if the news is favorable, and does not if it is unfavorable.

A seller obtains the highest bid if he reveals his information. The auctioned item has both a common value and private value component. After a seller decides whether to reveal their information, the item is auctioned in a sealed bid first price auction. Several possible Nash equilibria are considered in the game, but the authors focus on the ? assume the worst? solution, because all other outcomes cannot be obtained so long as the auction follows a sequential equilibrium. This type of equilibrium occurs when buyers make conjectures about a seller‘s motives when they adopt a strategy which is consistent with the seller‘s best interest.

To obtain an ?assume the worst? solution, a seller continues to blind bid items as long as there is at least one unsophisticated buyer: a buyer who bids the average of all quality levels, rather than assumes the worst about no revealed information. With the passage of time, buyers learn that when a seller withholds information it is not in their interest, forcing sellers to reveal information for lower quality levels. Eventually, the market reaches a point where no items are blind bid. In five of the six blind-bid auctions, the average winning bid declines over time. Although blind bidding is not eliminated by

the conclusion of the auctions, it is practiced less frequently and buyers dramatically lower their expectations for the value for the auctioned item. The authors conclude the anti-blind bidding laws are unnecessary, because with the passage of time, blind bidding would have been phased out completely. These two studies offer two important insights. Although Blumenthal (1988) concludes theater owners are worse off under blind bidding, she does not consider that theater owners can diversify the risk of films by converting to the multiplex theater. In this manner, theater owners can pool the risk of mediocre and

blockbuster films rather than run the risk of exhibiting a single inferior film. Regarding Forsythe, Isaac and Palfrey (1989), if the movie companies did not reveal their information for blockbuster films, they were not obtaining the highest auction price. Since the movie companies must have acted in their own self-interest, I assume blind bidding provided some cost benefits which outweighed the decision to trade screen films. 2. 2 Natural Experiments In this section, I discuss three natural experiments which provide a reference for testing the effects of the anti-blind bidding laws on exit, admission prices, and delays.

Natural experiments are often used to examine the effect of a policy change. A researcher examines two groups which have similar characteristics, one of which is exposed to a policy change while the other is not, and observes how the outcome differs between the two. Natural experiments are called quasi experiments, because the researcher has little or no control over the observed situation, which is in contrast to social experiments where researchers implement proper experimental design. Card and Krueger (1994), Milyo and Wardfogel (1999), and Bergen, Levy, Rubin and Zeliger (2004), conduct natural experiments assuming an exogenous change

in a law. All three natural experiments assume the treatment effect is not correlated with the outcome variable and any uncontrolled independent variables correlated with it. Card and Krueger (1994) investigate the effect on employment of a 50 cent raise in the New Jersey minimum wage in the fast food industry. Milyo and Wardfogel (1999) examine the impact on prices of advertised and non-advertised items after a ban on liquor advertising is lifted in Rhode Island. The ban permitted retailers to charge higher prices which was considered especially helpful to small ? mom and pop‘

retailers that could not offer the price discounts of larger chains. Bergen et tal. (2004) investigate the net effects of item pricing laws for supermarkets which require that retailers label every item individually with a price tag to help ensure that consumers are not overcharged at the register. The three empirical studies conduct natural experiments in similar geographic regions. Card and Krueger (1994) compare the neighboring states of New Jersey and Pennsylvania. The authors use descriptive statistics from their data to argue that wages, prices, and employment measures are similar.

For example, the mean starting wage for New Jersey and Pennsylvania is $4. 61 and $4. 63, respectively, before New Jersey‘s increase in the minimum wage. Bergen et tal. (2004) target a narrow tri-state region of Clifton, New Jersey, Tarrytown, New York, and Greenwich, Connecticut to study the impact of item pricing laws. Close geographic proximity is one factor for the selected towns as the greatest distance that separates the towns is only approximately 50 miles. In addition, these towns have similar population size, population densities, and access to quality public schools.

Milyo and Wardforgel (1999) follow a similar strategy to Bergen et tal. (2004) by comparing adjacent states but narrowing their focus to three areas: Southern Rhode Island, Northwest Boston suburbs, and the Rhode Island and Massachusetts border. In addition, the three studies utilize multiple control groups which provide the benefit of observing how sensitive the results are to different controls. Card and Krueger (1994) compare full-time-equivalent employment (FTE) for New Jersey and Pennsylvania, but also compare FTE in New Jersey fast food stores which already paid

at least the new minimum wage to those in New Jersey that paid under the new minimum. Milyo and Wardforgel (1999) compare retail prices in Rhode Island with those from Massachusetts, but also use Rhode Island wholesale prices as a second control. Bergen et tal. (2004) compare prices in New Jersey with two controls New York and Connecticut both of which have item pricing laws. However, Connecticut exempted stores from the law which installed the electronic shelf label system because it ensured that the price at the shelf was the same as the price at the register.

Therefore, the authors used Connecticut stores to observe how prices differed among non item pricing law stores and those which used the electronic shelf system. I adopt the idea of multiple control groups when I examine the exit of theater owners. The Card and Krueger (1994) study has additional significance to my study because they use the difference-in-differences estimator, and I adopt this method for the analysis of admission prices. The primary benefit of this method is that the researcher is able to cancel out other industry factors which are common to the treatment and control group through second differencing.

Therefore, the difference-in-differences measures the impact on the outcome solely from the policy change. These empirical studies provided some important insights on how to conduct my natural experiment on the anti-blind bidding laws. When selecting treatment and control groups, it is important to select homogenous regions so that there is a believable rationale that the control group will behave like the treatment group. Use of multiple control groups is encouraged in natural experiments to test the robustness of the results.

In addition, I follow the method of Card and Krueger (1994) and use the difference-in-differences estimator to examine admission prices. Chapter 3 ADMISSION PRICES In this paper, I investigate the claims made by theater owners and movie companies about the impact of the anti-blind bidding laws on admission prices. I examine the impact of the strictest laws of Ohio and Pennsylvania, which eliminated blind bidding and placed severe restrictions on guarantees. I selected these states, because they present the strongest case for the laws having an impact according to theater owners‘ claims.

I compare average admission prices in these states before and after the passage of the law with prices in two states that never had such a law. For Ohio, I compare average prices in Cleveland with those in Detroit. For Pennsylvania, I compare average prices from Philadelphia and Pittsburgh with those of Detroit. 1 Using the difference-in-differences estimator, I find some evidence that the laws raised admission prices. Theater owners argued that admission prices were higher under blind bidding, because they had to increase their prices to cover losses incurred from inferior films and to compensate for the guarantees they paid.

According to theater owners, the anti-blind bidding laws would eliminate the burden of blind bidding, and in some states also guarantees, so that lower prices would follow. Movie companies claimed initially considered comparing average Philadelphia and Pittsburgh prices with those in Manhattan. I decided against using New York City as a control because prices were consistently higher there than in any other market because of the high cost of living in the area. The laws would have the opposite effect for two reasons. Theater owners would identify blockbuster films after viewing the preview, and a bidding war would ensue.

Since film rentals were bid higher, this cost would be passed along to moviegoers. In addition, movie companies claimed that the anti-blind bidding laws would cause delays in the release of films, and this cost would be passed on to consumers. 3. 1 Model I consider the claims of theater owners and movie companies about admission prices to be invalid because of what is universally accepted in economics about the demand for factor inputs. The demand for a factor input (e. g. labor or capital) is a derived demand in that demand for the factor and its price is contingent upon the demand for the final product.

For example, the demand for movie stars depends not only on their current salaries, but also the total tickets sold. Movie stars would be unable to command high salaries if there is not an overwhelming demand for motion pictures. Therefore, prices charged at movie theaters, an input, are determined by demand. On the other hand, admission prices are likely to differ across cities due to costs outside the control of the industry. For example, theater owners in New York City had higher rent or mortgage payments than those in Atlanta, Georgia because of the relatively high cost of land.

Another factor that varied regionally was the price of labor. Theater owners facing higher minimum wages had greater variable costs than those in states with lower minimums. I expect the anti-blind bidding laws to influence admission prices if they impacted marginal costs, or if they restrict the supply of films. Although the laws did not affect theater owners‘ marginal costs, they may have impacted the movie companies‘. Additional expenses were incurred because sales prints had to be specially made for the purposes of trade screening. This cost was not present in blind bidding states. 3. 2 Data and Methods

I obtained the data from Variety, which reported theaters from 15 cities on a weekly basis. Variety sampled most cities once a month with about 10 to 20 theaters per sample. The same theaters were generally sampled, but over longer periods of time, the sample changed as some exited the marketplace. I sampled each city quarterly. On occasion, Variety reported theaters which charged one dollar for admission. These observations were dropped from the data set, since they were second-run movie houses. Table 5. 1 shows the descriptive statistics for the data. Any city sampled was a representation of the metropolitan area.

Therefore, the sample contained some downtown theaters as well as many suburban theaters. For example, Detroit included downtown theaters such as the Adams, Fox, and Renaissance, and theaters such as the Dearborn, Americana West, and Macomb Mall from surrounding areas of Wayne, Oakland, and Macomb counties. During the first year that the ant-blind bidding laws were in effect, it is not clear which films were blind bid. This is because theater owners bid on films six months to one year in advance of the release date. For example, Ohio enacted the law in October 1978, but theater owners may have been bidding for films to be released in

___________________________________________________________________________ 2 According to Barry Reardon, distributional president at Warner Brothers, the additional expense to trade screen amounted to approximately $50,000 per film in Jim Robbins, ? Distribs Adapt to AntiBlind Bid Laws? , Variety, July 3, 1985, 80. 3 A sales print is a reel of film with the movie preview. April 1979 or as far away as October 1979. The Pennsylvania law became effective in May 1980. At that date, theater owners would bid on films for November 1980 up to May 1981. I address the lagged effect of an anti-blind bidding law on films by

examining average admission prices using two different treatment and control groups: 1) two years before and after a law, and 2) three years before and after a law. Table 3. 1 provides the descriptive statistics for these variables. For the Ohio law, I calculate average prices in 1976 and 1977 (pre-treatment group) and average prices in 1979 and 1980 (post-treatment group). This measures the immediate effect of the law even though some of the admission prices in 1979 will be for films which were not trade screened. For three years before and after the law, I use average prices in 1975 and

1976 compared with those in 1980 and 1981. In this case, all films in the posttreatment group were trade screened. For the Pennsylvania law, I use the same procedure for selecting the pre and post-treatment groups. I consider the passage of the Ohio and Pennsylvania laws a natural experiment, and I proceed to measure the impact of a law by using the difference-indifferences estimator defined as the change in the population means from the treatment group less the change in population means from the control group. This method has an advantage over comparing the means of the treatment and control group after the

laws because the latter assumes the treatment and control groups are identical in every way except for the law. The difference-in-differences estimator makes the weaker assumption that regardless of the overall factors affecting admission prices, they affected the treatment and control groups in the same way. In order to understand the meaning of the difference-in-differences estimator, consider the interpretation of first differences between the treatment and control. The change in price in the control group informs us how prices would have behaved in the treatment group if the law was

not implemented. The change in price in the treatment group tells us how the average price behaved given the enactment of the law. By taking second differences, I obtain the difference-in-differences estimator which measures the effect of the law by taking the difference in what happened with average prices compared with what would have happened to them. 3. 3 Cleveland and Detroit Figure 5. 1 displays average admission prices for Cleveland and Detroit from 1975-1981. Detroit‘s average prices remain consistently above Cleveland‘s by approximately 59 cents throughout the observed period.

I examine average admission prices over time to see if the assumption that overall factors that affect them are the same for both treatment and control groups. Unobserved factors are more likely to be different if the trend in prices diverges before the treatment effect. Average admission prices for Cleveland and Detroit remain relatively steady before the implementation of the law implying the assumption of a common trend appears valid. The results for the difference-in-differences estimator are shown in Table 3. 2. Comparing average prices two years before and after the law, I find Detroit‘s

prices increase by seven cents and Cleveland‘s rise by 16 cents. The seven cent increase in average prices represents how Cleveland prices would have behaved in the absence of the anti-blind bidding law. After taking second differences, I find that the Ohio law significantly increases Cleveland‘s average prices by nine cents. Examining admission prices three years before and after the law does not produce the same conclusion. Cleveland‘s and Detroit‘s average prices increase by 20 and 21 cents, respectively. The difference-in-differences estimator shows that Cleveland‘s average prices are significantly lower by one cent.

3. 4 Philadelphia, Pittsburgh and Detroit Figure 5. 2 shows average prices in Philadelphia and Pittsburgh versus those in Detroit from 1977-1983. For the first two years, prices are nearly identical. In 1979 and 1980, the difference in average prices remains relatively steady at 10 and 15 cents, respectively. Beyond 1980, the difference in average prices increases, ranging from 36 to 41 cents. The assumption that factors have a common trend appears satisfied because the difference in average prices maintains itself in 1979 and 1980. The first and second differences for average admission prices are shown in Table 5. 3.

Comparing average prices two years before and after the Pennsylvania law, I find Philadelphia‘s and Pittsburgh‘s average prices rise by 43 cents while Detroit‘s increases by 11 cents. Detroit‘s prices are assumed to be behaving like Philadelphia‘s and Pittsburgh‘s if Pennsylvania had never passed an anti-blind bidding law. The difference-in-differences estimator shows that the law results in a statistically significant 32 cent increase in admission prices. Comparing three years before and after the law produces a similar result, the law causes higher average admission prices for Philadelphia and Pittsburgh by 53 cents.

3. 5 Conclusion I examine the impact of the Ohio and Pennsylvania anti-blind bidding laws on admission prices and I find higher admission prices in Cleveland, Philadelphia, and Pittsburgh in three of the four difference-in-differences estimators. The impact of the Pennsylvania law is more robust than the Ohio law because in one case, average admission prices decline by one cent. A potential explanation for higher average admission prices is that the movie companies‘ marginal costs increased in anti-blind bidding states, because sales prints had to be produced exclusively for trade screening films.

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